A generative ICU twin trained without task labels forecasts 13 endpoints at AUROC 0.83–0.98 and ranks first among 20 predictors

Intensive care prediction no longer needs a separately labelled, separately trained model per outcome: one generative model reads risk from simulated patient futures across death, new invasive ventilation, vasopressor starts, renal replacement and acute kidney injury. Intensive care prediction has rested on supervised models, each trained for one outcome with labels defined at one site, whose AUROC sometimes falls by 0.2 at new hospitals; multi-database training narrows but does not close the gap, and earlier intensive care generative models were each trained within one database or health system. On held-out stays, Didymos reached AUROC 0.831 for hyperkalaemia within 24 hours to 0.982 for death within 24 hours of the landmark across 13 primary endpoints; it exceeded LightGBM on 12 of 13 and TabPFN-3.5 on 9 of 12, and every difference in a comparator's favour had a 95% CI including zero.

Risk is read not by counting how often an event appears in simulated futures but by summing the model's step probability of the event along each future and averaging over futures. Counting introduces sampling noise, especially for rare events; with 32 futures the pre-specified analysis trailed LightGBM on three mortality-related endpoints, by 0.062 for death within 24 hours on rolling anchors. The hazard estimate gave AUROC 0.81–0.92 from a single simulated future where the sampled estimate gave 0.61–0.66, and for death within 24 hours eight hazard-read futures exceeded 128 sampled ones (0.937 against 0.918).

The model simulates how a patient evolves after a treatment starts, and its simulated contrasts agree in direction with propensity-matched observational contrasts, describing observed practice rather than causal effects. Earlier intensive care digital twins were rarely tested against observed treatment responses and were judged mainly by prediction accuracy. Eight of nine pre-specified responses had simulated contrasts inside the 95% CI of the observed contrast, such as mean arterial pressure after norepinephrine at −3.3 against −3.6 mmHg; insulin was the exception, with real starters' glucose 38.0 mg/dL above their matches against −0.3 mg/dL simulated, and the null arm stayed at chance in 0.40–0.55 of prefixes.

At two hospitals that contributed nothing to training, zero-shot transfer was followed by about 7.5 GPU-minutes of continued training on unlabelled local stays, which brought the model level with locally supervised models. Zero-shot, Didymos exceeded LightGBM trained on the seven databases on 10 of 15 endpoint–database pairs but ranked second among predictors that never saw the new databases (3.80 against TabPFN-3.5's 3.27), while a local labelled LightGBM led on 13 of 15 pairs. Continued training lowered next-token loss on held-out patients of the new databases from 2.10 to 1.13 nats per token while loss on the seven databases rose by 0.01–0.03; on locked test anchors the adapted model exceeded the zero-shot one on 8 of 13 pairs, with the largest gains for outcomes shaped by local practice, such as an ICU stay over 7 days in RICD (+0.119) and a new vasopressor in zigongICU (+0.125), though no single difference held after Holm adjustment.

The results describe held-out patients from seven known databases, and transfer and adaptation were tested at only two external hospitals, where several endpoints had fewer than 30 events. The toolkit packages forecasting, what-if simulation, explanation, similar patients, cohort synthesis, trial design and teaching cases as seven tools, each output carrying the evidence and caveats of the corresponding analysis. The authors propose prospective validation at new sites, adaptation from fewer unlabelled stays with less exposure of each stay, training with the model's own samples with recalibration within each site, and re-analysing completed trials with the trial designer.

Free generation postpones deaths: simulated futures carried 0.61 of the real 24-hour death hazard and about half in the first 6 hours, with deaths missing mainly among short stays, and the authors propose exposure bias as an untested explanation. Treatment starts were over-predicted step by step, with raw O/E of 0.46–0.55, and post hoc recalibration overcorrected some endpoints. Simulated contrasts inherit the data's confounding and are not causal effects. Membership inference stayed near chance at AUC around 0.55, a weak but measurable signal, and the audits are empirical and specific to the attacks tested rather than formal guarantees. The adapted model's membership test on the seven databases missed its pre-specified bound by a narrow margin. The headline simulations used one seed, and the landmark sample for the two death endpoints was case-cohort, making trial sizes there relative. The rater study did not analyse time per case or seniority, and the card's gain specific to Didymos was estimated rather than tested.