What changed

Question: When generative AI helps the least experienced workers most, does it level expertise, or does it hollow out the way expertise is reproduced?

Question: Under what conditions can foundation-model-mediated social research produce valid knowledge?

Question: What are the early labour-market effects of generative AI?

Question: Researchers, firms, regulators and governments describe generative AI in incompatible terms: a tool, a normal technology, a cultural technology, an agent, a partner in communication, an infrastructure, an investment boom. Which description is best, and does the choice predict anything a researcher could observe?

Question: AI firms build the largest models, hold the compute, collect the records of how people use AI, fund research on its effects and decide which outside researchers may test their systems. How independent can research on AI's social effects be under these conditions, and who is gaining the authority to say what AI does to society?

Question: Experiments find that generative AI saves workers time on many tasks. Why does so little of that show up in firm performance and national productivity, at least so far?

Question: Benchmark scores, leaderboard ranks, model judges, developers' own reports, red-teaming and audits are now used to decide what research is published, which models are bought, which are released and which comply with the law. Can they carry that weight?

Question: AI tools help individual scientists publish and be cited more, help individual writers produce work that readers rate higher, and give individual users quick answers. Do the same tools make the work of many people more alike, narrow what a field studies and thin out the shared stores of knowledge everyone draws on?

Question: When generative AI helps the least experienced workers most, does it level expertise, or does it hollow out the way expertise is reproduced?

Question: What are the early labour-market effects of generative AI?

Question: When public organisations introduce algorithmic, machine-learning or foundation-model systems into administrative decision-making, does human discretion actually shrink?

Question: When, and through which mechanisms, does generative AI change persuasion, information intermediation and the public information environment?

Question: Where is power concentrated across the AI stack, through which mechanisms does that concentration matter, and under what conditions can firms, states, researchers or publics reduce dependency?

Question: What does AI regulation become after legislation is announced or enacted?

What changed: The corrected disparity figures are no longer held back. The main result now gives them from the authors’ corrected analysis: for discretionary referrals in 2016–18, the gap between the screen-in rates of Black and white children was 17.9 percentage points for AFST-only (counterfactual) decisions (67.9% against 50.0%) and 7.1 points for decisions by workers using the AFST (50.2% against 43.1%). The public-facing claim now leads with the disparity result that the correction supports, and gives the 21.0% override share second, as a figure of the original analysis whose numbers the authors later said all changed. The limitations add that the corrected analysis is a preprint, that its authors did not report the override share again, and that the study period and population of the 21.0% share are not recorded here. The direction of the claim, its sources, scope and verification state are unchanged.

Why: Version 1.0 held back the exact 17.9→7.1 figure (marked HOLD in the R04 LD-05 Canonical Claim Ledger v1.0), pending direct extraction from the corrected analysis. On 21 October 2026 the full text of Stapleton et al., arXiv:2204.13872v1 (29 April 2022), was read line by line. Appendix A, "Detailed Comparisons of Analyses 1 and 2", first point, Analysis 2 column, reports that AFST-only decisions would have screened in 67.9% of Black and 50.0% of white children in discretionary referrals from 2016-18, "a racial disparity of 17.9%", and that workers using the AFST screened in 50.2% and 43.1%, "a disparity of 7.1%". The paper’s own "%" is a difference between two rates, so this version calls it percentage points. The check read a text extraction of the PDF and looked at its figure pages. The paper’s Figure 1(b) plots the same screen-in rates; it labels the AFST-only gap 17.9% but the worker+AFST gap 7.0%, 0.1 point below the 7.1% of Appendix A. This version follows the appendix text and its rates, whose difference is 7.1 points. Section 2 of the same paper says that "all of the specific numbers we reported in Analysis 1 changed in Analysis 2"; the HQ batch notes take the 21.0% override share from the original CHI 2022 paper, which reports Analysis 1, and the corrected analysis does not report that share again. The CHI 2022 paper itself was not read for this revision (the ACM Digital Library blocks the project’s tools), so the attribution of the 21.0% share to the original analysis rests on the HQ batch notes. The check and this revision were done by AI agents reading the paper, not by a person.

What changed: The correlation is no longer held back. The main result now gives it: across 469 effects from 70 experiments, GPT-4-derived predictions correlated with the original effect sizes at r = 0.85 (95% CI 0.81–0.88), and at r = 0.92 (95% CI 0.89–0.94) after the authors’ adjustment for sampling error in the original estimates. The limitations now say that these figures come from the authors’ accepted manuscript, not from the Nature version of record. The public-facing claim, the source, the scope, the verification state and the publication status are unchanged; the verification state is the one recorded for version 1.0 and does not cover the two correlations, which were read in the manuscript only.

Why: Version 1.0 held back the exact r=.85 figure and its attribution to the Nature version of record (marked HOLD in the R03 LD-07 Canonical Claim Ledger v1.0), because the exact figure had not been extracted line by line from the Nature article. On 21 October 2026 the project owner supplied the authors’ accepted manuscript of the paper, as posted on OSF, which states that it has been accepted for publication in Nature. Its page 4, under "Primary test archive", reports: "In an analysis of 469 effects from 70 experiments, GPT-4-derived predictions were strongly correlated with original effect sizes (r = 0.85, 95% CI = [0.81, 0.88]; r_adj = 0.92, 95% CI = [0.89, 0.94])". The Nature version of record (656:115–122) was still not read, because the publisher blocks the project’s tools, so this version does not claim that the published article prints the same figures; the project owner chose to publish them with that attribution rather than wait for the version of record. The copy read was a print of the manuscript without a text layer, so the figures were read from the page image. The check and this revision were done by AI agents reading the manuscript, not by a person.

What changed: The distributional ledger no longer says that an early-career earnings and hours null is reported. It now gives what the March 2026 revision of the paper reports for early-career workers (aged 22–25): their employment fell in several of the occupations, but their share of employment did not change differentially at workplaces that encourage chatbot use, with effects above about a third of a percentage point ruled out. The contradictory/supporting field now also notes the paper's workplace-level nulls for employment (total hours), job churn and the early-career share, and that Danmarks Nationalbank Working Paper 223 finds lower employment growth at AI-adopting firms. The public-facing claim, the 2% bound, the 11 occupations and the sample of about 25,000 workers in 7,000 workplaces are unchanged.

Why: A recheck on 14 October 2026 read the full text of NBER Working Paper 33777 as revised in March 2026 (retitled "Still Waters, Rapid Currents: Early Labor Market Transformation under Generative AI"; previously "Large Language Models, Small Labor Market Effects"). Version 1.0 was built from the paper's abstract, and the HQ batch notes left "full Humlum/Vestergaard early-career ... details" open. The full text reports early-career results only as the employment share at adopting workplaces (Section 3.4, footnote 21), not as earnings or hours, and the same section reports no differential change in workplace employment (total hours) or job churn. The main result is confirmed in the full text: confidence intervals rule out average earnings and hours effects larger than 2% two years after ChatGPT, in 11 occupations, with 25,000 workers across 7,000 workplaces in the late-2024 survey round. The recheck and this revision were done by an AI agent reading the paper, not by a person.

What changed: The contradictory/supporting field no longer says that this result simply complements Humlum & Vestergaard. It now says the two Danish studies are in tension: the March 2026 revision of Humlum & Vestergaard finds no differential change in employment (total hours), job churn or the early-career share at workplaces that encourage chatbot use, through December 2024. The public-facing claim and the Nationalbank estimate are unchanged.

Why: A recheck on 14 October 2026 read the full text of NBER Working Paper 33777 as revised in March 2026. Version 1.0 treated the two Danish studies as measuring different margins (incumbent earnings and hours against firm recruitment), but Section 3.4 of the revision also estimates workplace employment, job churn and the early-career share at adopting workplaces and finds no differential change. The studies differ in how adoption is measured (firm AI adoption against employer-encouraged chatbot use in 11 exposed occupations), in unit and in horizon (late 2025 against December 2024), so they need not contradict each other, but the difference is not explained by either paper as far as was read; the Nationalbank paper itself could not be opened for this recheck. The recheck and this revision were done by an AI agent, not by a person.

What changed: The public-facing claim now says that the racial-disparity result comes from working-paper evidence ("separate working-paper evidence" instead of "separate evidence"). The Kentucky erosion result and both sources are unchanged.

Why: A claim check on 13 October 2026 found that version 1.0 dropped the working-paper qualifier that the HQ cross-batch synthesis cleared for this claim ("separate working-paper evidence"); the HQ notes say the 2019 Albright paper is a working paper and must not be given the same maturity as Stevenson 2018. The check and this revision were done by AI agents against the HQ notes, not by a person.

What changed: The public-facing claim now names the one decision HQ verified, the Federal Administrative Court (BVwG) decision of 1 September 2025, instead of "Austrian courts", and the source field cites only that decision, dropping "prior VwGH/BVwG procedural history". The legal finding and the effective-discretion boundary are unchanged.

Why: A claim check on 13 October 2026 found that the HQ notes verify a single decision (BVwG W256 2235360-1, 1 September 2025); HQ recorded the earlier VwGH/BVwG procedural history as part of the legal record but did not verify its content, so the plural "courts" claimed more than the record shows. Field 6 now cites only the verified decision; the same Source record is still cited. The check and this revision were done by AI agents against the HQ notes, not by a person.

What changed: The public-facing claim now says that the advantage disappeared against coached elite debaters, the only comparison tested under the length and speed constraint, instead of implying it disappeared against all strong human persuaders.

Why: A claim check on 13 October 2026 found that the HQ notes report the constrained result only against coached elite debaters (0.0pp, 95% CI −1.7 to +1.6), while version 1.0 attached it to the advantage over all strong human persuaders. The check and this revision were done by AI agents against the HQ notes, not by a person.

What changed: The public-facing claim and scope no longer give a 48-market, about-100,000-respondent base for the 10% figure; they say "across surveyed markets" and add the 7% of a year earlier that HQ verified.

Why: A claim check on 13 October 2026 found that HQ verified the 10% figure only as a global aggregate (up from 7%) and recorded 27 markets for a different question; the 48-market base for this figure was never verified, and one secondary report gives 45 markets for the chatbot questions. An unverified number is removed rather than guessed. The check and this revision were done by AI agents, not by a person.

What changed: The public-facing claim now says the study does not establish that regulation causes the gap, instead of saying it does not identify regulation as the "sole" cause.

Why: A claim check on 13 October 2026 found that "not the sole cause" implies the study shows regulation to be a partial cause; the HQ primary read of Pan & Xu says the study explicitly does not establish a causal relationship between regulation and censorship behaviour. The check and this revision were done by AI agents against the HQ notes, not by a person.

What changed: The claim now says that generative AI systems already on the market before 2 August 2026 have until 2 December 2026 to meet the Article 50(2) machine-readable marking obligation, and cites Regulation (EU) 2026/1744 (the Digital Omnibus on AI) as a third Source. The 2 August 2026 date for the other Article 50 obligations is unchanged.

Why: A newer-evidence check on 13 October 2026 found that version 1.0 missed the Digital Omnibus on AI (Regulation (EU) 2026/1744 of 8 July 2026, published in the Official Journal on 24 July 2026, before the 25 September evidence cut-off), so a reader could take every Article 50 duty as binding from August. Recital 38 of the Regulation sets a four-month transitional period for providers who placed their systems on the market before 2 August 2026, which ends on 2 December 2026; that date is also stated by law-firm summaries (A&O Shearman; Ropes & Gray, 3 August 2026). The recital was read on EUR-Lex by an AI agent, not a person. The operative provision, Article 111(4) of Regulation (EU) 2024/1689 as inserted by Article 1, point (39)(b), of Regulation (EU) 2026/1744 (providers of AI systems generating synthetic content placed on the market before 2 August 2026 "shall take the necessary steps in order to comply with Article 50(2) by 2 December 2026"), was read by an AI agent in a secondary consolidated copy, and a second AI review run by the Owner located it in the EUR-Lex text.

What changed: The claim now reports, beside the OpenRouter/a16z figure, the lower open-source token share that Demirer, Fradkin, Tadelis & Peng (NBER Working Paper 34608, December 2025) report from OpenRouter data, and cites that paper as a second source. The OpenRouter/a16z figure is unchanged.

Why: A literature check on 13 October 2026 found a second analysis of the same platform, by academic authors with Microsoft and Amazon affiliations, that reports about 25% open-source share by December 2025, not about one-third. Version 1.0 cited only the platform's own report, so a reader could take one-third as settled. The figures were read from the NBER paper by AI agents, not by a person, to the same standard as the rest of this ledger (primary-text reading by AI, no named human expert).

What changed: The public-facing claim now says the order directed Commerce to condition some non-deployment BEAD funding, to the maximum extent allowed by law, on the absence of state AI laws identified as onerous, instead of saying the order itself "tied eligibility" to state AI-law conditions.

Why: A claim check on 13 October 2026 found that version 1.0 stated as done what the order only directed, and dropped the legal-limits hedge; the HQ primary read of the order records the direction to Commerce and the "to the maximum extent allowed by law" wording. The check and this revision were done by AI agents against the HQ notes, not by a person.

What changed: Pew Research Center (30 September 2026) built an AI “digital twin” for each panelist analyzed from three 2026 waves of its American Trends Panel, a nationally representative panel of randomly selected U.S. adults. Each twin was conditioned on that person’s profile and earlier survey answers, and weighted synthetic and human results were compared on nearly 300 questions. With its best-performing configuration (Claude Opus 4.6), synthetic estimates differed from human estimates by an average of 12.4 percentage points. Error was substantial for every subgroup reported, reaching 16.1 points for Republicans and Republican leaners and 15.1 points for Black adults. On 47% of questions at least one answer choice was selected by no synthetic respondent, which happened on no question among humans. Results also differed systematically by AI model, although some toplines matched closely. This strengthens the evidence for LD07-HQ-C06 on selected-average agreement, real-world response variance and subgroup heterogeneity. The report contains no regression or treatment-effect analysis and no individual-level accuracy result for its final configuration, so those parts of the claim are unchanged. The claim wording is unchanged.

What changed: The note on the nearest work by Chen, Zaharia and Zou no longer says its Harvard Data Science Review issue details are unconfirmed: the DOI's Crossref record (checked 21 October 2026) gives Harvard Data Science Review volume 6, issue 2 (2024), as the References already did. The question, design, literature check and verdict are unchanged.

Question: In small firms in Greece outside tourism (for example accounting offices, shops, small manufacturers and software companies), who uses generative AI and for which tasks, and has any firm changed how work is divided, checked or handed over because of it?

Question: In Greek accounting offices, law firms and software companies that use generative AI, which tasks that juniors used to learn on are now done with AI or by seniors, and how do juniors and their supervisors describe the feedback and practice juniors now get?

Question: When a language model answers a few European Social Survey Round 11 questions as Greek respondents of a given age, sex, education and region, do its answers come closer to or move further from those of the Greek respondents when the prompt is in Greek rather than in English, overall and across groups?

Question: If proponents of the normal-technology, cultural-technology, agent, artificial-communication, infrastructure and capital-formation accounts each state in advance, with thresholds and dates, observations their account predicts and observations it rules out, which predictions differ between accounts, and which hold over the following years?

Question: When the same items that showed sensitivity to output probability, the reversal curse, irrelevant clauses, compositional depth and counterfactual premises are put to successive model generations from 2023 to 2026, including reasoning and agentic models, which failure patterns shrink in size but keep their shape, and which disappear?

Question: Among deployed generative AI products that are built on the same base model (for example, customer-service assistants, writing tools or screening tools from different firms), are errors and harmful outputs more strongly correlated across products, by case and by the group affected, than among products built on different base models?

Question: In organizations that use generative AI, how is responsibility for an AI-produced error assigned in practice (to the employee who used the tool, the manager, a risk team, the vendor or no one), and does the assignment differ when the system is described as a tool, an assistant or an agent?

Question: Across open-weight and documented models released from 2020 to 2026, how closely does training compute predict measured generality (the range of distinct tasks performed competently), and how many models fall on the wrong side of the 10²³ FLOP indicative criterion that the European Commission uses for a general-purpose AI model?

Question: Where public services and clinics turn the time saved by generative-AI drafting into higher caseloads (social-work case records, clinical notes), does the time spent checking each output fall and the share of errors that survive into the signed record rise, and how much of any rise comes from time pressure rather than from a decline in the checkers' own skill?

Question: When people learning a writing or analysis task are randomly assigned to use a language model that does the work for them, a model that only explains while they do the work, or no model, do the same participants who lose more skill once the model is removed also produce work more similar to each other's and to the model's, and does the way the model is used account for both?

Question: Among published studies of AI's social effects (labour, information, bias, education), do studies funded by AI developers, or relying on their data or access, reach systematically different conclusions from comparable independent studies, after accounting for topic, design and venue?

Question: What share of authors of research on AI's social effects in social-science journals, interdisciplinary venues (FAccT, AIES) and policy reports have industry funding, employment or data agreements, how often is this disclosed, and how does it differ by discipline and region?

Question: When the same chatbot conversations are classified independently of the developer, with a validated scheme and human-coded benchmarks, how far do headline usage measures such as the automation share, the work share and task success move away from the figures developers publish?

Question: Under Article 40 of the Digital Services Act, which vetted-researcher applications concerning AI features of very large platforms are granted, refused or delayed, on what grounds, and how long does each stage take?

Question: Across social-science and humanities journals, books, policy reports and arXiv, what share of research on AI's social effects comes from computer-science teams, social scientists, mixed teams, industry and government, and how has that share changed since 2014?

Question: How do people who donate their chatbot conversations to researchers differ from the developers' user bases, and how much do findings from donated data change once donors are weighted to the user population?

Question: In China's register of generative-AI services, where every launched application must display the filed service or model it uses, how concentrated is applications' dependence on a few base models, and on a fixed set of test cases are the errors, refusals and biased outputs of applications that share a base model more strongly correlated than those of applications built on different models, beyond the correlation already found between models from different providers?

Question: For general-purpose AI providers that also run platforms or search engines designated under the Digital Services Act, what does each legal route for outside scrutiny deliver in practice (external evaluation under the GPAI Code of Practice, which applies only to models with systemic risk, vetted-researcher data access under the Digital Services Act, and the AI Office's information requests and model evaluations), recorded for each route as what object is reached (model, platform data or documents), who can start it, how long it takes and how deep the access goes?

Question: In real organizations, when generative AI is deployed to whole teams or units, with and without a redesign of the team's workflow, do coordination-dependent work (meetings, handoffs, jointly written documents) and the unit's measured output change, compared with units where only some individuals have the tool?

Question: When workers save time with generative AI, how much of it goes to more of the same output, to new tasks, to checking AI output, to on-the-job leisure or to shorter hours, measured with time-use diaries or telemetry linked to the same workers' measured output?

Question: In organizations where some staff produce work with generative AI, how much time do reviewers, managers and recipients spend checking, correcting and redoing that work, and once both are counted, does the downstream cost offset the time the author saved?

Question: In a multi-year panel of firms, does deeper integration of generative AI, together with measured complementary investment (process redesign, training, data and capitalized software), show an early dip and a later rise in measured productivity, and do firms that adopt without that investment show neither?

Question: When a government agency deploys generative AI to caseworkers, adjudicators or reviewers, do service outcomes recorded in administrative data (processing time, error and appeal rates, outcomes for citizens) improve against a credible comparison group, beyond staff time savings?

Question: Do organizations' formal generative-AI policies, mandates and announcements match measured use and work outcomes, and where they diverge, is the divergence ceremonial adoption (policy without practice) or shadow use (practice without policy)?

Question: Across many language models, do scores on public benchmarks predict measured outcomes when the same models are used in real work, such as code that maintainers merge in live repositories, support tickets resolved or error rates in use, and are the benchmarks calibrated to those outcomes or only correct in rank?

Question: When annual indices, industry reports and government or procurement documents cite benchmark and evaluation figures, what share come from the developers themselves, what share are independently measured, and how often is the figure, its unit or its scope changed between the primary source and the relay?

Question: When the same safety scenarios are presented with and without minimal cues that they are tests, how large is the gap in measured behaviour across open and closed frontier models, and does suppressing evaluation awareness in open-weight models on the same items reproduce the gap?

Question: Under the EU Code of Practice for general-purpose AI models with systemic risk, which signatories appoint independent external evaluators, how often are the exceptions used (a model judged similarly safe or safer, or no evaluator found after a public call), and what access and time do evaluators actually receive?

Question: Under China's national standard GB/T 45654-2025, who builds the generated-content and refusal test banks that decide whether a generative AI service passes, how are the banks validated, and do providers' banks and third-party evaluators' banks give the same verdicts on the same models?

Question: Among published studies in NLP, the social sciences and education research that evaluate closed language models through an API, what share used a model version that has since been retired or is due to retire, and how many of a sample can still be re-run to reproduce their main result?

Question: Since language models became widely used in 2023, has the range of topics covered by papers from adopting researchers shrunk relative to non-adopters, at the level of whole fields, and does the answer differ between the natural and the social sciences?

Question: When the same people write or brainstorm with a language model repeatedly over a term or a year, does the similarity of their work to each other's grow, stay level or fade, and does it carry over into what they write without the model?

Question: In markets for creative and intellectual work, such as self-published fiction, has the diversity of published works, of works that sell and of works that reach the top ranks changed since generative AI spread, beyond what changes in volume explain?

Question: Across successive generations of language models from several providers, how much diversity of ideas does pooling models add compared with one model, and is that gain shrinking as models' outputs and errors become more alike?

Question: When people write in their own language, not English, with AI suggestions, do their texts move toward the style and content of English-language or Western writing, and does this differ by language and by how much text in that language the model was trained on?

Question: In scientific papers and proposals written with language models, how much of the measured rise in similarity is shared wording and style, and how much is shared research questions, methods and claims, when the two are measured separately and validated against expert judgement?

What changed: The note on the nearest Danish work now says that its March 2026 revision (NBER w33777, retitled "Still Waters, Rapid Currents") no longer reports the 3–7% pass-through estimate the May 2025 version gave, and reports adopters' self-perceived earnings effects of 0 to 0.5% instead. Found when LD-02 was rechecked against the revised paper. The question, design, literature check and verdict are unchanged.

Question: Among people learning a professional or technical skill (clinical reasoning, programming, legal drafting), are those randomly assigned to learn with generative AI less able to do the work without it 6 to 12 months later than comparable learners trained without it, measured against an unassisted baseline test?

Question: After several weeks of AI-assisted practice, does performance without the tool depend jointly on how routine the task is and on the worker's prior expertise, as the split between existing tool-removed studies suggests?

Question: In open-source projects, after AI coding tools are adopted, do first-time contributors receive less substantive review feedback, less mentoring and fewer tasks handed to them by experienced maintainers than in comparable projects that have not adopted them?

Question: In law firms, hospitals and residency programmes, and software firms, what generative-AI tools, settings and rules do trainees and junior staff actually get, do they differ from what seniors get, and do any employers use the learning protections (hints instead of answers, AI-off practice) that experiments show protect skill?

Question: On the same tasks, does the advantage that AI gives less skilled workers when it assists them (a copilot) shrink or reverse when it carries out the work autonomously (an agent), as theory predicts?

Question: Does routine use of diagnostic AI lower experienced clinicians' detection rates when they work without it, tested with randomized AI-off sessions scheduled over time and analysed by each clinician's cumulative AI exposure?

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Narrowed after the literature check. The Census CES-WP-26-56 paper already measures initial penalties for the most AI-exposed majors, reports that they attenuate further from entry and compares the loss with "a large recession", so early-career penalties and a rough recession comparison are no longer open for the US. Only press coverage (Chronicle of Higher Education) reports a two-year figure (the earnings gap narrowing from 13% to about 5%); the paper's abstract gives no horizon and that figure is unconfirmed in the paper (it may conflate the 5-point employment drop). The abstract compares the loss with "a large recession" without naming the Great Recession. Years three to five, occupational match and catch-up, a same-model benchmark against recession cohorts, and any non-US register evidence remain open, so the question should be narrowed to those.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Narrowed after the literature check. The text-as-data half of the design is already under way in France: CEET-Cnam has mapped French company agreements mentioning AI signed from 2017 (Connaissance de l'emploi no. 200, 2024, and a working paper covering 2017-2026), IRES (working paper 03.2025) has mapped AI clauses in French agreements, and an FES report (Kahancova et al., October 2026) analyses 108 European agreements with AI provisions. None of these, on the pages read, links agreement content to later hiring or training outcomes, and no study found does the event-study half. The opportunity should be narrowed to the outcome link, building on the existing French coding rather than proposing it as new.

What changed: Narrowed after the literature check. The claim that no cross-system compilation of override rates exists is too broad. In offender risk assessment there is an established override literature that reports override rates and direction across tools and jurisdictions, now synthesised in a 2025 scoping review and meta-analyses of 21 studies covering eight tools (Psychology, Public Policy, and Law 31(3), doi:10.1037/law0000448), and single studies there report rates from about 7% to 74% with upward and downward overrides coded separately. No compilation was found for benefits, employment services, child welfare, pretrial or immigration systems, or across those sectors under one definition, so the opportunity should be narrowed to those sectors and use the correctional literature as a benchmark and coding template. The verdict changed from "No study found doing the core design" to "Related work exists".

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Narrowed after the literature check. A systematic review of publicly available US state-level AI procurement contracts now exists (Cusenza, SSRN 6812838, forthcoming Drexel Law Review), covering data access, intellectual property, stakeholder engagement, testing and cybersecurity provisions and finding that contracts rarely address algorithmic-governance risks. That covers part of the proposed contract analysis, but on the abstract it is US-only, state-level, not limited to decision-support systems, and does not code authority over thresholds, input variables, retraining or updates, nor compare vendor-built with in-house systems. Other new work codes vendor FactSheets (Kuehnert et al., 2026) or model clauses and guidance (Abdulbari, Frontiers 2026), not executed contracts. The opportunity should be narrowed to decision authority in contracts for decision-support systems, cross-nationally.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The verdict changed from "No study found doing the core design" to "Related work exists" because related work turned up; the question stands.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The verdict changed from "No study found doing the core design" to "Related work exists" because related work turned up; the question stands.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Narrowed after the literature check. The local-language and local-country sourcing part of the question is now partly answered: Zha and Chang audit Google and Baidu AI Overviews for health queries in 12 country settings and 4 languages and find that native-language queries raise locally sourced citations 3.5 to 13.5 times, Li et al. compare Baidu and Google overview source exposure across English and Chinese, and Zhen et al. map citations in Chinese generative search. None of these checks whether claims are supported by the cited pages (Zha and Chang name claim-level checking as future work), and the only grounding checks found (Xu et al.; Huang et al.; the Oumi analysis for the New York Times) are English and US-located. The opportunity should be narrowed to claim-level, human-validated fidelity across languages and markets, with source localization as a secondary measure.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Cost band corrected from "low to medium" to "medium": participant payments of about US$10,000 to 25,000 need a grant or project budget, in line with other opportunities of that size. Found in the independent review of the opportunity-page fixes. The question, design, literature check and verdict are unchanged.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The verdict changed from "No study found doing the core design" to "Related work exists" because related work turned up; the question stands.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The verdict changed from "No study found doing the core design" to "Related work exists" because related work turned up; the question stands.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Tightened after a test reading of the opportunity pages on 13 October 2026 (an AI stand-in run of the founder test, not an outside reader) found that the page did not show the procurement data exist in a usable form, the first thing a supervisor would ask. The data section now says what the open records contain (machine-readable notices from Contracts Finder and Find a Tender; G-Cloud sales with supplier and customer names, currency to be checked) and what they lack (the hosting provider behind a reseller), and the design now starts with a sample check of how often the provider can be identified, with freedom-of-information requests as the fallback. The question, the literature check and the verdict are unchanged.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Tightened after a test reading of the opportunity pages on 13 October 2026 (an AI stand-in run of the founder test, not an outside reader) judged it descriptive and asked whether the data exist. The question now uses a fixed project list and the projects' own announced dates; the page now says plainly that this is a descriptive tracking study; and the design starts with a five-project pilot that measures how many layer cells public sources can fill, narrowing to the disclosed layers if needed. The literature check and verdict are unchanged.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

What changed: Reworded after a test reading of the opportunity pages on 13 October 2026 (an AI stand-in run of the founder test, not an outside reader) found that the question's window, releases "between 2023 and 2028", ran past today, so the study could not be run as written. The question now covers releases from 2023 onwards and the two general-purpose model dates that have already passed; the high-risk dates (December 2027 and August 2028) become a later extension. It now asks whether delays cluster around legal dates, which the design can show, rather than implying it can prove what caused a delay, and the title says the same. The GovAI report entry now records that the report was read in full in the literature check. The literature check and verdict are unchanged.

What changed: Literature check added: a second, deeper search for existing work, with its queries, new nearest work and limits. The question and verdict stand.

Question: When the same exposure measure, age bands, occupation coding and event-study specification are applied to US data and to Nordic population registers, how much of the gap between the large US young-worker divergence and the near-zero Nordic estimates is explained by occupation mix, education composition, sensitivity to interest-rate rises and cohort size, and how much remains?

Question: If occupation-level AI exposure indices are replaced by AI-use rates measured in a nationally representative worker survey, does the relative fall in hiring of 22–25-year-olds into exposed occupations in US Current Population Survey data keep its size and sign, and how does the answer compare with exposure indices and chatbot-log usage measures?

Question: For graduates who entered the labour market between 2021 and 2025, do the employment, earnings and occupational-match penalties of AI-exposed fields of study narrow, persist or widen over the first three to five years after graduation, and how do they compare with the well-documented scarring from graduating into a recession?

Question: Among workers hired into junior positions before and after their employer began using AI, do promotion into higher-skill occupations, wage growth, recorded training and retention over the following two to four years differ between AI-adopting and comparable non-adopting firms?

Question: When a firm starts using generative AI, how much does its value added per worker change over the following two to three years, and what share of that change shows up in the wages of incumbent workers who stay, compared with profits and with the wages of new hires?

Question: In French firms, does signing a company-level collective agreement that addresses AI change the subsequent pattern of hiring (junior versus experienced, AI-related versus other roles) and training compared with similar firms in the same sector that have not signed one, and what do the agreements commit firms to?

Question: Across deployed public-sector risk and profiling systems, how often do officials formally or informally depart from the system's recommendation, in which direction, and how much of the variation between systems survives once override is defined and counted the same way?

Question: When public officials review a case selected for extra scrutiny, does knowing that a risk model selected it, or seeing its risk score, change how often they decline the claim, how hard they look, and whether they catch errors planted upstream in the case file, and do these effects differ by the claimant's nationality?

Question: For benefit claimants selected for extra checks by a risk model, how large are the burdens imposed before any formal decision (payment delay, evidence requests, withdrawn or abandoned claims, repeat applications), how do they compare with claimants selected at random or not selected, and how are they distributed by nationality and age?

Question: In local authorities using generative-AI transcription and summarisation in social work, what share of final, signed case records contain errors (invented content, omissions, changed meaning) that are absent from the recorded conversation, which kinds survive the practitioner's check, and what happens when people who draw on care read and try to correct them?

Question: In the contracts public agencies sign for risk-scoring, profiling and case-routing systems, who is given authority over the choices that shape decisions (thresholds, input variables, retraining and updates, performance targets), what audit and documentation rights does the agency keep, and does this differ between systems built in-house and those bought from vendors?

Question: For documented failures of public-sector algorithmic systems since 2020, who first detected the problem (internal monitoring, frontline staff, auditors, regulators, courts, journalists, advocacy groups, affected people), how long after deployment, and did detection lead to one-case correction or to system-level redesign?

Question: On a fixed battery of published social-science annotation tasks, how often does a substantive conclusion (sign, significance, interval coverage) change between repeated queries of a pinned model snapshot, a moving model alias over 6–12 months, and successive open-weight releases, and can design-based correction absorb those changes?

Question: With weights, prompts and hardware held fixed, do fp16, 8-bit and 4-bit builds of open-weight models, and different inference engines, change substantive estimates on published annotation and synthetic-respondent tasks more than prompt paraphrasing does?

Question: In probability-based panels, what share of completed interviews show AI assistance or autonomous-agent completion when measured with embedded multi-method detection validated against consented chatbot-history linkage, and how does that compare with opt-in platforms measured the same way?

Question: In probability-sample survey experiments fielded after model training cutoffs and selected for substantial, well-powered moderation, do synthetic samples recover the sign and ranking of conditional treatment effects better than a model that assumes no heterogeneity?

Question: Holding base weights fixed, how much do instruction tuning, preference tuning and region-specific fine-tunes shift coding validity and downstream estimates on stance and attitude annotation tasks, and do the shifts track the fine-tune's target culture?

Question: Across a sample of published social-science meta-analyses, do the studies retrieved by AI review tools, compared with those the original review included, change the pooled effect, its heterogeneity or the stated conclusion, and is the missed evidence systematically different (grey literature, non-English studies, null results)?

Question: How do ethics-board guidance documents across countries classify synthetic participants, LLM coding or interpretation of qualitative data, and transfer of participant data to commercial model APIs, and in a factorial vignette, do board members' decisions and requested safeguards vary with data sensitivity, model hosting and the degree of delegated interpretation?

Question: Using Afrobarometer, Arab Barometer and Latinobarómetro items fielded after model training cutoffs, does synthetic-sample accuracy at country, subgroup and individual level depend on interview language (for example Swahili or Hausa versus English, Arabic versus English), and do LLM codes of political constructs in low-resource languages pass a replacement test against trained in-country coders?

Question: On a corpus mixing human-written and LLM-written deliberative contributions, do LLM judges assign higher construct scores (for example on the Discourse Quality Index or argument quality) to LLM-authored text than expert coders blind to authorship, and is the gap larger when the judge model also wrote the text?

Question: Holding items and codebook fixed, how often does a formal replacement-test verdict flip depending on whether the comparator pool is crowdworkers, trained research assistants, the original study's coders or domain experts, and does the flip rate track construct ambiguity?

Question: When AI answer layers in search (Google AI Overviews and AI Mode) are shown or hidden at random on people's own smartphones, in at least one non-US market and language, how much do they change clicks to external websites, zero-click searches, the kinds of sources visited and trust in the information, compared with the US desktop estimates?

Question: Among people whose browsing is tracked across devices and platforms in 2025–26, does exposure to AI answers built into search (AI Overviews, AI Mode) and to standalone chatbots change the number, concentration and type of websites and news sources they visit over months, and does the change differ from what was found for early chatbot adoption?

Question: For matched public-interest queries (news, health, elections) issued in several languages and country markets, how often do claims in Google AI Overviews and AI Mode lack support in the pages they cite, how often do they cite sources in the user's own language and country, and do these rates differ from the US English baseline?

Question: When people are randomly assigned to search with AI answers as the default, or without them, for eight to twelve weeks of their normal information seeking, how do their source-checking behaviour, trust in AI answers, ability to spot wrong answers and reliance on AI for news and health questions change over time, and do early effects fade, persist or grow?

Question: On a live, open social platform, when labels saying that a post is AI-generated, or that it is AI-generated and potentially misleading, are applied at random to real political and news posts in users' feeds, how do they change actual reposts, likes and replies, and users' belief in the labelled claims, compared with unlabelled posts?

Question: Pooling randomized experiments published from 2023 to 2026, including those testing 2025–26 frontier models, how large is the persuasive effect of AI messages and conversations, relative to no message and to human persuaders, and how does it vary with model generation, conversation format, message length, topic, country and outcome type (attitude, vote intention, behaviour, persistence at follow-up)?

Question: Among US academic teams that received National AI Research Resource (NAIRR) pilot allocations, compared with similar teams that did not, does access change reliance on proprietary model APIs, industry co-authorship and the share of compute-intensive work, and how much of the access delivered depends on private-sector in-kind resources?

Question: How does the open-weight share of language-model use estimated from OpenRouter compare with shares estimated from other observable sources (other inference marketplaces and hosts, model downloads, self-hosting tool registries, and a survey of organisations' production deployments), and which population does each source actually represent?

Question: When UK public-sector cloud contracts came up for renewal before and after the 2024 egress-fee waivers and the CMA cloud investigation, how often did buyers move workloads to a different provider or add a second one, and did switching differ for workloads tied to Microsoft software licensing?

Question: Among AI startups that raised money from Amazon, Microsoft or Google (directly or through their venture arms), compared with similar startups funded by independent investors, how much more likely are they to build on the investing firm's cloud and models, and does that tie persist or loosen in later funding rounds?

Question: For language-model inference since 2023, how much of the fall in the price of a fixed capability level reflects lower serving costs (hardware and algorithmic efficiency) and how much reflects narrowing margins under competition, estimated by comparing prices for identical open-weight models across competing hosts with their estimated serving costs and with proprietary models of similar capability?

Question: For announced public or sovereign AI compute projects in the EU and the Gulf, how many reach operation on schedule, and at each layer (chips, memory, data-centre operator, cloud software, models) which suppliers and which jurisdictions does the operating project depend on, compared with what was announced?

Question: After the Court of Justice's 2025 ruling that people subject to automated decisions are owed meaningful information about the procedure and principles actually applied, how many explanation and objection requests do data subjects make in a few high-exposure sectors (credit scoring, insurance, platform work), how do organizations answer them, and how many escalate to a data protection authority or court and with what outcome?

Question: For each EU and EEA country, what staff numbers and budgets have been planned and actually provided for the authorities that enforce the AI Act, how do these compare with the tasks each authority has been given, and how do they compare with the resourcing of the same country's data protection authority?

Question: Between before and after August 2025, did providers that signed the EU General-Purpose AI Code of Practice change their documented safety, transparency and copyright practices more than providers that signed only part of it or did not sign, when the same documents are scored with the same rubric over time?

Question: Using the successive public lists of filed generative-AI services and registered applications published by China's internet regulator, together with interviews with applicants and filing consultants, how often do filings go through rejection and rework before approval, how often do listed services later disappear, and how concentrated is the dependence of registered applications on a small number of filed base models?

Question: For AI products and features released between 2023 and 2028 by a broad set of providers (not only frontier labs), how often is availability in the EU delayed or withheld relative to the US, the UK and Switzerland, and do delays change at the dates when specific AI Act obligations become applicable and enforceable, separately from data-protection and competition-law events?

Question: Under New York City's bias-audit law for automated hiring tools, how do the costs and forms of compliance (commissioning an audit, relying on a vendor-supplied audit, narrowing the tool's use to fall outside the law, or doing nothing visible) differ by employer size, and do these differences favour large employers and large tool vendors?