Literature reviews and decisions log (rounds 1-5) for the early-PVI TTE simulation

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

docs/decisions.md

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+# Decisions log
+
+Each decision is listed with the date and the reason for it. Settled decisions are changed only by adding a new entry below them, never by editing them.
+
+## Round 1: framing (2026-10-27)
+
+| # | Decision | Why |
+|---|---|---|
+| 1 | **Paper type: a "teaching" paper combined with a "threats" paper.** The backbone is that landmark, CCW and sequential trials answer three different clinical questions. The experimental factors are the threats specific to surgery. We do not claim that "TTE works". | Earlier simulations already show that the methods work. The new contribution is the surgical setting, plus showing what each estimand means in it. |
+| 2 | **Primary outcome: MALE composite. Secondary outcomes: each component on its own.** | Matches the VESS 2026 abstract and practice in vascular surgery. The components show how outcomes that physicians generate (reintervention) behave differently from outcomes that come from disease (CLTI, amputation). The exact definition of MALE is still open (round 2). |
+| 3 | **Include a simulated RCT arm in the same DGP** (ITT and naive per-protocol, with crossover, surgeon selection and small n). | Turns "why RCTs are hard in surgery" into numbers. |
+| 4 | **Experimental factors:** (1) surgeon skill, (2) surgeon preference or style, (3) style acting on the outcome directly, (4) deferral and crossover driven by symptom progression, (5) unmeasured symptom severity. **Built in through the RCT arm:** (6) trial selection of high-skill surgeons. **Fixed feature of the DGP:** (7) treatment effect that changes over time. **Supplement / sensitivity analysis:** (8) unmeasured co-intervention (uptake of supervised exercise). | Keeps the main grid readable. |
+| 5 | **Audience: surgeons. Target journal: JAMA Surgery.** Each method in the main text has a one-sentence clinical definition. The mathematics goes in the supplement. | The user is a surgical health-services researcher. Readers are clinicians. |
+| 6 | **The RCT limitations are covered as narrative in the introduction plus one evidence table** (claudication RCTs: n, endpoint, crossover, recruitment shortfall). There is no separate systematic review. | Scope. |
+
+## Round 2: the target trial (2026-10-27)
+
+| # | Decision | Why |
+|---|---|---|
+| 7 | **MALE = CLTI, major amputation, open bypass, or any revascularization after the first.** The index PVI does not count as an event in either arm, whenever it happens. Total procedures per patient is a secondary outcome. **Supplement:** the Sorber "late PVI" definition (any PVI after month 6), to show how the outcome definition alone changes the answer. | Avoids an outcome that is asymmetric between arms by construction. Not counting the index procedure is defined the same way in both arms. |
+| 8 | **Death is a competing event.** The primary measure is the 5-year cumulative incidence of MALE, reported as a risk difference. HR, and MALE-free survival (MALE or death), go in the supplement. | Medicare population with a mean age of about 76. Censoring at death would answer an unrealistic hypothetical question. |
+| 9 | **Time zero is the new claudication diagnosis. Strategy A is PVI within 6 months.** A 3-month window is a supplement-only sensitivity analysis. | Matches Sorber 2023, VESS 2026, Dun 2025, and the guidelines. |
+| 10 | **Strategy B, primary: no PVI in the first 6 months, then usual care.** **Strategy B, second (main text): no elective PVI unless a MALE-qualifying event occurs.** | Deferral vs abstention: "conservative" is not a single strategy (the ADAM/CAESAR lesson). |
+| 11 | **Each method gets two errors: estimation bias (estimate vs its own estimand) and question gap (its own estimand vs the clinically relevant estimand). Total error is the sum of the two.** The clinically relevant reference is A vs B(primary) in all new claudicants under full adherence, which is the CCW estimand. | The teaching paper needs to separate "the method fails" from "the method answers another question". |
+| 12 | **R, with a new self-contained package in this repo.** It follows the `tte-papers` conventions (YAML parameters, truths from simulating the interventions in large samples, Quarto, renv) but does not reuse its code. | The DGP differs (months, not hours; physicians as clusters). |
+
+## Round 3: comparators and the simulated world (2026-10-27)
+
+| # | Decision | Why |
+|---|---|---|
+| 13 | **Landmark:** month 6, among patients alive and MALE-free. Exposure is PVI in months 0–6. Outcome is MALE by month 60 *since diagnosis*. Adjust for baseline covariates plus measured covariates at month 6. | Same horizon as CCW. Mirrors the Sorber 2023 design, so the paper can say what that design estimated. |
+| 14 | **Sequential trials:** monthly trials in months 0–5 among patients still eligible. **ITT is primary**; per-protocol (weighted) goes in the supplement. | Sequential ITT estimates "now vs maybe later" (deferral), in contrast to CCW's "within 6 months vs not". |
+| 15 | **Physician-level variants, crossed with every method:** (1) ignore, (2) cluster-robust SE, (3) physician random intercept, (4) within-physician (FE or Mundlak). **Supplement:** (5) physician-preference IV. | Clustering fixes SEs, not bias. A random intercept does not remove confounding. FE can, but it risks Z-bias. The IV analysis is dubious when the surgeon also decides on reintervention. |
+| 16 | **Monthly discrete time over 60 months. Pooled logistic hazard models.** | Standard for CCW and sequential trials, and simple. |
+| 17 | **Measured:** age, sex, race, diabetes, CKD/dialysis, CHF, COPD, prior CVD, coded smoking, physician ID, practice setting (OBL/ASC vs hospital), calendar year, and a time-varying **proxy for symptom progression** (repeat vascular visits / noninvasive arterial testing). **Latent:** true symptom severity, ABI, true smoking, patient preference, surgeon skill, surgeon style. **Proxy strength is the dial for factor 5.** | What is "measured" means what is in Medicare claims. |
+| 18 | **Two simulated RCTs:** a *realistic* one (n ≈ 240, hospital-based, top-third skill, low-preference surgeons) and an *ideal pragmatic* one (all physicians, large n). Crossover is **generated by the DGP** in both. Each is analysed by ITT and naive per-protocol. | Separates bias from surgeon selection and small n from bias due to crossover. |
+| 19 | **Calibrate usual care to Medicare figures:** early PVI ≈ 3.2%; the physician distribution from Hicks 2020 (median 0%, range 0–58%, about 5.6% outliers); Sorber's crude late PVI and CLTI rates; age-appropriate mortality. **Truth scenarios:** null; harm (e.g. RD +5 points at 5 years); early benefit then late harm. | The null scenario shows pure bias. Calibration keeps the simulated world credible to surgeons. |
+
+## Round 4: DGP core (2026-10-27)
+
+| # | Decision | Why |
+|---|---|---|
+| 20 | **Mechanistic latent-severity engine.** Each patient has a latent severity that drifts with a patient-specific rate. Severity drives the CLTI hazard and the PVI decision. PVI lowers severity right away but adds a restenosis/progression hazard that depends on skill. | Benefit followed by harm, crossover in the conservative arm, and confounding by indication all come out of one mechanism. Truths are computed by simulating the interventions, so the extra complexity costs nothing there. |
+| 21 | **Estimand: PVI done by the patient's own physician, averaged over the real physician mix.** The gap between the realistic RCT (top-third skill) and the population effect is reported as a finding (external validity), not as bias. | Skill modifies the effect of PVI. |
+| 22 | **Skill and style are separate latent traits. Base correlation −0.3; comparison level 0.** | Sorber's outliers had more late PVI and CLTI. |
+| 23 | **Factor 3 = high users have a lower threshold for repeat revascularization AND code CLTI more intensively.** The two are switched on together. | These are paths outside the treatment decision. Style acting through deferred PVI after month 6 is part of strategy B, not bias. |
+| 24 | **Main analysis: one factor at a time from a clean base world, plus one "realistic, all threats on" world, in each of the 3 truth scenarios. Supplement: full factorial**, only if the one-at-a-time results suggest interactions. | Readability: one panel per threat. |
+| 25 | **Each replicate has 50,000 patients and about 1,500 physicians, with lognormal panel sizes (median about 20). Supplement: 200,000 patients.** Number of replicates is set later, with ADEMP. | About 1,600 early-PVI patients per replicate, enough for CCW and FE positivity. |
+
+## Round 5: analysis structure (2026-10-27)
+
+| # | Decision | Why |
+|---|---|---|
+| 26 | **All observational methods use the same adjustment.** IP weights come from pooled logistic models on the measured covariates. Weighted cause-specific hazards for MALE and death are then combined into a standardized 5-year cumulative incidence. Landmark uses IPW at month 6. Sequential trials use IPW at each trial baseline. CCW uses artificial-censoring weights. The RCTs are analysed unadjusted (ITT) and as-treated (naive per-protocol). No matching and no doubly robust variants. | Differences between methods then reflect design and estimand only. Paper 1 already covered the choice of adjustment method. |
+| 27 | **Performance measures:** estimation bias (against the method's own estimand), question gap, total error, empirical SE, model SE, coverage of the method's own estimand, RMSE, and MCSE for each. **The headline measure for clinicians is the false-alarm rate under the null** (CI excludes 0). | Separates two problems: whether the method fails, and whether it answers a different question. |
+| 28 | **Variance:** cluster-robust sandwich SE plus the delta method in every replicate. A physician-cluster bootstrap (200 resamples) is run on about 100 replicates in the base and realistic worlds. | A full bootstrap at scale costs too much. Same approach as Paper 1. |
+| 29 | **Replicates:** 100 at draft, 500 at final. MCSE is reported. | MCSE for coverage is about 1% at 500 replicates. |
+| 30 | **Figure 1, the "estimand ladder":** one row per method. Each row shows a hollow dot for the method's own truth, a filled dot with interval for its estimate, and a line for the clinically relevant truth. Panels are worlds; colour is the physician variant. Shown for the null and harm scenarios. **Figure 2:** false-alarm rate by threat and physician variant. | One picture that shows both the question gap and the estimation bias. |
+| 31 | **Next:** the analysis plan (md plus docx), then the table of claudication RCTs, then the build. The docs are committed on the branch `analysis-plan`. | |

docs/literature/01-surgical-rct-limitations.md

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+# Literature review 1: limitations of RCTs in surgery, mapped to TTE on claims data
+
+All citations were checked against PubMed through NCBI E-utilities, 2026-10-27. The numbers come from PubMed abstracts; full texts were not read. Papers with no PubMed abstract are described only in general terms.
+
+**Corrections and caveats**
+- Chapman 2014 was published in *BMJ*, not *Surgery*.
+- The page numbers for McCulloch 2002 are from memory, not from PubMed.
+- BASIL-3 recruited 481 of the planned 861 patients. That the paclitaxel signal caused the shortfall is a guess, not a verified finding.
+
+---
+
+## 1. Classic critiques and the IDEAL framework
+
+| Paper | PMID | Takeaway |
+|---|---|---|
+| McCulloch P et al. 2002, *BMJ* "Randomised trials in surgery: problems and possible solutions" | 12065273 | The founding critique. Barriers: equipoise, learning curve, quality control, blinding, surgeon preference. |
+| McLeod RS 1996, *Surgery* 119:483 | 8619200 | Problems specific to RCTs in surgery. |
+| Solomon MJ, McLeod RS 1995, *Surgery* | 7652679 | Many surgical questions could be randomized but are not. |
+| Solomon MJ, McLeod RS 1998, *Med J Aust* | 9803252 | Overview of RCTs in surgery: past, present and future. |
+| Barkun JS et al. 2009, *Lancet* 374:1089 | 19782874 | IDEAL series, paper 1: the stages of surgical innovation. |
+| Ergina PL et al. 2009, *Lancet* 374:1097 | 19782875 | Few of the challenges are unique to surgery, but in surgery they occur together: complexity, surgeon factors, and the range of outcomes. |
+| McCulloch P et al. 2009, *Lancet* 374:1105 | 19782876 | IDEAL recommendations: registries and prospective databases, with RCTs "whenever possible". |
+| McCulloch 2013 / Ergina 2013 / Cook 2013, *BMJ* (IDEAL series) | 23778427, 23778426, 23778425 | Observational studies in the Exploration and Assessment stages; RCTs and long-term registry evaluation. |
+| Hirst A et al. 2019, *Ann Surg* | 29697448 | IDEAL update: adds a Pre-IDEAL stage and covers devices. |
+| Cook JA 2009, *Trials* 10:9 | 19200379 | Checklist for the design, conduct and analysis of surgical RCTs. |
+| Pronk AJM et al. 2023, *Br J Surg* 110:1300 | 37379487 | Of 1,188 surgical RCTs, only **22.1%** published in 2019 were at low risk of bias (14.7% in 2009). |
+| Ahmed Ali U et al. 2018, *J Surg Res* 228:1 | 29907196 | Of 228 negative surgical RCTs, the median sample size was about 76–80, so most were underpowered. |
+
+## 2. Recruitment failure, discontinuation, and equipoise
+
+| Paper | PMID | Takeaway |
+|---|---|---|
+| **Chapman SJ et al. 2014, *BMJ* 349:g6870** | 25491195 | Of 395 surgical RCTs, **21% stopped early**. The main reason was poor recruitment (44% of stopped trials). Of completed trials, 34% were unpublished at a median of 4.9 years. |
+| **Rosenthal R et al. 2015, *Ann Surg* 262:68** | 24979608 | Discontinued: **43%** of surgical vs **27%** of medical RCTs. Stopped for slow recruitment: 18% vs 11%. Discontinuation predicted non-publication (OR 4.18). |
+| Kasenda B et al. 2014, *JAMA* 311:1045 | 24618966 | Across all fields, **24.9%** of RCTs were discontinued, most often for poor recruitment. |
+| Cook JA et al. 2008, *Contemp Clin Trials* 29:631 | 18397843 | **Trials of surgery vs medical treatment recruited about 2× slower** than trials of surgery vs surgery (median 68 vs 35 days per recruit). This applies directly to PVI vs exercise. |
+| Donovan J et al. 2002, *BMJ* 325:766 (ProtecT) | 12364308 | Qualitative work on how recruiters presented the options made an "impossible" trial feasible. |
+| Donovan JL et al. 2014, *J Clin Epidemiol* 67:912 | 24811157 | Clinicians' "hunches" undermined equipoise, and **surgeons felt this most intensely**. |
+| Rooshenas L et al. 2016, *PLoS Med* 13:e1002147 | 27755555 | In recorded consultations, the equipoise clinicians stated differed from how they actually presented the options. |
+| Donovan JL et al. 2022, *Trials* 23:258 (QRI-Two) | 35379301 | A rapid recruitment intervention for trials that are failing to recruit. |
+| Hamdy FC et al. 2023, *NEJM* 388:1547 (ProtecT at 15 years) | 36912538 | A monitor-vs-intervene trial can be completed. |
+
+## 3. Surgeon skill, learning curve, expertise-based trials, and clustering
+
+| Paper | PMID | Takeaway |
+|---|---|---|
+| **Devereaux PJ et al. 2005, *BMJ* 330:88** | 15637373 | Proposes expertise-based RCTs: each surgeon performs only the procedure they are expert in, to avoid differential-expertise bias. |
+| Cook JA et al. 2015, *Trials* 16:241 | 26025450 | Review of 43 expertise-based RCTs: 92% compliance, but expertise criteria were poorly reported. |
+| Cook JA et al. 2004, *Clin Trials* 1:421 | 16279280 | Statistical methods for learning curves in surgical trials. |
+| Ramsay CR et al. 2000 / 2001 | 11155830, 11319991 | Assessing learning curves in health technology. |
+| **Lee KJ, Thompson SG 2005, *BMJ* 330:142**; *Clin Trials* 2:163 | 15649931, 16279138 | Outcomes cluster by clinician even under individual randomization. Ignoring it makes the estimates look more precise than they are. |
+| Roberts C, Roberts SA 2005, *Clin Trials* 2:152 | 16279137 | Clustering induced by treatment, which can differ between arms (partially nested designs). |
+| Walters SJ 2010, *J Clin Nurs* 19:1102 | 20492055 | Therapist effects: cluster-level, random-effects, and marginal models compared. |
+| **Birkmeyer JD et al. 2013, *NEJM* 369:1434** | 24106936 | Peer ratings of surgical skill from video: the bottom quartile vs the top had **14.5% vs 5.2%** complications and **0.26% vs 0.05%** mortality. |
+| Birkmeyer JD et al. 2003, *NEJM* 349:2117 | 14645640 | Surgeon volume and mortality. |
+
+## 4. Blinding and sham surgery
+
+| Paper | PMID | Takeaway |
+|---|---|---|
+| **Wartolowska K et al. 2014, *BMJ* 348:g3253** | 24850821 | Across 53 placebo-controlled surgical RCTs, the placebo arm improved in 74%. Surgery was **no better than placebo in 51%**. |
+| Wartolowska K et al. 2016, *BMJ Open* | 27008687 | Placebo-controlled surgical trials are feasible but recruit slowly. |
+| Boutron I et al. 2017, *Ann Intern Med* 167:40 | 28630973 | CONSORT extension for non-pharmacologic treatments: expertise, blinding, and standardization. |
+
+## 5. Standardization, crossover, and contamination
+
+| Paper | PMID | Takeaway |
+|---|---|---|
+| **Garas G et al. 2018, *Ann Surg Oncol* 25:221** | 29110271 | Across 40 RCTs of minimally invasive vs open surgery, crossover averaged **12.6% (0–45%)** and worsened the ITT results. |
+| **Weinstein JN et al. 2006, *JAMA* 296:2441 (SPORT)** | 17119140 | **Only 50%** of the surgery arm had surgery, and **30%** of the nonoperative arm did, so the ITT comparison could not be interpreted. |
+| Hernán MA, Robins JM 2017, *NEJM* 377:1391 | 28976864 | Per-protocol effects in pragmatic trials. |
+
+## 6. Generalizability and external validity
+
+| Paper | PMID | Takeaway |
+|---|---|---|
+| **Rothwell PM 2005, *Lancet* 365:82** | 15639683 | "To whom do the results of this trial apply?" |
+| Rothwell PM 2006, *PLoS Clin Trials* | 16871331 | Factors that affect external validity. |
+| Cutteridge J et al. 2025, *BJS Open* | 40105904 | Patients in 307 vascular RCTs were **younger** than those in the UK National Vascular Registry. |
+| Jones HG et al. 2026, *EJVES* | 42526742 | Endovascular lower-limb revascularization is under-researched relative to how often it is done. Its trials are 72% efficacy trials and 39% industry-funded. |
+| Loudon K et al. 2015, *BMJ* (PRECIS-2) | 25956159 | Tool for rating how pragmatic or explanatory a trial is. |
+
+## 7. Trials of timing, "when to operate" (the key analogue)
+
+| Paper | PMID | Takeaway |
+|---|---|---|
+| **Fitzgibbons RJ et al. 2006, *JAMA* 295:285** | 16418463 | Hernia watchful waiting: 23% of the waiting arm crossed over to surgery, and 17% of the surgery arm crossed the other way. |
+| **Fitzgibbons RJ et al. 2013, *Ann Surg* 258:508** | 24022443 | Long-term crossover was **68%** (79% in men over 65). "Watchful waiting" works out as "delayed surgery". |
+| O'Dwyer PJ et al. 2006, *Ann Surg* | 16858177 | UK hernia trial: crossover was higher than predicted. |
+| **UK Small Aneurysm Trial 1998, *Lancet*** | 9853436 | HR 0.94. Operative mortality of 5.8% caused an early deficit in survival. |
+| **Lederle FA et al. 2002, *NEJM* (ADAM)** | 12000813 | **61.6% of the surveillance arm were eventually repaired.** Surveillance is a dynamic strategy, not "no treatment". |
+| Cao P et al. 2011, *EJVES* (CAESAR) | 20869890 | Delayed repair under surveillance: 59.7% by 36 months and 84.5% by 54 months. One in six aneurysms became unsuitable for EVAR, a harm of delay that the ITT effect on mortality does not capture. |
+| Ouriel K et al. 2010, *JVS* (PIVOTAL) | 20304589 | 31% of the surveillance arm were repaired by 20 months. HR 1.01. |
+| Ulug P et al. 2020, *Cochrane* | 32609382 | Early repair of small AAAs has no advantage. |
+
+## 8. Pragmatic trials, registry trials, and TTE
+
+| Paper | PMID | Takeaway |
+|---|---|---|
+| **Hernán MA, Robins JM 2016, *AJE* 183:758** | 26994063 | The foundational TTE paper. |
+| **Hernán MA et al. 2016, *J Clin Epidemiol* 79:70** | 27237061 | Specifying the target trial avoids self-inflicted biases such as immortal time. |
+| Hernán MA et al. 2022, *JAMA* 328:2446 | 36508210 | JAMA Guide to TTE. |
+| Cain LE et al. 2010, *Int J Biostat* | 21972433 | "When to start treatment?": dynamic regimes. |
+| **Maringe C et al. 2020, *Int J Epidemiol* 49:1719** | 32386426 | CCW tutorial on surgery in older patients with lung cancer. The naive 22% benefit fell to 11%. |
+| Wang SV et al. 2023, *JAMA* 329:1376 (RCT-DUPLICATE) | 37097356 | Of 32 RCTs emulated in claims data, agreement was r = 0.93 when the emulation was close and r = 0.53 when it was not. All were drug trials. |
+| Cashin AG et al. 2025, *JAMA* / *BMJ* (TARGET) | 40899949 / 40903028 | Reporting guideline for TTE. |
+| Scola G et al. 2023, *BMC Med Res Methodol* | 37587484 | Only 16% of TTEs used cloning to handle immortal time. |
+| Katsoulis M et al. 2024, *Epidemiology* 35:730 | 39024012 | TTE of bariatric surgery. |
+| Hoskins W et al. 2026, *JBJS Rev* | 42896011 | Orthopaedic primer. TTE **does not** address unmeasured confounding. |
+| Lauer MS, D'Agostino RB 2013, *NEJM* | 23991657 | The randomized registry trial. |
+| Zwarenstein M et al. 2008, *BMJ* | 19001484 | CONSORT extension for pragmatic trials. |
+| Brookhart MA et al. 2006, *Epidemiology* 17:268 | 16617275 | Physician preference as an instrumental variable. |
+
+**Gap:** we found no surgery-specific systematic review of TTE methods (JAMA Surg / Ann Surg, 2022–2026). Applied examples: Sakowitz 2025, *Ann Surg* (TCAR vs CEA), PMID 40607703; Talathi 2026, *Surgery* (STRASS 2 emulated), PMID 41936769.
+
+## 9. Vascular surgery
+
+| Paper | PMID | Takeaway |
+|---|---|---|
+| Farber A et al. 2022, *NEJM* (BEST-CLI) | 36342173 | Cohort 1: MALE or death 42.6% with surgery vs 57.4% with endovascular (HR 0.68). Whether a vein conduit was available decided which cohort a patient entered. |
+| Bradbury AW et al. 2023, *Lancet* (BASIL-2) | 37116524 | n = 345. Vein bypass first was worse (aHR 1.35), which conflicts with BEST-CLI. |
+| Hunt 2017 *Trials*; Bradbury 2025 *BMJ* (BASIL-3) | 28526046, 39993822 | **481 of 861 planned** randomized. No benefit from drug-coated balloons or drug-eluting stents. |
+| **Katsanos K et al. 2018, *JAHA*** | 30561254 | Paclitaxel: 5-year mortality 14.7% vs 8.1% (RR 1.93). Only 3 RCTs had 5-year data. |
+| Rocha-Singh KJ et al. 2020, *Circulation* | 32370548 | Individual patient data: **23–24% lost to follow-up or withdrew**. After recovering vital status, HR 1.38 → 1.27. |
+| Secemsky EA et al. 2019, *JAMA Cardiol* | 30747949 | Medicare: no excess mortality. |
+| Freisinger E et al. 2020, *Eur Heart J* | 31593987 | German claims data: no excess mortality. |
+| Nordanstig J et al. 2020, *NEJM* (SWEDEPAD, interim) | 33296560 | Registry RCT: HR 1.06. |
+| **Nordanstig J et al. 2025, *Lancet* (SWEDEPAD 2, claudication)** | 40902614 | No benefit in quality of life. 5-year mortality HR 1.47 (1.09–1.98). |
+| Falkenberg M et al. 2025, *Lancet* (SWEDEPAD 1, CLTI) | 40902617 | The CLTI companion trial. |
+| Fakhry F et al. 2015, *JAMA* (ERASE) | 26547465 | Revascularization plus exercise beat exercise alone at 12 months. |
+| Murphy TP et al. 2012, *Circulation* (CLEVER) | 22090168 | Exercise was better for walking time and stenting for quality of life. n = 111. |
+| Nordanstig 2014, *Circulation*; Djerf 2020, *Circ CV Interv* (IRONIC) | 25095886, 31937137 | The quality-of-life benefit seen at 1 year was **lost by 5 years**, at about twice the cost. |
+| **Sorber R et al. 2023, *JVS*** | 37276171 | Medicare. Early PVI 3.2%. Late PVI 22.5% vs 3.6% (aHR 6.89). High-use physicians. |
+| Dun C et al. 2025, *Ann Vasc Surg* 110:424 | 39419322 | Market competition predicts early PVI. |
+| Weaver ML et al. 2023, *JVS* | 37141948 | Market competition and claudication management in the VQI. |
+| Madabhushi V et al. 2021, *JVS* | 33775749 | Revascularizing claudicants: CLTI HR 2.9, amputation HR 4.5. |
+| Conte MS et al. 2025, *JVS* (SVS focused update) | 40316185 | Major evidence gaps for claudication. |
+
+---
+
+## Taxonomy: RCT limitations in surgery → what TTE on claims can do
+
+IV = internal validity, EV = external validity, F = feasibility.
+
+| # | Limitation | Threatens | Can TTE on claims fix it? | Can it go in the simulation DGP? |
+|---|---|---|---|---|
+| 1 | Recruitment failure and discontinuation | F (and EV) | **Yes.** No consent is needed. The price is confounding instead of randomization. | Indirectly: compare a "would-consent" subset with the whole population. |
+| 2 | Patient and surgeon equipoise and preference | F, EV, IV | **Partly.** Preference is what makes treatment vary in practice, and can serve as an IV (high-use physicians). Patient preference is unmeasured. | **Yes.** A latent physician "intervention propensity". |
+| 3 | Surgeon skill and learning curve | IV, EV | **Partly.** Skill is not in claims, but the operator NPI is, so random or fixed effects are possible. Skill and preference cannot be separated if they are correlated. | **Yes.** Latent skill, correlated with preference. |
+| 4 | Clustering and provider heterogeneity | IV (precision), EV | **Mostly.** Mixed models, cluster-robust SEs. | **Yes.** Random intercepts and random slopes by physician. |
+| 5 | Blinding and sham | IV | **No.** No patient-reported outcomes in claims, and outcome ascertainment is not blinded. | Optional: differential ascertainment of CLTI. |
+| 6 | Standardization and co-interventions | IV, EV | **Partly.** Procedure type and Part D fills are visible. Exercise, smoking, and adherence are not. | **Yes.** Unmeasured exercise uptake. |
+| 7 | Crossover and deferral | IV | **Yes, TTE's strongest case**, using dynamic strategies with CCW or sequential trials. It needs the triggers for crossover to be measured. | **Yes, central.** |
+| 8 | Immortal time and misaligned time zero | IV | **Yes, by design.** | **Yes.** The naive design as a comparator. |
+| 9 | Selected surgeons, centers, and patients | EV | **Yes, largely.** Population-based data, plus transportability. | **Yes.** A "trial of high-skill operators" vs the whole population. |
+| 10 | Long horizon, rare outcomes, changing technology | F, IV | **Partly.** Follow-up is long and complete, but device codes are coarse and calendar time confounds. | **Yes.** Time-varying effect (early benefit, late harm). |
+
+**In one line:** TTE fixes feasibility, generalizability, and (with dynamic strategies) crossover. It cannot fix unmeasured confounding by indication or the lack of patient-reported outcomes. Surgeon skill sits in between: it cannot be measured, but its structure can be modelled through the NPI.
+
+## Read first
+1. Sorber 2023 *JVS* (37276171)
+2. ADAM 2002 *NEJM* (12000813) and CAESAR 2011 (20869890)
+3. Fitzgibbons 2006 *JAMA* and 2013 *Ann Surg* (16418463, 24022443)
+4. Hernán & Robins 2016 *AJE*; Hernán 2016 *J Clin Epidemiol* (26994063, 27237061)
+5. Maringe 2020 *Int J Epidemiol* (32386426)
+6. McCulloch 2002 *BMJ*; Ergina 2009 *Lancet* (12065273, 19782875)
+7. Chapman 2014 *BMJ*; Rosenthal 2015 *Ann Surg* (25491195, 24979608)
+8. Katsanos 2018; Nordanstig 2020 and 2025 (30561254, 33296560, 40902614)

docs/literature/02-claudication-evidence-and-methods.md

@@ -0,0 +1,208 @@
+# Literature review 2: claudication evidence, and what landmark, CCW and sequential trials each estimate
+
+PMIDs were checked through NCBI E-utilities on 2026-10-27. The numbers come from PubMed abstracts. The guideline recommendation wording is from memory and needs checking against the full texts.
+
+---
+
+## Part A. Clinical evidence
+
+### A1. Randomized trials. Every one used walking distance or QoL as the endpoint; none used hard limb outcomes.
+
+| Trial | N and comparison | Result | Limitations |
+|---|---|---|---|
+| **CLEVER**: Murphy 2012 *Circulation* (22090168); 18-month results 2015 *JACC* (25766947); design (18440181); update (19660897) | 111 aortoiliac; OMC vs OMC+SE vs OMC+stent | Peak walking time at 6 months: SE better than stent (p=0.04). At 18 months: no difference (p=0.16). QoL better with stent. | **Under-recruited**: planned 252 in 4 arms, cut to 217 in 3 arms, finished with 111. Only 79 had 18-month data. |
+| **ERASE**: Fakhry 2015 *JAMA* (26547465); long-term Klaphake 2022 *Ann Surg* (33378308) | 212; endovascular + SET vs SET | MWD at 12 months +282 m with the combination | At 5.4 years the walking gap had closed (p=0.62). The SET arm had more later revascularizations (HR 2.50) but **fewer procedures in total (65 vs 149)**. |
+| **IRONIC**: Nordanstig 2014 *Circulation* (25095886); 5-year Djerf 2020 *Circ CV Interv* (31937137) | 158; revascularization + BMT + exercise vs BMT + exercise | SF-36 better with revascularization at 1 year | **No difference at 5 years.** Cost about 2× higher. |
+| **MIMIC**: Greenhalgh 2008 *EJVES* (19022184) | 93 femoropopliteal + 34 aortoiliac; PTA on top of SE + BMT | Walking distance +38% / +78% | Very small. No QoL benefit. |
+| **SUPER**: Koelemay 2022 *EJVES* (35151572) | 240 iliac; SET vs endovascular | MWD the same at 1 year | **Stopped early. 29% of the SET arm crossed over to revascularization within 1 year.** Only 50% complied with SET. |
+| **Mazari**: 2012 *BJS* (22021102); 2017 *BJS* (27763685) | 178; PTA vs SEP vs both | The same at 12 months and 5.2 years | |
+| **Spronk**: 2009 *Radiology* (19188327) | 151; endovascular vs SET | An early advantage for endovascular was gone by 6–12 months | |
+| **OBACT**: Nylaende 2007 *EJVES* (17055756) | 56; OMT vs OMT + PTA | PTA better at 2 years | **434 screened to randomize 56.** |
+| **Cochrane**: Fakhry 2018 (29518253) | 10 RCTs, 1,087 patients | Endovascular vs SET: no clear difference | Small, short trials, and **no hard limb outcomes**. |
+
+**Across these trials:**
+- Revascularization improves walking and QoL early, but the advantage fades by 2–5 years.
+- Crossover and non-adherence to SET are large.
+- No trial was powered for CLTI, amputation or cumulative reintervention.
+
+### A2. Observational evidence that intervention is associated with progression
+
+- **Madabhushi 2021 *JVS* (33775749).** n = 1,051. Revascularization was associated with CLTI (HR 2.9) and amputation (HR 4.5). The exposure is "ever revascularized", so the result is exposed to immortal time bias.
+- **Golledge 2018 *BJS* (29566427).** n = 456. Treatment depended on *which specialist the patient saw*, which is a natural physician-preference contrast. 5-year amputation was 6.2% with early revascularization vs 0.7% with conservative care.
+- **Sorber 2023 *JVS* (37276171).** aHR 6.89 for late PVI. Patients of outlier physicians had more late PVI and more CLTI.
+- **Dun 2025 *Surgery* (40782724).** Markov decision model.
+- **Alabi 2026 *JAMA Surg* (41405976).** VQI–Medicare, 10,012 patients. CLTI within 180 days of revascularization ranged up to 11.8% across subgroups.
+- **Bose 2025 *Ann Surg* (38841837) and *EJVES* (38906366).** Infrapopliteal PVI for claudication had poor outcomes.
+- **Natural history:**
+  - Sigvant 2016 *EJVES* (26777541): about 21% progress to CLI.
+  - Baubeta Fridh 2017 *EJVES* (28797662): amputation after revascularization for IC is 0.4% per year.
+- **Review:** Golledge 2022 *Nat Rev Cardiol* (34997200).
+
+### A3. Variation between physicians
+
+- **Hicks 2020 *JVS* (31208940), "Overuse of early PVI for claudication."** n = 194,974 patients, 3.2% with early PVI. The median physician's rate was 0%, with a range of 0–58%. **320 physicians (5.6%) were ≥2 SD outliers.** Office-based lab (OBL) or ambulatory surgery center (ASC) practice predicted outlier status. **This paper is the main empirical source for the physician component of the DGP.**
+- Dun 2024 *JAHA* (38958132): the OBL/ASC share of PVI went from 12.4% to 55.7% between 2011 and 2022.
+- Dun 2025 *Ann Vasc Surg* (39419322): market competition.
+- Weaver 2023 *JVS* (37141948).
+- Tsou 2024 *JVS* (38908807).
+- Smith 2019 *Ann Vasc Surg* (30684609).
+- Brown 2021 *JVS* (33617980).
+- Iannuzzi 2025 *JVS* (39824263).
+
+### A4. Guidelines
+
+- SVS 2015 (25638515; introduction 25721065)
+- ESVS 2024 (37949800)
+- ESC 2024 (39210722)
+- ACC/AHA 2024 (38743805; *JACC* 38752899). Advises against revascularizing only to prevent progression to CLTI.
+
+### A5. Why there is no RCT of early PVI vs initial conservative therapy on hard outcomes
+
+1. **Event rates are low, so the trial would have to be large and long.** These are rough two-proportion calculations with 80% power, ≥5-year follow-up and no crossover:
+   - Amputation 2% vs 1% at 5 years: about 2,300 per arm.
+   - CLTI 8% vs 5%: about 1,050 per arm.
+2. **Crossover is built into the comparator.** The conservative arm includes deferred PVI, so an ITT analysis dilutes the contrast. Examples: SUPER had 29% crossover in year 1; ERASE's SET arm had a revascularization HR of 2.5; CLEVER finished with 111 of 252 planned; OBACT randomized 56 of 434 screened.
+3. **Equipoise is asymmetric.** The guidelines already recommend against early PVI, and the high-use physicians who do most early PVI would not enroll their patients.
+4. **The hard endpoints are generated by physicians.** Reintervention and the coding of CLTI are decisions made by unblinded clinicians, and patients who get early PVI are watched more closely.
+5. **No sponsor and a lot of heterogeneity.** No device company will fund a "fewer devices" hypothesis. Anatomy and devices vary, and Medicare has covered SET only since 2017.
+
+---
+
+## Part B. Methods: which question each one answers
+
+### B1. Immortal time bias
+
+**Plain version:** if "early PVI" means "had PVI at month 4", that patient had to survive event-free to month 4 to be labelled early PVI. The fix is to line up eligibility, assignment and time zero.
+
+- Suissa 2008 *AJE* (18056625)
+- Lévesque 2010 *BMJ* (20228141)
+- Hernán 2016 *J Clin Epidemiol* (27237061)
+- Hernán 2025 *Epidemiology* (39494894). Reframes the problem: immortal time is a symptom of misclassification or selection.
+
+### B2. Landmark analysis
+
+**Estimand:** among patients alive and CLTI-free at 6 months, those who happened to have PVI in months 0–6 vs those who did not.
+
+- It is conditional and descriptive.
+- The comparator mixes patients who never have PVI with patients who have it at month 7.
+- Events in months 0–6 are dropped.
+- It conditions on a post-treatment variable.
+- **Sorber 2023 is effectively a 6-month landmark design.**
+
+References:
+- Anderson, Cain, Gelber 1983 *JCO* (6668489); revisited 2008 (18711176)
+- Dafni 2011 *Circ CV Qual Outcomes* (21586725)
+- van Houwelingen 2008 (18836831)
+- Putter & van Houwelingen 2017 (29225713)
+
+### B3. Clone–censor–weight (CCW)
+
+**Estimand:** the risk if *everyone* followed strategy A, "PVI within 6 months of diagnosis", vs strategy B, "no PVI in the first 6 months, then usual care (or PVI only for CLTI)". This is a per-protocol effect of sustained strategies starting at diagnosis.
+
+- The 6-month grace period means an event inside the window, before any PVI, counts in both arms.
+- **The answer depends on how strategy B is written.**
+- Natural and stochastic grace-period strategies are different estimands (Wanis 2024).
+
+References:
+- Hernán 2018 *BMJ* (29419381)
+- Cain 2010 *Int J Biostat* (21972433)
+- **Maringe 2020 *IJE* (32386426)**; correspondence 33349843, 33524137
+- Gaber 2024 *Cancer Med* (39642890)
+- **Wanis 2024 *JRSS-A* (39281783)**, on grace periods
+- Hernán & Robins 2017 *NEJM* (28976864)
+- Cole & Hernán 2008 *AJE* (18682488)
+
+### B4. Sequential trial emulation
+
+**Estimand:** among patients still eligible *this month* (no PVI yet, no CLTI, alive), PVI now vs not now.
+
+- "Not now" includes PVI next month, so it is a *deferral* effect, not an *abstention* effect.
+- The pooled population leans toward slowly progressing patients, because they stay eligible for more trials.
+
+References:
+- Hernán 2008 *Epidemiology* (18854702)
+- Danaei 2013 *SMMR* (22016461)
+- Gran 2010 *Stat Med* (20803557)
+- **Keogh 2023 *Stat Med* (37086186)**
+- Limozin/Seaman 2025 *SMMR* (40631395): CIs
+- Robins 2000 *Epidemiology* (10955408): MSMs
+- The TrialEmulation R package is on CRAN and has no PubMed citation.
+
+### B5. Studies comparing methods
+
+- **Duchesneau 2022 *CEBP* (35984990).** Surgery in metastatic breast cancer. Compares landmark with CCW against a plasmode known truth. This is **the closest template.**
+- Mi 2016 *Stat Med* (27350312). Landmark is unbiased under the null but biased when there is an effect.
+- Karim 2016 *AJE* (27455963)
+- Zhou 2005 *AJE* (16192344)
+- Pilleron 2023 *BJC* (36759725). Immortal time bias is larger in older patients.
+- Hoffman 2022 *JAMA Netw Open* (36190729)
+- Moreno-Betancur 2026 *Epidemiology* (41490058). "The Ideal Trial": the estimand you want vs the estimand your data allow.
+
+**Gap:** we found no simulation that compares landmark, CCW and sequential trials side by side as answers to *different* estimands.
+
+### B6. Physician clustering and unmeasured confounding at the surgeon level
+
+There are two separate problems.
+
+**1. Inference.** Clustered SEs or random effects fix only the standard errors.
+- Panageas 2003 *Ann Intern Med* (14568854); 2007 *Stat Med* (17016864)
+- Kahan & Morris 2013 *Stat Med* (23112128)
+
+**2. Confounding by physician.** Physician style affects both early PVI and the outcome. Here the outcome (late PVI, coding of CLTI) is *itself* a physician decision.
+- **Within-physician comparisons** (fixed effects, Mundlak, matching within surgeon) remove time-invariant confounding between physicians:
+  - Neuhaus & Kalbfleisch 1998 (9629647)
+  - Begg & Parides 2003 (12898546)
+  - **Li Y 2020 *SMMR* (31694489)**: closed-form bias results
+  - **Cafri 2020 *Biom J* (32419247)**: matching within surgeon on device data
+  - Li/Zaslavsky/Landrum 2013 (23526267)
+  - Thoemmes & West 2011 (26735885)
+  - Arpino & Cannas 2016 (26833893)
+  - Fuentes 2022 (34128730)
+  - Austin 2017 (27885709): median HR
+- **Caveats:**
+  - A random effect does **not** remove confounding when it is correlated with PVI use.
+  - Frailty HRs are conditional on physician and non-collapsible.
+  - Fixed effects need physicians who sometimes do and sometimes do not intervene early (positivity).
+- **Preference as an instrumental variable:**
+  - Brookhart 2006 (16617275); Brookhart & Schneeweiss 2007 (19655038)
+  - Rassen 2009 (19345561)
+  - Brookhart 2010 (20354968)
+  - Ertefaie 2017 (28239929)
+  - Hutchings 2022 (35588540)
+  - The exclusion restriction is doubtful when the same physician also decides on reintervention.
+- **Bias amplification (Z-bias):** Myers 2011 *AJE* (22025356); Pearl 2011 *AJE* (22034488).
+  - If physician preference is purely instrument-like, conditioning on the physician *amplifies* remaining unmeasured patient confounding.
+  - The simulation can show where the crossover lies.
+
+**Gap:** we found no paper on unmeasured surgeon-level confounding *inside* CCW or sequential trial emulation. The nearest are Cafri 2020 and Li 2020.
+
+### B7. Simulation methods
+
+Morris, White, Crowther 2019 *Stat Med* (30652356), the ADEMP framework. **Score each method against its own true estimand.**
+
+### B8. Reporting
+
+TARGET 2025: *BMJ* 40903028, *JAMA* 40899949; explanation and elaboration in *PLoS Med* 41091811.
+
+---
+
+## Summary table (early PVI ≤6 months)
+
+| Method | Estimand | Requires | Failure mode |
+|---|---|---|---|
+| Naive "ever early PVI" | None that is well defined | — | Immortal time and confounding by indication |
+| Landmark at 6 months | Among patients event-free at 6 months: had PVI in months 0–6 vs not | Confounders measured up to the landmark | Drops early harms. Mixed comparator. Selects on survival after treatment. |
+| CCW with 6-month grace | Everyone follows A vs everyone follows B | Time-varying predictors of PVI timing; positivity; a precise definition of strategy B | Unmeasured symptom progression or physician style. Extreme weights. Sensitive to how B is defined. |
+| Sequential trials (ITT) | PVI now vs not now, among patients eligible this month | Eligibility each month; covariates at each baseline | A deferral effect, not abstention. Leans toward slow progressors. |
+| Physician-clustered models | Clustered SEs: honest SEs. FE: within-physician effect. Frailty: conditional HR | FE needs within-physician variation | RE does not remove confounding. FE can show Z-bias. Conditional vs marginal mismatch. |
+
+## Read first
+
+1. Hernán 2018 *BMJ*, CCW (29419381)
+2. Hernán 2008 *Epidemiology*, sequential trials (18854702)
+3. Keogh 2023 *Stat Med* (37086186)
+4. Maringe 2020 *IJE* (32386426)
+5. Duchesneau 2022 *CEBP* (35984990)
+6. Morris 2019 *Stat Med*, ADEMP (30652356)
+7. Cafri 2020 *Biom J* (32419247)
+8. Myers 2011 *AJE* (22025356)