J31 | Macro Paper Warehouse

Across-Country Wage Compression in Multinationals

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

Layer 1 — Summary

Many multinationals do not fully adjust wages to the local context of their foreign establishments; instead, they partially link the wages of foreign workers in a given position to the wages paid in the same position at headquarters — a practice the authors call “wage anchoring.” Using yearly establishment-level compensation data on roughly 1,200 multinationals operating across 174 cities worldwide (2000–2015) and matched employer-employee administrative data (RAIS) from Brazil, Hjort, Li, and Sarsons document that a 10 percent higher headquarters wage is associated with 1.63–2.8 percent higher wages for workers in the same occupation at foreign establishments, with the within-firm across-country correlation substantially exceeding the correlation between a given establishment’s wages and the local average paid by other multinationals for the same position. To establish a causal link between externally imposed headquarters wage changes and subsequent foreign establishment wage responses, the paper exploits two identification strategies: minimum wage shocks in the headquarters country or U.S. state and exchange rate fluctuations, both of which generate plausibly exogenous variation in headquarters wages that is then partially transmitted to foreign workers in the same position. Wage change transmission appears to be direct and to operate through firm-wide wage-setting procedures rather than through associated changes in technology or employment at foreign establishments, a conclusion the Brazil RAIS data support because total employment at multinationals’ Brazilian establishments shows little change following positive external shocks to headquarters wages. Wage anchoring is strongest for low-skill occupations (cleaners, drivers, security guards), where a 10 percent higher headquarters wage is associated with a 2.8 percent higher foreign establishment wage, versus roughly 1.2 percent for middle- and high-skill occupations; the resulting spatial compression of wages is in line with how many multinationals themselves report setting pay across locations.

In depth

Q1. What is the central phenomenon documented in this paper, and what are the two broad empirical components of the analysis?

The central phenomenon is “wage anchoring”: multinationals link wages at their foreign establishments to the wage level at headquarters for the same narrowly-defined occupation, so that the within-firm across-country wage distribution is more compressed than what local labor-market conditions alone would imply. The first empirical component is descriptive — documenting the high cross-sectional correlation between headquarters and foreign establishment wages within a firm×occupation cell, controlling for city×year effects and local wage benchmarks. The second component is causal — using minimum wage shocks in the headquarters country or U.S. state and exchange rate shocks to generate externally imposed changes in headquarters wages, and tracing whether and how quickly those changes are partially transmitted to foreign establishments.

Q2. What is the primary dataset, what does it cover, and what are its key limitations?

The primary dataset was compiled by an unidentified consulting company that gathers compensation information from client employers and harmonizes positions globally into 309 occupations across 16 skill levels and 26 occupational categories. It covers roughly 1,200 multinationals (private-sector firms and multinational public-sector employers such as NGOs and multilateral organizations), operating in more than 170 cities, with yearly observations spanning 2000–2015. The data report average nominal gross total monthly wages for domestic (non-expat) workers in each establishment-occupation-year cell. Key limitations: the panel is unbalanced because multinationals choose which establishments report each year and often rotate establishments in and out; matching between the headquarters and any given foreign establishment requires observing the same occupation in the same year at both, which reduces the headquarters-matched sample to 80 employers and 611 foreign establishments (Sample 3, the most comparable subsample). The publicly listed U.S. firms in the data account for about one-third of total revenue of all publicly listed U.S. firms, so the sample is skewed toward unusually large employers.

Q3. How do the authors define and measure “wage anchoring” in the descriptive section?

The authors regress log average wages of workers in occupation j at a firm f’s foreign establishment in city c in year t (wjfct) on log average wages for the same occupation at the firm’s headquarters (HQwjft), controlling for firm×occupation fixed effects, city×year fixed effects, and a local market wage benchmark measured either as the average paid by other multinationals in the same city-occupation-year cell or as a city×occupation×year fixed effect. The estimated coefficient on the headquarters wage — around 0.163 using the benchmark-wage control and about 0.09 using the more restrictive city×occupation×year fixed effect — measures how much of a headquarters wage difference is “passed through” to foreign establishment wages within the same firm and occupation. They further document that the within-firm wage slope (the difference between wages in consecutive skill levels within an occupational category) at foreign establishments is similarly anchored to the corresponding slope at headquarters, with a 10 percent greater consecutive-skill wage gap at headquarters associated with about a 1.4 percent greater gap at the foreign establishment.

Q4. What exactly do the minimum wage and exchange rate identification strategies exploit, and what do they identify?

The minimum wage strategy compares multinationals whose headquarters are located in a country or U.S. state that experiences a minimum wage increase (“treated”) against multinationals whose headquarters are not exposed (“control”), conditioning on establishments being in the same foreign city. Within the treated group, it also exploits cross-occupation variation: within a given foreign establishment, workers in positions whose headquarters counterparts are more exposed to the minimum wage increase (because their wages are closer to the new minimum) experience larger foreign wage gains. The exchange rate strategy exploits appreciation of a non-U.S. headquarter country’s currency against the dollar: when the USD-measured headquarters wage of such a multinational increases following an appreciation, this tests whether foreign establishment wages in USD also rise. Because exchange rates increase and decrease, are less stable than minimum wages, and have different underlying drivers, the exchange rate design provides an independent corroboration of the minimum wage findings. Both strategies identify the effect of externally imposed headquarters wage changes on wages at the same firm’s foreign establishments in the same narrowly defined occupation.

Q5. What evidence is marshaled against indirect pathways (technology changes, employment changes, offshoring) as the driver of foreign wage transmission?

The paper presents three types of evidence against indirect pathways. First, including headquarters country×year fixed effects in the descriptive wage regressions — which absorbs any technology shocks originating in the headquarters country that affect all occupations uniformly — leaves the estimated wage anchoring coefficient essentially unchanged. Second, event study and panel regressions using the Brazil RAIS data show little change in total employment at multinationals’ Brazilian establishments following positive external shocks to headquarters wages, which is hard to reconcile with employment-driven or offshoring-driven wage adjustment. Third, a causal forest analysis of the conditional average treatment effect of minimum wage shocks on foreign wages — estimated allowing responses to vary with a wide range of job, employer, sector, and location characteristics — finds that occupation characteristics and sector have little explanatory power for which establishments transmit more, while differences in transmission are more closely related to characteristics of the headquarter-establishment country pair (proximity, similarity, shared language), which are more naturally associated with administrative coordination than with technology or production-style linkages.

Q6. How does occupation skill level moderate wage anchoring, and what does this heterogeneity imply?

Wage anchoring is strongest for low-skill occupations. In the descriptive correlations, a 10 percent higher headquarters wage is associated with 2.8 percent higher foreign wages in low-skill jobs (cleaners, drivers, data entry clerks, security guards) but only about 1.2 percent higher foreign wages in both middle-skill and high-skill jobs. The occupation heterogeneity is visible graphically (Figure 1 Panel C) and holds in regressions interacting the headquarters wage with skill-level indicators. A natural interpretation, consistent with the firm-wide wage-setting procedure explanation, is that firms are most likely to apply standardized pay rules to lower-level positions where local market customization may be seen as less important; higher-skill workers may be more likely to have individually negotiated contracts responsive to local conditions. The heterogeneity also implies that the spatial compression effect — wages in foreign establishments being pulled toward headquarters levels — is particularly pronounced at the lower end of the within-firm wage distribution, affecting positions like cleaners and guards in ways that can result in wages that are, relative to GDP per capita, an order of magnitude higher than what headquarters workers in the same position receive.

Q7. What is the “spatial compression” implication and how does it relate to within-firm wage inequality?

Wage anchoring implies that workers in the same occupation at foreign establishments located in lower-income countries receive wages that are compressed toward headquarters levels rather than fully adjusted to local wages. The paper shows that nominal wages at foreign establishments average about 89 percent of headquarters wages in the same occupation and year — and about 78 percent for establishments in countries poorer than the headquarter country — a ratio that is roughly stable across the within-firm headquarters wage distribution. This partial equalization is what the authors call “across-country wage compression”: it reduces the within-multinational cross-country wage dispersion relative to what would arise from purely market-based, locally responsive wage-setting. The spatial compression is consistent with how many firms self-report setting wages: a survey of primarily North American employers (Culpepper & Associates, 2011) found 29 percent report paying the same nominal wages across locations, and several large employers (Amazon, IKEA, Walmart) have self-imposed country-wide wage floors.

Q8. What role do headquarter-establishment country-pair characteristics play in predicting which establishments exhibit stronger wage transmission?

Using a causal forest algorithm to estimate the conditional average treatment effect of a minimum wage shock at headquarters and then constructing above- versus below-median predicted treatment groups, the paper finds that differences in transmission are “generally not large” but that higher transmission is somewhat associated with characteristics of the headquarter-establishment country pair: pairs that are more closely connected and share more similarities (e.g., common language, closer geographic distance) transmit more. Some foreign-establishment-country characteristics such as inequality and urbanization also appear related. In contrast, occupation characteristics (such as offshorability), the sector the multinational operates in, and characteristics of the headquarter country alone have little explanatory power. The paper notes these findings do not conclusively rule out alternative explanations but are more consistent with administrative coordination channels than with technology- or employment-based ones.

Q9. What role do potential fairness preferences and firm-wide wage norms play in the paper’s interpretation?

The authors suggest several possible mechanisms through which firm-wide wage-setting procedures could operate. Firms may adopt uniform wage-setting to reduce the menu and information costs of localized wage-setting (Lemieux et al., 2012); to increase foreign worker morale, particularly if workers are averse to pay inequality relative to headquarters peers (Card et al., 2012; Dube et al., 2019); or to respond to fairness preferences from headquarters workers or consumers (Harrison & Scorse, 2010). Survey evidence from Alfaro-Urena et al. (2019) explicitly records that multinationals pay high wages abroad in part to “ensure cross-country pay fairness within the MNC.” Alternatively, the authors note that firm-wide wage-setting may represent a form of firm inertia or mistakes — an inability or unwillingness to fully adapt pricing and compensation to local contexts — consistent with DellaVigna & Gentzkow (2019). The paper presents this as an open question for future research rather than definitively adjudicating among the explanations.

Q10. How does the Brazil RAIS data corroborate and extend the global multinationals findings?

The RAIS matched employer-employee administrative data cover all employees at each Brazilian establishment of the 44 multinationals in the global dataset that operate in Brazil, with individual-level information on wages, education, race, gender, age, and tenure. Because RAIS is an administrative census of formal-sector employment rather than a consulting firm’s client dataset, it provides independent corroboration of the main findings. The paper confirms using RAIS that wages of individual workers at multinationals’ Brazilian establishments rise abruptly when their foreign headquarters experience positive external shocks. The RAIS data then enable the additional step of examining employment responses, where event study and panel regressions find little change in total employment at multinationals’ Brazilian establishments following such shocks — evidence against employment- or technology-driven indirect pathways as the primary explanation for wage transmission.

Key Concepts

Wage anchoring: The practice by which a multinational ties wages at its foreign establishments, for workers in a given occupation, to the wage level at its headquarters for the same occupation. In this paper’s usage, anchoring does not mean wages are set identically across locations but that they are partially linked — externally imposed changes in headquarters wages are partially transmitted to foreign establishment wages — rather than being independently set based on local labor-market conditions.

Across-country wage compression: The reduction in the cross-country dispersion of wages within a multinational that results from wage anchoring. Because foreign establishment wages are partially pulled toward headquarters levels rather than fully adjusting to local wages, the multinational’s within-firm wage distribution is more compressed across countries than it would be under purely localized wage-setting. In the paper’s data, this compression is particularly pronounced for low-skill occupations in lower-income host countries.

Firm-wide wage-setting procedures: Administrative practices, such as applying a single pay scale or a fixed wage ratio across all of a firm’s establishments regardless of location, that mechanically link foreign establishment wages to headquarters wages. The paper argues these procedures — rather than correlated technology shocks or employment adjustments — are the proximate driver of wage anchoring, on the basis of the employment non-response in Brazil, the persistence of anchoring after controlling for headquarters-country technology shocks, and the pattern of heterogeneity across country pairs.

Partial transmission: A load-bearing qualifier in this paper describing the magnitude of wage anchoring: headquarters wage changes arising from external shocks are not fully extended to foreign workers, but a fraction of the change is passed through. The estimated pass-through in descriptive regressions ranges from about 0.09 to 0.31 depending on specification and sample, and is highest (around 0.28) for low-skill occupations. The partial nature of transmission means that the spatial compression is real but incomplete.

Wage slope: The difference between log average wages paid by an employer to workers in jobs of consecutive skill levels within an occupational category, at a given establishment. The paper documents that the wage slope at foreign establishments is correlated with the wage slope at headquarters — a 10 percent greater consecutive-skill wage gap at headquarters is associated with a roughly 1.4 percent greater gap at the foreign establishment — suggesting that the anchoring extends beyond the level of wages to the internal wage structure.

External shocks to headquarter wages: Minimum wage increases in the headquarters country or U.S. state, and exchange rate fluctuations that change the USD value of wages set in local currency. These shocks serve as instruments or quasi-experimental sources of variation in headquarters wages that are plausibly exogenous to conditions at foreign establishments, enabling causal identification of the effect of headquarter wage changes on foreign establishment wages.

Causal forest (heterogeneous treatment effect estimation): A machine learning algorithm used in the paper to estimate the conditional average treatment effect of a minimum wage shock at headquarters, allowing the size of the foreign wage response to vary flexibly with a large set of characteristics (job, employer, sector, headquarter country, establishment country, headquarter-establishment country pair). The resulting predicted treatment effect scores are used to construct above- and below-median transmission groups, which are then compared across observable characteristics to identify what predicts stronger wage anchoring.

Summary based on NBER Working Paper 26788 (February 2020, Revised April 2025). Source text was truncated after the beginning of Section 4.1 (minimum wage event study analysis); all causal evidence descriptions draw on the introduction and Section 3–4 framing rather than the full Section 4 tables and Section 5 heterogeneity analysis. AI-assisted, human review pending.

Automation and Rent Dissipation

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

Acemoglu and Restrepo examine the effects of automation in economies where labor market distortions cause some workers to earn rents—wages above their opportunity cost or outside option. The central question is how the interplay between automation and these distortions shapes wages, inequality, and productivity. The paper makes three contributions: a theoretical framework identifying a rent dissipation mechanism, reduced-form empirical evidence using US data from 1980 to 2016, and a general equilibrium quantification of automation’s aggregate effects.

The theoretical framework extends the task model of Acemoglu and Restrepo (2022) to incorporate task-specific wage wedges. In this setup, a firm employing labor of type g in task x pays a wage equal to the base wage multiplied by an exogenous wedge capturing rents from efficiency wages, bargaining, licensing, regulations, or norms. Because these wedges artificially inflate labor costs in high-rent tasks, firms have a stronger incentive to automate precisely those tasks—automation saves more in labor costs where rents are highest. Proposition 3 establishes that endogenous adoption decisions are tilted toward high-rent tasks: the rent distribution in automated tasks first-order stochastically dominates the rent distribution across all tasks. This targeting generates the rent dissipation mechanism. The equilibrium is inefficient on both the intensive margin (too little employment in high-rent tasks) and the extensive margin (excessive automation of high-rent tasks that a social planner would prefer to keep labor-intensive).

The rent dissipation mechanism has three consequences identified theoretically. First, it amplifies average wage losses for exposed groups beyond what displacement alone would produce, pushing displaced workers toward lower-paying jobs. Second, it compresses within-group wage dispersion by concentrating losses at higher percentiles of the within-group distribution, generating a U-shaped pattern of wage changes: workers at low percentiles earn no rents and experience only base-wage adjustments, while workers between the 70th and 95th percentiles face the steepest declines due to loss of high-rent jobs. Third, it is inefficient: because the tasks targeted by automation are not those where wages reflect scarcity or skill but rather distortionary rents, a planner would have preferred more labor allocated to these tasks, and rent dissipation offsets part or all of the cost-saving productivity gains from automation.

The empirical analysis covers 500 detailed demographic groups defined by education (five levels), gender, five age groups, five race/ethnicity groups, and nativity. Task displacement is measured as a weighted sum of industry-level automation exposure using three proxies: adjusted industrial robot penetration, specialized software services, and dedicated machinery in value added. Workers in the middle and lower-middle of the wage distribution lost 15–20% of their tasks to automation between 1980 and 2016, while post-college workers saw few tasks automated.

A 10 percentage point increase in task displacement is associated with a 24% decline in group-level relative wages (β = −2.36, s.e. = 0.13), falling to 19% after controlling for gender, education, sectoral demand, and rent shifters (β = −1.90, s.e. = 0.29). The U-shaped pattern in within-group wage changes is clearly visible: wages decline by 25–30% per 10 percentage point task displacement at the 70th–90th percentiles, compared to only 16% at the 5th–40th percentiles. Decomposing the average wage effect, the base-wage component is β = −1.53 (s.e. = 0.33) and the rent-dissipation component is β = −0.37 (s.e. = 0.11), implying a rent dissipation rate of approximately 37%. Across multiple proxies for rents—inter-industry/occupation wage differentials, wage losses after job displacement, and quit rates—the average estimated rent dissipation rate is approximately 35%. Rent dissipation accounts for one-fifth of the overall relative wage decline experienced by groups exposed to automation.

In the general equilibrium quantification (with elasticity of substitution λ = 0.5, average cost savings π = 30%, and average rent in automated tasks of 35%), automation accounts for 52% of the rise in between-group wage inequality since 1980: 42 percentage points via baseline displacement effects on labor demand, and 10 percentage points via rent dissipation. Cost savings from automation increased TFP by approximately 3% between 1980 and 2016, but inefficient rent dissipation offsets 60–90% of these gains, leaving net TFP gains of only 0.3–1.3% and net aggregate consumption gains of only 0.45–1.95% over the 36-year period.

Q: What is the rent dissipation mechanism, and why does it arise? A: Rent dissipation arises because labor market wedges make high-rent tasks artificially costly to staff with workers, giving firms a stronger incentive to automate precisely those tasks. When automation displaces workers from high-rent jobs, workers lose the premium above their opportunity cost that those jobs paid, amplifying wage losses beyond what displacement alone would cause. The mechanism is endogenous: firms do not randomly automate tasks but disproportionately target tasks where rents are highest, since doing so saves the most in labor costs. Proposition 3 formalizes this as first-order stochastic dominance of the rent distribution in automated tasks over the rent distribution in all tasks.

Q: Why is rent dissipation inefficient? A: In a distorted economy, high-rent tasks already feature too little employment at the equilibrium—firms under-hire in these tasks because the wage wedge makes labor artificially expensive. A social planner would want to allocate more labor to these tasks, not less. When automation further removes labor from high-rent tasks, it moves the economy further from the efficient allocation, dissipating rents that reflect distortions rather than true scarcity. The TFP formula shows that this inefficient targeting offsets part or all of the cost-saving gains from automation, and can even reduce aggregate productivity if the cost savings are small relative to the rent losses.

Q: What is the U-shaped pattern of within-group wage changes, and what does it indicate? A: The U-shaped pattern means that wage declines due to automation are smallest at the bottom percentiles of a group’s within-group wage distribution, largest in the 70th–95th percentile range, and then smaller again at the very top. Workers at low percentiles earn no rents, so they experience only the base-wage adjustment from reduced labor demand. Workers in the middle-upper range of the distribution hold the high-rent jobs that are disproportionately automated, so they lose both the base-wage component and the rent component of their wages. This pattern is directly visible in US data 1980–2016, with declines of 25–30% per 10 percentage point task displacement at the 70th–90th percentiles versus 16% at the 5th–40th percentiles.

Q: How is task displacement measured, and which groups are most exposed? A: Task displacement is measured as a weighted sum of industry-level automation exposure, accounting for each demographic group’s specialization in routine tasks within industries. Three proxies are used: the adjusted penetration of industrial robots, the increase in specialized software services, and the increase in dedicated machinery in value added. Workers in the middle and lower-middle of the wage distribution—broadly corresponding to non-college workers—lost 15–20% of their tasks to automation between 1980 and 2016. Post-college degree workers saw few tasks automated.

Q: How large is the rent dissipation rate, and how robust is this estimate? A: The baseline estimate from the U-shaped within-group wage change decomposition implies a rent dissipation rate (μ_Ag/μ_g − 1) of approximately 37% (β = −0.37, s.e. = 0.11). Using inter-industry and occupation wage differentials as a proxy for rents, the estimate is 39% (β = −0.39, s.e. = 0.11). Using wage losses after job displacement, the estimate is 20% (β = −0.20, s.e. = 0.04). After purging compensating differentials from the wage differential proxy the estimate remains 37%; after purging from the displacement-loss proxy it falls to 19%. Quit-rate evidence is consistent with rent dissipation: automation shifts workers toward higher-quit-rate jobs, which are lower-rent jobs. The average across proxies is approximately 35%.

Q: How much of between-group wage inequality since 1980 does automation explain, and what share is due to rent dissipation specifically? A: Automation accounts for 52% of the rise in between-group wage inequality in the US since 1980. Of this 52 percentage points, 42 percentage points are attributable to the baseline displacement effect working through reduced labor demand for exposed groups. The remaining 10 percentage points are attributable to rent dissipation—automation pushing exposed groups away from high-rent tasks into lower-paying employment. Rent dissipation thus accounts for roughly one-fifth (10/52) of automation’s total contribution to between-group inequality.

Q: How large are the productivity gains from automation, and how much does rent dissipation offset them? A: Cost savings from automation increased TFP by approximately 3% between 1980 and 2016. However, inefficient rent dissipation offsets 60–90% of these gains, because automation disproportionately targets high-rent tasks rather than tasks where the efficiency case is strongest. The net TFP increase attributable to automation is only 0.3–1.3% over the 36-year period, and the corresponding net increase in aggregate consumption is only 0.45–1.95%.

Q: How does automation affect within-group versus between-group inequality, and why is this notable? A: Automation increases between-group inequality by reducing relative wages of exposed groups (largely non-college workers) relative to unexposed groups, accounting for 52% of the rise in between-group inequality since 1980. At the same time, automation reduces within-group wage dispersion for exposed groups by compressing wages at higher percentiles. This contrasts with the standard view that inequality is fractal—rising at all levels of aggregation due to skill-biased demand—and helps explain why within-group inequality has risen steadily for college workers since the 1980s while remaining flat and then declining for non-college workers since the 1990s.

Q: What do the propagation matrix and rent-impact matrix represent in the general equilibrium analysis? A: The propagation matrix encodes how task reallocation due to automation in one demographic group creates competition for marginal tasks across other groups, transmitting the wage effects of automation to groups not directly displaced. The rent-impact matrix encodes how this task reallocation changes the rent composition of employment across groups. Both matrices are estimated from US data on task shares and group-level wage elasticities and are used to translate partial-equilibrium estimates of task displacement and rent dissipation into general equilibrium effects on wages and productivity for all demographic groups simultaneously.

Q: What are the policy implications of inefficient rent dissipation? A: Because rent dissipation is inefficient, the social value of automation is lower than what firms and consumers are willing to pay—firms capture all the labor cost savings but do not internalize the welfare cost of destroying high-rent jobs that the distorted equilibrium already under-supplies. Second-best interventions should address the underlying distortions generating rents rather than trying to slow automation directly. The paper suggests that strengthening labor market institutions supporting worker rents in non-automatable tasks could partially counteract the adverse distributional consequences of automation.

Q: How does this paper relate to Bound and Johnson (1992) and Borjas and Ramey (1995)? A: Bound and Johnson (1992) decompose changes in the US wage structure between 1979 and 1988 into technology, supply, and rent components (modeled as exogenous industry wedges), finding that 10–20% of between-group wage changes reflect rent losses. Borjas and Ramey (1995) estimate that trade increased the college premium by 1.3–2.6 log points between 1976 and 1990, with 15–33% due to loss of rents from trade-exposed jobs. Both are comparable to this paper’s finding that rent dissipation accounts for one-fifth of the wage effect of automation, though Bound and Johnson’s estimates include all factors affecting rents while this paper isolates automation specifically.

Worker rents: Wages above a worker’s opportunity cost or outside option, arising from efficiency wages, bargaining, licensing, regulations, or norms. Modeled as task-specific multiplicative wedges (μ_gx ≥ 1) that force firms to pay more than the base wage for labor in particular tasks. Explicitly excludes compensating differentials and skill premia.

Rent dissipation: The loss of above-opportunity-cost wages experienced by workers displaced from high-rent tasks into lower-paying employment. Occurs because automation endogenously targets high-rent tasks where labor is most expensive, and pushes workers into tasks where rents are lower. Quantified as the ratio of average rents in automated tasks to average rents across all tasks, minus one (approximately 35% in US data 1980–2016).

Task displacement: The share of tasks performed by a demographic group that are automated away, measured as a weighted sum of industry-level automation exposure accounting for the group’s specialization in routine tasks. Distinct from employment loss because it captures reallocation of tasks from labor to capital within the production function.

U-shaped within-group wage change profile: The pattern whereby automation generates the largest wage declines at intermediate-to-upper percentiles (70th–95th) of an exposed group’s within-group wage distribution, with smaller declines at the bottom, because high-percentile workers disproportionately hold high-rent jobs targeted by automation. Predicted theoretically and confirmed empirically in US data 1980–2016.

Propagation matrix: A matrix estimated from US data on task shares and group-level wage elasticities that encodes how automation of tasks performed by one demographic group creates competition for marginal tasks with other groups, transmitting wage effects across the demographic distribution in general equilibrium.

Inefficient automation targeting: The mechanism by which labor market distortions cause firms to automate high-rent tasks that a social planner would prefer to keep labor-intensive, since the distorted equilibrium already features too little employment in those tasks. Results in rent dissipation offsetting 60–90% of automation’s direct TFP gains from cost savings.

Rent-impact matrix: A matrix that encodes how task reallocation due to automation changes the rent composition of employment across demographic groups, used alongside the propagation matrix to compute general equilibrium effects of automation on wages and productivity accounting for distortions.

Bargaining and Inequality in the Labor Market

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

Layer 1 — Overview

Research Question. How prevalent is individual wage bargaining in the labor market, what determines firms’ bargaining strategies, how do bargaining encounters unfold for workers, and does heterogeneity in bargaining behavior translate into wage inequality—including the gender wage gap?

Data and Setting. The paper develops and validates novel linked survey data for Germany. A firm survey was fielded by the ifo Institute to senior HR professionals and managers in two waves (September 2021 and January 2022), yielding 772 complete responses across all major sectors and regions. These responses were linked—with consent obtained from 72% of firms—to German Social Security records (the Integrated Employment Biographies, IEB) covering 416,821 full-time employees at matched firms in 2020, and to Orbis balance sheet data for firm productivity proxies. A separate worker survey was fielded by the IAB to 135,000 full-time German workers, with 9,756 completing it; nearly 10,000 responses were used for analysis, with 7,079 workers employed at surveyed firms. The worker survey elicited detailed bargaining histories for workers who had received an outside offer in the prior six months, bargaining at the start of current employment (for workers with tenure of three years or less), and responses to a hypothetical salary expectation scenario.

Definition of Individual Bargaining. The authors define a firm as having a “bargaining strategy” if it differentiates pay between workers in the same position it perceives to have similar productivity—encompassing both variation in initial offers (which may reflect firms using information on workers’ salary expectations) and back-and-forth negotiation. Elicitation distinguishes four employee groups (recent labor market entrants, experienced non-managers, managers, and bottleneck-occupation workers) and two contexts (new external hires and incumbent workers who receive an outside offer).

Prevalence of Bargaining. Approximately 50% of surveyed firms are willing to differentiate base wages for recent labor market entrants, more than 80% for experienced non-managers and managers, and nearly all for workers in bottleneck occupations they are struggling to fill. For incumbent workers facing outside offers, 57% of firms would increase pay for recent entrants, and more than 80% for experienced incumbents, managers, and bottleneck workers. In total, 80% of workers in the sample are in positions where individual bargaining is possible.

Magnitude of Wage Differentiation. For new external hires, the typical firm expects a gap between the highest and lowest offers of 3% for recent entrants, 5% for experienced non-managers, and 10% for managers (conditional on a gap: 6%, 10%, and 12% respectively). For incumbent workers responding to outside offers, the typical firm will adjust pay by 3% for recent entrants, 6% for experienced non-managers, and 10% for managers (conditional on responding: 6%, 7%, and 14% respectively). Forty-four percent of firms report that variation in initial offers is at least as important as back-and-forth negotiation in determining workers’ final pay.

Predictors of Firm Bargaining Strategies. Contrary to models predicting more productive firms are more likely to bargain (Doniger 2015; Postel-Vinay and Robin 2004; Flinn and Mullins 2021), firms that bargain are not more productive—as proxied by firm age, size, or assets per employee—nor do they pay higher mean wages. A variance decomposition shows that employee-group dummies alone explain 33% of variation in bargaining strategies for new hires, comparable to more than 500 firm dummies. Labor market factors—particularly whether a position is hard to fill—are systematically associated with bargaining willingness. Collective bargaining agreement (CBA) coverage and East German location are negatively correlated with bargaining flexibility.

How Bargaining Unfolds. In 57% of worker-firm interactions, the worker provides salary expectations before the firm makes its initial offer; 29% of firms require this information. About one-third of applicants ask for more after the initial offer, requesting on average a 3% increase; conditional on asking, about half of firms raise the offer, but fewer than one-third match what was requested, with the typical worker improving the offer by 1.5%. The majority of outside offers are rejected: only 9% of workers who received an outside offer in the prior six months chose to move to a new firm. Of the 91% who remained at their incumbent firm, 13% successfully renegotiated their pay. Back-and-forth dynamics—where offers are accepted or rejected only after multiple rounds—are consistent with models of two-sided incomplete information.

Worker Heterogeneity and Wage Inequality. Workers with better self-assessed outside options are 9 percentage points more likely to ask for an increase after the initial offer and 7 percentage points more likely to successfully negotiate a raise, relative to same-occupation coworkers with worse outside options. Women are 6 percentage points less likely to successfully negotiate their pay upward and show lower salary expectation provision rates, including in a hypothetical scenario in which pay range information is equalized. These gender differences in bargaining are not explained by women negotiating more over non-wage amenities; controlling for outside options and risk tolerance shrinks the female coefficient by at most 15%. Among surveyed workers, after controlling for occupation-establishment fixed effects, there is no gender wage gap at firms that do not bargain, but a 4–5 percentage point gender wage gap at firms that do bargain. Across specifications, firms that engage in individual bargaining have a 3 percentage point higher gender wage gap. A simple decomposition suggests that at surveyed firms, 44% of the residual gender pay gap can be attributed to bargaining. For workers at bargaining firms, a 10 percentage point higher pay premium at the prior firm is associated with 0.5 percent higher pay at the current firm, conditional on occupation-establishment fixed effects; this relationship is statistically insignificant for workers at non-bargaining firms.

Scope Conditions. Results apply to full-time private-sector workers in Germany between ages 25 and 50, with the firm sample over-representing medium and large firms (median size 50–249 employees). CBA coverage in the sample (41%) reflects Germany’s institutional context where firms retain the right to pay above CBA floors. Results are robust to re-weighting to match the overall distribution of German firm size and sector.

In depth

Q1. How do the authors define “individual bargaining” and why is this definition broader than standard labor economics usage?

The authors define a firm as having a bargaining strategy if it differentiates pay between workers in the same position it perceives to have similar productivity, covering both tailoring of initial offers and back-and-forth negotiation. Standard labor economics definitions typically condition on wages being set ex post once outside options are revealed, and focus on back-and-forth negotiation alone. The authors’ definition is most analogous to standard definitions of price discrimination. Empirically, the vast majority of firms that differentiate initial offers (93%) are also willing to engage in back-and-forth negotiation.

Q2. How was the firm survey designed to elicit bargaining strategies reliably, and what is the “protocol question”?

The protocol question asked: “How much more could a person maximally receive compared to the fixed compensation you would have offered based on the person’s qualification/fit for the position alone?” with options ranging from “0%/no adjustments possible” to “more than 40%.” Wording was developed through over 100 conversations with HR professionals; “qualifications and fit” was the phrase most closely aligned with HR professionals’ concept of productivity. The survey was fielded by the ifo Institute—an organization with decades of experience surveying this population—with a 51% response rate, 83% completion rate, and median response time of 11 minutes.

Q3. What validation exercises support the reliability of the elicited firm bargaining measures?

Four exercises are reported. First, intra-respondent reliability: the cross-tabulations between the protocol and incidence questions show most mass on or below the diagonal (incidence-implied spread no greater than the protocol-implied flexibility). Second, inter-respondent reliability: among 37 firms with multiple respondents, there is significant overlap in independently provided answers. Third, external validity using publicly available data: for 90% of firms reporting no CBA, no CBA evidence is found; for 99% reporting no pay information in job ads, none is found in online postings; for 82% reporting no salary expectation elicitation, no evidence of it appears in online application forms. Fourth, the elicited firm strategies are highly correlated with the matching workers’ survey responses—e.g., workers at firms stating they elicit salary expectations are significantly more likely to report having provided these expectations.

Q4. Is firm productivity associated with whether a firm engages in individual bargaining?

No. Firms that bargain and those that do not are similar with respect to firm size, firm age, and total assets per employee, and they also do not differ significantly in their AKM wage premium. These findings are inconsistent with theoretical models predicting that more productive firms are more likely to set pay via bargaining (Doniger 2015; Postel-Vinay and Robin 2004; Flinn and Mullins 2021). The result holds for both binary and continuous measures of bargaining, and is not overturned by machine learning prediction attempts.

Q5. What firm characteristics other than productivity predict bargaining strategies?

CBA coverage is negatively correlated with wage flexibility—CBA-covered firms report less flexibility even for managers who are typically exempt from CBAs and for groups not covered by CBAs, suggesting institutional norms or culture matter. Firms headquartered in East Germany are less likely to bargain with workers in all groups. Publicly traded firms (stock-based corporations) are more likely to set wages flexibly. These correlations are consistent with the view that managerial style and firm culture (rather than productivity) shape wage-setting strategies.

Q6. What does the variance decomposition say about the relative importance of firm versus market factors in predicting bargaining strategies?

Employee-group dummies alone explain 33% of the variation in bargaining strategies for new hires. After adjusting for the number of fixed effects used, four employee-group dummies explain as much variation as more than 500 firm dummies. Adding firm characteristics or coarse industry dummies does not significantly improve the adjusted R-squared relative to a model containing only group dummies. This supports models emphasizing market-level factors (worker replaceability, labor market tightness) over firm-level factors.

Q7. How common is it for workers to provide salary expectations before receiving an initial offer, and what do firms do with this information?

In 57% of worker-firm interactions, the worker provides salary expectations before the firm makes its initial offer. Twenty-nine percent of firms require this information; most ask for it. Forty-four percent of firms report that variation in initial offers is at least as important as subsequent back-and-forth negotiations in determining workers’ final pay. HR professionals and prior research indicate firms interpret variation in stated expectations as reflecting outside options rather than productivity.

Q8. What fraction of outside offers are rejected, and what happens when workers stay at the incumbent firm?

Only 9% of workers who received one or more outside offers in the prior six months chose to move to a new firm. Of the 91% who remained at the incumbent firm, 13% successfully renegotiated their pay at the incumbent. A follow-up survey fielded in spring 2024 corroborates this finding, showing approximately 80% of workers who received an outside offer remained at the incumbent firm; even recoding all job-to-job transitions as accepted offers implies no more than 26% of offers lead to a transition.

Q9. What do the back-and-forth dynamics imply for appropriate theoretical models of wage bargaining?

That many offers are accepted or rejected only after multiple rounds of negotiation is difficult to rationalize with models assuming either firms or workers have perfect information, which typically predict immediate acceptance or rejection. The patterns are consistent with models of two-sided incomplete information (Perry 1986; Chatterjee and Samuelson 1983). Sixty-nine percent of HR professionals in the survey report that decision-makers at their firm only have market-level information on wages, not specific information on what competitors pay.

Q10. How do outside options predict worker bargaining behavior and outcomes, controlling for occupation-establishment fixed effects?

Workers who rated it “easy” or “very easy” to obtain a better outside offer are 9 percentage points more likely to ask for an increase after the initial offer and 7 percentage points more likely to successfully negotiate a raise relative to same-occupation-establishment coworkers who rated it “difficult” or “very difficult.” The same pattern persists during the employment spell: workers with better outside options are 9 percentage points more likely to initiate and 8 percentage points more likely to succeed in renegotiation. These workers are not more likely to receive raises without asking.

Q11. How does risk tolerance predict bargaining, and how does it compare to outside options?

Workers with greater risk tolerance (those rating themselves 7 or above on a 10-point scale) are more likely to engage in wage negotiations and more likely to succeed both at the start of and during employment spells. Gaps in successful negotiations are somewhat larger than gaps in attempted negotiations, suggesting risk-tolerant workers also negotiate more effectively. However, outside options explain more of the between-worker variation in bargaining behavior than risk tolerance does.

Q12. What are the gender differences in bargaining behavior, and can they be explained by differences in outside options or risk tolerance?

Women are less likely to engage in back-and-forth negotiations and are 6 percentage points less likely to successfully negotiate pay upward during an employment spell. Women are also less likely to provide salary expectations and provide lower expectations as a fraction of their current salary in the hypothetical scenario, including when the salary range is provided—women are 6 percentage points less likely to provide expectations above the top of the stated range. Controlling for outside options and risk tolerance shrinks the female coefficient by at most 15%. There is no evidence that women substitute toward negotiating for non-wage amenities. The pattern is most consistent with women finding negotiation uncomfortable, not with a belief that it will not pay off or fear of backlash.

Q13. What is the estimated gender wage gap attributable to individual bargaining?

Among surveyed workers, after controlling for occupation-establishment fixed effects, there is no gender wage gap at firms without individual bargaining (coefficient closes to zero), while a 4–5 percentage point gender wage gap persists at firms with individual bargaining. This difference is robust across measures of pay (total daily pay, base pay, pay conditioning on hours worked), alternative fixed effect specifications, and to including non-surveyed workers at surveyed firms. A simple decomposition suggests 44% of the residual gender pay gap at surveyed firms can be attributed to bargaining. Across the interaction specifications, bargaining firms have a 3 percentage point higher gender wage gap and—in one key specification—a 6 percentage point difference between the gender gaps at bargaining and non-bargaining firms.

Q14. How does a worker’s prior firm wage premium affect current wages, and does bargaining status matter?

In a regression of log current wages on the AKM wage premium of the prior firm (conditional on occupation-establishment fixed effects), a 10 percentage point higher pay premium at the prior firm is associated with 0.5 percent higher pay at the new firm for workers at bargaining firms. For workers whose pay is not set via individual bargaining, the relationship between the prior firm’s pay premium and current pay is statistically insignificant. The result is consistent with the idea that during negotiations with a new firm, workers use their prior firm’s pay policy as an outside option.

Q15. How do AKM person effects relate to bargaining behavior?

Higher-person-effect individuals are more likely to have provided salary expectations when applying to their current firm and ask for a larger fraction of their current salary in the hypothetical scenario (conditional on their wage). These differences persist when controlling for occupation-establishment fixed effects and age and experience. Higher-person-effect workers are not more likely to receive raises without asking. These results are inconsistent with AKM person effects reflecting only productivity differences and instead suggest that fixed differences in individual bargaining behavior contribute to the variance in person effects—which Card, Heining, and Kline (2013) estimated explains a large share (40%) of the growth in German wage inequality.

Q16. Are the bargaining patterns found at surveyed firms representative of bargaining more broadly?

Two robustness exercises support broader representativeness. First, similar bargaining dynamics are found when including a random sample of German workers employed at non-surveyed firms. Second, re-weighting the sample to match the overall distribution of firm size and sector in Germany yields similar results. Because medium and large firms are over-represented in the firm sample, and because small firms hire infrequently and are less likely to have formal bargaining strategies, the true prevalence of individual bargaining among all German firms may be somewhat lower.

Key Concepts

Individual Bargaining Strategy (firm-level). A firm has an individual bargaining strategy if it differentiates pay between workers in the same position that it perceives to have similar productivity. This definition encompasses both tailoring of initial offers (based on, e.g., workers’ stated salary expectations) and back-and-forth negotiation. It is analogous to price discrimination rather than to the standard labor economics distinction between wage posting and Nash bargaining.

Protocol Question. The main survey measure of firm bargaining strategies: firms are asked the maximum percentage by which pay could be increased for a new hire above the fixed compensation the firm would have offered based on qualifications and fit alone, with response bins from “0%/no adjustments” to “more than 40%.” A zero response is used to classify a firm as not bargaining.

Incidence Question. A supplementary survey measure eliciting the expected spread (between highest and lowest offers) that the firm would make to ten candidates with identical qualifications and fit but differing stated salary expectations and competing offers. Used to validate the protocol question and to quantify the importance of initial-offer differentiation relative to back-and-forth negotiation.

Bottleneck Occupation. A firm-defined category of workers in positions that are particularly difficult to fill, drawing on an official German Federal Employment Agency designation. In the paper, bargaining willingness is systematically higher for workers in these positions than for other workers at the same firm, providing evidence that labor market tightness drives bargaining strategies.

Outside Offer Renegotiation. Wage renegotiation at the incumbent firm triggered by a worker receiving an outside offer, without a change in job tasks. The paper documents this is empirically more common than actual job-to-job transitions: of workers receiving outside offers, 91% remain at the incumbent firm, and 13% of those who remain successfully renegotiate their pay.

AKM Person Effect. A worker fixed effect estimated from a two-way fixed effects regression of log wages on worker and firm fixed effects (following Abowd, Kramarz, and Margolis 1999). In this paper, AKM person effects are taken from Bellmann et al. (2020), estimated over 2010–2017 German population data. The paper provides evidence that these effects capture, in part, fixed differences in individual bargaining behavior rather than solely differences in productivity.

AKM Firm Effect (Wage Premium). The firm fixed effect from the same two-way fixed effects regression, representing the pay premium a firm pays relative to what would be expected given its workforce composition. The paper uses the prior firm’s AKM effect as a measure of a worker’s outside option quality when testing whether prior-firm pay policy influences current pay under individual bargaining.

Salary Expectations (Gehaltsvorstellungen). The wage figure a worker provides to a prospective employer, typically before the firm’s initial offer. Legally, German firms (like most US states) cannot ask for salary history but can ask for salary expectations. In the paper, 57% of worker-firm interactions begin with the worker providing expectations; firms report using these to tailor initial offers, interpreting variation in stated expectations as reflecting outside options rather than productivity.

Biased expectations and labor market outcomes: Evidence from German survey data and implications for the East–West wage gap

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

Layer 1 — Overview

Research question. The paper asks two questions: (1) How do workers’ biased expectations about job finding and job separation shape the labor market equilibrium and wages? (2) Are differences in expectation biases across workers a quantitatively important driver of wage differentials, specifically the East–West German wage gap?

Data. The empirical analysis uses the German Socio-Economic Panel (SOEP), a nationally representative longitudinal survey of approximately 30,000 participants per wave. The working-age sample (ages 25–65) covers nine biennial survey waves from 1999 to 2015, yielding 67,772 observations for job separation expectations and 6,423 for job finding expectations. Perceived transition probabilities are reported on a 0–100 scale in steps of 10 percentage points. Actual (statistical) transition probabilities are constructed by estimating probit models that predict realized transitions within 24 months using a rich set of individual, job, and employer characteristics, and are rounded to the nearest decile for consistency with the survey scale.

Main empirical findings. Employed workers in Germany overestimate their job separation probability by 6.4 percentage points on average (perceived: 19.8%; actual: 13.3%), a pessimistic bias significant at the 1% level. Unemployed workers overestimate their job finding probability by 8.2 percentage points on average (perceived: 57.0%; actual: 48.8%), an optimistic bias also significant at the 1% level. The East–West divergence is striking. East German workers exhibit a pessimistic job separation bias of 12.1 percentage points, compared to only 4.7 percentage points in the West, despite broadly similar actual separation rates (15.1% vs. 12.8%). For job finding, West Germans overestimate their probability by 12.9 percentage points, while East Germans overestimate by only 2.0 percentage points — meaning East Germans are also substantially less optimistic about re-employment. These East–West differences survive controls for compositional differences and alternative definitions of job separation (dismissals only; selected reasons; spell-based) and job finding (including those out of the labor force). The biases are stable over the 1999–2015 sample period with no discernible trend. A cohort analysis shows that the excess pessimism in East Germany is concentrated among cohorts who were already in the labor market at the time of German reunification (born in the 1950s and 1960s), consistent with persistent effects of the communist GDR experience. Individuals do not systematically learn over time: mean changes in individual-level absolute deviations between consecutive waves are close to zero. Individual deviations between perceived and actual rates have statistically significant but quantitatively negligible predictive power for subsequent transitions (a 1 pp higher perceived job separation is associated with only a 0.001 pp higher realized separation rate), ruling out private information as a first-order explanation for the biases.

Model. The authors extend the Diamond–Mortensen–Pissarides (DMP) frictional labor market framework by (i) allowing workers to hold biased perceived transition rates (λw for job finding, σw for job separation) while firms have rational expectations, and (ii) introducing wage contracts of explicit length T periods after which parties re-bargain. Common knowledge of each party’s perceived values is assumed, and generalized Nash bargaining is applied. The contract length T is a key parameter: there exists a critical threshold T* such that a pessimistic job separation bias raises the equilibrium wage for T < T* (the continuation-value effect dominates) and lowers it for T ≥ T* (the within-contract discounting effect dominates). An optimistic job finding bias unambiguously raises the equilibrium wage by inflating the perceived value of unemployment and hence the reservation wage.

Quantitative results. The model is calibrated to East Germany. The job separation bias (∆σ = 0.0194) and job finding bias (∆λ = 0.0044) are set to SOEP-based estimates. The critical threshold implied by calibrated parameter values is T* = 10 quarters. The baseline contract length, constructed from the share of permanent (88%) and temporary (12%) contracts in SOEP and average remaining tenure until retirement, is T = 67 quarters (a lower bound). This exceeds T*, so the pessimistic separation bias depresses wages in the baseline. A counterfactual experiment assigns West German bias levels to East German workers, while holding all other parameters fixed. For the preferred calibration range (γ ∈ {0.35, 0.50}, T ∈ {67, 106, 159}), East German wages rise by 1.07 to 2.36 percent. This corresponds to a reduction in the conditional East–West German wage gap (23 percent) of 4.6 to 10.6 percent, and a reduction in the unconditional gap (30 percent) of 3.6 to 7.9 percent. Although wages rise, equilibrium unemployment increases by 0.70 to 1.01 percentage points, widening the already large East–West unemployment gap (approximately 7 percentage points). Net of the unemployment effect, expected lifetime income (computed at actual, unbiased transition rates) rises by 0.7 to 1.88 percent for East German workers under West German biases, implying an unambiguous welfare gain. Under a biennial calibration (robustness), wages increase by up to 3.3 percent and expected lifetime income rises by up to 2.23 percent.

Scope conditions. Results apply to a stationary environment (no aggregate fluctuations). Firms are assumed to have rational expectations; an extension shows results hold provided firm bias is smaller than worker bias. Workers are assumed homogeneous in their bias levels; learning is abstracted from. The quantitative magnitudes are sensitive to the workers’ bargaining power γ and the contract length T, both of which are subject to uncertainty in calibration.

In depth

Q1. How are actual (statistical) transition probabilities constructed, and why are probit-predicted probabilities preferred over realized sample means?

A: Realized transition rates in the sample mix transitions for various idiosyncratic reasons that vary substantially across population groups, so raw sample means do not reflect the probability a given individual faces at interview time. The authors estimate probit models separately for job separation (employed sample) and job finding (unemployed sample), including a rich set of covariates — age, gender, education, tenure, firm size, unemployment experience, industry, survey year, and East Germany indicator, among others — and predict individual-level probabilities at the time of the interview. For consistency with the survey’s discrete response format, probit-predicted probabilities are rounded to the nearest decile (0%, 10%, …, 100%). The bias is computed as the individual-level difference between perceived and probit-predicted actual probabilities, averaged over the sample.

Q2. What is the magnitude and direction of the aggregate expectation biases in Germany?

A: Employed workers overestimate job separation by 6.4 percentage points on average (perceived 19.8% vs. actual 13.3%), a pessimistic bias significant at the 1% level. Unemployed workers overestimate job finding by 8.2 percentage points (perceived 57.0% vs. actual 48.8%), an optimistic bias also significant at the 1% level. Both directions are statistically robust across alternative definitions of separation and finding, as well as to trimming extreme responses (0% and 100% answers) and adjusting for directional rounding.

Q3. How large are the East–West differences in expectation biases, and do they survive controls for compositional differences?

A: East German workers exhibit a pessimistic job separation bias of 12.1 percentage points, more than 2.5 times the West German level of 4.7 percentage points, despite actual separation rates being broadly comparable (15.1% vs. 12.8%). For job finding, West Germans are optimistic by 12.9 percentage points while East Germans are optimistic by only 2.0 percentage points, a difference of 10.9 percentage points. The paper states these differences persist after accounting for compositional differences between regions, and are robust across all alternative definitions of job separation (Dismissals, Selected, Spell) and job finding (out of U or O). The table of robustness results (Table 2) confirms that in all specifications, the pessimistic separation bias is substantially larger in the East and the optimistic finding bias is substantially smaller.

Q4. What cohort analysis is conducted to explore the origins of greater East German pessimism?

A: The authors conduct a regression of the individual-level bias on birth-cohort indicators, controlling for age, demographic, and economic characteristics. They find that the pessimistic job separation bias is most pronounced among cohorts born in the 1950s and 1960s — those who experienced adult working life in the communist GDR and lived through reunification — and is smaller for cohorts born before 1950 and substantially smaller for cohorts born after 1970. For job finding, the optimistic bias is comparably low among cohorts born in the 1960s and earlier, but rises significantly for later-born East German cohorts. This cohort pattern is consistent with a long-lasting “experience effect” of communist institutions and the reunification shock on beliefs, analogous to findings in the broader literature on the persistent effects of communism.

Q5. Is there evidence that individuals update their biased expectations over time?

A: To assess learning, the authors use the panel dimension and compute for each individual in two consecutive survey waves the absolute value of the deviation between perceived and actual transition probabilities, then examine the change in this absolute deviation between waves. The histograms of individual-level changes show substantial dispersion but means close to zero in all four sub-groups (East/West, job separation/finding), indicating no systematic convergence of beliefs toward actual rates. Biases are also stable in the time-series dimension, with perceived and actual rates moving largely in parallel across survey waves from 1999 to 2015, leaving the aggregate bias level roughly constant.

Q6. How does the model rule out private information as an alternative explanation for the biases?

A: If biases reflected private information about idiosyncratic risk not captured by observable characteristics, individual-level deviations between perceived and actual rates should predict subsequent realized transitions. The authors add the individual-level deviation as an additional regressor in the probit transition models. The estimated coefficients are statistically significant and positive, but quantitatively negligible: a 1 percentage point higher expected job separation probability is associated with only a 0.001 percentage point higher realized separation probability, and a 1 percentage point higher expected job finding probability with a 0.002 percentage point higher realized finding probability. These magnitudes are too small to materially alter the interpretation of the biases as reflecting systematic expectation errors rather than private information.

Q7. What is the role of contract length T in the model, and what is the critical threshold T*?

A: The wage contract length T determines which of two opposing effects of pessimistic job separation expectations dominates in bargaining. The first (negative wage) effect: a pessimistic worker discounts future wages within the current contract more heavily than the firm does, so the worker values the contract less and accepts a lower wage. The second (positive wage) effect: a pessimistic worker also discounts the continuation value of future contracts more heavily, making it less attractive to remain in the match, so the firm must offer a higher wage to retain the worker. For short contract lengths (T < T*), the second (positive) effect dominates, so the pessimistic bias raises wages. For long contracts (T ≥ T*), the first (negative) effect dominates, so the pessimistic bias depresses wages. The critical threshold T* is the smallest positive integer such that T*/λw(θ) < β times a weighted sum involving σw and T*. Using calibrated parameter values for East Germany, T* = 10 quarters (2.5 years). The baseline contract length is T = 67 quarters (approximately 16.8 years), well above T*, placing the economy in the regime where pessimism depresses wages.

Q8. How does the optimistic job finding bias affect equilibrium wages and unemployment?

A: An optimistic job finding bias (λw > p(θ)) raises the perceived value of unemployment U because workers expect to escape unemployment sooner. A higher value of unemployment raises the worker’s outside option in bargaining, increases the reservation wage, and thereby pushes up the bargained wage. In general equilibrium, the job creation condition (which is unaffected by worker expectations) is unchanged, so the upward rotation of the wage curve reduces labor market tightness θ, raises equilibrium unemployment, and extends average unemployment duration. This comparative static holds unambiguously for any contract length T.

Q9. What are the quantitative results of the counterfactual experiment assigning West German biases to East German workers?

A: The counterfactual assigns West German bias levels (smaller pessimistic separation bias, larger optimistic finding bias) to East German workers while holding all other parameters at East German calibrated values. For the preferred calibration with γ ∈ {0.35, 0.50} and T ∈ {67, 106, 159}, wages in East Germany rise by 1.07 to 2.36 percent. This implies a reduction in the conditional East–West wage gap (23 percent) of 4.6 to 10.6 percent and a reduction in the unconditional gap (30 percent) of 3.6 to 7.9 percent. Equilibrium unemployment in East Germany rises by 0.70 to 1.01 percentage points as a side effect. Net of the unemployment effect, ex-ante unbiased expected lifetime income rises by 0.7 to 1.88 percent, confirming a positive welfare effect of reducing East German pessimism to West German levels. Under the biennial calibration robustness check, wage increases reach up to 3.3 percent, the conditional wage gap narrows by up to 11 percent, and lifetime income rises by up to 2.23 percent.

Q10. How is the bargaining power parameter γ calibrated and why does it matter for the results?

A: The paper considers a range γ ∈ {0.35, 0.50, 0.65}, rather than a single calibrated value, because γ plays a crucial role in the sensitivity of wages to expectation biases. Lower bargaining power reduces the equilibrium wage directly; however, because lower wages spur job creation, the model requires a higher vacancy cost κ to match the empirical job finding rate, which in turn increases the elasticity of wages with respect to the bias (see the wage equation, which shows that the bias effect scales with κθ/p(θ)). The paper argues that γ = 0.65 is inconsistent with the empirical wage–bias relationship estimated in SOEP data (which is negative and about twice as negative in East Germany as in the West), while γ ∈ {0.35, 0.50} is consistent. Lower bargaining power is also argued to be realistic for East Germany given weaker union representation there relative to the West.

Q11. How does the empirical relationship between the job separation bias and wages serve as a model validation target?

A: Using SOEP data, the authors regress log hourly wages on the individual-level difference between perceived and actual job separation rates, controlling for individual fixed effects and other covariates, and allow the slope to differ between East and West Germany. They find a statistically significant and negative relationship in both regions, with the effect approximately twice as large in East Germany as in the West. The estimate implies that if East German workers’ job separation pessimism were reduced to West German levels, hourly wages in the East would be about 1 percent higher. This empirical gradient is used as an external validation check — not a calibration target — to assess which combinations of (γ, T) in the model are quantitatively plausible.

Q12. What does the model predict about the general equilibrium effects on unemployment from reducing East German pessimism?

A: Reducing East German pessimism — both the pessimistic separation bias and the low optimistic finding bias — shifts the wage curve upward in equilibrium. Because the job creation condition is unaffected by worker beliefs (firms have rational expectations), higher wages reduce the firm’s incentive to post vacancies, lowering labor market tightness θ. This leads to higher equilibrium unemployment and longer average unemployment duration. The counterfactual with West German biases implies that East German unemployment would rise by 0.70 to 1.01 percentage points, further widening the approximately 7 percentage point East–West unemployment gap. The authors note this is a welfare-relevant trade-off, but show that the wage gain dominates the unemployment cost in terms of expected lifetime income.

Q13. What robustness checks are performed on the quantitative results?

A: The paper considers (i) a narrower definition of job separation (dismissals only) to match the most likely interpretation of the survey question; (ii) targeting the officially reported East German unemployment rate (14.5% average from the Federal Employment Agency) rather than the SOEP-implied rate of 8.6% as a calibration target; (iii) a biennial calibration frequency instead of quarterly. The main results — wage increases and narrowing of the wage gap — are quantitatively similar across these alternatives, with one exception: the biennial calibration yields substantially larger wage increases (up to 3.3%), a larger reduction in the conditional wage gap (up to 11%), and larger lifetime income gains (up to 2.23%).

Key Concepts

Expectation bias (job separation / job finding). In this paper, a bias in expectations is defined as a systematic average difference between an individual’s perceived transition probability and the actual (statistically predicted) transition probability for their demographic and job group. A pessimistic job separation bias means workers overestimate the probability of losing their job (σw > σ); an optimistic job finding bias means unemployed workers overestimate the probability of re-employment (λw > p(θ)). Biases are not attributed to private information but to systematic expectation errors.

Actual (statistical) transition probability. The paper defines actual transition probabilities not as raw sample transition rates but as individual-level predicted probabilities from probit models estimated on realized transitions within 24 months, conditional on a comprehensive set of individual, job, and employer characteristics observed at interview time. These are rounded to the nearest decile for comparability with the survey’s discrete response format.

Wage contract length (T). The contract length T is the number of periods for which a bargained wage is fixed before the match parties re-bargain. A job match consists of a sequence of consecutive wage contracts of length T. The paper departs from the standard DMP assumption of period-by-period bargaining (T = 1) and shows that T is central to how job separation expectations feed into the bargained wage. A permanent job approximates T → ∞.

Critical contract length (T).* A theoretically derived threshold: the pessimistic job separation bias raises equilibrium wages for contract lengths T < T* and depresses wages for T ≥ T*. Specifically, T* is the smallest positive integer such that T*/λw(θ) < β times a weighted sum involving β, σw, and T*. In the East German calibration, T* = 10 quarters.

Generalized Nash bargaining with common knowledge / agree to disagree. The model assumes that both the worker and the firm know each other’s perceived values of the job match and outside options and accept them as the basis for bargaining, even though they differ. Workers use their biased perceived transition rates to value employment and unemployment; firms use actual rates. There is no private information. The paper refers to this as workers and firms “agreeing to disagree.”

Ex-ante unbiased expected lifetime income (EI_{W,U}). A welfare measure defined as the present discounted value of income for an individual entering the economy, computed at actual (unbiased) job separation and job finding probabilities rather than at workers’ perceived (biased) rates. This measure captures the net welfare effect of changing expectation biases because it correctly accounts for actual employment transitions, even though the behavioral responses in equilibrium are driven by biased perceptions.

Effective discount factor (β(1 − σw)). When a worker holds pessimistic job separation expectations, future payoffs within the current contract are discounted not at the pure time discount factor β but at β(1 − σw), which is smaller when σw is larger. A more pessimistic worker therefore effectively discounts future wage payments more steeply, and this differential discounting relative to the firm (which uses β(1 − σ)) is the key mechanism generating the contract-length dependence of the wage effect.

Downward Rigidity in the Wage for New Hires

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

Layer 1 — Summary

Hazell and Taska use wages posted on online job vacancies — matched to job titles and establishment identifiers from Burning Glass Technologies — to measure the wage for new hires at the job level (same job title and establishment) over 2010Q1–2020Q2. They find that this measure of the wage for new hires is rigid downward and flexible upward. At the job level, the nominal posted wage changes infrequently — on average once every 5–6 quarters — and conditional on changing, is four times more likely to rise than to fall. In the cyclical dimension, job-level posted wages rise strongly when state unemployment falls but do not fall when state unemployment rises; real wages exhibit the same asymmetric pattern. These results do not appear in the average wage for new hires (which aggregates across all job types), because time-varying job composition inflates the variance of average wages and raises standard errors roughly twentyfold relative to job-level regressions — explaining why prior work using worker-level survey data found no evidence of downward rigidity. A Heckman (1979) selection correction for firms’ selection into vacancy posting suggests that selection bias in the job-level regression is moderate. The findings provide direct empirical support for models in which downward wage rigidity for new hires — specifically at the job level — amplifies unemployment fluctuations and generates asymmetric unemployment dynamics.

In depth

Q1. Q: What is the central empirical claim of the paper?

A: At the job level — defined as the same job title within the same establishment — the wage posted for new hires is rigid downward and flexible upward. It changes infrequently and, conditional on changing, rises far more often than it falls; and it responds to falls in unemployment but not to rises in unemployment.

Q2. Q: What data does the paper use, and what defines a “job”?

A: The paper uses the Burning Glass Technologies dataset of wages posted on online vacancies, covering January 2010 to June 2020. A “job” is a job title within an establishment whose wages are paid at a given frequency (e.g., hourly or annual). The data come from the near-universe of online job postings — roughly 40,000 sources — and the main regression sample consists of jobs that post wages, have job title and establishment information, and post vacancies in multiple quarters, yielding approximately 3.05 million vacancies, representing about 0.8% of total US vacancies.

Q3. Q: How do the authors validate that posted wages measure the wage for new hires?

A: They construct a measure of the wage for new hires from the Current Population Survey (CPS) — workers switching jobs or entering from unemployment — at the state, industry, and occupation level. Regressing log CPS wages on log Burning Glass wages (using an IV split-sample procedure to correct for attenuation bias) yields a coefficient close to 1 across specifications and levels of aggregation, indicating that average posted wages move roughly one-for-one with average wages for new hires in representative survey data.

Q4. Q: How is the frequency of wage change estimated?

A: Because wages are not observed in quarters without a vacancy posting, the authors adapt a constant-hazard model from the price-setting literature (following Nakamura–Steinsson and Klenow–Kryvtsov). The latent wage evolves stochastically between postings; the observed wage is treated as a draw from this process. The quarterly probability of wage change is estimated at 0.17–0.19 across specifications, implying implied durations of unchanged wages of 4–5 quarters.

Q5. Q: What is the asymmetry in the direction of wage changes?

A: In the unweighted baseline, the quarterly probability of a wage decrease is 0.04, whereas the probability of a wage increase is 0.12 — roughly a three-to-one ratio in probabilities, summarized in the paper’s abstract as wages being “four times more likely to rise than to fall.” The distribution of non-zero wage changes also shows a pronounced pile-up of small positive changes relative to small negative changes, consistent with a downward constraint on wage setting.

Q6. Q: What is the first piece of cyclical evidence for downward rigidity?

A: A binned scatterplot (Figure 1) of job-level wage growth against state-level quarterly changes in unemployment shows a strong, roughly linear relationship when unemployment is falling — wages rise with falls in unemployment, both for small and large declines. When unemployment rises, however, wages do not fall — neither for small nor for large increases in unemployment. This asymmetry is robust to regression-based analysis and to identified labor demand shocks.

Q7. Q: Are real wages also rigid downward?

A: Yes. The paper reports that real wages (nominal posted wages deflated) are also rigid downward and flexible upward, mirroring the pattern for nominal wages.

Q8. Q: What is the job-composition problem, and why does it matter?

A: The average wage for new hires — the object measured in most prior work — aggregates across all job types that are actively hiring. If the composition of jobs hiring shifts over the business cycle (e.g., the share of lower-wage jobs rises in recessions), then average wages can fall even if no individual job cuts its wage, and can stay flat or rise even if every job cuts its wage. Job composition therefore confounds cyclicality estimates based on average wages. By tracking the same job title at the same establishment across successive vacancies, the authors purge wage changes driven by shifting composition.

Q9. Q: Why did prior work find no evidence of downward rigidity for new hires?

A: Prior work used worker-level survey data (e.g., Bils 1985; Pissarides 2009 survey) that controls for worker characteristics but averages across jobs — the average wage for new hires. The volatility of job composition inflates the variance of this average measure. In the Burning Glass data, standard errors from regressions using average wages are roughly twenty times larger than those from job-level regressions, making it impossible to detect downward rigidity even if it exists. Point estimates in prior work suggested procyclicality but were too imprecise to exclude downward rigidity.

Q10. Q: How does this paper relate to Gertler, Huckfeldt, and Trigari (2020) and Grigsby, Hurst, and Yildirmaz (2021)?

A: Both papers attempt to control for job composition at the worker level. Gertler et al. focus on wages of workers hired from unemployment (less affected by composition than all new hires) and find weakly procyclical wages. Grigsby et al. use rich payroll data and worker-level matching to control for composition and also find weakly procyclical wages. The present paper complements these by using job-level data that directly purges composition without relying on worker characteristics, and adds evidence on the asymmetry of rigidity (not just average procyclicality).

Q11. Q: What is the role of the Heckman selection correction?

A: If firms select into vacancy posting depending on business-cycle conditions, the sample of observed posted wages may be non-random, biasing job-level wage-cyclicality estimates. The authors implement a standard Heckman (1979) two-step selection correction. The correction suggests that selection bias in the job-level regression is moderate — it does not overturn the finding of downward rigidity.

Q12. Q: What are the four main caveats the authors acknowledge?

A: (1) The main sample is small — 0.8% of US vacancies — though the authors show it is broadly representative on observables and that wages track representative survey data. (2) The paper measures rigidity only for jobs that post wages; jobs that do not post wages might be more flexible, though the share of vacancies posting wages does not decline during contractions. (3) Posted wages may differ from realized (bargained) wages; however, wages are rigid even in occupations where bargaining is uncommon. (4) The Pandemic Recession is the main contractionary episode in the sample, and it involved labor supply shocks as well as demand shocks; the authors address this through identified labor demand shock regressions and by ending the sample in June 2020.

Q13. Q: What are the implications for models of unemployment fluctuations?

A: In the Diamond–Mortensen–Pissarides search model, Pissarides (2009) emphasizes that the wage for newly hired workers — not continuing workers — is the relevant margin for unemployment fluctuations. Shimer (2005) showed the standard calibration produces too-small unemployment fluctuations; wage rigidity for new hires can resolve this. The paper’s finding of downward-but-not-upward rigidity additionally supports models (e.g., Dupraz, Nakamura, and Steinsson, 2020) in which this asymmetry generates asymmetric unemployment dynamics — unemployment rises sharply in contractions but falls more slowly in expansions.

Q14. Q: How do wages for new hires compare with wages for continuing workers in terms of rigidity?

A: The paper finds approximate parity. The implied duration of unchanged wages from the job-level posted wage data (4–5 quarters) is similar to estimates for continuing workers in the prior literature. This is perhaps surprising because wages could in principle be more flexible for new hires than continuing workers — firms might cut wages for new hires even while insuring continuing workers (Beaudry and DiNardo, 1991). The results instead suggest that internal equity concerns (Bewley, 2002) or other forces produce similar rigidity for both groups.

Key Concepts

Job level wage: The wage across successive vacancies posted by the same job title at the same establishment. This is the unit of observation in the paper’s main analysis and the object for which downward rigidity is documented. Distinct from the average wage for new hires (which aggregates across all job types).

Downward rigidity (as used in this paper): An empirical pattern in which wages at the job level do not fall during contractions — they do not respond to rising unemployment — while rising during expansions in response to falling unemployment. The claim is descriptive: the data show wages do not fall; the paper does not structurally identify the mechanism enforcing this floor.

Job composition problem: The bias introduced when measuring cyclicality of the average wage for new hires using data that aggregates across different types of jobs. If the mix of job types hiring shifts with the business cycle, average wages can change even when no individual job changes its wage, and can mask individual-job wage changes. Job-level data resolve this by holding the job fixed.

Burning Glass Technologies dataset: A database of wages posted on online job vacancies, drawn from approximately 40,000 online sources (job boards and company websites), covering the near-universe of US online vacancies. The paper’s main regression sample uses the subset with posted wages, job title, establishment identifiers, and multiple quarters of postings, spanning January 2010 to June 2020.

Constant hazard model (wage change frequency): An estimation procedure adapted from the price-setting literature to recover the quarterly probability of wage change from a dataset in which wages are only observed when a vacancy is posted. The latent wage evolves with a constant hazard of change between observations; observed wage changes identify the hazard rates for increases and decreases separately.

Average wage for new hires: The mean wage across all workers newly entering employment (or across all new-hire jobs), used in prior work (Bils 1985 and related). Does not control for job composition. Shown in this paper to exhibit no detectable downward rigidity, with standard errors roughly twenty times larger than in job-level specifications — because job composition variance inflates the residual variance.

Heckman selection correction: A two-step procedure (Heckman 1979) to correct for the possibility that firms that post vacancies — and post wages — are a selected sample that differs systematically across the business cycle. The paper applies this to assess whether selection into vacancy posting biases the job-level wage-cyclicality estimates; the correction suggests bias is moderate.

Summary based on LSE Research Online accepted version (accepted manuscript, covers full paper including introduction, data, and Section 3; extraction terminated at line 595 before Sections 4–5). AI-assisted, human review pending.

Education and the Margins of Cyclical Adjustment in the Labor Market

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

Overview

Research question. This paper asks how the cyclical sensitivity of wages varies with workers’ educational attainment, what mechanisms drive the differences, and what the welfare consequences are of ignoring this heterogeneity. The starting point is a well-known asymmetry: less-educated workers have much higher and more volatile job separation rates, yet the standard macroeconomic literature has treated wages as roughly acyclical for a representative worker. Doniger asks whether this employment-centric picture is incomplete—and finds that it is, in a direction opposite to what the employment pattern would suggest.

Data and methodology. The paper uses two primary data sources: the National Longitudinal Survey of Youth 1979 (NLSY), which provides detailed job histories enabling identification of current and completed employer tenure, and the Current Population Survey (CPS) from 1995 to 2020, used both for employment flow statistics and, via biennial Job Tenure Supplements, for replication of the main wage findings. The sample is restricted throughout to males with 0–30 years of potential experience, following the conventions of the user-cost-of-labor (UCL) literature (Kudlyak, 2014; Basu and House, 2016). Workers are grouped into three educational categories: less than high school, high school or some college, and bachelor’s degree or more.

A key methodological contribution is a new, more parsimonious estimator for the cyclical sensitivity of the UCL. Rather than the multi-step indicator-variable approach of Kudlyak (2014), the paper recovers the UCL sensitivity from interaction terms between a flexible function of tenure and the cyclical position at the time of hiring, estimated within an augmented Mincer regression. This estimator admits higher-frequency identification, enables transparent inference via the delta method, and facilitates nonparametric impulse response estimation via the Jorda (2005) local projection method. Cyclical position is measured primarily as the deviation of the unemployment rate from an HP-filtered trend (lambda = 100,000), with robustness checks using the Hamilton (2018) filter and GDP-based detrending.

Main findings — employment. Monthly separation rates from the CPS (1995–2020) show that workers with less than a high school degree separate at a rate of 9.4 percent per month, more than twice the 3.4 percent rate for workers with a bachelor’s degree or more, regardless of cyclical position. The volatility of the separation rate (measured by the time-series standard deviation) is also larger for the least educated (1.7) than for the most educated (0.6). All sub-components of separation-to unemployment, to inactivity, and job-to-job transitions-exhibit the same ordering. In response to a 100 basis point monetary policy contraction (Romer and Romer, 2004 shocks), employment of workers with less than a high school education falls significantly, while employment of college graduates or more is statistically unaffected.

Main findings — wages. Using the NLSY, the cyclical sensitivity of the UCL to a 1 percentage point deviation of the unemployment rate from trend is estimated at approximately −15.5 percent for workers with a bachelor’s degree or more, −4.9 percent for high school or some college workers, and −1.4 percent (statistically indistinguishable from zero) for workers without a high school degree. In contrast, average hourly earnings (AHE) show much smaller and more compressed differences across education groups (−1.4, −1.1, and −1.0 percent respectively). The pattern of increasing procyclicality with education holds for new hires’ wages (NHW) as well but is considerably less stark than for the UCL. Replication in the CPS confirms the ordering: UCL sensitivities are −7.0 percent for college graduates, −2.9 percent for high school or some college, and effectively zero for those without a high school degree.

Mechanism. Counterfactual decompositions show that differences in the cyclical sensitivity of the wage-tenure profile—not just differences in job duration (separation rates)-account for the vast majority of the divergence across education groups. When separation rates are held constant across groups, the UCL sensitivity of the college-educated falls from -15.5 to −13.0 percent; when wage-tenure profile sensitivities are held constant, it falls to −6.3 percent, and the ordering across groups largely disappears. This finding is consistent with implicit contracting theory (Thomas and Worrall, 1988): longer expected employment durations for the more educated make it optimal to defer a greater share of the wage response to shocks over time, rendering near-term rigidities functionally less binding and producing more persistent effects of hiring-period conditions on subsequent wages.

Robustness. After controlling for cyclical sorting in match quality using the Hagedorn and Manovskii (2013) proxies (cumulated market tightness during tenure and leading up to the present job), the UCL sensitivity for college graduates falls modestly to −12.4 percent, confirming that match-quality composition effects account for only a minority of the documented pattern. The monetary policy shock analysis (Romer-Romer shocks identified from Greenbook forecast errors) yields a 35 percent decrease in the UCL for the most educated at the two-year horizon following a 100 basis point contraction, with no discernible effect for the least educated.

Welfare consequences. Using a stylized New Keynesian model extended to two labor varieties with heterogeneous wage flexibility, the paper shows that ignoring the documented heterogeneity leads to underestimating the welfare costs of business cycle fluctuations by more than 15 percent under the baseline calibration (unit Frisch elasticity and unit elasticity of intertemporal substitution). Conditional on this model, the welfare loss due to fluctuations for the least educated is more than 15 times larger than for the most educated. The paper explicitly notes this is a conservative lower bound, because the model assumes pooled household consumption, and admitting idiosyncratic consumption risk would disproportionately burden less-educated workers who bear adjustment on the extensive (employment) rather than intensive (wage) margin.

In depth

Q1. What is the user cost of labor (UCL), and why does the paper use it rather than average hourly earnings or new hires’ wages?

The UCL, formalized by Kudlyak (2014), is the present discounted value of wage payments an employer expects to make to a worker over the duration of the employment relationship, net of the continuation value of retaining that worker. It equals the new hire’s wage plus the expected wage wedge—the discounted stream of future wage differences between workers hired in the current period versus workers hired one period later. Unlike average hourly earnings or new hires’ wages, the UCL captures the persistent effects of macroeconomic conditions at the time of hiring on all future remitted wages, making it the appropriate allocative wage concept from a macroeconomic standpoint. The paper documents that AHE understates the cyclicality of wages for all groups but especially for the most educated, because AHE omits the highly cyclically sensitive expected wage wedge that characterizes college-educated employment relationships.

Q2. How does the paper’s new estimator for the cyclical sensitivity of the UCL differ from the existing method, and what does this enable?

The existing Kudlyak (2014)/Basu and House (2016) method recovers the UCL by estimating a very large set of date-of-hire x current-date indicator interactions, constructing a time series of the UCL, and then analyzing that series—a multi-step procedure that loses covariances across steps and makes cross-sectional disaggregation or high-frequency identification impractical. The new method instead estimates the UCL sensitivity directly from coefficients on the interaction between a flexible tenure function and the cyclical position at hiring, estimated within a single augmented Mincer regression. The UCL semi-elasticity is recovered analytically from these coefficients via a formula that sums discounted weighted differences in the tenure-interaction coefficients across the tenure horizon. This single-step approach allows transparent inference via the delta method, enables fully interacted specifications for heterogeneous subgroups, permits the hiring-date frequency (e.g., weekly in NLSY) to differ from the wage observation frequency (annual or biannual), and permits estimation from repeated cross-sections—all of which were infeasible in the prior approach.

Q3. What are the quantitative magnitudes of the education gradient in UCL cyclicality, and how do they compare across wage measures?

Using the NLSY with unemployment deviations from HP-filtered trend as the cyclical indicator: the UCL sensitivity is −15.5 percent (se 3.86) for workers with a bachelor’s degree or more, −4.9 percent (se 1.52) for high school or some college, and −1.4 percent (se 2.48, statistically insignificant) for those without a high school degree. By contrast, new hires’ wages show sensitivities of −3.4, −1.8, and −1.2 percent respectively, and average hourly earnings show −1.4, −1.1, and −1.0 percent. The gradient is largest and most statistically significant for the UCL, indicating that the bulk of the education gap in cyclical wage sensitivity operates through the persistent effect of hiring-period conditions on subsequent wages rather than through the contemporaneous wage alone.

Q4. What mechanism accounts for the UCL gradient — differential job durations or differential sensitivity of the wage-tenure profile?

The paper decomposes the UCL into the new hire’s wage and the expected wage wedge, and performs counterfactual exercises holding either separation rates or wage-tenure profile sensitivities constant across education groups (Table 3). Holding separation rates constant while allowing wage-tenure profiles to differ reduces the college-educated UCL sensitivity only modestly, from -15.5 to −13.0 percent; holding wage-tenure profile sensitivities constant while allowing separation rates to differ reduces the college-educated sensitivity to −6.3 percent and compresses the education gradient substantially. Thus, differential sensitivity of the wage-tenure profile—the degree to which wages continue to respond to hiring-period conditions over the course of the job-is the primary driver of the UCL gradient, with differential separation rates playing a secondary but non-trivial role. This finding confirms the prediction of Thomas and Worrall (1988) that lower separation rates support greater use of deferred payment and intertemporal risk sharing in optimal wage contracts.

Q5. How does the paper rule out cyclical sorting in match quality as the explanation for the UCL gradient?

Workers hired during recessions may be of systematically lower match quality, producing persistently lower wages not because wages are more cyclically sensitive for the same quality match but because recession hires are worse matches. Using the Hagedorn and Manovskii (2013) proxies for match quality - cumulated market tightness during the worker’s tenure on the present job (mjob) and on all prior jobs leading to it (mctj) - the paper augments the wage regression with full interactions between these proxies and the tenure-cyclicality terms. After controlling for match quality, the UCL sensitivity for college graduates falls from -15.5 to −12.4 percent (se 5.56); the point estimate remains large, statistically significant, and well above the estimates for lower-education groups. Figure 4 shows that match-quality adjustment primarily affects the first two years of the wage-tenure profile, after which the bias from cyclical sorting fades, confirming that scarring in remuneration for college graduates hired in recessions persists beyond what sorting can explain.

Q6. What do monetary policy shocks reveal about the education gradient in wage sensitivity?

Monetary policy shocks (identified from Greenbook forecast errors as in Romer and Romer, 2004) subject all labor markets to the same aggregate demand shock simultaneously, providing a cleaner test of differential responsiveness than cyclical regressions that may conflate demand composition and supply factors. Using Jorda (2005) local projections, a 100 basis point monetary policy contraction is associated with a 35 percent decrease in the UCL for workers with a bachelor’s degree or more at the two-year horizon, with statistically insignificant effects on the UCL of workers without a high school degree. The employment results are symmetric: less-educated workers’ employment falls significantly after a monetary contraction, while college-educated workers’ employment is unaffected. This cross-validation using monetary policy shocks supports the main thesis that more-educated workers absorb aggregate demand variation through the wage margin, while less-educated workers absorb it through the employment margin.

Q7. How does acyclical wages for the least educated affect interpretation of the existing macro literature on wage rigidity?

The aggregate finding of Kudlyak (2014) and Basu and House (2016)-that the UCL is more procyclical than new hires’ wages or average hourly earnings, casting doubt on wage rigidity as an amplification mechanism—holds only for educated workers. The paper finds that the UCL for workers without a high school degree is statistically acyclical by all three wage measures. This result restores a potential role for nominal wage rigidity in generating amplification and persistence of shocks for less-educated labor markets, including in the Diamond-Mortensen-Pisarides class of search models criticized by Kudlyak (2014) and in New Keynesian models criticized by Basu and House (2016). The paper therefore reconciles the literature on wage rigidity with the empirical finding of cyclical employment volatility concentrated among the less educated.

Q8. What is the welfare calculation, and what are its key results and limitations?

The welfare exercise uses a parsimonious New Keynesian model with two labor varieties (capturing more- and less-educated workers) and price and wage rigidities. The model is extended to admit heterogeneous wage flexibility, and the welfare costs of fluctuations are evaluated following the second-order approximation method of Gali et al. (2007). Under the baseline calibration (unit Frisch elasticity, unit elasticity of intertemporal substitution), the heterogeneous-worker economy incurs welfare costs of fluctuations that exceed those of the output-gap-equivalent representative agent economy by more than 15 percent. The welfare loss of the least-educated workers is more than 15 times that of the most educated. The paper explicitly characterizes this as a conservative lower bound: the model assumes pooled household consumption (within varieties), which implies equal consumption sensitivity across education groups, whereas in reality less-educated workers face income loss on the extensive margin without the wage smoothing available to the more educated. Relaxing this assumption, as in Krusell et al. (2009), could yield welfare losses an order of magnitude larger.

Q9. What does the CPS replication add, and what are its limitations relative to the NLSY baseline?

The CPS replication (Table 7) confirms the main ordering: UCL sensitivities are −7.0, −2.9, and approximately 0 percent for college graduates, high school or some college, and less than high school respectively. This rules out the concern that the NLSY findings are artifacts of the single aging cohort that characterizes the NLSY 1979. However, the CPS must be treated as a repeated cross-section because the tenure data are only available biennially and individual-level panel linkage across tenure supplement waves is infeasible. As a result, the CPS estimates cannot include individual fixed effects and must rely more heavily on observable controls (industry, occupation) to absorb cyclical variation in workforce composition. The CPS also precludes the match-quality controls of Hagedorn and Manovskii (2013). Despite these limitations, the main qualitative and directional findings replicate.

Q10. What policy implications does the paper draw for monetary policy?

The paper argues that because less-educated workers bear adjustment to aggregate demand shocks disproportionately through the employment margin while their wages are acyclical, welfare assessments that focus on the aggregate output gap underweight the costs borne by less-educated workers. The paper suggests that re-optimizing the monetary policy rule to account for documented heterogeneity would entail placing greater weight on the unemployment rate of the least-educated when measuring the output gap. More broadly, the K-shaped nature of labor market adjustment across education groups — wage scarring for the educated versus employment volatility for the less educated - implies that policies targeting either margin in isolation will miss welfare costs concentrated in the other group.

Key Concepts

User Cost of Labor (UCL). The allocative wage from the employer’s perspective, defined as the present discounted value of expected future wage payments to a worker hired at date t, net of the continuation value of retaining that worker in the next period. Formally, UCL_t = w_{t,t} + E_t[sum beta^j(1-s)^j (w_{t+j,t} - w_{t+j,t+1})], decomposing into the new hire’s wage and the expected wage wedge. In this paper’s usage, the UCL is the appropriate measure of the cyclical impact of shocks on labor costs because it captures persistent effects of hiring-period conditions on the entire subsequent wage sequence, not just the contemporaneous wage.

Expected Wage Wedge (EWW). The component of the UCL beyond the new hire’s wage: the discounted stream of differences between wages a worker hired at date t will receive in future periods and the wages a worker hired one period later would receive in those same future periods. The EWW is non-zero whenever wages are history-dependent - i.e., whenever current macroeconomic conditions at the time of hiring affect future remitted wages. The paper finds that the EWW is larger, more negative, and more persistent for more-educated workers conditional on being hired during a cyclical downturn.

Self-enforcing implicit wage contract. A labor contract in which the sequence of remitted wages is not pinned down period-by-period by spot-market forces but instead reflects an intertemporal risk-sharing arrangement between employer and worker that is sustained by the mutual benefit of the ongoing employment relationship. In this paper’s framework (drawing on Thomas and Worrall, 1988), lower separation rates make longer planning horizons feasible, which in turn expands the scope for deferring wage adjustments across time - effectively allowing more-educated workers and their employers to smooth the effects of cyclical shocks over longer horizons than is possible for less-educated workers with shorter expected job durations.

Cyclical sorting / match quality bias. The compositional concern that workers hired during recessions may be of systematically different (in this context, lower) match quality than those hired during booms, so that the persistent wage depression observed for recession hires could reflect poor match quality rather than cyclically sensitive wages for equivalent-quality matches. The paper uses the Hagedorn and Manovskii (2013) proxies - cumulated labor market tightness during the current job and prior employment history - to control for cyclical variation in match quality and assess the residual sensitivity of the UCL for average-quality matches.

Extensive versus intensive margin of labor market adjustment. The distinction between adjustment through changes in the number of workers employed (extensive margin: hiring and separation) versus adjustment through changes in wages or hours conditional on employment (intensive margin). A central finding of the paper is that less-educated workers bear cyclical adjustment disproportionately on the extensive margin (more volatile separation rates, employment losses following monetary contractions) while their wages are acyclical, whereas more-educated workers exhibit the reverse: stable employment but highly cyclically sensitive wages, especially as measured by the UCL.

Wage scarring. The persistent negative effect of hiring-period macroeconomic conditions on wages throughout the subsequent employment spell, beyond what is explained by contemporaneous market conditions. In this paper’s context, wage scarring is concentrated among more-educated workers: being hired when the unemployment rate is one percentage point above trend is associated with wages that remain depressed for several years, with the depression being larger and more persistent for college-educated workers than for those with less education. This is demonstrated via the expected wage wedge profiles in Figure 3 and is confirmed to survive controls for match-quality sorting.

Output-gap-equivalent representative agent economy. A conceptual benchmark constructed in the paper’s welfare analysis: a single-worker-type New Keynesian economy whose wage and labor supply elasticities are set equal to the output-elasticity-weighted averages of the two labor variety types in the heterogeneous economy. The paper shows that the heterogeneous-worker economy and this representative-agent benchmark produce identical aggregate output gap and price level paths (under Cobb-Douglas production, earnings elasticities are identical across varieties), but welfare diverges because period utility is more volatile for the variety with more rigid wages. The 15 percent excess welfare cost of the heterogeneous economy relative to this benchmark is the paper’s headline welfare result.

Efficiency Criteria, Income Taxation, and Heterogeneous Elasticities

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

Overview

Research Question. Can income tax schedules be justified as utilitarian-optimal without adopting extreme normative assumptions about how household welfare should be measured? The paper proposes a welfare criterion strictly stronger than Pareto efficiency—called rationalizability with bounded curvature—and asks whether observed US income taxes satisfy it.

Starting Point. Any Pareto-efficient nonlinear income tax schedule can, in principle, be rationalized as utilitarian-optimal under some cardinalization of household utilities (i.e., some choice of how to measure the cardinal scale of each household’s well-being). However, the paper shows that rationalizing Pareto-efficient taxes in this way often requires cardinalizations under which there is no population upper bound on the curvature of utility with respect to consumption. Equivalently, a utilitarian planner’s marginal willingness to transfer resources to households must fall arbitrarily quickly with the size of those transfers—an extreme form of status quo bias violated by virtually all quantitative optimal-tax exercises.

The Proposed Criterion. The authors restrict attention to cardinalizations with locally bounded curvature: there exists a finite (though potentially arbitrarily large) upper bound on the coefficient of relative risk aversion across the population. This admits two interpretations: (i) ex post, it requires that the social value of transfers not change arbitrarily quickly with transfer size; (ii) ex ante, it corresponds to a decision-maker behind a veil of ignorance with bounded risk aversion.

Main Theoretical Result. Within a standard Mirrlees model of nonlinear income taxation with arbitrary preference heterogeneity and intensive-margin labor supply, the paper proves that a tax schedule can be rationalized with bounded curvature if and only if government revenues are both decreasing and concave (not merely decreasing) with respect to a class of narrowly targeted “two-bracket” reforms—reforms that raise retention by $1 local to some income level $z$ and zero elsewhere. This contrasts with Pareto efficiency, which requires only that revenues be decreasing in these reforms (Bierbrauer, Boyer, and Hansen 2023). The additional requirement of revenue concavity is what distinguishes the bounded-curvature criterion from pure Pareto efficiency.

Sufficient Statistics. The paper derives explicit sufficient-statistics expressions for the first- and second-order derivatives of tax revenue with respect to these targeted reforms. The second derivative depends on higher moments of the elasticity distribution, specifically the income-conditional variance of compensated elasticities of taxable income (ETIs). Revenue convexity—which causes the second-order condition to fail—arises when income-conditional ETI variance is sufficiently high, even holding the mean ETI fixed. The economic mechanism is a “sort-and-extort” dynamic: a small tax reform sorts higher-elasticity households into income brackets where marginal taxes fall and lower-elasticity households into brackets where marginal taxes rise; repeating the reform then exploits this sorting by differentially taxing households by elasticity, as if applying group-specific tax schedules within a uniform income tax.

Empirical Findings. Using the NBER panel of US tax returns from 1979 to 1990, the paper estimates income-conditional mean ETIs of approximately 0.2–0.3 at most income levels. Crucially, it estimates a lower bound on income-conditional ETI variance by comparing elasticities of light versus heavy itemizers (defined by whether a household claims above or below the mean value of deductions in its income bracket). The low-elasticity group has an ETI of approximately zero and the high-elasticity group has an ETI of approximately one, implying a lower bound on ETI variance of roughly 0.2 at most incomes and approximately 0.25 at the top of the distribution. This lower bound is close to—and under plausible assumptions above—the threshold required for the second-order condition to fail. The authors conclude that the US income tax schedule in 1990 was likely Pareto efficient but likely not rationalizable with bounded curvature.

Quantitative Welfare Gains. In a calibrated model with a 50% top marginal tax rate, Pareto-tail shape of 2.5, mean ETI of 0.3, and ETI standard deviation of 0.75 (50% above the estimated lower bound), the planner gains significant welfare from either raising or lowering top marginal taxes. The welfare-maximizing top rate below the baseline is 13.3%, generating social value equivalent to a transfer of $1,966 per top earner. The welfare-maximizing top rate above the baseline is 71.2%, generating social value equivalent to a transfer of $972 per top earner. The revenue-maximizing rate is 80.9% under the baseline calibration, ranging from 74.6% to 86.8% as ETI standard deviation varies by ±25% of the lower bound.

Scope Conditions. The theoretical analysis is restricted to intensive-margin labor supply (abstracting from extensive-margin decisions); the empirical application focuses on top incomes where extensive-margin effects are likely small. The empirical period is 1979–1990, covering major federal and state tax reforms. Results concern local efficiency of the tax schedule, not global optimization.

In depth

Q1. What exactly is “rationalizability with bounded curvature” and how does it differ from Pareto efficiency?

A: Pareto efficiency requires that no small reform makes someone better off without making anyone worse off. Rationalizability (with any cardinalization) is equivalent to Pareto efficiency in this setting. Rationalizability with bounded curvature additionally restricts the cardinalization: there must exist a finite upper bound on the coefficient of relative risk aversion (or equivalently, on the curvature of utility with respect to consumption) across the population. This is a strictly stronger criterion than Pareto efficiency. A schedule can be Pareto efficient but not rationalizable with bounded curvature if the only cardinalizations that rationalize it require unbounded consumption utility curvature.

Q2. Why do “extreme” cardinalizations with unbounded curvature arise when rationalizing Pareto-efficient taxes?

A: When a Pareto-efficient schedule is rationalized as utilitarian, the cardinalization must make the set of feasible, recardinalized utilities convex so it can be separated from the set of Pareto-improving allocations. The paper constructs such a cardinalization explicitly: it takes the form of a function whose second derivative approaches negative infinity as utility approaches its baseline value. This implies the planner’s marginal value of transfers to a household falls precipitously as the household is made even slightly better off—an extreme status quo bias. Theorem 2.b establishes that all cardinalizations rationalizing a schedule with convex revenues must share this pathology.

Q3. What is the “sort-and-extort” mechanism and how does it generate revenue convexity?

A: When elasticities of taxable income (ETIs) are heterogeneous within an income level and the income density is declining steeply, a reform that lowers marginal taxes around income $z$ brings more households into the local bracket (because there are more households just below $z$ than above). Crucially, it disproportionately attracts households with higher ETIs, since they respond more strongly to the marginal tax cut and relocate from further away, where the density differs more. Repeating the reform therefore faces a higher-elasticity composition at $z$, generating larger positive behavioral effects—making revenues convex in the size of the reform. The second step (“extort”) involves raising taxes on the now-concentrated low-elasticity households at adjacent brackets, achieving as-if group-specific taxation within a single income tax schedule.

Q4. What is the precise relationship between revenue convexity and ETI variance?

A: The paper shows (Theorem 4) that the second-order revenue derivative with respect to a narrow two-bracket reform around income $z$ equals a positive function of the income density times the expression $-[1-R’_0(z)]\varepsilon(z) + [1-R’_0(z)]\alpha(z)[\varepsilon^2(z) + \text{var}_h[\varepsilon^h | z^h_0=z]]$. The first term is always negative (pushing toward revenue concavity). The second term, which includes the income-conditional variance of ETIs, can dominate and create revenue convexity when ETI variance is sufficiently large. In the benchmark case with a single household type at each income (no within-income heterogeneity), the variance term vanishes and revenues are always concave whenever decreasing.

Q5. What is the sufficient statistics test for rationalizability at the top of the income distribution?

A: At top incomes (assuming no income effects, no super-elasticities, and CES preferences), taxes are Pareto efficient if and only if $\tau_\text{top} < \frac{1}{1+\alpha_\text{top}\varepsilon_\text{top}}$, and they are rationalizable with bounded curvature if and only if additionally $\tau_\text{top} < \frac{2}{1+\alpha_\text{top}(\varepsilon_\text{top} + \sigma^2_\text{top}/\varepsilon_\text{top})}$, where $\tau_\text{top}$ is the top marginal tax rate, $\alpha_\text{top}$ is the Pareto tail shape, $\varepsilon_\text{top}$ is the mean ETI at the top, and $\sigma^2_\text{top}$ is the income-conditional ETI variance at the top.

Q6. How does the paper estimate a lower bound on income-conditional ETI variance?

A: The authors divide households at each income level into “heavy” and “light” itemizers based on whether their total deductions exceed the local income-bracket mean. They then estimate group-specific ETIs using local polynomial regressions of log income changes on log marginal retention changes, interacting tax changes with heavy-itemizer indicators. The within-year difference in elasticities between groups provides a lower bound on within-income ETI variance, since the two-group decomposition captures only a fraction of true variance. The interaction coefficient is allowed to vary by year to isolate within-year, within-income variation in elasticities rather than between-year compositional changes.

Q7. What are the estimated magnitudes of mean and variance of ETIs?

A: Income-conditional average ETIs are estimated at between 0.2 and 0.3 at most income levels, consistent with but somewhat below prior literature estimates. The low-elasticity group (light itemizers) has an ETI of approximately zero, while the high-elasticity group (heavy itemizers) has an ETI of approximately one. Given roughly equal group sizes, this implies a lower bound on ETI variance of approximately 0.2 at most incomes and approximately 0.25 at the ninety-fifth percentile. Subdividing the high-elasticity group into two, three, and four subgroups yields a lower bound of approximately 0.25 for variance at the top.

Q8. How does the back-of-the-envelope calculation work to assess whether the second-order test fails?

A: With $\tau_\text{top} \approx 0.5$, $\alpha_\text{top} \approx 2.5$, and $\varepsilon_\text{top} \approx 0.3$ (from prior literature), the second-order condition fails if and only if ETI variance exceeds approximately 0.27. The authors’ lower bound estimate of ETI variance is already approximately 0.25 (standard deviation approximately 0.5), just below this threshold. The authors note that if the true standard deviation exceeds the lower bound by more than 4%, the second-order condition fails, making it empirically likely that the 1990 US tax schedule was not rationalizable with bounded curvature.

Q9. Why does the paper focus on the top of the income distribution for the empirical test?

A: The second-order condition is most likely to fail at high incomes for three reasons simultaneously: (i) the marginal tax rate is highest, (ii) ETI means are somewhat higher there, and (iii) the Pareto parameter $\alpha(z)$ is largest (income density falls steeply), which amplifies the sort-and-extort mechanism. The authors also note that extensive-margin labor supply responses—which are abstracted away in the theory—are likely small at high incomes.

Q10. What does the calibrated quantitative application reveal about optimal top tax policy?

A: Calibrated with a 50% initial top marginal tax rate, Pareto tail shape of 2.5, mean ETI of 0.3, and ETI standard deviation of 0.75 (50% above the estimated lower bound), the model finds welfare gains in both directions of reform. The welfare-maximizing rate below the baseline is 13.3%, yielding equivalent welfare gains of $1,966 per top earner. The welfare-maximizing rate above the baseline is 71.2%, yielding equivalent gains of $972 per top earner. The revenue-maximizing rate is 80.9%, ranging from 74.6% to 86.8% when ETI standard deviation varies by ±25% of the lower bound. This sensitivity highlights that the optimal direction and magnitude of reform depend substantially on the uncertain degree of ETI heterogeneity.

Q11. How does the paper relate to the “inverse optimum” literature?

A: The inverse optimum approach (Bourguignon and Spadaro 2012; Hendren 2020) infers the first-order welfare trade-offs implicit in an observed tax schedule. This paper goes further by inferring from second-order empirical moments—specifically the income-conditional ETI variance—whether taxes are consistent with minimal requirements on how sensitive the planner’s trade-offs are to household welfare levels. Rather than assuming a welfare function, it tests whether any welfare function with bounded curvature can rationalize the observed schedule.

Q12. Is revenue convexity possible without within-income heterogeneity in preferences?

A: Yes, but only under more specific conditions. The paper provides two supplemental examples. In the first, all households have constant-elasticity labor disutility but differ in both productivity and elasticity across income levels; when lower-income households have higher elasticities, a reform reducing marginal taxes at $z$ attracts higher-elasticity households and raises the average elasticity, leading to convex revenues. In the second, all households have the same initial elasticity but individual elasticities change in response to reforms. However, with the standard additively separable CES preferences and no within-income heterogeneity, revenues are always concave when decreasing—consistent with Werning’s (2007) observation that the Pareto planner’s problem is convex in this case.

Q13. What is the role of random tax reforms in the paper’s logic?

A: Random tax reforms serve as an expository bridge. The paper shows that if the second-order revenue effect of a two-bracket reform is positive at some income $z$, then a “randomized” reform that applies the reform with equal probability in positive and negative directions generates an expected Pareto improvement—because the convexity of revenues implies expected revenues rise, while for any household with bounded risk aversion the reform’s second-order utility effect is also positive when the reform is sufficiently narrow. This establishes that revenue convexity implies random Pareto inefficiency under bounded risk aversion, and then the paper shows the analogous deterministic result for rationalizability.

Q14. What scope conditions attach to the sufficient conditions for rationalizability (Theorem 3)?

A: Theorem 3 requires Assumptions 1 and 3 plus two boundary conditions: the ratio $\delta\text{Rev}(z)/(zg(z))$ must remain bounded away from zero as income approaches 0 or infinity, and at all incomes there must exist households with low enough compensated elasticities. Assumption 1 requires that average and marginal taxes have upper bounds below one, that marginal taxes have a lower bound, and that $zg(z)$ converges to zero at the boundaries. Assumption 3 is a regularity condition on how conditional moments of the elasticity distribution vary with income. These conditions ensure that the narrow, self-financing reforms considered in the necessity proof cannot generate welfare improvements once revenues are both decreasing and concave.

Key Concepts

Rationalizability with Bounded Curvature. The property that a tax schedule is utilitarian-optimal under some cardinalization of household utilities in which there exists a finite (though potentially arbitrarily large) upper bound on the curvature of utility with respect to consumption across the population. Formally, there exists a continuous function $\bar{\rho}$ such that, for all households, the absolute value of $[w_h \circ u_h]_{cc} / [w_h \circ u_h]_c$ is bounded by $\bar{\rho}$ evaluated at the household’s income. This criterion is strictly stronger than Pareto efficiency and strictly weaker than utilitarian optimality under a fixed cardinalization.

Two-Bracket Reform. A targeted tax reform that increases retention (post-tax income) by $1 at incomes local to some level $z$ over a small bracket of width $\ell$, and zero elsewhere (smoothed at the edges). As $\ell \to 0$, this becomes an infinitesimally narrow reform. The first- and second-order revenue effects of these reforms—denoted $\delta\text{Rev}(z)$ and $\delta^2\text{Rev}(z)$—are the paper’s key objects: Pareto efficiency requires $\delta\text{Rev}(z) < 0$ for all $z$, and rationalizability with bounded curvature additionally requires $\delta^2\text{Rev}(z) \leq 0$ for all $z$.

Income-Conditional ETI Variance. The variance of compensated elasticities of taxable income (ETIs) among households with the same income level, $\text{var}_h[\varepsilon^h | z^h_0 = z]$. This is the paper’s primary empirical object of interest and the key determinant of whether revenues are convex or concave in the size of targeted reforms. Unlike the literature’s focus on mean ETIs by income bracket, this within-income variance captures heterogeneity among households sharing the same pre-reform income.

Sort-and-Extort Mechanism. The two-step economic mechanism underlying revenue convexity from ETI heterogeneity. In the first step (“sort”), a marginal tax cut around income $z$ disproportionately attracts higher-ETI households from lower incomes (because they respond more strongly and relocate from further away), shifting the elasticity composition at $z$ upward. In the second step (“extort”), repeating the reform finds higher-elasticity households concentrated where marginal taxes fall and lower-elasticity households where taxes rise, effectively applying differential tax treatment by elasticity within a single income tax schedule.

Local Pareto Parameter $\alpha(z)$. Defined as $-d\log(zg(z))/d\log z$, where $g(z)$ is the income density. This captures the rate at which the income density is falling in income locally at $z$, and governs the strength of the sort-and-extort mechanism. High $\alpha(z)$ at top incomes (reflecting a steeply declining Pareto-type density) amplifies revenue convexity from ETI heterogeneity.

Super-Elasticity. A concept that captures how a household’s compensated ETI would change if its income were different, holding preferences fixed. Formally, it is the derivative of the household’s elasticity with respect to its log income, decomposing into effects from changes in preference curvature and changes in the local curvature of the tax schedule. Super-elasticities are zero in the benchmark case of additively CES preferences and locally CES retention schedules but contribute additional terms to the second-order revenue expression in the general case.

Cardinalizing Function. A strictly increasing function $w_h$ that maps household $h$’s indirect utility $V_h$ to a cardinalized utility level $w_h(V_h)$. The social planner maximizes the expectation of cardinalized utilities. Different choices of ${w_h}_h$ correspond to different stances on interpersonal comparisons, including unbounded curvature (rationalizing any Pareto-efficient schedule) or bounded curvature (the paper’s proposed restriction). Rawlsian social welfare is a limit of utilitarian welfare with increasingly concave cardinalizing functions.

Equal Pay for Similar Work

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

Layer 1 — Overview

Research Question

This paper studies the labor market effects of “Equal Pay for Similar Work” (EPSW) policies — laws that require firms to pay equal wages to workers of different protected-class identities (e.g., different genders) who perform “similar” work within a firm. EPSW has become increasingly prevalent: as of January 2023, more of the U.S. workforce falls under state EPSW laws than state “Equal Pay for Equal Work” (EPEW) laws. Despite this spread, the equilibrium consequences of EPSW were previously unknown.

Theoretical Framework

The authors develop two theoretical models. The first is a static cooperative game (whose outcomes coincide with the Nash equilibria of a non-cooperative simultaneous-wage-offer game). Homogeneous firms with constant-returns-to-scale production compete for a continuum of heterogeneous workers. Workers belong to one of two groups A or B (e.g., men and women), with group A constituting a β ≥ 1 majority. Each worker’s productivity v is drawn from a group-specific distribution (FA or FB); firms’ willingness to pay equals each worker’s productivity, but can embed taste-based discrimination. The analysis is framed as applying “within job” in a local labor market — only workers performing “similar” work in the eyes of the law.

The second model is a dynamic search-and-bargaining framework with an arbitrary number of firms, search frictions, reallocation frictions, and Nash-in-Nash bargaining. EPSW is introduced as a surprise, and constrained firms choose whether to segregate for one group or remain desegregated (paying a common wage to all workers).

Main Theoretical Findings

Without EPSW, Bertrand competition among firms drives every worker’s wage to equal her productivity; any wage gap between groups A and B exactly reflects the difference in average productivities (EA(v) − EB(v)), whether or not those productivity differences stem from discrimination.

With EPSW, the equilibrium is qualitatively transformed. In the static model (Proposition 2), firms generically fully segregate their workforces: one firm hires all A-group workers and the other hires all B-group workers. EPSW functions as an enforcement mechanism for this segregation analogous to location choices in Hotelling’s model — poaching a worker from the competing firm is costly because EPSW then requires the poaching firm to pay equal wages to all workers it employs. In the core with EPSW (Proposition 3), the wage gap moves in favor of the majority group (A-group, β > 1) in the sense that all core outcomes except one strictly increase the A-group wage advantage. Moreover, firm profits and the magnitude of the wage gap co-move: firms benefit from selecting equilibria with larger wage gaps. The directional conclusion — EPSW benefits the majority group — holds regardless of the distributions of the two groups’ productivities, conditional only on β > 1 for the wage gap; for the log wage gap the additional regularity condition βEA[v] > EB[v] is required.

In the dynamic search model (Proposition 4), all firms eventually segregate under any equilibrium, with the long-run wage ratio moving in favor of the group toward which more firms segregate. Under equitable search and sufficiently low reallocation frictions (Proposition 5), more firms segregate toward the majority group when βEA[v] > EB[v]. Firms that are nearly segregated at the time of EPSW enactment segregate sooner than others (Proposition 6).

Empirical Setting and Design

The authors test these predictions using Chile’s 2009 EPSW (Law 20.348), the country’s first equal pay law, which prohibited paying women less than men (or vice versa) for similar work. Firms with 10 or more long-term workers at the time of announcement (June 2009) face formal grievance procedures and financial penalties (69–1,384 USD per worker-month of violation); firms below this threshold face no financial penalty, providing a clean threshold-based treatment assignment.

The data are matched employer-employee administrative records from the Chilean unemployment insurance system covering January 2005 – December 2013, a random sample of approximately 4% of all firms stratified by size. The main estimation sample restricts to firms with 6–13 total workers at announcement (41% of active firms), and the design is a difference-in-differences (event study) comparing treated (≥ 10 long-term workers) to control (< 10 long-term workers) firms. The identifying assumption is parallel trends between similarly sized firms.

Main Empirical Findings

First, EPSW increases full gender segregation across firms. The share of fully gender-segregated firms increases by 4.4 percentage points (baseline: 34.3% of firms were fully segregated at announcement). Simultaneously, the share of nearly-but-not-fully segregated firms (majority gender share ∈ [0.8, 1)) declines by 4.0 percentage points — a “missing mass” of near-segregated firms consistent with the search model’s prediction that firms on the margin of full segregation segregate most readily (e.g., by separating the sole worker of the “wrong” gender). Moreover, firms that are nearly segregated at announcement experience an 8.7 percentage point increase in full segregation post-EPSW, compared to 2.8 percentage points for firms not nearly segregated at announcement.

Second, EPSW shifts the gender wage gap in favor of the local labor market majority group. In male-majority local labor markets (defined by industry × county), EPSW increases the gender wage gap in favor of men by 4.3 percentage points. In female-majority local labor markets, EPSW decreases the gender wage gap (i.e., in favor of women) by 6.2 percentage points. The wage gap change is primarily driven by reductions in minority-group wages: women’s average wages in male-majority markets fall by 3.3 percentage points, and men’s average wages in female-majority markets fall by 4.5 percentage points; there are no statistically significant changes in majority-group wages. Because men dominate Chile’s overall labor market (approximately 5/6 of all workers are employed in majority-male local labor markets), the overall effect of EPSW is to increase the gender wage gap (in favor of men) by 2.7 percentage points. Pre-treatment coefficients are statistically indistinguishable from zero across all specifications, supporting the parallel trends assumption. These findings are robust across six alternative specifications covering different samples, fixed-effect structures, and controls.

Scope Conditions

Theoretical results apply within a set of “similar” workers in a given local labor market — the paper does not predict differential effects across job types within a firm (e.g., custodians vs. lawyers) that do not perform similar work. Empirical results are identified for firms with 6–13 workers and pertain to Chile’s formal sector (informal labor share ~25% in 2009). Predictions on the wage ratio (log wage gap) require the additional regularity condition βEA[v] > EB[v], which is consistent with the Chilean data.

In depth

Q1. What is the core mechanism by which EPSW leads firms to fully segregate in the static model?

A: EPSW makes cross-group poaching prohibitively costly. If a firm that hires only A-group workers were to hire even a positive measure of B-group workers, EPSW would — by transitivity — require it to pay the same wage to all workers. This eliminates the firm’s ability to exploit productivity heterogeneity across workers; it would have to raise all wages to match the highest worker, destroying profit. As a result, firms segregate in equilibrium to avoid the bite of EPSW entirely: each firm caters to one group, and the within-group wage schedule remains unconstrained. The mechanism is analogous to Hotelling’s location model: segregation serves as the enforcement device for avoiding the equal-pay constraint.

Q2. How does the equal profit condition generate a wage gap in favor of the majority group?

A: In any core outcome under EPSW (Proposition 3), the Equal Profit Condition requires both firms to earn the same total profit. When there are β > 1 A-group workers (more than B-group workers), the firm serving A-group workers must pay higher average wages per worker to extract the same total profit from a larger pool, relative to the firm serving a smaller B-group. This mechanically raises A-group average wages relative to B-group average wages. Crucially, this directional conclusion — EPSW widens the majority-group wage advantage — holds regardless of the shapes of FA and FB, meaning it is robust to any underlying discriminatory or non-discriminatory productivity differences.

Q3. What is the baseline (without-EPSW) wage gap, and how does EPSW change it?

A: Without EPSW, Proposition 1 establishes that every worker is paid exactly her productivity in any core outcome (full employment, wages = productivity). Therefore, the wage gap equals EA(v) − EB(v) and the wage ratio equals EA(v)/EB(v): any gap reflects only productivity differences (including discrimination embedded in willingness to pay). Under EPSW, Proposition 3 shows that all core outcomes except a single (measure-zero) one strictly widen the wage gap beyond this level. The wage ratio result (Proposition 3, Part 4) requires the additional condition βEA[v] > EB[v] — that the majority group is not sufficiently less productive or more discriminated against to reverse the direction.

Q4. How does the dynamic search model modify the static predictions?

A: In the dynamic model (Proposition 4), full segregation is achieved in finite time T in any equilibrium, not instantaneously. Prior to T, firms make sequential segregation decisions; workers displaced by firm desegregation choices are replaced at rate ρ ∈ [0,1]. The long-run wage ratio is determined by the ratio nA/nB — the number of firms segregating toward group A versus B. If nA > nB, the long-run wage ratio moves in favor of A; if nA = nB, the policy has no long-run effect on the wage ratio. The key departure from the static model is that this outcome depends not only on the majority group size but also on search intensities and reallocation frictions (high firm tenure/low d can make segregating toward the majority costly if the firm already employs many minority-group workers).

Q5. Under what conditions does the dynamic model predict that more firms segregate toward the majority group?

A: Proposition 5 states that for sufficiently large d (fast worker turnover / low reallocation frictions) and equitable search (equal search intensity across firms within a group), the number of firms segregating toward A satisfies nA ∈ [xA−1, xA+1], where xA is defined by an equal-profit condition. Moreover, if βEA[v] > EB[v] (the majority group is collectively more valuable), then nA ≥ nB. Without equitable search, the conclusion holds under more stringent conditions: for any search intensity vector r, there exist d* and β* such that for d > d* and β > β*, any equilibrium yields nA > nB. Empirically, 94% of local-labor-market-by-month units in Chile exhibit more firms segregating toward the majority gender post-EPSW, consistent with these conditions being met.

Q6. Why do firms that are nearly segregated at announcement respond most strongly to EPSW?

A: Proposition 6 establishes that firms with a low ratio of minority-group to majority-group search intensity (i.e., nearly segregated in employment) segregate earliest, provided the discount rate is sufficiently low. The intuition is that for a nearly segregated firm, the cost of segregating — separating the few minority-group workers — is small relative to the costs of remaining desegregated (paying a common wage that compresses profit, and being unable to poach new workers). Empirically, firms nearly segregated at announcement (majority gender share ∈ [0.8,1) at announcement) show an 8.7 percentage point increase in full segregation post-EPSW, roughly three times larger than the 2.8 percentage point effect for firms not nearly segregated at announcement. This “missing mass” pattern (decline in near-segregation matched by increase in full segregation) is also consistent with Proposition 6.

Q7. What is the heterogeneous effect of EPSW on the wage gap by local labor market type?

A: The empirical design allows the wage gap effect to differ by local labor market (LLM) majority type (male vs. female). In male-majority LLMs (firm industry × county pairs where males comprise more than 50% of workers in June 2009), EPSW increases the gender wage gap in favor of men by 4.3 percentage points (SE = 0.0116). In female-majority LLMs, EPSW decreases the gender wage gap (in favor of women) by 6.2 percentage points (SE = 0.0234). These findings precisely match the theoretical prediction that EPSW benefits whichever group is in the majority of the local labor market. The dynamic event studies show no pre-trends in either subsample; effects begin at announcement (τ = 0) and grow over time.

Q8. What drives the wage gap change — majority wages rising or minority wages falling?

A: The change is primarily driven by a reduction in the minority group’s average wages, not an increase in majority wages. Women’s average wages in male-majority labor markets fall by 3.29 percentage points (SE = 0.0111) in treated versus control firms post-EPSW. Men’s average wages in female-majority labor markets fall by 4.45 percentage points (SE = 0.0178) in treated versus control firms post-EPSW. There are no statistically significant changes in the average wages of the majority group of workers within any LLM type. This is consistent with the model’s mechanism: segregation reduces competition for minority-group workers (fewer firms competing for them), depressing their wages.

Q9. What is the aggregate (economy-wide) effect of EPSW on the gender wage gap in Chile?

A: Because approximately 5/6 of all Chilean workers are employed in male-majority local labor markets (men have higher labor force participation, with female labor force participation at roughly 30% in 2009), the overall effect of EPSW is to increase the gender wage gap in favor of men by 2.74 percentage points (SE = 0.0102). This is a net effect that averages the positive (pro-male) gap increase in male-majority markets and the negative (pro-female) gap decrease in female-majority markets, weighted by market sizes.

Q10. How does the identification strategy deal with anticipation and compositional changes?

A: Treatment status is assigned based on firm size at the time of policy announcement (June 2009) rather than enactment (November 2009), creating an intent-to-treat framework: some “treated” firms may fall below the threshold by enactment, and some “control” firms may rise above it, both attenuating the estimates (implying estimated effects are plausible lower bounds). The no-anticipation assumption is supported by the absence of statistically significant pre-trends in either the segregation or wage-gap specifications. To address compositional changes in worker characteristics across LLMs induced by EPSW itself, the wage regressions include time fixed effects interacted with human capital dimensions (education, contract type, age decade) and firm comparison groups, controlling for observable composition shifts. Placebo tests at alternative firm-size thresholds find no statistically or economically meaningful effects, supporting the causal interpretation.

Q11. How does EPSW in Chile compare to EPEW theoretically and in the literature?

A: EPEW requires equal pay only for workers doing exactly equal work, which creates an easily exploitable loophole: firms can proliferate job titles or marginally differentiate duties to avoid compliance. EPSW closes this by requiring equal pay across a coarser “similar work” category, making evasion harder. Theoretically, the prior EPEW literature (Bhaskar et al. 2002, Kaas 2009, Lagerlöf 2020, Lanning 2014) generated ambiguous directional predictions — equal pay laws could either increase or decrease wage disparities within the same paper. The authors attribute this ambiguity to EPEW models’ requirement that workers be exactly equally productive. By contrast, EPSW applies across workers with heterogeneous productivities, and the authors derive unambiguous predictions: full segregation and a wage gap shift toward the majority group, both of which are confirmed empirically.

Q12. What is the analogy to “best-price guarantees” in product markets?

A: The paper draws a methodological parallel to most-favored-customer (MFC) clauses in product markets. MFC clauses commit firms to rebating past consumers if prices fall, which directly equalizes payments across buyers but unintentionally raises firm market power. In the EPSW setting, the policy plays the role of a best-wage guarantee — but because firms compete for workers, the constraint binds off the equilibrium path. Firms segregate so that no firm is ever exposed to the equal-pay constraint in equilibrium, yet the threat of the constraint (if a firm deviates and hires from both groups) effectively differentiates labor costs across groups, driving the unintended wage effects. This is related to “artificial” switching costs that create local market power in consumer markets (Klemperer, 1987).

Key Concepts

Equal Pay for Similar Work (EPSW): A legal constraint requiring that within a firm, workers belonging to different protected-class identities (e.g., different genders) who perform “similar” work receive equal wages. Distinguished from “Equal Pay for Equal Work” (EPEW) by its coarser similarity standard, which cannot be evaded by minor job-title differentiation. In the model, this constraint is formalized as: a firm cannot hire positive measures of workers from two different groups such that all workers in one group receive strictly higher wages than all workers in the other group; by transitivity, a firm hiring from both groups must pay almost all workers the same wage.

Core Outcome: The solution concept used in the static model, drawing on cooperative game theory (Shapley–Shubik assignment game). An outcome (specifying which firm hires each worker and at what wage) is in the core if no firm and subset of workers can form a blocking coalition that makes both the firm and each worker in the coalition strictly better off. The paper uses this concept because its pure-strategy Nash equilibrium outcomes (in the associated non-cooperative simultaneous wage-offer game) exactly coincide with the core outcomes under the restriction that firms pay the same wage to all workers of the same type.

Full Segregation: A labor market outcome in which each firm employs workers from only one group (all A-group workers at one firm, all B-group workers at the other). The paper proves (Proposition 2) that EPSW generically forces full segregation in equilibrium, because any deviation to hire from both groups exposes the firm to the equal-pay constraint. Empirically measured as a binary indicator for whether all workers at a given firm in a given month are of the same gender.

Near Segregation: A firm-level state in which the majority gender constitutes 80–99% of the firm’s workforce (the majority gender share is in [0.8, 1)). The paper uses this as a complementary outcome to full segregation; theory (Proposition 6) predicts a decline in near segregation post-EPSW because firms in this state face the lowest cost of transitioning to full segregation. Empirically, the near-segregation share falls by 4.0 percentage points post-EPSW, mirroring the 4.4 percentage point rise in full segregation.

Local Labor Market (LLM): Defined in the empirical analysis as a firm’s geographic county interacted with its industry code, creating 321 × 21 potential cells. The LLM is classified as male-majority or female-majority based on the share of female workers across all firms in the industry-county pair in June 2009. This is the unit at which the “majority group” for Proposition 3’s wage gap prediction is defined, and the level at which the heterogeneous wage effects of EPSW are estimated.

Equal Profit Condition: A necessary condition of any core outcome (with or without EPSW): both firms must earn the same total profit in equilibrium. Under EPSW with full segregation, this condition determines the relative average wages of the two groups — because firm sizes differ (β A-group workers vs. 1 B-group worker), equal profit requires the firm serving the larger group to pay higher average wages, mechanically moving the wage gap in favor of the majority group.

Nash-in-Nash Bargaining: The bargaining protocol used in the dynamic search model, following Horn and Wolinsky (1988). Each bilateral worker-firm bargain splits the available surplus in proportion to exogenous bargaining power parameter Δ ∈ (0,1), taking as given the outcome of all other bilateral bargains. A worker’s disagreement point is the wage she would receive from bargaining with the next firm in her search order. This generates the result that a worker’s realized payoff is increasing in the number of segregated (non-EPSW-constrained) firms competing for her, connecting firm segregation decisions to wage determination.

Reallocation Friction: In the dynamic search model, represented by a low departure probability d ∈ (0,1) for existing employees. When d is low, firms retain a large fraction of their workforce across periods, making segregation costly because the firm must separate from any existing workers of the “wrong” group. The paper shows (Proposition 5) that for sufficiently large d (low frictions), the equal-profit condition approximately pins down the number of firms segregating toward each group, and for d above a threshold, the majority group attracts weakly more segregating firms.

Firm Responses and Wage Effects of Foreign Demand Shocks with Fixed Labor Costs and Monopsony

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

Layer 1 — Overview

Research Question. The paper asks three related questions in the context of Belgium, a small open economy: (1) What do firms’ responses to demand shocks reveal about their cost structures? (2) What are the worker and wage impacts of foreign demand shocks? (3) How sensitive are the aggregate wage effects of foreign demand shifts to firms’ cost structures and imperfect competition in the labor market?

Data. The analysis combines administrative micro-data from Belgium for 2002–2014, provided by the National Bank of Belgium. The linked dataset covers 995,739 firm-year observations from private, non-financial firms with at least one FTE employee, and integrates: (a) a Business-to-Business (B2B) VAT transactions registry capturing all annual domestic firm-to-firm sales above €250; (b) customs records and intra-EU declarations for imports and exports at the 8-digit product level; (c) annual accounts containing data on sales, labor costs, intermediate inputs, capital, and firm characteristics; and (d) employer-employee matched data from the Belgian social security administration (BCSS) for a random sample of 500,000 workers in firms with 10 or more FTE employees, covering 2003–2014.

Identification Strategy. To isolate variation in firms’ sales driven by foreign demand rather than supply-side factors, the authors construct a firm-specific foreign demand instrument following Hummels et al. (2014) and Dhyne et al. (2021). The instrument is the weighted average of changes in world import demand facing a firm, using lagged export shares as weights and excluding Belgian imports from the world import measure. Crucially, the instrument captures both direct foreign demand exposure (for exporters) and indirect exposure through the domestic production network — including the foreign demand shocks passing through to upstream domestic suppliers via buyer-supplier links. Firm and industry-year fixed effects control for time-invariant heterogeneity and industry-level trends.

Key Empirical Facts. Within-firm analysis over four-year windows finds that intermediate input purchases respond nearly proportionally to changes in sales (slope coefficient 0.82), while labor costs respond less than proportionally (slope coefficient 0.57). The less-than-proportional response of labor costs — with the employment slope of 0.48 and the average wage slope of 0.09 — is consistent with sizable fixed overhead costs in labor inputs and upward-sloping labor supply curves. Output prices co-move more with input prices than with average wages, consistent with labor constituting a smaller share of variable costs than intermediate inputs.

IV Estimates of Firm Responses. In response to a foreign demand shock inducing a 10 percent instantaneous increase in a firm’s sales, the firm’s cumulative sales over four years increase by approximately 7.6 percent (balanced panel). Over the same four-year horizon, total input purchases increase by about 7.0–7.8 percent, while labor costs increase by only 3.5–4.1 percent — a substantially less-than-proportional response. Roughly one-quarter of the labor cost change comes from changes in average wages rather than employment changes. Domestic input purchases increase by 5.3–6.0 percent, indicating that firms pass on a large share of foreign demand shocks to their domestic suppliers.

Structural Parameters. The implied IV estimate of the labor cost elasticity with respect to sales is 0.53 (standard error 0.08), statistically significantly below one. The implied elasticity of total input purchases is 1.05 (standard error 0.15), close to one, so the fixed share of intermediate inputs is approximately zero. The labor supply elasticity estimated from the ratio of wage and employment responses is approximately 3.9 in the full sample and 2.3 in the stayer subsample; the implied wage markdown is 21 percent and 30 percent respectively. Incorporating upward-sloping labor supply into equation (15), the estimated share of total labor inputs that is fixed overhead is approximately 53 percent. By comparison, the fixed share of total costs (labor and intermediate inputs combined) is approximately 29 percent in Belgium — higher than the 18–22 percent found in U.S. data (De Loecker et al. 2020) and the 20 percent found in U.S. manufacturing plants (Ederhof et al. 2021).

General Equilibrium Counterfactuals. The authors parameterize and solve a small open economy general equilibrium model with monopsonistic competition in labor markets, monopolistic competition in product markets, and fixed and variable labor and intermediate input costs. Using the Dekle-Eaton-Kortum (2007) “hat algebra” technique, they simulate a 5 percent increase in foreign tariffs on all Belgian exports and compare four counterfactual economies: (1) baseline Belgium with fixed costs and imperfect labor market competition (ε = 3.9); (2) fixed costs and perfectly elastic labor supply (ε = ∞); (3) no fixed costs with imperfect competition; (4) no fixed costs and perfectly competitive labor markets.

Main Findings on Wages. In the baseline Belgian economy, a 5 percent increase in foreign tariffs produces a 4.9 percent fall in the average real wage. With fixed costs but perfectly elastic labor supply, the real wage falls by 4.8 percent — nearly identical. With upward-sloping labor supply but no fixed costs, the real wage falls by only 3.0 percent; without fixed costs and with perfectly competitive labor supply, the fall is only 2.8 percent. The paper concludes that fixed overhead costs in labor substantially amplify real wage declines, while incorporating upward-sloping labor supply appears quantitatively less consequential for aggregate wage outcomes. Standard models that assume no fixed costs and perfectly elastic labor supply — the typical modeling choice in the trade literature — may substantially understate (by roughly 43–75 percent of the true effect) the aggregate wage decline from a negative foreign demand shock.

Mechanism. Fixed overhead costs reduce labor’s share of variable costs. When labor is a smaller share of variable costs, output prices are less sensitive to changes in wages. With a fixed aggregate labor supply, the economy must lower prices through wage reductions to restore equilibrium after a negative demand shock; the required wage decline is larger when fixed labor costs are taken into account. The findings are robust to adjustment cost specifications, a nested logit extension of the labor market model, and controlling for location-year fixed effects and import price changes.

In depth

Q1. What two motivating empirical facts about Belgian firms does the paper establish?

A1: First, within-firm four-year changes show that intermediate input purchases respond nearly proportionally to changes in sales (slope coefficient 0.82), while labor costs respond less than proportionally (slope coefficient 0.57). The labor cost response decomposes into an employment slope of 0.48 and a wage slope of 0.09. Second, output prices co-move more strongly with input (intermediate goods) prices than with average wages, consistent with labor constituting a smaller share of variable costs than intermediate inputs.

Q2. How does the instrument for foreign demand shocks capture indirect exposure through production networks?

A2: The instrument for firm k is a weighted average of changes in world import demand, where the weights reflect both the firm’s own direct export shares across countries and products and the firm’s indirect export exposure through its domestic buyers’ export shares. The term H̃_{kn,t-1} captures the share of firm k’s total sales purchased by firm n directly and indirectly through all upstream chains. This means even non-exporting firms receive a non-zero instrument through their sales to directly-exporting firms. In fact, non-directly-exporting firms sell on average nearly 10 percent of their output indirectly to foreign markets.

Q3. What is the estimated magnitude of the labor supply elasticity facing Belgian firms, and what does it imply for wage markdowns?

A3: In the full main estimation sample (balanced panel), the IV estimate of the firm-specific labor supply elasticity is approximately 3.9, implying a wage markdown of about 21 percent relative to the marginal revenue product of labor. In the stayer subsample (incumbent workers only, holding workforce composition fixed), the estimated labor supply elasticity is approximately 2.3, implying a markdown of about 30 percent. The paper can reject perfect competition (infinite elasticity, zero markdown) at a significance level of 0.06 in the full sample and 0.001 in the stayer sample using the closure method.

Q4. What is the estimated labor cost elasticity with respect to demand-driven sales changes, and what does it imply about fixed labor costs?

A4: The IV estimate of the labor cost elasticity with respect to sales is 0.528 (standard error 0.085), statistically significantly below one. If labor supply were perfectly elastic, this would directly imply a fixed labor cost share of approximately 47 percent. Incorporating the estimated upward-sloping labor supply curve through equation (15), the model implies that approximately 53 percent of total labor inputs are fixed overhead. For context, occupational data from Belgium’s 2014 Structure of Earnings Survey shows that clerical support workers and managers together account for 21 percent of total earnings, and adding professionals raises this to 51 percent — broadly consistent with the estimated fixed share.

Q5. What does the estimated elasticity of input purchases with respect to sales imply about fixed intermediate input costs?

A5: The IV estimate of the elasticity of total input purchases with respect to sales is 1.050 (standard error 0.150), close to one. The implied fixed share of total intermediate inputs is therefore approximately zero. However, there is substantial heterogeneity by input type: purchases from the manufacturing sector (roughly half of all input purchases) have an elasticity close to one, whereas service-sector inputs (roughly 30 percent of total input purchases) have an implied fixed cost share of approximately 36 percent, with a size-weighted average cumulative response of 4.3 percent against a total cumulative sales increase of 6.7 percent.

Q6. How does the paper rule out alternative explanations for the less-than-proportional response of labor costs?

A6: The paper considers three main alternatives. First, adjustment costs: even in the presence of labor adjustment costs, under a homothetic constant-returns production function a permanent shock should eventually produce a proportional labor response. The paper focuses on four-year cumulative responses where firm responses change little after the first couple of years, and shows identification of fixed costs holds even in models with quadratic or Calvo-style adjustment costs. Second, a non-homothetic CES production function without fixed costs: Appendix B.3 shows that such a specification predicts that if the labor cost elasticity is below one, the input purchase elasticity must be above one — at odds with the data, which shows the input purchase elasticity is close to one while the labor cost elasticity is well below one. Third, variable markups: a uniform markup change would reduce both elasticities proportionally, not create the large gap between labor cost and input purchase elasticities observed.

Q7. Why are firms’ domestic suppliers affected by foreign demand shocks, and how large are the pass-through effects?

A7: Firms pass on foreign demand shocks to their domestic suppliers through buyer-supplier production network links. When a foreign demand shock increases a firm’s sales by 10 percent instantaneously, its domestic input purchases increase cumulatively by approximately 5.3–6.0 percent over four years. Total input purchases increase by 7.0–7.8 percent over the same period; the difference between total and domestic input purchases reflects service inputs (which have smaller responses) and the composition of imported versus domestic inputs.

Q8. What is the aggregate real wage effect of a 5 percent increase in foreign tariffs on Belgian exports in the baseline model?

A8: In the baseline counterfactual representing the actual Belgian economy (with fixed overhead costs and labor supply elasticity ε = 3.9), a uniform 5 percent increase in foreign tariffs on all Belgian exports produces a 4.9 percent fall in the average real wage. The median firm reduces output by 3.8 percent, marginal costs by 4.8 percent, and wages by 7.9 percent. The fall in wages is driven by a general equilibrium mechanism: since the foreign price is exogenous and trade balance must hold, wages are the key adjusting margin.

Q9. How much does the modeling of fixed overhead costs versus imperfect labor market competition matter for the aggregate wage counterfactual?

A9: Fixed overhead costs account for nearly all of the amplification relative to the standard model. With fixed costs but perfectly elastic labor supply, the real wage falls 4.8 percent — almost identical to the 4.9 percent in the baseline. Without fixed costs but with the estimated upward-sloping labor supply, the fall is only 3.0 percent. Without either, the fall is 2.8 percent. Thus, incorporating fixed overhead costs in labor raises the estimated wage decline by approximately 1.9 percentage points, while incorporating imperfect labor market competition adds only about 0.1 percentage points. The paper concludes that fixed overhead costs, not monopsony, are the essential feature for accurately predicting tariff impacts on wages.

Q10. What is the mechanism by which fixed overhead costs amplify the aggregate wage decline from a negative demand shock?

A10: Fixed overhead costs reduce the share of labor in firms’ total variable costs. When labor constitutes a smaller fraction of variable costs, output prices are less sensitive to changes in wages. With aggregate labor supply fixed, the economy restores equilibrium after a negative demand shock by reducing prices through wage cuts. To achieve the same magnitude of price reduction when labor is a smaller fraction of variable costs, wages must fall by a larger amount — amplifying the aggregate wage impact. Fixed overhead costs in labor also make foreign inputs relatively more important in variable costs, as shown empirically in Appendix D.1.

Q11. Is the conclusion about the relative importance of fixed costs versus labor market imperfections robust to alternative specifications of the labor market?

A11: Yes. The paper extends the model to a nested logit structure for worker preferences (following Lamadon et al. 2022), which allows Belgium to contain multiple labor markets (defined as industry-region nests), permits heterogeneous markdowns across markets, and is still identified from the data. Empirically, incorporating multiple labor markets and heterogeneous markdowns does not quantitatively alter the aggregate counterfactual predictions for the wage effects of foreign demand shocks.

Q12. Are heterogeneous responses to the foreign demand shock observed across exporters, importers, and domestic-only firms?

A12: The paper finds no systematic differences in the elasticities of labor cost and input purchases between firms that trade internationally and those that do not. This implies that exporters and importers have higher absolute fixed costs (consistent with fixed export and import costs) but comparable fixed cost shares — since these firms tend to be larger and thus spread higher absolute fixed costs over larger output volumes.

Q13. Do the findings about fixed overhead costs extend beyond foreign demand shocks?

A13: Yes. The paper shows in Appendix D.4 that a uniform 5 percent reduction in the productivity of all Belgian manufacturing firms generates qualitatively and quantitatively similar conclusions: fixed overhead costs amplify the predicted wage effects of domestic productivity shocks, while imperfect competition in the labor market matters to a lesser but still meaningful extent.

Key Concepts

Fixed Overhead Costs (Fixed Labor Costs / Fixed Intermediate Input Costs): In the paper’s model, each firm has firm-specific fixed overhead input requirements for labor (denoted ℓ̄_k^f) and intermediate inputs (denoted q̄_k^f) that must be satisfied regardless of the firm’s output level. These fixed requirements are separate from the variable inputs used in production. Fixed labor costs may reflect administration, worker management, facility maintenance, and other tasks that do not directly translate into output. Fixed intermediate input costs include waste management, accounting services, and electricity payments that occur irrespective of sales. The share of total labor inputs that is fixed is identified by how much less than proportionally labor costs respond to demand-driven changes in sales.

Monopsonistic Competition in the Labor Market: The paper models each firm as facing an upward-sloping firm-specific labor supply curve arising from workers’ heterogeneous idiosyncratic preferences over non-wage firm attributes (amenities). Because workers’ idiosyncratic tastes are private information, firms cannot price-discriminate and thus face an increasing marginal cost of labor. Each firm is infinitesimal within the aggregate labor market but has wage-setting power at the firm level. This gives rise to a constant-elasticity firm-level labor supply curve ℓ_k = A_k w_k^ε, where ε is the labor supply elasticity facing the firm.

Wage Markdown: The firm’s equilibrium wage is marked down relative to the marginal revenue product of labor by the factor ε/(1+ε), which is less than one when ε is finite. With a labor supply elasticity of 3.9, the implied markdown is approximately 21 percent; with a supply elasticity of 2.3 (stayer sample), the markdown is approximately 30 percent. Perfect competition corresponds to ε = ∞ and a markdown of zero.

Labor Cost Elasticity: The elasticity of a firm’s total labor cost with respect to a demand-driven change in the firm’s sales, as derived from the model’s comparative statics (equation 15). This elasticity depends on both the variable share of labor inputs (ℓ_k^v / ℓ_k) and the labor supply elasticity ε. It lies strictly between zero (all labor fixed) and one (all labor variable), and is declining in ε for a given variable share. The paper estimates this elasticity at 0.528 via IV, implying substantial fixed overhead in labor.

Total Foreign Demand Shock: The firm-level measure of foreign demand used as an instrument, defined as the weighted average of changes in world import demand (excluding Belgium) across country-product pairs, where the weights reflect both the firm’s own lagged direct export shares and its indirect exposure through the domestic production network (via the Leontief inverse matrix H̃). This measure captures both direct exporter exposure and indirect upstream exposure for non-exporting firms that supply to exporters.

Indirect Export Exposure: The share of a firm’s output that reaches foreign markets indirectly through sales to domestic buyers who subsequently export. Defined recursively: the total export share of firm k equals its direct export revenue share plus the sum over all domestic buyers of the product of k’s revenue share from that buyer and the buyer’s own total export share. Even non-direct-exporting firms sell on average approximately 10 percent of their output indirectly to foreign markets in the Belgian data.

Dekle-Eaton-Kortum Hat Algebra: A technique for solving general equilibrium counterfactuals in trade models by expressing all outcomes as proportional changes (“hats”) relative to the observed equilibrium, without needing to recover the underlying structural parameters. The paper uses this approach to compute counterfactual wages under alternative tariff scenarios, holding fixed the observed firm-level expenditure shares from the reference year (2012) while allowing parameters such as productivity and technology weights to vary across counterfactual economies to rationalize identical observed firm-level observables.

Worker Rents: In the monopsony model, inframarginal workers earn rents defined as the excess return over what would be required to make them indifferent between employers. These rents arise because firms cannot price-discriminate across workers with heterogeneous amenity valuations. The additional rents accruing to workers from a demand-driven increase in firm sales decompose into: (1) wage increases for incumbent workers multiplied by current employment, (2) rents for new hires (the excess of their wage bill over the amount required to induce them to switch to the expanding firm), and (3) a correction term related to the fraction of the labor cost increase borne by expanding employment rather than wages.

Homeownership, Polarization, and Inequality

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

This paper asks why job polarization and income inequality are higher in large U.S. cities, and proposes a novel housing-market mechanism that operates independently of — but interacts with — the skill-biased technical change (SBTC) explanations dominant in the existing literature.

The core argument is that large cities have experienced faster growth in house prices relative to both wages (price-wage ratio) and rents (price-rent ratio) since 1980. This excess price growth has priced middle-income households out of homeownership in expensive cities. Because low-income households cannot afford to own anywhere and high-income households can afford to own everywhere, it is specifically middle-income (middle-skilled) households whose location choice becomes entangled with their tenure choice. These households increasingly sort toward smaller, more affordable cities where they can purchase a home. This selective out-migration hollows out the middle of the income distribution in large cities, producing greater employment polarization and income inequality there.

Empirically, the paper uses Census and ACS data from 1980 to 2019 covering 465 commuting zones (CZs). Polarization is measured following Autor and Dorn (2013) by assigning 3-digit occupations to income percentiles fixed at 1980 levels; inequality is measured by the Gini coefficient and variance of log annual wages. Housing costs are captured by hedonic price and rent indices and three derived ratios. OLS and IV results (instrumented using the interaction of land unavailability and long-run changes in real interest rates) show that doubling of prices is associated with a 1 percentage point decline in the middle-skilled employment share; doubling of the price-rent ratio is associated with an 11.3 percentage point decline; doubling of the price-wage ratio with a 5.3 percentage point decline. Inequality follows the same pattern: doubling prices raises 100x the variance of log wages by 2.3 points; doubling the price-rent ratio raises it by 11.7 points; doubling the price-wage ratio by 7.7 points.

The migration mechanism is documented using 2001–2019 CPS ASEC data, which — uniquely among available sources — reports reasons for moving. A doubling of the price index, price-wage ratio, or price-rent ratio in the origin state relative to the destination raises the probability that a middle-income (2nd–4th quintile) household moves for housing-related reasons by approximately 5–10 percentage points in absolute terms, implying a 50–80% relative increase compared with low- or high-income households making a housing-related move.

The theoretical framework extends the standard spatial equilibrium (Rosen-Roback) model with two additions: skill heterogeneity and housing tenure choice. Households face a minimum house size constraint and a payment-to-income (PTI) constraint (calibrated at lambda = 0.308). These constraints create distinct skill thresholds for homeownership that vary by city; the interaction between location and tenure choices applies only to middle-skilled households who can afford ownership in cheap but not expensive cities.

In the quantitative model, calibrated separately for 1980 and 2019 with two locations (top 30 CZs vs. the rest), counterfactual experiments show that holding price-wage ratios at their 1980 levels reduces the excess polarization gap between large and small CZs by 93% and the excess inequality gap by 40%. Holding price-rent ratios constant reduces the polarization gap by 96% and the inequality gap by 27%. By contrast, shutting down SBTC entirely reduces the polarization gap by only 54% and the inequality gap by 73%. These results establish that while SBTC is an important driver, its effect on polarization and inequality is substantially amplified by faster house price growth in large cities; without the housing affordability channel, the effect of SBTC on disproportionate polarization would be 63–81% smaller and on the inequality gap 18–36% smaller.

Q: What is the paper’s central research question? A: The paper asks why job polarization and income inequality are systematically higher in large U.S. cities than in small ones. Prior literature attributed this to skill-biased technical change, external labor demand shocks, or IT-driven displacement of routine jobs; this paper proposes a complementary, housing-market-based explanation that does not rely on features of the production technology.

Q: What is the core mechanism linking house prices to polarization? A: When price-wage and price-rent ratios are higher in large cities, middle-income households face binding minimum-size and payment-to-income constraints that prevent them from owning a home there but not in cheaper cities. Because homeownership carries financial advantages, these households sort toward smaller, more affordable cities. Low-income households cannot afford ownership anywhere and high-income households can afford it anywhere, so only the middle group’s location choice is distorted by tenure considerations. This selective out-migration hollows out the middle of the income distribution in expensive large cities.

Q: What empirical patterns in CZ-level data motivate the paper? A: Doubling CZ size is associated with a 1.9 percentage point greater fall in the middle-skilled employment share and a 2.7 point higher growth in 100x the variance of log wages from 1980 to 2019. Larger CZs also experienced 3.4% higher price growth, 3.1% higher price-wage ratio growth, and a 10% greater increase in price-rent ratios. These associations persist after controlling for initial CZ size and other characteristics.

Q: What do the OLS and IV results show about house prices and polarization? A: A doubling of house prices is associated with a 1 percentage point decline in the middle-skilled share; a doubling of the price-rent ratio with an 11.3 percentage point decline; and a doubling of the price-wage ratio with a 5.3 percentage point decline. IV results using the interaction of land unavailability and the change in real interest rates as an instrument confirm the negative relationship remains statistically significant, suggesting a causal interpretation is plausible.

Q: What do the OLS and IV results show about house prices and income inequality? A: A doubling of prices is associated with a 2.3 point increase in 100x the variance of log wages; a doubling of the price-rent ratio with an 11.7 point increase; and a doubling of the price-wage ratio with a 7.7 point increase. IV results suggest a causal relationship between price growth and income inequality at the CZ level.

Q: What evidence does the paper provide for the migration mechanism? A: Using 2001–2019 CPS ASEC data (which reports stated reasons for moving, unlike the ACS), the paper estimates logit regressions of interstate migration for housing-related reasons. A doubling of the price index in the origin state relative to the destination raises the probability of a housing-related move for middle-income (2nd–4th quintile) households by 5–6 percentage points; a doubling of the price-wage ratio raises it by 6–7 percentage points; and a doubling of the price-rent ratio raises it by 7–10 percentage points. These effects imply a 50–80% relative increase in housing-related migration probability for the middle quintiles compared with the bottom or top quintile. Housing-related movers constitute over 12% of all interstate migrants in the sample.

Q: What is the key finding about homeownership rates? A: There is no statistically significant relationship between the change in homeownership rates and the growth in prices, price-rent, or price-wage ratios from 1980 to 2019. This is consistent with the model’s mechanism, in which middle-income households who cannot afford ownership in large cities move away rather than simply switching to renting there — so aggregate local ownership rates need not fall.

Q: How does the theoretical model generate the polarization result? A: The model extends the Rosen-Roback spatial equilibrium framework with skill heterogeneity and housing tenure choice. Two skill thresholds — one for minimum-size-constrained ownership and one for unconstrained ownership — interact with the price-wage and price-rent ratios of each city. Proposition 1 proves that a city with higher price-wage and price-rent ratios will have a lower middle-skilled share, because middle-skilled workers (those who can afford to own in cheap but not expensive cities) are drawn to cheaper locations. Proposition 2 shows that in a world with only renters or only owners, skill shares would be identical across cities regardless of price differences — the polarization result requires heterogeneity in tenure choice.

Q: What does the no-SBTC counterfactual show? A: Holding the parameters governing local returns to skills at their 1980 levels (shutting down skill-biased technical change) reduces the difference in the decline in the middle-skilled share between large and small CZs by 54% and the gap in the increase in the variance of log wages by 73%. This is broadly consistent with prior literature attributing the bulk of disproportionate polarization and inequality in big cities to SBTC.

Q: What do the constant price-ratio counterfactuals show? A: When price-wage ratios are held at 1980 levels (but SBTC is allowed to operate), the excess polarization gap between large and small CZs falls by 93% and the excess inequality gap by 40%. When price-rent ratios are held at 1980 levels, the polarization gap falls by 96% and the inequality gap by 27%. When both are held constant simultaneously, the polarization gap falls by 89% and the inequality gap by 27%. These results show that the effect of SBTC on polarization would be 63–81% smaller in the absence of the housing affordability amplification channel.

Q: Who are the largest losers from rising price-wage ratios in large cities? A: The counterfactual welfare analysis identifies middle-skilled workers with skill levels between approximately 0.29 and 0.80 as the primary losers. In the counterfactual with fixed price-wage ratios, workers with skills from 0.29 to 0.57 who previously could not afford ownership in large cities are now able to own there, and those with skills from 0.57 to 0.80 spend a smaller share of income on housing. This group either lost homeownership opportunities or was induced to move to less productive CZs by the actual price growth that occurred.

Q: How is the quantitative model calibrated and structured? A: The model is calibrated separately for 1980 and 2019 as two stationary spatial equilibria. It features two locations (the top 30 CZs, which account for 49.3% of employment, and the remaining CZs). Key parameters include a Frechet elasticity of 6.1, an agglomeration externality of 0.04, a PTI constraint of 0.308, and an annual discount factor of 0.96. Land shares differ between large and small CZs (0.3965 vs. 0.2239). The model finds that the price-rent ratio was relatively stable in large cities but fell in small ones, while the price-wage ratio increased much more in large CZs — both indicators point to purchasing a home becoming relatively more expensive in large CZs.

Q: What are the paper’s policy implications? A: Zoning reforms and other policies that increase housing supply in large, unaffordable cities could produce a more efficient spatial allocation of labor, greater aggregate productivity, and more economically diverse — less polarized and less unequal — cities, while also reducing the wealth gap between owners and renters. Policies that promote homeownership by reducing the cost of owning without raising housing supply may reduce local polarization and inequality but could lower aggregate output and do not necessarily increase homeownership rates.

Q: How does this paper relate to existing explanations for city-level polarization? A: The paper’s housing-market mechanism is explicitly complementary to SBTC-based explanations (Baum-Snow, Freedman, and Pavan, 2018; Cerina et al., 2023), external demand shock explanations (Davis, Mengus, and Michalski, 2020), and IT-displacement explanations (Eeckhout, Hedtrich, and Pinheiro, 2024). The paper’s key added contribution is that even if SBTC were the primary driver of disproportionate polarization, its measured effect would be substantially smaller in the absence of faster house price growth in large cities — the housing market amplifies rather than replaces the technology channel.

Job polarization (city-level): The hollowing out of middle-income employment shares in a commuting zone, measured as the change in the share of workers in occupations assigned to the 21st–80th income percentile (using the 1980 occupation-to-percentile mapping fixed over time). In this paper, polarization is greater in cities where price-wage and price-rent ratios grew faster, attributed to selective out-migration of middle-skilled households.

Price-wage ratio: The ratio of hedonic house prices to median annual wages in a commuting zone, constructed from Census and ACS data. A higher price-wage ratio tightens the payment-to-income constraint on potential homebuyers and is the primary driver of the skill threshold for homeownership in the model.

Price-rent ratio: The ratio of hedonic house prices to rents in a commuting zone. In the model, a higher price-rent ratio reduces the financial advantage of owning over renting, raising the skill threshold at which ownership becomes optimal. The paper treats price-rent and price-wage ratios as distinct channels that both independently amplify polarization.

Housing tenure choice: The household decision to own or rent, modeled as a discrete choice made at the start of life that interacts with location choice. Ownership requires satisfying both a minimum house size constraint and a payment-to-income (PTI) constraint (lambda = 0.308). The interaction between tenure and location choices is the paper’s key model innovation; it exists only for middle-skilled workers whose income is sufficient for ownership in cheap but not expensive cities.

Skill threshold for homeownership (s*_i): The minimum skill level at which a worker in city i chooses to own rather than rent, defined by Lemma 2. This threshold is decreasing in local labor productivity and increasing in price-wage and price-rent ratios. Workers with skill below s*_i in all cities always rent; those with skill above s*_i in all cities always own; those in between face city-dependent tenure choice that distorts their location decision.

Skill-biased technical change (SBTC): In the paper’s quantitative model, SBTC is represented by faster growth in the skill dispersion parameter (alpha_it) in large CZs, reflecting differential productivity growth concentrated at the top of the skill distribution. The paper finds SBTC accounts for 54% of the polarization gap and 73% of the inequality gap in its counterfactual, but argues its effect is amplified 4–5x by the housing affordability channel.

Payment-to-income (PTI) constraint: The constraint that a homebuyer cannot spend more than a fraction lambda (calibrated at 0.308) of annual labor earnings on the annual housing payment (user cost times price times quantity). This constraint, together with the minimum house size, determines the income threshold for ownership and makes location and tenure choices interdependent for middle-skilled workers.

International Trade Responses to Labor Market Regulations

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

Overview

Research Question. This paper asks whether differences in labor market regulations — specifically payroll taxes and minimum wages — shape countries’ comparative advantage in the cross-border provision of labor-intensive services. The question has broad policy relevance: if lower labor standards confer a systematic trade advantage, countries may face pressure to race to the bottom in labor protections, and political support for economic integration may erode.

Setting and Identification. The paper exploits the EU “posting policy,” a large trade program established in 1959 that allows firms in one EU member state to temporarily send their employees to perform service contracts in another member state. In 2017, posting accounted for roughly one-third of all within-EU trade in services (approximately 2% of EU GDP), involving about 2 million workers (in full-time equivalents) in 2019. The setting is analytically attractive because competing foreign and domestic firms serve the same customers at the same physical location using shared capital, holding most determinants of comparative advantage constant while labor market regulations vary by the firm’s country of origin.

Under posting rules, payroll taxes are generally origin-based (exporting firms pay their home country’s tax rate) but become destination-based when contracts exceed a regulatory duration threshold (12 months pre-2010, 24 months from 2010–2020, 18 months from 2020 onward). Minimum wages are destination-based: foreign firms must match the importing country’s statutory minimum wage floor when it exceeds the workers’ home-country wage level. This generates the paper’s key identifying variation — payroll taxes and minimum wages vary across countries, over time, and within countries across sectors.

Data. The author uses administrative A1 social security forms filed for every EU posting contract from 2007–2018, collected from 25 EU member states, supplemented by micro-level national posting registries in Belgium (LIMOSA), France (SIPSI), and Luxembourg (matched employer-employee data). Labor cost data (wages, payroll tax rates, minimum wages) come from Eurostat and the OECD Taxing Wages Dataset.

Methodology. The paper proceeds in three steps. First, it documents steady-state cross-sectional correlations between bilateral posting flows and labor cost differentials. Second, it estimates difference-in-differences (DiD) elasticities from four quasi-natural experiments. Third, it estimates a theory-consistent gravity model using all sources of variation across 25 EU countries from 2009–2018.

Main Findings.

Steady-state correlation: A strong negative relationship exists between bilateral posting flows and labor cost differentials, with a cross-sectional elasticity of approximately –0.58 (SE 0.08). In sharp contrast, the relationship between bilateral goods trade and labor cost differentials is weak and if anything marginally positive (point estimate +0.13), confirming that labor cost differences are a distinctive driver of trade specifically in labor-intensive services rather than goods.
Belgian tax shift (2016–2018): When Belgium cut employers’ social security contributions from 33% to 25%, imports of posting services into Belgium slowed relative to France (a neighboring control country on parallel pre-reform trends). The reduced-form elasticity of posting imports with respect to the payroll tax rate is 1.45 (SE 0.3).
Luxembourg EU regulation reform (2010): A new EU regulation required temporary employment agencies in border regions to pay destination-based payroll taxes, raising statutory rates faced by Luxembourgish exporters from 15% to 44%. Posting exports from Luxembourg’s temporary employment sector fell by 40% relative to the pre-reform level and relative to the domestic (control) sector, while the sheltered road transportation sector showed no response. The reduced-form elasticity with respect to the statutory payroll tax rate is –1.55 (SE 0.24), and the triple-difference estimate is –1.37 (SE 0.08).
Bunching at duration thresholds: The distribution of posting contract lengths in France (which has the EU’s highest payroll taxes) shows a sharp spike just below the 24-month payroll tax threshold. When the threshold was moved to 18 months in 2020, excess mass migrated to the new threshold, confirming that bunching reflects behavioral responses to the tax notch rather than reference-point effects. This documents that payroll tax differentials shape not only the quantity (extensive margin) but also the length (intensive margin) of posting contracts.
German minimum wage reform (2015): Germany’s introduction of a national minimum wage of €8.50 per hour — which was already binding on construction workers through a sectoral minimum, but not on foreign firms providing non-construction services — caused postings to Germany in manufacturing to fall by approximately 60% relative to the construction (control) sector. The reduced-form elasticity is –1.34 (SE 0.43). Heterogeneity analysis shows that export declines were monotonically larger for low-wage origin countries where the new minimum wage was binding, and placebo estimates using Germany’s high-wage neighboring countries (where minimum wage requirements did not change) are statistically indistinguishable from zero.
Gravity estimates: The preferred specification (PPML with origin-year, destination-year, and pair fixed effects, exploiting bilateral variation in minimum wage bindingness across origin countries) yields a model-implied trade elasticity θ of –1.2 (SE 0.2). The range across specifications is –1.2 to –2.4. These estimates are smaller than the goods trade elasticity (typically estimated around 5) and below the medium-run reduced-form elasticities from the DiD case studies, consistent with short-run gravity estimates capturing only partial adjustment while DiD designs measure longer-run equilibrium responses.

Policy Counterfactual. The paper’s estimates imply that the Bolkestein Directive — which proposed exempting foreign firms from all destination-country labor regulations — would have doubled exports of physical services from Eastern European countries (upper bound), as their cost advantage would have been dramatically amplified by removal of minimum wage requirements. Counterpart to this export boom, average posted workers’ wages would have fallen by approximately 16%, since workers would lose their entitlement to destination-country minimum wages. The paper documents that the Bolkestein controversy — sparked by the “Polish plumber” debate in early 2005 — coincided with a sharp and persistent drop in French voter support for the EU constitutional treaty, which was subsequently rejected.

Scope Conditions. Results apply specifically to trade in physical (labor-intensive) services traded via temporary worker posting within the EU, where productivity differences across countries for these tasks are plausibly small (Balassa-Samuelson), making institutional factors a primary driver of wage differences. The paper estimates intent-to-treat effects, assuming perfect compliance by exporting firms. The paper does not perform a comprehensive welfare analysis covering consumer price effects or general equilibrium wage and trade-balance responses.

In depth

Q1. What is the EU posting policy and why does it provide an unusually clean setting for identifying the causal effect of labor regulations on trade?

The EU posting policy, established in 1959, allows firms in one EU member state to temporarily send employees to perform service contracts in another member state. The policy keeps most determinants of comparative advantage constant — competing foreign and domestic firms serve the same customers at the same physical location using shared capital — while labor market regulations vary by the firm’s country of origin. Productivity differences for physical services across countries are also plausibly limited (Balassa-Samuelson), making institutional wage differences the primary cost driver. Enforcement is facilitated by the on-site nature of the service, and administrative A1 forms create a direct measure of the number of workers involved in cross-border transactions without a minimum reporting threshold.

Q2. What are the three sources of labor cost differences the paper identifies and quantifies?

Foreign firms competing for posting contracts face different costs through three channels: (i) equilibrium gross wages differ across origin countries, reflecting both productivity differences and institutional/information frictions that allow wage discrimination between posted and domestic workers; (ii) payroll tax rates are origin-based and differ substantially across countries (for example, France’s employer payroll tax is approximately 40% versus approximately 15% for Luxembourg before the 2010 reform); and (iii) destination-specific minimum wages impose a “posting allowance” on firms from countries with lower wages, equal to the shortfall between the firm’s home-country wage and the importing country’s minimum wage floor. Micro-level wage data from France confirm that most posted workers from low-wage countries are paid exactly at the French minimum wage, demonstrating the bindingness of the third channel, while French workers performing the same tasks receive wages near the French average (approximately €21.1 per hour versus a minimum wage of approximately €10 per hour in 2018).

Q3. What does the cross-sectional evidence show about the relationship between labor cost differentials and posting flows, and how does this compare to goods trade?

Bilateral posting flows and bilateral labor cost differentials have a tight negative cross-sectional relationship with an estimated elasticity of –0.58 (SE 0.08), indicating that countries export more posting services when their labor costs are substantially below those of the destination country. The same exercise applied to bilateral goods trade yields a coefficient of +0.13 (SE 0.07) — weak and marginally positive — consistent with goods trade being driven by capital, technology, and scale rather than labor cost differentials. The gap confirms that labor cost differences are a distinctive comparative advantage mechanism for labor-intensive services but not for less labor-intensive goods.

Q4. What does the Belgian tax shift reform demonstrate, and how is identification established?

Belgium cut employer social security contributions from 33% to 25% between 2016 and 2018 in a revenue-neutral reform (financed by VAT, excise duties, and dividend taxes). The DiD compares posting imports into Belgium with those into France (a neighboring, similarly sized importer on parallel pre-reform trends). Belgium and France imported posting services at similar rates before 2015; Belgian imports slowed immediately after the reform while French imports continued growing. The reduced-form elasticity of posting flows with respect to the destination payroll tax rate is 1.45 (SE 0.3). The elasticity with respect to total labor cost is 3.7 (SE 0.7). No discernible response is detected for trade in manufacturing goods, providing a within-reform placebo. A synthetic control using all available importing countries yields a smaller elasticity of 0.6 (SE 0.22).

Q5. How does the Luxembourg EU regulation reform (2010) improve on the Belgian case for identification?

The 2010 EU regulation required temporary employment agencies in border regions to pay destination-based (rather than origin-based) payroll taxes, raising statutory rates for Luxembourgish exporters from 15% to 44%. Unlike the Belgian reform, this created within-country variation: the same Luxembourgish firms were exposed in the temporary employment sector but not in road transportation (which received a 10-year exemption). This within-exporter, cross-sector design controls for all Luxembourg-wide demand or supply shocks. Posting exports by the temporary employment sector fell 40% relative to pre-reform levels and relative to the domestic (control) sector, while road transportation posting showed zero response. The monthly data confirm the drop occurred in the exact month following the regulation with no anticipation. The triple-difference elasticity (with respect to the payroll tax rate) is –1.37 (SE 0.08).

Q6. What does the bunching evidence at payroll tax duration thresholds add to the DiD findings?

When posting contracts exceed a regulatory duration threshold (24 months during 2010–2020, then 18 months from July 2020), payroll taxes become destination-based. Because France has the highest payroll tax in the EU, all exporting firms face strong incentives to avoid crossing the threshold. The distribution of posting contract lengths in France shows sharp excess mass just below 24 months in 2017. When the threshold moved to 18 months in 2020, the excess mass migrated to the new threshold while diminishing at the old one, confirming that bunching is tax-motivated rather than driven by a reference-point at 24 months. This establishes that labor tax differentials shape not only the quantity of posting contracts (extensive margin) but also their length (intensive margin).

Q7. What are the main findings from the German minimum wage reform, and how do the heterogeneity tests strengthen identification?

Germany’s January 2015 introduction of a national minimum wage of €8.50 per hour (preceded by a sectoral minimum in meat processing in August 2014) raised wage costs for foreign firms providing non-construction services, but not for construction firms already covered by a higher sectoral minimum. Postings to Germany in manufacturing fell by approximately 60% relative to the construction (control) sector, implying a reduced-form elasticity of –1.34 (SE 0.43). Two heterogeneity tests reinforce identification: (i) within the treated German sector, posting declines are monotonically increasing in the degree to which the new minimum wage is binding in the origin country, with Luxembourg (where the minimum is non-binding) showing no statistically significant effect; (ii) the same industry-by-country comparison in Germany’s high-wage neighboring countries (which did not change minimum wage rules) yields placebo estimates statistically indistinguishable from zero. The reform raised wages for German workers by an average of 6% (and up to 10% for most affected workers) but automatically raised wages for posted workers by an average of 40%, doubling them for workers from the poorest sending countries.

Q8. How do the gravity model estimates compare to the reduced-form DiD estimates, and what explains the difference?

Across gravity specifications, model-implied elasticities range from –0.75 to –2.4. The preferred specification — PPML with pair fixed effects, destination-year fixed effects, and origin-year fixed effects — yields θ = –1.2 (SE 0.2). These estimates are systematically below the medium-run reduced-form DiD estimates because: (a) the gravity model uses nationwide average tax and minimum wage measures that introduce measurement error relative to the sector-specific reforms in the case studies; and (b) the gravity model captures year-to-year (short-run) adjustments, while the DiD designs compare outcomes several years before and after the reform, picking up longer-run equilibrium reallocation. The finding that responses grow over time mirrors evidence on dynamic adjustment in goods trade (Boehm, Levchenko and Pandalai-Nayar, 2023), and contradicts the conventional belief that fiscal devaluations boost exports only in the short run.

Q9. What does the gravity model reveal about trade in goods as a function of posting-specific wage costs?

When the same gravity specification is applied to bilateral goods trade rather than posting flows, posting-specific wage costs have a positive — not negative — coefficient on goods trade. This is inconsistent with a model where unobserved shocks affect all exports symmetrically, and instead suggests a small substitution effect: as the cost to import labor services rises (due to tighter posting regulations), countries substitute toward importing goods. For some activities (such as meat processing), importing finished goods is a partial substitute for importing labor services to produce on-site.

Q10. What are the Bolkestein Directive counterfactual implications, and how do they connect to the political economy evidence?

The Bolkestein Directive (proposed 2005) would have enforced a “country of origin principle,” exempting foreign posting firms from destination-country minimum wages. Using the preferred lower-bound elasticity from the gravity model (column 5, θ = –1.2) and an upper bound averaging gravity and DiD estimates, the paper predicts this would have at least doubled exports of labor services from Eastern European countries. Tax revenues collected on posted workers in origin countries would also double. However, average posted workers’ wages would fall by approximately 16%, as workers would lose their entitlement to destination-country minimum wages. The paper documents that the Bolkestein controversy — introduced to the EU Parliament in March 2005 and popularized via the “Polish plumber” trope — coincided with a sharp and permanent drop in French voter support for the EU constitutional treaty, which was subsequently rejected in referendum. This is consistent with Rodrik’s (1998) hypothesis that voters withdraw support for economic integration when comparative advantage appears to be based on institutional choices that conflict with importing countries’ social norms.

Q11. How does the paper handle the incidence of payroll taxes — does the canonical result that payroll taxes are fully passed through to workers hold in this context?

The canonical competitive labor market model predicts full pass-through of payroll taxes to workers’ net wages, leaving firms’ labor costs unchanged. The paper finds substantial trade responses to payroll tax reforms, inconsistent with full pass-through. Nominal rigidities — including binding minimum wages that constrain downward wage adjustment — help rationalize incomplete pass-through in the EU context. The paper estimates elasticities both with respect to statutory tax rates (the reduced-form, making no incidence assumption) and with respect to total wage costs (instrumented with the reform, allowing for gross wage responses). Wage data from Belgium show no distinguishable wage response to the Belgian tax cut, suggesting the incidence fell largely on firms’ costs rather than workers’ wages in that episode.

Q12. What do the destination-based taxation counterfactual (tax cooperation proposal) calculations show?

A proposal to shift all posting payroll taxation to destination-based rates would decrease posting exports from Eastern European countries by between 10% and 25%. Despite the volume reduction, total taxes collected on posted workers would still increase under this reform even when the upper-bound elasticity (approximately –3.7 with respect to total wage cost) is used, because a 1% increase in the payroll tax rate translates to a much smaller proportional increase in total wage cost.

Key Concepts

Posted workers / posting policy: Employees temporarily sent by their employer (the “exporting firm”) to perform a service contract in another EU member state. Posted workers maintain their employment contract with the firm in the origin country but physically work in the destination country. This creates a setting where competing domestic and foreign firms serve the same customers at the same location under different labor regulations.

Posting allowance: The additional wage component that exporting firms must pay to posted workers to satisfy the destination country’s minimum legal wage when that minimum exceeds the firm’s home-country wage level. The posting allowance is zero when the exporting country’s average wage already exceeds the destination minimum wage; it can be large for low-wage origin countries. The allowance enters directly into firms’ labor costs and is the minimum-wage channel of the paper’s labor cost formula.

Origin-based vs. destination-based payroll taxation: Under posting, payroll taxes are normally assessed in the country where the exporting firm is registered (origin-based), creating tax rate differentials between competing firms in the same job site. EU regulations convert payroll taxes to destination-based when posting contracts exceed a duration threshold, eliminating the tax advantage of lower-tax origin countries for those contracts. The 2010 EU regulation additionally imposed destination-based taxation on border-region temporary employment agencies.

Trade elasticity for physical services (θ): The structural parameter from the Eaton-Kortum (2002) gravity model that governs the elasticity of bilateral posting flows with respect to changes in firms’ total wage costs when exporting services from country i to country j. The paper’s preferred estimate is –1.2 (from gravity estimation) to approximately –1.3 to –1.5 (from reduced-form DiD designs), substantially smaller in absolute value than the goods trade elasticity (typically estimated around 5).

Social standards as comparative advantage: The paper uses “standards” to refer to countries’ domestic policy choices about payroll taxes (which finance social insurance programs) and minimum wages (which set worker protection floors). The paper demonstrates that these regulatory choices — distinct from productivity differences, factor abundance, or technology — create measurable cost advantages that shape specialization in labor-intensive service sectors. This is in contrast to “benign” sources of comparative advantage.

Bolkestein Directive / country of origin principle: A 2005 EU legislative proposal that would have required posting firms to operate under the laws of their home country when supplying services in other EU member states, eliminating the hard core of destination-country regulations (including minimum wages) that the 1996 Posted Workers Directive had imposed on foreign firms. The proposal was withdrawn after a wave of protests and its association with a sharp fall in French support for the EU constitutional treaty.

Bunching / notch at duration threshold: A behavioral response in which exporting firms strategically keep posting contract lengths below the duration threshold that triggers destination-based payroll taxation, generating an excess mass in the distribution of contract lengths just below the threshold. The paper uses this bunching, together with the movement of the threshold from 24 to 18 months in 2020, as additional evidence that payroll tax differentials affect the intensive margin of posting.

Labor Market Competition and the Assimilation of Immigrants

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

Labor Market Competition and the Assimilation of Immigrants

Research Question

Why have immigrant-native wage gaps widened substantially across arrival cohorts in the United States since the 1960s, and why has the speed of wage convergence slowed? The paper argues that the existing literature, which attributes these trends entirely to declining immigrant cohort quality, omits a critical general-equilibrium channel: labor market competition arising from imperfect substitutability between immigrants and natives. The paper quantifies how much of the observed deterioration in wage assimilation profiles can be attributed to (i) increasing immigrant cohort sizes raising labor market competition, (ii) secular shifts in relative skill demand, and (iii) genuine changes in immigrant cohort quality.

Data and Methodology

The analysis uses U.S. Census microdata for 1970, 1980, 1990, and 2000, combined with American Community Survey (ACS) data pooled for 2009–2011 (labeled 2010) and 2018–2019 (labeled 2020), all drawn from IPUMS-USA. The sample covers individuals aged 25–64 who are employed in the civilian sector, not self-employed, not in group quarters, and report positive earnings. Immigrant cohort sizes grew from approximately 800,000 individuals in the 1960s cohort to 2.3 million in the 1980s cohort and 4.6 million in the 2000s cohort.

The theoretical framework is a constant elasticity of substitution (CES) production function in which workers supply two types of skills: “general” skills portable across countries and “specific” skills particular to the host country (including language proficiency and knowledge of cultural and institutional environment). Immigrants arrive with the same general skills as observationally equivalent natives but only a fraction of their specific skills; they accumulate specific skills over time. Because immigrants disproportionately supply general skills upon arrival, increasing immigrant inflows raise the relative supply of general skills, depress the relative price of general skills, and thereby widen the immigrant-native wage gap. This mechanism operates only when immigrants and natives are imperfect substitutes (elasticity of substitution σ < ∞).

The model is estimated in two steps using nonlinear least squares (NLS). First, productivity factor parameters are estimated from native wages year by year, with state dummies identifying state-level skill prices. Second, specific skill accumulation parameters and the elasticity of substitution σ are jointly identified from immigrant wage differences across labor markets (defined as U.S. states) and over time. The demand shift parameter δ_t, which captures changes in the relative demand for specific skills (e.g., technology that favors communication over manual tasks), enters as a linear time trend in the baseline specification.

Main Findings with Quantitative Magnitudes

Competition effect: Immigration-induced increases in labor market competition explain 14.2, 43.9, and 40.8 percent of the increase in the initial wage gap of the 1970s, 1980s, and 1990s cohorts relative to the 1960s cohort, respectively. Averaged across all years spent in the United States, the competition effect alone accounts for 14.1, 22.4, and 20.4 percent — approximately one fifth overall.

Competition plus demand effect: Adding secular shifts in relative skill demand raises these figures to 24.8, 68.3, and 109.5 percent at arrival and 21.2, 33.6, and 36.4 percent averaged across years — approximately one third overall.

Elasticity of substitution: The baseline estimate of σ (elasticity of substitution between general and specific skills) is 0.020 (s.e. 0.002), implying an inverse elasticity of approximately 50.5. The relative supply of general skills increased by 1.67 log points between 1970 and 2020, producing a predicted increase in the relative price of specific skills of approximately 59.6 log points. The demand shift trend is estimated at 1.3 log points per year.

Cohort quality: Once competition and demand effects are netted out, the remaining deterioration in assimilation profiles is entirely attributable to observable changes in immigrants’ educational attainment and country-of-origin composition. Conditional on these two observable characteristics, unobservable skill quality improved across cohorts (consistent with English language proficiency trends), reversing the conventional narrative of declining cohort quality.

Specific skills gap at arrival: The 1960s cohort faced a specific skills gap of approximately 52.4 percent relative to native equivalents; this narrowed to 41.8 percent for the 1970s cohort, 35.6 percent for the 1980s cohort, and 17.6 percent for the 1990s cohort, conditional on origin and education. After 20–30 years, all cohorts reach 83.7–92.0 percent of their native counterparts’ specific skill levels.

Scope Conditions

The analysis focuses on employed men in the main text (women are analyzed in an Online Appendix, showing qualitatively similar but quantitatively smaller patterns).
Labor markets are defined at the U.S. state level in the baseline; robustness checks use state-education and state-gender cells.
The decomposition covers the period from the 1960s to the 1990s arrival cohorts.
Results are robust to corrections for selective outmigration, undercounting of undocumented immigrants, immigrant network effects, alternative demand shift specifications, alternative labor market definitions, and endogenous immigrant location choice (using shift-share instruments in the spirit of Card, 2001).

In depth

Q1. What is the core theoretical mechanism by which increasing immigrant inflows widen the immigrant-native wage gap?

A: Because immigrants disproportionately supply general (country-portable) skills upon arrival, while natives disproportionately supply specific (host-country) skills, an increase in immigrant inflows raises the ratio of general to specific skills in the economy. Under imperfect substitutability (σ < ∞), this lowers the relative price of general skills and raises the relative price of specific skills, thereby widening the wage gap between immigrants (who earn predominantly from general skills) and natives (who earn more from specific skills). The effect is larger in the early years after arrival when immigrants’ specific skill endowment s is small, and diminishes as immigrants accumulate specific skills over time.

Q2. How does the paper model immigrants’ skill accumulation, and how do accumulation profiles differ across groups?

A: Immigrants’ specific skill endowment s(·) upon arrival and over time is modeled as a flexible polynomial in years since migration, interacted with dummies for region of origin, education, cohort of entry, and potential experience abroad. Mexican high school dropouts (the reference group) are estimated to arrive with approximately 80 percent of the specific skills of equivalent natives. Immigrants from Latin America, Asia, and other regions arrive with lower specific skills than Western immigrants, who arrive near native parity. Higher-educated immigrants arrive relatively less similar to equivalently educated natives than low-educated immigrants, reflecting the greater importance of language-intensive skills in high-skill occupations. Conditional on origin and education, more recent cohorts arrive with narrower specific skill deficits: the 1990s cohort faces a gap of 17.6 percent at arrival compared to 52.4 percent for the 1960s cohort.

Q3. What are the estimated technology parameters, and how are they interpreted?

A: The elasticity of substitution between general and specific skills is estimated at σ = 0.020 (s.e. 0.002), with a confidence interval of [0.017, 0.024]. This implies an inverse elasticity of approximately 50.5, meaning a one percent increase in the relative supply of general skills raises the relative price of specific skills by about 50.5 percent. The implied elasticity of substitution between natives and immigrants (evaluated at market-level averages) is approximately 0.013 in 1990, 0.020 in 2000, and 0.025 in 2010 — in the same range as the Ottaviano and Peri (2012) benchmark of 0.034 (s.e. 0.008). The demand shift trend is estimated at δ̃ = 0.013 (s.e. 0.001) log points per year, reflecting secular increases in the relative demand for specific (host-country) skills.

Q4. How does the paper identify the elasticity of substitution σ and the skill accumulation parameters separately?

A: The estimation proceeds in two steps. First, productivity factor parameters (returns to education and experience) are estimated from native wage regressions, with state-year dummies absorbing state-specific skill prices. Second, skill accumulation parameters θ are identified from wage differences between immigrants with different characteristics working in the same labor market, while σ and the demand shift δ̃ are identified from variation in immigrant wage gaps across states (which have different immigrant population shares) and over time. Specifically, states with higher immigrant shares display lower relative prices of general skills, providing the identifying variation for σ.

Q5. What are the quantitative magnitudes of the competition effect for specific cohorts at different time horizons?

A: At the time of arrival, the competition effect explains 14.2 percent (1970s cohort), 43.9 percent (1980s cohort), and 40.8 percent (1990s cohort) of the increase in initial wage gaps relative to the 1960s cohort. After 10 years, these figures are 17.1, 22.7, and 22.2 percent respectively. After 20 years, they are 12.2, 16.9, and 16.2 percent. After 30 years, 10.9, 15.3, and 13.7 percent. The declining share across years reflects the fact that as immigrants accumulate specific skills, their wages become less sensitive to equilibrium skill prices. Averaged across all years since migration, the competition effect accounts for 14.1, 22.4, and 20.4 percent for the three cohorts.

Q6. How does labor market competition affect the speed of wage assimilation, and does it prevent full convergence?

A: The effect on assimilation speed is theoretically ambiguous and depends on whether future cohorts are larger or smaller than the reference cohort, and whether immigrants fully converge to native skill levels. In the stylized examples, a one-time permanent increase in competition raises both the initial wage gap and the speed of subsequent convergence (since the gap between immigrant and native skill levels is larger and therefore more responsive to changes in skill prices). However, continuous inflows of increasingly large cohorts counteract this speedup by continuously shifting the wage profile downward — the “dynamic competition effect.” For immigrants who fully converge (s → 1), competition delays but does not prevent convergence; for those who only partially converge (s → < 1), competition permanently widens the long-run wage gap. Quantitatively, the paper finds the effect on assimilation speed to be small in the full-sample decomposition.

Q7. What do the illustrative examples for specific immigrant groups reveal about heterogeneous competition effects?

A: For a Mexican male high school dropout (1960s cohort skills), facing the same competition level as the 1990s cohort would widen the initial wage gap by 10.2 log points; facing 2010 competition levels would widen it by 21.1 log points. However, because this group fully converges (s → 1), the effect dissipates entirely after approximately 25 years, and long-run wage assimilation is not prevented. For a Latin American male high school graduate who only partially converges (s → < 1), facing 1990s competition would widen the initial gap by 17.4 log points and leave a 3.8 log-point larger long-run wage gap. For a Western college graduate who arrives near native skill parity, competition effects are negligible throughout.

Q8. What are the changes in absolute wage gaps documented in the baseline data?

A: The 1960s cohort arrived with an initial wage gap of approximately 17.2 log points relative to natives. The 1970s cohort arrived with a gap of 30.1 log points, the 1980s cohort 29.2 log points, and the 1990s cohort 20.8 log points. Under the no-competition counterfactual, these initial gaps narrow to 13.6, 24.7, 20.3, and 15.7 log points respectively. Removing both competition and demand effects further narrows them to 13.7, 23.4, 17.5, and 13.3 log points.

Q9. What does the paper find about the role of observable versus unobservable immigrant quality?

A: Once competition and demand effects are accounted for, all remaining cohort differences in assimilation profiles are attributable to observable changes in immigrants’ educational attainment and country-of-origin composition. Conditional on these two observable characteristics, immigrants in more recent cohorts display higher levels of unobservable skills (smaller specific skill deficits conditional on origin and education), consistent with rising English language proficiency across cohorts. This reverses the standard interpretation that unobservable immigrant quality has declined.

Q10. How do aggregate skill supplies and relative skill prices evolve over the sample period?

A: Between 1970 and 2020, the total supply of general skills from immigrants grew by a factor of 16.3, while the supply of specific skills grew by a factor of 15.0. The resulting increase in the relative supply of general skills caused the relative price of general skills to fall from 0.89 to 0.38. Accounting for growing relative demand for specific skills (the δ_t trend), the ratio of relative skill prices fell further to 0.20 by 2020. At the state level, relative prices of general skills are well below 0.3 in high-immigration states like California, Florida, and New York, and approach 1.0 in states with low immigrant shares.

Q11. Are the results robust to selective outmigration, undocumented immigrants, and alternative specifications?

A: Yes. Across twelve robustness checks covering selective outmigration corrections (using Borjas and Bratsberg 1996 or Rho and Sanders 2021 outmigration rates, and synthetic cohort reweighting), undocumented immigrant undercounting corrections, immigrant network controls (share and stock of compatriots in the same state), alternative demand shift specifications (quadratic and time dummies), alternative labor market definitions (state-education and state-gender cells), and endogenous immigrant location choice (GMM with shift-share instruments), the estimated elasticity of substitution σ ranges from 0.017 to 0.033 and the average competition effects remain stable. Averaged across all robustness checks, competition effects are 1.3 log points (1960s cohort), 3.0 log points (1970s), 5.2 log points (1980s), and 4.3 log points (1990s), compared to baseline values of 1.4, 3.1, 5.5, and 4.6 log points.

Q12. What are the policy implications highlighted by the authors?

A: First, since assimilation and competition effects are intertwined, the wage impact of immigration on natives is intrinsically dynamic: newly arrived immigrants initially compete relatively little with natives but increasingly substitute for them as their specific skills grow. Second, labor market competition may reduce immigrants’ incentives to invest in host-country-specific skills, a channel not modeled in most existing structural models. Third, dispersal policies (such as those used during refugee crises) that reallocate immigrants across regions will affect local skill price ratios and therefore alter wage assimilation trajectories — a potentially unintended consequence of geographic allocation policies.

Key Concepts

General skills: Skills that are portable across countries and can be used productively in any labor market. In the paper’s framework, general skills are those required for tasks (such as manual or physical labor) that are similar across national contexts. Upon arrival, immigrants are assumed to supply the same amount of general skills as observationally equivalent natives, making immigrants’ relative supply of general skills high at arrival.

Specific skills (host-country-specific skills): Skills particular to the host country, including language proficiency (English in the U.S. context) as well as familiarity with the institutional and cultural environment. Immigrants arrive with only a fraction s of the specific skills of comparable natives; this fraction evolves over time as immigrants spend time in the host country. The level of specific skills governs how substitutable a given immigrant worker is with native workers.

Labor market competition effect: The mechanism by which increasing immigrant inflows affect relative wages through equilibrium changes in skill prices rather than through individual skill accumulation. When immigrants and natives are imperfect substitutes, rising immigrant inflows raise the relative supply of general skills, depress the relative price of general skills, and widen the immigrant-native wage gap. This effect is larger for recently arrived immigrants (small s) and diminishes as immigrants assimilate.

Dynamic competition effect: The combined effect on a given cohort’s observed assimilation profile of continuous, growing immigrant inflows over its time in the country. Unlike a one-time permanent increase in competition (which would raise both the initial gap and assimilation speed), continuously growing inflows both widen the initial gap and exert a continuous downward shift on the cohort’s wage profile, with an ambiguous net effect on the speed of convergence.

Demand shift (δ_t): A time-varying parameter in the CES production function capturing secular changes in the relative demand for specific versus general skills beyond what is explained by standard skill-biased technological change. A positive trend in δ_t (estimated at 1.3 log points per year in the baseline) reflects technological change that favors communication-intensive (specific-skill-intensive) tasks over manual (general-skill-intensive) tasks, and amplifies the competition effect.

Elasticity of substitution between general and specific skills (σ): The key technology parameter governing the degree of imperfect substitutability between natives and immigrants in equilibrium. Estimated at σ = 0.020 in the baseline. When σ = ∞, immigrants and natives are perfect substitutes and labor market competition has no effect on relative wages. As σ decreases, the competition effect on relative wages becomes stronger for a given change in relative skill supplies.

Specific skill accumulation function s(·): A flexible parametric function of years since migration, interacted with region of origin, education level, cohort of entry, and potential experience at arrival, that governs the rate at which immigrants acquire host-country-specific skills over time. The intercept of s(·) at arrival (relative to a native s = 1) measures the initial specific skill deficit; the polynomial in years since migration captures how quickly this deficit closes.

Wage assimilation profile: The trajectory of the immigrant-native log wage gap as a function of years spent in the host country, conditional on a cohort of arrival. The paper distinguishes between changes in the level of the profile (the initial wage gap) and changes in its slope (the speed of convergence), and decomposes both dimensions into competition effects, demand effects, and cohort quality effects.

Labor Market Shocks and Monetary Policy

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

Overview

Research question. The paper asks two related questions: (1) How much, and through which channels, do employer-to-employer (EE) worker transitions affect macroeconomic outcomes — particularly inflation? (2) What is the optimal monetary policy within a class of Taylor rules when EE flows are taken explicitly into account?

Motivation. Standard monetary policy frameworks condition on the unemployment rate as the primary labor market slack measure and underemphasize the “quality” dimension of employment. The paper documents a striking empirical pattern: the 2016–2019 recovery and the 2021–2022 recovery from COVID-19 featured nearly identical declines in the unemployment rate, yet exhibited dramatically different EE rate dynamics and inflation outcomes. During 2016–2019, the EE rate remained flat despite a roughly 25 percent decline in the unemployment rate from trend. During 2021–2022, the EE rate rose by around 8 percent above trend over a comparable unemployment decline. Correspondingly, unit labor cost (ULC) growth reached approximately 6 percent during the COVID-19 recovery when unemployment fell below 4 percent, compared with only about 2 percent ULC growth in the 2016–2019 period at similar unemployment levels.

Methodology. The authors develop a Heterogeneous Agent New Keynesian (HANK) model with a frictional labor market featuring on-the-job search (OJS). Workers are heterogeneous in wealth (mutual fund shares), human capital, match-specific productivity, and endogenous piece-rate wages. Human capital stochastically appreciates when employed and depreciates when unemployed, capturing scarring effects and job-stayer wage growth. Wage determination follows a Bertrand competition protocol based on flow output: workers switch to higher-productivity matches and extract the full surplus from the new firm, while outside offers from lower-productivity firms can still trigger rebargaining with the incumbent firm and raise the piece rate without a job switch. Three vertically integrated sectors — labor services, intermediate goods, and final goods — are linked so that the real price of labor services pl is the real marginal cost for intermediate firms and the sole driver of inflation in the New Keynesian Phillips curve (absent aggregate productivity shocks). The economy is subject to AR(1) shocks to the discount rate β (demand), aggregate labor productivity z (supply), and OJS efficiency ν (the relative search efficiency of employed workers). The model is solved using the Sequence-Space Jacobian (SSJ) method, extended to handle discretized worker distributions as direct inputs to equilibrium conditions.

The model is calibrated to U.S. pre-Great Recession data (2004–2006), targeting the fraction of hand-to-mouth individuals (16 percent of SIPP sample), unemployment rate (5.1 percent), EU separation rate (3.8 percent quarterly), EE rate (2 percent quarterly from LEHD), earnings drop upon job loss (35 percent), wage growth of job switchers (9 percent), and the labor share (0.67). Shock processes are estimated by minimizing deviations from empirical correlations and standard deviations of output, unemployment, EE rate, and inflation over 1995:Q3–2008:Q4.

Main findings — positive analysis. Shocks to OJS efficiency account for 43.1 percent of fluctuations in inflation in the variance decomposition, and 78.7 percent of fluctuations in the EE rate. The mechanism: a higher OJS efficiency lowers the expected match value EJ for labor services firms through three channels — (i) a compositional shift toward employed job seekers who extract the entire match surplus, (ii) shorter expected match duration as workers face higher poaching probabilities, and (iii) more frequent wage rebargaining where outside offers bid up wages without accompanying productivity gains. To maintain the free-entry condition, the real price of labor services pl must rise, increasing the real marginal cost and inflation. This direct labor market effect explains 139 percent of the total increase in pl; general equilibrium effects through reduced tightness θ — which raises expected match values by making vacancies easier to fill and workers less likely to be poached — offset −42 percent; the remainder (3 percent) comes from real rate changes driven by the monetary policy reaction.

In two historical simulations, muted OJS efficiency during 2016–2019 generated approximately 0.23 percentage points lower annualized inflation at the peak relative to a counterfactual economy with the same unemployment path but an endogenously rising EE rate. Conversely, elevated OJS efficiency during 2021–2022 generated approximately 0.56 percentage points higher annualized inflation compared to the flat-EE-rate counterfactual. The paper notes that strong worker mobility accounts for roughly 10 percent of the approximately 6 percentage point total rise in annual inflation during the COVID-19 recovery episode.

An important cross-model comparison shows that the Representative Agent New Keynesian (RANK) version of the model overestimates the decline in demand, output, and labor market tightness upon a positive OJS shock, and underestimates the rise in real rate, marginal cost, and inflation. Household heterogeneity is therefore quantitatively important: hand-to-mouth households’ demand responds directly to labor income increases from job switches, mitigating the demand decline and amplifying inflation.

Main findings — normative analysis. The optimal monetary policy within an augmented Taylor rule — adding an EE gap term ΦEE(EEt − EE*) alongside the standard inflation and unemployment gap terms — prescribes Φ*_u = −3.18 and Φ*_EE = 2.22 (with Φπ fixed at 1.5). This yields a 78.7 percent reduction in the central bank loss relative to the baseline Taylor rule. A policy that ignores EE dynamics and optimizes only the unemployment gap coefficient (finding Φu = −2.71, ΦEE = 0) produces a 12 percent larger central bank loss than the full optimal policy. In terms of welfare, the optimal policy delivers 0.16 percent additional lifetime consumption equivalent in the aggregate. Workers at the bottom of the match quality distribution gain the most (0.24 percent), as do the unemployed (0.20 percent), while those at the top of the wealth distribution gain the least due to larger share price fluctuations under the more aggressive policy.

Scope conditions. Results are derived conditional on a dual-mandate central bank objective (variance of inflation and output gaps), within a class of Taylor-type rules (not fully optimal Ramsey policy), under first-order approximation around a non-stochastic steady state. The historical simulations abstract from supply shocks active in the normative exercises and assume the economy starts from steady state in 2016.

In depth

Q1. What is the OJS efficiency shock, and how does it differ from a standard demand or supply shock?

An OJS efficiency shock is modeled as a time-varying shift in νt, the relative job search efficiency of employed workers compared with unemployed workers. Unlike demand shocks (discount rate β innovations) and productivity shocks (aggregate z innovations), which move inflation and unemployment in opposite directions under standard New Keynesian logic (divine coincidence), OJS efficiency shocks move inflation and unemployment in the same direction: a positive OJS shock raises inflation while also raising unemployment (because the higher real rate induced by the central bank’s reaction reduces demand and employment). This makes OJS shocks behave like cost-push shocks and introduces a genuine policy trade-off for a dual-mandate central bank.

Q2. What are the three mechanisms through which higher OJS efficiency raises the real price of labor services, and what is the quantitative contribution of each?

The decomposition (Figure 8) shows that the direct effect of ν on EJ — encompassing the composition channel (more employed job seekers who extract the full surplus), the match-duration channel (shorter expected match lives), and the wage rebargaining channel (outside offers raise wages without productivity gains) — explains 139 percent of the total increase in pl. The general equilibrium reduction in labor market tightness θ, which raises EJ and partially offsets the cost increase, explains −42 percent in total: −18 percent through increased supply of labor services L (productivity-enhancing job switches improve the match distribution) and −24 percent through reduced output Y (lower aggregate demand). Real rate effects account for the remaining 3 percent net (8 percent from the inflation channel and −5 percent from the unemployment channel). Labor market effects in total therefore explain 97 percent of the marginal cost increase.

Q3. Does the positive relationship between EE rates and inflation require wage increases upon job switches?

No. The paper demonstrates (Section 2.4.2, Figure 3) that even when the piece rate for workers hired from unemployment is set to α = 0.95 (so that outside offers have negligible wage effects), a positive OJS efficiency shock still generates a decline in output and a rise in inflation in both the RANK and TANK models. Quantitatively, the inflation response is similar across the baseline and near-zero composition-channel specifications, confirming that the shorter expected match duration is the primary driver of the increase in the real price of labor services. The match duration channel operates independently of wage increases: firms anticipate shorter matches and require a higher flow price to break even on vacancy costs.

Q4. How does household heterogeneity change the quantitative effects of OJS shocks relative to the RANK benchmark?

Under a constant real rate, in the RANK model a higher OJS efficiency increases the real price of labor services and inflation but has no effect on aggregate demand or output (because higher labor income for the PIH household is exactly offset by lower firm profits). In the TANK model, hand-to-mouth households consume their entire labor income, so the rise in labor income from job switches directly boosts their demand, raising output and tightness and further amplifying inflation. Under an endogenous real rate, the RANK model overestimates the decline in demand and output, and underestimates the rise in real rate and inflation, compared with the TANK model. The TANK model requires a substantially larger equilibrium real rate increase to contain inflation because HtM households’ demand is less elastic to the real rate than PIH households'.

The six AR(1) parameters governing β, z, and ν (three persistence parameters ρj and three standard deviations σj) are estimated by minimizing the sum of squared deviations between model-generated and empirical moments: the autocorrelation of output; correlations of the unemployment rate, EE rate, and inflation with output; and standard deviations of output, unemployment rate, EE rate, and inflation. Data cover 1995:Q3–2008:Q4. Estimated values are ρβ = 0.909, ρz = 0.332, ρν = 0.936 and σβ = 0.001, σz = 0.002, σν = 0.003. The variance decomposition (Table 4) assigns 43.1 percent of inflation variance to OJS efficiency shocks ν, 52.0 percent to demand shocks β, and 4.9 percent to productivity shocks z.

Q6. How is the “missing inflation” during 2016–2019 quantified, and what is the counterfactual?

The exercise simulates two economies both replicating the same unemployment path — a 15 percent decline in unemployment relative to its 5.2 percent steady state, spread linearly over 16 quarters, followed by mean reversion. The first economy uses only positive demand shocks, which generate an endogenously rising EE rate consistent with the historical unemployment-EE correlation. The second economy additionally introduces negative OJS efficiency shocks to keep the EE rate unchanged, as observed in the data during 2016–2019. Annualized inflation in the second economy is 0.23 percentage points lower at the peak (16 quarters after the shock), implying that had the EE rate risen normally, inflation would have been around 2 percent in 2019 rather than the observed 1.8 percent.

Q7. How is the inflationary role of elevated EE transitions during 2021–2022 quantified?

Using the same unemployment path as the 2016–2019 exercise, the COVID-19 recovery economy combines positive demand shocks with positive OJS efficiency shocks to replicate the observed 0.16 percentage point (8 percent above trend) increase in the EE rate. Comparing this economy to the flat-EE-rate economy from the prior exercise, the elevated EE rate generates 0.56 percentage points higher annualized inflation. Because annual inflation rose approximately 6 percentage points in the data during this episode, the model attributes roughly 10 percent of the total inflation increase to strong worker mobility.

Q8. What are the optimal Taylor rule coefficients when EE dynamics are included, and what is the welfare cost of ignoring them?

The optimal policy over the augmented Taylor rule it = i* + Φπ(πt − π*) + Φu(ut − u*) + ΦEE(EEt − EE*), with Φπ fixed at 1.5 and a dual-mandate loss function W = var(πt − π*) + 0.25·var(Yt − Y*), prescribes Φ*_u = −3.18 and Φ*_EE = 2.22. This reduces the central bank loss by 78.7 percent relative to the baseline rule (Φu = −0.25, ΦEE = 0). If the EE gap term is excluded and only the unemployment gap coefficient is re-optimized (finding Φu = −2.71), the central bank loss is 12 percent higher than under the full optimal policy.

Q9. How does the optimal policy affect macroeconomic volatility, and who gains most from it?

Table 5 shows that the optimal policy substantially reduces volatility of inflation (standard deviation falls from 0.0013 to 0.0011), output (0.0059 to 0.0020), consumption (0.0059 to 0.0020), unemployment (0.0047 to 0.0013), labor market tightness (0.0600 to 0.0175), and the real marginal cost pl (0.0203 to 0.0081), at the cost of higher real rate volatility (0.0019 to 0.0033) and share price volatility (0.1975 to 0.3051). In terms of welfare (Table 6), the unemployed gain 0.20 percent in lifetime consumption equivalents (versus 0.15 percent for the employed), workers at the bottom quintile of match quality gain 0.24 percent (versus 0.16 percent at the top), and wealth-poor individuals in the bottom share quintile gain 0.23 percent (versus 0.11 percent at the top, whose gains are eroded by larger share price fluctuations).

Q10. How does the model extend the SSJ computational method, and why is this extension necessary?

The standard SSJ method of Auclert, Bardoczy, Rognlie, and Straub (2021) handles settings where only scalar aggregates enter equilibrium conditions in sequence space. In this model, the discretized distributions of employed workers µE(h, x) and unemployed workers µU(h) at the job search stage enter directly into the expected match value EJ (because human capital and current match productivity determine output and wage levels upon new contacts), and the distribution λE(h, x, α) at the production stage enters into labor services firm profits ΓS. The authors treat worker distributions as histograms and compute Jacobians for each mass point, combining the SSJ method with Reiter (2009)-style projection. This substantially increases computation time but remains feasible, extending the SSJ method to multi-stage models with search frictions where endogenous distributions are state variables.

Q11. What are the three sources of wage growth in the HANK model, and what is their relevance for inflation dynamics?

First, human capital h stochastically appreciates during employment (at rate πE = 0.018 per quarter, calibrated to annual job-stayer wage growth of approximately 2 percent), raising wages through a higher piece-rate base. Second, job switches to higher-productivity matches yield wage increases as the worker extracts the full surplus from the new firm (the new piece rate equals x/x’, the ratio of old to new match productivity). Third, outside offers with productivity x’ satisfying αx < x’ < x — not good enough to trigger a switch but better than the current bargaining threat — cause the incumbent firm to raise the piece rate to x’/x via rebargaining, increasing wages without a job change. The second and third channels are the ones directly affected by OJS efficiency shocks and are inflationary: they raise labor costs beyond productivity gains.

Q12. Why do OJS shocks have a shorter match duration channel even without wage increases?

When OJS efficiency ν rises, each employed worker faces a higher probability νtf(θt) of contacting another firm each period. Even if wages do not change upon contact (as in the α = 0.95 robustness exercise), a labor services firm posting a vacancy expects that any match it forms will be shorter-lived: the worker is more likely to be poached in the future. This shortens the expected present discounted value of the match for the firm, reducing EJ. To satisfy the free-entry condition (expected profit = vacancy cost κ), the price of labor services pl must rise, increasing the real marginal cost and inflation. Figure 3 confirms a nearly identical inflationary response under α = 0.95 as under the baseline, isolating this match-duration mechanism.

Key Concepts

OJS efficiency shock (νt shock). A time-varying shift in the relative job search efficiency of employed workers compared with unemployed workers. Modeled as an AR(1) process for νt (estimated persistence ρν = 0.936). An increase in νt raises the probability that employed workers contact outside firms each period, boosting the EE rate. In the model, this acts as a cost-push shock: it raises inflation and unemployment simultaneously, breaking divine coincidence and creating a policy trade-off for a dual-mandate central bank.

Expected match value (EJt). The ex-ante expected value to a labor services firm of a filled vacancy, conditional on contacting a worker, defined as a weighted average of match values J across the pool of job seekers (unemployed and employed). The free-entry condition Vt = κ/q(θt) = EJt pins down the real price of labor services pl: when EJt declines (due to shorter match durations or compositional shifts toward high-surplus-extracting workers), pl must rise to maintain zero expected profit for vacancy posters.

Composition channel. The mechanism by which a rise in OJS efficiency shifts the composition of the job-seeker pool toward employed workers, who (under Bertrand competition) extract the entire flow surplus of a new match and receive wage equal to plF(h,x). Since firms receive zero rent from poached workers, an increase in the fraction of employed in the applicant pool lowers EJt and requires a compensatory increase in pl.

Match duration channel. When OJS efficiency ν rises, each existing match faces a higher probability of dissolution because the worker is more likely to be poached. The reduced expected match duration lowers the present discounted value of a match for the firm (even holding wages fixed), reducing EJt and raising pl. Demonstrated as the primary driver of inflation in the α = 0.95 robustness exercise where wage increases upon job switches are near zero.

Piece-rate α (endogenous). The share of match output F(h,x) that the worker receives as wage, determined through Bertrand competition on flow output following Postel-Vinay and Robin (2002). A worker hired from unemployment starts at α = x̄/x’ (where x̄ is the lowest match productivity). Job switches to higher-x’ firms reset α = x/x’. Rebargaining upon a credible outside offer from a firm with αx < x̃ < x raises α to x̃/x. The piece rate endogenizes wage dynamics for switchers, stayers, and job losers, allowing the model to discipline these moments in the data.

Divine coincidence (and its breakdown under OJS shocks). In standard New Keynesian models, demand and productivity shocks move inflation and unemployment gaps in opposite directions, so stabilizing inflation also stabilizes the output gap. OJS efficiency shocks break this property: they generate simultaneous increases in inflation and unemployment, introducing a genuine trade-off between the two mandates and making EE-augmented Taylor rules welfare-improving relative to rules that respond only to unemployment.

Sequence-Space Jacobian (SSJ) method with distributed worker states. An extension of the Auclert, Bardoczy, Rognlie, and Straub (2021) computational method to settings where discretized distributions of workers (µE(h,x) and µU(h)) enter directly into equilibrium conditions — specifically into the free-entry condition via EJt and into firm profits. The authors treat distributions as histograms and compute Jacobians for each mass point, combining SSJ with Reiter (2009)-style projection to efficiently solve for transitional dynamics under aggregate uncertainty.

Life-Cycle Wages and Human Capital Investments: Selection and Missing Data

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

Layer 1 – Overview

Research Question

This paper asks how wage inequalities build up over the life cycle when individual wage trajectories are plagued by interruptions in private-sector participation, and when the standard Missing At Random (MAR) assumption used to handle those gaps may be violated. Specifically, it asks: what is the causal effect of career interruptions on both the level and the dispersion of wages after twenty years of potential experience, and does endogeneity of those interruptions matter for the dispersion result?

Data and Sample

The empirical analysis uses the 2011 DADS Grand Format-EDP panel, a French administrative dataset merging social security records (DADS) and census extracts (EDP). The working sample covers males who entered the private sector between 1985 and 1992, aged 16-30 at entry, and observed through 2011. The authors require at least 15 years of observed private-sector wages, yielding a working sample of 7,004 males and 137,315 person-year observations. Education is grouped into four levels (high-school dropouts, high-school graduates, some college, college graduates). Participation outside the private sector – including public-sector employment, self-employment, unemployment, and non-employment – constitutes the “alternative sector” and generates missing wage observations. On average, cumulative duration outside the private sector is 3.7 years, and the average number of interruptions is 1.44.

Model and Methodology

The paper builds on a structural Ben Porath (1967) human capital model extended to two sectors (private sector and an alternative sector), yielding a reduced-form log-wage equation with five individual-specific coefficients: an intercept (initial human capital), a linear trend in potential experience (growth rate), a curvature term in potential experience (Mincer concavity), the cumulative years of interruptions, and a curvature term in interruptions. Because parameters are individual-specific, the wage equation is a random-coefficient model estimated with a fixed-effects approach.

Selection into the private sector is addressed not by a standard MAR assumption but by a weaker “Missing At Random Conditionally On Factors” (MARCOF) assumption. Sector-preference shocks, human capital prices, and depreciation rates are each decomposed into a common factor (time-varying) and an individual factor loading, plus a residual that is mean-independent of factors and loadings. Conditional on factors and factor loadings, wage residuals and sector choices are independent, making covariates – including the interruption variables – exogenous. The preferred specification includes two unobserved factors, selected by four of six Bai-Ng (2002) information criteria.

Estimation proceeds via an Expectation-Maximization (EM) algorithm adapted from Bai (2009) and Song (2013), with initial values from Moon and Weidner (2018)’s nuclear-norm convex estimator. Because individual parameters converge at rate sqrt(T) and summary statistics of their distributions suffer from incidental-parameter bias, the authors use bias-correction methods from Jochmans and Weidner (2019) for quantiles and inter-decile ranges, and from Arellano and Bonhomme (2012) for variances. Monte Carlo experiments confirm that variances remain poorly corrected even when T > 20, so the paper focuses on inter-decile ranges as the dispersion measure.

Counterfactual “average structural functions” (Blundell and Powell, 2003) are constructed by holding individual parameters fixed and manipulating the history of interruptions. These compare four scenarios: the observed benchmark, the counterfactual with no interruptions (potential wage), the counterfactual with no current-period selection, and both combined.

Main Findings

Downward bias from omitting interruptions and factors. Omitting interruption variables and unobserved factors strongly downward biases estimated returns to experience after 20 years. Most of this bias is attributable to interruptions rather than to the interactive factor effects: selectivity is mainly captured through the interruption channel, not through residual factor structure.
Effect on mean wages. Potential experience increases log wages by approximately 65% over 20 years, consistent with cross-country evidence from homogeneous Mincer equations. The average cost of interruptions after 20 years is approximately 10% of log wages. Reassigning interruptions to the beginning of the working life has a persistent negative effect on mean log wages that never fully recovers over 20 years, while reassigning them to the end increases mean wages above the no-interruption benchmark at every experience level.
Effect on wage dispersion – a new stylized fact. Interruptions decrease, not increase, the inter-decile range of log wages after 20 years. After 20 years, with an average interruption duration of 2.47 years, interruptions decrease the inter-decile range by 0.52 log points (approximately 38%). This compression operates differentially: the 90th percentile falls by 0.34 and the 10th percentile rises by 0.18.
Endogeneity explains the dispersion compression. When years of interruption are randomly reassigned across time (holding total interruption years fixed), the inter-decile range diverges upward from the observed benchmark after about 5 years. This shows that the dispersion-reducing effect of actual interruptions is due to the endogenous timing of those interruptions – specifically to the negative correlation between the timing of interruptions and potential log wages – rather than to the correlation between the structural coefficients on interruptions and potential wages (which is also negative, with a Spearman rank correlation of -0.32 between eta_i1 and eta_i3). Endogenously chosen interruptions smooth inequality over time.
Current-period selection is negligible. Current-period selection into private-sector employment has no statistically significant effect on median, mean, variance, or inter-decile range of wages at any experience level, as confirmed by the small inter-decile range of the interactive factor component.

Scope Conditions

Results pertain to cohorts of French males entering the private sector between 1985 and 1992, restricted to those with at least 15 observed private-sector years. The French context is distinctive: wage inequality in the working population was stable over 1985-2011, driven in part by minimum wage policy and payroll tax exemptions for lower-skilled workers, in contrast to rising inequality in the United States and Germany. Results on timing of interruptions (eta_i3 and eta_i4) are identified only for individuals with at least two interruptions followed by re-entry (roughly those with K_T >= 2). The paper does not analyze female wages.

In depth

Q1. What is the structural model and how does it generate a reduced-form wage equation?

The model is a Ben Porath (1967) two-sector human capital model in which individuals divide time between investing in human capital and earning wages in either the private sector (e) or an alternative sector (n). Human capital accumulation in each sector has a sector-specific return rate (rho^s) and depreciation (lambda^s_t). Period utility is log income minus a quadratic investment cost, plus a sector preference shock. Solving the dynamic program backwards (because of log-linearity) yields closed-form optimal investments that are linear in the individual-specific terminal value of human capital (kappa). The resulting log-wage equation (Proposition 5) is a function of five terms: an intercept (eta_i0), a linear trend in potential experience t (eta_i1), a geometric curvature term beta^{-t} (eta_i2), cumulative years of interruptions x^(3)_it (eta_i3), and a curvature in interruptions x^(4)_it (eta_i4), all with individual-specific coefficients. This provides a tractable random-coefficient structure.

Q2. What is the MARCOF assumption and why is it weaker than MAR?

MARCOF – Missing At Random Conditionally On Factors – posits that sector-preference shocks, human capital prices, and depreciation rates each follow factor structures: a common time-varying factor (phi_t) multiplied by an individual loading (theta_i) plus an i.i.d. residual. The residuals are assumed mean-independent of factors and loadings, and independent over time. Under standard MAR, missingness is assumed independent of outcomes conditional on observables alone. Under MARCOF, residuals in the wage equation and the sector choice equation are independent conditional on (unobserved) factors and factor loadings. This is weaker than MAR because it allows the unobservable determinants of wages and participation to share common factors, accommodating the high persistence observed in human capital stocks (20-year lag correlation of 0.28, far above the geometric decay benchmark of 0.024).

Q3. How are the individual-specific parameters identified?

Under exogenous selection (or, under MARCOF, conditional on factors), identification of eta_i0, eta_i1, and eta_i2 requires variation in potential experience within the individual’s time series. Identification of eta_i3 and eta_i4 separately requires individuals to experience at least two spells out of the private sector each followed by re-entry (at least four transitions, so K_T >= 2). An individual with only one interruption spell generates proportional variation in x^(3) and x^(4), so only a linear combination of eta_i3 and eta_i4 is identified. The “flat spot” approach – using the observed fact that individuals aged 50-55 have stopped investing in human capital – separately identifies time, cohort, and age effects and provides the restriction that factors are orthogonal to the level, trend, and curvature in potential experience.

Q4. What do the distributions of estimated individual-specific coefficients look like?

Focusing on the main (two-factor) specification with bias correction: the median of the growth parameter eta_i1 is positive (consistent with rising wages with experience) and the median of the curvature parameter eta_i2 is negative (consistent with concavity). However, heterogeneity is substantial: the 90th percentile of eta_i1 is 6.2 times the median, and the first quartile of eta_i1 is negative (implying declining potential wages for a non-negligible share). For the interruption coefficients eta_i3 (year of interruptions) and eta_i4 (curvature), bias-corrected medians are close to zero in the sub-sample with >=2 interruptions, but dispersion is large and symmetric around zero. Bias correction reduces the 90th percentile of eta_i1 by approximately 20% and reduces the absolute 10th percentile of eta_i3 by approximately 27%.

Q5. How important are interruptions relative to potential experience and factors in explaining wage variation?

A wage decomposition using inter-decile ranges (preferred over variance due to bias) shows that the potential experience component is the largest contributor to wage dispersion, followed by the interruption component (described as “sizable”), while factors play a minor role. Crucially, the potential experience and interruption components are highly negatively rank-correlated: the Spearman rank correlation between the growth coefficient eta_i1 and the interruption coefficient eta_i3 is -0.32. This negative correlation is central to understanding why interruptions compress dispersion rather than expanding it.

Q6. What is the finding on the effect of interruptions on mean wages, and what does the timing experiment show?

After 20 years, the average cost of interruptions (relative to a counterfactual of no interruptions) is approximately 10% of log wages. The timing of interruptions matters: reassigning interruptions to the beginning of the working life causes a persistent loss in mean log wages that does not fully recover over the 20-year horizon, while reassigning them to the end raises mean log wages above the no-interruption level at every experience level. For median wages, the early-interruption loss is eventually recovered (median log wages do catch up), but the mean does not catch up. These asymmetries are consistent with early interruptions having a larger negative effect on human capital accumulation due to the geometric structure of investment returns.

Q7. What is the key finding on wage dispersion and what explains it?

Interruptions compress the inter-decile range of log wages by 0.52 log points (approximately 38%) after 20 years, with average interruption duration of 2.47 years. This compression is asymmetric: the 90th percentile of wages falls by 0.34 and the 10th percentile rises by 0.18. The dispersion-reducing effect is established by comparing the benchmark (observed interruptions) to the counterfactual of no interruptions. When interruptions are instead randomly reassigned across time (holding total interruption duration fixed), the inter-decile range diverges upward from the benchmark starting around 5 years of experience. This demonstrates that the compression is due to the endogenous timing of interruptions – individuals who have high potential wages tend to time their interruptions in ways that reduce the measured spread of actual wages – rather than to the negative structural coefficient (eta_i3 < 0 for high-wage workers on average).

Q8. How does the paper handle the incidental parameter problem for distributional statistics?

Because individual parameters are estimated at rate sqrt(T) and the panel is unbalanced (some individuals observed for as few as 15 years while the model has up to 7 individual parameters), standard distributional statistics like the variance suffer from substantial incidental parameter bias. Monte Carlo experiments show that bias-corrected variance estimates remain strongly biased even at T > 20. Inter-decile ranges are better behaved and the Jochmans and Weidner (2019) bias-correction procedure reduces their bias satisfactorily. This is why the paper reports inter-decile ranges as its primary dispersion measure rather than variances. The bias in corrected inter-decile ranges is at most approximately 10% of the uncorrected estimate.

Q9. What does the paper show about the MAR assumption in the context of this data?

The results directly challenge the MAR assumption that is standard in the life-cycle earnings literature. Under MAR, interruptions would be treated as random conditional on observables, and their endogeneity would be ignored. The paper shows that treating interruptions as endogenous (through the MARCOF + structural model approach) substantially changes estimated returns to experience (there is a strong downward bias when interruptions and factors are omitted) and reverses the sign of the effect of interruptions on dispersion (under exogenous interruptions, randomly reassigned, dispersion would be higher than observed; the actual compression is an artifact of endogenous timing). The conclusion is that MAR assumptions produce systematically misleading pictures of life-cycle wage inequality dynamics.

Q10. What are the robustness and external validity considerations?

The working sample excludes individuals observed fewer than 15 years. A robustness exercise compares the subsample observed 10-14 years to a censored version of the 20+ subsample with matched marginal distributions of observation counts. Median profiles for the uncensored and censored 20+ samples are similar, and inter-decile ranges are slightly more dispersed in the censored sample only for potential experience greater than 7. However, the 10-14 year sample shows substantially different patterns – larger median gaps between benchmark and no-interruption cases, and a larger inter-decile range – consistent with lower private-sector returns to human capital for that group. The authors conclude that selection into the 15+ working sample matters, and results are explicitly restricted to that working sample. The French context (stable aggregate wage inequality, minimum wage policy) limits direct comparability to countries with rising inequality.

Key Concepts

MARCOF (Missing At Random Conditionally On Factors): The paper’s central identifying assumption, weaker than standard MAR. It posits that sector-preference shocks, human capital prices, and depreciation rates follow factor structures (common time-varying factor x individual loading + i.i.d. residual), and that residuals are mean-independent of factors, loadings, and their own histories. Conditional on factors and loadings, wage residuals and sector-choice residuals are independent, making selection exogenous.

Interactive effects / factor structure for selection: An approach in which unobserved confounders are modeled as a bilinear product of time-varying common factors (phi_t) and individual factor loadings (theta_i). This allows flexible correlation between wage processes and participation choices without requiring exclusion restrictions or instrumental variables. The paper’s preferred specification uses two unobserved factors identified by Bai-Ng information criteria.

Average structural functions: Objects defined by Blundell and Powell (2003) that integrate counterfactual outcomes (wages evaluated at a manipulated interruption history) over the distribution of individual-specific parameters. They allow estimation of the causal impact of a change in interruption timing or presence while holding individual structural parameters fixed, under identification conditions analogous to those of Chernozhukov et al. (2013).

Individual-specific coefficients (random coefficients): The five parameters (eta_i0, eta_i1, eta_i2, eta_i3, eta_i4) governing each individual’s wage equation, with structural interpretations: initial log human capital, return to potential experience, curvature (Mincer concavity), effect of cumulative interruption years, and curvature in interruptions. Their individual-specificity is the source of the incidental parameter problem for distributional statistics.

Flat spot approach: An identification device (from Heckman, Lochner, and Taber, 1998; Bowlus and Robinson, 2012) that uses median wages of workers aged 50-55 – who are assumed to have stopped investing in human capital – as consistent estimates of human capital prices by education group and year. This separates the volume of human capital from its price, and provides the restriction identifying the level, trend, and curvature factors from the time-varying unobserved factors phi_t.

Interruption variables x^(3) and x^(4): Reduced-form variables derived from the structural model summarizing the history of private-sector participation gaps. x^(3)_it is the cumulative number of periods spent in the alternative sector prior to date t; x^(4)_it is a geometric-weighted version of those interruptions that reflects the timing (early vs. late) through the discount factor beta. They enter the wage equation with individual-specific coefficients that are identified only for workers with at least two complete interruption spells.

Mincer dip: A U-shaped profile in wage variance (or inter-decile range) over potential experience, predicted by the Ben Porath model because high-return workers invest more at the start of their careers (reducing current wages), causing their wage profile to cross below then above low-return workers. Estimated in this paper at approximately 5 years of potential experience under the main specification.

Incidental parameter bias in distributional statistics: The bias that arises when estimating moments or quantiles of the distribution of individual-specific parameters that converge at rate sqrt(T) rather than sqrt(N). The paper shows through Monte Carlo experiments that variance estimates remain substantially biased even after Arellano-Bonhomme (2012) correction when T >= 20, while inter-decile ranges corrected by Jochmans-Weidner (2019) are more reliable.

Marginal Returns to Public Universities

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

This paper asks whether enrolling in an American public university generates positive net returns for marginal students — those who barely qualify for admission — and whether those returns justify public expenditures. The question is policy-relevant because marginal students have weak academic preparation, face high dropout risk, and the net returns to expanding admission margins are theoretically ambiguous.

The author assembles administrative records spanning all 35 public universities in Texas, covering the universe of Texas public high school graduates from 2004–2014 (approximately 2.7 million students). Texas public universities collectively enroll over 10 percent of all American public university students. The data link high school records (test scores, demographics, coursework, attendance, disciplinary infractions) to college application and admission records, postsecondary enrollment and degree completion records, financial aid packages, institutional expenditure data from IPEDS, and quarterly earnings records from the Texas Workforce Commission unemployment insurance system.

The identification strategy exploits hundreds of decentralized SAT/ACT score cutoffs in university admissions — varying across schools and application years — that generate sharp discontinuities in admission probability. A fuzzy regression discontinuity design compares applicants just above versus just below each cutoff. On average, crossing a cutoff raises the probability of admission by 27 percentage points and the probability of enrolling at the target university by 15 percentage points. Density tests and pre-college covariate balance validate the smoothness assumptions. The typical cutoff complier is more disadvantaged than the average college applicant but comparable to the average Texas high school graduate.

Roughly half of cutoff compliers would fall back to another, typically less selective, four-year institution if rejected; 43 percent would fall back to a two-year community college; and only about 6 percent would forgo higher education entirely. The pooled estimates therefore blend intensive-margin effects (more selective versus less selective four-year college) with extensive-margin effects (four-year college versus community college or no college).

Main causal findings for enrollment compliers: the typical marginally admitted student completes approximately one additional year of credits in the four-year sector and becomes 12 percentage points more likely to ever earn a bachelor’s degree from any institution. About half of the additional four-year credits are offset by 15 fewer credits in the two-year sector, and associate degree or certificate completion falls by 7 percentage points. All bachelor’s degree gains are in non-STEM fields; STEM degree completion shows no detectable increase. Compliers become about 3 percentage points more likely to hold a graduate degree by 10 years out.

On earnings, admitted compliers earn less than rejected counterparts in the first five years due to continued enrollment. Year six is the crossover point; by years 8–12, compliers earn a stable 8.6 percent earnings premium in log terms (8.2 percent in dollar ratio terms, representing a LATE of $3,339 against an untreated complier mean of $40,829), with earnings ranks rising approximately 4 percentiles from a base near the 50th percentile.

Marginally admitted students pay no additional net tuition on average: $4,600 in additional gross tuition is nearly fully offset by grant aid, though they take on $5,300 more in student loans. Society incurs approximately $10,000 in additional educational expenditures per complier. Internal rates of return are 26 percent for students, 16 percent for society, and 7 percent for the government budget. At a 3 percent discount rate, the lifetime net present value of enrolling the typical marginal applicant is approximately $80,000 — $70,000 accruing to the student and $10,000 to taxpayers.

Earnings gains are similar across institutions of varying selectivity, but significantly smaller for low-income compliers, who spend more time enrolled, complete fewer degrees, and major in less lucrative fields. A bounding method shows that extensive-margin compliers (those who would otherwise not attend any four-year college) experience larger effects than intensive-margin compliers.

Q: What is the core research question and why is credible evidence scarce? A: The paper asks whether enrolling marginal students in American public universities generates positive net returns — private, social, and fiscal — and what drives heterogeneity in those returns. Credible evidence is scarce because most existing work is correlational and fails to account for selection bias: individuals with more college education may have had pre-existing advantages, confounding college’s causal effect with systematic sorting into it. Even if average returns are positive, the policy-relevant question is whether the marginal student — who has weak preparation and high dropout risk — represents a good investment.

Q: What is the regression discontinuity design, and what does the first stage look like? A: The author infers hundreds of decentralized SAT/ACT score cutoffs across approximately 700 application cells (combinations of university, year, GPA quartile, and test type) by searching for the score value with the largest discontinuity in admission and enrollment within each cell. This procedure delivers a superconsistent estimator of each cell’s true cutoff. Pooled across all cells, crossing a cutoff raises the probability of admission by 27 percentage points and the probability of enrollment at the target university by a precisely estimated 15 percentage points. The density of applicants and a rich set of pre-college characteristics run smoothly through the cutoffs, supporting the exclusion restriction.

Q: Who are the cutoff compliers, and are they representative of any broader population? A: Compliers — applicants who enroll in the target university if and only if they barely cross its cutoff — comprise approximately 15 percent of marginal applicants. In observable characteristics, compliers are roughly representative of the broader population of marginal applicants at the cutoff. They are significantly more disadvantaged than the average public university applicant, but broadly comparable to the average Texas public high school graduate in terms of academic preparation and family income.

Q: What are the next-best alternatives for marginal applicants who are rejected? A: Approximately 47 percent of compliers would fall back to another Texas four-year college (mostly public), 43 percent to a two-year community college, and approximately 9 percent would not enroll in any Texas institution. National Student Clearinghouse data for the 2008–2014 cohorts confirm that only 4 percent of untreated compliers attend a college outside the THECB universe, meaning approximately 6 percent of all compliers truly forgo higher education altogether if rejected. The empirically relevant extensive margin is therefore between the four-year sector and the two-year sector, not between college and no college.

Q: How does cutoff crossing change the institutional characteristics a complier experiences? A: Compliers are propelled into substantially better-resourced environments: the average math test score of college peers rises by half a standard deviation; peers are 12 percentage points less likely to have been low-income; gross tuition rises by $2,400 (a 42 percent increase over the untreated complier mean of $5,700); educational spending per student rises by $3,200 (43 percent over the untreated mean); peers’ 10-year BA completion rate rises by 28 percentage points; and peer mean earnings 8–12 years after college entry are $6,700 higher.

Q: What are the educational attainment effects? A: Cutoff crossing causes compliers to complete approximately 28 additional credits at any four-year institution (roughly one full year of a four-year program) and increases the probability of ever earning a bachelor’s degree by 12 percentage points, raising the completion rate from approximately 40 percent to just above 50 percent. About 15 fewer two-year sector credits are offset against the four-year gains, and associate degree or certificate completion falls by 7 percentage points. All bachelor’s degree gains are in non-STEM fields; there is no detectable increase in STEM degrees. Graduate degree completion rises by approximately 3 percentage points by 10 years out.

Q: What is the earnings trajectory, and when does the premium materialize? A: Admitted compliers earn less than rejected counterparts in the first five years after application because they remain enrolled longer. Year six is the crossover point. By years 8–12, the earnings premium stabilizes at approximately 8.6 percent in log terms and 8.2 percent in dollar ratio terms (a LATE of $3,339 against an untreated complier mean of $40,829). Earnings rank rises by approximately 4 percentiles from a base near the 50th percentile. These results are robust across sandwich earnings, all-quarters-with-earnings, and zero-imputed specifications.

Q: What does the cost-benefit analysis show? A: Marginally admitted students pay no additional net tuition on average: $4,600 in additional gross tuition is nearly fully offset by additional grant aid. They do borrow $5,300 more in student loans, likely financing higher room, board, and consumption costs at four-year colleges. From society’s perspective, compliers generate approximately $10,000 in additional educational expenditures. Cumulative undiscounted earnings benefits surpass costs after 8 years for students, 11 years for society, and 19 years for taxpayers. At a 3 percent discount rate, the lifetime net present value is approximately $80,000 total — $70,000 accruing to the student and $10,000 to taxpayers — with internal rates of return of 26 percent for students, 16 percent for society, and 7 percent for the government budget.

Q: Does selectivity of the admitting institution predict larger earnings returns? A: No. Compliers at more selective institutions experience substantially larger increases in peer quality than those at less selective institutions, but they are also less likely to be on the extensive margin of four-year enrollment and experience smaller BA attainment gains. These factors roughly offset, producing no systematic difference in earnings gains across institutions of varying selectivity. More selective institutions also impose no additional cumulative cost on society, while compliers actually pay slightly less in additional net tuition at more selective schools.

Q: How does the commonly used measure of college value-added (mean peer earnings) compare to actual complier returns? A: Mean peer earnings overpredicts actual value-added for marginal students by a factor of two: compliers attend an institution with $6,700 higher average peer earnings as a result of admission but gain only $3,300 themselves. The measure also overpredicts the earnings return to selectivity by a factor of three: a 100-SAT-point increase in target school selectivity predicts $3,000 higher peer earnings but only a statistically insignificant $900 higher gain in the complier’s own earnings.

Q: How do earnings returns differ by family income? A: Compliers from low-income families experience significantly smaller earnings gains compared to higher-income compliers. The gap is not explained by differential changes in college quality induced by admission. Instead, low-income compliers gain fewer degrees despite spending more time in college and major in less lucrative fields, consistent with related findings in the literature on family income gaps in degree completion and major choice.

Q: How do earnings returns differ by gender and by race? A: Female and male compliers eventually earn similar log earnings and earnings rank gains, but women reach their gains more quickly — likely because men take longer to finish college. White and Asian compliers experience similar earnings gains and BA completion improvements as Black and Hispanic compliers, despite white and Asian students experiencing larger increases in college selectivity and spending per student as a result of admission.

Q: What is the method for separating intensive- and extensive-margin effects? A: The two complier types are not directly distinguishable in the data. The author first uses an endogenous but strong stratification variable — having at least one other Texas public university admission offer — to identify some mean potential outcomes for each type. He then imposes an empirically-informed rank assumption to bound the remaining unknown mean potential outcomes, delivering tightly informative upper and lower bounds on each margin’s effects without requiring full nonparametric identification. The results show that pooled effects are driven by larger returns for extensive-margin compliers who would not have attended any four-year college, with smaller contributions from intensive-margin compliers shifting between four-year institutions.

Q: How do this paper’s earnings estimates compare to prior studies, and what explains the differences? A: This paper’s 8 percent earnings gain is smaller than the 17–26 percent reported in prior studies (Zimmerman 2014: 22%; Kozakowski 2023: 26%; Smith, Goodman, and Hurwitz 2025: 17%; Bleemer 2024: 21%; Hoekstra 2009: 20%). The differences are likely explained by the much larger educational attainment and institutional quality gains induced by those studies’ natural experiments: in Zimmerman (2014), enrollment compliers gain roughly three additional years of four-year education versus one year in this paper; in Bleemer (2024), compliers experience roughly $30,000 more in institutional spending per student versus approximately $3,000 in this paper.

Q: What are the scope conditions for these results? A: The results pertain to marginal applicants to Texas public universities (excluding UT-Austin, which uses holistic admission with no detectable SAT/ACT cutoffs) from the 2004–2014 high school graduation cohorts. The identified effects are local average treatment effects for compliers — applicants who would enroll in the target university if and only if they barely crossed its admission cutoff — and do not represent effects for always-takers or infra-marginal students. Earnings are measured only for Texas-based workers covered by the state unemployment insurance system, which captures an estimated 90 percent of the civilian labor force.

Cutoff complier: An applicant who enrolls in their target university if and only if their SAT/ACT score barely exceeds that university’s admission cutoff. Compliers are the population whose behavior — and thus whose treatment effects — are identified by the fuzzy RD design. They comprise approximately 15 percent of marginal applicants and are more disadvantaged than the average public university applicant but broadly comparable to the average high school graduate.

Extensive versus intensive margin: The extensive margin refers to the contrast between attending any four-year college versus falling back to a two-year community college or no college. The intensive margin refers to the contrast between attending a more selective versus a less selective four-year institution. Approximately half of cutoff compliers are on each margin; the paper treats them as economically distinct parameters requiring separate identification.

Fuzzy regression discontinuity (RD) design: An identification strategy that uses the discontinuous jump in admission probability at a test score cutoff as an instrument for enrollment, recovering the LATE for compliers via the ratio of the reduced-form discontinuity in outcomes to the first-stage discontinuity in enrollment. “Fuzzy” refers to the fact that crossing the cutoff changes admission and enrollment probabilities with a discrete jump rather than with certainty.

Internal rate of return (IRR): The discount rate at which the net present value of an investment equals zero — here, the discount rate equating the discounted stream of earnings benefits to the discounted stream of costs. The paper estimates IRRs separately for students (26 percent), society (16 percent), and the government budget (7 percent), reflecting different cost and benefit definitions from each perspective.

Rank assumption (bounding method): An empirically-informed assumption about the ordering of mean potential outcomes across latent complier types (extensive vs. intensive margin) that, combined with partial identification from a strong endogenous stratification variable, yields tight upper and lower bounds on each margin’s causal effects without requiring full nonparametric identification.

Net tuition: Gross tuition charges minus grant aid. For the typical marginal complier, gross tuition rises by $4,600 but is nearly fully offset by additional grant aid, yielding approximately zero additional net tuition cost — meaning the private financial cost of attending a public university for marginal students is effectively zero on net, though they take on $5,300 more in student loans to finance room, board, and consumption.

Sandwich earnings measure: A procedure applied to quarterly state earnings data that retains only quarters with positive earnings sandwiched between other quarters with positive earnings, discarding high-variance transition quarters between employment spells. Annualized by multiplying the quarterly average by four; used to reduce noise from entry and exit transitions in administrative earnings records.

Robot adoption and inflation dynamics

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

Robot Adoption and Inflation Dynamics

Research Question

Basso and Rachedi investigate how robot adoption influences inflation dynamics — specifically, whether the surge in automation during the 2000s and 2010s can explain the muted sensitivity of inflation to unemployment (the “flat Phillips curve”) observed in advanced economies prior to the Covid pandemic, and whether the same framework can account for the subsequent resurgence of steep inflation-unemployment co-movement.

Data and Methodology

The empirical analysis uses an annual panel covering 384 U.S. metropolitan statistical areas (MSAs) from 2008 to 2018. The dependent variables are non-tradable goods inflation (log-difference of services prices excluding rents and utilities, from BEA regional price parities) and wage inflation (log-difference of average compensation per job). Robot adoption at the MSA-year level is constructed following Acemoglu and Restrepo (2020a): industry-level robots per employee at the U.S. national level are weighted by industry employment shares in each MSA, yielding an MSA-year robot-per-employee ratio.

The regression specification extends Hazell et al. (2022) by adding an interaction term between the lagged unemployment rate and the (demeaned) robot-per-employee ratio, along with MSA and year fixed effects. Year fixed effects absorb common inflation expectations and the endogenous response of monetary policy to aggregate demand shocks. To address endogeneity, unemployment is instrumented with a Bartik shift-share variable of tradable demand spillovers, and robot adoption is instrumented with average industry-level robot penetration in the five largest European economies — under the identifying assumption that robot demand shocks are weakly correlated across advanced countries.

The theoretical framework is a New Keynesian model augmented with (i) directed search frictions in the labor market, and (ii) producer-level automation decisions in the spirit of Acemoglu and Restrepo (2020a). Producers pay a fixed entry cost, draw idiosyncratic efficiency for employing labor, and then choose between a robot technology (certain output at low efficiency) and a labor technology (uncertain hiring, higher potential efficiency). This generates an automation threshold: low-efficiency producers install robots, displacing low-wage jobs. A Taylor rule closes the model. Quantitative exercises compare two steady states calibrated to robot-per-employee ratios of 0.2% (low automation, targeting the U.S. in the early 2000s) and 0.6% (high automation, calibrated to one standard deviation of robot penetration variation across MSAs).

Main Findings

Empirical. In the baseline IV regression, a one standard deviation increase in robot adoption reduces the sensitivity of price inflation to unemployment by 17%, and the sensitivity of wage inflation to unemployment by 9%, relative to a MSA with the average robot penetration. The larger flattening effect on price inflation than on wage inflation implies that robot adoption also diminishes the pass-through from wages to prices. All three effects are statistically significant at the 5% level, and are robust to controls for demographic structure (age composition, gender/race/education participation rates, MPC heterogeneity), occupational structure (abstract, routine, manual, and offshorable occupations), and import competition exposure (Chinese and Mexican import shares).

Model quantification. Comparing the high-automation to the low-automation steady state, the model generates a 14% reduction in the slope of the price Phillips curve and a 13% reduction in the slope of the wage Phillips curve, conditional on the same-sized demand shocks in both economies. The price Phillips curve result accounts for 82% of the empirical estimate (17%). The model overstates the flattening of the wage Phillips curve (13% vs. 9% in the data), and therefore understates the reduction in the wage-to-price pass-through.

Mechanisms. Automation flattens the Phillips curve through two primary channels. First, the outside option of automating production reduces workers’ bargaining power and dampens the elasticity of wages to unemployment (the “Wage Setting Effect”). Second, a higher share of robot firms reduces the aggregate labor share, muting the pass-through from wages into prices (the “Steady State Effect”). A third channel — firms cyclically substituting workers for machines in response to a shock (the “Cyclical Effect”) — operates during the transition but the Wage Setting Effect accounts for the bulk of the flattening.

Non-linearity and the post-Covid resurgence. When robot-production is subject to convex adjustment costs, the threat of automation that underlies the Wage Setting Effect becomes inoperative during large expansionary shocks. When investment in machines surges, the marginal cost of producing robots rises sharply, raising the price of machines and pushing the automation threshold downward — more firms must use labor. Workers then negotiate higher wages, which pass into prices. Conditional on small demand shocks, the high-automation economy still exhibits a flatter Phillips curve than the low-automation economy. Conditional on large demand shocks (simulated as a 2 percentage point drop in unemployment), there is no difference in the inflation response between the low- and high-automation economies, so the Phillips curve reverts to steep.

In depth

Q1. What is the exact empirical specification and how does it map to a structural object?

The regression is: non-tradable goods inflation = β × lagged unemployment + γ × (lagged unemployment × demeaned robot adoption) + ζ × lagged robot adoption + χ × relative non-tradable price + MSA fixed effects + year fixed effects + error. In a multi-region model without automation, Hazell et al. (2022) show that the coefficient β identifies the aggregate slope of the Phillips curve because year fixed effects absorb both common inflation expectations and the endogenous monetary policy response to aggregate demand shocks. Adding the interaction term extends this logic: γ identifies how robot adoption causally shifts the slope of the local Phillips curve, which maps into changes in the aggregate slope.

Q2. What are the first-stage instruments and why are they valid?

Unemployment is instrumented with local tradable demand spillovers — a Bartik variable weighting national industry value-added growth (excluding each MSA’s own contribution) by each MSA’s average industry value-added shares, so national supply disturbances uncorrelated with MSA-level heterogeneity generate plausibly exogenous unemployment variation. Robot adoption is instrumented with the implied robot-per-employee ratio obtained by replacing U.S. industry robot installations with the average across the five largest European economies, weighted by U.S. industry employment shares; this isolates the supply-side efficiency improvements in robot technology that drove global adoption, conditional on robot demand shocks being weakly correlated across countries. The correlation between the two instruments in the sample is 0.2, ensuring they do not strongly co-move.

Q3. What are the point estimates and their magnitudes in the baseline IV regression?

For price inflation (Panel A, Column 4), the base sensitivity β = −0.5069 (SE 0.1381, significant at 1%), and the interaction coefficient γ = 0.0066 (SE 0.0030, significant at 5%). For wage inflation (Panel B, Column 4), β = −0.9580 (SE 0.2450, significant at 1%), and γ = 0.0049 (SE 0.0024, significant at 5%). A one standard deviation increase in robot adoption reduces price inflation sensitivity by 17% and wage inflation sensitivity by 9% relative to the average-automation MSA.

Q4. What does the difference in flattening magnitudes (17% for prices vs. 9% for wages) imply about the wage-price pass-through?

Because automation reduces the price Phillips curve slope by proportionally more than the wage Phillips curve slope, each percentage-point change in wages translates into a smaller percentage-point change in prices in higher-automation areas. This indicates that robot adoption diminishes the influence of wage changes on price changes — i.e., it reduces the wage-to-price pass-through. In the model, this operates through the Steady State Effect: a larger share of production carried out by robot firms means that a given change in average wages applies to a smaller portion of total marginal costs, weakening the price response.

Q5. How is the automation threshold determined in the theoretical model, and what economic forces govern it?

A producer opts for the labor technology if and only if the expected value of a labor firm (= job-filling probability × (producer price × labor efficiency − posted wage) − entry cost) exceeds the value of a robot firm (= producer price × robot efficiency − machine price − entry cost). Since the value of a labor firm increases in labor efficiency, there is a unique cut-off efficiency level γ* at which a producer is indifferent. Producers with labor efficiency above γ* post vacancies; those below γ* install robots. The cut-off rises (more automation) when wages rise relative to machine prices, and falls (less automation) when machine prices rise due to costly robot production during large expansionary shocks.

Q6. How does the wage-posting equilibrium under directed search generate the Wage Setting Effect of automation?

Under directed search, each labor firm posts a wage to maximize its expected value, and workers sort into sub-markets offering higher wages but lower job-finding probabilities. The equilibrium posted wage for a firm with labor efficiency γj is Wγj,t = PP,t × γj × (1 − η), where η is the elasticity of matches to vacancies. The option to install a robot — available at any time — limits how much any individual firm needs to offer workers. When automation increases, the outside option becomes more attractive to more firms, which constrains wage offers industry-wide, reducing the elasticity of average wages to unemployment fluctuations.

Q7. How is the slope of the price Phillips curve characterized analytically?

Log-linearizing the model around the steady state and substituting labor market and wholesaler equilibrium conditions into the pricing equation yields: inflation = −[(ε−1)/φ] × Ψ(γ*; Θ) × unemployment gap + β × expected future inflation, where Ψ(γ*; Θ) is a function of the automation cut-off γ*, the elasticity of substitution ε, the matching function elasticity η, the efficiency bounds γM and γH, and the distribution shape parameter α. In contrast to standard New Keynesian models where the slope depends only on markup and nominal rigidity parameters, this expression depends directly on the degree of automation through the steady-state threshold γ*.

Q8. Across different structural parameter configurations, does automation always flatten the Phillips curve?

Yes. Numerical analysis of the closed-form Phillips curve expression (Figure 1) shows that robot adoption unambiguously decreases the slope of the price Phillips curve across all combinations of the key structural parameters — the distribution shape parameter α, the matching elasticity η, the upper bound of labor efficiency γH, and the steady-state unemployment rate ū. The flattening effect is more pronounced when η is low, when α implies a larger fraction of low-efficiency producers, and when the steady-state unemployment rate is low.

Q9. How do the three mechanism channels (Cyclical, Wage Setting, Steady State) compare quantitatively?

The paper isolates channels by comparing alternative model specifications: (i) Baseline directed search with endogenous automation, (ii) Directed search with fixed automation (removing Cyclical and Wage Setting Effects, leaving only the Steady State Effect), (iii) Random search with τ = 0.5 (efficient bargaining, retaining both the Cyclical and Wage Setting Effects), (iv) Random search with τ = 0.01 (near-zero worker bargaining power, removing the Wage Setting Effect but retaining the Cyclical Effect). Figure 5 shows that the Steady State Effect alone accounts for only a small portion of the total inflation differential between low- and high-automation economies. The Wage Setting Effect — isolated by comparing τ = 0.01 and τ = 0.5 economies with endogenous automation — accounts for the bulk of the flattening. The Cyclical Effect (isolated by comparing fixed and endogenous automation with τ = 0.01) contributes an intermediate amount.

Q10. What is the quantitative exercise comparing low- and high-automation steady states?

The low-automation economy targets the U.S. robot-per-employee ratio of 0.2% in the early 2000s (Acemoglu and Restrepo, 2020a), calibrated with robot-specific technological change ζ = 2. The high-automation economy features a 200% higher robot-per-employee ratio of 0.6%, calibrated to replicate one standard deviation of cross-MSA dispersion in robot penetration in the data. Both economies are simulated with 10,000 realizations of preference shocks, and the slopes of the price and wage Phillips curves are estimated from simulated inflation and unemployment outcomes. The price Phillips curve flattens by 14% and the wage Phillips curve by 13% moving from low to high automation, conditional on the same-sized shock in both economies.

Q11. How does the model account for the Covid-era resurgence of high inflation despite high automation?

The paper extends the machine manufacturer’s production function to include an asymmetric convex adjustment cost that activates when investment deviates more than 5% from its steady-state level (parameterized with δ = 0.0015 and ϱ = 100). Under a small expansionary shock (0.25 percentage point decrease in unemployment), inflation rises less in the high-automation economy, consistent with a flat Phillips curve. Under a large expansionary shock (2 percentage point decrease in unemployment), the surge in robot investment triggers sharply rising machine prices, eliminating the automation outside option for marginal producers and fully restoring workers’ bargaining power — so the inflation response is identical in the low- and high-automation economies, consistent with a steep Phillips curve. The paper interprets this as a proof-of-concept consistent with post-Covid wage compression evidence for low-wage workers documented by Autor, Dube, and McGrew (2023).

Q12. What do the robustness checks establish regarding alternative explanations?

The interaction of unemployment and robot adoption remains statistically significant at the 5% level across all the robustness checks (Appendix A). These include controlling for: (i) demographic heterogeneity — shares of young (below 30) and old (above 60) individuals, female/Black/Asian labor market participation, low-education attainment shares, overall participation, and MSA-level average marginal propensity to consume (MPC); (ii) occupational structure — shares of abstract, routine, manual, and offshorable occupations; and (iii) import competition — MSA exposure to Chinese and Mexican import competition. The coefficient on the robot-unemployment interaction term is stable across specifications, with the magnitude remaining close to that in the baseline (approximately 0.0140 across all demographic robustness columns in Table A.1).

Key Concepts

Automation threshold (γ):* The paper-specific level of idiosyncratic labor efficiency at which a producer is indifferent between installing a robot and posting a vacancy. Producers with labor efficiency below γ* choose the machine technology; those above choose the labor technology. The threshold is determined by the relative profitability of the two technologies, and it shifts endogenously with wages, machine prices, and job-filling probabilities. A higher γ* means more of the production sector is automated.

Wage Setting Effect of automation: The channel through which the existence of the outside option to install robots reduces workers’ bargaining power and dampens the elasticity of wages to unemployment fluctuations. Under directed search, firms’ ability to substitute machines for labor at a lower cost constrains the wage offers they need to post, so that a given decline in unemployment generates a smaller increase in average wages in higher-automation economies.

Steady State Effect of automation: The channel through which a larger steady-state fraction of robot firms reduces the aggregate labor share, so that even a given change in wages translates into a smaller change in aggregate marginal costs and prices. This channel operates even when automation cannot change upon a shock (fixed automation baseline).

Cyclical Effect of automation: The channel through which firms actively replace workers with machines in response to expansionary shocks that raise wages, generating an endogenous dampening of labor demand and putting downward pressure on the wage increase itself. This channel requires endogenous automation choices at business-cycle frequencies.

Robot-specific technological change (ζ): In the paper’s model, the parameter governing the efficiency with which machine manufacturers transform final goods into robots. A higher ζ reduces the relative price of machines (PM/P = 1/ζ), making automation more attractive to lower-efficiency producers and raising the automation threshold γ*. In quantitative exercises, variation in ζ across steady states drives differences in the degree of automation.

Price Phillips curve slope (Ψ): In the paper’s log-linearized model, the structural coefficient linking inflation to the unemployment gap. Unlike in standard New Keynesian models — where the slope depends only on the markup and nominal rigidity — Ψ is a function of the automation threshold γ*, the matching elasticity η, the efficiency distribution parameters (γM, γH, α), and the elasticity of substitution ε. Robot adoption shifts γ* and thereby changes Ψ.

Asymmetric investment adjustment cost: An extension of the machine manufacturer’s production function that imposes convex costs when robot investment deviates above 5% from its steady-state level (parameterized by δ and ϱ). This specification makes it increasingly costly to rapidly scale up automation in response to large demand shocks, causing the machine price to spike and the automation outside option to cease being effective for marginal producers, thereby restoring workers’ bargaining power and steepening the Phillips curve during large expansionary episodes.

Supply, Demand, Institutions, and Firms: A Theory of Labor Market Sorting and the Wage Distribution

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

Layer 1 — Overview

Research question. How do workforce composition (labor supply), labor demand, and minimum wage policy jointly determine the wage distribution in imperfectly competitive labor markets, and what were the quantitative contributions of each force to the dramatic decline in Brazilian wage inequality between 1998 and 2012?

Motivation. Brazil’s formal-sector wage inequality fell sharply over this period. Three candidate shocks are well-documented: (1) a large increase in educational attainment — the share of adults completing at least secondary school rose by 20 percentage points (a 68 percent increase) between 1998 and 2012; (2) labor demand shocks, primarily the commodities boom of the 2000s; and (3) a 93.7 percent (66.1 log point) real increase in the federal minimum wage. Existing frameworks analyze these shocks separately — competitive supply/demand models on one side and imperfectly competitive minimum wage models on the other — and therefore cannot detect interactions or jointly explain all observed patterns, including the novel finding that assortative matching between high-wage workers and high-wage establishments rose in 104 out of 151 microregions, a fact inconsistent with the predictions of leading minimum wage models.

Data. The paper uses the RAIS (Relação Anual de Informações Sociais), a confidential linked employer-employee dataset covering the Brazilian formal sector, together with Brazilian Census data for 1991, 2000, and 2010. Statistics are computed for 151 microregions (analogous to US commuting zones) with at least 15,000 workers in RAIS in both base years and at least 1,000 formal workers per educational group. The final sample covers 73 percent of the adult population. Firm wage premiums and assortative matching are measured via AKM two-way fixed effects regressions using the bias-corrected KSS (Kline, Saggio, Sølvsten 2018) estimator, run separately for each microregion and period on three-year panels.

Theoretical framework. The paper develops a unified general-equilibrium model featuring: (i) a task-based production function with distance-dependent complementarity between worker types; (ii) monopsony power arising from idiosyncratic worker preferences for firms, generating constant firm-level labor supply elasticity β (calibrated at 4, implying markdowns of 20 percent); (iii) heterogeneous firms differentiated by their production “blueprints” (the complexity of tasks they require), with blueprint shape parameterized as a Gamma distribution; and (iv) free firm entry, endogenous participation, and goods market general equilibrium with CES consumer preferences (elasticity σ). A key result is that firms with different blueprints exhibit different within-firm substitution patterns: worker types that are substitutes at low-skill, low-wage firms may be complements at high-skill, high-wage firms.

Estimation. A parsimonious parameterization is estimated by simultaneous-equation nonlinear least squares, targeting 26 endogenous outcomes per region (13 per period) including between- and within-group wage inequality, variance of establishment effects, covariance of worker and establishment effects, formal employment rates by education, and minimum wage bindingness. The model requires solving for equilibrium more than 15,000 times per optimization step (151 regions × 2 periods × 53 Jacobian columns). The elasticity of substitution between goods is estimated at σ = 8.36 (significantly above 1), and the aggregate labor supply parameter λ implies formal-sector elasticities of approximately 0.6–0.7 for college workers and around 1.1 for less-than-secondary workers. The model fits the data well, with R² above 0.5 for most targeted moments and perfect fit for the six moments used in the inversion procedure.

Main findings.

Demand shocks and the minimum wage are the primary drivers of falling inequality. In counterfactual simulations, the minimum wage alone (a 66.1 log point increase) reduces the variance of log wages by 0.13. Demand shocks reduce it by a further 0.18. Supply shocks (rising education) increase the variance by 0.04, leaving their net inequality-reducing contribution negligible.
Supply shocks increase assortative matching despite compressing within-firm skill premiums. Within-firm task reassignment would reduce the variance of log wages by 0.221 and the correlation between worker and establishment effects by 0.165, holding production levels and firm entry fixed. However, scale, entry, and price adjustments — driven by the large estimated σ = 8.36 > β + 1 = 5 — reallocate skilled labor toward high-wage, skill-intensive firms, counteracting within-firm compression and raising assortative matching by 0.189. These two channels largely offset each other.
Concurrent supply and demand changes attenuate minimum wage impacts by roughly half. When the minimum wage is the only shock, it would have reduced the variance of log wages by 0.13; in the presence of supply and demand changes, its incremental contribution is approximately 0.07. Minimum wage effects on sorting (which would reduce assortative matching when acting alone) disappear when accompanied by supply and demand transformations.
Minimum wage effects are concentrated in the bottom two productivity deciles. Wage effects for workers in productivity deciles three through ten from the minimum wage are approximately 1 percent or less once all channels are considered. Strong wage gains are concentrated at the bottom, primarily through the monopsony channel. The wage-posting channel (within-firm returns to skill) reduces wages for low- and middle-skill workers and raises them at the top two deciles due to the reallocation of low-skilled workers toward high-wage firms, which reduces those workers’ marginal products there.
Cross-firm differences in substitution patterns generate non-standard minimum wage spillovers. Conditional on the task demands of the firm employing them, a pair of worker types may be substitutes in low-skill firms and complements in high-skill firms. This firm-heterogeneity channel causes minimum wage impacts to be non-monotone across the productivity distribution, contrasting with the smooth inequality-reducing effects predicted by both competitive task-based models and frictional minimum wage models.

In depth

Q1. What is the novel empirical fact that motivates the unified framework?

A: Using KSS bias-corrected AKM decompositions performed separately for each of 151 microregions, the paper documents that assortative matching — measured as the correlation between worker and establishment fixed effects — rises in 104 out of 151 regions between 1998 and 2012. The covariance term accounts for less than 7 percent of the average decline in the variance of log wages. This finding is inconsistent with the leading imperfectly competitive minimum wage model (Engbom and Moser 2022), in which minimum wages reduce assortative matching. It is also inconsistent with purely competitive supply/demand models, which have no role for firm wage premiums or sorting. The divergence from prior national-level studies (which do not find rising sorting) is explained by the fact that national-level sorting conflates geographical sorting with supply-demand dynamics.

Q2. What is the key mechanism through which the task-based production function generates cross-firm differences in substitution patterns?

A: In the task-based production function, each firm assigns workers to tasks assortatively — lower types handle lower-complexity tasks, higher types handle higher-complexity tasks, with cutoff thresholds determined by the firm’s blueprint. When a firm has a blueprint concentrated in complex tasks (a high-skill, high-wage firm), adjacent worker types are more differentiated in the tasks they perform, making them complements. When a firm has a blueprint concentrated in simple tasks (a low-skill, low-wage firm), adjacent worker types are assigned to a narrow, similar range of tasks and are therefore closer substitutes. The elasticity of complementarity between any pair of worker types is thus endogenous, depending on which tasks the firm uses and, in the monopsony case, on the firm’s skill intensity — a prediction validated empirically using nonroutine cognitive task content data for Brazilian occupations.

Q3. Under what conditions can a positive supply shock (rising educational attainment) widen the aggregate skill wage premium rather than compress it?

A: The paper’s Proposition 4 and Corollary 2 show that a supply shock that increases the relative supply of skilled workers can widen the aggregate skill wage premium when the elasticity of substitution between goods (σ) exceeds the firm-level elasticity of labor supply plus one (β + 1). Intuitively, when σ is large, the reduction in prices for skill-intensive goods generated by the supply shock shifts consumption toward those goods, causing net entry of skill-intensive firms. If the gains in firm wage premiums earned by skilled workers reallocated to those firms outweigh the compression in within-firm productivity differentials, the aggregate skill premium can rise. This mechanism does not require non-convexities from endogenous innovation; it operates through imperfect competition and firm entry alone. In the estimated Brazilian model, σ = 8.36 substantially exceeds β + 1 = 5, so this condition holds, explaining why rising education increases rather than compresses assortative matching in the data.

Q4. How does the model generate positive employment effects from minimum wages, and how do these interact with reallocation?

A: In the monopsonistic baseline without a minimum wage, firms post wages below workers’ marginal revenue products, causing some workers to choose non-employment. A minimum wage increase raises posted wages at constrained firms, shifting some workers from non-employment (or home production) to formal employment, generating positive employment effects at the margin where the minimum wage binds. Simultaneously, minimum wages price out the least productive workers at low-wage firms (disemployment), while workers in the intermediate productivity range reallocate from low- to high-wage firms, because high-wage firms have higher revenue productivity and can profitably hire workers that low-wage firms can no longer afford. The net employment elasticity for the lowest productivity decile with respect to the log minimum wage is −0.61 (Table 7), while the mean wage for that decile rises substantially through the monopsony channel.

Q5. What are the three channels through which the minimum wage affects wages and employment in the model, and what does each channel contribute?

A: The paper decomposes minimum wage effects into three channels. Channel 1 (monopsony): mechanical wage increases, positive employment effects at firms where the minimum wage binds, disemployment of very low-productivity workers, and reallocation from low- to high-wage firms, holding posted wage schedules, prices, and entry fixed. This channel accounts for nearly all of the strong wage effects at the bottom two productivity deciles. Channel 2 (wage posting): firms reoptimize earnings schedules following changes in worker composition and marginal products induced by Channel 1, holding prices and entry fixed. This channel reduces wages for low- and middle-skill workers (productivity deciles 1–7) by approximately 0.01–0.02 log points and increases wages for top deciles (decile 9: +0.04, decile 10: +0.11), because reallocation of low-skill labor to high-wage firms lowers those workers’ marginal products there. Channel 3 (general equilibrium): firm entry and price responses. The fall in low-wage-firm profits causes entry of high-wage, skill-intensive firms, while the price of low-skill goods falls. General equilibrium effects generate modest positive wage effects for most workers but negative effects for very low-productivity workers due to reduced aggregate demand for low-skill labor.

Q6. Why do the minimum wage’s inequality-reducing effects diminish when accompanied by concurrent supply and demand changes?

A: The paper documents that, under concurrent supply and demand transformations, the minimum wage’s reduction of the variance of log wages is approximately 0.07, roughly half the 0.13 reduction it would achieve acting alone. The attenuation occurs through interactions: supply and demand shocks raise the average productivity level of the labor market and shift workers toward high-wage, skill-intensive firms. In this altered equilibrium, the minimum wage binds less tightly (or hits a different part of the distribution), and the reallocation effects of the minimum wage that would normally reduce assortative matching are offset by the sorting-increasing effects of supply and demand changes. The estimated model shows that interactions between the minimum wage and supply/demand changes (columns 6, 7, 8 of Table 5) are economically meaningful, something undetectable without a unified framework.

Q7. How does the model’s prediction regarding minimum wage spillovers differ from Engbom and Moser (2022), and what explains the difference?

A: Engbom and Moser (2022) find that the Brazilian minimum wage hike had significant wage effects extending far up the worker productivity distribution, while this paper’s model finds negligible effects (approximately 1 percent) beyond the bottom two productivity deciles. Two structural differences explain this divergence. First, Engbom and Moser (2022) assume perfect substitutability between worker types within firms, so a minimum wage increase at low-wage firms mechanically raises posted wages at all other firms to maintain relative competitiveness. In this paper’s framework, wage-posting responses at high-wage firms can be negative for low-skill workers because the inflow of reallocated low-skill workers reduces their marginal products — a channel absent under perfect substitution. Second, Engbom and Moser (2022) use a national model, allowing displaced low-skill workers to reallocate to top-productivity firms anywhere in the country, dampening disemployment; this paper’s local labor markets approach restricts reallocation to within-region boundaries, consistent with low rates of interregional migration documented for Brazil by Dix-Carneiro and Kovak (2017).

Q8. How are firm wage premiums generated in the model, and why do differences in physical productivity between firms not generate wage differentials?

A: Proposition 3 establishes that wage dispersion for similar workers across firms requires either (i) differences in blueprint shapes (firm heterogeneity in skill intensity) or (ii) differences in entry costs. Differences in physical productivity (z_g) or consumer taste parameters alone are insufficient, because with equal entry costs, differences in productivity lead to additional firm entry until the marginal revenue product of labor is equalized across firm types. Wage premiums proportional to entry costs arise because optimal firm creation requires larger-scale operation for higher-entry-cost firms, and hiring more workers forces those firms to post higher wages. Additionally, skill-intensive firms (firms with blueprints tilted toward complex tasks) pay relative wage premiums for the worker types they use most intensively, and if skill intensity and entry costs co-vary, all workers at high-skill firms may receive a wage premium.

Q9. How does the estimation procedure handle unobserved regional heterogeneity in labor demand?

A: Demand shocks are not directly observed; they are inferred as a residual from changes in targeted outcomes after accounting for observed supply (education shares from Census) and minimum wage changes. Five region-time-specific demand parameters — TFP (z), blueprint complexities (θ₁, θ₂), relative entry costs (F₂/F₁), and relative consumer preferences (γ₂/γ₁) — are modeled as linear functions of 1998 regional covariates (educational shares, agricultural share, manufacturing share, and initial minimum wage bindingness) with time-specific coefficients. This formulation allows unobserved demand shifters to correlate with initial educational levels, preventing incorrect attribution of demand-supply correlations to causal supply effects. Region-specific parameters (TFP in each period, education-group-specific formal employment shifters) are inverted exactly from six targeted moments within each region, eliminating incidental parameter bias.

Q10. What micro-level empirical validations does the paper conduct for the task-based model’s mechanisms?

A: The paper tests four micro-level predictions using nonroutine cognitive task content data for Brazilian occupations. First, skill-intensive firms have greater demand for complex tasks (consistent with Figure 1 of the model). Second, within firms, more skilled workers are assigned to more complex tasks (Lemma 1). Third, workers who move to more skill-intensive firms are assigned more complex tasks (Lemma 2, consistent with the monopsony model’s mismatch prediction). Fourth, wage gaps between high- and low-skill firms are larger for skilled workers (Proposition 3). The paper reports finding strong support for all four predictions in the data, lending credibility to the theoretical structure and quantitative results.

Key Concepts

Task-based production function (paper’s definition): A production function in which a firm produces output by assigning workers of different types to tasks indexed by complexity. The assignment is assortatively optimal: lower-type workers handle lower-complexity tasks, with unique threshold complexities separating adjacent worker types. The critical property is distance-dependent complementarity — any pair of worker types that are “close” in skill rank are substitutes, while pairs distant in skill rank are complements. This differs from CES production functions where the elasticity of complementarity is the same for all pairs; in the task-based version, substitutability depends on endogenous assignment and thus on the firm’s blueprint.

Blueprint (paper’s definition): A function b_g(x) that specifies the density of tasks of each complexity level x required to produce one unit of good g. It is the fundamental source of firm heterogeneity in the model: firms producing goods with blueprints tilted toward complex tasks are more skill-intensive, hire workers of higher average type, and pay higher wages. The paper parameterizes blueprints as Gamma distributions with shape parameter θ_g indexing average task complexity; firms with higher θ_g are more skill-intensive.

Firm wage premium (paper’s definition): The component of wages at a given establishment that accrues equally to all workers at that firm regardless of their type, measured as the establishment fixed effect ψ_j in AKM two-way fixed effects regressions. In this model, firm wage premiums arise from heterogeneity in blueprints (skill intensity) and entry costs, not from differences in TFP or consumer tastes. Under monopsony, firms with higher entry costs must operate at larger scale and post higher wages; blueprint heterogeneity generates differential wage premiums by skill type.

Sorting / assortative matching (paper’s definition): The correlation between the worker fixed effect (ν_i,r capturing worker skill) and the establishment fixed effect (ψ_j capturing firm wage premium) in the AKM decomposition, measured as Cov(ν_i,r, ψ_{J(i,r,τ)} | r). In this paper’s framework, sorting arises because firms with blueprints demanding complex tasks (high-wage firms) have a comparative advantage in employing high-skill workers; labor market sorting can therefore change over time due to supply, demand, or minimum wage shocks, even without changes in search frictions.

Monopsony power / markdown (paper’s definition): Arising from idiosyncratic worker preferences for firms (modeled as a nested logit), firms face upward-sloping labor supply curves with constant firm-level elasticity β. Optimal posted wages equal a constant markdown β/(β+1) of the marginal revenue product of labor, set to β = 4 (implying a 20 percent markdown). The macro elasticity of formal sector labor supply is governed by a separate parameter λ, estimated from the data, yielding aggregate formal-sector supply elasticities of approximately 0.6–0.7 for college workers and around 1.1 for less-educated workers.

Wage posting responses (paper’s definition): The second channel of minimum wage effects, in which firms reoptimize their entire earnings schedule following the wage-composition changes induced by the minimum wage’s mechanical and reallocation effects (Channel 1), while keeping goods prices and firm entry fixed. Because task-based production functions are concave, changes in factor proportions (due to reallocation of low-skill workers to high-wage firms) alter marginal products of all worker types within those firms, causing firms to adjust all posted wages — not just those directly constrained by the minimum wage.

Distance-dependent complementarity (paper’s definition): The property, proven as a Corollary to Proposition 1, that for a fixed worker type h, the partial elasticity of complementarity between h and any other type h’ is strictly increasing in h’ for h’ ≥ h (more distant high types are stronger complements) and strictly decreasing in h’ for h’ ≤ h (more distant low types are weaker substitutes / stronger complements). This pattern results from the division of labor: adding a very different worker type allows specialization gains that do not arise when adding similar-type workers competing for the same tasks.

The Earnings and Labor Supply of U.S. Physicians

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

Overview

Research Question. What do U.S. physicians earn, how is that earnings variation structured across geography and specialty, and how much does government healthcare payment policy shape those earnings and — through them — physicians’ labor supply and long-run talent allocation?

Data. The paper builds a novel administrative panel by merging the universe of U.S. federal individual income tax returns (2005–2017) with: the National Plan and Provider Enumeration System (NPPES) physician registry; Medicare billing records with procedure-level Relative Value Unit (RVU) rates (2012–2017); restricted-use American Community Survey responses; Social Security Administration demographic records; and medical school ranking and graduation data. The main sample covers 11.6 million physician-year observations for 965,000 unique physicians aged 20–70.

Earnings Facts. In 2017, average physician total individual income was $350,000 (median $265,000); the distribution is right-skewed — the top 1% of age-40–55 physicians averages $4.0 million. Physicians in aggregate earned $297 billion in pre-tax dollars, equaling 8.6% of total U.S. healthcare spending. The age-earnings profile is steep: earnings are approximately $60,000 during residency, rise to roughly $185,000 by the early thirties, and peak near $425,000 at age 50. Business income — systematically underreported in survey data (ACS estimates are approximately $140,000 lower than tax data during peak career years, almost entirely due to non-reporting of business income) — accounts for nearly one-quarter of earnings at age 50. Earnings differ sharply across specialties: primary care physicians average $201,200 (ages 40–55), about half the sample mean, while surgeons earn roughly twice as much.

Geographic Pattern. Contrary to the pattern for lawyers and workers broadly, physician earnings are not highest on the coasts. A movers-based event study (physicians who changed commuting zones once during 2005–2017) finds that roughly 70% of the cross-location income difference is driven by place rather than worker composition. A two-way fixed-effects variance decomposition reveals pronounced negative physician-location sorting: high-earning physicians tend to locate in lower-income commuting zones, while lower-earning physicians locate in higher-income areas — the opposite of the pattern for lawyers. Medicare’s relatively weak adjustment of reimbursement rates for local costs (the empirical elasticity of the Geographic Adjustment Factor to median household income is 0.09, versus 0.33 for a broader local price index) can, by the authors’ estimates, account for approximately one-third of this unusual geographic earnings pattern.

Government Influence — Medicare Price Changes. Using procedure-specific RVU changes as a simulated instrument for each physician’s Medicare price exposure, the authors find that a 10% increase in the Medicare price instrument leads to a 2.4% increase in professional earnings of physicians aged 40–55. The behavioral supply response is substantial: physicians bill 4.4% more RVUs (supply elasticity of 0.4 after netting out the mechanical component), of which 3.9% reflects more unique procedures and the rest a shift toward higher-paid procedures. Nearly all of the procedure-level supply increase (3.4 out of 3.8 percentage points) comes from treating additional patients rather than more frequent treatment of existing patients. Converting to pass-through: physicians retain $62 of each $100 in additional Medicare spending directly, or approximately $25 of each $100 of any insurance spending once Medicare’s documented spillover into private insurance rates is accounted for. For physicians aged 56–70, a 10% increase in earnings driven by reimbursement changes reduces retirement probability by 0.5 percentage points in that year.

Government Influence — ACA Insurance Expansion. Using county-level variation in pre-ACA uninsurance rates (as of 2013) as a source of differential exposure to the ACA’s Medicaid expansions and Marketplace subsidies (in 24 states expanding Medicaid in 2014 or early 2015), the authors estimate that a 10 percentage point higher baseline uninsurance rate led to 3.9% higher physician earnings four years post-expansion. Scaling by the first stage (a 10 p.p. higher uninsurance rate translating to 4.96 p.p. higher insurance coverage post-expansion), the implied elasticity of physician earnings to the insurance rate is 0.41. The ACA expansion also reduced retirement probability — a 10 p.p. higher insurance coverage rate leads to a 1 p.p. decline in retirement probability — consistent with a medium-run retirement-to-income elasticity of approximately −1.1. In aggregate, 6% of the $110 billion in annual ACA insurance expansion spending accrued to physicians personally, slightly below their 8.6% baseline share of healthcare spending.

Talent Allocation. Specialty choice is sticky and entry-restricted. The authors estimate a discrete-choice model of specialty choice using graduates of top-5 medical schools — physicians with effectively unconstrained specialty access — and an aggregate model using USMLE Step 1 score buckets as ability proxies. At the top of the ability distribution, higher specialty earnings strongly attract physicians: increasing primary care physicians’ hourly income from $98 to $168 per hour (the level of medicine subspecialists) would raise the share of top-5 medical school graduates choosing primary care by approximately 20 percentage points (nearly doubling their representation in primary care). Moving down the USMLE score distribution, the earnings coefficient falls monotonically and turns negative for the lowest score groups — consistent with the model’s prediction that entry restrictions cause higher-paying specialties to displace lower-ability applicants as earnings rise, rather than simply attracting more entrants. A more modest counterfactual — raising internal medicine earnings to dermatology levels — raises the average USMLE score in internal medicine by 10 points (from 230.2 to 239.6).

Scope Conditions. The earnings estimates are for the period 2005–2017. Pass-through estimates use a short-run price instrument; long-run pass-through may differ depending on private market spillovers and entry. The ACA analysis is restricted to 24 early-expanding states. The specialty-choice model is estimated on medical graduates entering the residency match; the extensive margin of entering medicine itself is not modeled. Health outcome effects of changing physician ability distributions are not estimated.

In depth

Q1. What is the level and composition of physician earnings in the tax data, and how do they compare to survey-based estimates?

In 2017, average physician total individual income was $350,000 and median was $265,000; the top 1% of age-40–55 physicians earned $4.0 million on average, more than twice the average of the top 5%. Business income constitutes nearly one-quarter of earnings at age 50 and is concentrated among top earners: 80% of physicians in the top 1% have business income exceeding $25,000, versus 35% overall. ACS survey data for the same physicians underestimate earnings by approximately $140,000 (roughly one-third of the administrative mean) during peak career years, driven entirely by non-reporting of business income on the extensive margin.

Physicians in aggregate earned $297 billion pre-tax in 2017, equaling 8.6% of total U.S. healthcare spending (approximately $913 of the average American’s $10,611 annual healthcare expenditure). After applying a 30% income tax rate, after-tax physician earnings equal approximately 6% of total healthcare spending, or roughly 1% of GDP. The authors note this provides an upper bound on the magnitude of savings available from policies aimed at reducing physician incomes as a strategy for lowering overall healthcare spending.

Q3. How does the age-earnings profile of physicians evolve, and what drives growth during peak years?

Physician earnings average approximately $60,000 during residency, rise to roughly $185,000 by the early thirties, and peak near $425,000 at age 50, before declining gradually to approximately $270,000 in the late 60s. Growth during peak earning years (ages 40–55) is driven almost entirely by business income: average wages are approximately flat at $285,000 across this age range, while business income and the probability of filing Schedule C rise steadily.

Q4. How large and unusual is the geographic pattern of physician earnings, and what is the causal role of location?

Physician earnings are highest in lower-income states (not on the coasts), unlike lawyers and the broader workforce. A movers event study finds that approximately 70% of the cross-commuting-zone income difference is attributable to location rather than worker characteristics; within specialty the estimate rises to approximately 85%. A two-way fixed-effects variance decomposition (with limited-mobility-bias corrections following Andrews et al. 2008 and Kline et al. 2020) reveals pronounced negative physician-location sorting, with the corrected covariance between individual and location effects being 0.6–0.8 times the variance of location effects in magnitude but opposite in sign — a pattern that reverses to positive sorting when the same methods are applied to lawyers.

Q5. What instrument is used to identify the causal effect of Medicare price changes on physician earnings, and why is it valid?

The authors construct a physician-year “Medicare price instrument” by fixing each physician’s service mix at its 2012–2017 average and then multiplying those fixed quantities by annually-updated RVU rates, summing over services. Because the fixed quantity weights exclude behavioral responses, and because national RVU changes from CMS periodic reviews affect physicians differentially according to their pre-determined service mix, variation across physicians and over time is plausibly exogenous to individual physicians’ income shocks. Year-by-specialty fixed effects absorb common specialty-level price trends.

Q6. What are the magnitudes of the earnings and labor supply responses to Medicare price changes?

A 10% increase in the Medicare price instrument raises earnings of 40–55 year-old physicians by 2.4% (reduced-form), with a 2SLS elasticity of income to billed RVUs of 0.17. The total-RVU billing coefficient of 1.437 implies a supply elasticity of 0.437 (subtracting 1 for the mechanical component). At the procedure level, a 10% price increase for a specific code leads to 3.8% more billings for that code, of which 3.4 percentage points reflects treating additional patients. For physicians aged 56–70, a 10% earnings increase reduces that year’s retirement probability by 0.5 percentage points.

Q7. How does the ACA insurance expansion affect physician earnings and retirement, and what is the implied pass-through?

Counties with a 10 percentage point higher pre-ACA uninsurance rate saw 3.9% higher physician earnings by 2017 (four years post-expansion). Scaled by the first stage (4.96 p.p. higher coverage), the elasticity of physician earnings to insurance coverage is 0.41. A 10 p.p. higher insurance coverage rate leads to a 1 p.p. lower retirement probability post-expansion (medium-run elasticity of retirement to income of approximately −1.1). In aggregate, 6% of $110 billion in annual ACA expansion spending — roughly $7.1 billion, or about $8,400 per physician — accrued to physicians.

Q8. How does the earnings-specialty choice relationship vary across the physician ability distribution?

In the individual-level discrete-choice model estimated on top-5 medical school graduates (likely unconstrained in specialty choice), the coefficient on hourly earnings is 0.014. In the aggregate score-group model, the implied earnings coefficient is 0.016 for USMLE scores above 260 and declines monotonically to −0.008 for scores at or below 190. This negative coefficient for low scorers is consistent with the theoretical prediction that higher earnings attract high-ability physicians, leaving fewer slots for lower-ability applicants due to binding entry restrictions — not a reversal of preferences.

Q9. What are the quantitative implications for specialty choice if primary care incomes were raised to subspecialty levels?

Raising primary care hourly income from $98 to $168 (the level of medicine subspecialists) would increase the share of top-5 medical school graduates choosing primary care by approximately 20 percentage points (about 48% would enter primary care, versus the current share), nearly doubling their representation. Nearly half of these reallocations would come from procedural specialties. An analogous exercise raising internal medicine earnings to dermatology levels shifts the average USMLE score in internal medicine from 230.2 to 239.6 — a 10-point increase — as higher-scoring applicants displace lower-scoring ones within a fixed slot constraint.

Direct estimates imply physicians retain $62 of each $100 in additional Medicare spending. Accounting for Medicare’s documented spillover into private insurance rates (following Clemens and Gottlieb 2017), the pass-through drops to $25 per $100 of total insurance spending. The authors note this is substantially higher than the modest rent-sharing found for average workers in response to firm-level shocks (Card et al. 2018), but comparable to rent-sharing with high-skilled workers benefiting from patent rents (Kline et al. 2019).

Q11. Can Medicare’s geographic pricing policy explain the unusual geographic earnings pattern for physicians?

The elasticity of Medicare’s Geographic Adjustment Factor (GAF) to commuting zone median household income is 0.09, compared to 0.33 for a broader local price index. Using the authors’ short-run estimate that a 10% increase in Medicare prices raises earnings by 2.4%, a counterfactual simulation shows that if the GAF-to-income elasticity rose to 0.33 (aligning Medicare rates with the general cost-of-living gradient), the geographic physician earnings pattern would more closely resemble that of lawyers. The authors estimate that the gap in Medicare’s local cost adjustment explains approximately one-third of the unusual physician earnings geography, conditional on the short-run pass-through estimate.

Q12. How does the theoretical model of specialty choice and entry restrictions guide the empirical predictions?

The model features a unit mass of physicians with heterogeneous ability (Pareto-distributed) and idiosyncratic specialty preferences (exponentially distributed). Physicians choose whether to specialize in period 1; government sets reimbursement rates in period 2; physicians choose labor supply in period 3. With a fixed number of residency slots, higher specialty earnings raise the ability cutoff for entry (rationing by ability). This generates a key nonmonotonic empirical prediction: higher-ability physicians respond positively to earnings increases (choosing a specialty more frequently), while lower-ability physicians respond negatively (displaced by the shift upward in the ability cutoff). The model also implies that demand shocks are not moderated by contemporaneous entry, so incumbents capture the full rent — motivating the estimated pass-through.

Key Concepts

Medicare Price Instrument (Simulated RVU Instrument). A physician-year measure of Medicare payment exposure constructed by holding each physician’s service mix fixed at its 2012–2017 average and multiplying those fixed quantities by time-varying national RVU rates, then summing across services. This purges the instrument of behavioral responses, creating exogenous cross-physician variation in price exposure arising from the interaction of fixed service mix with national RVU policy changes.

Relative Value Unit (RVU). The unit by which Medicare defines and reimburses each physician service in the Physician Fee Schedule. RVUs are intended to reflect the time, effort, and resources required to provide each service, but are subject to periodic review by CMS’s RVU Update Committee (RUC) and influenced by political factors. Changes in RVUs translate directly into changes in Medicare reimbursement rates for affected services.

Pass-Through (Reimbursement to Earnings). The share of an additional dollar of Medicare (or insurance) spending that accrues to physicians personally as earnings, after accounting for practice costs, intermediaries, and behavioral responses. The paper estimates $62 per $100 of direct Medicare spending or $25 per $100 of total insurance spending (the latter accounting for Medicare’s spillover into private rates).

Negative Physician-Location Sorting. The empirical finding — robust to limited-mobility-bias corrections — that higher-ability (higher-earning) physicians disproportionately locate in lower-income commuting zones, while lower-earning physicians concentrate in higher-income areas. This is the opposite of the pattern for lawyers and for worker-firm matching in the broader labor literature. The paper attributes part of this pattern to Medicare’s incomplete geographic adjustment of reimbursement rates.

Ability Cutoff (am) in Residency Matching. In the paper’s theoretical model, the minimum ability level required to gain entry into a restricted-entry specialty. Because the number of residency slots is fixed, the cutoff rises when a specialty’s relative earnings increase (attracting more high-ability applicants), displacing lower-ability physicians who would otherwise have entered. This makes the earnings-specialty relationship nonmonotonic across the ability distribution.

Business Income (Pass-Through Entity Income). Income from physician-owned practices organized as sole proprietorships, S-corporations, or partnerships, reported on Schedule C or through pass-through entities rather than on Form W-2. In the tax data, business income accounts for nearly one-quarter of physician earnings at career peak and is the main source of earnings for top physicians, but is systematically underreported in survey data (ACS), leading to a roughly one-third underestimate of total earnings during peak years.

Geographic Adjustment Factor (GAF). A Medicare policy parameter that multiplies the national RVU rate to adjust physician reimbursements for local input costs (specifically physicians’ work, practice expenses, and malpractice). The paper documents that the GAF’s elasticity to local median household income is 0.09 — far below the 0.33 elasticity of the general local price index — constituting an effective subsidy to rural and lower-income markets relative to higher-income areas.

The Gender Pay Gap: Micro Sources and Macro Consequences

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

Layer 1: Overview

This paper uses linked employer-employee data from Brazil (RAIS, 2007–2014, covering 267 million worker-years, 56 million unique workers, and 607,000 employers) to document that the gender pay gap of 13.3 log points is overwhelmingly driven by women sorting into lower-paying employers — 78.7% of the gender gap in employer pay fixed effects is attributable to between-employer sorting, not within-employer discrimination. To interpret this sorting, the authors develop an equilibrium on-the-job search model (extending Burdett and Mortensen 1998) with endogenous firm pay, amenities, and hiring, and provide a constructive proof that all model parameters are point-identified from linked employer-employee data. The estimated model finds that amenities explain approximately half of total compensation for both genders (mean amenity share 48.8% for men, 52.2% for women), that compensating differentials account for roughly half of the gender pay gap (reducing it from 13.3 to 4.6 log points in total-compensation terms), and that higher-ranked employers offer women higher amenities rather than higher pay — resolving the puzzle that women disproportionately work at large employers despite a flat employer-size-pay gradient for women. Eliminating gender differences in employer preferences (gender wedges) would raise output by 12.9% but pull women into low-amenity firms, reducing their welfare, while equal-pay and equal-hiring policies close part of the pay gap but lower worker welfare through adverse incentive effects on firms’ compensation and hiring decisions.

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

In depth

Q1. What empirical patterns motivate the paper’s framework?

Three facts from Brazilian linked employer-employee data require a richer model than standard pay-only frameworks: (i) 78.7% of the 11.3 log-point gender gap in employer pay fixed effects is a between-employer sorting gap (women work at lower-paying firms); (ii) pay is increasing in employer size for men (R² = 3.3%) but essentially flat for women (R² = 0.1%); and (iii) women are disproportionately concentrated at the largest employers, which is inconsistent with models in which large firms pay more if pay is all that matters. These three facts together reveal that women value employer attributes other than pay, particularly at larger firms. Direct amenity proxies confirm this: women at larger employers are substantially less likely to be exposed to workplace hazards (coefficient −0.013, p < 0.01), less likely to be fired unjustly (coefficient −0.005, p < 0.01), much more likely to receive generous parental leave (coefficient 1.054, p < 0.01), and more likely to work part time. The AKM two-way fixed effects decomposition further shows that employer fixed effects account for 12.5% of the variance of log earnings for men and 11.1% for women, with the variance of earnings explained at 92.3% (men) and 93.1% (women).

Q2. What is the equilibrium model and how does it generate compensating differentials?

The model extends Burdett-Mortensen on-the-job search to allow firms to simultaneously choose wages, amenities, and vacancies, with firms differing in three dimensions: productivity p, gender wedges τ (an implicit tax on employing women capturing taste-based discrimination or comparative advantage), and gender-specific amenity cost shifters ca,0 — making firm pay, amenities, and hiring jointly determined in equilibrium. Workers maximize flow utility x = w + a (wage plus amenity value), and each gender climbs a separate firm utility ladder. Firms with higher composite productivity p̃ = (1−τ)p + a* − c(a*) offer higher utility to attract more workers given convex vacancy posting costs. Because amenity costs are convex and increasing in amenity value, firms optimally set amenities so that the marginal cost equals one (the unit wage), creating endogenous compensating differentials: high-amenity firms can pay lower wages while still attracting workers. The model is isomorphic to a standard wage-only Burdett-Mortensen model with wages replaced by flow utility and productivity replaced by composite productivity.

Q3. How are all model parameters identified constructively?

The authors provide a five-step constructive identification proof that recovers all parameters — including the unobservable amenity values, gender wedges, and productivity distribution — without distributional assumptions: (1) gender-specific employer pay components from AKM; (2) employer utility ranks from the employer size distribution (higher-utility firms are larger in equilibrium); (3) labor market flow hazards (λU, λE, λG, δ) from worker flow data conditional on ranks; (4) firm-level parameters (p, τ, ca,0) by inverting equilibrium profit functions; (5) economy-wide parameters (cv,0, ηv, ηa) from aggregate labor share, firm pay-profit gradient, and aggregate amenity cost share. The key insight for step (4) is that unobserved firm profits per matched worker can be inferred from equilibrium firm sizes (more profitable firms post more vacancies and hire more workers), and comparing utility levels inferred from sizes with observed wages identifies amenity values. For step (3), the involuntary job offer hazard λG is separately identified because job-to-job transitions involving a decline on the utility rank ladder — which cannot be voluntary (workers strictly prefer higher utility) — must be involuntary, allowing the hazard to be estimated by counting down-rank transitions.

Q4. What are the estimated structural results on amenities and the pay-amenity tradeoff?

Amenities are pervasive and quantitatively large: the mean amenity share of total compensation is 48.8% for men and 52.2% for women, yet compensating differentials explain the lion’s share of firm pay dispersion, with utility dispersion accounting for only 4.4% of pay dispersion for men and 3.6% for women — far less than pay dispersion alone might suggest. Higher-ranked firms for men mostly offer higher pay, but higher-ranked firms for women mostly offer higher amenities. The estimated gender productivity gap is 8.3 log points (employment-weighted mean log productivity 0.864 for men, 0.781 for women), and the employment-weighted mean gender wedge is 0.059 for women but 0.235 for men (wedge represents an implicit disutility from hiring women, so higher means women face higher wedge on average in firms where they are less likely to work). Estimated labor market parameters show women receive fewer job offers from nonemployment (λU_F = 9.1% monthly vs. 10.4% for men) and have lower job destruction rates (δ_F = 2.8% vs. 3.6% for men), contributing to slower job-ladder climbing.

Q5. How does the paper decompose the gender pay gap into micro sources?

Shutting down firm heterogeneity in amenities — replacing gender-specific amenity values with their mean — closes 45% of the gender pay gap, largely because women relocate toward formerly male-dominated, higher-paying, lower-amenity firms; shutting down differences in employer preferences (gender wedges) eliminates the pay gap entirely; differences in labor market flow rates have little effect. The total-compensation gender gap, which accounts for amenity differences, is only 4.6 log points — 40.7% of the raw pay gap of 11.3 log points — confirming that compensating differentials explain approximately half of the measured pay disadvantage. This decomposition is a novel contribution over Card et al. (2016), who rationalized the gap through exogenous gender-specific bargaining parameters without modeling amenities or their equilibrium provision.

Q6. What are the macro consequences of the gender pay gap for output and welfare?

Removing all gender differences from the economy (wedges, amenity costs, and flow rates) raises output by 6.1% and welfare by 2.1%, substantially below what pay differences alone might suggest; however, eliminating employer preferences over gender (gender wedges only) raises output by 12.9% at the cost of a welfare reduction for women, because women are pulled into high-paying, low-amenity firms. The quantitative wedge between output gains (12.9%) and welfare gains when wedges are removed reveals that women’s sorting into amenity-rich firms is partly welfare-enhancing from their perspective, even if it involves accepting lower wages. This is a key insight for policy: policies targeting pay gaps without accounting for amenity losses can be welfare-reducing.

Q7. What do equal-pay and equal-hiring policies achieve in equilibrium?

Both equal-pay mandates (forcing firms to pay men and women identical wages) and equal-hiring mandates (requiring gender-neutral hiring) close part of the gender pay gap but lower worker welfare for both genders, because the policies generate adverse incentive effects: equal-pay mandates induce firms to reduce amenities for women (since the wage-amenity tradeoff is disrupted), and equal-hiring mandates distort firms’ recruiting decisions in ways that raise vacancy costs. These general-equilibrium effects would be missed in partial-equilibrium analyses. The paper thus provides a rigorous case that equal-treatment policies — while closing observable pay gaps — fail to achieve the underlying welfare gains from eliminating gender differences, and may generate unintended welfare losses.

Q8. How does the model resolve the employer-size puzzle and what discriminatory mechanisms does it admit?

The flat employer-size-pay gradient for women (versus steeply increasing for men) is rationalized in the model because large employers offer women high amenities that substitute for pay; women optimally accept lower wages at large employers in exchange for amenity bundles that are unavailable at smaller firms. The model accommodates three discrimination channels simultaneously: taste-based discrimination (Becker 1971, via the gender wedge τ), compensating differentials reflecting gender-specific job characteristics (Rosen 1986, via amenity cost shifters), and monopsony power (Robinson 1933, via search frictions). Even nondiscriminatory firms treat women differently than men as a best response to the equilibrium distribution of discriminatory firms — an equilibrium spillover of discrimination that purely partial-equilibrium analyses miss.

Key Concepts

gender wedge (τ) : a firm-level parameter capturing the implicit disutility cost per unit of female employment, encompassing taste-based discrimination (Becker 1971) and comparative-advantage differences (Goldin 1992); estimated to explain substantial variation in women’s employment shares across firms, with female managers, routine manual tasks, and smaller size associated with lower wedges (R² = 54.6%).

compensating differentials : the wage reduction a worker accepts in exchange for favorable non-wage job attributes (amenities); in this paper, estimated to explain approximately half of the gender pay gap — the total-compensation gap is 4.6 log points vs. a pay gap of 11.3 log points — implying that women’s lower wages partly reflect their preference for amenity-rich employers.

amenity share : the fraction of total compensation (wages plus amenities) attributable to non-wage job attributes; estimated at 48.8% for men and 52.2% for women, indicating that amenities are quantitatively as important as wages in total compensation for both genders.

employer rank : a revealed-preference ordering of employers by gender-specific utility offered to workers, identified by the employer size distribution (larger firms are higher-utility in equilibrium); the paper’s key object for separating the between-employer sorting component of the pay gap from the within-employer component.

composite productivity (p̃) : the model’s reduced-form measure of a firm’s profitability per worker, combining raw productivity p, the gender wedge τ, and the optimized amenity net of amenity costs; allows the equilibrium to be analyzed as a standard Burdett-Mortensen model with composite productivity replacing raw productivity and flow utility replacing wages.

involuntary job offer hazard (λG) : the arrival rate of unsolicited job offers that workers must accept regardless of utility ranking, capturing spousal relocations and other idiosyncratic transitions; identified from the frequency of utility-rank-decreasing job transitions, since voluntary transitions can only increase utility.

The Long-Run Impacts of Public Industrial Investment on Local Development and Economic Mobility: Evidence from World War II

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

Overview

Research Question. Does government-led construction of large manufacturing plants in previously under-industrialized regions generate long-run improvements in regional economic development and in the lifetime earnings of the incumbent residents who were already living there at the outset? And, if so, through what mechanism — developmental improvements during childhood or expanded adult labor market opportunities?

Setting and Identification. The paper exploits the United States industrial mobilization for World War II, specifically the construction of 90 large, government-financed, newly-built manufacturing plants (each costing $10 million or more in contemporary dollars, approximately $150 million in 2020 dollars) in dispersed locations outside the major prewar manufacturing hubs. Strategic and security considerations — not economic optimization — drove the military to insist these plants be sited away from congested industrial centers. Because private firms were unwilling to finance construction in isolated locations with uncertain postwar value, the government built them directly as government-owned, contractor-operated (GOCO) facilities through the Defense Plant Corporation. Site selection within the set of sufficiently populated regions was governed by idiosyncratic, short-run factors — the immediate availability of suitable parcels, informal connections to procurement officers, and expedience — rather than systematic economic characteristics of the receiving counties. The paper documents no systematic association between publicly-funded wartime plant construction and prewar county-level economic or demographic characteristics conditional on population size, and finds parallel prewar trends and balanced outcome levels across treatment and comparison counties in all decades leading up to WWII. A placebo test using 1910-to-1940 intergenerational mobility in matched Census records confirms no differential prewar upward mobility in treatment counties.

The comparison group consists of 1,400 counties outside the 100 largest prewar manufacturing counties that did not receive large public plants. Treatment assignment for individuals is based on birth county, not adult county of residence, enabling the paper to track outcomes regardless of where individuals ultimately live.

Data. The analysis draws on the 1945 War Production Board data book for plant-level investment; county-level panels from Decennial and Economic Censuses spanning 1900–2000; the SSA NUMIDENT file (birth county and date); IRS Form 1040 individual income tax returns in 1969, 1974, 1979, and 1984 (covering wage earnings and adjusted gross income); the full-count 1940 Census (parent earnings, demographics); the 2000 Census long form (educational attainment); and W-2 earnings histories from the SSA Detailed Earnings Record matched to a CPS-linked subsample, with employer information linked to the Business Register.

Regional Effects. By 1970, counties receiving large public wartime plants had approximately 30 percent higher manufacturing employment, 20 percent larger populations, and 7–8 percent higher median family income than comparison counties. Manufacturing employment as a share of total employment rose and remained elevated through the 1970s before converging toward parity with the comparison group by 1990. Treated counties were permanently larger — with population stabilizing at a new, persistently higher equilibrium roughly 20 percent above comparison counties by end of century — even after the manufacturing employment share converged, consistent with path dependence and multiple equilibria. Average production worker pay in manufacturing rose by approximately 10 percent, closely tracking value-added per worker, while average retail wages rose by only one-third as much and were not statistically significant in most years. In the 40 years after the war, treated counties saw median family earnings increase by 5–10 percent, concentrated in higher average wages and employment shares in manufacturing and semi-skilled blue-collar occupations, with limited effects on non-manufacturing, white-collar occupations, or female individual income.

Individual Earnings Effects. Men born in treatment counties in the 18 years before the war (birth cohorts 1922–1940) earned approximately $1,200–$1,300 more per year (2020 dollars) in average wage earnings reported on 1040 returns in 1969, 1974, 1979, and 1984 — an increase of 2.5–3 percent and roughly a one-percentile rise in the national earnings distribution. Effects were largest for children of parents at the bottom of the 1939 earnings distribution: children of the lowest-income parents saw adult wage earnings rise by approximately $1,800–$2,000 per year (3–4 percent), with effects declining linearly by parent rank and effectively vanishing for children of the highest-earning parents. Black men experienced larger average earnings effects (4–6 percent, or $1,500–$2,500 in 2020 dollars) than White men (2–3 percent, or $1,000–$1,500), with the racial earnings gap estimated to have narrowed by about 2 percent in the treatment group. When examining Form 1040 returns (tax-unit level), effects are comparable for men and women, but W-2 individual earnings data from the SSA-CPS subsample show no positive effect on women’s own earnings — the 1040 effects for women are entirely driven by their husbands’ higher earnings.

Mechanism. The balance of evidence points to access to higher-wage jobs in adulthood as the primary channel, rather than developmental human capital improvements accumulated during childhood. War plants modestly increased male educational attainment — children from the lowest-earning families completed approximately one-quarter of a year more schooling and were 3 percentage points more likely to graduate high school — but education effects are too small to account for the full earnings increase. Critically, there is no gradient in earnings effects by birth cohort: children who were younger at the start of the war and therefore had longer childhood exposure to improved regions did not benefit more, contradicting a childhood exposure-effect mechanism as in Chetty and Hendren (2018b). Adult earnings effects are entirely accounted for by adult location: conditioning on 1979 county of residence eliminates the treatment effect. Stayers in treatment counties show large earnings differences relative to stayers in comparison counties, while movers show none. Men born in treatment counties are also directly documented to have worked in industries with higher wage premiums as adults, with coarse industry classification alone accounting for approximately one-third of the estimated log wage increase.

Policy Scope Conditions. The paper argues these effects are specific to the WWII postwar institutional context — high global demand for U.S. manufactured goods, limited international competition, labor-intensive production techniques, and strong union bargaining power — conditions that no longer hold. Reexamination of “million-dollar plant” openings in the 1980s and 1990s shows manufacturing employment expanded but average manufacturing wages did not increase, suggesting contemporary plant openings do not generate the same high-wage opportunities. The association between manufacturing employment density and upward mobility visible in 1950 has entirely vanished by the end of the twentieth century.

In depth

Q1. What exactly defines the treatment group, and why were these plants built by the government rather than private firms?

A: The treatment group consists of 90 counties outside the 100 largest prewar manufacturing regions that received at least one new, fully publicly-financed manufacturing plant costing $10 million or more (approximately $150 million in 2020 dollars) under the WWII industrial mobilization. Private firms refused to finance construction in dispersed, isolated locations with highly uncertain postwar value; the Air Force historians recorded that “industrialists’ reluctance to invest in dispersed plant facilities was at odds with the government’s hope that private capital could finance new inland construction.” The government built and owned these facilities as GOCO plants, operated by private firms under contract. The 353 plants meeting the cost threshold (including both large and smaller public plants) account for 70 percent of all spending on new plants during the war.

Q2. How do the authors establish that plant siting was quasi-random conditional on population size?

A: Identification rests on three forms of evidence. First, historical documents show procurement decisions were driven by idiosyncratic factors — availability of a suitable parcel, informal connections to procurement officers, short-run expedience — rather than systematic economic characteristics. Members of Congress had little ability to influence siting, and Rhode et al. (2018) find little evidence that federal politics drove the geographic distribution of wartime spending. Second, balance tests (estimating prewar county characteristics as outcomes in Equation 1) show no significant differences between treatment and comparison counties in earnings levels, demographics, manufacturing development, or industrial composition after conditioning on 1940 population, with a joint p-value of 0.30 (0.36 when also conditioning on geography and infrastructure). Third, a placebo test using children in the 1910 Census matched to the 1940 Census finds no differential economic outcomes or upward mobility rates in counties that would eventually receive treatment plants, conditional on basic region size.

Q3. What are the county-level effects on the structure of the labor market in the medium run?

A: By the 1960s–1970s, treated counties had higher predicted union coverage rates and a greater share of men in semi-skilled production occupations, driven primarily by movement away from farm work and supplemented by higher male labor force participation. Average wages in craftsperson and operator occupations rose by 8 percent in treated counties — more than double the increase in wages for high-skill professional and managerial occupations. Treated counties had 8 percent higher median male individual incomes by 1979. Effects on female median individual income were minimal, and there were no effects on female labor force participation rates.

Q4. What is the estimated magnitude of the individual earnings effects, and how do they vary by parent income?

A: Men born in treatment counties averaged $1,200–$1,300 more per year in real wage earnings (2020 dollars) on 1040 tax returns across the four observation years 1969, 1974, 1979, and 1984, a 2.5–3 percent increase equivalent to roughly one percentile in the national earnings distribution. Heterogeneity by parent rank is pronounced and monotone: children of parents at the very bottom of the 1939 earnings distribution gained approximately $2,000 per year (about 4 percent), while children of the highest-earning parents experienced no significant effect. When county weighting is equalized to eliminate the differential representation of rural (lower-income) counties, effects are roughly constant across the bottom six deciles of the parent earnings distribution and then drop steeply at the top, showing that the earnings gradient was not simply an artifact of plant openings in poorer, smaller counties.

Q5. How did effects differ by race?

A: Wartime plant construction increased annual adult earnings of Black men by 4–6 percent ($1,500–$2,500 in 2020 dollars) and of White men by 2–3 percent ($1,000–$1,500 in 2020 dollars). The racial earnings gap in the treatment group is estimated to have narrowed by about 2 percent. However, the pattern of heterogeneity by parent income differs by race: for White men, effects are largest for children of below-median parents and effectively zero for children of above-median parents. For Black men, the largest effects — 7–10 percent ($4,000–$5,000 in 2020 dollars) — accrue to children of parents with earnings above the pooled-race national median, while effects for lower-income Black families range from 3–6.5 percent, suggesting that Black workers from higher-income backgrounds particularly benefited from wartime anti-discrimination policies and the opening of previously restricted manufacturing occupations.

Q6. Why do the 1040 returns show comparable effects for men and women, while W-2 data show no effect on women’s individual earnings?

A: Form 1040 returns are filed at the tax-unit level — for married couples, they report the combined wages of both spouses. Because more than 80 percent of women in the sample are married, an increase in a husband’s earnings raises the joint 1040 figure for both spouses. The SSA-CPS subsample with individual W-2 records shows that the entire effect on men’s Form 1040 wages directly reflects increases in their own W-2 earnings, while women’s own W-2 earnings show no positive treatment effect. This finding is consistent with county-level evidence of no impact on female individual income or female labor force participation, and with Rose (2018) finding that women were almost universally excluded from manufacturing jobs after the war’s conclusion despite high wartime female manufacturing employment.

Q7. What evidence tests the developmental-effects mechanism?

A: Three tests argue against childhood developmental effects as the primary driver. First, educational attainment effects — while statistically significant for children of the lowest-income parents (approximately one-quarter of a year more schooling, 3 percentage points more likely to graduate high school) — are too small to account for the earnings increase: a Mincer-equation calculation shows that the education effects can explain less than one-half of the estimated effect on 1979 wages. Second, there is no gradient in earnings effects by birth cohort — children younger at the war’s start, who had longer post-treatment childhood exposure, did not benefit more, in direct contrast to the Chetty-Hendren childhood-exposure framework. Third, postwar in-migrants into treatment counties were not drawn from better-educated or higher-income families and did not themselves have more education than in-migrants into comparison regions, ruling out peer effects from selective in-migration.

Q8. What evidence directly implicates adult labor market access as the operative mechanism?

A: Four pieces of evidence point to contemporaneous adult labor market access. First, individuals born in treatment counties lived as adults in counties with 3–4 percent higher median male earnings and higher wages in semi-skilled blue-collar occupations but not in highly-skilled professional occupations — a pattern quantitatively consistent with the individual earnings effects. Second, the entire earnings effect is concentrated among those who remain in their birth counties: stayers in treatment counties show earnings differences of similar magnitude to county-level manufacturing wage effects, while movers show no difference compared to movers from comparison counties. Third, conditioning on 1979 county of residence eliminates the earnings effect entirely (1979 location fixed effects specification). Fourth, using W-2 data matched to the Business Register in the SSA-CPS sample, men born in treatment counties are directly shown to work in industries with higher wage premiums, with coarse industry classification alone accounting for approximately one-third of the log wage increase.

Q9. Is the persistence of regional effects driven by continued Cold War military spending at the plants?

A: No. The paper separates ordnance and ammunition plants — which predominantly became GOCO facilities or Air Force Bases after WWII and received disproportionately more Vietnam War-era defense spending — from general manufacturing plants, which overwhelmingly transitioned to privatized civilian production. Both types of plants show similarly persistent effects on manufacturing employment and comparable impacts on the long-run earnings of local children. Moreover, general manufacturing plants — which did not generate increased postwar military spending — had large permanent effects on overall population growth, while ordnance plants had smaller population effects. The persistence therefore does not appear to reflect continued federal expenditure.

Q10. What mechanism explains the permanent population effect even after manufacturing employment shares converge?

A: The authors interpret the permanent population differential — treated counties remain roughly 20 percent larger than comparison counties even at the end of the 20th century, after manufacturing employment shares converge — as evidence of path dependence and multiple equilibria. Once a region reaches a new, larger equilibrium, self-sustaining forces (expanded non-tradable employment, public infrastructure investment) maintain it. Treatment counties are more likely to have been connected to the interstate highway system in subsequent decades and show positive effects on local government capital outlays for utilities. The medium-term persistence is attributed partly to the sunk costs of site establishment (surveying, local approvals, infrastructure connections), which make reinvestment at existing sites more attractive than greenfield construction elsewhere.

Q11. Do smaller plant openings generate comparable effects?

A: No. Counties receiving smaller publicly-financed plants costing between $1 and $10 million show no detectable effects on manufacturing employment, population, median family income, or individual adult earnings comparable to those from the large plants. The authors cannot rule out the presence of small effects, but the null results for smaller plants — combined with evidence that the largest effects are in counties with the highest investment intensity per 1940 resident — are consistent with threshold effects (“big push”) in regional development, though the wide confidence intervals do not allow the authors to conclusively distinguish threshold effects from a linear-in-investment model.

Q12. What do modern “million-dollar plant” openings reveal about the contemporary relevance of these findings?

A: Reexamining plant openings from Greenstone et al. (2010) using an event-study design, the authors find that 1980s–1990s million-dollar plant openings expanded manufacturing employment (consistent with Greenstone et al.) but had no impact on average manufacturing wages — in sharp contrast to the WWII findings. Slattery and Zidar (2020) similarly find no impacts on county-level incomes for plant openings since 2000. The correlation between manufacturing employment density and upward mobility rates visible in 1950 had entirely vanished by the end of the 20th century. The authors attribute the divergent results to the changed institutional environment: contemporary production is highly automated, relies on interchangeable labor from staffing agencies, faces intense international competition, and is conducted under much weaker collective bargaining institutions.

Q13. What is the paper’s assessment of aggregate welfare implications?

A: The paper is explicit that its local estimates do not allow clean conclusions about aggregate effects. Publicly-financed plant construction in peripheral locations may have crowded out private investment that would otherwise have occurred in major manufacturing hubs. If so, the documented regional gains represent geographic reallocation of manufacturing activity rather than a net increase in the aggregate plant stock. Aggregate gains from reallocation would require that the benefits in the selected dispersed locations exceeded what would have occurred in the counterfactual locations — a plausible conjecture given the paper’s evidence that effects are larger in counties with lower prewar manufacturing employment shares and lower initial market access, but one the authors cannot demonstrate decisively.

Key Concepts

Government-Owned, Contractor-Operated (GOCO) Plants: Manufacturing facilities built and owned by a U.S. government agency (typically the Defense Plant Corporation) during WWII but built and operated by private firms under cost-plus contracts. GOCO status meant the government bore full construction risk and that post-war disposition (sale to private buyers at a fraction of construction cost, or continued GOCO operation for ordnance production) was determined by public agencies, not by the constructing firm’s investment calculus.

Place-Based Predistribution: The paper’s term for the mechanism by which wartime plant construction raised the incomes of existing residents — not through ex-post redistribution of income via taxes and transfers, but by expanding the set of high-wage employment opportunities available to incumbent workers in the region, thereby changing the pre-tax, pre-transfer wage structure facing those workers.

Adult Labor Market Access (vs. Childhood Developmental Exposure): A distinction the paper draws in explaining why children born in treated counties had higher adult earnings. The “developmental exposure” mechanism (as in Chetty and Hendren 2018b) implies benefits scale with the amount of time spent in an improved childhood environment. The “adult labor market access” mechanism means children benefit irrespective of years of childhood exposure because they can access improved local labor market conditions when they reach working age as adults — what the paper operationalizes through the finding that earnings effects are entirely accounted for by 1979 county of residence and are concentrated among individuals who remain in their birth counties.

Upward Mobility (Absolute and Relative): Following Chetty et al. (2014), the paper uses both concepts: absolute upward mobility means children from low-income backgrounds have higher lifetime earnings than comparable children in counterfactual regions; relative upward mobility means their outcomes converge toward those of children from affluent backgrounds. The paper documents both: large earnings effects for the lowest parent-income deciles, declining linearly to zero for the top deciles.

Conditional Independence (Plant Siting as Quasi-Random): The paper’s identification assumption — that among counties with observably similar population sizes and basic geographic/infrastructure characteristics, the specific choice of plant siting locations was driven by idiosyncratic, short-run factors uncorrelated with potential postwar outcomes. This is a level-balance assumption (not merely a parallel-trends assumption), required because individual outcomes are only observed in the post-period.

Industry Wage Premium: The paper uses Krueger and Summers (1988) estimates of inter-industry wage differentials (the portion of a sector’s average wage unexplained by worker characteristics) to classify adult employers of treated individuals. Finding that men born in treatment counties work at employers in higher-premium industries — with industry category alone explaining approximately one-third of the log wage increase — provides direct evidence of the adult labor market access mechanism operating through industry sorting.

Path Dependence / Multiple Equilibria in Regional Development: The paper documents that treated counties remain permanently larger in population than comparison counties even after manufacturing employment shares converge and the original plants begin to close. This self-sustaining population differential, inconsistent with a unique spatial equilibrium, is interpreted as evidence that the temporary wartime shock shifted treated regions into a permanently higher equilibrium, sustained by subsequent infrastructure investment and non-tradable sector expansion proportional to the larger population base.

Voluntary Minimum Wages: The Local Labor Market Effects of National Retailer Policies

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

Layer 1 — Overview

Research Question

This paper studies the labor market effects of voluntary minimum wages (VMWs) — company-wide, publicly announced wage floors set by large private employers — in the U.S. low-wage retail and service sector from 2014 to 2023. The central questions are: (1) How do VMWs affect wages and employment at the adopting large retailers? (2) Do VMWs generate wage spillovers to other employers in shared local labor markets?

Data and Setting

The authors use anonymized payroll data obtained from a large U.S. credit bureau, covering the wage distributions and employment of over 4,000 firms and approximately 18 million hourly workers (roughly 22–24% of the U.S. hourly workforce) from January 2013 to August 2023. The database is skewed toward retail and service sectors: over a third of covered workers are in retail, and over half in retail and services combined. Critically, the data also include worker flow information — records of individual workers moving between firms — enabling the authors to define shared labor markets via actual employment transitions rather than broad geographic or industry proxies.

The sample of VMW events consists of 20 voluntary minimum wage policies across 5 large retailers (each with over 150,000 employees nationally), restricted to events with no other major wage policy within six months before or after the focal event. Voluntary minimum wage announcements were identified from an inventory maintained by the National Employment Law Project and independently verified through media sources, then matched to anonymized companies using employer size, industry, and observed shifts in the wage distribution.

Identification Strategy

The authors adapt the gap design from the national minimum wage literature. For each company-by-commuting-zone (CZ) cell, the “gap” measures the percent increase in average hourly wages that would be required to bring all workers in the area up to the company’s new voluntary minimum. The gap is averaged over months −6 to −3 before the event (months −3 to −1 serve as a built-in placebo-in-time check). This variation in bite across CZs — arising because the same nominal VMW level implies different wage increases depending on local wage distributions — is combined with a stacked event study across 20 VMW events. Spillover effects are estimated by regressing log average wages at non-policy establishments on the large retailer’s CZ-level gap measure, progressively narrowing the definition of “labor market” from: (i) all non-policy establishments in the same CZ, to (ii) establishments in industries connected to the large retailer by worker flows (15 three-digit NAICS industries), to (iii) specific establishments with documented pre-event worker flows to or from the large retailer (“connected establishments”).

Main Findings

Own effects: For $15 VMW events, moving from a CZ gap of 0 to a gap of 1 is associated with an approximately 88 log point increase in average hourly wages in the six months after adoption. Given that the average establishment-level gap for $15 VMWs is 0.11, the implied average wage increase is approximately 10.45% (the authors’ estimate is 9–10%, consistent with small wage increases even in zero-gap comparison areas). Employment of workers earning under $30 per hour rose by 4.62% after $15 VMW events, 2.01% after major events (affecting ≥30% of workforce), and 1.25% across all 20 events. These employment increases are entirely attributable to reduced separations rather than new hiring: separation rates fell by 0.42, 0.57, and 1.09 percentage points after all, major, and $15 VMW events respectively — equivalent to reductions of 6.57%, 8.73%, and 15.33% relative to pre-period means. Separations specifically to other database companies fell by 0.07–0.19 percentage points (5.63–13.48% relative to base rates). If anything, new hiring fell modestly after VMW adoption. Total monthly base pay and gross compensation both rose after VMWs, indicating increased total take-home pay without compensatory reductions in hours or bonuses. The total employment elasticity with respect to wages ranges from approximately 0.35 to 0.45, while the quit elasticity is 2.20–2.38 (consistent with dynamic monopsony models in which the labor supply elasticity is twice the quit elasticity).

Spillover effects: Across all three definitions of the labor market, the paper estimates precise, economically negligible cross-employer wage spillovers in the six months following VMW events. Cross-employer wage elasticities are statistically indistinguishable from zero across all specifications. Among the most narrowly defined sample — establishments with documented pre-event worker flows to or from the large retailer — the upper bound of the confidence interval rules out spillovers greater than 0.2% of wages. No wage spillovers are detected for new hires at non-policy establishments either. These null results are confirmed over a 12-month post-event horizon for the subsample of events with no other major policy nearby.

Mechanism: The reason for negligible spillovers is that VMWs reduced labor market churn rather than expanding the large retailer’s total employment. Hiring away from large retailers by connected non-policy firms falls after VMW adoption — consistent with fewer separations to recruit from — but overall hiring by non-policy firms does not decline, as these firms substitute toward other hiring sources. This substitutability across new hire sources in a thick market is the proximate explanation for the absence of wage pressure on competitor firms.

Scope Conditions

Results pertain to large national retailers (>150,000 employees) operating in U.S. commuting zones during 2014–2023. The database covers only employers large enough to participate in credit bureau income verification; smaller employers (representing over 75% of U.S. hourly workers by the BLS comparison) are not observed, and the authors caution that spillover effects on smaller firms cannot be assessed. The authors also explicitly note that their null local spillover results do not rule out national-level strategic wage-setting dynamics — the rapid sequential adoption of VMWs across major retailers may reflect national-level competition rather than local market competition.

In depth

Q1. What exactly are “voluntary minimum wages” and how do they differ from statutory minimum wages?

Voluntary minimum wages (VMWs) are company-wide, publicly announced wage floors set unilaterally by private employers, typically well above the applicable statutory (federal, state, or local) minimum. Unlike statutory minimums, which bind all employers in a jurisdiction, VMWs apply only to the announcing company across all of its geographic operations in the U.S. The paper studies VMWs adopted by retailers with over 150,000 workers, which include wage floors at levels such as $9, $10, $12, and $15 per hour. $15 VMWs were adopted at a time when few states or localities had yet reached that threshold, meaning the policy bit into the company wage distribution far more deeply than prevailing statutory floors.

Q2. How were VMW events identified and matched to anonymized firms in the payroll database?

VMW events were identified from a database maintained by the National Employment Law Project and verified through an independent review of business news articles. These publicly reported announcements were then matched to the anonymized companies in the credit bureau payroll database using employer size, industry, and the timing of observed shifts in the firms’ wage distributions. An additional three events were identified directly from data: months where the share of workers earning below a given wage level dropped by at least 15 percentage points (for non-$15 events) or 10 percentage points (for $15 events) while the share at exactly that wage bin jumped by at least 10–20 percentage points. The final sample of 20 events was restricted to those with no other major wage policy in the six months before or after.

Q3. How does the gap design work and why does it improve on the fraction-affected approach?

The gap for a given company, commuting zone, and time period is defined as the total wage increase needed to bring all sub-$30 workers up to the company minimum, divided by total wage costs — formally a labor-share-weighted average shortfall from the new minimum across wage bins. The gap leverages more cross-sectional variation in treatment intensity than the simple fraction of workers below the minimum: for a $15 VMW, an area where all workers earn $10 has a gap of 0.50 while an area where all earn $12 has a gap of 0.25. The gap is averaged over months −6 to −3 before the event. The period months −3 to −1 then serve as a placebo window: genuine VMW effects should appear only after the policy’s adoption month, not during the period immediately after the gap is measured. If instead the regression picks up mean reversion in noisy wage data, spurious effects would appear in months −3 to −1 rather than at event time 0.

Q4. What is the magnitude of the wage effect on the large retailers themselves?

For $15 VMW events, the stacked event study estimates that moving from a gap of 0 to a gap of 1 is associated with an approximately 88 log point increase in average hourly wages beginning exactly in the month of policy adoption. Given the average establishment-level gap of 0.11 for $15 VMWs, this implies the average establishment raised wages by approximately 9–10% (the authors compute 10.45% from the average gap, consistent with a slight dampening because zero-gap CZs experienced marginally higher wages too). Wage increases are confirmed persistent at 12 months in robustness checks. For all 20 VMW events pooled, effects are somewhat smaller commensurate with the lower average bite.

Q5. How did VMWs affect total employment and its components at the large retailers?

After $15 VMW events, log total employment of sub-$30 workers rose by 4.62%; after major VMW events (≥30% bite), 2.01%; after all 20 events, 1.25%. The increases are entirely driven by retention gains. Separation rates fell by 1.09 percentage points after $15 VMWs, 0.57 p.p. after major events, and 0.42 p.p. after all events — translating to reductions of 15.33%, 8.73%, and 6.57% relative to pre-period means. Separations to other database companies specifically fell by 0.07–0.19 percentage points (5.63–13.48% relative to the base mean). New hiring — measured as year-on-year log change in hires to control for seasonality — fell after VMW adoption, consistent with a reduced need to replace departing workers.

Q6. What do the labor supply elasticities implied by the VMW results look like?

The total employment elasticity with respect to wages ranges from approximately 0.35 to 0.45 across the three event groupings. Under standard dynamic monopsony models, the labor supply elasticity facing the firm equals twice the quit elasticity in steady state (Manning, 2003). The quit elasticity — derived by dividing the proportional reduction in separations by the log wage increase — ranges from 2.20 to 2.38, consistent with the earlier monopsony-based case study of Ford’s $5 workday (Raff and Summers, 1987) and implying substantial firm-level wage-setting power.

Q7. Did VMWs increase total take-home pay or were wage gains offset by reductions in hours or bonuses?

The paper examines log average monthly base pay and log average gross compensation (which includes bonuses and overtime) as additional outcomes. Both measures rose after $15 VMW events, indicating that the wage floor increase translated into genuine improvements in total take-home pay without compensatory reductions in hours or other non-wage compensation. The monthly gross pay series is an average over calendar year-to-date months, so increases appear gradually rather than as a sharp jump at the adoption month; nevertheless the upward trend is evident and consistent.

Q8. What are the estimated spillover effects on wages at non-policy employers?

Across all three definitions of the labor market — all non-policy establishments in the same CZ, establishments in the 15 connected industries in the same CZ, and establishments with documented pre-event worker flows — the estimated cross-employer wage effects are precise zeros. The stacked event study in the post-period shows coefficients centered on zero with small confidence intervals. The difference-in-differences cross-employer wage elasticity (instrumenting the large retailer’s wage change with the gap) is also indistinguishable from zero. Among the most exposed connected establishments, the point estimate is slightly positive but economically negligible; the upper confidence interval bound rules out spillovers greater than 0.2%. Results are confirmed over a 12-month horizon for the clean-event subsample.

Q9. Could the null spillover result reflect mean reversion bias rather than a true zero?

The authors address this concern explicitly. For the policy-company gap design, they build in a placebo-in-time check by measuring the gap over months −6 to −3 and checking that no wage effects appear in months −3 to −1. For the non-policy spillover analysis, they also examine an alternative treatment variable — the gap between non-policy establishments’ wages and the large retailer’s new VMW — and find evidence of mean reversion: wages begin rising in the pre-period in the direction of this gap measure. They correct for this by detrending post-period estimates using a linear extrapolation of the pre-period trend. After detrending, spillover effects remain indistinguishable from zero.

Q10. Why are spillover effects so limited if the large retailer is drawing fewer workers away from competitors?

The paper’s mechanism analysis shows that while the probability of a non-policy firm hiring a worker from the large retailer falls after a VMW event (consistent with fewer separations to recruit from the large retailer), the overall rate of hiring by non-policy firms does not decline. Non-policy firms substitute toward other hiring sources — primarily other non-policy companies — rather than hiring fewer workers overall. This substitutability across recruiting sources in a thick labor market mutes the competitive pressure on competitor wages: since non-policy firms can replace the reduced flow from VMW companies with workers from other sources without changing total employment, they face no pressure to raise wages.

The authors test whether larger local market presence amplifies spillovers by splitting the sample at the median employment share of the large retailer in the CZ. They find no evidence of positive wage spillovers even in CZs where the large retailer’s employment share is above the median, confirming that neither local market size nor market concentration is a mechanism for spillover transmission in this setting.

Q12. How do these VMW spillover results compare to prior evidence on employer wage-setting spillovers?

The main prior U.S. evidence (Staiger et al., 2010) studied a federally mandated wage increase at Veterans Affairs hospitals and found a cross-establishment wage elasticity of approximately 0.19 for registered nurses at neighboring hospitals. The authors note two key differences: first, the VA policy increased both wages and employment at treated facilities, whereas VMWs primarily reduced separations without increasing hiring, so the supply of workers to competitor firms was not squeezed. Second, the market for low-wage retail and service workers is likely thicker (more potential hires available) than the market for registered nurses, allowing competitors to substitute hiring sources without bidding up wages.

Q13. What do the null local spillover results imply about national-level wage dynamics?

The authors explicitly caution against reading the null local spillover result as implying VMWs have no broader effect on the low-wage labor market. The rapid and successive adoption of VMWs across major retailers during 2021–2022 could reflect national-level strategic wage-setting competition — firms mimicking each other’s announcements in an arms-race dynamic during tight labor markets — rather than local competitive transmission. The paper does not test for national-level strategic interactions and calls for further research on this dimension.

Key Concepts

Voluntary Minimum Wage (VMW): A company-wide, publicly announced wage floor set unilaterally by a private employer, applying across all of the firm’s geographic operations in the U.S., typically well above applicable statutory minimums. Distinct from legally mandated minimum wages in that they bind only the announcing firm and arise from the firm’s own strategic or reputational motivations.

Gap Measure: Borrowed from the national minimum wage literature (Card, 1992; Draca et al., 2011), this is the percent increase in a firm’s average hourly wage that would be required to bring all workers in a given commuting zone up to the company’s new voluntary minimum. Formally the labor-share-weighted average shortfall from the VMW across sub-$30 wage bins. A gap of 0 means no workers fall below the new minimum; a gap of 1 means all workers would need to be raised to the minimum, doubling the average wage. Used as a continuous treatment variable capturing the local bite of the policy.

Stacked Event Study: An empirical design in which a separate 12-month panel (6 months pre- and post-event) is constructed for each of the 20 VMW events, these datasets are stacked, and the effect of the continuous gap treatment is estimated jointly across all events, with event-specific indicators interacting all regressors to allow each event to have its own intercept.

Placebo-in-Time Check: A robustness test built into the gap design by computing the gap over months −6 to −3 and verifying that wage effects do not appear in months −3 to −1 (the period between gap measurement and VMW adoption). Genuine policy effects should materialize at the adoption month; spurious effects driven by mean reversion in noisy wage data would appear in months −3 to −1 because the gap would mechanically predict wage reversion toward the mean in the period immediately following its measurement.

Connected Establishments / Poaching and Feeder Establishments: Specific firm-by-CZ cells identified as sharing a labor market with the large retailer via actual worker flows. “Poaching establishments” hired at least one worker from the large retailer in the 12 months before the VMW event. “Feeder establishments” had at least one worker subsequently hired by the large retailer in the same pre-period. These are the most narrowly defined and most economically relevant labor market competitors for testing spillover effects.

Quit Elasticity / Labor Supply Elasticity (Firm-Level): The quit elasticity is the percent change in the separation rate divided by the percent change in wages induced by the VMW. Under standard dynamic monopsony models (Manning, 2003), in steady state the recruit elasticity equals the quit elasticity, and the firm-level labor supply elasticity equals twice the quit elasticity. The authors estimate quit elasticities of 2.20–2.38, implying labor supply elasticities of 4.40–4.76 to the firm — consistent with meaningful but not extreme monopsony power.

Cross-Employer Wage Elasticity: The percent change in wages at a non-policy employer’s establishment associated with a 1% change in wages at the large retailer in the same commuting zone, instrumented using the large retailer’s gap interacted with the post-event indicator. Estimated to be a precise zero across all market definitions and event groupings in this paper.

What's My Employee Worth? The Effects of Salary Benchmarking

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

This paper studies how salary benchmarking tools — products that reveal aggregate market pay statistics for specific job titles — affect employee compensation. The research question is whether firms’ access to such tools causally changes how they set salaries, and what this implies about information frictions in labor markets and the policy debate over benchmarking regulation.

The authors collaborated with the largest U.S. payroll processing company (serving 650,000 firms and 20 million workers), exploiting the staggered roll-out of a proprietary Compensation Benchmark Tool. The tool aggregates payroll data into salary benchmarks by standardized job title, with the median base salary as its most prominent statistic. The study draws on three linked administrative datasets: payroll records (January 2017 to July 2021), tool usage logs (September 2019 to August 2021), and historical benchmark snapshots. The main analytical sample covers new hires at 586 treatment firms that gained tool access and 1,419 matched control firms that did not, within a 10-quarter window around each firm’s onboarding date.

The identification strategy is difference-in-differences, exploiting three sources of variation: which firms gain access; the staggered timing of access (driven by the arbitrary order in which sales representatives introduced the tool); and within treatment firms, whether a specific position was actually searched in the tool. New hires are classified into Searched positions (5,266 hires at treatment firms for positions eventually looked up), Non-Searched positions (39,686 hires at treatment firms for positions not looked up), and Non-Searchable positions (156,865 hires at control firms). Event-study analyses confirm flat pre-trends across all groups, supporting causal interpretation.

The primary finding is that benchmark access reduces salary dispersion around the median market benchmark by 25%. Before onboarding, the average absolute deviation of offered salaries from the median benchmark in Searched positions was 19.8 percentage points (pp). After onboarding, this fell to 14.9 pp — a drop of 5.0 pp using Non-Searched positions as control (p-value < 0.001) and 6.2 pp using Non-Searchable positions as control (p-value < 0.001). Compression runs in both directions: firms previously paying above the benchmark reduce salaries toward the median, and firms previously paying below raise salaries toward the median. The probability of setting a salary within 2.5% of the median benchmark nearly doubled, from 11.6% to 22.1% after onboarding.

Effects are heterogeneous by skill level. For low-skill positions (approximately 42% of the sample, e.g., bank teller, receptionist), dispersion falls from 14.5 pp to 8.7 pp — a 40% reduction. For high-skill positions (e.g., software developer), dispersion falls from 24.0 pp to 20.5 pp — a 14.6% reduction. For low-skill positions, compression from below dominates, producing a net average salary increase of +5.0% to +6.7% (p-values 0.014 and 0.001 depending on control group). For high-skill positions, the average salary effect is small and statistically insignificant overall. Twelve-month retention rates for low-skill workers increase by 6.6 to 6.8 pp after benchmarking, and the implied retention elasticity is consistent with prior literature estimates.

The authors propose a theoretical model to rationalize these findings. Firms are assumed uncertain about the wage distribution (aggregate uncertainty), with private information about their own value of filling a position and affiliated valuations across firms. In equilibrium, firms with higher values make higher offers — generating wage dispersion among identical workers without monopsony power, efficiency wages, or amenity differences. When a firm gains benchmark access, it adjusts its offer toward the threshold wage needed to hire, compressing offers from both sides. In the full-information equilibrium where benchmarks are common knowledge, the mean salary is weakly higher than without benchmarks, because the marginal firm had previously underestimated labor market tightness and offered too little, capturing extraordinary profits. Benchmarking eliminates these informational rents, intensifying competition and raising average pay.

The scope of the empirical findings is restricted to new hires at firms in the top quartile of U.S. firm size by employment, across all industries and U.S. states, over 2017–2020. The estimated effect is the incremental causal impact of one additional high-quality benchmarking source, since most firms already had access to some pay information through other channels.

Q: What is the main causal finding of the paper? A: Access to the salary benchmarking tool reduces the absolute deviation of new-hire salaries from the median market benchmark by approximately 25%. Specifically, average dispersion in Searched positions falls from 19.8 pp before onboarding to 14.9 pp after, a drop of 5.0 pp (using Non-Searched controls, p-value < 0.001) or 6.2 pp (using Non-Searchable controls, p-value < 0.001). The two estimates are statistically indistinguishable from each other, and both are robust to a wide range of specification checks.

Q: How does compression operate — does it raise or lower salaries? A: Compression operates in both directions. Firms that would otherwise have paid above the median benchmark reduce salaries toward the median (“compression from above”), and firms that would otherwise have paid below the median benchmark raise salaries toward the median (“compression from below”). The probability of offering a salary within 2.5% of the median benchmark nearly doubled, from 11.6% before onboarding to 22.1% after.

Q: What is the identification strategy, and why is the treatment considered as good as random? A: The authors use a difference-in-differences design with three sources of variation: which firms gain tool access, the staggered timing of access, and whether specific positions were actually searched within a treatment firm. The payroll company introduced the tool through sales representatives contacting clients in an arbitrary order, not in response to firm characteristics or outcomes. This is corroborated by empirical tests: event-study pre-trends for Searched versus Non-Searched (and Non-Searchable) positions are flat and statistically indistinguishable from zero (pre-treatment coefficients of -0.346 and -0.310, p-values 0.749 and 0.604, respectively).

Q: How large are the effects for low-skill versus high-skill positions? A: For low-skill positions (approximately 42% of the sample, e.g., bank teller, receptionist), dispersion drops from 14.5 pp to 8.7 pp — a 40% decline (p-value < 0.001). For high-skill positions (e.g., software developer), dispersion drops from 24.0 pp to 20.5 pp — a 14.6% decline (p-value = 0.021). The larger effect for low-skill positions is consistent with anecdotal accounts from compensation managers, who report treating low-skill candidates as interchangeable and therefore wanting to offer exactly the market rate.

Q: Does benchmarking raise or lower average salaries? A: On average across all skill levels, the effect on mean salary is small and statistically insignificant: -0.2% (p-value = 0.756) using Non-Searched controls and +1.7% (p-value = 0.308) using Non-Searchable controls. For low-skill positions specifically, average salaries increase by +5.0% (p-value = 0.014) using Non-Searched controls and +6.7% (p-value = 0.001) using Non-Searchable controls. This net increase for low-skill workers reflects compression from below dominating compression from above in that subset.

Q: What are the effects on employee retention? A: For low-skill workers, benchmarking increases the probability of remaining employed at the hiring firm 12 months after the hire date by +6.6 pp (p-value = 0.101) using Non-Searched controls and +6.8 pp (p-value = 0.029) using Non-Searchable controls. The implied retention elasticity from the ratio of salary and retention effects is consistent with average estimates in the prior literature (Sokolova and Sorensen, 2021). No retention effects are reported for high-skill positions.

Q: What is the theoretical mechanism through which aggregate uncertainty generates wage dispersion? A: The model assumes a unit mass of firms simultaneously making wage offers to a mass Q < 1 of workers, with only the top Q offers accepted. Firms have private information about their value of filling the position, and values are affiliated (correlated in the sense of Milgrom and Weber, 1982). Because each firm is uncertain about what other firms will offer, higher-value firms rationally form higher beliefs about the prevailing wage distribution and make higher offers. This generates equilibrium wage dispersion among identical workers without monopsony power, efficiency wages, or amenity differences.

Q: What does the model predict about the equilibrium effects of benchmarking when all firms have access? A: When the benchmark is common knowledge, all firms make offers with full information about the wage distribution. The firms with the highest values win workers at a uniform wage that makes the marginal firm indifferent between hiring and not hiring. The model proves that the mean salary is higher in expectation under the benchmark equilibrium than in the no-benchmark equilibrium. The intuition is that without benchmarks, the marginal firm underestimates labor market tightness, offers less than the full-information competitive wage, and thereby captures extraordinary profits; benchmarking eliminates those rents and intensifies competition.

Q: What are the policy implications of the findings regarding antitrust concerns? A: In 2023, the DOJ and FTC rescinded a long-standing antitrust “safety zone” for salary benchmarks due to concerns that they could facilitate wage collusion. A 2021 executive order had mandated that agencies consider procompetitive effects as well. The authors’ model addresses the collusion concern directly: in equilibrium, benchmarking raises (not lowers) average salaries. The empirical evidence is consistent with this — low-skill workers see average salary increases of 5-7% after benchmarking — suggesting a procompetitive justification for the tools.

Q: How robust are the main results? A: The main estimates are robust across a wide range of specification checks, including alternative winsorization levels, log-difference and binary (>10% deviation) dependent variables, heteroskedasticity-robust standard errors, exclusion of controls, inclusion of firm fixed effects, exclusion of tipping positions, restriction to Searched positions only, dropping SOC reweighting, and age restrictions. Two additional pieces of evidence corroborate the quasi-experimental findings: a survey experiment with SHRM HR managers shows that hypothetical benchmarks compress stated salary offers from both above and below; and quasi-random benchmark shocks (when large firms abruptly raise a position’s base salary by 10% or more) cause firms with tool access to converge to the new benchmark faster than firms without access.

Q: What does the survey of HR managers reveal about how firms use benchmarks? A: In a survey of 2,696 HR professionals conducted through SHRM’s research panel, 87.6% of those involved in salary-setting report using salary benchmarks. The vast majority (97.4%) use benchmarks to set pay for new hires. The most popular sources are industry surveys (68.0%) and free online data (58.1%), with payroll data services used by 23.2%. The median salary is ranked the most important benchmark statistic by 56.73% of respondents. Most respondents apply filters by state (84.15%) and industry (87.33%) when using the tool.

Q: What are the main sources of potential attenuation or amplification bias in the estimated effects? A: Attenuation bias may arise because (1) the benchmark tool studied is among the most advanced available, so firms already had some wage information from other sources, meaning the estimates capture only the incremental effect of one additional high-quality source; and (2) not all positions at treatment firms were searched, so the sample is restricted to positions where firms actually engaged with the benchmark. Potential upward bias could arise if firms adopting the tool were also undergoing broader HR system changes, but the flat event-study pre-trends argue against this explanation.

Salary Benchmarking: The practice of using aggregated market pay data — provided by third parties such as payroll processors, consulting firms, or online platforms — to identify typical salaries for specific job titles and set internal pay accordingly. In the paper’s context, this refers specifically to an online tool that allows employers to look up the median and distributional statistics of base salaries for standardized position titles, filtered by industry and state.

Aggregate Uncertainty: The paper’s label for a distinct source of information friction in which firms are uncertain about the distribution of wages offered by other firms in the market — as opposed to uncertainty about individual worker characteristics. This uncertainty is assumed to be the primitive that generates equilibrium wage dispersion in the model, and its resolution through benchmarking is the mechanism driving the empirical results.

Salary Dispersion (around the benchmark): Measured empirically as the average absolute percentage difference between a new hire’s starting base salary and the median market benchmark for that position, expressed in percentage points. This is the paper’s primary outcome variable. Dispersion reflects firms’ deviation from the market rate in either direction.

Compression from Above / Compression from Below: Compression from above refers to the reduction in salaries at firms that would otherwise have paid more than the median benchmark after gaining benchmark access. Compression from below refers to the increase in salaries at firms that would otherwise have paid less than the median benchmark. Both directions of adjustment are documented empirically and are predicted by the model.

Searched / Non-Searched / Non-Searchable Positions: The paper’s classification of new hires into three groups for identification purposes. Searched positions are those at treatment firms for which the firm actually looked up the benchmark. Non-Searched positions are at treatment firms but were not looked up, serving as a within-firm control. Non-Searchable positions are at control firms with no tool access, serving as a cross-firm control.

Affiliation (across firm values): A technical condition borrowed from auction theory (Milgrom and Weber, 1982) used in the paper’s model to characterize the correlation structure of firms’ private valuations of filling a position. Affiliation implies that when one firm has a high value, others are also more likely to have high values, and hence to offer high wages — generating the model’s equilibrium wage dispersion.

Procompetitive Effect of Benchmarking: The paper’s term for the welfare-improving property of salary benchmarks identified in the model: by resolving aggregate uncertainty, benchmarks cause the marginal firm to offer closer to the full-information competitive wage, reducing extraordinary profits that arise from informational rents and raising the mean salary in equilibrium. This is the key concept in the paper’s contribution to the antitrust policy debate.