Radiology used to have something that was almost invisible because it was so routine: The reading room consult. Rounding teams came down. Surgeons pulled up their cases. Internists brought the scan that didn't quite fit the clinical picture. Sometimes the radiologist solved the problem. Sometimes the clinician supplied one piece of history that completely changed how the images were interpreted. And usually everyone simply walked away a little sharper. But something else was happening during all of those conversations. We were learning each other. As a radiologist, I learned what individual physicians cared about. I knew which findings mattered to a particular surgeon. Which measurements an oncologist was following. Which details a specialist wanted emphasized. What questions they were really asking, even when the order just said "pain." And they learned me. They knew who was reading their study. They knew they could walk in, point at something, challenge an interpretation, or ask, "What do you think?" That relationship created context. It created feedback. It created trust. And over years, it created a kind of institutional knowledge that never appears in the medical record. When radiology becomes a report produced by someone hundreds or thousands of miles away, we don't just lose proximity. We risk losing that entire feedback loop. The report may still be technically excellent. But the radiologist knows less about the physician. The physician knows less about the radiologist. The radiologist sees less of what happened after the report. And both sides lose opportunities to make each other better. The reading room was never just a room. It was where imaging became part of the clinical conversation. We should think very carefully before designing that conversation out of medicine. Inspired by a conversation yesterday with @PaleoOnc . Also @909One and @brianchiong .

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PARTNER 2A at ten years is a genuinely important paper. Extending a randomised TAVI-versus-surgery trial to a full decade, in an elderly intermediate-risk cohort, is hard, expensive, and exactly the long-horizon evidence the field has lacked. So this isn’t a critique of a flawed study — it’s a note on why two of its headline numbers, both pointing the same way, carry different evidentiary weight. Start with what the authors did well. Reintervention was analysed as a cumulative incidence function with Gray’s test, accounting for the competing risk of death — precisely the right estimand in a cohort with ~83% ten-year mortality. They even report the naïve Kaplan–Meier (16.1% vs 2.7%, HR 4.26) transparently as a sensitivity analysis, flagging it as the one that overstates risk by treating death as independent censoring. The model isn’t the issue. The limitation lies upstream, and the authors are candid about it. Nonfatal outcomes did not use the vital-status sweep. Mortality was recovered to ~90% completeness from public records — an impressive salvage. Reintervention runs on the on-study cohort alone. At year six, mortality has ~380/396 patients at risk per arm; reintervention has 174/159. After the five-year reconsent cliff, the durability endpoint is estimated on less than half the randomised population. What’s worth adding is how much that missingness matters. Among surgical patients alive at five years, 59.3% (270/455) declined reconsent and left at the start of years five to ten — the very window the paper flags as vulnerable for bioprosthetic failure. The 1.6% surgical estimate rests on eight events, three in that late window, while the cohort most likely to generate late events is largely unobserved. Dropout was differential (more in surgery). Reconsent that tracks health is informative censoring, which can bias the CIF itself, not only its variance — and the asymmetry favours surgery looking more durable. To put a number on it: reconstructing the published CIFs (Aalen–Johansen, validated to reproduce 6.3% / 1.6% and a p-value near the reported Gray’s test), how many unobserved surgical reinterventions would change the conclusion? About ten erase significance; ~25 reach parity. Across the ~425 surgical study-leavers, ten events is a reintervention rate of only ~2–4%. The literature says that’s a low bar. Around 15% of the trial’s surgical valves were Mitroflow and Trifecta — known early failures; Mitroflow reintervention at ten years ran ~22% Annalsthoracicsurgery. Even durable comparators show late attrition: in NOTION at ten years, with near-complete follow-up, surgical severe structural deterioration was ~10% and bioprosthetic valve failure ~14% PCRonline nih. Reintervention also undercounts failure, since frail octogenarians are often never reoperated — as the authors note. So 1.6% is a floor on a partly observed denominator. In statistical terms this is a fragility issue, not a flaw: a four-fold relative claim resting on eight events, in an arm that shed ~45% of its follow-up non-randomly, is hard to lean on — however well Gray’s test was applied. The direction is believable; the XT device genuinely predicts more TAVI reintervention (second-generation frame, no CT-based sizing, no 29 mm valve for the first 42.5% of enrolment). What the data can’t pin down is the magnitude. Contrast the mortality endpoint, where the paper is strongest: HR 1.13 (1.02–1.25), ~90% complete via the sweep, concordant in the ITT sensitivity analysis. That holds up. Its nuances — RMST over years five to ten non-significant, the excess confined to TA/TAo while transfemoral was neutral — are matters of careful reading, not missing data. So the honest summary is generous: a landmark, methodologically sound trial that delivers a robust mortality result and a directionally sound but quantitatively soft durability signal. The two rest on different foundations — one recovered, one necessarily incomplete — and the authors give us everything we need.