D54: paper framing - can TTE overcome the problems of surgical RCTs

Co-Authored-By: Claude Opus 5.5 <[email protected]>

docs/decisions.md

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 | 52 | **Draft run done:** 8 worlds × 3 scenarios × 100 replicates of 50,000 patients; 9.4 h on 11 cores; 0 errors. 16 of 288,000 estimates are NA (sequential trials, V4, 4 replicates) and are dropped. Summary: `simulations/04_summarise.R` writes `results/summary/`. Report: `reports/draft-report.Rmd`. Two open questions: (Q1) the landmark propensity model adjusts for month-5 severity, a post-PVI mediator, which drives the landmark question gap (W1 own truth about 20 pp vs a reference of 7.2 pp); with baseline covariates only, the 20-replicate oracle mean is 8.1. (Q2) NCO-1 has no severity term in the DGP, contrary to D32, so it cannot detect W5/WR bias. The bootstrap check (D28) waits on Q1/Q2. | Surfaced by the draft results. |
 | 53 | **Answers to D52 (user, 2026-10-28).** (Q1) **The primary landmark propensity score uses baseline covariates only** (diagnosis covariates and month-0 severity). The version that also adjusts for month-5 severity becomes `landmark_m5` (supplement). It conditions on a mediator, because a PVI in months 0–5 has already changed that severity. Both versions get their own oracle. (Q2) **NCO-1 now depends on severity (coefficient 0.3)**, using the patient's **PVI-free severity path** (the same baseline, rate and monthly noise, with no relief and no kappa). That way NCO-1 shares the confounder but still cannot be affected by PVI (only through death as a competing risk, D46). Intercept −6.75 keeps 5-year NCO-1 incidence at about 9.3%. This is the best case for a patient-level negative control, and the paper says so. **Bootstrap (D28, reduced):** W0 and WR × null and harm, replicates 1–20 of the main run, 50 physician-cluster resamples each, V1 point estimates, about 8 s per resample. Compare the bootstrap SD with the model SE (patient and cluster) and the empirical SE. **The rerun goes to `results/main/n50k_v2`;** the first draft stays in `n50k`. Truths are recomputed (NCO-1 changed). | Landmark analyses in practice adjust for baseline covariates. D32 intended NCO-1 to share severity. |
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+## Paper framing (2026-10-28)
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+| # | Decision | Why |
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+| 54 | **The paper's question: "Can target trial emulation overcome the problems that make randomized trials hard in surgery?"** Early PVI for claudication is the worked example. Medicare only supplies realistic simulation inputs, and the paper makes no claims about Medicare findings or the authors' earlier papers. The structure is a scorecard: each surgical-RCT barrier (small/stopped early, short follow-up/soft endpoints, crossover, selected surgeons, practice style, unmeasured severity) against whether TTE solves it, checked against the known truth. Aims 1–3 stay. Aim 1 = "TTE is not one method", Aim 2 = the scorecard rows, Aim 3 = whether the one unfixable problem can be detected. The MALE/repeat-revascularization point is secondary, general outcome-definition guidance. The Medicare "dial" idea is dropped. **Novelty (quick PubMed check, 2026-10-28):** there are TTE guides for surgeons (e.g. JBJS Rev 2026) and immortal-time design comparisons (Duchesneau 2022 *CEBP*), but no search hit for a known-truth simulation comparing TTE with a feasible surgical RCT under surgeon-level threats. | User: the aim is to test whether TTE can solve RCT challenges in surgery, without arguing against the authors' earlier results. |