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Late mortality comparisons after transcatheter and surgical aortic valve replacement can compare different survivor populations. We bounded these differences using matched low-risk trial estimates. Conditional on the balloon-expandable trial estimates representing potential-outcome marginals, a selection-only binary explanation is infeasible for years 1–7 but feasible for years 5–7. An allocation-to-initiation mixture model with aligned time origins and unrestricted omitted outcomes allows the modeled overall mortality difference to range from -4.77 to 5.27 percentage points. These are conditional identification calculations, not confidence intervals, estimated intention-to-treat effects, or evidence establishing clinical harm; sampling uncertainty, censoring and the interpretation of selected cohorts remain unresolved.
We asked whether survival selection before a landmark can, on its own, reproduce a later binary mortality contrast. This is an interpretation of published aggregate evidence, not a comparison of newly observed patient outcomes. Transcatheter aortic valve replacement (TAVR) and surgical aortic valve replacement (SAVR) are the two strategies.
We scoped randomized studies specifically designed for low surgical risk, using contemporary transcatheter platforms and reporting at least five years of comparative mortality. The primary applications were PARTNER 3 and Evolut Low Risk. Earlier-device NOTION, mixed-risk UK TAVI and intermediate-risk trials were contextual evidence, not pooled substitutes; the younger NOTION-2 population has shorter follow-up. The Europe PMC query and retrieved bibliographic records are supplied in . Targeted reading of primary reports, supplements, registry records and investigator presentations informed selection. This was not a comprehensive systematic review with independent duplicate screening.
data/For PARTNER 3, we used the single all-cause-death curve including vital-status sweeps in slide 14 of the public investigator presentation, read alongside Leon et al. (2025). It gives mortality at years 1, 5 and 7 as 1.0%, 10.4% and 19.5% after TAVR and 2.4%, 9.5% and 16.8% after surgery. Using this matched curve avoids substituting earlier publications' estimates from different database locks. The disposition diagram reports allocation to TAVR/SAVR as 503/497 and procedure initiation as 496/454. These selected-cohort risks are not automatically the intention-to-treat marginal risks.
For Evolut, Forrest et al. (2026) provides mature six-year follow-up and incomplete seven-year follow-up. We inspected original Supplemental Figure 8A and main Figure 1D, preserving the difference between mortality without and with a vital-status sweep. Exact late labels were allowed their rounding intervals. Because early risks were not numerically labeled on those curves, we used deliberately broad, visually checked ranges: at year 1, TAVR 0–3% and surgery 0–4%; at year 5 on the nonsweep curve, 12–15% and 14–17%, respectively. These are conservative input regions, not estimated sampling intervals. Source locations, ascertainment, denominators and access limitations appear in data/mortality_inputs.json and the source audit.
Principal stratification defines a population by potential survival under both strategies, as in Frangakis and Rubin (2002). Survivor-effect bounds under varying identifying assumptions are established by Zhang and Rubin (2003). Binary bounds and linear programming are also established methods; Shan et al. (2015) studies such bounds under monotonicity, whereas we allow both early benefit and early harm in the primary calculation.
Let be death risks through landmark and death risks through later time , with TAVR indexed 1 and surgery 0. Each potential outcome has three ordered states: death by , survival through followed by death by , or survival through . Let be their joint probability table, with TAVR states in rows and surgery states in columns, indexed 0, 1 and 2. Its margins are and .
The always-survivor mass and late-death contrast are
The contrast compares binary death by among people who would survive under either strategy. It differs from the observed comparison of actual survivors and from a late hazard ratio. Changing changes the potential-survivor population, so the resulting contrasts are not repeated estimates of the same target.
Interpreting observed arm risks as these potential-outcome marginals requires consistency, exchangeability and appropriate handling of censoring. A selected as-treated cohort need not inherit randomization's exchangeability. Our calculation is explicitly conditional on the supplied marginals; it does not establish those assumptions in the actual trial populations.
We minimized and maximized Eq. (1) over every nonnegative joint table with the specified margins. The transformation , makes the problem linear: the always-survivor cells of sum to one and row/column sums equal the supplied margins multiplied by . SciPy's HiGHS solver returns endpoints and attaining tables. A separate calculation optimizes over the common-early-death mass using stratum capacities; it does not call the matrix solver. code/derivation.md supplies the derivation and conditions for a closed form.
A selection-only binary null imposes : every always-survivor has the same binary death-by- outcome under both strategies. This does not require equal exact death times. It is feasible exactly when a zero average binary contrast is feasible, because equal off-diagonal masses can be transferred to the two diagonal cells without changing margins. We also minimized the population fraction whose survival through differs across strategies. That additional optimization was exploratory, added after preliminary bounds were computed.
We then explored the stronger restriction , so every always-survivor remains alive through . All observed late deaths can then be placed in people who would have died before under the opposite strategy. This is possible when and . Within this restricted class, the maximum common-early-death mass is ; the derivation gives an attaining table. Late death times outside the always-survivors can follow any compatible marginal pattern, while always-survivors have identical survival through the entire interval. This is a feasibility construction, not a reconstruction of individual event times or a statement of plausibility. Its minimum discordance is not the minimum required for all possible equal-trajectory constructions.
The primary landmark/horizon was years 1–7; we also evaluated years 1–5 and 5–7 wherever matched inputs were available, and the available Evolut six-year comparisons. PARTNER rounding regions allow each displayed risk to vary by 0.05 percentage points in either direction. Optimization over the entire input region, rather than only a point estimate, supplies deterministic envelopes. A monotone-early-benefit calculation is an additional assumption-based sensitivity, not the primary model.
We calibrated the effect of shifting the surgery late risk while holding the other risks fixed. Separately, a diagram-based omission model treated the procedure-initiated cohorts as selected fractions of their allocated groups and allowed every omitted participant any of the three nested states. Unlike C1's common-population interpretation of selected arm risks, this model does not require selected subgroups to be exchangeable across arms: it mixes each selected distribution with unrestricted outcomes within its allocated arm. It still treats selected survival estimates and cohort proportions as fixed valid risks and weights.
The mixture model assumes aligned time origins. The source curves are indexed by procedure, and we did not reconstruct randomization-to-procedure waiting times or index dates for people without the assigned procedure. Consequently, these are common-horizon sensitivity bounds, not an actual intention-to-treat reanalysis, and they do not establish that omitted outcomes or other intention-to-treat analyses were unavailable to investigators. We bounded both overall allocated-population mortality and the always-survivor contrast. An exploratory calibration minimized mortality in the omitted surgery subgroup needed to permit a binary survivor null; among tied solutions, the witness minimizes omitted TAVR mortality. The overall-mortality-null threshold is a distinct calculation. We did not convert Kaplan–Meier percentages multiplied by baseline denominators into observed event counts.
We also displayed the already-derived fixed-common-death bounds as a sensitivity frontier, and added an exploratory nonnegative-association assumption for early potential mortality: . This is an untestable cross-world assumption, not a measured association. It was imposed separately on the binary null and the stronger all-always-survivors-alive class.
We checked feasibility, marginal sums and the objective of every returned witness, compared matrix and independent capacity formulations on synthetic configurations with seed 281106, and checked interval-region optimization against singleton inputs and a closed-form vertex calculation. No hypothesis test, meta-analysis or clinical-effect confidence interval was calculated. Published mortality uncertainty is described separately. The data-informed plan was committed before numerical implementation, after reading trial rates and considering their algebraic implications; it was not outcome-blinded. The exploratory optimizations, association sensitivity and graph-range choices are disclosed in deviations.json.
Table 1 shows conditional identified sets for different survivor populations. The earlier-landmark comparison excludes a binary null at the supplied point risks; the later-landmark comparison includes it. Allowing rounding leaves that distinction unchanged. These intervals express uncertainty about the joint potential-outcome distribution at fixed marginal risks; they do not express sampling uncertainty.
Table 1. Conditional PARTNER late-death risk-difference bounds, TAVR minus surgery.
| Landmark / horizon (years) | Point-input lower (percentage points) | Point-input upper (percentage points) | Rounding-envelope lower (percentage points) | Rounding-envelope upper (percentage points) |
|---|---|---|---|---|
| 1 / 5 | -0.1 | 3.42 | -0.26 | 3.58 |
| 1 / 7 | 1.76 | 5.28 | 1.6 | 5.44 |
| 5 / 7 | -9.11 | 11.36 | -9.24 | 11.49 |
For the later landmark, a population can match the supplied margins while every always-survivor has identical binary late outcomes under the procedures. The minimum fraction with treatment-dependent landmark survival is 4.5%. Figure 2 displays an attaining table, not estimated patient strata. A binary null is infeasible for the earlier-landmark point inputs. This does not mean the observed later contrast was actually caused by selection.
For the stronger construction, the minimum discordance within its class is 19.1%, decreasing to 18.9% over the rounding region. Every always-survivor remains alive through the late horizon. Thus any compatible within-window death-time pattern can be assigned to the other strata without a survival difference among always-survivors. Figure 2 compares this deliberately extreme construction with the minimum-discordance binary null. Neither is an estimate of the actual counterfactual population.
The Evolut nonsweep later-horizon region gives bounds 0.72 to 8.49 percentage points with the earlier landmark, versus -14.01 to 22.18 with the later landmark. The mature nonsweep earlier-horizon region gives -0.97 to 6.77; its sweep counterpart gives 0 to 7.74. These are envelopes over specified graph-read regions, not point estimates or confidence limits. All input scenarios are listed in the full table.
In the aligned-horizon PARTNER omission model, both targets admit benefit and harm (Table 2). A zero binary survivor-contrast witness is retained. Figure 3 varies the omitted surgery fraction within the model.
Table 2. Allocated-population sensitivity bounds with selected risks fixed and omitted outcomes unrestricted.
| Target | Lower (percentage points) | Upper (percentage points) |
|---|---|---|
| Overall mortality by the late horizon | -4.77 | 5.27 |
| Late death among people who would survive the early landmark under both strategies | -6.63 | 8.6 |
At these fixed selected-cohort risks, a binary survivor null requires at least 33.47% mortality by the late horizon in the modeled omitted surgery subgroup, allowing the most favorable omitted TAVR outcomes for that null. An attaining witness leaves the omitted TAVR subgroup alive through the horizon. The corresponding threshold for a zero overall mortality difference is 44.87%, which is a different target. These are model tipping points, not estimates of what happened to omitted participants; sampling uncertainty can change the thresholds.
A separate calibrated increase of 1.7 percentage points in the surgery late risk allows the lower selected-cohort survivor bound to reach zero; this is not an estimate of censoring bias or missing deaths.
The later-landmark binary null ceases to be feasible when assumed common early mortality exceeds 7.7% of the modeled population, equivalent to 81.05% of its surgery early deaths. The stronger all-always-survivors-alive class requires common mortality no greater than 0.4%, below the product-of-marginals benchmark 0.988%. Under the additional nonnegative-association assumption, the binary null remains feasible but the stronger class does not. These are assumption thresholds, not estimated overlap frequencies.
The independent capacity and matrix optimizations agreed over 1006 validation configurations; the maximum absolute discrepancy was 1.2212453270876722e-15 in risk-proportion units. Every endpoint has a feasible attaining table. Validation supports the calculation, not the clinical identification assumptions.
The results distinguish two claims that are often blurred: a later mortality pattern can be observed, while its interpretation in a common survivor population remains underidentified. At the supplied PARTNER earlier-landmark risks, all feasible couplings have a positive average late binary contrast among always-survivors. At the later landmark, a coupling with no individual binary late contrast is feasible. This is not a biological reversal established by the analysis: the landmarks define different latent populations.
The constructed later-landmark binary null allows both people helped and people harmed before that landmark. It does not assert that surgery's perioperative mortality alone explains everything or that TAVR has no overall mortality effect. The stronger all-always-survivors-alive construction demonstrates that the supplied margins alone also allow equal survival indicators throughout the late interval, but it requires a substantially different latent population. The discordance minima are thresholds for feasibility within their specified classes, not measured frequencies or probabilities that selection explains the data. Requiring monotone early survival or a particular dependence between potential outcomes would add substantive assumptions that should not be silently inferred from an observed average early advantage.
Existing syntheses address different questions. Marin-Cuartas et al. (2026) pooled low- and intermediate-risk trials at a common follow-up, reporting a mortality risk ratio of 1.12 with a 95% credible interval of 1.02–1.22 overall, but 1.05 (0.88–1.26) within the low-risk stratum. Our work neither re-estimates that pooled effect nor treats a nonsignificant risk-stratum interaction as proof of equal effects. Leon et al. (2025) and Forrest et al. (2026) appropriately report no statistically significant difference for their principal long-term composite outcomes; the computations here address a separate fixed-horizon binary survivor contrast. We do not claim new principal-stratification theory or the first assessment of late mortality.
For interpretation of valve trials, an observed late hazard, an overall randomized mortality contrast, and a survivor-average binary effect answer different questions. Their denominators, follow-up ascertainment, selection assumptions and clinical time horizons should be stated explicitly. An intention-to-treat analysis with complete outcome ascertainment and access to joint sampling information would address important limitations of this aggregate exercise. Individual-level covariates or credible structural assumptions may tighten survivor-effect bounds, but their justification requires additional evidence.
The main quantities are conditional mathematical calculations. The published arm curves do not establish the required potential-outcome marginals in a selected common population. Postrandomization exclusions, crossover, informative censoring and treatment selection remain possible. The omission model assumes aligned time origins, although the source curves use time from procedure and index dates for omitted participants were not reconstructed. It deliberately withholds outcomes outside the selected cohorts; it does not establish that those outcomes were uncollected or that all available trial information would give the same broad bounds. The reported model tipping points condition on noisy selected-cohort point estimates and are not the mortality rates an actual clinical null would require after accounting for statistical uncertainty.
These identification sets are not confidence intervals. The PARTNER investigator presentation reports an overall mortality hazard ratio of 1.17 (95% confidence interval 0.86–1.59), and the Evolut nonsweep seven-year curve reports a mortality risk difference of 3.7 percentage points (95% confidence interval −2.4 to 9.9). Neither establishes mortality superiority. We did not obtain joint sampling information for the early and late risks and did not manufacture a confidence interval for their derived bounds. Positive bounds at displayed risks therefore do not establish positive clinical effects at a stated confidence level.
The PARTNER presentation was publicly accessible, while the complete primary journal supplement was not; the journal abstract confirms its late mortality endpoints, but the matched early inputs came from the inspected presentation. Evolut graphical ranges are intentionally broad, and seven-year follow-up is incomplete. Sweep and nonsweep results were kept separate. Rounding and graph-reading envelopes do not cover selection or ascertainment bias.
The primary estimand concerns death status at a fixed horizon. The additional trajectory construction is deliberately extreme; its feasibility does not establish plausibility or identify the actual survivor stratum. In particular, a nonnegative-association assumption for the potential early-death indicators rules out that stronger class at the supplied point risks, although it leaves the binary null feasible. Neither result identifies an actual effect on the timing or cause of death, progressive valve dysfunction, stroke, reintervention, or lifetime durability. There is no younger-patient subgroup estimate. The low-risk trial populations and devices do not represent every patient undergoing contemporary valve replacement. The evidence search was a scoping exercise, and the application is not a comprehensive comparative-effectiveness systematic review. The registered plan was data-informed, and both the minimum-discordance optimization and stronger trajectory/association analyses were exploratory.
The GPT family, using gpt-6, performed source selection, the derivation, code, numerical validation, interpretation and writing. The work uses factual public aggregate trial reports and an investigator presentation. It generates counterfactual probability tables and scientific figures; none are individual patient records or newly observed clinical outcomes. Established principal-stratification concepts are attributed to the methodological literature. Copyrighted source documents were inspected for extraction and are not redistributed. The bundle contains original prose and code, aggregate inputs with source locations, a data-informed committed plan and generated outputs. No independent prepublication review has yet been completed.