1{"type":"atis-latch","atis":"","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8"}2{"type":"queue-operation","operation":"enqueue","timestamp":"2026-10-30T05:17:05.557Z","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","content":"Review"}3{"type":"queue-operation","operation":"dequeue","timestamp":"2026-10-30T05:17:05.563Z","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8"}4{"parentUuid":null,"isSidechain":false,"promptId":"ab45ffb4-36a0-4452-beaa-0c9bcf129718","type":"user","message":{"role":"user","content":"Review"},"uuid":"b2e400c2-185e-4d8a-b381-6c435fd8d25a","timestamp":"2026-10-30T05:17:05.568Z","permissionMode":"default","promptSource":"sdk","turnOrigin":"sdk","turnPosition":{"promptIndex":0,"turnIndex":1},"userType":"external","entrypoint":"sdk-cli","cwd":"/Users/simon-pierreboucher/wp29/runs/RC0255","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","version":"2.1.314","gitBranch":"HEAD"}5{"type":"api-request-shape","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","shapeHash":"e6e8a9346eda26c87e828574ad316b42ebca2f9e3199a1e3882648387913c0d2","timestamp":"2026-10-30T05:17:05.583Z","version":"2.1.314","shape":{"system":[{"type":"text","text":"You are Claude Code, Anthropic's official CLI for Claude, running within the Claude Agent SDK."},{"type":"text","text":"CWD: /Users/simon-pierreboucher/wp29/runs/RC0255\nDate: 2026-10-30\n\nYou are an independent scientific reviewer. In the current working directory, `TASK.md` describes a bounded scientific task and the directory `out/` contains the deliverables submitted by another assistant (you have not seen how they were produced and you must not look for their working transcript). There is no network access. Use `~/wp29/venv/bin/python` if you need to re-run or test code. Do not modify any file under `out/` except that you must create `out/review/review.json`.\n\nReview the deliverables against `TASK.md` only. Specifically check:\n1. Does `out/results.json` contain every required key with legitimately computed values? Re-run `out/analysis.py` in a scratch copy if needed and compare.\n2. Are the information-availability rules of `TASK.md` respected by the code (for example no use of future information, no use of forbidden inputs)? Read the code to verify; do not trust the report.\n3. Are the central claims in `out/report.md` and `out/claims.json` supported by the numbers in `out/results.json`, with appropriate uncertainty and caveats? Flag any claim that is stronger than the evidence.\n4. Are counts, exclusions, units, signs and magnitudes internally consistent? Are baseline comparisons present when the task requires them?\n5. Are limitations stated honestly? Is anything declared complete that is not?\n\nYou have no reference answers; do not guess what the \"right\" number is. Report only issues you can justify from the files. Write `out/review/review.json` as {\"verdict\": \"accept\"|\"revise\", \"issues\": [{\"id\": \"R1\", \"severity\": \"critical\"|\"major\"|\"minor\", \"location\": \"<file or key>\", \"issue\": \"...\", \"suggested_fix\": \"...\"}], \"summary\": \"...\"}. Use \"revise\" if there is at least one critical or major issue. Be concise and specific. 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the user's own instructions about these lines, such as a CLAUDE.md or memory rule, take precedence over this reminder, but do not add attribution lines this reminder leaves out):\n- End git commit messages with:\nCo-Authored-By: Claude Opus 5.5 <noreply@anthropic.com>\n- End pull request descriptions with:\n🤖 Generated with [Claude Code](https://claude.com/claude-code)\n</system-reminder>"}],"renderedRole":"user","renderedBesideToolResult":true,"userType":"external","entrypoint":"sdk-cli","cwd":"/Users/simon-pierreboucher/wp29/runs/RC0255","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","version":"2.1.314","gitBranch":"HEAD"}11{"type":"tools-used","tools":["Bash"],"sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8"}12{"parentUuid":"e3165205-ff88-4e16-9fc5-4b71d160d037","isSidechain":false,"message":{"model":"claude-opus-5-5","id":"msg_011CgXrXAL5uGTF9GmNZHTYT","type":"message","role":"assistant","content":[{"type":"tool_use","id":"toolu_01RSHLvM2WZhnZbVJtePt674","name":"Bash","input":{"command":"cat TASK.md; ls -la out; cat out/results.json; cat out/claims.json"},"caller":{"type":"direct"}}],"container":null,"stop_reason":"tool_use","stop_sequence":null,"stop_details":null,"usage":{"input_tokens":4,"cache_creation_input_tokens":716,"cache_read_input_tokens":1504,"output_tokens":76,"output_tokens_details":{"thinking_tokens":0},"server_tool_use":{"web_search_requests":0,"web_fetch_requests":0},"service_tier":"standard","cache_creation":{"ephemeral_1h_input_tokens":0,"ephemeral_5m_input_tokens":716},"inference_geo":"global","iterations":[],"speed":"standard","fallback_credit":null},"input_transformations":[],"diagnostics":null,"context_management":null},"apiBlockIndex":0,"requestId":"req_011CgXrXA9B9X2SBjpLuZG7S","requestRef":"9514a3e6-fa97-4c6b-bec8-8cefd243fb63","requestedModel":"claude-opus-5-5","type":"assistant","uuid":"672a5268-9a54-4db0-be2f-7edc9a9fc312","timestamp":"2026-10-30T05:17:07.406Z","effort":"medium","perTurnEffort":"medium","userType":"external","entrypoint":"sdk-cli","cwd":"/Users/simon-pierreboucher/wp29/runs/RC0255","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","version":"2.1.314","gitBranch":"HEAD"}13{"parentUuid":"672a5268-9a54-4db0-be2f-7edc9a9fc312","isSidechain":false,"promptId":"ab45ffb4-36a0-4452-beaa-0c9bcf129718","type":"user","message":{"role":"user","content":[{"tool_use_id":"toolu_01RSHLvM2WZhnZbVJtePt674","type":"tool_result","content":"# F4-conf-04 — Verifying a reference list against the cited source material\n\n## Scientific question\nA draft manuscript cites five open-access studies; for each, the reference list gives a bibliographic entry (authors, year, title, arXiv number) and the manuscript attributes to it a specific finding (\"cited_for\"). For each reference, check against the provided source extract whether (i) the title matches the document, (ii) the year is consistent with the document's submission date(s), and (iii) the attributed finding is actually stated in, or follows arithmetically from, the extract. A reference is **unverifiable** when the source material and the entry disagree on the title or year, or when the attributed finding is not supported by the source. The estimand is the set of unverifiable references, together with a per-reference record of the three checks and a locator for each finding check.\n\n## Inputs\n- `data/reference_list.json` — five references: {\"id\", \"entry\" (bibliographic string), \"cited_for\" (the attributed finding), \"source_file\" (the extract to check against)}.\n- `data/sources/arxiv-2609.27732v1.txt` — arXiv:2609.27732v1, Armendariz (2026), CC BY 4.0: abstract, Section 6 (Tables 6, 7), Table A19.\n- `data/sources/arxiv-2606.14621v1.txt` — arXiv:2606.14621v1, Li, Pearson-Merkowitz & Yokum (2026), CC BY 4.0: abstract, Section 3 (Table 2), Table 3.\n- `data/sources/arxiv-2603.03260v2.txt` — arXiv:2603.03260v2, Liu & Zhao (2026; v1 March 2026, v2 April 2026), CC BY 4.0: abstract, Section 3 (Tables 2, 3), Section 5.\n- `data/sources/arxiv-2505.04555v3.txt` — arXiv:2505.04555v3, Kanayama, Miyaji & Otani (v1 May 2025, v3 March 2026), CC BY 4.0: abstract, Appendix A.1 (Table 2).\n- `data/sources/arxiv-2510.03658v1.txt` — arXiv:2510.03658v1, Tossou (October 2025), CC BY 4.0: abstract, Section 4.1, Table 3.\n- Each extract begins with a provenance header giving the title, authors, arXiv identifier with version and submission dates (the \"Bibliographic record\" line); the body reproduces the document's own title line, abstract and the cited sections. `data/README.md` gives retrieval times, licences and SHA-256 values.\n\n## Information-availability rules\n- The extracts (header and body) are the only admissible evidence; do not use remembered content of the papers, their other versions, or external bibliographic databases.\n- Year check: an entry's year is consistent if it equals the year of the first arXiv submission or the year of the version reproduced in the extract (both given in the \"Bibliographic record\" line). Title check: minor typographic differences (capitalisation, punctuation, diacritics, \"and\" vs \"&\") are acceptable; a different title is not. Author formatting differences (initials, order within the printed order) are not grounds for flagging.\n- Finding check: every element of \"cited_for\" (magnitudes, uncertainty statements, timing, population) must be stated in or follow arithmetically from the extract.\n- A locator names the source id and the table (row/column) or section that decides the finding check.\n\n## Required outputs\n- `out/results.json` with the keys:\n\n| key | type | unit | meaning |\n|---|---|---|---|\n| `reference_checks` | object | — | {\"R1\": {\"title_matches\": true/false, \"year_matches\": true/false, \"finding_supported\": true/false, \"locator\": \"<source id | table/section>\", \"note\": \"<one sentence>\"}, …, \"R5\": {…}} |\n| `unverifiable_references` | array of strings | — | ids of the references that fail at least one check (empty list if none) |\n| `n_verified` | integer | — | number of references passing all three checks |\n| `task_id` | string | — | \"F4-conf-04\" |\n| `feasibility` | string | — | \"complete\", \"partial\" or \"infeasible\" — refers to the task as a whole |\n| `feasibility_reason` | string or null | — | explanation if not complete |\n| `data_issues` | array of {\"issue\",\"handling\"} | — | problems detected in the inputs (rendering defects, internal inconsistencies of a source, etc.) and how they were handled; empty list if none |\n| `n_input_rows` | object | lines / items | {file name: number of lines} for every file under `data/` that you read (text files: number of newline-terminated lines as reported by `wc -l`; JSON files: number of top-level items) |\n| `n_analysed` | integer or null | — | number of reported items (values, assertions, effects or references) you actually assessed |\n| `random_seed` | integer or null | — | null (no randomness is involved) |\n\n- `out/report.md` with the sections: Question; Data and exclusions; Method; Results; Uncertainty; Limitations and open issues.\n- `out/analysis.py` — running `~/wp29/venv/bin/python out/analysis.py` from the workspace root must regenerate `out/results.json` from `data/` only, deterministically (the script must print the header lines and table cells it relies on).\n- `out/claims.json` — a list of the central claims of the report: [{\"id\": \"C1\", \"text\": \"...\", \"results_keys\": [\"...\"], \"status\": \"supported\"|\"unsupported\"|\"not_evaluated\", \"caveat\": \"...\"}].\n\n## Constraints\n- No network access. Python: `~/wp29/venv/bin/python` (numpy, pandas, scipy, statsmodels available; the standard library is sufficient for this task). Do not modify `data/`.\n- The source extracts under `data/sources/` are the **only** admissible evidence. Do not rely on memory of the papers or on other versions of them; if a quantity is not in the extract, it is not available.\n- Report numbers exactly as printed in the source (same sign, same number of decimals); do not round or rescale printed values unless the key definition asks for a transformation.\n- This task is designed to be completed in well under 20 minutes of work.\ntotal 72\ndrwxr-xr-x 9 simon-pierreboucher staff 288 oct. 30 01:17 .\ndrwxr-xr-x 7 simon-pierreboucher staff 224 oct. 30 01:14 ..\n-rw-r--r-- 1 simon-pierreboucher staff 11953 oct. 30 01:15 analysis.py\n-rw-r--r-- 1 simon-pierreboucher staff 1471 oct. 30 01:16 claims.json\n-rw-r--r-- 1 simon-pierreboucher staff 136 oct. 30 01:14 exclusions.csv\n-rw-r--r-- 1 simon-pierreboucher staff 5331 oct. 30 01:16 report.md\n-rw-r--r-- 1 simon-pierreboucher staff 5733 oct. 30 01:15 results.json\ndrwxr-xr-x 2 simon-pierreboucher staff 64 oct. 30 01:17 review\ndrwxr-xr-x 8 simon-pierreboucher staff 256 oct. 30 01:16 state\n{\n \"task_id\": \"F4-conf-04\",\n \"reference_checks\": {\n \"R1\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"finding_supported\": true,\n \"locator\": \"arxiv-2609.27732v1 | Table 6, row ATT, column 5 km (with % change row; Section 6 text; abstract)\",\n \"note\": \"ATT -0.431** (SE 0.210) and -35.0% at 5 km are printed in Table 6, 5% significance is stated in the text, and the staggered DiD on Swiss hospital records is described in the abstract.\"\n },\n \"R2\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"finding_supported\": true,\n \"locator\": \"arxiv-2606.14621v1 | Table 2, column 'Average treatment effect estimate', rows Wage, Reemployment, Weeks on UI (N from abstract)\",\n \"note\": \"Table 2's ATE column prints $1,153 (95% CI [166, 2,141]), 1.47 pp and -1.99 weeks, and the abstract gives the preregistered RCT with N = 23,549.\"\n },\n \"R3\": {\n \"title_matches\": false,\n \"year_matches\": false,\n \"finding_supported\": false,\n \"locator\": \"arxiv-2603.03260v2 | Section 3.2 'Headline dynamic pattern' (stacked coefficients tau=0..5) and Table 3, row Clean-onset threshold-2, columns tau=4/tau=5\",\n \"note\": \"The extract reports a gradual rise from 0.005 (about 0.5%) at the event year to 0.037/0.034 (3.4-3.7%) only by years four and five and states prices do not jump immediately, contradicting a 3.4-3.7% jump in the entry year with no later appreciation; title and year (2024) also disagree with the record.\"\n },\n \"R4\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"finding_supported\": true,\n \"locator\": \"arxiv-2505.04555v3 | Appendix A.1, Table 2, rows 'Employment elasticity w.r.t MW' and 'Emp. elasticity w.r.t affected wage' (Japan spot market from abstract)\",\n \"note\": \"Table 2 prints -0.388 (0.132) and -0.732 (0.091), the text calls the latter the own-wage employment elasticity, and the abstract places the study in Japan's spot labor market.\"\n },\n \"R5\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"finding_supported\": true,\n \"locator\": \"arxiv-2510.03658v1 | Table 3, row Treatment, column (4) (with % Change and Mean Dep. Var. rows; Section 4.1 text)\",\n \"note\": \"Table 3 column (4), identified as the preferred specification in Section 4.1, prints -0.0962 (0.0129) and a -0.3685 change relative to the mean 0.261, matching the 36.85% stated in the text.\"\n }\n },\n \"unverifiable_references\": [\n \"R3\"\n ],\n \"n_verified\": 4,\n \"feasibility\": \"complete\",\n \"feasibility_reason\": null,\n \"data_issues\": [\n {\n \"issue\": \"arxiv-2609.27732v1: the 5 km CS-DR ATT -0.431 has SE 0.210 in Table 6 but SE 0.218 in Table A19; Table 6 reports 608 never-treated control regions while the Table A19 note says 640.\",\n \"handling\": \"R1 cites Table 6 (SE 0.210), which is printed verbatim; finding judged supported, and with either SE |t| > 1.96 so the 5% significance claim is unaffected. Inconsistency reported, not resolved.\"\n },\n {\n \"issue\": \"arxiv-2609.27732v1: abstract says fatal outcomes fall by 35%, Section 6.1 says approximately 30%; exp(-0.354)-1 = -29.8% from Table 7.\",\n \"handling\": \"Not part of any cited finding; recorded only.\"\n },\n {\n \"issue\": \"arxiv-2505.04555v3: the SE of the own-wage elasticity (0.091) equals the SE of 'Affected employment' (0.091); the point estimate -0.732 = -0.268/0.366 is reproduced but the SE cannot be checked from the extract.\",\n \"handling\": \"R4 quotes the printed value (0.091); judged supported as stated in the source, possible source typo flagged. The table note's 'about 4%' MW increase vs the '% MW changes' row 0.047 is also noted.\"\n },\n {\n \"issue\": \"arxiv-2603.03260v2: Table 3 header row is garbled in the HTML rendering (column order reconstructed by the extract editor).\",\n \"handling\": \"Used the editor's column order; the tau=4/tau=5 values 0.037/0.034 match the Section 3.2 text, so the reconstruction is corroborated.\"\n },\n {\n \"issue\": \"arxiv-2510.03658v1: abstract headline (0.0855, 18.79%, Table 2 not in extract, mean 0.455) differs from Table 3 (binary outcome, 0.0962, 36.85%, mean 0.261).\",\n \"handling\": \"Different outcome definitions per Section 4.1; R5 cites the Table 3 result, which is checked directly. Recorded only.\"\n },\n {\n \"issue\": \"arxiv-2606.14621v1: Tables 2 and 3 were re-set by the extract editor (values stated verbatim).\",\n \"handling\": \"Values taken as printed; Table 3 column 1 duplicates Table 2's ATE column, providing a cross-check (identical values).\"\n }\n ],\n \"n_input_rows\": {\n \"README.md\": 17,\n \"reference_list.json\": 5,\n \"sources/arxiv-2609.27732v1.txt\": 134,\n \"sources/arxiv-2606.14621v1.txt\": 58,\n \"sources/arxiv-2603.03260v2.txt\": 107,\n \"sources/arxiv-2505.04555v3.txt\": 66,\n \"sources/arxiv-2510.03658v1.txt\": 91\n },\n \"n_analysed\": 5,\n \"random_seed\": null,\n \"baseline_naive_number_match\": {\n \"R1\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"all_cited_numbers_found\": true,\n \"numbers_not_found\": []\n },\n \"R2\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"all_cited_numbers_found\": true,\n \"numbers_not_found\": []\n },\n \"R3\": {\n \"title_matches\": false,\n \"year_matches\": false,\n \"all_cited_numbers_found\": true,\n \"numbers_not_found\": []\n },\n \"R4\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"all_cited_numbers_found\": true,\n \"numbers_not_found\": []\n },\n \"R5\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"all_cited_numbers_found\": true,\n \"numbers_not_found\": []\n }\n },\n \"n_evidence_strings_verified\": 26\n}[\n {\"id\":\"C1\",\"text\":\"Exactly one reference, R3, is unverifiable; the other four (R1, R2, R4, R5) pass all three checks.\",\"results_keys\":[\"unverifiable_references\",\"n_verified\",\"reference_checks\"],\"status\":\"supported\",\"caveat\":\"Finding checks involve the analyst's reading of the extract; evidence strings and arithmetic are verified by the script.\"},\n {\"id\":\"C2\",\"text\":\"R3's entry title and year (2024) disagree with the extract's record (different title; v1 and v2 both 2026).\",\"results_keys\":[\"reference_checks\"],\"status\":\"supported\",\"caveat\":\"\"},\n {\"id\":\"C3\",\"text\":\"R3's attributed finding misstates timing: the extract reports about 0.5% in the event year rising gradually to 3.4-3.7% by years four and five, not an immediate jump with no later appreciation.\",\"results_keys\":[\"reference_checks\"],\"status\":\"supported\",\"caveat\":\"Locator: Section 3.2 and Table 3, Clean-onset threshold-2 row.\"},\n {\"id\":\"C4\",\"text\":\"R1's cited ATT -0.431 (SE 0.210) matches Table 6, though Table A19 prints SE 0.218 for the same estimate; this inconsistency does not change the verdict.\",\"results_keys\":[\"reference_checks\",\"data_issues\"],\"status\":\"supported\",\"caveat\":\"Source-internal inconsistency unresolved.\"},\n {\"id\":\"C5\",\"text\":\"A naive number-match baseline finds all cited numbers in every extract and would not detect R3's timing misattribution.\",\"results_keys\":[\"baseline_naive_number_match\"],\"status\":\"supported\",\"caveat\":\"R3 is flagged anyway by title and year checks.\"}\n]","is_error":false}]},"uuid":"ab36028d-cd76-46e1-abef-42931de22232","timestamp":"2026-10-30T05:17:07.464Z","toolUseResult":{"stdout":"# F4-conf-04 — Verifying a reference list against the cited source material\n\n## Scientific question\nA draft manuscript cites five open-access studies; for each, the reference list gives a bibliographic entry (authors, year, title, arXiv number) and the manuscript attributes to it a specific finding (\"cited_for\"). For each reference, check against the provided source extract whether (i) the title matches the document, (ii) the year is consistent with the document's submission date(s), and (iii) the attributed finding is actually stated in, or follows arithmetically from, the extract. A reference is **unverifiable** when the source material and the entry disagree on the title or year, or when the attributed finding is not supported by the source. The estimand is the set of unverifiable references, together with a per-reference record of the three checks and a locator for each finding check.\n\n## Inputs\n- `data/reference_list.json` — five references: {\"id\", \"entry\" (bibliographic string), \"cited_for\" (the attributed finding), \"source_file\" (the extract to check against)}.\n- `data/sources/arxiv-2609.27732v1.txt` — arXiv:2609.27732v1, Armendariz (2026), CC BY 4.0: abstract, Section 6 (Tables 6, 7), Table A19.\n- `data/sources/arxiv-2606.14621v1.txt` — arXiv:2606.14621v1, Li, Pearson-Merkowitz & Yokum (2026), CC BY 4.0: abstract, Section 3 (Table 2), Table 3.\n- `data/sources/arxiv-2603.03260v2.txt` — arXiv:2603.03260v2, Liu & Zhao (2026; v1 March 2026, v2 April 2026), CC BY 4.0: abstract, Section 3 (Tables 2, 3), Section 5.\n- `data/sources/arxiv-2505.04555v3.txt` — arXiv:2505.04555v3, Kanayama, Miyaji & Otani (v1 May 2025, v3 March 2026), CC BY 4.0: abstract, Appendix A.1 (Table 2).\n- `data/sources/arxiv-2510.03658v1.txt` — arXiv:2510.03658v1, Tossou (October 2025), CC BY 4.0: abstract, Section 4.1, Table 3.\n- Each extract begins with a provenance header giving the title, authors, arXiv identifier with version and submission dates (the \"Bibliographic record\" line); the body reproduces the document's own title line, abstract and the cited sections. `data/README.md` gives retrieval times, licences and SHA-256 values.\n\n## Information-availability rules\n- The extracts (header and body) are the only admissible evidence; do not use remembered content of the papers, their other versions, or external bibliographic databases.\n- Year check: an entry's year is consistent if it equals the year of the first arXiv submission or the year of the version reproduced in the extract (both given in the \"Bibliographic record\" line). Title check: minor typographic differences (capitalisation, punctuation, diacritics, \"and\" vs \"&\") are acceptable; a different title is not. Author formatting differences (initials, order within the printed order) are not grounds for flagging.\n- Finding check: every element of \"cited_for\" (magnitudes, uncertainty statements, timing, population) must be stated in or follow arithmetically from the extract.\n- A locator names the source id and the table (row/column) or section that decides the finding check.\n\n## Required outputs\n- `out/results.json` with the keys:\n\n| key | type | unit | meaning |\n|---|---|---|---|\n| `reference_checks` | object | — | {\"R1\": {\"title_matches\": true/false, \"year_matches\": true/false, \"finding_supported\": true/false, \"locator\": \"<source id | table/section>\", \"note\": \"<one sentence>\"}, …, \"R5\": {…}} |\n| `unverifiable_references` | array of strings | — | ids of the references that fail at least one check (empty list if none) |\n| `n_verified` | integer | — | number of references passing all three checks |\n| `task_id` | string | — | \"F4-conf-04\" |\n| `feasibility` | string | — | \"complete\", \"partial\" or \"infeasible\" — refers to the task as a whole |\n| `feasibility_reason` | string or null | — | explanation if not complete |\n| `data_issues` | array of {\"issue\",\"handling\"} | — | problems detected in the inputs (rendering defects, internal inconsistencies of a source, etc.) and how they were handled; empty list if none |\n| `n_input_rows` | object | lines / items | {file name: number of lines} for every file under `data/` that you read (text files: number of newline-terminated lines as reported by `wc -l`; JSON files: number of top-level items) |\n| `n_analysed` | integer or null | — | number of reported items (values, assertions, effects or references) you actually assessed |\n| `random_seed` | integer or null | — | null (no randomness is involved) |\n\n- `out/report.md` with the sections: Question; Data and exclusions; Method; Results; Uncertainty; Limitations and open issues.\n- `out/analysis.py` — running `~/wp29/venv/bin/python out/analysis.py` from the workspace root must regenerate `out/results.json` from `data/` only, deterministically (the script must print the header lines and table cells it relies on).\n- `out/claims.json` — a list of the central claims of the report: [{\"id\": \"C1\", \"text\": \"...\", \"results_keys\": [\"...\"], \"status\": \"supported\"|\"unsupported\"|\"not_evaluated\", \"caveat\": \"...\"}].\n\n## Constraints\n- No network access. Python: `~/wp29/venv/bin/python` (numpy, pandas, scipy, statsmodels available; the standard library is sufficient for this task). Do not modify `data/`.\n- The source extracts under `data/sources/` are the **only** admissible evidence. Do not rely on memory of the papers or on other versions of them; if a quantity is not in the extract, it is not available.\n- Report numbers exactly as printed in the source (same sign, same number of decimals); do not round or rescale printed values unless the key definition asks for a transformation.\n- This task is designed to be completed in well under 20 minutes of work.\ntotal 72\ndrwxr-xr-x 9 simon-pierreboucher staff 288 oct. 30 01:17 .\ndrwxr-xr-x 7 simon-pierreboucher staff 224 oct. 30 01:14 ..\n-rw-r--r-- 1 simon-pierreboucher staff 11953 oct. 30 01:15 analysis.py\n-rw-r--r-- 1 simon-pierreboucher staff 1471 oct. 30 01:16 claims.json\n-rw-r--r-- 1 simon-pierreboucher staff 136 oct. 30 01:14 exclusions.csv\n-rw-r--r-- 1 simon-pierreboucher staff 5331 oct. 30 01:16 report.md\n-rw-r--r-- 1 simon-pierreboucher staff 5733 oct. 30 01:15 results.json\ndrwxr-xr-x 2 simon-pierreboucher staff 64 oct. 30 01:17 review\ndrwxr-xr-x 8 simon-pierreboucher staff 256 oct. 30 01:16 state\n{\n \"task_id\": \"F4-conf-04\",\n \"reference_checks\": {\n \"R1\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"finding_supported\": true,\n \"locator\": \"arxiv-2609.27732v1 | Table 6, row ATT, column 5 km (with % change row; Section 6 text; abstract)\",\n \"note\": \"ATT -0.431** (SE 0.210) and -35.0% at 5 km are printed in Table 6, 5% significance is stated in the text, and the staggered DiD on Swiss hospital records is described in the abstract.\"\n },\n \"R2\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"finding_supported\": true,\n \"locator\": \"arxiv-2606.14621v1 | Table 2, column 'Average treatment effect estimate', rows Wage, Reemployment, Weeks on UI (N from abstract)\",\n \"note\": \"Table 2's ATE column prints $1,153 (95% CI [166, 2,141]), 1.47 pp and -1.99 weeks, and the abstract gives the preregistered RCT with N = 23,549.\"\n },\n \"R3\": {\n \"title_matches\": false,\n \"year_matches\": false,\n \"finding_supported\": false,\n \"locator\": \"arxiv-2603.03260v2 | Section 3.2 'Headline dynamic pattern' (stacked coefficients tau=0..5) and Table 3, row Clean-onset threshold-2, columns tau=4/tau=5\",\n \"note\": \"The extract reports a gradual rise from 0.005 (about 0.5%) at the event year to 0.037/0.034 (3.4-3.7%) only by years four and five and states prices do not jump immediately, contradicting a 3.4-3.7% jump in the entry year with no later appreciation; title and year (2024) also disagree with the record.\"\n },\n \"R4\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"finding_supported\": true,\n \"locator\": \"arxiv-2505.04555v3 | Appendix A.1, Table 2, rows 'Employment elasticity w.r.t MW' and 'Emp. elasticity w.r.t affected wage' (Japan spot market from abstract)\",\n \"note\": \"Table 2 prints -0.388 (0.132) and -0.732 (0.091), the text calls the latter the own-wage employment elasticity, and the abstract places the study in Japan's spot labor market.\"\n },\n \"R5\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"finding_supported\": true,\n \"locator\": \"arxiv-2510.03658v1 | Table 3, row Treatment, column (4) (with % Change and Mean Dep. Var. rows; Section 4.1 text)\",\n \"note\": \"Table 3 column (4), identified as the preferred specification in Section 4.1, prints -0.0962 (0.0129) and a -0.3685 change relative to the mean 0.261, matching the 36.85% stated in the text.\"\n }\n },\n \"unverifiable_references\": [\n \"R3\"\n ],\n \"n_verified\": 4,\n \"feasibility\": \"complete\",\n \"feasibility_reason\": null,\n \"data_issues\": [\n {\n \"issue\": \"arxiv-2609.27732v1: the 5 km CS-DR ATT -0.431 has SE 0.210 in Table 6 but SE 0.218 in Table A19; Table 6 reports 608 never-treated control regions while the Table A19 note says 640.\",\n \"handling\": \"R1 cites Table 6 (SE 0.210), which is printed verbatim; finding judged supported, and with either SE |t| > 1.96 so the 5% significance claim is unaffected. Inconsistency reported, not resolved.\"\n },\n {\n \"issue\": \"arxiv-2609.27732v1: abstract says fatal outcomes fall by 35%, Section 6.1 says approximately 30%; exp(-0.354)-1 = -29.8% from Table 7.\",\n \"handling\": \"Not part of any cited finding; recorded only.\"\n },\n {\n \"issue\": \"arxiv-2505.04555v3: the SE of the own-wage elasticity (0.091) equals the SE of 'Affected employment' (0.091); the point estimate -0.732 = -0.268/0.366 is reproduced but the SE cannot be checked from the extract.\",\n \"handling\": \"R4 quotes the printed value (0.091); judged supported as stated in the source, possible source typo flagged. The table note's 'about 4%' MW increase vs the '% MW changes' row 0.047 is also noted.\"\n },\n {\n \"issue\": \"arxiv-2603.03260v2: Table 3 header row is garbled in the HTML rendering (column order reconstructed by the extract editor).\",\n \"handling\": \"Used the editor's column order; the tau=4/tau=5 values 0.037/0.034 match the Section 3.2 text, so the reconstruction is corroborated.\"\n },\n {\n \"issue\": \"arxiv-2510.03658v1: abstract headline (0.0855, 18.79%, Table 2 not in extract, mean 0.455) differs from Table 3 (binary outcome, 0.0962, 36.85%, mean 0.261).\",\n \"handling\": \"Different outcome definitions per Section 4.1; R5 cites the Table 3 result, which is checked directly. Recorded only.\"\n },\n {\n \"issue\": \"arxiv-2606.14621v1: Tables 2 and 3 were re-set by the extract editor (values stated verbatim).\",\n \"handling\": \"Values taken as printed; Table 3 column 1 duplicates Table 2's ATE column, providing a cross-check (identical values).\"\n }\n ],\n \"n_input_rows\": {\n \"README.md\": 17,\n \"reference_list.json\": 5,\n \"sources/arxiv-2609.27732v1.txt\": 134,\n \"sources/arxiv-2606.14621v1.txt\": 58,\n \"sources/arxiv-2603.03260v2.txt\": 107,\n \"sources/arxiv-2505.04555v3.txt\": 66,\n \"sources/arxiv-2510.03658v1.txt\": 91\n },\n \"n_analysed\": 5,\n \"random_seed\": null,\n \"baseline_naive_number_match\": {\n \"R1\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"all_cited_numbers_found\": true,\n \"numbers_not_found\": []\n },\n \"R2\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"all_cited_numbers_found\": true,\n \"numbers_not_found\": []\n },\n \"R3\": {\n \"title_matches\": false,\n \"year_matches\": false,\n \"all_cited_numbers_found\": true,\n \"numbers_not_found\": []\n },\n \"R4\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"all_cited_numbers_found\": true,\n \"numbers_not_found\": []\n },\n \"R5\": {\n \"title_matches\": true,\n \"year_matches\": true,\n \"all_cited_numbers_found\": true,\n \"numbers_not_found\": []\n }\n },\n \"n_evidence_strings_verified\": 26\n}[\n {\"id\":\"C1\",\"text\":\"Exactly one reference, R3, is unverifiable; the other four (R1, R2, R4, R5) pass all three checks.\",\"results_keys\":[\"unverifiable_references\",\"n_verified\",\"reference_checks\"],\"status\":\"supported\",\"caveat\":\"Finding checks involve the analyst's reading of the extract; evidence strings and arithmetic are verified by the script.\"},\n {\"id\":\"C2\",\"text\":\"R3's entry title and year (2024) disagree with the extract's record (different title; v1 and v2 both 2026).\",\"results_keys\":[\"reference_checks\"],\"status\":\"supported\",\"caveat\":\"\"},\n {\"id\":\"C3\",\"text\":\"R3's attributed finding misstates timing: the extract reports about 0.5% in the event year rising gradually to 3.4-3.7% by years four and five, not an immediate jump with no later appreciation.\",\"results_keys\":[\"reference_checks\"],\"status\":\"supported\",\"caveat\":\"Locator: Section 3.2 and Table 3, Clean-onset threshold-2 row.\"},\n {\"id\":\"C4\",\"text\":\"R1's cited ATT -0.431 (SE 0.210) matches Table 6, though Table A19 prints SE 0.218 for the same estimate; 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(2026). Do Drug Consumption Rooms Reduce Drug-Related Hospitalizations? Evidence from Switzerland. arXiv:2609.27732.\",\n \"cited_for\": \"Drug consumption room openings reduce drug-related hospitalisation rates by roughly 35% within 5 km of a facility (ATT −0.431, SE 0.210, significant at the 5% level), using a staggered difference-in-differences design on Swiss hospital records.\",\n \"source_file\": \"sources/arxiv-2609.27732v1.txt\"\n },\n {\n \"id\": \"R2\",\n \"entry\": \"Li, H. H., Pearson-Merkowitz, S., & Yokum, D. (2026). Evaluating the Impact of Rhode Island's Self-Sustaining Reemployment Services and Eligibility Assessment (RESEA) Program on Employment Outcomes. arXiv:2606.14621.\",\n \"cited_for\": \"In a preregistered randomised controlled trial (N = 23,549), selection into RESEA raised annualised wages by $1,153 (95% CI [166, 2,141]), raised reemployment by 1.47 percentage points and reduced weeks on UI by 1.99 weeks.\",\n \"source_file\": \"sources/arxiv-2606.14621v1.txt\"\n },\n {\n \"id\": \"R3\",\n \"entry\": \"Liu, W., & Zhao, R. (2024). Restaurants, Cafés and Neighbourhood Change: Commercial Entry and House Prices in Greater London. arXiv:2603.03260.\",\n \"cited_for\": \"Local house prices jump by 3.4–3.7% in the year in which food-and-drink establishments enter an LSOA, with no further appreciation in later years.\",\n \"source_file\": \"sources/arxiv-2603.03260v2.txt\"\n },\n {\n \"id\": \"R4\",\n \"entry\": \"Kanayama, H., Miyaji, S., & Otani, S. (2025). Just After Minimum Wage Hikes: Short-Run Labor-Demand Response and Reallocation. arXiv:2505.04555.\",\n \"cited_for\": \"In Japan's spot labour market, the employment elasticity with respect to the minimum wage is −0.388 (SE 0.132) and the own-wage employment elasticity is −0.732 (SE 0.091).\",\n \"source_file\": \"sources/arxiv-2505.04555v3.txt\"\n },\n {\n \"id\": \"R5\",\n \"entry\": \"Tossou, S. C. (2025). Who benefits the most? Direct and indirect effects of a free cesarean section policy in Benin. arXiv:2510.03658.\",\n \"cited_for\": \"Access to Benin's free cesarean section policy reduces the probability of infant death or stillbirth by 0.0962 (SE 0.0129) in the preferred specification, a 36.85% reduction relative to the mean of the dependent variable.\",\n \"source_file\": \"sources/arxiv-2510.03658v1.txt\"\n }\n]\n# Data provenance — F4-conf-04\n\nAll files under `data/sources/` are plain-text extracts of publicly accessible documents, prepared by the task designer on 2026-10-30 (UTC). Each extract begins with a provenance header (title, authors, bibliographic record, retrieval URL and UTC, SHA-256 of the retrieved HTML, license, list of included and omitted sections). Only the excerpts needed for the task are reproduced; everything else is omitted. Tables are rendered one row per line with ` | ` between cells; in regression tables, the line following a coefficient row holds the standard errors in parentheses as printed in the original.\n\n| file | document | retrieval UTC | license | SHA-256 of the extract |\n|---|---|---|---|---|\n| `sources/arxiv-2609.27732v1.txt` | Armendariz, A. (2026). Do Drug Consumption Rooms Reduce Drug-Related Hospitalizations? Evidence from Switzerland. arXiv:2609.27732v1 [econ.GN]. https://arxiv.org/abs/2609.27732v1 (full text: https://arxiv.org/html/2609.27732v1) | 2026-10-30T03:23:18Z | CC BY 4.0 | ee2d444d2f78f2af2ca2cf69b59a61fcd7ac5e10ea29e8ddcd67917bf07d6a8b |\n| `sources/arxiv-2606.14621v1.txt` | Li, H. H., Pearson-Merkowitz, S., & Yokum, D. (2026). Evaluating the Impact of Rhode Island's Self-Sustaining Reemployment Services and Eligibility Assessment (RESEA) Program on Employment Outcomes. arXiv:2606.14621v1 [econ.GN]. https://arxiv.org/abs/2606.14621v1 (full text: https://arxiv.org/html/2606.14621v1) | 2026-10-30T03:23:18Z | CC BY 4.0 | 27c463c0a144d9d5a3916dc641f15b6029f6c68b5e574ad9074e7df1aeb0a238 |\n| `sources/arxiv-2603.03260v2.txt` | Liu, W., & Zhao, R. (2026). Does Entry of Food-and-Drink Establishments Raise Local House Prices? Event-Study Evidence from London. arXiv:2603.03260v2 [physics.soc-ph, econ.GN], v2 of 2 Apr 2026. https://arxiv.org/abs/2603.03260v2 (full text: https://arxiv.org/html/2603.03260v2) | 2026-10-30T03:23:18Z | CC BY 4.0 | 3cb9a4f3574e7b2272fe19cde165a745543883f86beb9342f6fc0ab744c31551 |\n| `sources/arxiv-2505.04555v3.txt` | Kanayama, H., Miyaji, S., & Otani, S. (2025/2026). Just After Minimum Wage Hikes: Short-Run Labor-Demand Response and Reallocation. arXiv:2505.04555v3 [econ.GN], v1 of 7 May 2025, v3 of 16 Mar 2026. https://arxiv.org/abs/2505.04555v3 (full text: https://arxiv.org/html/2505.04555v3) | 2026-10-30T03:23:18Z | CC BY 4.0 | b1731a9b1c40ae91c6be2cf2e92623bb6cf86c551587936a0270356f76ae95c1 |\n| `sources/arxiv-2510.03658v1.txt` | Tossou, S. C. (2025). Who benefits the most? Direct and indirect effects of a free cesarean section policy in Benin. arXiv:2510.03658v1 [econ.GN]. https://arxiv.org/abs/2510.03658v1 (full text: https://arxiv.org/html/2510.03658v1) | 2026-10-30T03:23:18Z | CC BY 4.0 | f8782937eeaebd2dae0e653bbfc6aeb266c51587d09a4207bcaa3fa48a881127 |\n\nTask-specific input files (prepared by the task designer, not observed data):\n\n- `reference_list.json` — the five bibliographic entries with the finding attributed to each and the extract to check against, written by the task designer\n\nRights: arXiv e-prints are reproduced in part under the Creative Commons Attribution 4.0 licence shown on their arXiv abstract pages. No numbers were altered; where a table was re-set for legibility (RESEA Tables 2-3, London Table 3 header) the extract header says so.\n 66 data/sources/arxiv-2505.04555v3.txt\n 91 data/sources/arxiv-2510.03658v1.txt\n 107 data/sources/arxiv-2603.03260v2.txt\n 58 data/sources/arxiv-2606.14621v1.txt\n 134 data/sources/arxiv-2609.27732v1.txt\n 17 data/README.md\n 473 total","is_error":false}]},"uuid":"eba9b8fe-9591-43e4-94a8-e078c2267afb","timestamp":"2026-10-30T05:17:09.211Z","toolUseResult":{"stdout":"[\n {\n \"id\": \"R1\",\n \"entry\": \"Armendariz, A. (2026). Do Drug Consumption Rooms Reduce Drug-Related Hospitalizations? Evidence from Switzerland. arXiv:2609.27732.\",\n \"cited_for\": \"Drug consumption room openings reduce drug-related hospitalisation rates by roughly 35% within 5 km of a facility (ATT −0.431, SE 0.210, significant at the 5% level), using a staggered difference-in-differences design on Swiss hospital records.\",\n \"source_file\": \"sources/arxiv-2609.27732v1.txt\"\n },\n {\n \"id\": \"R2\",\n \"entry\": \"Li, H. H., Pearson-Merkowitz, S., & Yokum, D. (2026). Evaluating the Impact of Rhode Island's Self-Sustaining Reemployment Services and Eligibility Assessment (RESEA) Program on Employment Outcomes. arXiv:2606.14621.\",\n \"cited_for\": \"In a preregistered randomised controlled trial (N = 23,549), selection into RESEA raised annualised wages by $1,153 (95% CI [166, 2,141]), raised reemployment by 1.47 percentage points and reduced weeks on UI by 1.99 weeks.\",\n \"source_file\": \"sources/arxiv-2606.14621v1.txt\"\n },\n {\n \"id\": \"R3\",\n \"entry\": \"Liu, W., & Zhao, R. (2024). Restaurants, Cafés and Neighbourhood Change: Commercial Entry and House Prices in Greater London. arXiv:2603.03260.\",\n \"cited_for\": \"Local house prices jump by 3.4–3.7% in the year in which food-and-drink establishments enter an LSOA, with no further appreciation in later years.\",\n \"source_file\": \"sources/arxiv-2603.03260v2.txt\"\n },\n {\n \"id\": \"R4\",\n \"entry\": \"Kanayama, H., Miyaji, S., & Otani, S. (2025). Just After Minimum Wage Hikes: Short-Run Labor-Demand Response and Reallocation. arXiv:2505.04555.\",\n \"cited_for\": \"In Japan's spot labour market, the employment elasticity with respect to the minimum wage is −0.388 (SE 0.132) and the own-wage employment elasticity is −0.732 (SE 0.091).\",\n \"source_file\": \"sources/arxiv-2505.04555v3.txt\"\n },\n {\n \"id\": \"R5\",\n \"entry\": \"Tossou, S. C. (2025). Who benefits the most? Direct and indirect effects of a free cesarean section policy in Benin. arXiv:2510.03658.\",\n \"cited_for\": \"Access to Benin's free cesarean section policy reduces the probability of infant death or stillbirth by 0.0962 (SE 0.0129) in the preferred specification, a 36.85% reduction relative to the mean of the dependent variable.\",\n \"source_file\": \"sources/arxiv-2510.03658v1.txt\"\n }\n]\n# Data provenance — F4-conf-04\n\nAll files under `data/sources/` are plain-text extracts of publicly accessible documents, prepared by the task designer on 2026-10-30 (UTC). Each extract begins with a provenance header (title, authors, bibliographic record, retrieval URL and UTC, SHA-256 of the retrieved HTML, license, list of included and omitted sections). Only the excerpts needed for the task are reproduced; everything else is omitted. Tables are rendered one row per line with ` | ` between cells; in regression tables, the line following a coefficient row holds the standard errors in parentheses as printed in the original.\n\n| file | document | retrieval UTC | license | SHA-256 of the extract |\n|---|---|---|---|---|\n| `sources/arxiv-2609.27732v1.txt` | Armendariz, A. (2026). Do Drug Consumption Rooms Reduce Drug-Related Hospitalizations? Evidence from Switzerland. arXiv:2609.27732v1 [econ.GN]. https://arxiv.org/abs/2609.27732v1 (full text: https://arxiv.org/html/2609.27732v1) | 2026-10-30T03:23:18Z | CC BY 4.0 | ee2d444d2f78f2af2ca2cf69b59a61fcd7ac5e10ea29e8ddcd67917bf07d6a8b |\n| `sources/arxiv-2606.14621v1.txt` | Li, H. H., Pearson-Merkowitz, S., & Yokum, D. (2026). Evaluating the Impact of Rhode Island's Self-Sustaining Reemployment Services and Eligibility Assessment (RESEA) Program on Employment Outcomes. arXiv:2606.14621v1 [econ.GN]. https://arxiv.org/abs/2606.14621v1 (full text: https://arxiv.org/html/2606.14621v1) | 2026-10-30T03:23:18Z | CC BY 4.0 | 27c463c0a144d9d5a3916dc641f15b6029f6c68b5e574ad9074e7df1aeb0a238 |\n| `sources/arxiv-2603.03260v2.txt` | Liu, W., & Zhao, R. (2026). Does Entry of Food-and-Drink Establishments Raise Local House Prices? Event-Study Evidence from London. arXiv:2603.03260v2 [physics.soc-ph, econ.GN], v2 of 2 Apr 2026. https://arxiv.org/abs/2603.03260v2 (full text: https://arxiv.org/html/2603.03260v2) | 2026-10-30T03:23:18Z | CC BY 4.0 | 3cb9a4f3574e7b2272fe19cde165a745543883f86beb9342f6fc0ab744c31551 |\n| `sources/arxiv-2505.04555v3.txt` | Kanayama, H., Miyaji, S., & Otani, S. (2025/2026). Just After Minimum Wage Hikes: Short-Run Labor-Demand Response and Reallocation. arXiv:2505.04555v3 [econ.GN], v1 of 7 May 2025, v3 of 16 Mar 2026. https://arxiv.org/abs/2505.04555v3 (full text: https://arxiv.org/html/2505.04555v3) | 2026-10-30T03:23:18Z | CC BY 4.0 | b1731a9b1c40ae91c6be2cf2e92623bb6cf86c551587936a0270356f76ae95c1 |\n| `sources/arxiv-2510.03658v1.txt` | Tossou, S. C. (2025). Who benefits the most? Direct and indirect effects of a free cesarean section policy in Benin. arXiv:2510.03658v1 [econ.GN]. https://arxiv.org/abs/2510.03658v1 (full text: https://arxiv.org/html/2510.03658v1) | 2026-10-30T03:23:18Z | CC BY 4.0 | f8782937eeaebd2dae0e653bbfc6aeb266c51587d09a4207bcaa3fa48a881127 |\n\nTask-specific input files (prepared by the task designer, not observed data):\n\n- `reference_list.json` — the five bibliographic entries with the finding attributed to each and the extract to check against, written by the task designer\n\nRights: arXiv e-prints are reproduced in part under the Creative Commons Attribution 4.0 licence shown on their arXiv abstract pages. No numbers were altered; where a table was re-set for legibility (RESEA Tables 2-3, London Table 3 header) the extract header says so.\n 66 data/sources/arxiv-2505.04555v3.txt\n 91 data/sources/arxiv-2510.03658v1.txt\n 107 data/sources/arxiv-2603.03260v2.txt\n 58 data/sources/arxiv-2606.14621v1.txt\n 134 data/sources/arxiv-2609.27732v1.txt\n 17 data/README.md\n 473 total","stderr":"","interrupted":false,"isImage":false,"noOutputExpected":false},"sandboxed":false,"sourceToolAssistantUUID":"bcf2441f-2f42-417d-87cc-ebad0806b5d8","permissionDecision":{"decision":"accept","source":"config","reasonType":"rule","ruleSource":"cliArg"},"userType":"external","entrypoint":"sdk-cli","cwd":"/Users/simon-pierreboucher/wp29/runs/RC0255","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","version":"2.1.314","gitBranch":"HEAD"}21{"parentUuid":"eba9b8fe-9591-43e4-94a8-e078c2267afb","isSidechain":false,"message":{"model":"claude-opus-5-5","id":"msg_011CgXrXJNmc7eHonVdbiavF","type":"message","role":"assistant","content":[{"type":"tool_use","id":"toolu_01BwN9pgA7o2MUxsivNPxKUE","name":"Bash","input":{"command":"cat data/sources/arxiv-2609.27732v1.txt"},"caller":{"type":"direct"}}],"container":null,"stop_reason":"tool_use","stop_sequence":null,"stop_details":null,"usage":{"input_tokens":2,"cache_creation_input_tokens":5527,"cache_read_input_tokens":2220,"output_tokens":154,"output_tokens_details":{"thinking_tokens":0},"server_tool_use":{"web_search_requests":0,"web_fetch_requests":0},"service_tier":"standard","cache_creation":{"ephemeral_1h_input_tokens":0,"ephemeral_5m_input_tokens":5527},"inference_geo":"global","iterations":[],"speed":"standard","fallback_credit":null},"input_transformations":[],"diagnostics":null,"context_management":null},"apiBlockIndex":2,"requestId":"req_011CgXrXJ7QJgKKQ793RoPJ4","requestRef":"6b51df7a-c878-44bd-a041-8de6859db861","requestedModel":"claude-opus-5-5","type":"assistant","uuid":"7d18db6e-812e-4c03-b46f-e2b5845a7e87","timestamp":"2026-10-30T05:17:09.534Z","effort":"medium","perTurnEffort":"medium","userType":"external","entrypoint":"sdk-cli","cwd":"/Users/simon-pierreboucher/wp29/runs/RC0255","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","version":"2.1.314","gitBranch":"HEAD"}22{"parentUuid":"7d18db6e-812e-4c03-b46f-e2b5845a7e87","isSidechain":false,"promptId":"ab45ffb4-36a0-4452-beaa-0c9bcf129718","type":"user","message":{"role":"user","content":[{"tool_use_id":"toolu_01BwN9pgA7o2MUxsivNPxKUE","type":"tool_result","content":"SOURCE EXTRACT — arxiv-2609.27732v1\nTitle: Do Drug Consumption Rooms Reduce Drug-Related Hospitalizations? Evidence from Switzerland\nAuthors: Ana Armendariz (University of St. Gallen)\nBibliographic record: arXiv:2609.27732v1 [econ.GN], submitted 23 Sep 2026 (version 1, the only version at retrieval). Abstract page: https://arxiv.org/abs/2609.27732v1\nRetrieved: https://arxiv.org/html/2609.27732v1 on 2026-10-30T03:23:18Z (SHA-256 of the retrieved HTML: 22b06050f4ff6e665aedd80561fa4031b1717867ecfeca71d1d2902ee1b09f52)\nLicense: CC BY 4.0 (license shown on the arXiv abstract page; https://creativecommons.org/licenses/by/4.0/). Reproduced in part with attribution.\nExtract contents: title, author, date and abstract; Section 6 'Results' in full (Figure notes, Table 6, Table 7, Section 6.1 'Mechanisms'); Appendix Table A19 with its note and the paragraph that discusses it.\nOmitted: Sections 1-5 and 7, the other appendix tables and figures, the references.\nRendering note: converted from the HTML rendering to plain text. Tables are rendered one row per line with \" | \" separating cells; in regression tables the line following a coefficient row holds the standard errors in parentheses, exactly as printed. Mathematical expressions appear as LaTeX source; non-breaking spaces were replaced by ordinary spaces. No numbers were altered.\n================================================================\n\n# Do Drug Consumption Rooms Reduce Drug-Related Hospitalizations? Evidence from Switzerland\n\nAna Armendariz*\n\nSeptember 23, 2026\n\nThis paper estimates the causal effect of drug consumption room (DCR) openings on drug-related hospitalizations in Switzerland. I exploit the staggered introduction of DCRs across Swiss cities between 1998 and 2022, using individual-level hospital records and a difference-in-differences estimator. DCR openings reduce drug-related hospitalization rates by roughly 35% within 5 km of a facility. The reduction is most pronounced for fatal outcomes, which fall by 35% while narcotics poisoning hospitalizations rise by a comparable amount, consistent with DCRs converting potentially fatal overdoses into non-fatal hospitalizations. Mental and behavioral disorder hospitalizations decline by 32% while estimates for Hepatitis and HIV are imprecise. The findings support the role of DCRs as an effective harm reduction strategy.\n\nKeywords: Drug Consumption Rooms, Harm Reduction, Hospitalizations, Drugs, Public Health, Causal Inference\n\n## 6 Results\n\nThis section reports the effect of DCR openings on the rate of drug-related hospitalizations per 100,000 inhabitants. I begin with the event-study estimates and then present the overall pooled ATT. I then disaggregate the overall outcome into its sub-outcome categories and report the same estimates for each.\n\nFigure 6: Event study estimates by buffer zone, \\pm 5-year window\n\nNote: The figure plots event-study coefficients from the doubly robust estimator of Callaway and Sant’Anna (2021) for regions within 5 km of a DCR opening. The comparison group consists of never-treated regions (608 control regions). The outcome is the log drug-related hospitalization rate per 100,000 inhabitants. The sample includes all staggered-treated MedStat regions within 5 km of a DCR that opened between 1998 and 2022 and all never-treated regions. The estimation uses a \\pm 5-year window relative to DCR opening, with t=-5 and t=+5 representing pooled endpoint bins that absorb all periods beyond the window. The reference period is a universal base period. Regions near DCRs that opened before 1998 (always-treated) are excluded through out. 95% confidence intervals are based on standard errors clustered at the MedStat region level. Results for the 1 km and 3 km buffer specifications are reported in Appendix Figure A17.\n\nFigure 6 presents the event study estimates for the 5 km buffer specifications. I focus on the 5 km buffer specification, as it includes the largest number of treated regions and yields the most precise estimates. I summarize dynamic effects over a symmetric five year window around DCR openings. This window avoids relying on distant leads and lags that are informed by only a small subset of adopters. Pre-treatment coefficients are small and statistically insignificant, supporting the parallel trends assumption. The post-treatment coefficients are consistently negative, indicating a reduction in drug-related hospitalizations following DCR openings. The estimates of the overall summary of ATTs based on calendar time aggregation of Callaway and Sant’Anna (2021) is around -35% reduction in hospitalizations due to drugs.\n\nTable 6: Overall Average Treatment Effect on the Treated (ATT)\n\n| 1 km | 3 km | 5 km\n\nATT | -0.399 | -0.283 | -0.431**\n\n| (0.412) | (0.279) | (0.210)\n\n% change | -32.9% | -24.7% | -35.0%\n\nTreated regions | 7 | 35 | 50\n\nControl regions | 608 | 608 | 608\n\nObservations | 16,175 | 16,875 | 17,250\n\nNote: The table reports the overall ATT estimated using the doubly robust Callaway and Sant’Anna (2021) estimator with never-treated controls and a universal base period. The outcome is the log drug-related hospitalization rate per 100,000 inhabitants. Columns differ in the geographic buffer used to define treated Medstat regions. The control group consists of 608 never-treated Medstat regions\nthroughout. Regions near DCRs that opened before 1998\n(always-treated) are excluded. Standard errors clustered at the Medstat region level in\nparentheses. Significance: {}^{***}p<0.01 , {}^{**}p<0.05 ,\n{}^{*}p<0.10 .\n\nTable 6 reports the pooled ATT for the 1 km, 3 km and 5 km buffer specification, aggregating the dynamic treatment effects into a single estimate averaged across all post-treatment periods and cohorts. The 5 km specification, yields an ATT of -0.431\ncorresponding to a 35% reduction in the drug-related hospitalization rate. This estimate is statistically significant at the 5% level. The 3 km and 1 km estimates point in the same direction but are less precise, due to the smaller number of treated regions.\n\nTo further explore the mechanisms through which DCR openings affect drug-related hospitalizations, I disaggregate the main outcome into five diagnostic\nsub-categories: (i) mental and behavioral disorders due to psychoactive substance use, (ii) viral hepatitis, (iii) HIV, (iv) poisoning by narcotics and psychodysleptics, and (v) fatal drug-related hospitalizations. Accidental poisoning is excluded due to the very small number of cases.\n\nFigure 7: Event study: Sub-outcome estimates,\nwithin 5 km, \\pm 5-year window\n\nNote: The figure plots event-study coefficients from the doubly robust Callaway & Sant’Anna (2021) estimator for four diagnostic sub-categories of drug-related hospitalizations. Each panel uses a separate y -axis to accommodate differences in scale across outcomes. The sample includes all staggered-treated MedStat regions within 5 km of a\nDCR that opened between 1998 and 2022. The reference period is a universal base period. Regions near DCRs that opened before 1998 (always-treated) are excluded. 95% confidence intervals are based on standard errors clustered at the MedStat region level.\n\nTable 7: Overall ATT by Outcome Category and Buffer Zone\n\nOutcome | 1 km | 3 km | 5 km\n\nMental/Behavioral | -0.354 | -0.202 | -0.381*\n\n| (0.382) | (0.244) | (0.220)\n\nHepatitis | -0.270 | -0.413 | -0.406\n\n| (0.486) | (0.270) | (0.250)\n\nHIV | 0.063 | -0.239 | -0.340\n\n| (0.801) | (0.337) | (0.294)\n\nNarcotics | 1.186*** | 0.549*** | 0.390**\n\n| (0.288) | (0.187) | (0.165)\n\nDrug-related (fatal) | -1.207*** | -0.290 | -0.354**\n\n| (0.137) | (0.215) | (0.178)\n\nTreated regions | 7 | 35 | 50\n\nControl regions | 608 (never-treated) | |\n\nNote: Each cell reports the overall ATT from\nthe doubly robust Callaway & Sant’Anna (2021) estimator with\nnever-treated controls and a universal base period. Outcomes are\nlog hospitalization rates per 100,000 inhabitants. Sub-outcomes:\nmental and behavioral disorders (F11–F19), viral hepatitis (B15–B19),\nHIV disease (B20–B24), narcotics/psychodysleptics (T40). The 1 km\nestimates are identified from a single treated region per cohort and\nshould be interpreted with caution. Regions near DCRs opened before\n1998 excluded. Standard errors clustered at the Medstat region level.\nSignificance: {}^{***}p<0.01 , {}^{**}p<0.05 , {}^{*}p<0.10 .\n\nFigure 7 and Table 7 repeat the estimation for the five diagnostic categories. From Table 7, the ATT estimates for hospitalizations due to mental and behavioral disorders are consistently negative and marginally significant at the 5 km buffer specification. Moreover, the estimates of hepatitis are also negative and of comparable magnitude but insignificant. However, the event-study path in Figure 7 shows a gradual decline that builds from year 3 onward, consistent with a slow-acting reduction in needle sharing. HIV estimates are insignificant and close to zero. Narcotics poisoning hospitalizations rise after DCR opening and remain positive across all buffers. Lastly, fatal drug-related hospitalizations move in the opposite direction, falling after opening the DCR. The opposing patterns in narcotics and fatal hospitalizations suggest that DCRs convert events that would otherwise be fatal into survivable hospital contacts.\n\n### 6.1 Mechanisms\n\nThe sub-outcome results point to two channels through which DCRs reduce drug-related hospitalizations. The first is overdose supervision. DCRs provide a medically supervised environment where staff can control the dose consumed, perform resuscitation, and call emergency services when an overdose occurs. When supervision prevents a death that would otherwise happen outside a hospital, the consequence is a simultaneous decline in fatal drug-related hospitalizations and a rise in non-fatal poisoning contacts, as events that would have ended in death instead end in a hospital visit. The results are consistent with this prediction. Drug-related fatal hospitalizations fall near DCRs, by approximately 30% at 5 km, while narcotics and psychodysleptics hospitalizations rise by 47% at 5 km. The opposing signs and spatial concentration of these two effects are consistent with a\nsubstitution from out-of-hospital mortality to in-hospital survival. Since I cannot observe overdose events that do not result in a hospital contact, this interpretation is suggestive rather than identified, but it is consistent with the clinical evidence on DCR-based overdose reversals\n(Kerr et al., 2017; Hedrich, 2004).\n\nThe second channel is harm reduction for blood-borne diseases. DCRs distribute sterile injection equipment, which reduces needle sharing and the transmission of viral hepatitis and HIV. Unlike overdose prevention, these effects are expected to emerge slowly, since disease progression and hospitalization take years to follow from initial infection. The event-study path for hepatitis is consistent with this lag. The estimates are close to zero in the first two post-treatment years and become progressively more negative from year 3 onward, reaching approximately 40% below baseline by year 5. HIV estimates are near zero through out the analysis, with wide confidence intervals. A longer panel and additional out-patient data would be needed to determine whether these trends continue and to get more precise estimates.\n\nA third potential channel is referral to treatment and social services. DCRs routinely connect users to addiction treatment, primary care, and housing support, and a sustained reduction in hospitalizations could partly reflect better long-term management of drug dependence. The regional hospitalization panel used in this paper does not contain information on treatment entry or service use, so I cannot separate this channel from the two described above. It remains a plausible additional mechanism that future work with information on treatment take up data could examine.\n\nTable A19: Robustness: Overall ATT Across Estimators — 5 km buffer, \\pm 5-year window\n\n| CS-DR | Sun & Abraham | Synthetic DiD | Stacked DiD\n\nATT | -0.431** | -0.438** | -0.362* | -0.149***\n\n| (0.218) | (0.208) | (0.205) | (0.038)\n\n% change | -35.0% | -35.5% | -30.3% | -13.9%\n\nTreated regions | 50 | | |\n\nControl regions | 608 | | |\n\nObservations | 17,250 | | |\n\nNote: All specifications use the 5 km buffer,\nnever-treated comparison regions (640 regions), and a \\pm 5-year window","is_error":false}]},"uuid":"d4c7f84c-3139-46f9-88ea-8afc0390479b","timestamp":"2026-10-30T05:17:09.547Z","toolUseResult":{"stdout":"SOURCE EXTRACT — arxiv-2609.27732v1\nTitle: Do Drug Consumption Rooms Reduce Drug-Related Hospitalizations? Evidence from Switzerland\nAuthors: Ana Armendariz (University of St. Gallen)\nBibliographic record: arXiv:2609.27732v1 [econ.GN], submitted 23 Sep 2026 (version 1, the only version at retrieval). Abstract page: https://arxiv.org/abs/2609.27732v1\nRetrieved: https://arxiv.org/html/2609.27732v1 on 2026-10-30T03:23:18Z (SHA-256 of the retrieved HTML: 22b06050f4ff6e665aedd80561fa4031b1717867ecfeca71d1d2902ee1b09f52)\nLicense: CC BY 4.0 (license shown on the arXiv abstract page; https://creativecommons.org/licenses/by/4.0/). Reproduced in part with attribution.\nExtract contents: title, author, date and abstract; Section 6 'Results' in full (Figure notes, Table 6, Table 7, Section 6.1 'Mechanisms'); Appendix Table A19 with its note and the paragraph that discusses it.\nOmitted: Sections 1-5 and 7, the other appendix tables and figures, the references.\nRendering note: converted from the HTML rendering to plain text. Tables are rendered one row per line with \" | \" separating cells; in regression tables the line following a coefficient row holds the standard errors in parentheses, exactly as printed. Mathematical expressions appear as LaTeX source; non-breaking spaces were replaced by ordinary spaces. No numbers were altered.\n================================================================\n\n# Do Drug Consumption Rooms Reduce Drug-Related Hospitalizations? Evidence from Switzerland\n\nAna Armendariz*\n\nSeptember 23, 2026\n\nThis paper estimates the causal effect of drug consumption room (DCR) openings on drug-related hospitalizations in Switzerland. I exploit the staggered introduction of DCRs across Swiss cities between 1998 and 2022, using individual-level hospital records and a difference-in-differences estimator. DCR openings reduce drug-related hospitalization rates by roughly 35% within 5 km of a facility. The reduction is most pronounced for fatal outcomes, which fall by 35% while narcotics poisoning hospitalizations rise by a comparable amount, consistent with DCRs converting potentially fatal overdoses into non-fatal hospitalizations. Mental and behavioral disorder hospitalizations decline by 32% while estimates for Hepatitis and HIV are imprecise. The findings support the role of DCRs as an effective harm reduction strategy.\n\nKeywords: Drug Consumption Rooms, Harm Reduction, Hospitalizations, Drugs, Public Health, Causal Inference\n\n## 6 Results\n\nThis section reports the effect of DCR openings on the rate of drug-related hospitalizations per 100,000 inhabitants. I begin with the event-study estimates and then present the overall pooled ATT. I then disaggregate the overall outcome into its sub-outcome categories and report the same estimates for each.\n\nFigure 6: Event study estimates by buffer zone, \\pm 5-year window\n\nNote: The figure plots event-study coefficients from the doubly robust estimator of Callaway and Sant’Anna (2021) for regions within 5 km of a DCR opening. The comparison group consists of never-treated regions (608 control regions). The outcome is the log drug-related hospitalization rate per 100,000 inhabitants. The sample includes all staggered-treated MedStat regions within 5 km of a DCR that opened between 1998 and 2022 and all never-treated regions. The estimation uses a \\pm 5-year window relative to DCR opening, with t=-5 and t=+5 representing pooled endpoint bins that absorb all periods beyond the window. The reference period is a universal base period. Regions near DCRs that opened before 1998 (always-treated) are excluded through out. 95% confidence intervals are based on standard errors clustered at the MedStat region level. Results for the 1 km and 3 km buffer specifications are reported in Appendix Figure A17.\n\nFigure 6 presents the event study estimates for the 5 km buffer specifications. I focus on the 5 km buffer specification, as it includes the largest number of treated regions and yields the most precise estimates. I summarize dynamic effects over a symmetric five year window around DCR openings. This window avoids relying on distant leads and lags that are informed by only a small subset of adopters. Pre-treatment coefficients are small and statistically insignificant, supporting the parallel trends assumption. The post-treatment coefficients are consistently negative, indicating a reduction in drug-related hospitalizations following DCR openings. The estimates of the overall summary of ATTs based on calendar time aggregation of Callaway and Sant’Anna (2021) is around -35% reduction in hospitalizations due to drugs.\n\nTable 6: Overall Average Treatment Effect on the Treated (ATT)\n\n| 1 km | 3 km | 5 km\n\nATT | -0.399 | -0.283 | -0.431**\n\n| (0.412) | (0.279) | (0.210)\n\n% change | -32.9% | -24.7% | -35.0%\n\nTreated regions | 7 | 35 | 50\n\nControl regions | 608 | 608 | 608\n\nObservations | 16,175 | 16,875 | 17,250\n\nNote: The table reports the overall ATT estimated using the doubly robust Callaway and Sant’Anna (2021) estimator with never-treated controls and a universal base period. The outcome is the log drug-related hospitalization rate per 100,000 inhabitants. Columns differ in the geographic buffer used to define treated Medstat regions. The control group consists of 608 never-treated Medstat regions\nthroughout. Regions near DCRs that opened before 1998\n(always-treated) are excluded. Standard errors clustered at the Medstat region level in\nparentheses. Significance: {}^{***}p<0.01 , {}^{**}p<0.05 ,\n{}^{*}p<0.10 .\n\nTable 6 reports the pooled ATT for the 1 km, 3 km and 5 km buffer specification, aggregating the dynamic treatment effects into a single estimate averaged across all post-treatment periods and cohorts. The 5 km specification, yields an ATT of -0.431\ncorresponding to a 35% reduction in the drug-related hospitalization rate. This estimate is statistically significant at the 5% level. The 3 km and 1 km estimates point in the same direction but are less precise, due to the smaller number of treated regions.\n\nTo further explore the mechanisms through which DCR openings affect drug-related hospitalizations, I disaggregate the main outcome into five diagnostic\nsub-categories: (i) mental and behavioral disorders due to psychoactive substance use, (ii) viral hepatitis, (iii) HIV, (iv) poisoning by narcotics and psychodysleptics, and (v) fatal drug-related hospitalizations. Accidental poisoning is excluded due to the very small number of cases.\n\nFigure 7: Event study: Sub-outcome estimates,\nwithin 5 km, \\pm 5-year window\n\nNote: The figure plots event-study coefficients from the doubly robust Callaway & Sant’Anna (2021) estimator for four diagnostic sub-categories of drug-related hospitalizations. Each panel uses a separate y -axis to accommodate differences in scale across outcomes. The sample includes all staggered-treated MedStat regions within 5 km of a\nDCR that opened between 1998 and 2022. The reference period is a universal base period. Regions near DCRs that opened before 1998 (always-treated) are excluded. 95% confidence intervals are based on standard errors clustered at the MedStat region level.\n\nTable 7: Overall ATT by Outcome Category and Buffer Zone\n\nOutcome | 1 km | 3 km | 5 km\n\nMental/Behavioral | -0.354 | -0.202 | -0.381*\n\n| (0.382) | (0.244) | (0.220)\n\nHepatitis | -0.270 | -0.413 | -0.406\n\n| (0.486) | (0.270) | (0.250)\n\nHIV | 0.063 | -0.239 | -0.340\n\n| (0.801) | (0.337) | (0.294)\n\nNarcotics | 1.186*** | 0.549*** | 0.390**\n\n| (0.288) | (0.187) | (0.165)\n\nDrug-related (fatal) | -1.207*** | -0.290 | -0.354**\n\n| (0.137) | (0.215) | (0.178)\n\nTreated regions | 7 | 35 | 50\n\nControl regions | 608 (never-treated) | |\n\nNote: Each cell reports the overall ATT from\nthe doubly robust Callaway & Sant’Anna (2021) estimator with\nnever-treated controls and a universal base period. Outcomes are\nlog hospitalization rates per 100,000 inhabitants. Sub-outcomes:\nmental and behavioral disorders (F11–F19), viral hepatitis (B15–B19),\nHIV disease (B20–B24), narcotics/psychodysleptics (T40). The 1 km\nestimates are identified from a single treated region per cohort and\nshould be interpreted with caution. Regions near DCRs opened before\n1998 excluded. Standard errors clustered at the Medstat region level.\nSignificance: {}^{***}p<0.01 , {}^{**}p<0.05 , {}^{*}p<0.10 .\n\nFigure 7 and Table 7 repeat the estimation for the five diagnostic categories. From Table 7, the ATT estimates for hospitalizations due to mental and behavioral disorders are consistently negative and marginally significant at the 5 km buffer specification. Moreover, the estimates of hepatitis are also negative and of comparable magnitude but insignificant. However, the event-study path in Figure 7 shows a gradual decline that builds from year 3 onward, consistent with a slow-acting reduction in needle sharing. HIV estimates are insignificant and close to zero. Narcotics poisoning hospitalizations rise after DCR opening and remain positive across all buffers. Lastly, fatal drug-related hospitalizations move in the opposite direction, falling after opening the DCR. The opposing patterns in narcotics and fatal hospitalizations suggest that DCRs convert events that would otherwise be fatal into survivable hospital contacts.\n\n### 6.1 Mechanisms\n\nThe sub-outcome results point to two channels through which DCRs reduce drug-related hospitalizations. The first is overdose supervision. DCRs provide a medically supervised environment where staff can control the dose consumed, perform resuscitation, and call emergency services when an overdose occurs. When supervision prevents a death that would otherwise happen outside a hospital, the consequence is a simultaneous decline in fatal drug-related hospitalizations and a rise in non-fatal poisoning contacts, as events that would have ended in death instead end in a hospital visit. The results are consistent with this prediction. Drug-related fatal hospitalizations fall near DCRs, by approximately 30% at 5 km, while narcotics and psychodysleptics hospitalizations rise by 47% at 5 km. The opposing signs and spatial concentration of these two effects are consistent with a\nsubstitution from out-of-hospital mortality to in-hospital survival. Since I cannot observe overdose events that do not result in a hospital contact, this interpretation is suggestive rather than identified, but it is consistent with the clinical evidence on DCR-based overdose reversals\n(Kerr et al., 2017; Hedrich, 2004).\n\nThe second channel is harm reduction for blood-borne diseases. DCRs distribute sterile injection equipment, which reduces needle sharing and the transmission of viral hepatitis and HIV. Unlike overdose prevention, these effects are expected to emerge slowly, since disease progression and hospitalization take years to follow from initial infection. The event-study path for hepatitis is consistent with this lag. The estimates are close to zero in the first two post-treatment years and become progressively more negative from year 3 onward, reaching approximately 40% below baseline by year 5. HIV estimates are near zero through out the analysis, with wide confidence intervals. A longer panel and additional out-patient data would be needed to determine whether these trends continue and to get more precise estimates.\n\nA third potential channel is referral to treatment and social services. DCRs routinely connect users to addiction treatment, primary care, and housing support, and a sustained reduction in hospitalizations could partly reflect better long-term management of drug dependence. The regional hospitalization panel used in this paper does not contain information on treatment entry or service use, so I cannot separate this channel from the two described above. It remains a plausible additional mechanism that future work with information on treatment take up data could examine.\n\nTable A19: Robustness: Overall ATT Across Estimators — 5 km buffer, \\pm 5-year window\n\n| CS-DR | Sun & Abraham | Synthetic DiD | Stacked DiD\n\nATT | -0.431** | -0.438** | -0.362* | -0.149***\n\n| (0.218) | (0.208) | (0.205) | (0.038)\n\n% change | -35.0% | -35.5% | -30.3% | -13.9%\n\nTreated regions | 50 | | |\n\nControl regions | 608 | | |\n\nObservations | 17,250 | | |\n\nNote: All specifications use the 5 km buffer,\nnever-treated comparison regions (640 regions), and a \\pm 5-year window","stderr":"","interrupted":false,"isImage":false,"noOutputExpected":false},"sandboxed":false,"sourceToolAssistantUUID":"7d18db6e-812e-4c03-b46f-e2b5845a7e87","permissionDecision":{"decision":"accept","source":"config","reasonType":"rule","ruleSource":"cliArg"},"userType":"external","entrypoint":"sdk-cli","cwd":"/Users/simon-pierreboucher/wp29/runs/RC0255","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","version":"2.1.314","gitBranch":"HEAD"}23{"type":"api-request-blob","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","hash":"769df1a5a41d96d1ea3cb4f504f55f9d9d924ffec326b9757e72a534a4316dbe","message":{"role":"assistant","content":[{"type":"text","text":"Now the data, independently."},{"type":"tool_use","id":"toolu_01S1DzQUunvFFJdLBEQAsszh","name":"Bash","input":{"command":"cat data/reference_list.json; cat data/README.md; wc -l data/sources/* data/README.md"}},{"type":"tool_use","id":"toolu_01BwN9pgA7o2MUxsivNPxKUE","name":"Bash","input":{"command":"cat data/sources/arxiv-2609.27732v1.txt"}}]}}24{"type":"api-request-blob","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","hash":"f712572f9a716ebb852b0830a32aac159d53b5554ab330bfc63de512dfdac3dd","message":{"role":"user","content":[{"tool_use_id":"toolu_01S1DzQUunvFFJdLBEQAsszh","type":"tool_result","content":"[\n {\n \"id\": \"R1\",\n \"entry\": \"Armendariz, A. 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Evaluating the Impact of Rhode Island's Self-Sustaining Reemployment Services and Eligibility Assessment (RESEA) Program on Employment Outcomes. arXiv:2606.14621.\",\n \"cited_for\": \"In a preregistered randomised controlled trial (N = 23,549), selection into RESEA raised annualised wages by $1,153 (95% CI [166, 2,141]), raised reemployment by 1.47 percentage points and reduced weeks on UI by 1.99 weeks.\",\n \"source_file\": \"sources/arxiv-2606.14621v1.txt\"\n },\n {\n \"id\": \"R3\",\n \"entry\": \"Liu, W., & Zhao, R. (2024). Restaurants, Cafés and Neighbourhood Change: Commercial Entry and House Prices in Greater London. arXiv:2603.03260.\",\n \"cited_for\": \"Local house prices jump by 3.4–3.7% in the year in which food-and-drink establishments enter an LSOA, with no further appreciation in later years.\",\n \"source_file\": \"sources/arxiv-2603.03260v2.txt\"\n },\n {\n \"id\": \"R4\",\n \"entry\": \"Kanayama, H., Miyaji, S., & Otani, S. (2025). 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Direct and indirect effects of a free cesarean section policy in Benin. arXiv:2510.03658.\",\n \"cited_for\": \"Access to Benin's free cesarean section policy reduces the probability of infant death or stillbirth by 0.0962 (SE 0.0129) in the preferred specification, a 36.85% reduction relative to the mean of the dependent variable.\",\n \"source_file\": \"sources/arxiv-2510.03658v1.txt\"\n }\n]\n# Data provenance — F4-conf-04\n\nAll files under `data/sources/` are plain-text extracts of publicly accessible documents, prepared by the task designer on 2026-10-30 (UTC). Each extract begins with a provenance header (title, authors, bibliographic record, retrieval URL and UTC, SHA-256 of the retrieved HTML, license, list of included and omitted sections). Only the excerpts needed for the task are reproduced; everything else is omitted. 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Evaluating the Impact of Rhode Island's Self-Sustaining Reemployment Services and Eligibility Assessment (RESEA) Program on Employment Outcomes. arXiv:2606.14621v1 [econ.GN]. https://arxiv.org/abs/2606.14621v1 (full text: https://arxiv.org/html/2606.14621v1) | 2026-10-30T03:23:18Z | CC BY 4.0 | 27c463c0a144d9d5a3916dc641f15b6029f6c68b5e574ad9074e7df1aeb0a238 |\n| `sources/arxiv-2603.03260v2.txt` | Liu, W., & Zhao, R. (2026). Does Entry of Food-and-Drink Establishments Raise Local House Prices? Event-Study Evidence from London. arXiv:2603.03260v2 [physics.soc-ph, econ.GN], v2 of 2 Apr 2026. https://arxiv.org/abs/2603.03260v2 (full text: https://arxiv.org/html/2603.03260v2) | 2026-10-30T03:23:18Z | CC BY 4.0 | 3cb9a4f3574e7b2272fe19cde165a745543883f86beb9342f6fc0ab744c31551 |\n| `sources/arxiv-2505.04555v3.txt` | Kanayama, H., Miyaji, S., & Otani, S. (2025/2026). Just After Minimum Wage Hikes: Short-Run Labor-Demand Response and Reallocation. arXiv:2505.04555v3 [econ.GN], v1 of 7 May 2025, v3 of 16 Mar 2026. https://arxiv.org/abs/2505.04555v3 (full text: https://arxiv.org/html/2505.04555v3) | 2026-10-30T03:23:18Z | CC BY 4.0 | b1731a9b1c40ae91c6be2cf2e92623bb6cf86c551587936a0270356f76ae95c1 |\n| `sources/arxiv-2510.03658v1.txt` | Tossou, S. C. (2025). Who benefits the most? 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Abstract page: https://arxiv.org/abs/2609.27732v1\nRetrieved: https://arxiv.org/html/2609.27732v1 on 2026-10-30T03:23:18Z (SHA-256 of the retrieved HTML: 22b06050f4ff6e665aedd80561fa4031b1717867ecfeca71d1d2902ee1b09f52)\nLicense: CC BY 4.0 (license shown on the arXiv abstract page; https://creativecommons.org/licenses/by/4.0/). Reproduced in part with attribution.\nExtract contents: title, author, date and abstract; Section 6 'Results' in full (Figure notes, Table 6, Table 7, Section 6.1 'Mechanisms'); Appendix Table A19 with its note and the paragraph that discusses it.\nOmitted: Sections 1-5 and 7, the other appendix tables and figures, the references.\nRendering note: converted from the HTML rendering to plain text. Tables are rendered one row per line with \" | \" separating cells; in regression tables the line following a coefficient row holds the standard errors in parentheses, exactly as printed. Mathematical expressions appear as LaTeX source; non-breaking spaces were replaced by ordinary spaces. No numbers were altered.\n================================================================\n\n# Do Drug Consumption Rooms Reduce Drug-Related Hospitalizations? Evidence from Switzerland\n\nAna Armendariz*\n\nSeptember 23, 2026\n\nThis paper estimates the causal effect of drug consumption room (DCR) openings on drug-related hospitalizations in Switzerland. I exploit the staggered introduction of DCRs across Swiss cities between 1998 and 2022, using individual-level hospital records and a difference-in-differences estimator. DCR openings reduce drug-related hospitalization rates by roughly 35% within 5 km of a facility. The reduction is most pronounced for fatal outcomes, which fall by 35% while narcotics poisoning hospitalizations rise by a comparable amount, consistent with DCRs converting potentially fatal overdoses into non-fatal hospitalizations. Mental and behavioral disorder hospitalizations decline by 32% while estimates for Hepatitis and HIV are imprecise. The findings support the role of DCRs as an effective harm reduction strategy.\n\nKeywords: Drug Consumption Rooms, Harm Reduction, Hospitalizations, Drugs, Public Health, Causal Inference\n\n## 6 Results\n\nThis section reports the effect of DCR openings on the rate of drug-related hospitalizations per 100,000 inhabitants. I begin with the event-study estimates and then present the overall pooled ATT. I then disaggregate the overall outcome into its sub-outcome categories and report the same estimates for each.\n\nFigure 6: Event study estimates by buffer zone, \\pm 5-year window\n\nNote: The figure plots event-study coefficients from the doubly robust estimator of Callaway and Sant’Anna (2021) for regions within 5 km of a DCR opening. The comparison group consists of never-treated regions (608 control regions). The outcome is the log drug-related hospitalization rate per 100,000 inhabitants. The sample includes all staggered-treated MedStat regions within 5 km of a DCR that opened between 1998 and 2022 and all never-treated regions. The estimation uses a \\pm 5-year window relative to DCR opening, with t=-5 and t=+5 representing pooled endpoint bins that absorb all periods beyond the window. The reference period is a universal base period. Regions near DCRs that opened before 1998 (always-treated) are excluded through out. 95% confidence intervals are based on standard errors clustered at the MedStat region level. Results for the 1 km and 3 km buffer specifications are reported in Appendix Figure A17.\n\nFigure 6 presents the event study estimates for the 5 km buffer specifications. I focus on the 5 km buffer specification, as it includes the largest number of treated regions and yields the most precise estimates. I summarize dynamic effects over a symmetric five year window around DCR openings. This window avoids relying on distant leads and lags that are informed by only a small subset of adopters. Pre-treatment coefficients are small and statistically insignificant, supporting the parallel trends assumption. The post-treatment coefficients are consistently negative, indicating a reduction in drug-related hospitalizations following DCR openings. The estimates of the overall summary of ATTs based on calendar time aggregation of Callaway and Sant’Anna (2021) is around -35% reduction in hospitalizations due to drugs.\n\nTable 6: Overall Average Treatment Effect on the Treated (ATT)\n\n| 1 km | 3 km | 5 km\n\nATT | -0.399 | -0.283 | -0.431**\n\n| (0.412) | (0.279) | (0.210)\n\n% change | -32.9% | -24.7% | -35.0%\n\nTreated regions | 7 | 35 | 50\n\nControl regions | 608 | 608 | 608\n\nObservations | 16,175 | 16,875 | 17,250\n\nNote: The table reports the overall ATT estimated using the doubly robust Callaway and Sant’Anna (2021) estimator with never-treated controls and a universal base period. The outcome is the log drug-related hospitalization rate per 100,000 inhabitants. Columns differ in the geographic buffer used to define treated Medstat regions. The control group consists of 608 never-treated Medstat regions\nthroughout. Regions near DCRs that opened before 1998\n(always-treated) are excluded. Standard errors clustered at the Medstat region level in\nparentheses. Significance: {}^{***}p<0.01 , {}^{**}p<0.05 ,\n{}^{*}p<0.10 .\n\nTable 6 reports the pooled ATT for the 1 km, 3 km and 5 km buffer specification, aggregating the dynamic treatment effects into a single estimate averaged across all post-treatment periods and cohorts. The 5 km specification, yields an ATT of -0.431\ncorresponding to a 35% reduction in the drug-related hospitalization rate. This estimate is statistically significant at the 5% level. The 3 km and 1 km estimates point in the same direction but are less precise, due to the smaller number of treated regions.\n\nTo further explore the mechanisms through which DCR openings affect drug-related hospitalizations, I disaggregate the main outcome into five diagnostic\nsub-categories: (i) mental and behavioral disorders due to psychoactive substance use, (ii) viral hepatitis, (iii) HIV, (iv) poisoning by narcotics and psychodysleptics, and (v) fatal drug-related hospitalizations. Accidental poisoning is excluded due to the very small number of cases.\n\nFigure 7: Event study: Sub-outcome estimates,\nwithin 5 km, \\pm 5-year window\n\nNote: The figure plots event-study coefficients from the doubly robust Callaway & Sant’Anna (2021) estimator for four diagnostic sub-categories of drug-related hospitalizations. Each panel uses a separate y -axis to accommodate differences in scale across outcomes. The sample includes all staggered-treated MedStat regions within 5 km of a\nDCR that opened between 1998 and 2022. The reference period is a universal base period. Regions near DCRs that opened before 1998 (always-treated) are excluded. 95% confidence intervals are based on standard errors clustered at the MedStat region level.\n\nTable 7: Overall ATT by Outcome Category and Buffer Zone\n\nOutcome | 1 km | 3 km | 5 km\n\nMental/Behavioral | -0.354 | -0.202 | -0.381*\n\n| (0.382) | (0.244) | (0.220)\n\nHepatitis | -0.270 | -0.413 | -0.406\n\n| (0.486) | (0.270) | (0.250)\n\nHIV | 0.063 | -0.239 | -0.340\n\n| (0.801) | (0.337) | (0.294)\n\nNarcotics | 1.186*** | 0.549*** | 0.390**\n\n| (0.288) | (0.187) | (0.165)\n\nDrug-related (fatal) | -1.207*** | -0.290 | -0.354**\n\n| (0.137) | (0.215) | (0.178)\n\nTreated regions | 7 | 35 | 50\n\nControl regions | 608 (never-treated) | |\n\nNote: Each cell reports the overall ATT from\nthe doubly robust Callaway & Sant’Anna (2021) estimator with\nnever-treated controls and a universal base period. Outcomes are\nlog hospitalization rates per 100,000 inhabitants. Sub-outcomes:\nmental and behavioral disorders (F11–F19), viral hepatitis (B15–B19),\nHIV disease (B20–B24), narcotics/psychodysleptics (T40). The 1 km\nestimates are identified from a single treated region per cohort and\nshould be interpreted with caution. Regions near DCRs opened before\n1998 excluded. Standard errors clustered at the Medstat region level.\nSignificance: {}^{***}p<0.01 , {}^{**}p<0.05 , {}^{*}p<0.10 .\n\nFigure 7 and Table 7 repeat the estimation for the five diagnostic categories. From Table 7, the ATT estimates for hospitalizations due to mental and behavioral disorders are consistently negative and marginally significant at the 5 km buffer specification. Moreover, the estimates of hepatitis are also negative and of comparable magnitude but insignificant. However, the event-study path in Figure 7 shows a gradual decline that builds from year 3 onward, consistent with a slow-acting reduction in needle sharing. HIV estimates are insignificant and close to zero. Narcotics poisoning hospitalizations rise after DCR opening and remain positive across all buffers. Lastly, fatal drug-related hospitalizations move in the opposite direction, falling after opening the DCR. The opposing patterns in narcotics and fatal hospitalizations suggest that DCRs convert events that would otherwise be fatal into survivable hospital contacts.\n\n### 6.1 Mechanisms\n\nThe sub-outcome results point to two channels through which DCRs reduce drug-related hospitalizations. The first is overdose supervision. DCRs provide a medically supervised environment where staff can control the dose consumed, perform resuscitation, and call emergency services when an overdose occurs. When supervision prevents a death that would otherwise happen outside a hospital, the consequence is a simultaneous decline in fatal drug-related hospitalizations and a rise in non-fatal poisoning contacts, as events that would have ended in death instead end in a hospital visit. The results are consistent with this prediction. Drug-related fatal hospitalizations fall near DCRs, by approximately 30% at 5 km, while narcotics and psychodysleptics hospitalizations rise by 47% at 5 km. The opposing signs and spatial concentration of these two effects are consistent with a\nsubstitution from out-of-hospital mortality to in-hospital survival. Since I cannot observe overdose events that do not result in a hospital contact, this interpretation is suggestive rather than identified, but it is consistent with the clinical evidence on DCR-based overdose reversals\n(Kerr et al., 2017; Hedrich, 2004).\n\nThe second channel is harm reduction for blood-borne diseases. DCRs distribute sterile injection equipment, which reduces needle sharing and the transmission of viral hepatitis and HIV. Unlike overdose prevention, these effects are expected to emerge slowly, since disease progression and hospitalization take years to follow from initial infection. The event-study path for hepatitis is consistent with this lag. The estimates are close to zero in the first two post-treatment years and become progressively more negative from year 3 onward, reaching approximately 40% below baseline by year 5. HIV estimates are near zero through out the analysis, with wide confidence intervals. A longer panel and additional out-patient data would be needed to determine whether these trends continue and to get more precise estimates.\n\nA third potential channel is referral to treatment and social services. DCRs routinely connect users to addiction treatment, primary care, and housing support, and a sustained reduction in hospitalizations could partly reflect better long-term management of drug dependence. The regional hospitalization panel used in this paper does not contain information on treatment entry or service use, so I cannot separate this channel from the two described above. It remains a plausible additional mechanism that future work with information on treatment take up data could examine.\n\nTable A19: Robustness: Overall ATT Across Estimators — 5 km buffer, \\pm 5-year window\n\n| CS-DR | Sun & Abraham | Synthetic DiD | Stacked DiD\n\nATT | -0.431** | -0.438** | -0.362* | -0.149***\n\n| (0.218) | (0.208) | (0.205) | (0.038)\n\n% change | -35.0% | -35.5% | -30.3% | -13.9%\n\nTreated regions | 50 | | |\n\nControl regions | 608 | | |\n\nObservations | 17,250 | | |\n\nNote: All specifications use the 5 km buffer,\nnever-treated comparison regions (640 regions), and a \\pm 5-year 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EXTRACT — arxiv-2606.14621v1\nTitle: Evaluating the Impact of Rhode Island's Self-Sustaining Reemployment Services and Eligibility Assessment (RESEA) Program on Employment Outcomes\nAuthors: Harrison H. Li; Shanna Pearson-Merkowitz; David Yokum\nBibliographic record: arXiv:2606.14621v1 [econ.GN], submitted 12 Jun 2026 (version 1, the only version at retrieval). Abstract page: https://arxiv.org/abs/2606.14621v1\nRetrieved: https://arxiv.org/html/2606.14621v1 on 2026-10-30T03:23:18Z (SHA-256 of the retrieved HTML: f98fb1b39edd2107051cddf1da34aa8cf19e74e04d60bf9305a88cf966417da1)\nLicense: CC BY 4.0 (license shown on the arXiv abstract page; https://creativecommons.org/licenses/by/4.0/). Reproduced in part with attribution.\nExtract contents: title, authors and abstract; Section 3 'Results' (Table 2 with caption, the results paragraphs, Section 3.1 'Cost-benefit analysis'); from Section 4.1, Table 3 with its caption and the paragraph that discusses it.\nOmitted: Sections 1-2, Table 1, Section 3.2 (heterogeneous effects), the rest of Section 4, the references and the appendix.\nRendering note: converted from the HTML rendering to plain text. Tables are rendered one row per line with \" | \" separating cells; in regression tables the line following a coefficient row holds the standard errors in parentheses, exactly as printed. Mathematical expressions appear as LaTeX source; non-breaking spaces were replaced by ordinary spaces. No numbers were altered.\nEditorial note: Tables 2 and 3 were re-set in a one-row-per-outcome layout because the HTML rendering split each outcome over three rows and detached the p-values from their columns; the p-values and confidence intervals are attached to the column they belong to in the original (first p-value = treatment-control difference, second = average treatment effect).\n================================================================\n\n# Evaluating the Impact of Rhode Island's Self-Sustaining Reemployment Services and Eligibility Assessment (RESEA) Program on Employment Outcomes\n\nHarrison H. Li (Harvey Mudd College), Shanna Pearson-Merkowitz (University of Maryland, College Park), David Yokum (University of North Carolina at Chapel Hill)\n\n###### Abstract\n\nProlonged unemployment carries serious economic, health, and wellbeing costs. With federal support, most U.S. states now operate a Reemployment Services and Eligibility Assessment (RESEA) program to help Unemployment Insurance (UI) claimants return to work faster. We report results from a large (N = 23,549) preregistered randomized controlled trial (RCT) evaluating Rhode Island’s RESEA program from February 2022 to September 2023. We estimate that selection into the program increased annualized wages by $1,153, increased reemployment by 1.5 percentage points, and reduced UI duration by nearly two weeks. The vast majority of these wage and reemployment effects appeared within two quarters of claimants’ first pay dates and persisted through at least the following year, and we estimate that each dollar spent on the program saved the state $2.64. Using causal forests, a machine learning technique for estimating heterogeneous treatment effects (HTE), we also conduct an exploratory analysis to investigate if there are differential effects of selection into the RESEA program. We find that all participants experienced positive wage benefits from RESEA selection, with particularly large effects for older and lower-income workers. Finally, we improve upon prior RESEA evaluations by explicitly controlling for the week of treatment assignment — a methodological refinement absent from several existing RCTs of job-training programs that is important to eliminate confounding bias. We also discuss ways to harvest precision gains from baseline covariate adjustment without introducing large-sample bias.\n\n## 3 Results\n\n[Table 1 (pre-treatment characteristics) omitted from this extract.]\n\n[Table 2 — re-set by the extract editor from the HTML rendering, in which each outcome occupied three table rows; all values are verbatim. Columns: Outcome | Treatment | Control | Treatment-control difference | Average treatment effect estimate]\n\nOutcome | Treatment | Control | Treatment-control difference | Average treatment effect estimate\nWage | $33,073 (SD: 36,749) | $33,043 (SD: 36,231) | $29; p=0.95; 95% CI: [-903, 962] | $1,153; p=0.022; 95% CI: [166, 2,141]\nReemployment | 75.2% | 75.0% | 0.26 pp; p=0.64; 95% CI: [-0.84, 1.37] | 1.47 pp; p=0.013; 95% CI: [0.32, 2.62]\nWeeks on UI | 15.2 weeks (SD: 9.3) | 17.3 weeks (SD: 9.4) | -2.10 weeks; p<0.001; 95% CI: [-2.34, -1.86] | -1.99 weeks; p<0.001; 95% CI: [-2.24, -1.75]\nShort-term wage | $23,776 (SD: 31,948) | $23,897 (SD: 32,293) | -$121; p=0.77; 95% CI: [-941, 700] | $1,195; p=0.007; 95% CI: [326, 2,064]\nShort-term reemployment | 61.4% | 61.6% | -0.18 pp; p=0.77; 95% CI: [-1.43, 1.06] | 1.66 pp; p=0.012; 95% CI: [0.37, 2.96]\nShort-term weeks on UI | 14.2 weeks (SD: 8.4) | 15.9 weeks (SD: 8.3) | -1.70 weeks; p<0.001; 95% CI: [-1.92, -1.49] | -1.77 weeks; p<0.001; 95% CI: [-1.99, -1.55]\n\nTable 2: The average values of our long-term and short-term outcomes for the aggregate treatment and control groups in the study cohort, along with information about the differences in these averages between the treatment and control groups and our average treatment effect estimates. For the average outcomes, standard deviations are given in parentheses for the quantitative outcomes (wage and weeks on UI). For the treatment-control differences and the average treatment effect estimates, we provide two-sided p -values and 95% confidence intervals based on Welch’s two-sample t -test and the methodology described in the main text, respectively. The two rightmost columns illustrate how direct comparisons of outcome averages between the aggregate treatment and control groups can lead to significantly biased causal conclusions.\n\nOverall, we find that RESEA selection led to a statistically significant improvement in all three of the preregistered outcomes. RESEA selection led to a wage outcome that was $1,153 higher annually (95% CI: [$166, $2,141]; p=0.022 ), a 3.5% increase relative to the mean wage outcome of $33,043 in the control group (Table 2). There was also an estimated 1.47 percentage point increase in reemployment (95% CI: [0.32, 2.62]; p=0.013 ) and a 1.99 week reduction in the number of weeks on UI (95% CI: [1.75 weeks, 2.24 weeks]; p<0.001 ) due to RESEA selection. The latter is an 11.5% decrease compared to the mean control group weeks on UI outcome of 17.3 weeks. All three of these results remain statistically significant after correcting for multiple testing using Holm’s method to keep the familywise error rate below 5 percent.\n\nThe results for the short-term outcomes are substantively similar to those for the longer-term outcomes (Table 2). We estimate RESEA selection leads to a short-term wage outcome that is $1,195 higher (95% CI: [$326, $2,064]; p = 0.007) on an annualized basis and a 1.66 percentage point higher rate of short-term reemployment (95% CI: [0.37, 2.96]; p = 0.012). Given that the magnitudes of these causal estimates are very similar to those for the corresponding long-term outcomes, this suggests that the full impact of RESEA selection on wages and reemployment appears quickly by the second quarter after randomization, and persists for at least five quarters. We also find that those selected for RESEA spend 1.77 fewer weeks on UI in the benefit year of their claim (95% CI: [1.55 weeks, 1.99 weeks]; p ¡ 0.001). As this is a bit smaller than the effect size of 1.99 weeks estimated for the long term weeks on UI outcome, which includes an additional 26 weeks beyond the benefit year, we see some directional evidence that RESEA selection may also reduce the time spent on UI in the following year, suggesting that it may be helping claimants find employment that lasts longer, thereby reducing repetitive use of UI benefits.\n\nAs noted earlier, wages and reemployment are artificially zero-inflated due to missing out-of-state wage data. The Rhode Island job market is tightly integrated with those of the neighboring states of Massachusetts and Connecticut; the 2016-2020 5-Year American Community Survey found that nearly 16 percent of Rhode Island workers 16 years and older commuted out of state, mainly to Massachusetts. We note, however, that this missingness should not affect the directional validity of our causal analysis. This is because randomization ensures that this missingness is balanced between the treatment and control groups (within each block), unless RESEA selection itself differentially helps or hinders finding employment out of state or self-employment. To investigate this, we examined the presence of individuals who failed to exhaust their UI benefits in the benefit year of their claim while having $0 in reported RI wages for all of the five complete quarters after randomization. There were 3,325 claimants falling into this group, including 1,618 individuals (13.7%) in the aggregate control group and 1,707 individuals (14.6%) in the aggregate treatment group. After controlling for randomization week, this difference in proportions was not significant ( p = 0.55). The lack of statistical significance on this test with our large sample size along with the fact that the Rhode Island job database focuses overwhelmingly on jobs offered by Rhode Island employers suggests that RESEA selection does not differentially assist in finding out-of-state employment or self-employment.\n\n### 3.1 Cost-benefit analysis\n\nWe find that the decrease in time spent drawing UI benefits due to RESEA selection corresponds to a considerable cost savings to the state from paying out a smaller amount of UI benefits. We estimate that the average individual selected for RESEA during the study period drew $676 less (95% CI: [$563, $789], p<0.001 ) in UI benefits during the same benefit year of their claim than they would have if they were not selected for RESEA. This is a 9.9 percent reduction relative to the control group average of $6,839 in UI benefits drawn during the benefit year of the claim. Multiplying the estimate by the total number of individuals selected for RESEA in the study ( n=11,700 ) suggests that as a result of the program, the state paid out about $7.9 million fewer in UI benefits to claimants randomized during the study period over the same benefit year as their UI claims. This is much higher than the total expenditures of $2.99 million for the RESEA program over the study period, representing $2.64 in savings for the state budget for every $1 spent on the program.\n\n### 4.1 Methodological lessons (excerpt)\n\n[Table 3 — re-set by the extract editor from the HTML rendering; all values are verbatim. Columns: Outcome | Difference in means | Covariate adjusted | Fixed effects regression]\n\nOutcome | Difference in means | Covariate adjusted | Fixed effects regression\nWage | $1,153; p=0.022; 95% CI: [166, 2,141] | $1,137; p=0.014; 95% CI: [228, 2,047] | $1,100; p=0.027; 95% CI: [127, 2,073]\nReemployment | 1.47 pp; p=0.013; 95% CI: [0.32, 2.62] | 1.48 pp; p=0.012; 95% CI: [0.32, 2.63] | 1.49 pp; p=0.011; 95% CI: [0.34, 2.64]\nWeeks on UI | -1.99 wks; p<0.001; 95% CI: [-2.24, -1.75] | -1.93 wks; p<0.001; 95% CI: [-2.18, -1.68] | -1.97 wks; p<0.001; 95% CI: [-2.22, -1.72]\n\nTable 3: A comparison of the ITT estimates, two-sided p -values, and 95% confidence intervals for our primary outcomes from three different methodologies: the preregistered analysis based on eq. (1), the covariate adjusted analysis based on eq. (2), and the fixed effects regression in eq. (3). The leftmost column based on the preregistered analysis duplicates the rightmost column in Table 2 for ease of comparison.\n\nIf we directly compared treatment group and control group outcome averages without accounting for the week of randomization, the results would suggest RESEA selection had no detectable average effect on the wage and reemployment outcomes (column 4, Table 2). However, such an analysis is potentially biased under the experimental design because it does not respect the blocked randomization, which makes the week of randomization a known confounder. For example, weeks with a larger number of UI applicants, which had a higher proportion of control group individuals, tended to have lower-earning applicants (Fig. 7), thereby inflating the average wage outcome in the control group relative to the treatment group. This is critical because out of the thirteen publically available studies of RESEA-related employment assistance programs rated by CLEAR as having high causal evidence, six used block randomization like we do, yet only two of these (Black, Smith, Berger, & Noel., 2002; Klerman et al., 2019) properly adjusted for the block. Three others among these six studies used regression or matching methods in an attempt to control for observed demographic variables but not the block (Poe-Yamagata et al., 2011; Michaelides et al., 2012; Manoli et al., 2018), while the remaining study (Michaelides & Mueser, 2018) fit a linear regression model with the block indicators as fixed effects, as did two other more recent evaluations in Nevada (Michaelides & Mian, 2021; Brigandi et al., 2024) . These fixed effects regressions amount to estimating the coefficient in the regression model\nSOURCE EXTRACT — arxiv-2603.03260v2\nTitle: Does Entry of Food-and-Drink Establishments Raise Local House Prices? Event-Study Evidence from London\nAuthors: Wanqi Liu; Rong Zhao\nBibliographic record: arXiv:2603.03260v2 [physics.soc-ph, econ.GN], version 1 submitted 3 Mar 2026, version 2 (this extract) submitted 2 Apr 2026. Abstract page: https://arxiv.org/abs/2603.03260v2\nRetrieved: https://arxiv.org/html/2603.03260v2 on 2026-10-30T03:23:18Z (SHA-256 of the retrieved HTML: 6e9a3c5fead449da09a981b0bacc36e1a4f652750caef972a173c3193525c327)\nLicense: CC BY 4.0 (license shown on the arXiv abstract page; https://creativecommons.org/licenses/by/4.0/). Reproduced in part with attribution.\nExtract contents: title, authors and abstract; Section 3 'Empirical Strategy and Main Results' in full (equation (1), Table 2, Table 3 with notes, Figure 2 caption, Section 3.3); Section 5 'Conclusion'.\nOmitted: Sections 1-2 and 4, the appendix (Tables 4-5), the references.\nRendering note: converted from the HTML rendering to plain text. Tables are rendered one row per line with \" | \" separating cells; in regression tables the line following a coefficient row holds the standard errors in parentheses, exactly as printed. Mathematical expressions appear as LaTeX source; non-breaking spaces were replaced by ordinary spaces. No numbers were altered.\n================================================================\n\n# Does Entry of Food-and-Drink Establishments Raise Local House Prices? Event-Study Evidence from London\n\nWanqi Liu, Rong Zhao (Centre for Advanced Spatial Analysis, University College London)\n\n###### Abstract\n\nRestaurants, cafes, pubs, and takeaways are among the most visible markers of neighborhood change, yet whether their arrival is capitalised into nearby housing values remains empirically unsettled. We assemble a London-wide panel linking Land Registry prices, non-domestic EPC lodgement timings for food-and-drink establishments, and neighborhood amenity measures at the LSOA level. Our preferred annual event-study design defines treatment as the first clean-onset year in which an LSOA records at least two eligible EPC lodgements for food-and-drink establishments, after a two-year lookback with no prior entries. In this specification, pre-trend tests are not rejected in either the stacked or Sun-Abraham estimators, and log house prices rise gradually from about 0.5% in the event year to roughly 3.4–3.7% by years four and five. The results are consistent with local amenity capitalization following commercial entry, while remaining appropriately cautious about endogenous siting and concurrent redevelopment.\n\n## 3 Empirical Strategy and Main Results\n\n### 3.1 Empirical Strategy\n\nOur main estimand is the reduced-form change in local log house prices following the first clean entry wave of food-and-drink establishments in an LSOA, relative to untreated LSOAs that remain at risk in the relevant event-time comparisons. It is best interpreted as a local capitalization estimand: it bundles direct amenity value, signaling, and related neighborhood revaluation, rather than isolating a single structural channel.\n\nThe central identification threat is endogenous siting. If businesses open where appreciation was already accelerating, post-entry coefficients will confound commercial entry with prior neighborhood change. To trace the dynamic price response while reducing that concern, we exploit the staggered timing of openings of food-and-drink establishments using EPC lodgement records for restaurants, cafes, drinking establishments, and takeaways. In the preferred specification, treatment begins in the first year an LSOA records at least two such EPC lodgements after a two-year lookback window with no prior eligible entry. Let E_{i} denote the treatment year for LSOA i (undefined for never-treated units). This clean-onset rule is intended to capture a discrete local entry wave rather than ongoing turnover. Our annual event-study specification is:\n\ny_{it}=\\alpha_{i}+\\delta_{t}+\\sum_{\\begin{subarray}{c}\\tau=-5\\\\\n\\tau\\neq-1\\end{subarray}}^{5}\\beta_{\\tau}\\,\\mathbf{1}\\{t-E_{i}=\\tau\\}+\\varepsilon_{it} | | | (1)\n\nwhere \\mathbf{1}\\{t-E_{i}=\\tau\\} equals one when LSOA i is observed \\tau years relative to its treatment date, with \\tau=-1 as the omitted reference period. The coefficients \\{\\beta_{\\tau}\\} trace out the dynamic treatment effect, while the pre-period coefficients \\beta_{-5},\\ldots,\\beta_{-2} provide the main visual and joint-test check on parallel trends.\n\n#### Estimator comparisons.\n\nBecause staggered treatment timing can induce negative weighting in conventional TWFE [22], we treat the stacked design as the main estimator and compare it with a Sun and Abraham [23] interaction-weighted estimator. The point of this comparison is to check whether the post-entry path survives an alternative treatment-timing aggregation scheme, not to elevate a broad specification horse race into the main text.\n\n### 3.2 Main Event-Study Results\n\nUsing EPC lodgement records, we construct an annual design for entry of food-and-drink establishments in which treatment begins when an LSOA first records at least two eligible lodgements after a two-year clean-onset window with no prior entry. The preferred stacked sample contains 657,197 LSOA-year observations, 774 treated-role LSOAs, and 4,459 control-role LSOAs across risk sets. Treatment is distributed across sixteen cohorts from 2008 to 2023, with the largest cohort in 2009 (178 treated units) and meaningful support throughout the subsequent decade. Appendix cohort tables report the full cohort composition.\n\n#### Support across event time.\n\nTable 2 summarizes the support behind the stacked sample. Treated observations are most numerous near event time and then decline as the window moves farther into the tails, but support remains substantial even at \\tau=5 , where 546 treated observations from 11 contributing stacks remain in the estimating sample. This pattern matters for interpretation: medium-run coefficients are identified from fewer cohorts than the event-year effect, so later horizons should be read as economically informative but mechanically noisier.\n\nTable 2: Event-Time Support in the Stacked Sample\n\nEvent Time | Treated Obs. | Treated LSOAs | Contributing Stacks\n\n-5 | 572 | 572 | 14\n\n-4 | 751 | 751 | 15\n\n-3 | 769 | 769 | 16\n\n-2 | 763 | 763 | 16\n\n-1 | 761 | 761 | 16\n\n0 | 756 | 756 | 16\n\n1 | 689 | 689 | 15\n\n2 | 648 | 648 | 14\n\n3 | 610 | 610 | 13\n\n4 | 586 | 586 | 12\n\n5 | 546 | 546 | 11\n\n•\n\nNotes: Support counts from the preferred clean-onset stacked design for entry of food-and-drink establishments. “Contributing stacks” records how many cohort-specific risk sets identify each event-time coefficient.\n\n#### Headline dynamic pattern.\n\nFigure 2 reports the preferred clean-onset event-study path and overlays the event-time support behind each coefficient. Pre-treatment coefficients are small and imprecise, and the stacked joint pre-trend test does not reject ( p=0.241 ). The estimated effect is close to zero at event time and then turns positive: the stacked coefficient is 0.005 at \\tau=0 , 0.012 at \\tau=1 , 0.018 at \\tau=2 , 0.037 at \\tau=4 , and 0.034 by \\tau=5 . Interpreted in logs, these magnitudes correspond to a gradual appreciation of roughly 0.5% in the event year and about 3.4–3.7% after four to five years. The pattern is notable for its slope as much as for its level: prices do not jump immediately, but instead drift upward as the new commercial entry becomes part of the local amenity bundle.\n\n#### Estimator comparison and design diagnostics.\n\nFor the preferred clean-onset design, the Sun-Abraham interaction-weighted path closely tracks the stacked path in the post-treatment period. The Sun coefficients are 0.005 at \\tau=0 , 0.012 at \\tau=1 , 0.016 at \\tau=2 , 0.036 at \\tau=4 , and 0.033 at \\tau=5 , and its joint pre-trend test is not rejected ( p=0.472 ). Table 3 places the preferred specification next to two nearby alternatives. Relative to the broader baseline threshold-2 design, clean-onset imposes more discipline on timing while preserving a similar medium-run magnitude. Relative to the neighbor-buffer variant, it avoids an extra layer of spatial pruning that mechanically strengthens post-treatment coefficients but yields tighter pre-trend p -values. We therefore retain the unbuffered clean-onset design as the headline specification.\n\nTable 3: Main Design Diagnostics for the Headline Event-Study Specification\n\n[Extract editor's note: the header row of Table 3 is garbled in the HTML rendering; the six columns are, in order: Specification | Treated-role LSOAs | Stacked pre-trend p | Sun pre-trend p | tau=4 coefficient | tau=5 coefficient.]\n\np p \\tau=4 \\tau=5 Specification | Treated-role LSOAs | Stacked pre-trend | Sun pre-trend | |\n\nBaseline threshold-2 | 1,084 | 0.342 | 0.223 | 0.029 | 0.022\n\nClean-onset threshold-2 | 774 | 0.241 | 0.472 | 0.037 | 0.034\n\nClean-onset + neighbor buffer | 774 | 0.126 | 0.239 | 0.042 | 0.040\n\n•\n\nNotes: Entries in the last two columns are log-point coefficients relative to \\tau=-1 . The baseline row uses the broader threshold-2 treatment without the clean-onset restriction. The preferred row uses the clean-onset threshold-2 treatment with a two-year lookback window and no prior eligible entry. The buffer row applies a first-order neighboring-control exclusion to the preferred design.\n\nFigure 2: Preferred clean-onset event-study estimates for entry of food-and-drink establishments. Point estimates are reported relative to the year before treatment ( \\tau=-1 ), which is shown as the open reference marker at zero, and plotted with 95% confidence intervals. Gray bars report the number of treated observations contributing to each event-time coefficient. The estimated path rises gradually from near zero in the event year to roughly 3.4–3.7% by years four and five after entry.\n\n### 3.3 Robustness Checks\n\nThe main robustness question is whether the positive post-entry path survives plausible threats from spatial spillovers and concurrent redevelopment. Excluding first-order neighboring controls leaves the qualitative pattern intact and slightly strengthens post-treatment coefficients, but it also yields tighter pre-trend p -values. We therefore treat the buffer variant as a supporting robustness check rather than as a replacement for the headline design. Planning-start outcome diagnostics are reported in Appendix Table 5 and are not used to select the preferred specification.\n\n## 5 Conclusion\n\nThis paper studies whether entry of food-and-drink establishments is followed by changes in neighborhood house prices in Greater London. In the preferred clean-onset event-study estimates, areas exposed to entry experience a gradual post-entry appreciation that reaches roughly 3.4–3.7% after four to five years. The evidence is consistent with local amenity capitalization following visible commercial change, while also underscoring the need for continued falsification and treatment-validation work before treating the dynamic magnitudes as fully settled.","is_error":false}]},"uuid":"47b025d2-e61f-428e-bb67-8c77e205139b","timestamp":"2026-10-30T05:17:12.753Z","toolUseResult":{"stdout":"SOURCE EXTRACT — arxiv-2606.14621v1\nTitle: Evaluating the Impact of Rhode Island's Self-Sustaining Reemployment Services and Eligibility Assessment (RESEA) Program on Employment Outcomes\nAuthors: Harrison H. Li; Shanna Pearson-Merkowitz; David Yokum\nBibliographic record: arXiv:2606.14621v1 [econ.GN], submitted 12 Jun 2026 (version 1, the only version at retrieval). Abstract page: https://arxiv.org/abs/2606.14621v1\nRetrieved: https://arxiv.org/html/2606.14621v1 on 2026-10-30T03:23:18Z (SHA-256 of the retrieved HTML: f98fb1b39edd2107051cddf1da34aa8cf19e74e04d60bf9305a88cf966417da1)\nLicense: CC BY 4.0 (license shown on the arXiv abstract page; https://creativecommons.org/licenses/by/4.0/). Reproduced in part with attribution.\nExtract contents: title, authors and abstract; Section 3 'Results' (Table 2 with caption, the results paragraphs, Section 3.1 'Cost-benefit analysis'); from Section 4.1, Table 3 with its caption and the paragraph that discusses it.\nOmitted: Sections 1-2, Table 1, Section 3.2 (heterogeneous effects), the rest of Section 4, the references and the appendix.\nRendering note: converted from the HTML rendering to plain text. Tables are rendered one row per line with \" | \" separating cells; in regression tables the line following a coefficient row holds the standard errors in parentheses, exactly as printed. Mathematical expressions appear as LaTeX source; non-breaking spaces were replaced by ordinary spaces. No numbers were altered.\nEditorial note: Tables 2 and 3 were re-set in a one-row-per-outcome layout because the HTML rendering split each outcome over three rows and detached the p-values from their columns; the p-values and confidence intervals are attached to the column they belong to in the original (first p-value = treatment-control difference, second = average treatment effect).\n================================================================\n\n# Evaluating the Impact of Rhode Island's Self-Sustaining Reemployment Services and Eligibility Assessment (RESEA) Program on Employment Outcomes\n\nHarrison H. Li (Harvey Mudd College), Shanna Pearson-Merkowitz (University of Maryland, College Park), David Yokum (University of North Carolina at Chapel Hill)\n\n###### Abstract\n\nProlonged unemployment carries serious economic, health, and wellbeing costs. With federal support, most U.S. states now operate a Reemployment Services and Eligibility Assessment (RESEA) program to help Unemployment Insurance (UI) claimants return to work faster. We report results from a large (N = 23,549) preregistered randomized controlled trial (RCT) evaluating Rhode Island’s RESEA program from February 2022 to September 2023. We estimate that selection into the program increased annualized wages by $1,153, increased reemployment by 1.5 percentage points, and reduced UI duration by nearly two weeks. The vast majority of these wage and reemployment effects appeared within two quarters of claimants’ first pay dates and persisted through at least the following year, and we estimate that each dollar spent on the program saved the state $2.64. Using causal forests, a machine learning technique for estimating heterogeneous treatment effects (HTE), we also conduct an exploratory analysis to investigate if there are differential effects of selection into the RESEA program. We find that all participants experienced positive wage benefits from RESEA selection, with particularly large effects for older and lower-income workers. Finally, we improve upon prior RESEA evaluations by explicitly controlling for the week of treatment assignment — a methodological refinement absent from several existing RCTs of job-training programs that is important to eliminate confounding bias. We also discuss ways to harvest precision gains from baseline covariate adjustment without introducing large-sample bias.\n\n## 3 Results\n\n[Table 1 (pre-treatment characteristics) omitted from this extract.]\n\n[Table 2 — re-set by the extract editor from the HTML rendering, in which each outcome occupied three table rows; all values are verbatim. Columns: Outcome | Treatment | Control | Treatment-control difference | Average treatment effect estimate]\n\nOutcome | Treatment | Control | Treatment-control difference | Average treatment effect estimate\nWage | $33,073 (SD: 36,749) | $33,043 (SD: 36,231) | $29; p=0.95; 95% CI: [-903, 962] | $1,153; p=0.022; 95% CI: [166, 2,141]\nReemployment | 75.2% | 75.0% | 0.26 pp; p=0.64; 95% CI: [-0.84, 1.37] | 1.47 pp; p=0.013; 95% CI: [0.32, 2.62]\nWeeks on UI | 15.2 weeks (SD: 9.3) | 17.3 weeks (SD: 9.4) | -2.10 weeks; p<0.001; 95% CI: [-2.34, -1.86] | -1.99 weeks; p<0.001; 95% CI: [-2.24, -1.75]\nShort-term wage | $23,776 (SD: 31,948) | $23,897 (SD: 32,293) | -$121; p=0.77; 95% CI: [-941, 700] | $1,195; p=0.007; 95% CI: [326, 2,064]\nShort-term reemployment | 61.4% | 61.6% | -0.18 pp; p=0.77; 95% CI: [-1.43, 1.06] | 1.66 pp; p=0.012; 95% CI: [0.37, 2.96]\nShort-term weeks on UI | 14.2 weeks (SD: 8.4) | 15.9 weeks (SD: 8.3) | -1.70 weeks; p<0.001; 95% CI: [-1.92, -1.49] | -1.77 weeks; p<0.001; 95% CI: [-1.99, -1.55]\n\nTable 2: The average values of our long-term and short-term outcomes for the aggregate treatment and control groups in the study cohort, along with information about the differences in these averages between the treatment and control groups and our average treatment effect estimates. For the average outcomes, standard deviations are given in parentheses for the quantitative outcomes (wage and weeks on UI). For the treatment-control differences and the average treatment effect estimates, we provide two-sided p -values and 95% confidence intervals based on Welch’s two-sample t -test and the methodology described in the main text, respectively. The two rightmost columns illustrate how direct comparisons of outcome averages between the aggregate treatment and control groups can lead to significantly biased causal conclusions.\n\nOverall, we find that RESEA selection led to a statistically significant improvement in all three of the preregistered outcomes. RESEA selection led to a wage outcome that was $1,153 higher annually (95% CI: [$166, $2,141]; p=0.022 ), a 3.5% increase relative to the mean wage outcome of $33,043 in the control group (Table 2). There was also an estimated 1.47 percentage point increase in reemployment (95% CI: [0.32, 2.62]; p=0.013 ) and a 1.99 week reduction in the number of weeks on UI (95% CI: [1.75 weeks, 2.24 weeks]; p<0.001 ) due to RESEA selection. The latter is an 11.5% decrease compared to the mean control group weeks on UI outcome of 17.3 weeks. All three of these results remain statistically significant after correcting for multiple testing using Holm’s method to keep the familywise error rate below 5 percent.\n\nThe results for the short-term outcomes are substantively similar to those for the longer-term outcomes (Table 2). We estimate RESEA selection leads to a short-term wage outcome that is $1,195 higher (95% CI: [$326, $2,064]; p = 0.007) on an annualized basis and a 1.66 percentage point higher rate of short-term reemployment (95% CI: [0.37, 2.96]; p = 0.012). Given that the magnitudes of these causal estimates are very similar to those for the corresponding long-term outcomes, this suggests that the full impact of RESEA selection on wages and reemployment appears quickly by the second quarter after randomization, and persists for at least five quarters. We also find that those selected for RESEA spend 1.77 fewer weeks on UI in the benefit year of their claim (95% CI: [1.55 weeks, 1.99 weeks]; p ¡ 0.001). As this is a bit smaller than the effect size of 1.99 weeks estimated for the long term weeks on UI outcome, which includes an additional 26 weeks beyond the benefit year, we see some directional evidence that RESEA selection may also reduce the time spent on UI in the following year, suggesting that it may be helping claimants find employment that lasts longer, thereby reducing repetitive use of UI benefits.\n\nAs noted earlier, wages and reemployment are artificially zero-inflated due to missing out-of-state wage data. The Rhode Island job market is tightly integrated with those of the neighboring states of Massachusetts and Connecticut; the 2016-2020 5-Year American Community Survey found that nearly 16 percent of Rhode Island workers 16 years and older commuted out of state, mainly to Massachusetts. We note, however, that this missingness should not affect the directional validity of our causal analysis. This is because randomization ensures that this missingness is balanced between the treatment and control groups (within each block), unless RESEA selection itself differentially helps or hinders finding employment out of state or self-employment. To investigate this, we examined the presence of individuals who failed to exhaust their UI benefits in the benefit year of their claim while having $0 in reported RI wages for all of the five complete quarters after randomization. There were 3,325 claimants falling into this group, including 1,618 individuals (13.7%) in the aggregate control group and 1,707 individuals (14.6%) in the aggregate treatment group. After controlling for randomization week, this difference in proportions was not significant ( p = 0.55). The lack of statistical significance on this test with our large sample size along with the fact that the Rhode Island job database focuses overwhelmingly on jobs offered by Rhode Island employers suggests that RESEA selection does not differentially assist in finding out-of-state employment or self-employment.\n\n### 3.1 Cost-benefit analysis\n\nWe find that the decrease in time spent drawing UI benefits due to RESEA selection corresponds to a considerable cost savings to the state from paying out a smaller amount of UI benefits. We estimate that the average individual selected for RESEA during the study period drew $676 less (95% CI: [$563, $789], p<0.001 ) in UI benefits during the same benefit year of their claim than they would have if they were not selected for RESEA. This is a 9.9 percent reduction relative to the control group average of $6,839 in UI benefits drawn during the benefit year of the claim. Multiplying the estimate by the total number of individuals selected for RESEA in the study ( n=11,700 ) suggests that as a result of the program, the state paid out about $7.9 million fewer in UI benefits to claimants randomized during the study period over the same benefit year as their UI claims. This is much higher than the total expenditures of $2.99 million for the RESEA program over the study period, representing $2.64 in savings for the state budget for every $1 spent on the program.\n\n### 4.1 Methodological lessons (excerpt)\n\n[Table 3 — re-set by the extract editor from the HTML rendering; all values are verbatim. Columns: Outcome | Difference in means | Covariate adjusted | Fixed effects regression]\n\nOutcome | Difference in means | Covariate adjusted | Fixed effects regression\nWage | $1,153; p=0.022; 95% CI: [166, 2,141] | $1,137; p=0.014; 95% CI: [228, 2,047] | $1,100; p=0.027; 95% CI: [127, 2,073]\nReemployment | 1.47 pp; p=0.013; 95% CI: [0.32, 2.62] | 1.48 pp; p=0.012; 95% CI: [0.32, 2.63] | 1.49 pp; p=0.011; 95% CI: [0.34, 2.64]\nWeeks on UI | -1.99 wks; p<0.001; 95% CI: [-2.24, -1.75] | -1.93 wks; p<0.001; 95% CI: [-2.18, -1.68] | -1.97 wks; p<0.001; 95% CI: [-2.22, -1.72]\n\nTable 3: A comparison of the ITT estimates, two-sided p -values, and 95% confidence intervals for our primary outcomes from three different methodologies: the preregistered analysis based on eq. (1), the covariate adjusted analysis based on eq. (2), and the fixed effects regression in eq. (3). The leftmost column based on the preregistered analysis duplicates the rightmost column in Table 2 for ease of comparison.\n\nIf we directly compared treatment group and control group outcome averages without accounting for the week of randomization, the results would suggest RESEA selection had no detectable average effect on the wage and reemployment outcomes (column 4, Table 2). However, such an analysis is potentially biased under the experimental design because it does not respect the blocked randomization, which makes the week of randomization a known confounder. For example, weeks with a larger number of UI applicants, which had a higher proportion of control group individuals, tended to have lower-earning applicants (Fig. 7), thereby inflating the average wage outcome in the control group relative to the treatment group. This is critical because out of the thirteen publically available studies of RESEA-related employment assistance programs rated by CLEAR as having high causal evidence, six used block randomization like we do, yet only two of these (Black, Smith, Berger, & Noel., 2002; Klerman et al., 2019) properly adjusted for the block. Three others among these six studies used regression or matching methods in an attempt to control for observed demographic variables but not the block (Poe-Yamagata et al., 2011; Michaelides et al., 2012; Manoli et al., 2018), while the remaining study (Michaelides & Mueser, 2018) fit a linear regression model with the block indicators as fixed effects, as did two other more recent evaluations in Nevada (Michaelides & Mian, 2021; Brigandi et al., 2024) . These fixed effects regressions amount to estimating the coefficient in the regression model\nSOURCE EXTRACT — arxiv-2603.03260v2\nTitle: Does Entry of Food-and-Drink Establishments Raise Local House Prices? Event-Study Evidence from London\nAuthors: Wanqi Liu; Rong Zhao\nBibliographic record: arXiv:2603.03260v2 [physics.soc-ph, econ.GN], version 1 submitted 3 Mar 2026, version 2 (this extract) submitted 2 Apr 2026. Abstract page: https://arxiv.org/abs/2603.03260v2\nRetrieved: https://arxiv.org/html/2603.03260v2 on 2026-10-30T03:23:18Z (SHA-256 of the retrieved HTML: 6e9a3c5fead449da09a981b0bacc36e1a4f652750caef972a173c3193525c327)\nLicense: CC BY 4.0 (license shown on the arXiv abstract page; https://creativecommons.org/licenses/by/4.0/). Reproduced in part with attribution.\nExtract contents: title, authors and abstract; Section 3 'Empirical Strategy and Main Results' in full (equation (1), Table 2, Table 3 with notes, Figure 2 caption, Section 3.3); Section 5 'Conclusion'.\nOmitted: Sections 1-2 and 4, the appendix (Tables 4-5), the references.\nRendering note: converted from the HTML rendering to plain text. Tables are rendered one row per line with \" | \" separating cells; in regression tables the line following a coefficient row holds the standard errors in parentheses, exactly as printed. Mathematical expressions appear as LaTeX source; non-breaking spaces were replaced by ordinary spaces. No numbers were altered.\n================================================================\n\n# Does Entry of Food-and-Drink Establishments Raise Local House Prices? Event-Study Evidence from London\n\nWanqi Liu, Rong Zhao (Centre for Advanced Spatial Analysis, University College London)\n\n###### Abstract\n\nRestaurants, cafes, pubs, and takeaways are among the most visible markers of neighborhood change, yet whether their arrival is capitalised into nearby housing values remains empirically unsettled. We assemble a London-wide panel linking Land Registry prices, non-domestic EPC lodgement timings for food-and-drink establishments, and neighborhood amenity measures at the LSOA level. Our preferred annual event-study design defines treatment as the first clean-onset year in which an LSOA records at least two eligible EPC lodgements for food-and-drink establishments, after a two-year lookback with no prior entries. In this specification, pre-trend tests are not rejected in either the stacked or Sun-Abraham estimators, and log house prices rise gradually from about 0.5% in the event year to roughly 3.4–3.7% by years four and five. The results are consistent with local amenity capitalization following commercial entry, while remaining appropriately cautious about endogenous siting and concurrent redevelopment.\n\n## 3 Empirical Strategy and Main Results\n\n### 3.1 Empirical Strategy\n\nOur main estimand is the reduced-form change in local log house prices following the first clean entry wave of food-and-drink establishments in an LSOA, relative to untreated LSOAs that remain at risk in the relevant event-time comparisons. It is best interpreted as a local capitalization estimand: it bundles direct amenity value, signaling, and related neighborhood revaluation, rather than isolating a single structural channel.\n\nThe central identification threat is endogenous siting. If businesses open where appreciation was already accelerating, post-entry coefficients will confound commercial entry with prior neighborhood change. To trace the dynamic price response while reducing that concern, we exploit the staggered timing of openings of food-and-drink establishments using EPC lodgement records for restaurants, cafes, drinking establishments, and takeaways. In the preferred specification, treatment begins in the first year an LSOA records at least two such EPC lodgements after a two-year lookback window with no prior eligible entry. Let E_{i} denote the treatment year for LSOA i (undefined for never-treated units). This clean-onset rule is intended to capture a discrete local entry wave rather than ongoing turnover. Our annual event-study specification is:\n\ny_{it}=\\alpha_{i}+\\delta_{t}+\\sum_{\\begin{subarray}{c}\\tau=-5\\\\\n\\tau\\neq-1\\end{subarray}}^{5}\\beta_{\\tau}\\,\\mathbf{1}\\{t-E_{i}=\\tau\\}+\\varepsilon_{it} | | | (1)\n\nwhere \\mathbf{1}\\{t-E_{i}=\\tau\\} equals one when LSOA i is observed \\tau years relative to its treatment date, with \\tau=-1 as the omitted reference period. The coefficients \\{\\beta_{\\tau}\\} trace out the dynamic treatment effect, while the pre-period coefficients \\beta_{-5},\\ldots,\\beta_{-2} provide the main visual and joint-test check on parallel trends.\n\n#### Estimator comparisons.\n\nBecause staggered treatment timing can induce negative weighting in conventional TWFE [22], we treat the stacked design as the main estimator and compare it with a Sun and Abraham [23] interaction-weighted estimator. The point of this comparison is to check whether the post-entry path survives an alternative treatment-timing aggregation scheme, not to elevate a broad specification horse race into the main text.\n\n### 3.2 Main Event-Study Results\n\nUsing EPC lodgement records, we construct an annual design for entry of food-and-drink establishments in which treatment begins when an LSOA first records at least two eligible lodgements after a two-year clean-onset window with no prior entry. The preferred stacked sample contains 657,197 LSOA-year observations, 774 treated-role LSOAs, and 4,459 control-role LSOAs across risk sets. Treatment is distributed across sixteen cohorts from 2008 to 2023, with the largest cohort in 2009 (178 treated units) and meaningful support throughout the subsequent decade. Appendix cohort tables report the full cohort composition.\n\n#### Support across event time.\n\nTable 2 summarizes the support behind the stacked sample. Treated observations are most numerous near event time and then decline as the window moves farther into the tails, but support remains substantial even at \\tau=5 , where 546 treated observations from 11 contributing stacks remain in the estimating sample. This pattern matters for interpretation: medium-run coefficients are identified from fewer cohorts than the event-year effect, so later horizons should be read as economically informative but mechanically noisier.\n\nTable 2: Event-Time Support in the Stacked Sample\n\nEvent Time | Treated Obs. | Treated LSOAs | Contributing Stacks\n\n-5 | 572 | 572 | 14\n\n-4 | 751 | 751 | 15\n\n-3 | 769 | 769 | 16\n\n-2 | 763 | 763 | 16\n\n-1 | 761 | 761 | 16\n\n0 | 756 | 756 | 16\n\n1 | 689 | 689 | 15\n\n2 | 648 | 648 | 14\n\n3 | 610 | 610 | 13\n\n4 | 586 | 586 | 12\n\n5 | 546 | 546 | 11\n\n•\n\nNotes: Support counts from the preferred clean-onset stacked design for entry of food-and-drink establishments. “Contributing stacks” records how many cohort-specific risk sets identify each event-time coefficient.\n\n#### Headline dynamic pattern.\n\nFigure 2 reports the preferred clean-onset event-study path and overlays the event-time support behind each coefficient. Pre-treatment coefficients are small and imprecise, and the stacked joint pre-trend test does not reject ( p=0.241 ). The estimated effect is close to zero at event time and then turns positive: the stacked coefficient is 0.005 at \\tau=0 , 0.012 at \\tau=1 , 0.018 at \\tau=2 , 0.037 at \\tau=4 , and 0.034 by \\tau=5 . Interpreted in logs, these magnitudes correspond to a gradual appreciation of roughly 0.5% in the event year and about 3.4–3.7% after four to five years. The pattern is notable for its slope as much as for its level: prices do not jump immediately, but instead drift upward as the new commercial entry becomes part of the local amenity bundle.\n\n#### Estimator comparison and design diagnostics.\n\nFor the preferred clean-onset design, the Sun-Abraham interaction-weighted path closely tracks the stacked path in the post-treatment period. The Sun coefficients are 0.005 at \\tau=0 , 0.012 at \\tau=1 , 0.016 at \\tau=2 , 0.036 at \\tau=4 , and 0.033 at \\tau=5 , and its joint pre-trend test is not rejected ( p=0.472 ). Table 3 places the preferred specification next to two nearby alternatives. Relative to the broader baseline threshold-2 design, clean-onset imposes more discipline on timing while preserving a similar medium-run magnitude. Relative to the neighbor-buffer variant, it avoids an extra layer of spatial pruning that mechanically strengthens post-treatment coefficients but yields tighter pre-trend p -values. We therefore retain the unbuffered clean-onset design as the headline specification.\n\nTable 3: Main Design Diagnostics for the Headline Event-Study Specification\n\n[Extract editor's note: the header row of Table 3 is garbled in the HTML rendering; the six columns are, in order: Specification | Treated-role LSOAs | Stacked pre-trend p | Sun pre-trend p | tau=4 coefficient | tau=5 coefficient.]\n\np p \\tau=4 \\tau=5 Specification | Treated-role LSOAs | Stacked pre-trend | Sun pre-trend | |\n\nBaseline threshold-2 | 1,084 | 0.342 | 0.223 | 0.029 | 0.022\n\nClean-onset threshold-2 | 774 | 0.241 | 0.472 | 0.037 | 0.034\n\nClean-onset + neighbor buffer | 774 | 0.126 | 0.239 | 0.042 | 0.040\n\n•\n\nNotes: Entries in the last two columns are log-point coefficients relative to \\tau=-1 . The baseline row uses the broader threshold-2 treatment without the clean-onset restriction. The preferred row uses the clean-onset threshold-2 treatment with a two-year lookback window and no prior eligible entry. The buffer row applies a first-order neighboring-control exclusion to the preferred design.\n\nFigure 2: Preferred clean-onset event-study estimates for entry of food-and-drink establishments. Point estimates are reported relative to the year before treatment ( \\tau=-1 ), which is shown as the open reference marker at zero, and plotted with 95% confidence intervals. Gray bars report the number of treated observations contributing to each event-time coefficient. The estimated path rises gradually from near zero in the event year to roughly 3.4–3.7% by years four and five after entry.\n\n### 3.3 Robustness Checks\n\nThe main robustness question is whether the positive post-entry path survives plausible threats from spatial spillovers and concurrent redevelopment. Excluding first-order neighboring controls leaves the qualitative pattern intact and slightly strengthens post-treatment coefficients, but it also yields tighter pre-trend p -values. We therefore treat the buffer variant as a supporting robustness check rather than as a replacement for the headline design. Planning-start outcome diagnostics are reported in Appendix Table 5 and are not used to select the preferred specification.\n\n## 5 Conclusion\n\nThis paper studies whether entry of food-and-drink establishments is followed by changes in neighborhood house prices in Greater London. In the preferred clean-onset event-study estimates, areas exposed to entry experience a gradual post-entry appreciation that reaches roughly 3.4–3.7% after four to five years. 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Sho Miyaji; Suguru Otani\nBibliographic record: arXiv:2505.04555v3 [econ.GN], version 1 submitted 7 May 2025, version 2 submitted 27 May 2025, version 3 (this extract) submitted 16 Mar 2026. Abstract page: https://arxiv.org/abs/2505.04555v3\nRetrieved: https://arxiv.org/html/2505.04555v3 on 2026-10-30T03:23:18Z (SHA-256 of the retrieved HTML: f2b68299cbc49f208a0340bd233007fe922f6d4245e0a642db526662d359789b)\nLicense: CC BY 4.0 (license shown on the arXiv abstract page; https://creativecommons.org/licenses/by/4.0/). Reproduced in part with attribution.\nExtract contents: title, authors and abstract; Appendix A.1 'Elasticities Related to Minimum Wages' in full (Table 2 with its note and the discussion paragraph).\nOmitted: Sections 1-7, the other appendices, the references. The 'Current version' date printed in the HTML rendering is generated at rendering time and is not the submission date.\nRendering note: converted from the HTML rendering to plain text. Tables are rendered one row per line with \" | \" separating cells; in regression tables the line following a coefficient row holds the standard errors in parentheses, exactly as printed. Mathematical expressions appear as LaTeX source; non-breaking spaces were replaced by ordinary spaces. No numbers were altered.\n================================================================\n\n# Just After Minimum Wage Hikes: Short-Run Labor-Demand Response and Reallocation\n\nHayato Kanayama (Waseda University), Sho Miyaji (Yale University), Suguru Otani (The University of Tokyo)\n\n###### Abstract\n\nHow labor markets adjust immediately after minimum wage hikes remains an open, policy-relevant question. This paper studies short-run minimum-wage effects in Japan’s spot labor market using Timee data and a wage-bin difference-in-differences design. We find a 2% employment decline in affected bins, driven by reduced vacancy creation rather than worker supply. Effects are more negative where the minimum-wage bite is higher and in low-wage occupations. Using job descriptions and amenity information, we document reallocation across job types: postings shift toward greater amenity provision and experienced-worker targeting, while female-targeted descriptions become less common, suggesting short-run labor-demand adjustments may foreshadow longer-run reallocation.\n\nKeywords: minimum wage, employment, job amenities, gig workers, spot work, difference-in-differences\n\nJEL codes: J21, J23, J38, J88\n\n## Appendix A Additional Analysis\n\n### A.1 Elasticities Related to Minimum Wages\n\nFollowing the method of Cengiz et al. (2019), we estimate (i) the elasticity of employment with respect to minimum wages and (ii) the employment elasticity with respect to the affected wages.\n\nTable 2: Impact of Minimum Wages on Employment and Wages\n\n| Estimate (SE)\n\nMissing jobs below new MW | -0.03\n\n| (0.006)\n\nExcess jobs above new MW | 0.012\n\n| (0.002)\n\nAffected wages | 0.366\n\n| (0.171)\n\nAffected employment | -0.268\n\n| (0.091)\n\nEmployment elasticity w.r.t MW | -0.388\n\n| (0.132)\n\nEmp. elasticity w.r.t affected wage | -0.732\n\n| (0.091)\n\nJob below new MW | 0.068\n\n% MW changes | 0.047\n\nNote: The table reports the effects of a minimum wage increase based on the event study analysis exploiting 47 prefecture-level minimum wage changes in 2023 (i.e., about 4% minimum wage increase). The table reports six-month averaged post-treatment estimates on missing jobs up to 100 JPY below the new minimum wage, excess jobs at and up to 300 JPY above it, employment, and wages. Robust standard errors in parentheses are clustered by wage bins separated by 10 JPY.\n\nTable 2 reports six-month–averaged post-treatment effects for the baseline specification depicted in Figure 7.\nThe magnitude of missing jobs below new minimum wages exceeds the magnitude of excess jobs above new minimum wages in the six-month window.\nThe estimated employment elasticity with respect to the minimum wage is - 0.388 , which is consistent with Figure 7. Unlike the findings of Cengiz et al. (2019) and Dube and Zipperer (2024), our own-wage employment elasticity is - 0.732 , indicating a larger (absolute) employment response to affected wages than the median estimate (- 0.13 ) reported by Dube and Lindner (2024).\nSOURCE EXTRACT — arxiv-2510.03658v1\nTitle: Who benefits the most? Direct and indirect effects of a free cesarean section policy in Benin\nAuthors: Selidji Caroline Tossou\nBibliographic record: arXiv:2510.03658v1 [econ.GN], submitted 4 Oct 2025 (version 1, the only version at retrieval). Abstract page: https://arxiv.org/abs/2510.03658v1\nRetrieved: https://arxiv.org/html/2510.03658v1 on 2026-10-30T03:23:18Z (SHA-256 of the retrieved HTML: f2d9f04dcf4789983c28f97dc13705eb2d6ed583c4860c940f921d7b549aea59)\nLicense: CC BY 4.0 (license shown on the arXiv abstract page; https://creativecommons.org/licenses/by/4.0/). Reproduced in part with attribution.\nExtract contents: title, author and abstract; Section 4.1 'Infant Mortality' (text with footnotes 9-12); Table 3 'Probability of infant death and stillbirth' with its notes.\nOmitted: Sections 1-3, 4.2-6, Tables 1-2 and 4-16, the references. The date printed in the HTML rendering is generated at rendering time and is not the submission date.\nRendering note: converted from the HTML rendering to plain text. Tables are rendered one row per line with \" | \" separating cells; in regression tables the line following a coefficient row holds the standard errors in parentheses, exactly as printed. Mathematical expressions appear as LaTeX source; non-breaking spaces were replaced by ordinary spaces. No numbers were altered.\n================================================================\n\n# Who benefits the most? Direct and indirect effects of a free cesarean section policy in Benin\n\nSelidji Caroline Tossou (University of Wisconsin-Madison)\n\n###### Abstract\n\nThis paper evaluates the causal effect of the access to Benin’s free cesarean section policy on females and their children. I use a large sample of Demographic and Health Surveys (DHS) for West African countries and analyze how the exemption of the cesarean section user fees for females in Benin directly impacts maternal and infant mortality, family size decisions, and labor market participation. I use a Difference in Differences approach and find that having access to the free cesarean section policy significantly reduces the number of stillbirths and infant mortality by 0.0855 (a 18.79 percentage change). Second, for the surviving children, I find that access to the free cesarean section increases the likelihood of maternal mortality by 0.00465 (a 5.21 percentage change). The policy is effective at reducing infant mortality and saving the newborn. However, it harms the mother’s health which translates to lower fertility after the first birth and decreased maternal labor supply post-birth.\n\n## 4 Findings\n\n### 4.1 Infant Mortality\n\nI first investigate the infant death rate under the policy.\nFigure 15 shows that the exemption of cesarean section fees in Benin leads to an increase in the use of the service. What are the implications for infant mortality? I use a Difference in Differences specification to explore the possible impacts of access to the free cesarean section on infant mortality. The result in table 2 suggests that the access to the policy significantly reduced the number of infant death and stillbirth in Benin by 0.0855 (this represents a percentage change of 18.79 percent^9^9\n9\n\nI divide the estimate of beta by the mean of the dependent variable: -0.0855/0.455=-0.1879 ). This means that for over 100 newborns who would have died in the absence of the policy, approximately 18 are saved because of the access to the exemption of the cesarean section user fees. This result is promising and aligns with the goals of the free cesarean section policy, which primarily intends to lower the infant mortality in Benin. To the best of my knowledge, this is the first paper that evaluates the causal effect of free cesarean section policy on Benin’s infant mortality. Wealth and education attainment play a role in decreasing infant mortality. This can be explained by the fact that the free cesarean section covers only the surgery and a medicine kit for the mother. It does not cover prenatal and antepartum checkups. So a pregnant woman who has the means is more likely to identify and prevent any problems related to the pregnancy and the newborn’s health. Table 3 gives an easier interpretation of the effect of the access to the policy on infant mortality. In this table, the outcome of interest is a binary variable that takes value 1 if a female has an infant death or a pregnancy loss in the three years preceding the data collection and 0 otherwise. Thus, I interpret the coefficient \\hat{\\beta_{1}} as the effect of the policy on the likelihood of infant mortality. Using my most preferred specification (Column (4)), the result suggests that access to the policy decreases the likelihood of infant death or pregnancy loss of a female in Benin by 0.0962. Compared to the mean of the dependent variable, this effect represents a percentage change of 36.85 percent. To see which female category is driving this result, I decompose the effect by age group, wealth index, and education attainment.\n\nThe first panel of table 4 presents the stratification by age group. The policy is more effective at reducing infant mortality for females older than 25. For females between 15 and 24, the probability of infant mortality is reduced by only 4.65 percent compared to a reduction of 30.85 percent for a female between 25 and 34, a reduction of 43.53 percent for females between 35 and 44, and the highest decrease of 47.25 percent for females between 45 and 49^10^10\n10\n\nThese are the percentage change of infant mortality obtained by dividing the coefficient estimated by the mean of the dependent variable. The same exercise is done by using the wealth index of females. The results in the second panel of table 4 suggest that the effect of the free cesarean section on infant mortality is the biggest for females who are the poorest, poorer, or have a middle wealth index^11^11\n11\n\nThe modalities Poorest, Poorer, Middle, Richer, and Richest are pre-computed in the DHS data (46.36 percent, 35.84 percent, and 41.72 percent respectively). For the richer and richest females, the effect of the policy is a percentage change reduction of 28.52 percent and 16.47 percent on the likelihood of infant death. The last panel of table 4 gives a stratification by education level. The highest effect of the policy on the reduction of the likelihood of infant death (-39.07 percent) is for females who have no education level. The lowest effect of the policy on the reduction of the likelihood of infant death (-1.4 percent) is for females who have higher education levels.^12^12\n12\n\nI test the difference between all the coefficients and they are all significant and statistically different\n\nTo summarize, I find that access to the free cesarean section in Benin reduces the likelihood of infant mortality on average by 36.85 percent. The policy is more effective at reducing infant death for older females, females who are below the middle wealth index, and females who have no education.\n\nTable 3: Probability of infant death and stillbirth\n\n| Probability of Infant death or stillbirth | | |\n\n| (1) | (2) | (3) | (4)\n\nTreatment | -0.0911 | -0.0908 | -0.0961 | -0.0962\n\n| (0.0113) | (0.0113) | (0.0126) | (0.0129)\n\nEducation Attainment | -0.0578 | -0.0576 | -0.0443 | -0.0443\n\n| (0.00346) | (0.00340) | (0.00415) | (0.00420)\n\nAge of Female | 0.0168 | 0.0170 | 0.0171 | 0.0171\n\n| (0.00108) | (0.00112) | (0.00104) | (0.00108)\n\nAge of Partner | | -0.000425 | -0.000448 | -0.000435\n\n| | (0.000183) | (0.000151) | (0.000152)\n\nWealth Index | | | -0.0302 | -0.0302\n\n| | | (0.00277) | (0.00277)\n\nMarital Status | | | | 0.00128\n\n| | | | (0.00421)\n\nCountry Fixed Effect | Yes | Yes | Yes | Yes\n\nTime Fixed Effect. | Yes | Yes | Yes | Yes\n\n_cons | -0.129 | -0.114 | -0.0400 | -0.0406\n\n| (0.0323) | (0.0298) | (0.0266) | (0.0255)\n\nObservations | 196554 | 196424 | 196424 | 196423\n\n% Change | -0.3490 | -0.3478 | -0.3681 | -0.3685\n\nR-squared | 0.196 | 0.197 | 0.204 | 0.204\n\nMean Dep. Var. | 0.261 | 0.261 | 0.261 | 0.261\n\nStandard errors in parentheses; Standard errors are clustered at the household level. | | | |\n\nDep. Var. Mean is the dependent variable mean. Treatment is Benin Females after 2008 | | | |","is_error":false}]},"uuid":"3de1a918-3090-4238-a390-b8a8a4abf2ce","timestamp":"2026-10-30T05:17:17.347Z","toolUseResult":{"stdout":"SOURCE EXTRACT — arxiv-2505.04555v3\nTitle: Just After Minimum Wage Hikes: Short-Run Labor-Demand Response and Reallocation\nAuthors: Hayato Kanayama; Sho Miyaji; Suguru Otani\nBibliographic record: arXiv:2505.04555v3 [econ.GN], version 1 submitted 7 May 2025, version 2 submitted 27 May 2025, version 3 (this extract) submitted 16 Mar 2026. Abstract page: https://arxiv.org/abs/2505.04555v3\nRetrieved: https://arxiv.org/html/2505.04555v3 on 2026-10-30T03:23:18Z (SHA-256 of the retrieved HTML: f2b68299cbc49f208a0340bd233007fe922f6d4245e0a642db526662d359789b)\nLicense: CC BY 4.0 (license shown on the arXiv abstract page; https://creativecommons.org/licenses/by/4.0/). Reproduced in part with attribution.\nExtract contents: title, authors and abstract; Appendix A.1 'Elasticities Related to Minimum Wages' in full (Table 2 with its note and the discussion paragraph).\nOmitted: Sections 1-7, the other appendices, the references. The 'Current version' date printed in the HTML rendering is generated at rendering time and is not the submission date.\nRendering note: converted from the HTML rendering to plain text. Tables are rendered one row per line with \" | \" separating cells; in regression tables the line following a coefficient row holds the standard errors in parentheses, exactly as printed. Mathematical expressions appear as LaTeX source; non-breaking spaces were replaced by ordinary spaces. No numbers were altered.\n================================================================\n\n# Just After Minimum Wage Hikes: Short-Run Labor-Demand Response and Reallocation\n\nHayato Kanayama (Waseda University), Sho Miyaji (Yale University), Suguru Otani (The University of Tokyo)\n\n###### Abstract\n\nHow labor markets adjust immediately after minimum wage hikes remains an open, policy-relevant question. This paper studies short-run minimum-wage effects in Japan’s spot labor market using Timee data and a wage-bin difference-in-differences design. We find a 2% employment decline in affected bins, driven by reduced vacancy creation rather than worker supply. Effects are more negative where the minimum-wage bite is higher and in low-wage occupations. Using job descriptions and amenity information, we document reallocation across job types: postings shift toward greater amenity provision and experienced-worker targeting, while female-targeted descriptions become less common, suggesting short-run labor-demand adjustments may foreshadow longer-run reallocation.\n\nKeywords: minimum wage, employment, job amenities, gig workers, spot work, difference-in-differences\n\nJEL codes: J21, J23, J38, J88\n\n## Appendix A Additional Analysis\n\n### A.1 Elasticities Related to Minimum Wages\n\nFollowing the method of Cengiz et al. (2019), we estimate (i) the elasticity of employment with respect to minimum wages and (ii) the employment elasticity with respect to the affected wages.\n\nTable 2: Impact of Minimum Wages on Employment and Wages\n\n| Estimate (SE)\n\nMissing jobs below new MW | -0.03\n\n| (0.006)\n\nExcess jobs above new MW | 0.012\n\n| (0.002)\n\nAffected wages | 0.366\n\n| (0.171)\n\nAffected employment | -0.268\n\n| (0.091)\n\nEmployment elasticity w.r.t MW | -0.388\n\n| (0.132)\n\nEmp. elasticity w.r.t affected wage | -0.732\n\n| (0.091)\n\nJob below new MW | 0.068\n\n% MW changes | 0.047\n\nNote: The table reports the effects of a minimum wage increase based on the event study analysis exploiting 47 prefecture-level minimum wage changes in 2023 (i.e., about 4% minimum wage increase). The table reports six-month averaged post-treatment estimates on missing jobs up to 100 JPY below the new minimum wage, excess jobs at and up to 300 JPY above it, employment, and wages. Robust standard errors in parentheses are clustered by wage bins separated by 10 JPY.\n\nTable 2 reports six-month–averaged post-treatment effects for the baseline specification depicted in Figure 7.\nThe magnitude of missing jobs below new minimum wages exceeds the magnitude of excess jobs above new minimum wages in the six-month window.\nThe estimated employment elasticity with respect to the minimum wage is - 0.388 , which is consistent with Figure 7. Unlike the findings of Cengiz et al. (2019) and Dube and Zipperer (2024), our own-wage employment elasticity is - 0.732 , indicating a larger (absolute) employment response to affected wages than the median estimate (- 0.13 ) reported by Dube and Lindner (2024).\nSOURCE EXTRACT — arxiv-2510.03658v1\nTitle: Who benefits the most? Direct and indirect effects of a free cesarean section policy in Benin\nAuthors: Selidji Caroline Tossou\nBibliographic record: arXiv:2510.03658v1 [econ.GN], submitted 4 Oct 2025 (version 1, the only version at retrieval). Abstract page: https://arxiv.org/abs/2510.03658v1\nRetrieved: https://arxiv.org/html/2510.03658v1 on 2026-10-30T03:23:18Z (SHA-256 of the retrieved HTML: f2d9f04dcf4789983c28f97dc13705eb2d6ed583c4860c940f921d7b549aea59)\nLicense: CC BY 4.0 (license shown on the arXiv abstract page; https://creativecommons.org/licenses/by/4.0/). Reproduced in part with attribution.\nExtract contents: title, author and abstract; Section 4.1 'Infant Mortality' (text with footnotes 9-12); Table 3 'Probability of infant death and stillbirth' with its notes.\nOmitted: Sections 1-3, 4.2-6, Tables 1-2 and 4-16, the references. The date printed in the HTML rendering is generated at rendering time and is not the submission date.\nRendering note: converted from the HTML rendering to plain text. Tables are rendered one row per line with \" | \" separating cells; in regression tables the line following a coefficient row holds the standard errors in parentheses, exactly as printed. Mathematical expressions appear as LaTeX source; non-breaking spaces were replaced by ordinary spaces. No numbers were altered.\n================================================================\n\n# Who benefits the most? Direct and indirect effects of a free cesarean section policy in Benin\n\nSelidji Caroline Tossou (University of Wisconsin-Madison)\n\n###### Abstract\n\nThis paper evaluates the causal effect of the access to Benin’s free cesarean section policy on females and their children. I use a large sample of Demographic and Health Surveys (DHS) for West African countries and analyze how the exemption of the cesarean section user fees for females in Benin directly impacts maternal and infant mortality, family size decisions, and labor market participation. I use a Difference in Differences approach and find that having access to the free cesarean section policy significantly reduces the number of stillbirths and infant mortality by 0.0855 (a 18.79 percentage change). Second, for the surviving children, I find that access to the free cesarean section increases the likelihood of maternal mortality by 0.00465 (a 5.21 percentage change). The policy is effective at reducing infant mortality and saving the newborn. However, it harms the mother’s health which translates to lower fertility after the first birth and decreased maternal labor supply post-birth.\n\n## 4 Findings\n\n### 4.1 Infant Mortality\n\nI first investigate the infant death rate under the policy.\nFigure 15 shows that the exemption of cesarean section fees in Benin leads to an increase in the use of the service. What are the implications for infant mortality? I use a Difference in Differences specification to explore the possible impacts of access to the free cesarean section on infant mortality. The result in table 2 suggests that the access to the policy significantly reduced the number of infant death and stillbirth in Benin by 0.0855 (this represents a percentage change of 18.79 percent^9^9\n9\n\nI divide the estimate of beta by the mean of the dependent variable: -0.0855/0.455=-0.1879 ). This means that for over 100 newborns who would have died in the absence of the policy, approximately 18 are saved because of the access to the exemption of the cesarean section user fees. This result is promising and aligns with the goals of the free cesarean section policy, which primarily intends to lower the infant mortality in Benin. To the best of my knowledge, this is the first paper that evaluates the causal effect of free cesarean section policy on Benin’s infant mortality. Wealth and education attainment play a role in decreasing infant mortality. This can be explained by the fact that the free cesarean section covers only the surgery and a medicine kit for the mother. It does not cover prenatal and antepartum checkups. So a pregnant woman who has the means is more likely to identify and prevent any problems related to the pregnancy and the newborn’s health. Table 3 gives an easier interpretation of the effect of the access to the policy on infant mortality. In this table, the outcome of interest is a binary variable that takes value 1 if a female has an infant death or a pregnancy loss in the three years preceding the data collection and 0 otherwise. Thus, I interpret the coefficient \\hat{\\beta_{1}} as the effect of the policy on the likelihood of infant mortality. Using my most preferred specification (Column (4)), the result suggests that access to the policy decreases the likelihood of infant death or pregnancy loss of a female in Benin by 0.0962. Compared to the mean of the dependent variable, this effect represents a percentage change of 36.85 percent. To see which female category is driving this result, I decompose the effect by age group, wealth index, and education attainment.\n\nThe first panel of table 4 presents the stratification by age group. The policy is more effective at reducing infant mortality for females older than 25. For females between 15 and 24, the probability of infant mortality is reduced by only 4.65 percent compared to a reduction of 30.85 percent for a female between 25 and 34, a reduction of 43.53 percent for females between 35 and 44, and the highest decrease of 47.25 percent for females between 45 and 49^10^10\n10\n\nThese are the percentage change of infant mortality obtained by dividing the coefficient estimated by the mean of the dependent variable. The same exercise is done by using the wealth index of females. The results in the second panel of table 4 suggest that the effect of the free cesarean section on infant mortality is the biggest for females who are the poorest, poorer, or have a middle wealth index^11^11\n11\n\nThe modalities Poorest, Poorer, Middle, Richer, and Richest are pre-computed in the DHS data (46.36 percent, 35.84 percent, and 41.72 percent respectively). For the richer and richest females, the effect of the policy is a percentage change reduction of 28.52 percent and 16.47 percent on the likelihood of infant death. The last panel of table 4 gives a stratification by education level. The highest effect of the policy on the reduction of the likelihood of infant death (-39.07 percent) is for females who have no education level. The lowest effect of the policy on the reduction of the likelihood of infant death (-1.4 percent) is for females who have higher education levels.^12^12\n12\n\nI test the difference between all the coefficients and they are all significant and statistically different\n\nTo summarize, I find that access to the free cesarean section in Benin reduces the likelihood of infant mortality on average by 36.85 percent. The policy is more effective at reducing infant death for older females, females who are below the middle wealth index, and females who have no education.\n\nTable 3: Probability of infant death and stillbirth\n\n| Probability of Infant death or stillbirth | | |\n\n| (1) | (2) | (3) | (4)\n\nTreatment | -0.0911 | -0.0908 | -0.0961 | -0.0962\n\n| (0.0113) | (0.0113) | (0.0126) | (0.0129)\n\nEducation Attainment | -0.0578 | -0.0576 | -0.0443 | -0.0443\n\n| (0.00346) | (0.00340) | (0.00415) | (0.00420)\n\nAge of Female | 0.0168 | 0.0170 | 0.0171 | 0.0171\n\n| (0.00108) | (0.00112) | (0.00104) | (0.00108)\n\nAge of Partner | | -0.000425 | -0.000448 | -0.000435\n\n| | (0.000183) | (0.000151) | (0.000152)\n\nWealth Index | | | -0.0302 | -0.0302\n\n| | | (0.00277) | (0.00277)\n\nMarital Status | | | | 0.00128\n\n| | | | (0.00421)\n\nCountry Fixed Effect | Yes | Yes | Yes | Yes\n\nTime Fixed Effect. | Yes | Yes | Yes | Yes\n\n_cons | -0.129 | -0.114 | -0.0400 | -0.0406\n\n| (0.0323) | (0.0298) | (0.0266) | (0.0255)\n\nObservations | 196554 | 196424 | 196424 | 196423\n\n% Change | -0.3490 | -0.3478 | -0.3681 | -0.3685\n\nR-squared | 0.196 | 0.197 | 0.204 | 0.204\n\nMean Dep. Var. | 0.261 | 0.261 | 0.261 | 0.261\n\nStandard errors in parentheses; Standard errors are clustered at the household level. | | | |\n\nDep. Var. Mean is the dependent variable mean. Treatment is Benin Females after 2008 | | | 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verify a reference list against provided arXiv extracts.\n\nReads only data/, writes out/results.json deterministically. No randomness.\nRun from workspace root: ~/wp29/venv/bin/python out/analysis.py\n\"\"\"\nimport json, math, os, re, unicodedata\n\nDATA = \"data\"\nOUT = os.path.join(\"out\", \"results.json\")\n\n\ndef read_lines(path):\n with open(path, encoding=\"utf-8\") as f:\n return f.read().split(\"\\n\")\n\n\ndef wc_l(path):\n with open(path, \"rb\") as f:\n return f.read().count(b\"\\n\")\n\n\ndef norm_title(s):\n s = unicodedata.normalize(\"NFKD\", s)\n s = \"\".join(c for c in s if not unicodedata.combining(c))\n s = s.lower().replace(\"&\", \" and \")\n s = re.sub(r\"[^a-z0-9 ]\", \" \", s)\n return \" \".join(s.split())\n\n\ndef find_line(lines, needle):\n \"\"\"Return (1-based line number, line) of first line containing needle; raise if absent.\"\"\"\n for i, l in enumerate(lines, 1):\n if needle in l:\n return i, l\n raise AssertionError(f\"evidence not found: {needle!r}\")\n\n\ndef show(src, lines, needle):\n i, l = find_line(lines, needle)\n txt = l.strip()\n if len(txt) > 220: # long prose line: print the matched passage with context\n k = txt.index(needle)\n txt = \"...\" + txt[max(0, k - 40):k + len(needle) + 40] + \"...\"\n print(f\" [{src} L{i}] {txt}\")\n return l\n\n\nrefs = json.load(open(os.path.join(DATA, \"reference_list.json\"), encoding=\"utf-8\"))\nn_input_rows = {\"README.md\": wc_l(os.path.join(DATA, \"README.md\")),\n \"reference_list.json\": len(refs)}\n\n# ---- per-reference evidence specification -------------------------------------------\n# For each reference: the evidence strings (must exist verbatim in the extract) that decide\n# the finding check, arithmetic checks, and the decision with its locator.\nspec = {\n \"R1\": dict(\n evidence=[\"ATT | -0.399 | -0.283 | -0.431**\", \"| (0.412) | (0.279) | (0.210)\",\n \"% change | -32.9% | -24.7% | -35.0%\",\n \"This estimate is statistically significant at the 5% level\",\n \"using individual-level hospital records and a difference-in-differences estimator\",\n \"staggered introduction of DCRs across Swiss cities\",\n \"roughly 35% within 5 km of a facility\"],\n arithmetic=[(\"exp(-0.431)-1 (5 km % change)\", math.exp(-0.431) - 1, -0.350, 0.0005),\n (\"|ATT/SE| = 0.431/0.210 > 1.96\", 0.431 / 0.210, 2.052, 0.001)],\n supported=True,\n locator=\"arxiv-2609.27732v1 | Table 6, row ATT, column 5 km (with % change row; Section 6 text; abstract)\",\n note=\"ATT -0.431** (SE 0.210) and -35.0% at 5 km are printed in Table 6, 5% significance is stated in the text, and the staggered DiD on Swiss hospital records is described in the abstract.\"),\n \"R2\": dict(\n evidence=[\"large (N = 23,549) preregistered randomized controlled trial\",\n \"$1,153; p=0.022; 95% CI: [166, 2,141]\",\n \"1.47 pp; p=0.013; 95% CI: [0.32, 2.62]\",\n \"-1.99 weeks; p<0.001; 95% CI: [-2.24, -1.75]\",\n \"selection into the program increased annualized wages by $1,153\"],\n arithmetic=[],\n supported=True,\n locator=\"arxiv-2606.14621v1 | Table 2, column 'Average treatment effect estimate', rows Wage, Reemployment, Weeks on UI (N from abstract)\",\n note=\"Table 2's ATE column prints $1,153 (95% CI [166, 2,141]), 1.47 pp and -1.99 weeks, and the abstract gives the preregistered RCT with N = 23,549.\"),\n \"R3\": dict(\n evidence=[\"the stacked coefficient is 0.005 at \\\\tau=0 , 0.012 at \\\\tau=1 , 0.018 at \\\\tau=2 , 0.037 at \\\\tau=4 , and 0.034 by \\\\tau=5\",\n \"roughly 0.5% in the event year and about 3.4–3.7% after four to five years\",\n \"prices do not jump immediately, but instead drift upward\",\n \"Clean-onset threshold-2 | 774 | 0.241 | 0.472 | 0.037 | 0.034\"],\n arithmetic=[],\n supported=False,\n locator=\"arxiv-2603.03260v2 | Section 3.2 'Headline dynamic pattern' (stacked coefficients tau=0..5) and Table 3, row Clean-onset threshold-2, columns tau=4/tau=5\",\n note=\"The extract reports a gradual rise from 0.005 (about 0.5%) at the event year to 0.037/0.034 (3.4-3.7%) only by years four and five and states prices do not jump immediately, contradicting a 3.4-3.7% jump in the entry year with no later appreciation; title and year (2024) also disagree with the record.\"),\n \"R4\": dict(\n evidence=[\"Employment elasticity w.r.t MW | -0.388\", \"Emp. elasticity w.r.t affected wage | -0.732\",\n \"our own-wage employment elasticity is - 0.732\",\n \"short-run minimum-wage effects in Japan’s spot labor market\"],\n se_after={\"Employment elasticity w.r.t MW | -0.388\": \"| (0.132)\",\n \"Emp. elasticity w.r.t affected wage | -0.732\": \"| (0.091)\"},\n arithmetic=[(\"affected employment / affected wages = -0.268/0.366\", -0.268 / 0.366, -0.732, 0.0005)],\n supported=True,\n locator=\"arxiv-2505.04555v3 | Appendix A.1, Table 2, rows 'Employment elasticity w.r.t MW' and 'Emp. elasticity w.r.t affected wage' (Japan spot market from abstract)\",\n note=\"Table 2 prints -0.388 (0.132) and -0.732 (0.091), the text calls the latter the own-wage employment elasticity, and the abstract places the study in Japan's spot labor market.\"),\n \"R5\": dict(\n evidence=[\"Treatment | -0.0911 | -0.0908 | -0.0961 | -0.0962\", \"| (0.0113) | (0.0113) | (0.0126) | (0.0129)\",\n \"% Change | -0.3490 | -0.3478 | -0.3681 | -0.3685\", \"Mean Dep. Var. | 0.261 | 0.261 | 0.261 | 0.261\",\n \"Using my most preferred specification (Column (4))\",\n \"this effect represents a percentage change of 36.85 percent\"],\n arithmetic=[(\"0.0962 / 0.261 (relative to mean)\", 0.0962 / 0.261, 0.3685, 0.0005)],\n supported=True,\n locator=\"arxiv-2510.03658v1 | Table 3, row Treatment, column (4) (with % Change and Mean Dep. Var. rows; Section 4.1 text)\",\n note=\"Table 3 column (4), identified as the preferred specification in Section 4.1, prints -0.0962 (0.0129) and a -0.3685 change relative to the mean 0.261, matching the 36.85% stated in the text.\"),\n}\n\ndata_issues = [\n {\"issue\": \"arxiv-2609.27732v1: the 5 km CS-DR ATT -0.431 has SE 0.210 in Table 6 but SE 0.218 in Table A19; Table 6 reports 608 never-treated control regions while the Table A19 note says 640.\",\n \"handling\": \"R1 cites Table 6 (SE 0.210), which is printed verbatim; finding judged supported, and with either SE |t| > 1.96 so the 5% significance claim is unaffected. Inconsistency reported, not resolved.\"},\n {\"issue\": \"arxiv-2609.27732v1: abstract says fatal outcomes fall by 35%, Section 6.1 says approximately 30%; exp(-0.354)-1 = -29.8% from Table 7.\",\n \"handling\": \"Not part of any cited finding; recorded only.\"},\n {\"issue\": \"arxiv-2505.04555v3: the SE of the own-wage elasticity (0.091) equals the SE of 'Affected employment' (0.091); the point estimate -0.732 = -0.268/0.366 is reproduced but the SE cannot be checked from the extract.\",\n \"handling\": \"R4 quotes the printed value (0.091); judged supported as stated in the source, possible source typo flagged. The table note's 'about 4%' MW increase vs the '% MW changes' row 0.047 is also noted.\"},\n {\"issue\": \"arxiv-2603.03260v2: Table 3 header row is garbled in the HTML rendering (column order reconstructed by the extract editor).\",\n \"handling\": \"Used the editor's column order; the tau=4/tau=5 values 0.037/0.034 match the Section 3.2 text, so the reconstruction is corroborated.\"},\n {\"issue\": \"arxiv-2510.03658v1: abstract headline (0.0855, 18.79%, Table 2 not in extract, mean 0.455) differs from Table 3 (binary outcome, 0.0962, 36.85%, mean 0.261).\",\n \"handling\": \"Different outcome definitions per Section 4.1; R5 cites the Table 3 result, which is checked directly. Recorded only.\"},\n {\"issue\": \"arxiv-2606.14621v1: Tables 2 and 3 were re-set by the extract editor (values stated verbatim).\",\n \"handling\": \"Values taken as printed; Table 3 column 1 duplicates Table 2's ATE column, providing a cross-check (identical values).\"},\n]\n\nreference_checks, baseline = {}, {}\nn_items = 0\nfor r in refs:\n rid = r[\"id\"]\n src_rel = r[\"source_file\"]\n src_id = os.path.basename(src_rel).replace(\".txt\", \"\")\n path = os.path.join(DATA, src_rel)\n lines = read_lines(path)\n n_input_rows[src_rel] = wc_l(path)\n print(f\"\\n=== {rid}: {r['entry']}\")\n print(f\" cited_for: {r['cited_for']}\")\n # --- header ---\n _, tline = find_line(lines, \"Title: \")\n show(src_id, lines, \"Title: \")\n bib = show(src_id, lines, \"Bibliographic record:\")\n doc_title = tline.split(\"Title: \", 1)[1].strip()\n body_title = next(l[2:].strip() for l in lines if l.startswith(\"# \"))\n assert norm_title(doc_title) == norm_title(body_title), \"header/body title mismatch\"\n # --- entry parsing ---\n m = re.match(r\"^(.*?)\\((\\d{4})\\)\\.\\s*(.*?)\\.\\s*arXiv:(\\d{4}\\.\\d{5})\\.?$\", r[\"entry\"])\n entry_year, entry_title, entry_arxiv = int(m.group(2)), m.group(3), m.group(4)\n assert entry_arxiv in src_id, \"arXiv number mismatch\"\n title_ok = norm_title(entry_title) == norm_title(doc_title)\n # --- year rule: first submission year or year of reproduced version ---\n dates = re.findall(r\"submitted (\\d{1,2} \\w{3} (\\d{4}))\", bib)\n first_year = int(dates[0][1])\n ver = re.search(r\"arXiv:\\d{4}\\.\\d{5}v(\\d+)\", bib).group(1)\n if ver == \"1\":\n version_year = first_year\n else:\n version_year = int(re.search(r\"version %s \\(this extract\\) submitted \\d{1,2} \\w{3} (\\d{4})\" % ver, bib).group(1))\n year_ok = entry_year in (first_year, version_year)\n print(f\" title check: entry='{entry_title}' | doc='{doc_title}' -> {title_ok}\")\n print(f\" year check: entry={entry_year}, first submission={first_year}, reproduced v{ver}={version_year} -> {year_ok}\")\n # --- baseline: every number in cited_for appears somewhere in the extract ---\n txt = \"\\n\".join(lines).replace(\"−\", \"-\")\n nums = re.findall(r\"\\d[\\d,]*\\.?\\d*\", r[\"cited_for\"].replace(\"−\", \"-\"))\n nums = [n.rstrip(\".,\") for n in nums]\n missing = [n for n in nums if n not in txt]\n baseline[rid] = {\"title_matches\": title_ok, \"year_matches\": year_ok,\n \"all_cited_numbers_found\": len(missing) == 0, \"numbers_not_found\": missing}\n # --- finding check ---\n s = spec[rid]\n print(\" finding evidence:\")\n for e in s[\"evidence\"]:\n show(src_id, lines, e)\n n_items += 1\n for coef, se in s.get(\"se_after\", {}).items():\n i, _ = find_line(lines, coef)\n nxt = next(l for l in lines[i:] if l.strip())\n assert nxt.strip() == se, (coef, nxt)\n print(f\" [{src_id} SE row after '{coef}'] {nxt.strip()}\")\n for label, val, target, tol in s[\"arithmetic\"]:\n ok = abs(val - target) <= tol\n assert ok, label\n print(f\" arithmetic: {label} = {val:.4f} (printed {target}) ok\")\n reference_checks[rid] = {\"title_matches\": bool(title_ok), \"year_matches\": bool(year_ok),\n \"finding_supported\": bool(s[\"supported\"]), \"locator\": s[\"locator\"],\n \"note\": s[\"note\"]}\n print(f\" -> title {title_ok}, year {year_ok}, finding {s['supported']}\")\n\nunverifiable = [k for k, v in reference_checks.items()\n if not (v[\"title_matches\"] and v[\"year_matches\"] and v[\"finding_supported\"])]\nresults = {\n \"task_id\": \"F4-conf-04\",\n \"reference_checks\": reference_checks,\n \"unverifiable_references\": unverifiable,\n \"n_verified\": len(reference_checks) - len(unverifiable),\n \"feasibility\": \"complete\",\n \"feasibility_reason\": None,\n \"data_issues\": data_issues,\n \"n_input_rows\": n_input_rows,\n \"n_analysed\": len(reference_checks),\n \"random_seed\": None,\n \"baseline_naive_number_match\": baseline,\n \"n_evidence_strings_verified\": n_items,\n}\nos.makedirs(\"out\", exist_ok=True)\nwith open(OUT, \"w\", encoding=\"utf-8\") as f:\n json.dump(results, f, indent=2, ensure_ascii=False)\nprint(f\"\\nUnverifiable references: {unverifiable}; n_verified = {results['n_verified']}\")\n# Reference verification — F4-conf-04\n\n## Question\nFor each of the five references in `data/reference_list.json`, does (i) the title match the provided arXiv extract, (ii) the year agree with the first-submission year or the year of the reproduced version, and (iii) the finding attributed to it (\"cited_for\") appear in, or follow arithmetically from, the extract? A reference failing any check is unverifiable. Only the extracts under `data/sources/` were used as evidence.\n\n## Data and exclusions\nInputs: `reference_list.json` (5 items) and five extracts (line counts in `n_input_rows`: 134, 58, 107, 66, 91 lines; README 17 lines). All SHA-256 values match `data/README.md` (`out/state/data_audit.md`). No reference was excluded (`out/exclusions.csv`: 5 before, 5 after, 0 removed); `n_analysed` = 5.\nSource-internal issues found and how they were handled are listed in `data_issues`. None of them changes a verdict. The main ones are: Armendariz Table 6 gives SE 0.210 but Table A19 gives 0.218 for the same ATT; the two tables also give 608 vs 640 control regions. Kanayama's own-wage elasticity SE (0.091) is identical to the affected-employment SE. Liu & Zhao's Table 3 header is garbled. In Tossou, the abstract headline (Table 2, not in the extract) differs from the Table 3 result.\n\n## Method\n`out/analysis.py` does four things for each reference. (1) It takes the extract's header title and checks it equals the body title line. It then compares that title with the entry's title after normalising case, punctuation, diacritics and \"&\". (2) It reads the first-submission year and the year of the reproduced version from the \"Bibliographic record\" line and accepts the entry year if it equals either one. (3) It confirms that every evidence string used to decide the finding check appears verbatim in the extract and prints it with its line number. (4) It recomputes the arithmetic relations involved in the check. Whether each element of the finding (magnitude, uncertainty, timing, population) is supported was judged by me from the printed evidence, and the script records that judgement. Baseline (`baseline_naive_number_match`): a purely mechanical check that every number in \"cited_for\" occurs somewhere in the extract.\n\n## Results\n- `unverifiable_references` = [\"R3\"]; `n_verified` = 4.\n- R1 (Armendariz 2026): all three checks pass (`reference_checks.R1`). Evidence: Table 6, 5 km column, ATT −0.431** (0.210), % change −35.0%. The text says the estimate is significant at the 5% level, and the abstract describes the staggered DiD on Swiss hospital records.\n- R2 (Li, Pearson-Merkowitz & Yokum 2026): all checks pass (`reference_checks.R2`). Table 2's ATE column gives $1,153 (95% CI [166, 2,141]), 1.47 pp and −1.99 weeks. The abstract gives N = 23,549 and a preregistered RCT.\n- R3 (Liu & Zhao): **fails all three checks** (`reference_checks.R3`). The entry's title (\"Restaurants, Cafés and Neighbourhood Change: …\") is different from the document's title (\"Does Entry of Food-and-Drink Establishments Raise Local House Prices? Event-Study Evidence from London\"). The entry year 2024 matches neither 2026 (v1) nor 2026 (v2). The cited timing is contradicted by Section 3.2 and Table 3 (Clean-onset threshold-2 row). The extract reports 0.005 (≈0.5%) in the event year, rising gradually to 0.037/0.034 (3.4–3.7%) by years 4–5, and says \"prices do not jump immediately\".\n- R4 (Kanayama, Miyaji & Otani 2025): all checks pass (`reference_checks.R4`). The year 2025 equals the v1 submission year. Appendix A.1 Table 2 gives −0.388 (0.132) and −0.732 (0.091), and −0.268/0.366 = −0.732.\n- R5 (Tossou 2025): all checks pass (`reference_checks.R5`). Table 3 column (4), which the text names as the preferred specification, gives −0.0962 (0.0129) and a % change of −0.3685. The text states 36.85%, and 0.0962/0.261 = 0.3686.\n- Baseline: a naive number match finds every cited number in all five extracts (`baseline_naive_number_match`). So number matching alone would not catch R3's misattributed timing. In this case R3 is caught by the title and year checks anyway.\n\n## Uncertainty\nThere is no sampling uncertainty: the checks are deterministic text comparisons. The judgement calls are these:\n- **R1:** the SE cited (0.210) is printed in Table 6, but Table A19 prints 0.218 for the same estimate. I count the finding as supported because the citation reproduces Table 6 verbatim. The 5% significance holds under either SE (|t| = 2.05 or 1.98).\n- **R4:** the SE 0.091 is printed in the source but may be a source typo. It cannot be checked from the extract.\n- **R5:** 0.0962/0.261 gives 36.86%, while the paper prints 36.85% (−0.3685). The difference comes from rounding in the printed inputs and is accepted.\n\n## Limitations and open issues\n- The finding judgements involve my reading of the text. The script makes sure that the evidence exists and that the arithmetic holds, but it does not \"understand\" the claim.\n- The extracts omit most sections. A finding stated only in an omitted section could not have been verified. No reference relied on omitted material, except that the Tossou abstract cites Table 2, which is not in the extract and was not needed.\n- The source-internal inconsistencies listed in `data_issues` are reported but not resolved.\n- `feasibility` = \"complete\".\nstep,rule,n_before,n_after,n_removed,rationale\n0,no exclusions: all 5 references assessed,5,5,0,Task requires assessing every reference\nchecks.md\ncontract.md\ndata_audit.md\ngate_receipts\nlog.md\nphases.json\n\nout/state/gate_receipts:\n20261030T051633.690877Z.json\n20261030T051639.226441Z.json\n20261030T051652.405577Z.json\n20261030T051655.983844Z.json\n20261030T051705.353934Z.json","is_error":false}]},"uuid":"10cb433f-084c-433d-8eff-4207a195febc","timestamp":"2026-10-30T05:17:23.370Z","toolUseResult":{"stdout":"\"\"\"F4-conf-04: verify a reference list against provided arXiv extracts.\n\nReads only data/, writes out/results.json deterministically. No randomness.\nRun from workspace root: ~/wp29/venv/bin/python out/analysis.py\n\"\"\"\nimport json, math, os, re, unicodedata\n\nDATA = \"data\"\nOUT = os.path.join(\"out\", \"results.json\")\n\n\ndef read_lines(path):\n with open(path, encoding=\"utf-8\") as f:\n return f.read().split(\"\\n\")\n\n\ndef wc_l(path):\n with open(path, \"rb\") as f:\n return f.read().count(b\"\\n\")\n\n\ndef norm_title(s):\n s = unicodedata.normalize(\"NFKD\", s)\n s = \"\".join(c for c in s if not unicodedata.combining(c))\n s = s.lower().replace(\"&\", \" and \")\n s = re.sub(r\"[^a-z0-9 ]\", \" \", s)\n return \" \".join(s.split())\n\n\ndef find_line(lines, needle):\n \"\"\"Return (1-based line number, line) of first line containing needle; raise if absent.\"\"\"\n for i, l in enumerate(lines, 1):\n if needle in l:\n return i, l\n raise AssertionError(f\"evidence not found: {needle!r}\")\n\n\ndef show(src, lines, needle):\n i, l = find_line(lines, needle)\n txt = l.strip()\n if len(txt) > 220: # long prose line: print the matched passage with context\n k = txt.index(needle)\n txt = \"...\" + txt[max(0, k - 40):k + len(needle) + 40] + \"...\"\n print(f\" [{src} L{i}] {txt}\")\n return l\n\n\nrefs = json.load(open(os.path.join(DATA, \"reference_list.json\"), encoding=\"utf-8\"))\nn_input_rows = {\"README.md\": wc_l(os.path.join(DATA, \"README.md\")),\n \"reference_list.json\": len(refs)}\n\n# ---- per-reference evidence specification -------------------------------------------\n# For each reference: the evidence strings (must exist verbatim in the extract) that decide\n# the finding check, arithmetic checks, and the decision with its locator.\nspec = {\n \"R1\": dict(\n evidence=[\"ATT | -0.399 | -0.283 | -0.431**\", \"| (0.412) | (0.279) | (0.210)\",\n \"% change | -32.9% | -24.7% | -35.0%\",\n \"This estimate is statistically significant at the 5% level\",\n \"using individual-level hospital records and a difference-in-differences estimator\",\n \"staggered introduction of DCRs across Swiss cities\",\n \"roughly 35% within 5 km of a facility\"],\n arithmetic=[(\"exp(-0.431)-1 (5 km % change)\", math.exp(-0.431) - 1, -0.350, 0.0005),\n (\"|ATT/SE| = 0.431/0.210 > 1.96\", 0.431 / 0.210, 2.052, 0.001)],\n supported=True,\n locator=\"arxiv-2609.27732v1 | Table 6, row ATT, column 5 km (with % change row; Section 6 text; abstract)\",\n note=\"ATT -0.431** (SE 0.210) and -35.0% at 5 km are printed in Table 6, 5% significance is stated in the text, and the staggered DiD on Swiss hospital records is described in the abstract.\"),\n \"R2\": dict(\n evidence=[\"large (N = 23,549) preregistered randomized controlled trial\",\n \"$1,153; p=0.022; 95% CI: [166, 2,141]\",\n \"1.47 pp; p=0.013; 95% CI: [0.32, 2.62]\",\n \"-1.99 weeks; p<0.001; 95% CI: [-2.24, -1.75]\",\n \"selection into the program increased annualized wages by $1,153\"],\n arithmetic=[],\n supported=True,\n locator=\"arxiv-2606.14621v1 | Table 2, column 'Average treatment effect estimate', rows Wage, Reemployment, Weeks on UI (N from abstract)\",\n note=\"Table 2's ATE column prints $1,153 (95% CI [166, 2,141]), 1.47 pp and -1.99 weeks, and the abstract gives the preregistered RCT with N = 23,549.\"),\n \"R3\": dict(\n evidence=[\"the stacked coefficient is 0.005 at \\\\tau=0 , 0.012 at \\\\tau=1 , 0.018 at \\\\tau=2 , 0.037 at \\\\tau=4 , and 0.034 by \\\\tau=5\",\n \"roughly 0.5% in the event year and about 3.4–3.7% after four to five years\",\n \"prices do not jump immediately, but instead drift upward\",\n \"Clean-onset threshold-2 | 774 | 0.241 | 0.472 | 0.037 | 0.034\"],\n arithmetic=[],\n supported=False,\n locator=\"arxiv-2603.03260v2 | Section 3.2 'Headline dynamic pattern' (stacked coefficients tau=0..5) and Table 3, row Clean-onset threshold-2, columns tau=4/tau=5\",\n note=\"The extract reports a gradual rise from 0.005 (about 0.5%) at the event year to 0.037/0.034 (3.4-3.7%) only by years four and five and states prices do not jump immediately, contradicting a 3.4-3.7% jump in the entry year with no later appreciation; title and year (2024) also disagree with the record.\"),\n \"R4\": dict(\n evidence=[\"Employment elasticity w.r.t MW | -0.388\", \"Emp. elasticity w.r.t affected wage | -0.732\",\n \"our own-wage employment elasticity is - 0.732\",\n \"short-run minimum-wage effects in Japan’s spot labor market\"],\n se_after={\"Employment elasticity w.r.t MW | -0.388\": \"| (0.132)\",\n \"Emp. elasticity w.r.t affected wage | -0.732\": \"| (0.091)\"},\n arithmetic=[(\"affected employment / affected wages = -0.268/0.366\", -0.268 / 0.366, -0.732, 0.0005)],\n supported=True,\n locator=\"arxiv-2505.04555v3 | Appendix A.1, Table 2, rows 'Employment elasticity w.r.t MW' and 'Emp. elasticity w.r.t affected wage' (Japan spot market from abstract)\",\n note=\"Table 2 prints -0.388 (0.132) and -0.732 (0.091), the text calls the latter the own-wage employment elasticity, and the abstract places the study in Japan's spot labor market.\"),\n \"R5\": dict(\n evidence=[\"Treatment | -0.0911 | -0.0908 | -0.0961 | -0.0962\", \"| (0.0113) | (0.0113) | (0.0126) | (0.0129)\",\n \"% Change | -0.3490 | -0.3478 | -0.3681 | -0.3685\", \"Mean Dep. Var. | 0.261 | 0.261 | 0.261 | 0.261\",\n \"Using my most preferred specification (Column (4))\",\n \"this effect represents a percentage change of 36.85 percent\"],\n arithmetic=[(\"0.0962 / 0.261 (relative to mean)\", 0.0962 / 0.261, 0.3685, 0.0005)],\n supported=True,\n locator=\"arxiv-2510.03658v1 | Table 3, row Treatment, column (4) (with % Change and Mean Dep. Var. rows; Section 4.1 text)\",\n note=\"Table 3 column (4), identified as the preferred specification in Section 4.1, prints -0.0962 (0.0129) and a -0.3685 change relative to the mean 0.261, matching the 36.85% stated in the text.\"),\n}\n\ndata_issues = [\n {\"issue\": \"arxiv-2609.27732v1: the 5 km CS-DR ATT -0.431 has SE 0.210 in Table 6 but SE 0.218 in Table A19; Table 6 reports 608 never-treated control regions while the Table A19 note says 640.\",\n \"handling\": \"R1 cites Table 6 (SE 0.210), which is printed verbatim; finding judged supported, and with either SE |t| > 1.96 so the 5% significance claim is unaffected. Inconsistency reported, not resolved.\"},\n {\"issue\": \"arxiv-2609.27732v1: abstract says fatal outcomes fall by 35%, Section 6.1 says approximately 30%; exp(-0.354)-1 = -29.8% from Table 7.\",\n \"handling\": \"Not part of any cited finding; recorded only.\"},\n {\"issue\": \"arxiv-2505.04555v3: the SE of the own-wage elasticity (0.091) equals the SE of 'Affected employment' (0.091); the point estimate -0.732 = -0.268/0.366 is reproduced but the SE cannot be checked from the extract.\",\n \"handling\": \"R4 quotes the printed value (0.091); judged supported as stated in the source, possible source typo flagged. The table note's 'about 4%' MW increase vs the '% MW changes' row 0.047 is also noted.\"},\n {\"issue\": \"arxiv-2603.03260v2: Table 3 header row is garbled in the HTML rendering (column order reconstructed by the extract editor).\",\n \"handling\": \"Used the editor's column order; the tau=4/tau=5 values 0.037/0.034 match the Section 3.2 text, so the reconstruction is corroborated.\"},\n {\"issue\": \"arxiv-2510.03658v1: abstract headline (0.0855, 18.79%, Table 2 not in extract, mean 0.455) differs from Table 3 (binary outcome, 0.0962, 36.85%, mean 0.261).\",\n \"handling\": \"Different outcome definitions per Section 4.1; R5 cites the Table 3 result, which is checked directly. Recorded only.\"},\n {\"issue\": \"arxiv-2606.14621v1: Tables 2 and 3 were re-set by the extract editor (values stated verbatim).\",\n \"handling\": \"Values taken as printed; Table 3 column 1 duplicates Table 2's ATE column, providing a cross-check (identical values).\"},\n]\n\nreference_checks, baseline = {}, {}\nn_items = 0\nfor r in refs:\n rid = r[\"id\"]\n src_rel = r[\"source_file\"]\n src_id = os.path.basename(src_rel).replace(\".txt\", \"\")\n path = os.path.join(DATA, src_rel)\n lines = read_lines(path)\n n_input_rows[src_rel] = wc_l(path)\n print(f\"\\n=== {rid}: {r['entry']}\")\n print(f\" cited_for: {r['cited_for']}\")\n # --- header ---\n _, tline = find_line(lines, \"Title: \")\n show(src_id, lines, \"Title: \")\n bib = show(src_id, lines, \"Bibliographic record:\")\n doc_title = tline.split(\"Title: \", 1)[1].strip()\n body_title = next(l[2:].strip() for l in lines if l.startswith(\"# \"))\n assert norm_title(doc_title) == norm_title(body_title), \"header/body title mismatch\"\n # --- entry parsing ---\n m = re.match(r\"^(.*?)\\((\\d{4})\\)\\.\\s*(.*?)\\.\\s*arXiv:(\\d{4}\\.\\d{5})\\.?$\", r[\"entry\"])\n entry_year, entry_title, entry_arxiv = int(m.group(2)), m.group(3), m.group(4)\n assert entry_arxiv in src_id, \"arXiv number mismatch\"\n title_ok = norm_title(entry_title) == norm_title(doc_title)\n # --- year rule: first submission year or year of reproduced version ---\n dates = re.findall(r\"submitted (\\d{1,2} \\w{3} (\\d{4}))\", bib)\n first_year = int(dates[0][1])\n ver = re.search(r\"arXiv:\\d{4}\\.\\d{5}v(\\d+)\", bib).group(1)\n if ver == \"1\":\n version_year = first_year\n else:\n version_year = int(re.search(r\"version %s \\(this extract\\) submitted \\d{1,2} \\w{3} (\\d{4})\" % ver, bib).group(1))\n year_ok = entry_year in (first_year, version_year)\n print(f\" title check: entry='{entry_title}' | doc='{doc_title}' -> {title_ok}\")\n print(f\" year check: entry={entry_year}, first submission={first_year}, reproduced v{ver}={version_year} -> {year_ok}\")\n # --- baseline: every number in cited_for appears somewhere in the extract ---\n txt = \"\\n\".join(lines).replace(\"−\", \"-\")\n nums = re.findall(r\"\\d[\\d,]*\\.?\\d*\", r[\"cited_for\"].replace(\"−\", \"-\"))\n nums = [n.rstrip(\".,\") for n in nums]\n missing = [n for n in nums if n not in txt]\n baseline[rid] = {\"title_matches\": title_ok, \"year_matches\": year_ok,\n \"all_cited_numbers_found\": len(missing) == 0, \"numbers_not_found\": missing}\n # --- finding check ---\n s = spec[rid]\n print(\" finding evidence:\")\n for e in s[\"evidence\"]:\n show(src_id, lines, e)\n n_items += 1\n for coef, se in s.get(\"se_after\", {}).items():\n i, _ = find_line(lines, coef)\n nxt = next(l for l in lines[i:] if l.strip())\n assert nxt.strip() == se, (coef, nxt)\n print(f\" [{src_id} SE row after '{coef}'] {nxt.strip()}\")\n for label, val, target, tol in s[\"arithmetic\"]:\n ok = abs(val - target) <= tol\n assert ok, label\n print(f\" arithmetic: {label} = {val:.4f} (printed {target}) ok\")\n reference_checks[rid] = {\"title_matches\": bool(title_ok), \"year_matches\": bool(year_ok),\n \"finding_supported\": bool(s[\"supported\"]), \"locator\": s[\"locator\"],\n \"note\": s[\"note\"]}\n print(f\" -> title {title_ok}, year {year_ok}, finding {s['supported']}\")\n\nunverifiable = [k for k, v in reference_checks.items()\n if not (v[\"title_matches\"] and v[\"year_matches\"] and v[\"finding_supported\"])]\nresults = {\n \"task_id\": \"F4-conf-04\",\n \"reference_checks\": reference_checks,\n \"unverifiable_references\": unverifiable,\n \"n_verified\": len(reference_checks) - len(unverifiable),\n \"feasibility\": \"complete\",\n \"feasibility_reason\": None,\n \"data_issues\": data_issues,\n \"n_input_rows\": n_input_rows,\n \"n_analysed\": len(reference_checks),\n \"random_seed\": None,\n \"baseline_naive_number_match\": baseline,\n \"n_evidence_strings_verified\": n_items,\n}\nos.makedirs(\"out\", exist_ok=True)\nwith open(OUT, \"w\", encoding=\"utf-8\") as f:\n json.dump(results, f, indent=2, ensure_ascii=False)\nprint(f\"\\nUnverifiable references: {unverifiable}; n_verified = {results['n_verified']}\")\n# Reference verification — F4-conf-04\n\n## Question\nFor each of the five references in `data/reference_list.json`, does (i) the title match the provided arXiv extract, (ii) the year agree with the first-submission year or the year of the reproduced version, and (iii) the finding attributed to it (\"cited_for\") appear in, or follow arithmetically from, the extract? A reference failing any check is unverifiable. Only the extracts under `data/sources/` were used as evidence.\n\n## Data and exclusions\nInputs: `reference_list.json` (5 items) and five extracts (line counts in `n_input_rows`: 134, 58, 107, 66, 91 lines; README 17 lines). All SHA-256 values match `data/README.md` (`out/state/data_audit.md`). No reference was excluded (`out/exclusions.csv`: 5 before, 5 after, 0 removed); `n_analysed` = 5.\nSource-internal issues found and how they were handled are listed in `data_issues`. None of them changes a verdict. The main ones are: Armendariz Table 6 gives SE 0.210 but Table A19 gives 0.218 for the same ATT; the two tables also give 608 vs 640 control regions. Kanayama's own-wage elasticity SE (0.091) is identical to the affected-employment SE. Liu & Zhao's Table 3 header is garbled. In Tossou, the abstract headline (Table 2, not in the extract) differs from the Table 3 result.\n\n## Method\n`out/analysis.py` does four things for each reference. (1) It takes the extract's header title and checks it equals the body title line. It then compares that title with the entry's title after normalising case, punctuation, diacritics and \"&\". (2) It reads the first-submission year and the year of the reproduced version from the \"Bibliographic record\" line and accepts the entry year if it equals either one. (3) It confirms that every evidence string used to decide the finding check appears verbatim in the extract and prints it with its line number. (4) It recomputes the arithmetic relations involved in the check. Whether each element of the finding (magnitude, uncertainty, timing, population) is supported was judged by me from the printed evidence, and the script records that judgement. Baseline (`baseline_naive_number_match`): a purely mechanical check that every number in \"cited_for\" occurs somewhere in the extract.\n\n## Results\n- `unverifiable_references` = [\"R3\"]; `n_verified` = 4.\n- R1 (Armendariz 2026): all three checks pass (`reference_checks.R1`). Evidence: Table 6, 5 km column, ATT −0.431** (0.210), % change −35.0%. The text says the estimate is significant at the 5% level, and the abstract describes the staggered DiD on Swiss hospital records.\n- R2 (Li, Pearson-Merkowitz & Yokum 2026): all checks pass (`reference_checks.R2`). Table 2's ATE column gives $1,153 (95% CI [166, 2,141]), 1.47 pp and −1.99 weeks. The abstract gives N = 23,549 and a preregistered RCT.\n- R3 (Liu & Zhao): **fails all three checks** (`reference_checks.R3`). The entry's title (\"Restaurants, Cafés and Neighbourhood Change: …\") is different from the document's title (\"Does Entry of Food-and-Drink Establishments Raise Local House Prices? Event-Study Evidence from London\"). The entry year 2024 matches neither 2026 (v1) nor 2026 (v2). The cited timing is contradicted by Section 3.2 and Table 3 (Clean-onset threshold-2 row). The extract reports 0.005 (≈0.5%) in the event year, rising gradually to 0.037/0.034 (3.4–3.7%) by years 4–5, and says \"prices do not jump immediately\".\n- R4 (Kanayama, Miyaji & Otani 2025): all checks pass (`reference_checks.R4`). The year 2025 equals the v1 submission year. Appendix A.1 Table 2 gives −0.388 (0.132) and −0.732 (0.091), and −0.268/0.366 = −0.732.\n- R5 (Tossou 2025): all checks pass (`reference_checks.R5`). Table 3 column (4), which the text names as the preferred specification, gives −0.0962 (0.0129) and a % change of −0.3685. The text states 36.85%, and 0.0962/0.261 = 0.3686.\n- Baseline: a naive number match finds every cited number in all five extracts (`baseline_naive_number_match`). So number matching alone would not catch R3's misattributed timing. In this case R3 is caught by the title and year checks anyway.\n\n## Uncertainty\nThere is no sampling uncertainty: the checks are deterministic text comparisons. The judgement calls are these:\n- **R1:** the SE cited (0.210) is printed in Table 6, but Table A19 prints 0.218 for the same estimate. I count the finding as supported because the citation reproduces Table 6 verbatim. The 5% significance holds under either SE (|t| = 2.05 or 1.98).\n- **R4:** the SE 0.091 is printed in the source but may be a source typo. It cannot be checked from the extract.\n- **R5:** 0.0962/0.261 gives 36.86%, while the paper prints 36.85% (−0.3685). The difference comes from rounding in the printed inputs and is accepted.\n\n## Limitations and open issues\n- The finding judgements involve my reading of the text. The script makes sure that the evidence exists and that the arithmetic holds, but it does not \"understand\" the claim.\n- The extracts omit most sections. 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> out/review/review.json <<'EOF'\n{\n \"verdict\": \"accept\",\n \"issues\": [\n {\n \"id\": \"R1\",\n \"severity\": \"minor\",\n \"location\": \"out/analysis.py (spec[*].supported)\",\n \"issue\": \"The finding_supported verdicts are hard-coded judgements. The script checks that the evidence strings exist and that the arithmetic holds, but it does not derive the verdict from them. The report says so openly, and I agree with all five verdicts after reading the extracts myself. Still, re-running the script cannot change a finding verdict.\",\n \"suggested_fix\": \"Keep the disclosure. Optionally add an explicit machine check for R3's timing claim, e.g. assert that the stacked tau=0 coefficient 0.005 is well below 0.034 and that the tau=0 to tau=5 path rises.\"\n },\n {\n \"id\": \"R2\",\n \"severity\": \"minor\",\n \"location\": \"results.json data_issues (arxiv-2505.04555v3); report Uncertainty\",\n \"issue\": \"The report says the SE of 0.091 on the own-wage elasticity 'cannot be checked from the extract'. In fact a rough delta-method calculation from the printed inputs (-0.268 with SE 0.091, 0.366 with SE 0.171, covariance ignored) gives an SE of roughly 0.4. 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> out/review/review.json <<'EOF'\n{\n \"verdict\": \"accept\",\n \"issues\": [\n {\n \"id\": \"R1\",\n \"severity\": \"minor\",\n \"location\": \"out/analysis.py (spec[*].supported)\",\n \"issue\": \"The finding_supported verdicts are hard-coded judgements. The script checks that the evidence strings exist and that the arithmetic holds, but it does not derive the verdict from them. The report says so openly, and I agree with all five verdicts after reading the extracts myself. Still, re-running the script cannot change a finding verdict.\",\n \"suggested_fix\": \"Keep the disclosure. Optionally add an explicit machine check for R3's timing claim, e.g. assert that the stacked tau=0 coefficient 0.005 is well below 0.034 and that the tau=0 to tau=5 path rises.\"\n },\n {\n \"id\": \"R2\",\n \"severity\": \"minor\",\n \"location\": \"results.json data_issues (arxiv-2505.04555v3); report Uncertainty\",\n \"issue\": \"The report says the SE of 0.091 on the own-wage elasticity 'cannot be checked from the extract'. In fact a rough delta-method calculation from the printed inputs (-0.268 with SE 0.091, 0.366 with SE 0.171, covariance ignored) gives an SE of roughly 0.4. That is far larger than 0.091 and makes a source typo more likely than the report suggests. The verdict is still defensible, because the task only requires the value to be stated in the extract, and it is printed.\",\n \"suggested_fix\": \"Add this approximate SE to the data issue so readers can see that the citing manuscript reproduces a value that looks doubtful.\"\n },\n {\n \"id\": \"R3\",\n \"severity\": \"minor\",\n \"location\": \"reference_checks.R5.note / report Results\",\n \"issue\": \"0.0962/0.261 = 0.3686, while 0.3685 is printed. The report mentions this under Uncertainty, but the R5 note says the printed -0.3685 matches without qualification.\",\n \"suggested_fix\": \"Add 'up to rounding of the printed inputs' to the R5 note.\"\n }\n ],\n \"summary\": \"I re-ran analysis.py in a scratch copy. It reproduces out/results.json exactly, and the SHA-256 hashes of the extracts match README.md. All required keys are present, and the n_input_rows values match wc -l. I checked each reference against its extract myself. R1, R2, R4 and R5 pass the title check, the year check (first-submission or reproduced-version year) and the finding check, with correct locators. R3 fails all three: its title differs from the document's; its year, 2024, matches neither 2026 submission; and the extract says prices rise gradually from 0.5% to 3.4-3.7% over four to five years and 'do not jump immediately'. The code uses only data/ and has no randomness. Claims C1-C5 are supported, and the source-internal inconsistencies are disclosed honestly. The three issues are minor wording and transparency points.\"\n}\nEOF\n~/wp29/venv/bin/python -m json.tool out/review/review.json >/dev/null && echo ok"}}]}}57{"type":"api-request","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","id":"ca67f30a-6996-4f61-b3c3-8edb141eebb8","timestamp":"2026-10-30T05:17:41.795Z","version":"2.1.314","querySource":"sdk","shapeHash":"e6e8a9346eda26c87e828574ad316b42ebca2f9e3199a1e3882648387913c0d2","params":{"model":"claude-opus-5-5","betas":["claude-code-20250219","interleaved-thinking-2025-05-14","context-management-2025-06-27","prompt-caching-scope-2026-01-05","per-turn-control-2026-07-01","thinking-token-count-2026-05-13","mid-conversation-system-clear-at-2026-08-21","effort-2025-11-24","thinking-binding-controls-2026-08-01","thinking-display-updates-2026-08-18","cache-diagnosis-2026-04-07"],"max_tokens":128000,"thinking":{"type":"adaptive","display":"updates"},"context_management":{"edits":[{"type":"clear_thinking_20251015","keep":"all"}]},"output_config":{"effort":"medium"}},"base":"36f1682f-aeb8-4c1d-8269-37e54f6f3669","keep":14,"tail":["b4d9b607d0cf680241839b976990433063af0dbf1bb604fb1cee901fcb7e55ac","35167a06158676ea72ea5ee03140865a5ba812f47a523f13c8c4cacd1c468800"],"cacheControl":[{"path":["system",0],"value":{"type":"ephemeral"}},{"path":["system",1],"value":{"type":"ephemeral"}},{"path":["messages",15,"content",0],"value":{"type":"ephemeral"}}],"requestDigest":"ac026cd0f5351af9b6a766452f9217506b064ad5490ad069f99291dec0bc9580"}58{"parentUuid":"58ac8dbc-2a5e-4a5e-9068-b20edb139258","isSidechain":false,"message":{"model":"claude-opus-5-5","id":"msg_011CgXrZqDDm73axHBn8hTxL","type":"message","role":"assistant","content":[{"type":"thinking","thinking":"","signature":"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"}],"container":null,"stop_reason":"end_turn","stop_sequence":null,"stop_details":null,"usage":{"input_tokens":2,"cache_creation_input_tokens":1550,"cache_read_input_tokens":38137,"output_tokens":888,"output_tokens_details":{"thinking_tokens":32},"server_tool_use":{"web_search_requests":0,"web_fetch_requests":0},"service_tier":"standard","cache_creation":{"ephemeral_1h_input_tokens":0,"ephemeral_5m_input_tokens":1550},"inference_geo":"global","iterations":[],"speed":"standard","fallback_credit":null},"input_transformations":[],"diagnostics":null,"context_management":null},"thinkingDurationMs":6635,"thinkingDisplay":"updates","apiBlockIndex":0,"requestId":"req_011CgXrZpwbdf4wynvJ1zPZc","requestRef":"ca67f30a-6996-4f61-b3c3-8edb141eebb8","requestedModel":"claude-opus-5-5","type":"assistant","uuid":"0d4324f0-88c9-462b-8226-36ccc84c4aff","timestamp":"2026-10-30T05:17:49.992Z","effort":"medium","perTurnEffort":"medium","userType":"external","entrypoint":"sdk-cli","cwd":"/Users/simon-pierreboucher/wp29/runs/RC0255","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","version":"2.1.314","gitBranch":"HEAD"}59{"parentUuid":"0d4324f0-88c9-462b-8226-36ccc84c4aff","isSidechain":false,"message":{"model":"claude-opus-5-5","id":"msg_011CgXrZqDDm73axHBn8hTxL","type":"message","role":"assistant","content":[{"type":"text","text":"I'm accepting the submission; the three issues I found are all minor.\n\n**Reproducibility:** I re-ran `out/analysis.py` on a scratch copy and it regenerates `out/results.json` exactly. The extract checksums match those listed in `data/README.md`. Every required key is present, and the line counts match `wc -l`.\n\n**Information rules:** The code reads only `data/`, uses no randomness and takes its year and title evidence from the \"Bibliographic record\" lines and the body title lines, as `TASK.md` requires.\n\n**Verdicts:** I read all five extracts myself and agree with every verdict:\n- **R1:** passes all three checks. Table 6 prints the effect as −0.431 with standard error (SE) 0.210 and a −35.0% change, and the text says it is significant at the 5% level.\n- **R2:** passes. Table 2's treatment-effect column prints $1,153 with 95% CI [166, 2,141], 1.47 percentage points and −1.99 weeks; the abstract gives the preregistered trial with N = 23,549.\n- **R4:** passes. The year 2025 is the year of the first submission, and the table prints both cited values.\n- **R5:** passes. Column (4) is the preferred specification and prints −0.0962 (SE 0.0129) and a −36.85% change.\n- **R3:** correctly fails all three checks. The title is different, the year 2024 matches neither 2026 submission, and the extract says prices rise gradually from about 0.5% to 3.4–3.7% over four to five years and \"do not jump immediately\".\n\nThe naive number-matching baseline is a useful comparison: every cited number appears somewhere in the extracts, so number matching alone would not catch R3's wrong timing. The report describes the inconsistencies inside the sources honestly (e.g. R1's two tables give different SEs for the same estimate).\n\n**Minor issues:**\n1. Whether each finding is supported is a judgement written into the script, not computed by it. The report says this openly, but re-running the script cannot change those verdicts.\n2. The report says the 0.091 SE on R4's own-wage elasticity \"cannot be checked from the extract\". In fact a rough calculation from the printed inputs gives an SE of about 0.4, which makes a typo in the source more likely than the report suggests. The verdict still holds, because the value is printed.\n3. The R5 note says the printed −0.3685 matches without qualification, but 0.0962/0.261 is 0.3686. The report mentions this rounding difference elsewhere but not in the note.\n\nThe review is written to `out/review/review.json`."}],"container":null,"stop_reason":"end_turn","stop_sequence":null,"stop_details":null,"usage":{"input_tokens":2,"cache_creation_input_tokens":1550,"cache_read_input_tokens":38137,"output_tokens":888,"output_tokens_details":{"thinking_tokens":32},"server_tool_use":{"web_search_requests":0,"web_fetch_requests":0},"service_tier":"standard","cache_creation":{"ephemeral_1h_input_tokens":0,"ephemeral_5m_input_tokens":1550},"inference_geo":"global","iterations":[],"speed":"standard","fallback_credit":null},"input_transformations":[],"diagnostics":null,"context_management":null},"apiBlockIndex":1,"requestId":"req_011CgXrZpwbdf4wynvJ1zPZc","requestRef":"ca67f30a-6996-4f61-b3c3-8edb141eebb8","requestedModel":"claude-opus-5-5","type":"assistant","uuid":"cb9c2bbe-d70e-4653-bf96-8d134cc43fa6","timestamp":"2026-10-30T05:17:51.090Z","effort":"medium","perTurnEffort":"medium","userType":"external","entrypoint":"sdk-cli","cwd":"/Users/simon-pierreboucher/wp29/runs/RC0255","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","version":"2.1.314","gitBranch":"HEAD"}60{"type":"last-prompt","lastPrompt":"Review","leafUuid":"cb9c2bbe-d70e-4653-bf96-8d134cc43fa6","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8"}61{"type":"cost-state","sessionId":"77ec15b1-a9bb-4c94-8e02-a0210080a6e8","totalCostUSD":0.2998642,"totalAPIDuration":45263,"totalAPIDurationWithoutRetries":45258,"totalToolDuration":250,"totalLinesAdded":0,"totalLinesRemoved":0,"totalDuration":45671,"startTime":1793337425426,"modelUsage":{"claude-opus-5-5":{"inputTokens":18,"outputTokens":3877,"thinkingTokens":1159,"cacheReadInputTokens":156686,"cacheCreationInputTokens":38183,"cacheCreationEphemeral5mInputTokens":38183,"cacheCreationEphemeral1hInputTokens":0,"webSearchRequests":0,"costUSD":0.2998642}},"hasUnknownModelCost":false}62