Journal of Economic Growth | Macro Paper Warehouse

Armed conflict exposure and trust: evidence from a natural experiment

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

This paper asks how individual-level exposure to internal armed conflict shapes social capital, specifically trust in institutions and trust in people. The question matters because trust is a core component of social capital that underpins cooperation, economic growth, financial development, political participation, and post-conflict recovery; yet the empirical literature is split between studies finding conflict erodes trust and studies finding “post-traumatic growth” that enhances pro-sociality. The authors argue prior work cannot cleanly identify causal effects because of non-random selection into exposure, attrition from migration/death, and confounding conflict-induced changes in the socio-economic environment.

The empirical strategy exploits a natural experiment in Turkey: mandatory conscription assigns every male citizen, via a lottery, to a military base, and a significant share are randomly sent to bases in the eastern/south-eastern conflict zone where the state has fought the PKK since 1984. By sampling ex-recruits who live in peaceful western districts, exposure during military service is the respondents’ only personal contact with the conflict, isolating individual-level effects from environmental confounds. Data come from a field survey of 5,024 randomly selected adult males in 29 western districts in summer/fall 2019 (response rate 83%); eligible men had completed service between 1984 and 2014. Only 5 respondents did not answer the military-service questions.

Two exposure measures are built. ACE (Exposure to Armed Conflict Environment) is the standardized number of combatant casualties in the county and during the period of a respondent’s service, drawn from the Turkish State-PKK Conflict Event Database; its variation comes from four exogenous components (birthdate-driven timing, regulation-driven duration, clash intensity, and lottery-assigned location). TDE (Traumatic Direct Experiences) is a binary indicator equal to 1 if the respondent was wounded in armed clashes or had someone around them killed/hurt; 2% reported being wounded and 15% reported others around them killed or hurt. ACE and TDE correlate only 0.25. Two trust outcomes: Institutional Trust (average of 14 five-point items: army, judiciary, parliament, TV, newspapers, parties, clergy, universities, environmental orgs, charities, police, banks, private companies, EU) and Social Trust (trust in unfamiliar people / strangers). The army was the most trusted institution (~75% high trust vs. 43% for courts, 35% for parliament). Estimation is OLS with age, education, and minority controls, standard errors clustered at the living-block level.

Main findings: the two exposure types have opposing effects. In the preferred specification including both measures, ACE raises Institutional Trust (about 0.02, significant at 5%) and Social Trust (about 0.03, significant at 5%), while TDE lowers Institutional Trust (about -0.15, 5%) and Social Trust (about -0.11, 1%). ACE is insignificant when TDE is omitted because it then pools traumatized and non-traumatized recruits, biasing it toward zero. There is no significant ACE-by-TDE interaction, so the negative trauma effect is independent of conflict intensity. Effects are similar in sign and magnitude across both trust dimensions, indicating an encompassing change rather than institution-specific distrust. Interactions with time-since-service are insignificant, implying the effects are permanent.

Mechanism: the authors invoke Janoff-Bulman’s (1992) “shattered assumptions” theory. TDE is positively associated with depression and insecurity indexes, which in turn correlate negatively with both trust measures; ACE is not significantly related to depression/insecurity. There is no significant relationship between exposure and trust in the army, ruling out an accountability mechanism. Heterogeneity by in-group: TDE raises trust in family (coping mechanism) but, like strangers, friends show positive ACE and (insignificant) negative TDE effects, arguing against parochialism as the main driver. Implications: distinguish contextual from direct exposure; design psychological recovery programs for veterans; estimates are likely conservative given the limited 6-18 month exposure window.

In depth

Q1. What is the identification strategy and what are the main threats to it?

Identification relies on Turkey’s conscription lottery, which randomly assigns drafted men to military bases, a significant share of which lie in the eastern/south-eastern conflict zone. Because the sample is drawn only from peaceful western districts, service is the respondents’ sole exposure to the conflict, isolating individual-level effects from conflict-induced changes in the socio-economic environment. ACE’s variation comes from four exogenous components: birthdate-driven timing of service, regulation-driven service duration (18 months in the 80s, 15 in 1992, 18 in 1995, 15 in 2003, 12 in 2014), clash intensity around the base, and lottery-assigned location. Threats: (1) non-random base assignment - addressed by balance tests (Table 2) showing no systematic differences in age, ethnicity, or height by conflict-zone assignment; education differs because college graduates are slightly skewed toward western bases (40% of non-college-grads served in the east vs. 30% of college grads), but the difference vanishes when college graduates (9.3% of sample) are excluded, education is controlled in all specs, and a no-college-grad sample (Table A2) is robust; (2) self-selection into dangerous tasks/violence for TDE - addressed by the fact that task assignments are made by command at the start of service before behavior is observed, and Table 3 balance tests show wounded vs. non-wounded respondents do not differ on pre-military characteristics; an alternative TDE (observing a fellow soldier hurt/killed, immune to own risk-taking) yields similar results (Table A1).

Q2. What are the main mechanisms and how are they distinguished empirically?

The proposed mechanism is a transformation of fundamental world assumptions (benevolence, meaning, safety of the world) per Janoff-Bulman (1992). Distinguishing tests: (1) TDE affects a broad range of trust dimensions but is NOT significantly related to trust in the army, ruling out an accountability interpretation (which would predict distrust concentrated on state security institutions) and a comradeship interpretation (which would predict effects only on social trust). (2) TDE is positively and significantly associated with depression and insecurity indexes (Tables 7-8), and these indexes are themselves negatively and significantly related to both trust measures, consistent with shattered world assumptions. (3) ACE is not significantly associated with depression/insecurity; the authors note these scales are worded to detect negative states and may miss the positive feelings ACE could elicit, and that indirect environmental exposure plausibly has weaker effects on fundamental beliefs than direct trauma.

Q3. What heterogeneity is documented?

The central heterogeneity is by exposure type: contextual exposure (ACE) raises trust, direct trauma (TDE) lowers it. No significant ACE-by-TDE interaction, so trauma’s effect does not depend on conflict intensity. No significant moderation by time since service (Table 6), implying permanent effects. In-group heterogeneity (Table 9, ordered logit): TDE significantly raises trust in family (coefficient 0.26, 5%), interpreted as a coping mechanism of retreating to closest networks; trust in friends shows positive ACE (0.07, 5%) and negative but insignificant TDE, mirroring the stranger result. The similar pattern for strangers and friends argues against parochialism as the primary driver.

Q4. What robustness checks are run?

(1) Alternative TDE defined as observing a fellow soldier hurt/killed, more immune to own risk-taking (Table A1) - results unchanged. (2) Excluding college graduates (Table A2) - results unchanged. (3) Tobit specification accounting for the censored nature of trust measures (Table A3) - similar results. (4) Including a conflict-zone dummy and base-district fixed effects (Tables A4-A5) to absorb unobserved location heterogeneity (though the authors note these likely absorb part of the ACE variation, so they are not in the baseline). (5) Separate results for each of the 14 institutional-trust dimensions (Table A6) and excluding one dimension at a time from the composite index - results stable. (6) Alternative standard-error clustering at home-district or region levels - unchanged.

It builds on the draft-lottery natural-experiment tradition (Angrist 1990 on Vietnam; Angrist-Chen 2011; Galiani et al. 2011; Grossman et al. 2015) and the conflict-and-social-capital literature (Rohner et al. 2013; Cassar et al. 2013; Bauer et al. 2016; Kijewski-Freitag 2018). It differs by: (1) cleanly identifying causal effects free of environmental confounds, since trust is measured in untouched western locations rather than in transformed post-conflict settings; (2) carefully separating contextual from direct exposure, which many studies cannot; (3) proposing a novel individual-level psychological mechanism (shattered world assumptions) rather than the economic/institutional-legacy channels (Besley-Reynal-Querol 2014; Nunn-Wantchekon 2011; Grosjean 2014) or the inter-group-competition/parochialism explanation (Bauer et al. 2016). The authors argue the heterogeneity they document can help reconcile the conflicting positive and negative findings in prior literature - prior ‘pro-social’ effects may reflect coping-driven re-creation of safe social space (consistent with Grosjean’s (2014) ‘dark nature’ of conflict-induced pro-sociality), not genuine restoration of trust.

Q6. What are the policy implications and their scope conditions?

Two main implications: (1) researchers and policy advisers should carefully distinguish contextual from direct conflict exposure when studying behavioral outcomes; (2) the findings inform the design of psychological and social recovery programs for combat veterans and victimized post-conflict populations. Scope conditions: the study is specific to the Turkish conflict setting and limited to male ex-combatants; it remains open whether effects generalize to women, civilians, or other countries. Because exposure lasted only a pre-determined 6-18 months after which recruits returned to peaceful lives, the authors argue estimates are conservative relative to populations living in protracted conflict environments.

Q7. What additional findings or caveats are noted?

The authors report (results not shown) that individuals with traumatic experiences are more likely to participate in political organizations, and cite Kibris-Nelson (2021) that such individuals are more likely to start their own businesses (while being less successful at it), consistent with coping strategies of creating a controllable environment. They concede the mechanism evidence for the positive ACE effect is ‘somewhat less clear’ than for TDE, and offer an alternative possibility that whether intense-environment survival raises trust may be moderated by how heroically the veteran’s social network views his service. The depression subscale is the 6-item Brief Symptoms Inventory; insecurity is an 8-item scale. Roughly 6.5 million of the 15 million men drafted since 1984 are estimated to have served in the conflict zone.

Key Concepts

Exposure to Armed Conflict Environment (ACE): A standardized, individual-specific measure of contextual conflict exposure equal to the number of combatant casualties in the county and during the time period of a respondent’s military service. It captures immersion in the conflict environment with high geo-temporal precision and is treated as exogenous because its components (birthdate-driven timing, regulation-driven duration, clash intensity, lottery-assigned location) are outside the individual’s control.

Traumatic Direct Experiences (TDE): A binary indicator equal to 1 if a respondent was personally wounded in armed clashes or had someone around them killed or hurt during military service. It captures direct, personal experience of violence as distinct from mere presence in a conflict environment; in the sample 2% were wounded and 15% had others around them hurt/killed.

Institutional Trust: In the paper’s sense, the simple average of a respondent’s 5-point Likert trust ratings across 14 public and private organizations (army, judiciary, parliament, media, parties, clergy, universities, environmental orgs, charities, police, banks, private companies, EU) - deliberately broad so as not to over-weight state institutions directly tied to the conflict.

Social Trust: A generalized form of trust measured by how much a respondent trusts people they are not familiar with (strangers), rather than the vaguer ‘most people’ wording, chosen to minimize in-group/out-group and ethnic associations and isolate generalized trust in others.

Shattered assumptions: The paper’s operative mechanism, drawn from Janoff-Bulman (1992): people hold core assumptions that the world is benevolent, meaningful, and safe; traumatizing experiences shatter these positive assumptions, eroding deeply rooted trust - whereas surviving a dangerous environment without mishap can instead reinforce them. Trust, depression, and insecurity are treated as observable implications of these otherwise-unobservable world assumptions.

Parochialism / parochial altruism: The rival hypothesis (associated with Bauer et al. 2016) that conflict exposure increases in-group favoritism while eroding out-group trust. The paper tests and largely rejects it as the primary driver because ACE raises trust in both strangers and friends and the in-group (family) pattern does not match parochial predictions.

Manipulation of information in times of crisis: evidence from Covid excess mortality

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

Karlinsky and Shayo ask which governments manipulate public information, in which direction, and by how much — questions that are normally intractable because the ground truth is unobservable. The Covid-19 pandemic supplies an unusual opportunity: all countries faced a broadly similar crisis simultaneously, and all-cause mortality — collected by national statistical offices as a routine bureaucratic function independently of Covid — provides a manipulation-resistant benchmark against which officially-reported Covid deaths can be evaluated.

The authors hand-collect all-cause mortality data for 134 countries and territories from national statistical offices, population registries, health ministries, and, in some cases, right-to-information requests facilitated by local journalists. Data span 2015–2021 at weekly, monthly, or annual frequency. Their sample covers 93 percent of countries with at least 75 percent Death Registration Completeness. They compute, for each country, a Misreporting Rate (MRR) defined as estimated Covid deaths minus officially reported Covid deaths, normalised by expected total deaths derived from pre-pandemic trends. Estimated Covid deaths equal excess mortality — itself estimated from a country-specific model with weekly/monthly fixed effects and an annual trend (R² = 0.997 in pre-pandemic prediction) — minus adjustments for excess deaths attributable to conflicts, natural disasters, and other identifiable non-Covid causes. Those adjustments are small: the mean total adjustment across the sample is 0.04 percent of expected deaths.

Six main findings emerge. First, between 45 and 55 percent of the 134 countries misreported Covid deaths. Second, the direction of manipulation is overwhelmingly one-sided: of 131 countries with sufficient data to estimate confidence intervals, 59 reported accurately, 62 significantly underreported, and only 10 overreported. The theoretical prediction that governments might exaggerate a crisis — to rally populations, legitimise repressive measures, or attract foreign aid — finds no empirical support. Third, the magnitude of underreporting is large: the sample reported 5.08 million Covid deaths in 2020–2021 while estimated actual Covid deaths were 12.47 million, nearly 2.5 times the official figure; the implied global MRR is 12.8 percent. Among the 62 underreporting countries, the average MRR is 14.5 percent of expected total deaths and the median is 12 percent. Individual-country MRRs range from above 37 percent (Bolivia, Nicaragua) downward, with Russia at 24 percent. Fourth, state capacity in counting and registering deaths explains some but far from most cross-country variation; the R² of the best capacity-only regression is 0.115. Chile and Russia have virtually identical Death Registration Completeness and Percent Well-Certified Death Registrations, yet Chile accurately reported while Russia’s MRR is 24 percent. Fifth, the extent of underreporting is strongly associated with constraints on governmental power. In individual regressions conditioning on capacity, each of three institutional constraint measures — Clean Elections, Executive Constraints, and Freedom of the Press — is associated with a 0.4–0.5 standard deviation lower MRR per one standard deviation stronger constraint. In a joint model including all 12 factors from four domains (macroeconomic incentives, culture, audience sophistication, institutions), institutional constraints are the strongest predictor (partial R² ≈ 0.11), followed by audience sophistication (partial R² ≈ 0.04–0.06). Macroeconomic incentives — tourism reliance, unemployment, foreign direct investment — are not jointly significant. Cultural factors (trust, individualism, religiosity) lose significance once other factors are controlled. The full model explains more than 50 percent of MRR variation. Sixth, countries with a communist legacy (defined as having had a communist or socialist regime for at least 10 years, covering 34 countries) show significantly higher misreporting even holding current institutional and cultural conditions constant. Countries that held elections during 2020–2021 also show significantly higher misreporting.

The results are robust to alternative expected-mortality models, alternative MRR normalisations, the inclusion of Bangladesh, China, and Indonesia (treated separately due to data quality concerns), year-by-year (2020 vs. 2021) splits, controls for age structure and GDP per capita, and alternative manipulation measures (underdispersion, Benford’s law deviations). The evidence that manipulation cannot be attributed to varying standards for false-positive attribution of cause of death is direct: four pre-pandemic measures of a country’s tendency to use unspecified cause-of-death categories are uncorrelated with MRR and individually account for less than 1 percent of its variation.

The paper’s contribution to the economics of information manipulation is methodological as well as empirical: it provides a comparable, country-level measure of governmental misinformation based on actual observable actions regarding a policy issue of central importance, covering a large and diverse cross-section of countries.

In depth

Q1. What is the identification strategy and what are the main threats to it?

The strategy compares officially-reported Covid deaths (the variable that attracted political attention and over which governments had strong incentives and ability to intervene) with estimated Covid deaths derived from excess all-cause mortality (a statistic collected routinely by national bureaucracies under very different incentive structures, harder to manipulate, and less visible publicly during the pandemic). The identifying assumption is that all-cause mortality data are not themselves systematically manipulated in response to Covid. The authors defend this on four grounds: (1) all-cause mortality has long been collected independently of Covid; (2) ascertaining that someone died is far easier than attributing a cause of death; (3) Covid figures attracted vastly more public attention, making their manipulation more urgent; (4) when governments appear to have discovered the evidential value of excess mortality, their response has been to delay publication of all-cause data rather than to alter it (Belarus is cited as an example). The main remaining threat is that the adjustment for non-Covid excess deaths (conflicts, disasters, traffic accidents, suicides, homicides) is imperfect in countries with poor data on those causes. The authors note this caveat but show mean adjustments are tiny (0.04% of expected deaths) and the largest individual adjustments (Armenia 6.1%, Azerbaijan 3.2%) are driven by the Nagorno-Karabakh war and are handled explicitly.

Q2. How is excess mortality estimated, and how sensitive are the results to modelling choices?

Country-specific models are estimated using 2015–2019 all-cause mortality data, including country-specific weekly or monthly fixed effects and a country-specific annual trend to capture seasonality and long-run factors (population ageing, improvements in health care, etc.). The model achieves R² = 0.997 in predicting pre-pandemic mortality. The authors report in Supplementary Material B that alternative expected-mortality approaches from the literature yield very similar results, as do alternative normalisations of the MRR. Sensitivity to model choice is low because the discrepancies between excess and reported deaths in weak-institution countries are so large that they persist across methodological variants.

Q3. How do the authors distinguish intentional manipulation from limited state capacity?

They use two pre-pandemic, capacity-specific measures: (1) Death Registration Completeness (DRC) — the share of deaths captured by the vital registration system — and (2) Percent of Well-Certified Death Registrations (PWC) — the share with proper cause-of-death attribution. Both are computed before the pandemic so they are not contaminated by Covid-era behaviour. Regressions confirm that capacity predicts MRR negatively (R² up to 0.115), but the residual variation remains large. The clearest illustration is Chile vs. Russia: both have complete DRC and near-identical high PWC, yet Chile reports accurately and Russia has an MRR of 24 percent. All subsequent analysis of correlates conditions on these capacity measures.

Q4. How do the authors rule out the possibility that differences in false-positive aversion (rather than manipulation) explain MRR variation?

They construct four pre-pandemic measures from WHO Mortality Database ICD-10 cause-of-death data: (1) number of ICD codes reported; (2) share of specific-viral deaths among all viral deaths; (3) share of specific-infection deaths among all infection deaths; (4) share of specific-respiratory deaths among all respiratory deaths. A country more averse to false positives would report less specific causes. None of the four measures is significantly associated with MRR, and none accounts for more than 1 percent of its variation. This rules out differences in diagnostic/reporting standards as a driver of the observed discrepancies.

Q5. What is the direction of manipulation and what does this imply for theories of governmental information behaviour?

Of 131 countries with estimable confidence intervals, 62 significantly underreported and only 10 overreported. The four main theoretical channels for overreporting — rally-around-the-flag effects, legitimising repression, attracting foreign aid, and inducing flight-to-safety compliance — find no empirical support. The authors argue that the rally-around-the-flag mechanism requires an outgroup-related threat (Covid, unlike a foreign military attack, was not easily framed this way), that Covid mortality does not signal repressive capacity, and that international economic actors appear sufficiently sophisticated to be sceptical of inflated figures. The pattern is consistent instead with governments downplaying to project competence, reduce accountability, and justify inadequate responses.

Q6. What factors are most strongly associated with misreporting, and how are they ranked?

In joint regressions with all 12 factors from four domains, after conditioning on capacity: (1) Institutional constraints (Clean Elections, Executive Constraints, Freedom of the Press) have the highest partial R² (approximately 0.11 for Executive Constraints alone) and are jointly significant at p < 0.001; each standard deviation of stronger institutional constraint is associated with roughly 0.4–0.5 standard deviations lower MRR. (2) Audience Sophistication (tertiary education, HDI Education Index, internet access) is the second strongest domain (partial R² in the range of 0.04–0.06 per variable; jointly significant at p < 0.05). (3) Cultural factors (trust, individualism, religiosity) are individually significant in bivariate regressions but lose significance when institutional and other factors are controlled. (4) Macroeconomic incentives (tourism, unemployment, net FDI) are not jointly significant in any specification. Specification-curve analysis across all combinations of controls confirms that Executive Constraints is the single most robust predictor, retaining sign, magnitude, and significance across all models. The full model (Table 4, column 1) has R² exceeding 0.50.

Q7. What is the communist legacy finding and how is it interpreted?

Countries defined as having had a communist or socialist regime for at least 10 years (34 countries) show significantly higher MRRs even after conditioning on contemporary institutional constraints, audience sophistication, culture, and capacity. The coefficient is statistically significant at p < 0.05 or better in the main and most robustness specifications. The authors point to Harrison (2017) on the pervasiveness of information manipulation in communist states as a historical precedent, and interpret the finding as a persistent legacy operating through channels not fully captured by current measures. This suggests that historical exposure to a political culture of systematic information manipulation may have durable effects on bureaucratic behaviour or political norms that current V-Dem indices do not fully absorb.

Q8. What is the elections finding?

Countries holding national parliamentary or presidential elections during 2020–2021 (76 of 134 countries) show significantly higher misreporting, consistent with electoral incentive theories of information manipulation. This finding is robust to including controls for GDP per capita, population age structure, and other domains, and is stable across the 2020-only and 2021-only sub-samples.

Q9. What robustness checks are performed?

The authors conduct: (1) specification-curve analysis across all combinations of covariates; (2) a joint model with all 12 individual factors; (3) principal component analysis within each domain to recover common variation and reduce dependence on specific measurement choices; (4) alternative expected-mortality models (Supplementary Material B.1); (5) alternative MRR normalisations (Supplementary Material B.2); (6) separate year-by-year analysis for 2020 and 2021; (7) inclusion of Bangladesh, China, and Indonesia as robustness cases despite lower data reliability; (8) addition of GDP per capita to check whether the institution-misreporting link is proxying for development; (9) analysis using underdispersion (Kobak 2022) and Benford’s law deviations as alternative manipulation measures; (10) exploration of colonial legacy as an additional historical variable (no significant effect found). The primacy of institutional constraints is robust across all of these.

Q10. How do the authors treat China, Bangladesh, and Indonesia?

These three large countries are excluded from the main analysis because their all-cause mortality data come from surveys (Bangladesh, China) rather than vital registration systems, or are very incomplete (Indonesia), making excess mortality estimation unreliable. They are included in a robustness regression (Table 4, column 6) and results are described as qualitatively similar. The authors flag that China’s data may itself be informative as a potential indicator of data suppression.

Q11. How does this paper relate to and differ from prior work?

The paper is closest in spirit to Olken (2007), who uses the gap between reported and actual infrastructure spending to measure corruption, and Martinez (2022), who compares GDP growth to night-time-light-implied growth and finds autocracies overstate growth by more than a third. The authors extend this approach to a different domain (health/mortality) with broader country coverage. Prior Covid-specific work documented anomalies — underdispersion (Kobak 2022) and Benford’s law deviations (Kapoor et al. 2020; Kilani 2021) — and noted that autocratic regimes reported lower-than-expected deaths (Annaka 2021; Cassan and Van Steenvoort 2021), but these studies relied on regime type as the sole or primary explanatory variable and did not systematically rank competing factors. Neumayer and Plümper (2022) and Wigley (2024) used the authors’ own World Mortality Dataset to test data manipulation. This paper is distinctive in that it: (a) provides what the authors describe as the most systematic estimates to date of Covid mortality and misreporting; (b) examines a broad range of factors across four domains without a priori privileging any; (c) directly tests and rejects capacity and false-positive aversion as alternative explanations; and (d) identifies communist legacy and elections as additional significant correlates.

Q12. What are the policy implications and their scope conditions?

Three implications are highlighted. First, unconstrained regimes appear to manipulate not only economic statistics but also health information during the most salient public policy event of the era; travel restrictions and multilateral actions during the pandemic relied on reported Covid figures, so manipulation had direct international externalities. This raises broader questions about the credibility of official data from such governments across domains — foreign aid targeting, climate action, vaccination campaigns. Second, the MRR provides a comparable cross-country measure of institutional quality grounded in actual governmental behaviour, potentially useful as an input to studies of institutions, conflict, electoral outcomes, and economic performance. Third, some countries that score respectably on conventional executive constraint indices — Albania, El Salvador, India, Serbia — show high MRRs, suggesting these rates may be leading indicators of democratic erosion not yet captured by standard measures. The scope condition the authors flag is external validity: if pandemic mortality is an extreme case with unique incentive structures (tourism, investment, aid eligibility), then findings about determinants of manipulation may not generalise beyond crisis settings. The authors argue against this interpretation on the grounds that macroeconomic factors — which would be pandemic-specific — are not significant, while institutional constraints — which reflect general governmental behaviour — are.

Q13. What limitations do the authors acknowledge?

First, the analysis is explicitly descriptive rather than causal; factors are correlates, not proven determinants. Second, the MRR may understate true manipulation if all-cause mortality data are themselves selectively withheld or manipulated; the authors argue this is probably modest but acknowledge it cannot be fully ruled out. Third, important large countries — Pakistan, Nigeria, Ethiopia, Venezuela — cannot be scored because sufficient all-cause mortality data are not publicly available; the authors note this absence may itself be informative but cannot be quantified. Fourth, data on other causes of excess deaths (traffic accidents, suicides, homicides) are patchy in many countries, though the scale of these adjustments is very small. Fifth, some capacity controls (PWC) use data from as early as 2003, introducing measurement error. The paper does not claim to fully separate the channels through which institutions reduce manipulation (electoral accountability, press scrutiny, judicial oversight, professional agency independence), treating them as joint constraints rather than separately identified mechanisms.

Key Concepts

Misreporting Rate (MRR): The paper’s central measure, defined as (estimated Covid deaths minus officially reported Covid deaths) divided by expected total deaths for the country in the same period based on pre-pandemic trends. A positive MRR indicates underreporting; a negative MRR indicates overreporting. Normalising by expected total deaths rather than by reported Covid deaths accounts for differences in population size, age structure, and baseline mortality across countries.

Excess mortality: The number of deaths above and beyond what would have been expected in the absence of the pandemic, estimated from country-specific models with weekly or monthly fixed effects and an annual trend fitted to 2015–2019 data. Used as the primary building block for estimated Covid deaths after subtracting excess deaths due to identified non-Covid causes (conflict, natural disasters, traffic accidents, homicides, suicides).

Death Registration Completeness (DRC): In this paper’s usage, the share of all deaths in a country captured by its vital registration system each year, measured using pre-pandemic data. Treated as the most basic indicator of a country’s capacity to count deaths. Used as a control to separate capacity constraints from intentional manipulation.

Percent of Well-Certified Death Registrations (PWC): The share of death certificates in a country that carry a properly specified cause of death, measured using pre-pandemic data. Used alongside DRC as a second capacity control capturing not just whether deaths are registered but whether causes are correctly attributed.

Informational Autocrat: Following Guriev and Treisman (2022), the paper uses this concept to describe executives in countries where formal and informal checks and balances are weak, who systematically manipulate public information to project competence and reduce accountability. The paper’s empirical results are interpreted as evidence that such executives behave as informational autocrats not only in economic statistics but also in health data.

False-positive aversion: The tendency of some countries to apply a higher evidentiary bar before attributing a death to a specific cause — such as Covid — rather than leaving the cause unspecified, independently of capacity or intention to deceive. The paper operationalises this using pre-pandemic ICD-10 data on specificity of reported causes of death and shows it is uncorrelated with MRR, ruling it out as a driver of observed discrepancies.

Communist legacy: The paper’s binary indicator for countries that had a communist or socialist regime for at least 10 consecutive years (34 countries). The variable captures historical exposure to a political culture of systematic information manipulation and is found to be a significant positive predictor of MRR even after conditioning on current institutional constraints, consistent with persistent norms or bureaucratic practices.

Property rights, fiscal capacity, and social capacity: The lasting impact of the Taiping Rebellion

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

Research question and motivation: How do civil wars affect long-term development, and through which institutional mechanisms? The paper studies the Taiping Rebellion (1850-1864) in Qing China, one of history’s deadliest civil wars (at least ~20 million deaths, with some estimates of 70-100 million), as a critical juncture in China’s path to modernity. It matters because the rebellion generated large, persistent regional institutional variation that can help explain what the authors call the “Intra-China Divergence” — regional GDP-per-capita gaps as large as 27-to-1 (Dongguan vs. Tianshui, 2010) that rival the world’s largest inter-regional gaps.

Data and design: A prefecture-level (occasionally county-level) panel covering 266 prefectures in China proper (1820 delineation). 55 prefectures fell under Taiping control (treatment) — split into 37 “Early Taiping” prefectures (occupied up to 1859, in Anhui/Jiangxi/Hubei, ambiguous land rights) and 18 “Late Taiping” prefectures (occupied from 1860, in Jiangsu/Zhejiang, stronger land rights) — and 211 control prefectures. Population is observed at seven points (1820, 1851, 1880, 1910, 1953, 1982, 2000). The core strategy is difference-in-differences (1820 reference year, prefecture and year fixed effects), supplemented by propensity-score matching (135-prefecture matched sample), a spatial autoregressive (SAR) model, and an instrumental-variable strategy using the longitude of the prefectural seat (motivated by the Taiping Navy’s eastward-along-the-Yangtze military strategy; first-stage F-statistics above 20).

Main quantitative findings (with scope conditions): (1) Population: The rebellion caused large, permanent population losses. The Taiping DID coefficient is -0.45 in 1880 (a 36% lower population growth rate vs. control) and -0.51 in 1953 (40% lower) — no convergence. Crucially, in the matched sample Late Taiping areas recovered (no significant long-run population gap vs. control) while Early Taiping areas did not (an immediate ~30% drop in 1880 plus further decline). (2) Property rights: In 1915 county data, the idle-land share is 3.6 percentage points higher in Early Taiping than control counties, while Late Taiping is not significantly different from control — supporting the property-rights hypothesis. (3) Fiscal capacity (likin): Taiping areas collected ~12 times (e^2.5) as much likin per 1,000 sq km as control areas in 1869-1879, still 3.7 times as much in 1922-1925. Late Taiping areas had even higher intensity (22.2x in 1869-1879; 6.1x in 1922-1925) than Early Taiping (9.0x; 2.7x). (4) Social capacity (charities): On average the rebellion had no significant effect, but Late Taiping areas saw charity growth ~56 percentage points (44 log points) above control by 1880, rising to ~78 percentage points (58 log points) by mid-20th century. (5) Long-term development: Driven entirely by Late Taiping areas — 1982 agricultural+industrial output per capita 90% higher (64 log points), 2010 GDP per capita 87% higher (63 log points), and 2010 fiscal revenue per capita 203% higher (111 log points) than control; Early Taiping is statistically indistinguishable from control. Late Taiping counties also show higher post-1895 industrial firm entry. (6) Civic outcomes and resilience: Using CGSS 2010, Late Taiping residents show higher trust in personal networks and greater civic engagement (political attention, local participation). During the Great Famine (1959-1961), Taiping areas had 6.9% larger survivor cohorts; the effect is 28% stronger in Late Taiping (8.4%) than Early Taiping (6.5%).

Implications: Violent conflict can leave lasting positive institutional imprints — through property rights, decentralized local fiscal capacity (“war made the state” at the local level), and elite-led social capacity — conditional on favorable initial conditions (strong gentry, wealthier commercial regions). The authors argue cultivating civil society and social capacity could yield large payoffs given China’s strong-state/weak-society configuration.

In depth

Q1. What is the core identification strategy and what are the main threats to it?

The baseline is a difference-in-differences comparing Taiping vs. control prefectures over 1820-2000, with prefecture and year fixed effects and 1820 as the reference year. Identification rests on parallel pre-trends: the Taiping coefficient in 1851 (pre-rebellion) is small and insignificant, indicating no differential selection conditional on controls. The main threats are: (i) the binary Taiping measure aligning with provincial boundaries and picking up broad regional dynamics; (ii) control-group contamination because some control prefectures were temporarily conquered (but not governed) by the Taiping Army; (iii) spatial spillovers between neighbors (Tobler’s law / Kelly 2019 critique); (iv) omitted subsequent historical events; and (v) omitted variables differing systematically between treated and control areas. The authors address these with dosage measures (battles, occupation months), matching, a SAR model, an IV (longitude), explicit controls for the Taiping conquest, an adjacent-treatment indicator, leave-one-province-out checks, and controls for many other historical events.

Q2. How does the instrumental-variable strategy work and why might longitude be valid?

Longitude of the prefectural seat instruments for the Taiping dummy. Relevance: the Taiping leaders’ July 1852 military plan was to march eastward along the Yangtze, capture Jiangning (Nanjing), and expand from there using their dominant navy — so eastern (higher-longitude) prefectures were far more likely to fall under Taiping rule (Table 1 confirms Taiping prefectures have significantly larger longitudes; first-stage F-statistics above 20, Shea’s partial R-squared above 0.1). Exclusion: prefecture fixed effects absorb time-invariant geographic advantages, and year-dummy interactions with key geography (distances to coastline, Grand Canal, Yangtze) allow flexible time-varying geographic effects; conditional on these, longitude is argued to be excludable. IV estimates are larger in magnitude than OLS but qualitatively confirm a persistent negative population effect (robust to Anderson-Rubin weak-IV inference). The authors caution that omitted determinants correlated with longitude cannot be fully ruled out.

Q3. What are the four hypotheses and how are they distinguished empirically?

(1) Property-rights hypothesis: Late Taiping areas (post-1860 ‘direct tenant payment’ system creating de facto/de jure tenant ownership) had better-defined land rights than Early Taiping areas (collapsed landlord system, lost deeds, anti-rent movements), so should have less idle land and faster population recovery — tested via the 1915 idle-land cross-section and the Early-vs-Late population DID. (2) Likin-as-fiscal-capacity hypothesis: Qing fiscal decentralization and the likin tax (introduced 1853) strengthened local fiscal capacity, persistently higher in Taiping (especially Late Taiping) areas — tested via the likin-intensity DID. (3) Social-change hypothesis: elite-led militias and reconstruction spurred charities (‘benevolent halls’/shantang) as bridging social capital, especially in Late Taiping areas — tested via charity-stock DID and by adding charities as a mediator in long-term regressions. (4) Social-cohesion-and-civic-engagement hypothesis: forged social capital persists, raising modern trust/civic engagement and reducing Great Famine deaths — tested via CGSS 2010 and famine-survivor cohort ratios.

Q4. What heterogeneity is documented?

The central heterogeneity is Early vs. Late Taiping. Early Taiping areas (Anhui/Jiangxi/Hubei) suffered permanent population loss, higher idle land (+3.6pp), only modest likin gains, no charity growth, no long-term development advantage, and weaker famine resilience. Late Taiping areas (Jiangsu/Zhejiang) recovered population, had no excess idle land, far higher likin intensity (22x early period), large charity growth (+56 to +78pp), strong long-term development gains (90%/87%/203% in output/GDP/fiscal revenue), higher modern trust and civic engagement, and the strongest famine resilience (8.4% vs 6.5%). Industrialization heterogeneity is also temporal: no Early/Late firm-entry difference before 1895, but after the 1895 Treaty of Shimonoseki liberalized private industry, Late Taiping counties had more entry and Early Taiping fewer.

Q5. What robustness checks are run?

For the population results: dosage interactions (log battles, log occupation months); excluding six most-intense-fighting prefectures (Wuchang, Songjiang, Anqing, Jiangning, Suzhou, Hangzhou); controlling for newly selected jinshi (civil-service quota channel); a SAR spatial model (after Pesaran cross-sectional-dependence tests); PSM matched sample; longitude IV with Anderson-Rubin inference; controls for seven other historical events (Guangxu Drought, Hui Revolt, Nian Rebellion, early-Republic conflicts, Sino-Japanese War, Chinese Civil War, missionary activity); explicit controls for Taiping conquest vs. regime; an adjacent-treatment indicator (Butts 2021) for spillovers; and leave-one-province-out exclusion. Long-term development results add SAR, matching, historical-event controls including the Cultural Revolution, and an ‘intermediate-term’ 1930s industrialization check. Famine results are robust to alternative famine-severity measures, SAR, matching, and historical-event controls.

Q6. How is the mediation analysis handled and what does it show?

The authors add likin intensity (1880) and average charities (1880-1941) to cross-sectional long-term regressions, explicitly flagging these as endogenous ‘bad controls’ (Angrist-Pischke 2009; Imai et al. 2011) to be interpreted cautiously as descriptive mediation. Findings: a one-SD increase in likin intensity is associated with +1.7pp middle-school completion, +4.8pp literacy, +5.3% schooling, and +12.2% (11.5 log points) GDP per capita in 2010. A one-SD increase in charities is associated with +15% 1982 output, +20% 2010 GDP, and +55% 2010 fiscal revenue per capita. Once charities are netted out, Late Taiping advantages in output, GDP, and fiscal revenue are attenuated by about 17%, 14%, and 22% respectively — highlighting the social-capacity channel.

Q7. How does the Great Famine resilience result connect to the rebellion?

Famine severity is measured by ‘Famine Control’ = ratio of cohort size born during the famine (1959-1961) to cohort size born pre-famine (1954-1957) from the 1990 census 1% sample (higher = less severe). Taiping areas had a 6.9% larger survivor cohort than non-Taiping; the effect is 8.4% in Late Taiping vs. 6.5% in Early Taiping. Back-of-envelope, the Late Taiping experience would have ‘saved’ ~31,374 people in an average prefecture (17% of the 1959-1961 cohort) vs. ~24,145 (13%) for Early Taiping. Controlling for political radicalism (reverse party-member density, -1*PMD, after Yang 1996) does not change the result. The mechanism: higher social capital made local officials more sympathetic/less radical in grain procurement and citizens better able to act collectively (paralleling Cao-Xu-Zhang 2022 on clan density and Hu-Yao-You 2023 on home-county officials).

Prior Taiping studies examined narrower consequences: civil-service exam quotas (Li 2014), demographic and industrialization effects (Li and Ma 2016), migration and public goods (Hao and Xue 2017), and late-Qing power distribution (Bai, Jia, and Yang 2023). None addressed the rebellion’s enduring impacts on modern development, social trust, and Great Famine responses, nor the property-rights/fiscal-capacity/social-capacity mechanism triad. It complements Xue (2021) on Qing charities, generalized trust, and political participation, but extends to development outcomes. Against the European state-building literature (war strengthens central state capacity via centralization), this paper’s distinctive claim is that the Taiping Rebellion strengthened LOCAL fiscal capacity through DECENTRALIZATION, and expanded local social capacity that constrained the central state.

Q9. What are the policy implications and their scope conditions?

The benefits of war-induced institutions are conditional, not universal: they appeared chiefly in Late Taiping areas with a strong gentry class and favorable initial conditions for modern sectors (the wealthier, more commercial Lower Yangtze). The likin/fiscal-capacity benefits are explicitly stated to be conditional on strong gentry and good modern-sector initial conditions. The broad implication is that, given China’s very strong state but still weak society today, cultivating civil society and strengthening social capacity could yield particularly large long-term payoffs. The authors also caution (Appendix F.1) that likin could be distortionary taxation rather than fiscal capacity, arguing the fiscal-capacity interpretation is more relevant for long-term development.

Q10. What significant caveats does the paper acknowledge?

Long-term mechanisms cannot be exhaustively identified — likin and charities are endogenous outcomes, so mediation magnitudes are descriptive, not causal. History contains near-infinite interrelated events, so confounding cannot be fully eliminated (a fundamental limitation of all history-based work). The IV may have omitted correlates of longitude. Some 2SLS estimates for development outcomes were largely insignificant. The charity-stock measure assumes charities persisted once founded (no closure dates in the data). On property-rights persistence: using 2005 World Bank Enterprise Survey data they find no association between modern firms’ perceived property-rights protection and Taiping regimes, suggesting the channel works through income effects rather than persistence of property rights per se.

Key Concepts

Early vs. Late Taiping areas: Early Taiping = prefectures occupied by the rebels up to 1859 (Anhui, Jiangxi, Hubei), where the old landlord system collapsed and land rights stayed ambiguous; Late Taiping = prefectures occupied from 1860 (Jiangsu, Zhejiang), where the Taiping introduced a ‘direct tenant payment’ (作佃交粮) system and issued new deeds, granting tenants de facto/de jure ownership. This distinction is the paper’s central source of institutional variation.

Likin (lijin): A local tax on trade and commerce introduced in 1853 (a transit tax on travelling merchants’ goods plus a business tax on resident merchants), collected in a decentralized, province-specific way. In the paper it is the operational measure of local fiscal capacity (likin revenue per 1,000 sq km), not central state capacity.

Social capacity: In the paper’s sense, the ability of society to act collectively, constrain the state, and empower its members — operationalized empirically by the stock of local charity organizations (‘benevolent halls’/shantang) that functioned as bridging social capital across classes.

Likin-as-fiscal-capacity hypothesis: The claim that the rebellion-induced likin system durably raised LOCAL fiscal capacity (an instance of Tilly’s ‘war made the state’ operating locally rather than centrally), which improved public-goods provision and long-run development — conditional on strong gentry and favorable modern-sector initial conditions.

Stationary bandit (applied to Late Taiping rulers): Borrowing Olson (1993): in Late Taiping areas the consolidated, longer-horizon Taiping regime behaved like a stationary bandit, lowering effective tax rates, encouraging land registration, and securing tenant property rights to expand the tax base and promote production, unlike the looting/confiscation of the early stage.

Famine Control: The paper’s local famine-severity measure: the ratio of the cohort born during the Great Famine (1959-1961) to the cohort born pre-famine (1954-1957) in the 1990 census; a higher value means less severe famine and more survivors, and it is less vulnerable to government understatement of famine deaths.

Intra-China Divergence: The authors’ term for China’s persistent, very large regional disparities in economic performance (up to 27-to-1 in GDP per capita) despite all regions historically sharing similar Malthusian income levels — the macro puzzle the rebellion’s institutional legacy helps explain.

The macroeconomics of automation

Thu, 01 Jan 2026 00:00:00 +0000

Layer 1: Overview

This paper asks a foundational question: can the economy-wide degree of automation be measured coherently from standard macroeconomic data, without relying on technology-specific proxies such as robot counts or AI investment surveys? Existing micro-level proxies are fragmented across technologies and difficult to aggregate, leaving it unclear how automation evolves at the macro level or how it relates to capital deepening, factor shares, and productivity growth. The authors, Hideki Nakamura, Masakatsu Nakamura, and Shota Moriwaki, address this by developing a task-based general equilibrium framework in which the aggregate degree of automation emerges endogenously and is fully identified from observable macroeconomic aggregates.

The theoretical architecture begins with a continuum of tasks, each exhibiting Leontief technology at the task level. Within each task, capital and labor are perfectly substitutable, but firms choose the least-cost input given factor prices. Tasks are ordered by the relative efficiency of capital to labor; as the wage-to-capital-service-price ratio rises with capital deepening, capital performs an expanding range of tasks. Aggregating task-level Leontief decisions over a firm generates a global (envelope) production function. The paper’s first main theorem shows that under a mild regularity condition on task efficiency orderings, this aggregation delivers a standard neoclassical production function. Its second set of results identifies the precise efficiency structure under which the aggregate function takes the CES form: that structure corresponds to a Pareto cumulative distribution of input efficiencies. This Pareto structure yields a clean closed-form relationship: the degree of automation is determined entirely by the capital-labor ratio (in efficiency units) and the elasticity of substitution. When the elasticity exceeds one, the degree of automation equals the capital income share; when the elasticity falls below one, it equals the labor income share. Neutral technical progress leaves the degree of automation unchanged at a given capital-labor ratio; capital-augmenting progress raises it; labor-augmenting progress lowers it.

The empirical application uses panel data from the 2023 Japan Industrial Productivity (JIP) database covering 52 manufacturing industries from 1994 to 2020 (N = 1,404 industry-year observations; two industries excluded for data quality). The CES production function is estimated via GMM using first-differenced factor-share equations derived from the normalized CES system (de La Grandville 1989 normalization), with five sets of instrumental variables drawn from lagged factor prices, information stock and its price, trade openness, workforce age composition, and part-time employment shares.

The main quantitative findings are as follows. Under the assumption of neutral technical progress, the elasticity of substitution sigma is significantly above one but close to one, ranging from 1.049 to 1.102 across the five IV sets (all significant at least at the 10 percent level). Under the assumption of capital-augmenting technical progress (gK > 0, gL = 0), sigma ranges from 1.035 to 1.068, again robustly greater than one. Capital-augmenting technical progress is statistically significant across all specifications; labor-augmenting technical progress cannot be confirmed in any specification. The average estimated degree of automation across the 52 industries over the full sample period is 0.417 (standard deviation 0.171, minimum 0.138, maximum 0.811). The average rises steadily from 0.407 in 1994 to 0.426 in 2020, temporarily declining around the 2008 financial crisis before recovering. Substantial heterogeneity persists across industries throughout the sample. The distribution shifts rightward over time but retains a fat left tail, with the mode just above 0.3 and several industries exceeding 0.7.

The two-level CES extension decomposes aggregate capital into industrial robots and other capital, exploiting a purpose-built robot capital stock constructed via the RAS and perpetual inventory methods (initial year 1985). Industrial robots account for only 0.44 percent of aggregate capital stock on average. The two-level estimation yields higher elasticities (sigma-a between 1.191 and 1.346 across IV sets for the composite-labor margin; sigma-b between 1.049 and 1.096 for the robots-other-capital margin). The degree of automation for the composite rises from 0.398 to 0.430 over the sample, a more pronounced increase than the standard CES estimate, reflecting robots’ amplifying role in automation.

The paper benchmarks three automation measures against an internal consistency criterion: the squared distance between the automation degree inferred from the capital-labor ratio and that inferred from output per worker, given the same CES structure. The Pareto-based measure (the paper’s preferred measure) achieves a distance of 0.0000319, far below the Cobb-Douglas alternative (0.002484) and the continuity-preserving alternative (0.00999), validating the Pareto efficiency-distribution assumption. The Cobb-Douglas alternative yields a mean automation of 0.500 rising from 0.454 to 0.529; the continuity alternative rises more sharply from 0.208 to 0.589 but is discontinuous and sometimes falls outside the unit interval.

For policy and theory, the paper’s framework implies that Japan’s sustained capital accumulation during its prolonged stagnation after 1990 translated into rising automation even without commensurate TFP growth, connecting automation dynamics to the “productivity paradox.” The model also shows that automation can rise alongside an increasing labor income share when sigma is below one, caution against interpreting a stable or rising labor share as evidence against ongoing automation. The degree of automation provides a unified lens connecting capital deepening, factor shares, and productivity in a single theory-consistent measure.

In depth

Q1. What is the core identification strategy and what observables are used to infer the degree of automation?

The degree of automation is identified from the first-order conditions of the CES production function. Under the Pareto efficiency-distribution assumption, the CES structure implies a one-to-one mapping from the aggregate capital-labor ratio (in efficiency units), the share parameter s, and the elasticity of substitution rho to the degree of automation (Theorem 4, Eq. 25 and 31). In practice, the authors estimate the CES production function via GMM on first-differenced factor-share equations, recover rho and gK, and plug those into the formula for the degree of automation. No direct observation of tasks, robots (in the standard CES step), or technology-specific adoption decisions is required.

Q2. What are the main threats to identification and how do the authors address them?

The main threats are endogeneity of the output-to-labor and output-to-capital ratios (both simultaneously determined with factor prices) and measurement error in the capital-labor ratio (arising from industry classification changes and the RAS procedure used to construct robot data). The authors address endogeneity via GMM estimation using five distinct IV sets that include lagged factor prices, information stock and its price, trade openness, and workforce composition variables. They report that elasticity estimates are stable across all five IV sets and across alternative sample windows (including a longer 1973-2011 sample from pre-SNA-revision data), and conclude that measurement error is unlikely to drive the results. The overidentification test is not rejected for any IV set in the baseline CES specification (and for most in the two-level specification).

Q3. What theoretical result connects the degree of automation to factor income shares?

Corollary 1 establishes that under the Pareto efficiency structure (Eq. 22) with competitive factor markets, the degree of automation equals the capital income share when sigma > 1, and equals the labor income share when sigma < 1. This makes the degree of automation directly readable from income-share data in the theoretically preferred case (sigma > 1 for Japan). The empirical results are consistent with this: the average degree of automation across manufacturing industries is close to the average capital income share over the sample, providing a cross-check for Corollary 1.

Q4. Why does the paper use a Leontief production function at the task level while obtaining a CES function at the aggregate level?

The Leontief specification at the task level reflects the idea of a bottleneck in production: within a single narrowly-defined task, only capital or labor is used (once a task is automated, capital fully replaces labor in that task). Perfect substitutability between capital and labor operates at the extensive margin (which tasks are automated) rather than within a task. The aggregate (envelope) function, formed by varying the automation cutoff as the capital-labor ratio changes, generates any elasticity of substitution from zero to infinity. The Pareto efficiency-distribution assumption pins down the specific case of a CES aggregate.

Q5. How does the two-level CES extension work, and what does it add?

The two-level CES nests industrial robots and other capital into a capital composite at the inner level (robots vs. other capital, with elasticity sigma-b), then combines that composite with labor at the outer level (composite vs. labor, with elasticity sigma-a). Robot data for 52 industries are constructed via the RAS and perpetual inventory methods with an initial year of 1985. Because robots account for only 0.44 percent of aggregate capital on average, they have a small direct weight, but the two-level decomposition isolates their specific contribution to the automation margin. The two-level CES estimates sigma-a between 1.191 and 1.346 (higher than the standard CES estimates), and finds that the test of equality between sigma-a and sigma-b is rejected for three of five IV sets, suggesting the two elasticities genuinely differ. The average degree of automation rises more steeply under the two-level estimate (0.398 to 0.430) than under the standard CES estimate (0.407 to 0.426), indicating that explicitly accounting for robots reveals a more pronounced automation trend.

Q6. What is the paper’s internal consistency criterion, and how does it rank alternative automation measures?

Internal consistency is defined as the mean squared gap between the degree of automation inferred from the capital-labor ratio (Eq. 37, the paper’s preferred measure) and the degree of automation implied by observed output per worker given the same CES structure (Eq. 41). A smaller gap means the measure is more coherent with the CES framework from which it is derived. The Pareto-based measure achieves a distance of 0.0000319, more than seventy times smaller than the Cobb-Douglas alternative (0.002484) and over three hundred times smaller than the continuity-preserving alternative (0.00999). The authors therefore select the Pareto-based measure as most internally consistent with CES production.

Q7. What is documented about heterogeneity in automation across industries?

The degree of automation varies substantially across the 52 manufacturing industries, with a standard deviation of 0.171 and a range from 0.138 to 0.811 in the standard CES estimation. The kernel density in 1994 has a fat left tail with a mode just above 0.3, and several industries already exceed 0.7. The distribution shifts rightward by 2020 but remains dispersed. The authors split industries into those with an increasing capital income share (34 industries) and those with a decreasing share (18 industries) and test whether the elasticity of substitution differs between groups; they find no statistically significant difference for any IV set, implying the CES structure is uniform across industries even though automation levels differ.

Q8. How does the paper connect automation to TFP and the productivity paradox?

The theoretical framework shows that automation via task reallocation shifts the production function in a northeast direction in (k, y) space but does not shift it upward in a way that registers as TFP growth. Formally, increasing automation does not appear to impact TFP growth (citing Nakamura and Nakamura, 2008). The empirical finding that the degree of automation rose from 0.407 to 0.426 during Japan’s prolonged stagnation (1994-2020), a period of slow output-per-worker growth, is consistent with this: capital accumulation drove automation forward even though measured TFP growth was subdued. The paper thus links automation dynamics to Japan’s productivity paradox and implies that standard TFP accounting may understate the technological transformation underway.

The CES framework implies that when sigma > 1 (capital and labor more substitutable), capital accumulation raises the capital income share and lowers the labor share; the degree of automation equals the capital income share. When sigma < 1, capital accumulation raises the wage-to-rental ratio by more, increasing the labor income share; the degree of automation equals the labor income share. In both cases automation rises with capital deepening. A key implication is that observing a stable or rising labor income share does not rule out rising automation when sigma is below one or close to one. The authors’ estimate of sigma slightly above one for Japanese manufacturing implies a slightly rising capital share, consistent with the panel-estimated trend (b-hat = 0.00102, t-value = 6.84).

Q10. What are the robustness checks and how stable are the estimates?

Robustness checks include: (1) five distinct IV sets spanning different combinations of lagged wages, capital rental prices, information stock, trade openness, and workforce composition; (2) estimation under both neutral and capital-augmenting technical progress assumptions; (3) estimation using a longer sample (1973-2011 using pre-SNA-revision data), which yields a sigma still significantly above one and close to one, with slightly larger capital-augmenting technical progress reflecting higher growth in that period; (4) estimation of the full CES production function equation simultaneously with the two FOC equations (Appendix E.2), yielding similar elasticity estimates; (5) a structural change test splitting industries by capital-share trend, finding no significant difference in elasticity between subgroups. Unit root tests (Harris-Tzavalis and augmented Dickey-Fuller) confirm stationarity of all key variables except the part-time ratio, which also passes the ADF test.

Q11. What are the caveats and acknowledged limitations?

The authors acknowledge several limitations. First, three conditions cannot be simultaneously satisfied: a CES aggregate, the degree of automation lying in the unit interval, and continuity of the automation measure at unit elasticity (sigma = 1). The preferred measure prioritizes the unit-interval restriction and sacrifices continuity at sigma = 1, making direct comparisons across the sigma < 1 and sigma > 1 cases problematic (an alternative continuous measure is derived in Appendix C but may fall outside the unit interval). Second, the framework abstracts from the creation of new tasks; changes in the total number of tasks over time would affect the automation measure. Third, the paper does not decompose automation by skill level; the observed differences between skilled and unskilled labor in automation suggest a need for nested CES structures in future work. Fourth, the two-level CES nesting (robots within capital composite) is dictated by data availability; alternative nestings, such as grouping robots and labor at the first level, are not separately identifiable.

Q12. How does this paper differ from and improve upon the prior literature?

The paper improves on micro-proxy approaches (robot counts, AI investment, task-exposure indices from Acemoglu-Restrepo 2020, Adachi 2025, etc.) by providing an aggregate, theory-consistent measure that does not require technology-specific data. It extends prior CES microfoundation work (Jones 2005 Pareto-Cobb-Douglas result, Growiec 2008 Weibull-CES results) by deriving the Pareto efficiency structure that yields CES specifically from task-level automation decisions. It improves on the authors’ own prior work (Nakamura and Nakamura 2008, Nakamura 2009, 2010) by providing a complete theoretical justification for input efficiencies, a full treatment of the elasticity of substitution, and an empirical implementation. Relative to Artuc et al. (2023) and Adachi (2025), which use Frechet distributions for task productivity, this paper uses a deterministic framework with Pareto-distributed input efficiencies and emphasizes aggregate-level identification rather than cross-occupational substitution.

Q13. What are the policy implications?

The paper does not make direct policy prescriptions, but its framework has several implications. First, policymakers tracking automation can use standard national accounts data (capital stock, labor input, output, factor shares) rather than waiting for technology-specific surveys, enabling faster and more comprehensive monitoring. Second, the result that automation can advance during periods of slow TFP growth suggests that technology policy focused solely on productivity metrics may underestimate the pace of labor displacement. Third, the finding that Japan’s capital accumulation drove automation even through prolonged stagnation implies that capital subsidies or policies encouraging investment could accelerate automation independent of TFP. Fourth, the model’s prediction that automation rises alongside increasing labor shares under low substitutability (sigma < 1) warns against complacency: labor-income gains and technology-driven labor displacement can coexist. Fifth, the need for future work on skill heterogeneity and task creation suggests that the framework can be extended to inform distributional policies.

Key Concepts

Degree of automation: In this paper, the share of the unit task continuum performed by capital rather than labor, denoted a_t, ranging from 0 to 1. It is determined endogenously in equilibrium by relative factor prices and increases with the capital-labor ratio. It is distinct from any technology-specific proxy and emerges as a function of aggregate macroeconomic observables.

Task-based production framework: A model in which output requires completing a continuum of tasks, each exhibiting Leontief technology at the task level (capital and labor are perfectly substitutable within a task, but the firm either fully automates a task or uses labor exclusively). Tasks are ordered by the relative efficiency of capital to labor, and firms choose the automation cutoff that minimizes cost given factor prices.

Pareto efficiency distribution: The specific parametric form of aggregate capital- and labor-input efficiency functions (Eq. 22) under which the task-level aggregation yields a CES production function at the macro level. The relationship between the degree of automation and aggregate input efficiencies follows a Pareto cumulative distribution, which also delivers the highest internal consistency among automation measures tested.

Internal consistency criterion: A criterion for selecting among automation measures, defined as the mean squared gap between the automation degree inferred from the capital-labor relationship and the automation degree implied by the output-per-worker relationship, within the same CES structure (Eq. 42). A smaller gap indicates that the measure is more coherent with the CES production framework from which it is derived.

Capital-augmenting technical progress: An exogenous shift in the efficiency of capital inputs (A_K,t) that raises the effective capital-labor ratio and therefore the degree of automation at any given physical capital-labor ratio. Distinguished from labor-augmenting and neutral technical progress. In the empirical estimation, capital-augmenting technical progress is statistically significant across all specifications, while labor-augmenting technical progress cannot be confirmed.

Two-level CES production function: An extension of the standard CES that nests industrial robots and other capital into a capital composite at the inner level (with substitution elasticity sigma-b), then combines the composite with labor at the outer level (with elasticity sigma-a). Allows separate identification of the automation role of robots versus other capital, yielding a more pronounced increase in the degree of automation than the standard CES when robots are explicitly accounted for.

Automation frontier: The marginal task at which the cost of capital use exactly equals the cost of labor use, i.e., the task a_t at which lambda(a_t)/theta(a_t) = w_t/R_t. Tasks with indices below this frontier are automated; tasks above are performed by labor. As the wage-to-rental ratio rises, the frontier expands (more tasks become automated), capturing the central mechanism by which capital deepening drives automation.

Journal of Economic Growth | Macro Paper Warehouse

Armed conflict exposure and trust: evidence from a natural experiment

Layer 1: Overview

In depth

Q1. What is the identification strategy and what are the main threats to it?

Q2. What are the main mechanisms and how are they distinguished empirically?

Q3. What heterogeneity is documented?

Q4. What robustness checks are run?

Q5. How does this paper relate to and differ from closely related prior work?

Q6. What are the policy implications and their scope conditions?

Q7. What additional findings or caveats are noted?

Key Concepts

Manipulation of information in times of crisis: evidence from Covid excess mortality

Layer 1: Overview

In depth

Q1. What is the identification strategy and what are the main threats to it?

Q2. How is excess mortality estimated, and how sensitive are the results to modelling choices?

Q3. How do the authors distinguish intentional manipulation from limited state capacity?

Q4. How do the authors rule out the possibility that differences in false-positive aversion (rather than manipulation) explain MRR variation?

Q5. What is the direction of manipulation and what does this imply for theories of governmental information behaviour?

Q6. What factors are most strongly associated with misreporting, and how are they ranked?

Q7. What is the communist legacy finding and how is it interpreted?

Q8. What is the elections finding?

Q9. What robustness checks are performed?

Q10. How do the authors treat China, Bangladesh, and Indonesia?

Q11. How does this paper relate to and differ from prior work?

Q12. What are the policy implications and their scope conditions?

Q13. What limitations do the authors acknowledge?

Key Concepts

Property rights, fiscal capacity, and social capacity: The lasting impact of the Taiping Rebellion

Layer 1: Overview

In depth

Q1. What is the core identification strategy and what are the main threats to it?

Q2. How does the instrumental-variable strategy work and why might longitude be valid?

Q3. What are the four hypotheses and how are they distinguished empirically?

Q4. What heterogeneity is documented?

Q5. What robustness checks are run?

Q6. How is the mediation analysis handled and what does it show?

Q7. How does the Great Famine resilience result connect to the rebellion?

Q8. How does this paper relate to and differ from closely related prior work?

Q9. What are the policy implications and their scope conditions?

Q10. What significant caveats does the paper acknowledge?

Key Concepts

The macroeconomics of automation

Layer 1: Overview

In depth

Q1. What is the core identification strategy and what observables are used to infer the degree of automation?

Q2. What are the main threats to identification and how do the authors address them?

Q3. What theoretical result connects the degree of automation to factor income shares?

Q4. Why does the paper use a Leontief production function at the task level while obtaining a CES function at the aggregate level?

Q5. How does the two-level CES extension work, and what does it add?

Q6. What is the paper’s internal consistency criterion, and how does it rank alternative automation measures?

Q7. What is documented about heterogeneity in automation across industries?

Q8. How does the paper connect automation to TFP and the productivity paradox?

Q9. What is the relationship between the elasticity of substitution and the direction of factor share changes under automation?

Q10. What are the robustness checks and how stable are the estimates?

Q11. What are the caveats and acknowledged limitations?

Q12. How does this paper differ from and improve upon the prior literature?

Q13. What are the policy implications?

Key Concepts