urn:uuid:e4aec4d0-73c2-5277-82bf-80acd77e1c19 New debate versions, claim revisions and Radar updates. 2026-10-21T00:00:00Z SocioLens urn:uuid:a722cf9b-de44-5a9b-a994-4b1e80bf0107 2026-10-21T00:00:00Z

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.

urn:uuid:7c7b070b-ecca-5b10-8552-b26d4beb8e3b 2026-10-21T00:00:00Z

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.

urn:uuid:38d68a67-7480-589b-8164-99671890599f 2026-10-18T00:00:00Z

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

urn:uuid:0ac41e9e-927f-52c1-8102-7443f3eb7cea 2026-10-18T00:00:00Z

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

urn:uuid:0b01dcd1-03b0-5361-88a8-73083f3c0889 2026-10-17T00:00:00Z

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

urn:uuid:3e3ba63f-ffb9-5982-9b2a-216eef3ec9e9 2026-10-16T00:00:00Z

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?

urn:uuid:a116288a-d6c6-560f-8dd0-4f8e7c7fd45e 2026-10-16T00:00:00Z

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?

urn:uuid:04536b98-8d79-5e0d-94eb-37bf543b75d1 2026-10-15T00:00:00Z

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?

urn:uuid:3f3272d8-ee14-5fb2-82b2-fe8a79e49f1a 2026-10-15T00:00:00Z

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?

urn:uuid:253bd482-a330-5e36-b2c1-9c151d23388b 2026-10-15T00:00:00Z

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?

urn:uuid:a3ad5dff-b432-5d6a-bc43-11f6a33bd6d5 2026-10-14T00:00:00Z

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

urn:uuid:d3f7d835-fdba-5de5-91d0-f9667ff8f8e7 2026-10-14T00:00:00Z

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.

urn:uuid:7d4b2153-7734-59ed-af34-9ee9360ae543 2026-10-14T00:00:00Z

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.

urn:uuid:eb17ffd1-83ef-5a54-a385-e4ac57c9d641 2026-10-13T00:00:00Z

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.

urn:uuid:123f967b-fccb-59cf-b26a-5c603929a0c6 2026-10-13T00:00:00Z

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.

urn:uuid:476ae4d2-ec93-5697-ab09-59e08fae8ebc 2026-10-13T00:00:00Z

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.

urn:uuid:3755d307-3753-56c0-a063-21fa1500a8a0 2026-10-13T00:00:00Z

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.

urn:uuid:bc923090-8886-5f73-a419-9b5650eb3895 2026-10-13T00:00:00Z

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.

urn:uuid:fa72f85a-1041-58e8-b506-994b1f91516b 2026-10-13T00:00:00Z

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.

urn:uuid:ed438383-06c2-5a93-99ac-519c1febda04 2026-10-13T00:00:00Z

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).

urn:uuid:b6b8474c-721f-5f8a-be0a-7490529e15e9 2026-10-13T00:00:00Z

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.

urn:uuid:e45e89a7-6dcd-5688-9188-341e77865a9f 2026-10-07T00:00:00Z

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.

urn:uuid:8a377541-9d02-5d35-92c3-63f5c06ae009 2026-09-25T00:00:00Z

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

urn:uuid:84be7910-a30f-5542-a481-b6309f4dc31d 2026-09-25T00:00:00Z

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

urn:uuid:a4513e23-3db3-5c99-af8e-20ce69622ea7 2026-09-25T00:00:00Z

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

urn:uuid:e63ba49c-4f34-5768-83c9-9cff69c9b5b7 2026-09-25T00:00:00Z

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?

urn:uuid:b7e5f938-aab6-50fe-8f34-d6321dbed454 2026-09-25T00:00:00Z

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