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Artificial intelligence and technological unemployment

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

Wang and Wong develop a continuous-time labor-search model to assess the dynamic effects of generative AI (GenAI) on labor productivity and unemployment. The paper is motivated by conflicting empirical evidence: micro studies find productivity gains of 14% (Brynjolfsson, Li, and Raymond 2025) and 55.8% faster coding (Peng et al. 2023), while macro estimates suggest modest TFP gains of at most 0.064% annually (Acemoglu 2024), and occupation-level evidence shows a 13% relative employment decline in AI-exposed jobs (Brynjolfsson, Chandar, and Chen 2025).

The model distinguishes GenAI from earlier automation technologies by its learning-by-using mechanism: AI capability grows at rate µ per employed worker (law of motion dAt/At = µHt − δ), raises employed workers’ productivity, and creates a displacement threat through renegotiation. When renegotiation fails, AI replaces the worker, generating technological unemployment. Firms renegotiate wages at a rate ρµAt proportional to AI’s learning rate and the job’s exposure ρ. The joint surplus condition governs whether replacement occurs: AI replaces a worker if and only if πA (AI’s net present value per output) exceeds the post-renegotiation joint surplus St.

The model admits three steady states: (i) a some-AI steady state with finite AI capability, persistent AI adoption (It = 1), expanded job creation but declining employment at H∞ = δ/µ; (ii) an unbounded-AI equilibrium with sustained endogenous growth, no displacement (It = 0), and employment at H∞ = α/(α+σ); and (iii) a no-AI equilibrium reverting to the Mortensen-Pissarides benchmark. In the benchmark model (exogenous job-finding rate, AI-augmented productivity), multiple steady states can coexist—global indeterminacy—when condition (28) holds. In the full model (endogenous job creation via free entry), both global and local indeterminacy are possible, and a continuum of oscillatory transition paths converge to the some-AI steady state.

Calibrated to U.S. data, targeting a pre-AI unemployment rate of 5%, AI elasticity of productivity εy = 1.069 (from Czarnitzki et al. 2023), initial AI productivity boost of 14% (Brynjolfsson et al. 2025), worker exposure ρ = 0.618 (Brynjolfsson et al. 2018’s machine learning suitability index), AI replacement cost ϕ = 0.0043 (from U.S. business GenAI spending), AI learning rate µ = 0.632, and AI error rate δ = 0.462 (Moore’s law half-life of 1.5 years), the model converges to a some-AI steady state. The long-run results are: a 23% employment loss (H∞ = 0.732 vs. H0 = 0.95), AI capability improvement of 321%, and labor productivity gain of 366%. Approximately half of the employment loss—11.5 percentage points—occurs within the first five years, alongside a 49.3% output gain and 45.5% AI capability improvement over that period.

Untargeted moments are validated: the model implies 7.08% labor productivity growth over the first 10 years (consistent with Briggs and Kodnani 2023) and an AI elasticity of vacancies averaging 0.16 over the first five years (consistent with Acemoglu et al. 2022).

On welfare, equilibria are inefficient even when the Hosios condition holds. AI introduces four externalities beyond standard matching frictions: job destruction via displacement, productivity enhancement for employed workers, feedback from AI learning depending on employment, and direct effects on matching surpluses. A constrained-optimal subsidy to jobs at risk of AI displacement is 26.6% in the short run and exceeds 50% in the long run. In the full model, the Hosios condition requires fixing firm bargaining power θ to the vacancy elasticity of matching ξ, but an additional per-output transfer T = µApωA to firm-worker matches is necessary to correct AI adoption inefficiency.

Q: What is the core mechanism by which AI generates unemployment in this model? A: AI capability grows through a learning-by-using process (dAt/At = µHt − δ), improving as it observes employed workers. As capability rises, firms gain a displacement option that arrives at rate ρµAt per matched pair. When renegotiation over wages fails—i.e., when the AI’s NPV πA exceeds the joint surplus—firms replace workers with AI, causing unemployment. This creates a feedback loop: higher employment accelerates AI learning, which increases displacement pressure and reduces employment.

Q: What are the three steady states and what distinguishes them? A: The some-AI steady state features finite AI capability, persistent displacement (It = 1), and long-run employment H∞ = δ/µ; it involves technological unemployment. The unbounded-AI steady state features infinite AI capability, no displacement (It = 0), endogenous productivity growth, and employment H∞ = α/(α+σ) as in the standard Mortensen-Pissarides model. The no-AI steady state has A∞ = 0 with the same H∞ = α/(α+σ) but no AI contribution. Employment is higher in the unbounded-AI equilibrium than in the some-AI equilibrium.

Q: What does the calibration imply for long-run employment and productivity? A: The calibrated full model converges to a some-AI steady state with a 23% employment loss (H∞ = 0.732), a 321% improvement in AI capability, and a 366% gain in labor productivity. The parameters yield a unique equilibrium under the baseline calibration (πA = 1.949 > sAI = 0.8735 confirms some-AI existence). These results reflect a large worker replacement effect under the calibrated AI learning and error rates, while the job creation effect is relatively modest.

Q: How fast does technological unemployment materialize? A: Approximately half of the total 23% employment loss occurs within the first five years; specifically, employment falls by 11.5 percentage points over that period. Over the same five years, AI capability improves by 45.5% and output rises by 49.3%. Over the first 10 years, AI capability improvement accumulates to 94.0% and output gain to 103% (approximately double the five-year output gain).

Q: How does the full model differ from the benchmark model in transition dynamics? A: In the full model, job-finding rates are endogenous: firms post vacancies until a free-entry condition (κyt = ftΠt) is satisfied, tying job-finding rate αt to the surplus ratio st via αt = α(st). This endogeneity implies that as AI raises labor productivity, firms create more vacancies, slowing the employment decline relative to the benchmark model with a fixed job-finding rate. At the same time, AI capability grows faster in the full model because higher employment accelerates AI learning.

Q: What is global indeterminacy and when does it arise? A: Global indeterminacy occurs when both the some-AI and unbounded-AI steady states coexist, so the long-run outcome depends on initial conditions or expectations. In the benchmark model this requires condition (28): 0 < r + σ + α(1−θ) − (1−b)/πA ≤ εy(µα/(α+σ) − δ). In the full model, global indeterminacy is plausible when firm bargaining power rises to θ = 0.95 given the baseline AI replacement cost ϕ = 0.0043. The region of global indeterminacy is larger when firm bargaining power is higher.

Q: What is local indeterminacy and what does it imply for transition paths? A: Local indeterminacy means there is a continuum of equilibrium paths converging to the some-AI steady state in the neighborhood of that steady state, rather than a unique saddle path. In the full model, under alternative parameters (θ = 1, ξ = 0.765, εy = 6), the eigenvalues feature a negative real root and two complex roots with negative real parts, yielding oscillatory local dynamics in employment and AI capability. This implies short-run cycles in productivity and unemployment, consistent with the wide range of empirical findings on AI’s labor-market effects.

Q: Why does the Hosios condition fail to deliver efficiency in this model? A: The Hosios condition eliminates the standard matching externality by setting firm bargaining power to the vacancy elasticity of matching. But AI introduces four additional externalities: (i) job destruction through displacement, (ii) productivity enhancement for employed workers, (iii) feedback from AI learning that depends on aggregate employment, and (iv) direct effects on matching surpluses and job-finding rates. These externalities mean the standard Hosios rule alone is insufficient; additional instruments are required.

Q: What is the constrained-optimal policy response? A: In the simple model, the constrained optimal AI adoption threshold differs from the equilibrium threshold because firm bargaining power θ distorts adoption decisions: AI is over-adopted when πA > (1−b)/(r+σ+α(1−θ)) and under-adopted when (1−b)/(r+σ+α) < πA ≤ (1−b)/(r+σ+α(1−θ)). In the full model, constrained optimality requires setting θ = ξ (Hosios) plus a per-output subsidy T = µApωA to firm-worker matches exposed to AI displacement. This targeted subsidy is 26.6% in the short run and exceeds 50% in the long run.

Q: How does AI compare to computers in this model’s counterfactual? A: The paper reports that exogenous productivity growth from computers reduced unemployment only modestly—by 0.16 percentage points. By contrast, AI’s learning-by-using and displacement features imply a nearly 20% long-run employment loss in a comparable counterfactual. The key distinction is that computers lack the self-learning improvement and associated renegotiation-triggered displacement that characterize GenAI in this model.

Q: How is AI exposure parameterized and what does it capture? A: The exposure parameter ρ captures the degree to which a job is subject to AI-driven replacement risk. It is calibrated using Brynjolfsson et al. (2018)’s suitability for machine learning (SML) index: on a 1–5 scale, SML averages 3.47 across 964 O*NET occupations, translating to (3.47−1)/(5−1) = 61.8%, so ρ = 0.618. The effective exposure measure is ρµ, which is higher when facing a faster-learning AI.

Q: What is the predator-prey analogy in the model’s dynamics? A: The dynamical system for AI capability (At) and employment (Ht) in the simple model resembles the Lotka-Volterra predator-prey system. Employment (prey) feeds AI learning; as AI capability (predator) grows, it displaces workers faster, reducing employment; lower employment then slows AI learning, causing capability to decay; and the cycle repeats with diminishing magnitude until the steady state is reached. This mechanism operates only when the AI learning rate µ is neither too high nor too low, with the convergence path being a spiral when µα < 4δ²(1 − δ(α+σ)/(µα)).

Q: What is the labor-share implication of the unbounded-AI equilibrium? A: In the unbounded-AI steady state, employment is higher than in the some-AI steady state (H^AJJ > H^AI) and labor productivity grows without bound. However, the labor share is lower in the unbounded-AI equilibrium if the firm’s bargaining power θ is sufficiently low. This implies that while workers are not fully displaced and rising AI-augmented productivity sustains employment, workers’ income share may still decline even in the more favorable unbounded scenario.

Technological unemployment: A phenomenon in which AI adoption raises labor productivity and expands job creation, yet still causes sizable employment losses because the worker displacement effect (driven by renegotiation failure when AI’s NPV πA exceeds the joint surplus) dominates the job-creation effect. In the calibrated model this amounts to a 23% employment loss despite a 366% productivity gain.

Learning-by-using AI: The model’s representation of GenAI as a technology whose capability At grows through reinforced learning from employed workers at rate µ per worker, so aggregate AI growth is µHt, offset by deterioration at rate δ. This distinguishes GenAI from earlier automation technologies (computers, robotics) that do not self-improve through usage.

Some-AI steady state: A long-run equilibrium with finite AI capability (gA∞ = 0), persistent AI adoption (It = 1), and employment pinned at H∞ = δ/µ—the ratio of AI’s error rate to its learning rate. Characterized by expanded job creation but lower employment than the no-AI benchmark, constituting the model’s primary calibrated outcome.

Unbounded-AI steady state: A long-run equilibrium with infinite AI capability (A∞ = ∞), no displacement (It = 0), and endogenous growth at rate gA = µH^AJJ − δ. Employment equals the Mortensen-Pissarides level H∞ = α/(α+σ), and labor productivity grows without bound, complementing Aghion, Jones, and Jones (2019)’s idea production framework.

Global indeterminacy: Coexistence of multiple steady states (some-AI and unbounded-AI) such that the long-run equilibrium depends on initial conditions or expectations rather than being uniquely determined. Arises in the benchmark model when condition (28) holds and becomes more likely with higher firm bargaining power θ.

Local indeterminacy: A continuum of equilibrium transition paths converging to a single steady state from nearby initial conditions, rather than a unique saddle path. Arises in the full model under certain parameter configurations (e.g., θ = 1, ξ = 0.765, εy = 6), implying oscillatory short-run dynamics in employment and AI capability.

AI exposure (ρ): A firm-level parameter capturing the degree to which a job-match is subject to AI-driven displacement risk. The displacement option arrives at rate ρµAt per matched pair; ρ is calibrated at 0.618 using the average suitability-for-machine-learning score across O*NET occupations. The effective exposure measure is the product ρµ.

Renegotiation-proof displacement: Proposition 1’s result that the joint surplus Snt is independent of the renegotiation round n, so the AI adoption decision It is also round-invariant. This simplifies the model to a single indicator function: AI replaces the worker if and only if πA exceeds the joint surplus St, regardless of how many renegotiation rounds have occurred.

Civil War–Induced Displacement and Human Capital

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

This paper examines the impact of conflict-driven forced displacement on human capital accumulation using the Mozambican civil war (1977–1992) as the empirical setting. During this war, over four million civilians — roughly a third of the population — fled to rural areas, cities, neighboring countries, or UN-managed refugee camps. The study advances on prior work in three dimensions: it uses the full post-war population census (12 million individuals) rather than a small survey; it studies multiple displacement trajectories in a single framework; and it separately identifies place-based exposure effects from a general uprootedness effect.

The primary data source is the 1997 Mozambican census, which records each individual’s place of birth, residence in 1992 (the war’s end), and residence in 1997. Key outcomes are educational attainment and sectoral employment (agricultural versus services). The authors supplement the census with digitized colonial road and school maps, georeferenced conflict events, and landmine contamination data.

The main identification strategy compares approximately 135,000 siblings (from 45,000 families) separated during the war, using the sibling who stayed behind as a within-family counterfactual. This design controls for household-level characteristics including religious and ethnic background, aspirations, and exposure to violence.

The key findings are as follows. First, rural-born IDPs displaced to cities have a 7.3 percentage point higher likelihood of attending primary school and 0.53 more years of schooling compared to their siblings who stayed behind — roughly one-third of the non-displaced mean. Rural-born IDPs displaced to other rural areas also show gains, with a 3 percentage point higher likelihood of attending school and 0.24 additional years, supporting the uprootedness hypothesis even for displacements that did not reach urban centers. Urban-born IDPs forcibly relocated to the countryside — primarily through FRELIMO’s villagization scheme — experienced 9 percentage point lower primary school attendance and approximately 0.5 fewer years of schooling relative to siblings who remained in cities.

External displacement (to camps in Malawi or Zimbabwe) generated no significant schooling gains relative to staying siblings, despite UN-built schools in camps, likely because scarce employment opportunities reduced perceived returns to education.

Second, the paper jointly estimates place-based and uprootedness effects in a single within-family framework. Place effects are statistically significant: displacement to a district one standard deviation more developed than one’s birthplace raises schooling likelihood by approximately 3 percentage points (OLS) to 5 percentage points (2SLS reduced form). Crucially, a residual uprootedness effect of approximately 2–4 percentage points persists even after controlling fully for destination-origin differences in development and conflict intensity. This uprootedness effect is quantitatively comparable to being displaced to a district one standard deviation more developed than one’s birthplace.

Third, a primary survey of 208 Nampula residents conducted in early 2020 — three decades after the war — confirms lasting educational gains. IDPs displaced to Nampula have a 10 percentage point higher likelihood of completing primary school relative to their siblings who stayed in the countryside, and their educational attainment converged to levels of urban-born, never-displaced residents despite large urban-rural education gaps. However, IDPs report significantly lower social capital, civic participation, and community trust than urban-born respondents, and score significantly worse on mental health indicators, including depression, loneliness, and pessimism. These psychosocial costs persist three decades after the war’s end.

The findings apply to a low-income, post-colonial African setting characterized by widespread illiteracy (over 60%) and subsistence agriculture (over 85% of employment) at the war’s close. The results are robust to alternative age restrictions, extended family comparisons, dropping the oldest sibling, same-sex sibling pairs, and narrowing the age gap between sibling pairs to as few as two years.

Q: What is the core identification strategy and why is it preferred over cross-sectional estimates? A: The authors compare siblings within the same household who experienced different displacement trajectories during the war. Because siblings share household-level characteristics — parental preferences for education, ethnic and religious background, wealth, and local conflict exposure — the within-family design controls for confounders that would bias cross-sectional estimates. The within-family estimates are systematically smaller than cross-sectional ones (e.g., 7.3 pps vs. 24–30 pps for rural-to-urban displacement in primary school attendance), confirming that sorting was present even in the unpredictable civil war setting.

Q: What do the results show for rural-born IDPs displaced to urban centers? A: Within the sibling-pair framework, rural-born IDPs displaced to cities and towns have a 7.3 percentage point higher likelihood of attending primary school and 0.53 more years of schooling compared to their siblings who stayed in rural birthplaces, against a non-displaced sibling mean of approximately 20% primary school access and one year of formal schooling. These IDPs also show a 4 percentage point higher likelihood of non-agricultural employment five years after the war’s end.

Q: What do the results show for rural-born IDPs displaced to other rural areas? A: Even displacement to a different rural district — not a city — generates modest but statistically significant gains: a 3 percentage point higher likelihood of attending school and 0.24 additional years of schooling relative to siblings staying in their birthplace rural district. The authors interpret this as evidence for the uprootedness hypothesis, since rural Mozambique at the time was among the most impoverished and insecure environments in the world, meaning destination quality alone cannot explain the gain.

Q: What do the results show for externally displaced refugees? A: Refugees displaced to camps and settlements in Malawi, Zimbabwe, Tanzania, Zambia, and Swaziland show schooling levels statistically similar to their siblings who remained in their rural birthplaces, despite UN-built primary schools in camps. The authors attribute the absence of gains to low perceived returns to education stemming from scarce employment opportunities at displacement destinations. Externally displaced individuals do show a 5 percentage point lower likelihood of agricultural employment relative to staying siblings.

Q: What are the consequences of urban-to-rural forced displacement? A: Urban-born individuals forcibly relocated to the countryside — primarily through FRELIMO’s villagization and food production programs — have approximately 9 percentage point lower likelihood of attending primary school and 0.5 fewer years of schooling compared to siblings who remained in urban areas. These results indicate that FRELIMO’s coercive relocation policies imposed material human capital costs on the displaced.

Q: How are place-based and uprootedness effects separated empirically? A: The authors construct principal component indices for destination-origin differences in regional development (aggregating population density, Portuguese-speaking share, offspring mortality, road density, colonial market density, and school density) and conflict intensity (conflict events per capita and landmine contamination per capita). They then include these continuous exposure measures alongside a binary displacement indicator in within-family regressions. The coefficient on the binary displacement indicator — conditional on destination-origin development and conflict differences — isolates the uprootedness effect for individuals displaced to districts with identical characteristics to their birthplace.

Q: What are the magnitudes of the place-based and uprootedness effects? A: Under OLS, displacement to a district one standard deviation more developed than one’s birthplace raises schooling likelihood by approximately 3 percentage points. The residual uprootedness effect — displacement per se, controlling for destination quality — raises schooling likelihood by approximately 2 percentage points. Under 2SLS (instrumenting destination-origin development differences with the development of districts within 100 km of birthplace), the place-based effect rises to approximately 5 percentage points in the reduced form, and the uprootedness effect remains significant at approximately 4 percentage points. Both the uprootedness and place-based effects are of comparable magnitude.

Q: What instrument is used in the 2SLS specifications and what is its first-stage strength? A: The instrument exploits the fact that Mozambique’s heavily mined and rudimentary transportation network constrained civilian movement — the median displaced sibling ended up roughly 97 kilometers from birthplace. The authors instrument actual destination-origin development and conflict differences with the predicted differences based on the characteristics of districts within 100 km of the birthplace. The first-stage elasticity between actual and proximity-predicted differences in development is 0.86, and for conflict is 0.88, both precisely estimated.

Q: What do the long-run survey results from Nampula show about educational persistence? A: In a 2020 survey of 208 Nampula residents aged over 35, IDPs who fled to Nampula during the war have a 10 percentage point higher likelihood of completing primary school relative to their siblings who stayed in the countryside. Their educational attainment converges to the level of urban-born, never-displaced Nampula residents, despite large historical and contemporary urban-rural education gaps in northern Mozambique. The majority of IDPs (73%) report that extended relatives or friends advised them to attend school upon arriving in the city, and most believed education was necessary for urban employment.

Q: What are the long-run psychosocial costs documented in the Nampula survey? A: Even three decades after the war’s end, IDPs in Nampula report significantly lower social capital, civic participation, and community trust compared to urban-born never-displaced residents. IDPs also score significantly worse on mental health indicators including depression, loneliness, and pessimism. These findings suggest that forced displacement imposes persistent psychosocial costs that are not remediated by economic or educational convergence.

Q: What drives displacement in the data, and does selection threaten identification? A: Linear probability and multinomial logit models show that conflict intensity and geographic proximity (distance to the border for external displacement; distance to cities for urban displacement) are the primary correlates of displacement type, while differences in destination development are uncorrelated with displacement. Nevertheless, the overall explanatory power of these models is low, confirming many idiosyncratic and unpredictable features of the war. The within-family design addresses residual selection on household characteristics, and the 2SLS design addresses selection on destination-specific characteristics.

Q: How do educational gains translate into sectoral employment outcomes? A: Across specifications, gains in schooling move in tandem with a shift out of agriculture into services. Rural-to-urban IDPs have a 4 percentage point higher likelihood of non-agricultural employment five years after the war, while externally displaced show a 5 percentage point lower likelihood of agricultural employment. Urban-born IDPs displaced to the countryside are more likely to work in agriculture after the war. The authors interpret this co-movement as suggesting that conflict-driven human capital accumulation may contribute to structural transformation away from subsistence agriculture.

Q: How robust are the within-family estimates? A: The authors conduct six sensitivity checks: adding family fixed effects to cross-sectional regressions, restricting to individuals aged 12–18 in 1997 to address co-habitation concerns, extending comparisons to cousins and other relatives, dropping the oldest male sibling to minimize favoritism concerns, restricting to same-sex sibling pairs, and narrowing the age gap to two years. Across all permutations, the qualitative ordering is preserved: refugees show no significant schooling gains, rural-to-urban IDPs show gains of 5–6 percentage points in primary attendance and 0.35–0.5 extra years, rural-to-rural IDPs show small positive gains, and urban-to-rural IDPs show losses.

Uprootedness hypothesis: The idea, traced in the paper to Stigler and Becker (1977) and earlier scholars, that forced displacement incentivizes human capital investment precisely because education is a mobile asset that cannot be expropriated — distinct from place-based effects of destination quality.

Place-based (exposure) effects: The impact on human capital outcomes attributable to differences between the development level and conflict intensity of the displacement destination and the individual’s birthplace, measured as destination-origin differences in a principal component index of regional development.

Separated siblings design: An identification strategy that compares siblings from the same household who experienced different displacement trajectories during the war, holding constant all household-level characteristics including parental preferences, ethnicity, religion, wealth, and local conflict exposure.

Internal displacement (IDP): Conflict-driven movement within national borders to either rural areas or urban centers, constituting approximately 60% of global forced displacement and the majority of displacement in the Mozambican civil war context.

Source text origin: A categorization of the working paper text used for summarization — distinguishing full PDF or HTML text from abstract-only text. Abstract-only text is a hard block for summary generation in the pipeline.

Structural transformation: In this paper’s usage, the shift of workers out of subsistence agriculture into services associated with human capital accumulation triggered by conflict-driven displacement, treated as a potential mechanism of post-conflict recovery.

Psychosocial costs of displacement: Long-run deficits in social capital, civic engagement, community trust, and mental health (depression, loneliness, pessimism) reported by IDPs three decades after displacement, persisting despite convergence in educational attainment and employment.

Global Working Hours

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

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

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

In depth

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Q9. What is the paper’s overall interpretation?

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

Q10. What are the main scope conditions and caveats?

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

Key concepts

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

Key concepts

Monopsony Makes Firms Not Only Small but Also Unproductive: Why East Germany Has Not Converged

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

Layer 1 — Summary

When employers face a trade-off between growing large and paying low wages — that is, when they have monopsony power — some productive employers will decide to acquire fewer customers, forgo sales, and remain small; these decisions have adverse consequences for aggregate labor productivity beyond the standard monopsony result that firms are too small. The paper documents that East German plants (compared to West German ones) face a steeper size-wage curve, invest less into marketing, and remain smaller, with the share of employment at plants with more than 249 employees standing at roughly 25% in East Germany versus 39% in West Germany in 2014 (and 31% versus 55% in manufacturing specifically). The steeper size-wage curve in East Germany is traceable to the historically determined underrepresentation of collective bargaining and union membership in small East German plants — a legacy of communist-era labor organization that caused union membership to collapse after reunification. The authors combine this evidence with a heterogeneous-plant model in which plants have product market power and choose how many customers to acquire subject to an upward-sloping size-wage schedule; two channels reduce aggregate productivity: a love-of-variety loss (fewer active plants means consumers bundle from a smaller variety of suppliers) and a compositional reallocation loss (labor is shifted from more productive to less productive plants, an effect exacerbated by product market power). When the model is calibrated to West Germany and the steeper East German size-wage trade-off is imposed, it predicts 10 percentage points lower aggregate labor productivity in East Germany — and for manufacturing, where East-West differences in plant size and the size-wage trade-off are particularly pronounced, the model predicts 18 percentage points lower productivity; in both cases the compression of the plant size distribution accounts for the largest share of the predicted productivity loss. The paper thus offers an explanation for why, more than thirty years after reunification, labor productivity and wages remain roughly 25% lower in the East German private sector despite uniform legal institutions across the two regions.

In depth

Q1. What is the core mechanism by which monopsony power reduces aggregate productivity, and how does it differ from the standard “firms are too small” result?

In the standard monopsony account, firms face an upward-sloping labor supply curve and choose to employ fewer workers than the competitive optimum, so individual firms are below efficient scale. The paper identifies an additional, investment-distortion channel: plants must also decide how large a customer base to acquire, and doing so requires marketing expenditure as well as the labor to service additional customers — labor whose cost rises with plant size along the size-wage schedule. A steeper size-wage curve therefore makes customer acquisition more expensive at the margin, and some productive plants optimally choose to acquire fewer customers, forgo sales, and remain small. The new aggregate productivity loss stems from this distorted investment margin: plants that could generate high value added at large scale instead operate at sub-optimal customer networks, suppressing aggregate output through both a love-of-variety effect (fewer active large plants means consumers access a smaller product variety) and a misallocation effect (the compressed size distribution shifts employment toward less productive plants).

Q2. What empirical patterns do the authors document to link the East-West productivity gap to missing large plants and steeper size-wage curves?

The authors document three nested empirical facts using the German Structure of Earnings Survey (SES) pooled across 2006, 2010, and 2014, supplemented by administrative wage panel data (AWFP) and national accounts (VGR). First, East German labor productivity in the private non-primary sector is about 25% below West Germany’s and has not converged since roughly 1995. Second, the share of employment at large plants (>249 employees) is substantially smaller in the East, and this gap is present both cross-sectionally across survey years and conditionally: East German plants enter smaller and remain smaller over their life-cycles, so plant age does not explain the difference. Third, industries where missing large plants are most pronounced in East Germany relative to West Germany are also the industries with the largest East-West productivity and wage gaps — the employment-weighted correlation between the large-plant share gap and the productivity gap is 0.53 across industries. The steeper size-wage curve itself is documented using within-industry comparisons: on average the plant size elasticity of wages is one-fifth larger in East Germany, and those industries with a steeper East-West size-wage differential are also the industries with the most missing large plants and the lowest average wages in the East.

Q3. Why is the steeper size-wage curve specific to East Germany, and why does it persist decades after reunification?

In communist East Germany, trade unions did not have the role of representing worker interests; consequently, after reunification, union membership fell dramatically. The key institutional consequence is that collective bargaining coverage in East Germany is underrepresented specifically in small plants. Workers at small plants in East Germany are more likely to have individually rather than collectively bargained wages than their West German counterparts, whereas workers at large plants in both regions are more similarly covered. Because collective bargaining flattens the size-wage curve (larger plants pay a smaller premium over small plants’ wages when both are covered by the same bargaining agreement), its absence in small East German plants produces a steeper gradient of wages with plant size in the East. This is a persistent structural feature rather than a transitional one: government policies and their enforcement are essentially uniform across regions, so the asymmetric bargaining coverage, which originates in communist-era institutional history, has not been erased by market forces or policy since 1990.

Q4. How is the model structured, and what are the three decision stages for plants?

The model is a static, long-run heterogeneous-plant framework that yields closed-form solutions. Within a period, plants face a three-stage decision problem. First, they decide whether to enter the market. Second, after entry, they choose how many customers to acquire, trading off additional sales revenue against marketing costs and the labor cost of servicing a larger customer base — a cost that rises with the number of customers because the upward-sloping size-wage curve means each additional worker hired requires a higher wage for all infra-marginal workers. Third, taking into account their product market power (each plant is a monopolistic competitor with its own customers), plants set prices to each customer and thereby determine how many workers they need. The size-wage schedule enters the second stage directly, so a steeper schedule reduces optimal customer acquisition across all plants, with the distortion being largest for the most productive plants (which would otherwise grow the largest).

Q5. Through what two channels does the steeper size-wage trade-off reduce aggregate labor productivity in the model?

The first channel is a love-of-variety effect in the product market: because more productive plants acquire fewer customers and operate at smaller scale under a steeper size-wage schedule, the average consumer bundles goods from a smaller number of distinct plants, and aggregate efficiency falls through the standard CES love-of-variety mechanism. The second channel is a misallocation effect in the labor market: the steeper size-wage schedule compresses the employment distribution across plants, reallocating labor from more productive to less productive plants relative to the benchmark with a flatter schedule. The paper shows that this second channel is exacerbated by product market power, because plants with stronger pricing power respond more aggressively to the changed labor cost trade-off. In the model’s decomposition, the compression of the plant size distribution (the misallocation channel) accounts for the largest part of the predicted 10 percentage point productivity shortfall.

Q6. What quantitative predictions does the model make, and how does it perform in untargeted moments?

The model is calibrated to two moments for West Germany: average plant size and the share of large plants (>249 employees). When the steeper East German size-wage trade-off is imposed without re-calibrating other parameters, the model predicts 10 percentage points lower aggregate labor productivity in East Germany — accounting for at least 10 of the roughly 25 percentage point observed gap. For the manufacturing sector alone, where East-West differences in plant size, the size-wage trade-off, and aggregate productivity are particularly pronounced, the calibrated model predicts 18 percentage points lower productivity. As an untargeted validation, the model also replicates the plant size distribution in East Germany, matching both the smaller average plant size and the relatively small number of large plants. These untargeted predictions provide additional support for the mechanism.

Q7. What alternative explanations for East Germany’s non-convergence does the paper rule out or place in context?

The paper addresses several confounds. In Appendix A, the authors show that East-West aggregate labor productivity differences are driven by differences in aggregate total factor productivity, not by labor quality differences, capital intensity differences, or capital quality differences — confirming within-country the finding that TFP explains a large fraction of productivity dispersion. The TFP differences are shown to be unlikely the result of greater labor market flexibility in West Germany or differences in industry composition. Appendix B shows that the East-West plant size distribution gap is not driven by differences in urbanization (West Germany has more metropolitan areas). The paper also addresses plant age: East German plants enter smaller and remain smaller at every age and across entry cohorts, ruling out the hypothesis that the size gap is purely a transitional legacy of the restructuring that destroyed many large East German plants at reunification.

Q8. How does this paper relate to the Heise and Porzio (2021) finding that plant productivity differences, not worker quality differences, drive the East-West wage gap?

Heise and Porzio (2021) use matched employer-employee data to document that plant productivity differences (as opposed to worker quality differences) account for most of the East-West wage differential, and they explain why low worker mobility does not remove these differences. The present paper complements this by providing an explanation for why plant productivity is lower in East Germany in the first place and why firm-level convergence does not occur: the steeper size-wage curve induced by the legacy of missing collective bargaining coverage in small East German plants distorts the investment and customer acquisition decisions of productive plants, keeping them small and unproductive. The two papers are thus complementary: Heise and Porzio take the plant productivity gap as given; Bachmann et al. endogenize it through the size-wage mechanism.

Key Concepts

Size-wage curve: The empirical relationship between plant size (measured by employment) and wages paid to workers, conditional on worker characteristics. A steeper size-wage curve means that the wage premium for working at a large plant relative to a small plant is larger. In this paper’s model, plants internalize that expanding their customer base and workforce requires paying higher wages to all workers (not just the marginal hire), making growth more costly when the size-wage curve is steeper.

Monopsony power (monopsonistic competition): The market structure in which an individual employer faces an upward-sloping labor supply curve — i.e., it must raise wages to attract additional workers. The paper uses “monopsonistic competition” to describe a setting with many such employers, each with some wage-setting power, in contrast to oligopsony. The paper focuses on allocative effects of this power, not on normative efficiency questions.

Customer capital / customer acquisition: Plants must incur marketing expenses to build a customer base; each customer relationship generates a stream of sales but requires labor to service. The size of the customer network is a long-run investment decision. Under monopsonistic labor markets, the cost of expanding the customer base includes not only marketing expenses but also the higher wages that a larger workforce requires, making customer acquisition a margin that is distorted by labor market power.

Love-of-variety effect: A welfare loss that arises in models with monopolistic competition and CES preferences when the number of active product varieties declines. In this paper it applies to the product market: when plants remain small and acquire fewer customers, the effective number of distinct varieties consumed falls, reducing aggregate efficiency even holding plant-level productivity fixed.

Misallocation / compressed size distribution: A situation in which factors of production are not allocated to their highest-value uses. Here, the steeper size-wage curve induces productive plants to remain small, so labor that would otherwise be employed at high-productivity large plants is instead employed at lower-productivity small plants. The resulting compression of the plant size distribution — fewer very large plants, more mass in the middle — is both the key empirical fact and the primary quantitative driver of the predicted aggregate productivity shortfall.

Collective bargaining coverage: The fraction of workers whose wages are set by collective agreements between employers (or employer associations) and trade unions, rather than by individual negotiation. The paper establishes that collective bargaining flattens the size-wage curve by compressing wages across plants of different sizes. The historically low collective bargaining coverage among small East German plants — a legacy of communist-era labor relations — is the institutional root cause of the steeper East German size-wage schedule.

Summary based on IZA Discussion Paper 15293. AI-assisted, human review pending.

The Impact of Incarceration on Employment, Earnings, and Tax Filing

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

Overview

This paper estimates the causal effect of incarceration on employment, wage earnings, self-employment, and tax filing behavior using administrative criminal justice data linked to Internal Revenue Service (IRS) records for approximately half a million felony defendants in two U.S. states: North Carolina and Ohio. The study period covers cases filed from the early 2000s through 2014, with outcomes tracked through 2020 using IRS W-2 and 1040 records.

Research Question

The central question is whether incarceration itself — as distinct from arrest, conviction, and other criminal justice interactions that precede or accompany it — causes lasting reductions in defendants’ labor market outcomes. The paper explicitly holds fixed upstream interactions (conviction, arrest) to isolate the effect of the incarceration sentence.

Data and Sample

Criminal justice records from Ohio (Common Pleas courts in Franklin, Cuyahoga, and Hamilton counties, covering Columbus, Cleveland, and Cincinnati) and North Carolina (Administrative Office of the Courts and Department of Public Safety) are linked to de-identified IRS records via name, date of birth, sex, address, and partial Social Security Numbers. Match rates are 92% in Ohio and 95% in North Carolina. The sample is restricted to defendants aged 18–50 at time of offense with cases filed 2002–2014. IRS records include employer-reported W-2 wages (regardless of individual tax filing), self-employment income from Schedule C/SE, non-employee compensation (1099-MISC), and gig-economy earnings from 1099 returns. All dollar figures are adjusted to 2016 dollars using the PCE deflator.

Empirical Strategy

Two independent quasi-experimental research designs are used:

North Carolina — Sentencing guideline discontinuities: North Carolina’s structured sentencing guidelines map offense class (E through I, the five least severe felony classes) and prior record points (a numerical criminal history score) into permissible punishment types (incarceration vs. probation) and sentence lengths. Allowable punishment types change discretely at five cell boundaries, generating discontinuities in incarceration sentences for otherwise similar defendants. The paper uses these five boundary discontinuities as excluded instruments in a parameterized regression discontinuity design stacked across offense classes. First-stage F-statistic = 115.
Ohio — Random assignment to judges: Cases are randomly assigned by computer to judges at arraignment in the three counties studied. Judge leave-out mean sentence length is used as an instrument for individual sentence length. The design follows Norris et al. (2021) and yields F-statistic = 321. The instrument shifts sentences along both the extensive margin (any vs. no incarceration) and intensive margin (longer vs. shorter sentences).

Both designs produce complier populations for whom at least 37–45% are shifted on the extensive margin (from no incarceration to some incarceration), based on partial identification bounds using linear programming.

Main Findings

The paper’s central finding is that incarceration generates large short-run reductions in labor market activity during the incapacitation period, but no detectable long-run reductions in annual employment or earnings once defendants have been released and the incapacitation effects have dissipated.

In the first year after case filing, when incarceration rates peak (roughly 75–100 additional days incarcerated for a 12-month sentence), employment falls by approximately 10 percentage points and total W-2 earnings contract commensurately.
Within 3–4 years of filing, employment effects return to near zero and are statistically insignificant in both states.
Five to nine years after filing, when effects on contemporaneous incarceration have dissipated, the estimated effect of a 12-month sentence on annual earnings is positive or near zero in both states. The combined 95% confidence interval rules out reductions in annual wages greater than $231 (approximately 5% of the untreated complier mean) and rules out any adverse employment effects.
Despite no long-run level effects, losses during incapacitation are never recouped. A one-year sentence reduces cumulative earnings over five years by approximately $2,914 — a 13% reduction relative to the complier mean.
Effects on self-employment, independent contracting, 1040 filing, adjusted gross income, EITC take-up, and interstate migration are similarly null in the long run.

Incapacitation vs. Post-Release Scarring

The paper provides two tests for whether short-run earnings losses reflect incapacitation alone or also post-release scarring (e.g., human capital depreciation, employer discrimination, or discouragement effects):

A “visual IV” regression of year-t earnings effects on year-t days-incarcerated effects yields an R² of 0.83–0.85 across states, with the intercept near zero (positive and small), indicating that virtually all dynamic earnings impacts flow through contemporaneous incapacitation and not through a post-release channel.
Constructed outcomes that impose the null of pure incapacitation (scaling pre-case average earnings or covariate-predicted earnings by the share of the year free from prison) closely track actual earnings effects in both states, further confirming that incapacitation is the dominant mechanism.

Pre-existing Labor Market Detachment

A key scope condition is defendants’ severe labor market disadvantage prior to their case. Fewer than 50–60% of defendants are employed in the year before filing; average pre-case W-2 earnings (including zeros) are below $6,000. Among employed defendants, only 10% earn more than $22,000 per year. Untreated complier means for earnings in the year after case filing are below $4,000, with virtually no earnings or employment growth over the following nine years. The paper concludes that returning to pre-filing earnings levels is sufficient for incarcerated defendants to match their non-incarcerated peers — a low bar that is readily met.

Policy Implications

Back-of-envelope aggregation implies incapacitation losses of approximately $6.16 billion per year in foregone earnings for the U.S. prison population, concentrated in communities heavily affected by incarceration. However, a marginal reduction in incarceration rates would increase average earnings by only $51 for white men and $213 for black men, suggesting incarceration’s direct contribution to labor market inequality is modest relative to the $21,100 black-white earnings gap estimated by Bayer and Charles (2018). The paper concludes that upstream factors — other criminal justice interactions, human capital deficits, and broader socioeconomic disadvantage — are more plausibly responsible for low earnings among the formerly incarcerated.

In depth

Q1. What is the exact treatment variable, and what is the counterfactual?

The treatment variable is months of incarceration sentenced in the focal case (a continuous, weakly positive ordered treatment). The counterfactual for non-incarcerated defendants in North Carolina is probation (all defendants are convicted by construction under structured sentencing guidelines). In Ohio, the authors cannot reject that all compliers who do not receive a prison sentence are still convicted, implying the counterfactual is also conviction and probation. All compliers therefore acquire a criminal record regardless of sentence. The treatment effect is thus the effect of incarceration conditional on conviction, holding fixed the criminal record.

Q2. How are effects interpreted given multiple instruments and continuous treatment?

Under a “weakly positive ordered treatment” assumption and standard LATE conditions, the 2SLS estimates can be interpreted as Average Causal Responses (ACRs) — weighted averages of the marginal dose effects (12 vs. 11 months, 6 vs. 5 months, 1 vs. 0 months, etc.) for complier subgroups shifted by each instrument. In North Carolina with five parameterized RD instruments, the estimate averages ACRs weighted by first-stage strength. In Ohio with a leave-out mean instrument, the estimate is a convex average of ACRs under the assumption that the linear first-stage model is a good approximation. Dosage weights for both states put mass on a wide range of sentence lengths including both extensive and intensive margins, though Ohio’s weights are more skewed toward shorter sentences.

Q3. How large are the first-stage effects, and how strong is the instrument?

In North Carolina, sentences jump by 50% or more at sentencing guideline cell boundaries where allowable punishment types change to include incarceration. The first-stage F-statistic is 115. In Ohio, defendants assigned to the most severe judge receive incarceration sentences approximately six months longer than those assigned to the least severe judge (roughly 30% of the average non-zero sentence), with a slope of approximately 0.8 in the first-stage regression; F-statistic = 321. At least 37% of compliers in North Carolina and 45% in Ohio are shifted on the extensive margin (from no incarceration to some positive incarceration), with upper bounds as high as 95%.

Q4. What evidence supports instrument validity (exclusion restriction and independence)?

Instrument validity is tested by estimating 2SLS “effects” on pre-case outcomes measured 2–4 years before the focal case. In both states, the instruments show no relationship with pre-case employment, W-2 wages, total days previously incarcerated, or binary severe prior incarceration. The probability of being matched to IRS records and the quality of the match are also uncorrelated with the instruments. In Ohio, potential exclusion restriction violations from judges affecting conviction (not just sentence) are addressed empirically: nearly 90% of defendants are convicted, the most severe judge is only 0.7 p.p. more likely to convict than the least severe judge (t-stat = 1.53), and the estimated conviction rate among untreated compliers is 0.972 (s.e. 0.018), so one cannot reject that all non-incarcerated compliers are convicted.

Q5. How does the paper test for the incapacitation mechanism against post-release scarring?

Two complementary exercises are conducted. First, a “visual IV” plot regresses year-t earnings effects on year-t days-incarcerated effects across all post-filing years. If incapacitation is the sole channel, all points should lie on a line through the origin. The R² is 0.83 in North Carolina and 0.85 in Ohio, the estimated intercept is near zero (positive and small) in both states, and the slope (earnings lost per day incarcerated) is approximately $12. This implies cumulative earnings losses of $12 × 268 days = $3,216, very close to the directly estimated $2,914. Second, constructed outcomes that scale pre-case earnings or covariate-predicted earnings by the share of the year not incarcerated closely track actual earnings effects throughout the post-filing period, and both converge to zero as incapacitation effects fade — consistent with pure incapacitation and no net scarring.

Q6. What are the long-run (5–9 years) earnings and employment estimates, and how precisely are null effects ruled out?

Averaged across both states using inverse-variance weights, the estimated effect of a 12-month sentence on annual W-2 earnings five to nine years after filing is positive but statistically indistinguishable from zero. The 95% confidence interval rules out reductions in annual wages greater than $231 (approximately 5% of the untreated complier mean of roughly $4,500–$5,000). The 95% CI also rules out any adverse employment effects. The untreated complier mean for employment 5–9 years post-filing is approximately 40% in North Carolina and slightly above 40% in Ohio.

Q7. What happens to cumulative earnings over five years despite null long-run level effects?

Even though long-run annual earnings are unaffected, earnings losses during incapacitation are never made up. A one-year sentence reduces cumulative employment (measured as years with any W-2) and cumulative earnings over five years by approximately $2,914 — a 13% reduction relative to the complier mean. This reflects the mechanical loss of earnings during the period of physical incapacitation, without a subsequent compensating period of higher earnings after release.

Q8. Do defendants with stronger pre-case labor market attachment show different long-run patterns?

The sample is split between defendants employed in at least 2 of the 4 years prior to the case (53–57% of the sample across states) and those less attached. Both groups show zero long-run earnings and employment effects. Previously employed defendants experience much larger short-run earnings drops — more than three times larger in the first year post-filing — and their earnings recover more slowly, reaching zero effect approximately six years after filing (vs. three years for the previously unemployed). For a stricter cut (pre-case average earnings above $15,000, representing only 12–15% of the sample), the long-run earnings effect is −$1,426 (8% of the untreated complier mean), significant only at the 10% level, and partly attributable to residual incapacitation (19.6 additional days incarcerated 5–9 years post-filing). For defendants with pre-case earnings below $15,000, incarceration slightly increases long-run employment (2.4 pp, p = 0.01) and earnings ($400, p = 0.03), possibly reflecting rehabilitative benefits (GED or educational programs) for labor-market-detached individuals.

Q9. Does first-time incarceration (extensive-margin exposure) have larger long-run effects than repeat exposure?

The paper tests this by splitting the sample into defendants with and without prior incarceration history. Among defendants with no prior incarceration, the instruments generate large differences in lifetime exposure: a 12-month sentence increases the probability of ever being incarcerated over the next 5–9 years by 26 p.p. (North Carolina) and 41 p.p. (Ohio). Among those not receiving a sentence, 48% (North Carolina) and 19% (Ohio) are eventually incarcerated anyway, implying treatment causes a 52 and 81 p.p. increase in lifetime incarceration probability for extensive-margin compliers. Despite these large differences in lifetime exposure, long-run earnings and employment effects remain small and statistically insignificant in both subsamples. The difference in long-run effects between previously and never incarcerated defendants is not statistically significant (p = 0.29 for employment, p = 0.82 for earnings).

Q10. Are there heterogeneous effects by race, sex, or criminal history?

There is no evidence of long-run scarring for any demographic or criminal history subgroup. Effects for black and non-black defendants are both positive for long-run earnings and employment. Non-black defendants show somewhat larger cumulative losses (consistent with marginally higher counterfactual earnings), but differences are not statistically significant. Estimates for women are imprecise due to small sample size. Among defendants with and without prior felony charges in the four years preceding the case, there are neither economically nor statistically significant long-run earnings or employment effects. Cumulative losses are somewhat larger for defendants without prior felony charges (p = 0.07), reflecting their higher pre-case earnings.

Q11. How does the paper handle potential migration bias in outcomes?

Tax filing and W-2 receipt in the state of sentencing are used to proxy for whether defendants remain in the same state. Among untreated compliers, 88% of those with a tax footprint maintain it in the state of sentencing. No statistically significant effects of incarceration on migration (measured as filing or receiving a W-2 in North Carolina or Ohio) are detected, suggesting prior studies of recidivism measured within-state are unlikely to be severely biased by migration responses.

Q12. What effect does incarceration have on mortality?

Incarceration reduces five-year mortality by approximately 0.8 percentage points (about 20% of the untreated mean). The authors note this is too small to explain the null long-run labor market effects: even if all defendants whose death was averted were employed, removing them from the employment count would reduce the employment effect of a 12-month sentence only to approximately zero.

Q13. How do the paper’s findings compare to prior studies, particularly Mueller-Smith (2015)?

Mueller-Smith (2015) finds large and persistent negative incarceration effects on labor market outcomes in Texas using a structural decomposition and Lasso-based judge-covariate interactions as instruments. The paper argues methodological differences are the likely explanation: the Lasso-selected interacted instruments can be susceptible to many-weak instruments bias toward OLS. It notes that Mueller-Smith’s simpler 2SLS specifications (analogous to those used here) show no statistically significant earnings effects. North Carolina and Ohio are documented to be broadly similar to Texas (and the U.S. average) in rehabilitation program participation, recidivism rates, and incarceration rates, reducing the likelihood that genuine geographic heterogeneity explains the divergence.

Q14. What is the paper’s aggregate extrapolation of incapacitation earnings losses?

Scaling the estimated $2,914 cumulative loss per 12-month sentence by the ratio of days exposed to total days in a year gives a per-day loss of approximately $12. Applied to the 1,435,500 people incarcerated in U.S. prisons on any given day in 2019 (excluding the more than 700,000 in jail), the implied aggregate yearly earnings loss from incapacitation is approximately $6.16 billion.

Key Concepts

Incapacitation effect: The mechanical reduction in earnings and employment that occurs while a defendant is physically confined in prison and unable to work, as distinct from any post-release scarring effect. The paper shows this is the dominant — and essentially sole — causal channel through which incarceration affects labor market outcomes in their sample.

Post-release scarring: Persistent reductions in earnings or employment that persist after a defendant is released from prison, caused by mechanisms such as employer discrimination based on incarceration history, human capital depreciation, loss of job contacts, or psychological discouragement effects. The paper finds no evidence of scarring in either state.

Average Causal Response (ACR): The weighted average of the marginal dose effects of incarceration (e.g., effect of 12 vs. 11 months, 1 vs. 0 months) for groups of defendants whose sentence lengths are shifted by a given instrument. Contrasted with a binary LATE, the ACR averages across the full dosage distribution for compliers.

Complier: An individual whose incarceration sentence is shifted by the instrument — either from zero to some positive sentence (extensive margin) or from a shorter to a longer sentence (intensive margin). Counterfactual outcome means for compliers sentenced to zero months provide the baseline for evaluating effect magnitudes.

Sentencing guideline discontinuity: The discrete jump in permissible punishment types and minimum sentence lengths at specific criminal history score thresholds within North Carolina’s structured sentencing grid. Defendants just above a threshold are more likely to be incarcerated than otherwise similar defendants just below, generating quasi-experimental variation exploited as an instrument.

Leave-out mean judge instrument: In Ohio, each defendant’s assigned judge’s average incarceration sentence length computed over all other cases that judge handles (excluding the defendant’s own case), residualized on court-by-month fixed effects. Because judges are randomly assigned to cases, this measure is conditionally independent of defendant potential outcomes and serves as an instrument for sentence length.

Control complier mean: The estimated mean potential outcome for compliers under the counterfactual of receiving zero months of incarceration. Used as a benchmark to evaluate the magnitude of treatment effects and to characterize how low the earnings baseline is for the population driving the causal estimates.

Extensive vs. intensive margin of incarceration: The extensive margin refers to the binary shift from receiving no prison sentence to receiving any prison sentence; the intensive margin refers to increasing sentence length conditional on some incarceration. The paper argues that neither margin appears to produce long-run labor market scarring, and uses linear programming bounds to estimate that at least 37–45% of compliers in each state are shifted on the extensive margin.

J20 | Macro Paper Warehouse

Artificial intelligence and technological unemployment

Civil War–Induced Displacement and Human Capital

Global Working Hours

In depth

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

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

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

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

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

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

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

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

Q9. What is the paper’s overall interpretation?

Q10. What are the main scope conditions and caveats?

Key concepts

Key concepts

Monopsony Makes Firms Not Only Small but Also Unproductive: Why East Germany Has Not Converged

Layer 1 — Summary

In depth

Q1. What is the core mechanism by which monopsony power reduces aggregate productivity, and how does it differ from the standard “firms are too small” result?

Q2. What empirical patterns do the authors document to link the East-West productivity gap to missing large plants and steeper size-wage curves?

Q3. Why is the steeper size-wage curve specific to East Germany, and why does it persist decades after reunification?

Q4. How is the model structured, and what are the three decision stages for plants?

Q5. Through what two channels does the steeper size-wage trade-off reduce aggregate labor productivity in the model?

Q6. What quantitative predictions does the model make, and how does it perform in untargeted moments?

Q7. What alternative explanations for East Germany’s non-convergence does the paper rule out or place in context?

Q8. How does this paper relate to the Heise and Porzio (2021) finding that plant productivity differences, not worker quality differences, drive the East-West wage gap?

Key Concepts

The Impact of Incarceration on Employment, Earnings, and Tax Filing

Overview

Research Question

Data and Sample

Empirical Strategy

Main Findings

Incapacitation vs. Post-Release Scarring

Pre-existing Labor Market Detachment

Policy Implications

In depth

Q1. What is the exact treatment variable, and what is the counterfactual?

Q2. How are effects interpreted given multiple instruments and continuous treatment?

Q3. How large are the first-stage effects, and how strong is the instrument?

Q4. What evidence supports instrument validity (exclusion restriction and independence)?

Q5. How does the paper test for the incapacitation mechanism against post-release scarring?

Q6. What are the long-run (5–9 years) earnings and employment estimates, and how precisely are null effects ruled out?

Q7. What happens to cumulative earnings over five years despite null long-run level effects?

Q8. Do defendants with stronger pre-case labor market attachment show different long-run patterns?

Q9. Does first-time incarceration (extensive-margin exposure) have larger long-run effects than repeat exposure?

Q10. Are there heterogeneous effects by race, sex, or criminal history?

Q11. How does the paper handle potential migration bias in outcomes?

Q12. What effect does incarceration have on mortality?

Q13. How do the paper’s findings compare to prior studies, particularly Mueller-Smith (2015)?

Q14. What is the paper’s aggregate extrapolation of incapacitation earnings losses?

Key Concepts