Device–vessel mismatch is one quantity on four axes.

How this page works

Device–vessel failure is treated here as a property of the agreement between device and vessel rather than of either alone, and the same operator is applied in six arterial beds with only the bed's own parameters changed. Four axes, each mapped to [0, 1]:

• Γ_G geometric — sizing against the bed's band, edge coverage, conformability, taper.
• Γ_M mechanical — device/wall compliance mismatch, overstretch wall stress, cyclic fatigue.
• Γ_H hemodynamic — flow lumen restored, strut flow disturbance, side branches, runoff.
• Γ_B biological — antiproliferative supply against neointimal drive, healing window.

They combine as a weighted geometric mean, Γ_sc = Π Γ_i^w_i, with bed-specific weights. The geometric mean is the modelling commitment: a device fails along its worst-matched axis, and a product cannot be rescued by a high score elsewhere the way a sum can. Everything is a function of time, so two scalars come off the trajectory — τ_sc, the time by which Γ_sc(t) has accumulated 63.2% of its total variation, and the time-averaged mismatch dose — and the hazard link is λ(t) = λ₀ · exp(β·(Γ*−Γ_sc(t))), anchored per bed at the match level that bed's own reference device achieves.

Calibration, and the audit behind it

Eleven of the thirteen free constants were fitted against 12 audited 12-month event rates across six beds, by least squares on log-odds weighted by audited evidence quality — one shared parameter set, no per-bed tuning. Mean absolute error 1.4 percentage points.

The first version of this anchor set was audited adversarially: every value was independently hunted, then attacked by two further checkers, one asking only whether the citation exists and says this, the other only whether the endpoint, timepoint and population match. Three of sixteen survived, and two of those three were the two arms of one trial. Thirteen were too high by factors of 1.0 to 5.8, and five were recoverable exactly from a different endpoint in the correctly cited paper — a patency loss read as a revascularisation rate, a confidence bound read as a point estimate, a composite safety endpoint read as restenosis. Within one trial, target lesion failure and clinically driven TLR differ two- to threefold, so an endpoint stated as "either" fixes nothing.

What changed: one preferred construct (12-month clinically driven TLR), seven declared provenance fields per anchor, four anchors excluded but kept visible, trust weights reset to audited evidence quality rather than author confidence, and all six bed baseline rates revised downward.

What this cannot claim

• Nothing here has seen a patient. 12 anchors against eleven free constants is calibration, not validation: it shows the operator can reproduce the published spread with one parameter set, not that it is right.
• The calibration rests on six informative comparisons, and half the headline error is an identity. Six of the twelve anchors are their own bed's reference case and reproduce its baseline rate by construction; on the six genuinely informative anchors the error is 2.3 percentage points, not 1.4. Carotid, iliac and renal contribute one anchor each, which is also that bed's baseline rate, so those beds are fitted trivially. Four anchors are two arms each of two trials that share sites, adjudication committee and endpoint trigger, so they are not four independent residuals.
• Three revascularisation constructs remain mixed in the retained set. Symptom-driven TLR without routine angiography biases low; surveillance-triggered TLR biases high. They are labelled and weighted, not unified.
• The pan-vascular transfer claim is not supported — it is refuted. In simulation, once the comparison is against a linear model given the same continuous bed physiology, the operator's cross-bed advantage in discrimination is -0.024 AUC (95% bootstrap -0.041 to -0.010), an interval that excludes zero. What survives is sample efficiency: the four physics-derived numbers sit at AUC 0.790 from n = 100 procedures, a level 44 raw features have not reached by n = 800. For a single-centre cohort, where the number of procedures is the binding constraint, that is the whole argument for the operator.
• Across beds the operator transfers an ordering, not a risk scale — and an offset does not fix it. Its raw cross-bed Brier score is 0.249 against 0.135 for simply predicting the base rate. Shifting the intercept alone still leaves it worse than the base rate (0.151); what repairs it is refitting the slope as well, and the slope it needs is 0.26 — the operator's log-odds are about four times too steep across beds. A new bed therefore needs a two-parameter recalibration on real events, not a constant anyone can look up.
• Device entries are representative class parameters, not specific commercial specifications, and several — radial force, device compliance, fatigue resistance — are order-of-magnitude estimates. Bed parameters are declared priors, not measurements.
• Four of the fitted constants sit on their bounds, which says the drug and strut terms need reformulating rather than refitting.

Next

The operator is built to be refitted on real cohorts by maximum likelihood, and reported against a logistic model on the same raw features as a floor. If the refitted operator does not beat that floor out of sample, that is the finding.