Who would run it.

Why this page exists.

Episode 07 of Road to CEPAS 2026 picks up where Episode 06 stopped. The Substack post argues that the absence of a second impact trial in this field is not a failure of nerve but an accurate response to a set of incentives, and that the thing most worth proving is precisely the thing nobody can own.

This page is the working file: the sequence that put the HeRO device on the market before the trial began, the asymmetry between what a model publication costs and what a trial costs, two much better-funded groups stopping at the same rung we stop at, the enrolment arithmetic set against two Dutch-Belgian trials, and the argument that a validated response protocol is a public good.

The market did not require the trial.

The assumption worth discarding first is that the 2011 randomised trial existed because somebody needed it in order to sell something. The order of events runs the other way. The HeRO monitoring system already held 510(k) clearance when the trial began, for reporting heart rate characteristics as a measure of variability and transient decelerations, and the device was supplied by its manufacturer for use in the study (Moorman et al. 2011).

The commercial pathway was therefore already complete. A cleared device had reached the bedside by a route that never asked anyone to demonstrate that displaying the number changed anything for a baby. The trial was surplus to that route. It ran because a group wanted to know.

Doing it first, and being remembered for the wrong line.

The trial was powered to detect a two-day difference in days alive and off the ventilator, which is what set the sample size near three thousand. It found 2.3 days at P = 0.083. The primary endpoint did not reach significance. The result the field remembers, the reduction in all-cause mortality from 10.2% to 8.1%, was a secondary outcome, and the Dutch systematic review flagged the absence of correction for multiple testing among its reasons for rating the trial at high risk of bias (Koppens et al. 2023). The endpoint structure is set out in full on the Episode 06 page.

Read as a career, rather than as a result: a group did the hardest thing available in this field, did it first, did it at a scale nobody has matched in the fifteen years since, and the headline was a miss. The trial is now cited constantly, most often for the line beneath the one it was built to test.

What the field pays for instead.

The two options are not close to each other in cost, in risk, or in the probability of producing something publishable.

Two of the best-funded groups in medical AI stop at the same rung.

If money were the binding constraint, the constraint should relax where the money is abundant. Two systems published in Nature in the same issue suggest it does not.

MIRA is an autonomous agent operating inside a sandboxed electronic health record, able to take histories, order and interpret laboratory, imaging and microbiology tests, generate differential diagnoses and formulate treatment plans including prescriptions and admissions. On simulations built from real patient cases it outperformed physicians on diagnostic accuracy while making guideline-concordant and medication-safe decisions (Ferber et al. 2026). The paper closes by stating that generalisation, safety and governance still need to be established through prospective, real-world studies.

AMIE was compared with 21 primary care physicians across 100 multivisit case scenarios in a randomised, blinded virtual OSCE. It was non-inferior on management reasoning as assessed by specialists, and scored better on the preciseness of the treatment and investigation it proposed and on its grounding in clinical guidelines (Liévin et al. 2026). The paper likewise notes that further research is needed before real-world translation.

The accompanying commentary names the underlying difficulty as a measurement problem: the instruments used to evaluate these systems are changing faster than the studies that use them (Nature 2026). Base models improve every few months, which makes it hard to say where a system's capability came from, and a result about one version judged one way may not survive the next release. Both papers show scaffolding that helped an older model doing little for a newer one.

The enrolment arithmetic, without the excuses.

Two recent trials in this region give an objective sense of the distance, and both are properly conducted studies that answered real questions. The comparison is about what a mortality endpoint in this population demands, not about any country's capacity.

Closed both ways.

A trial on that scale would cost millions, so it is worth asking who recovers the money. There are two candidate things it could be testing, and neither route pays.

A validated response protocol gets published, and then it gets copied, and nobody pays a licence fee to follow a guideline. Worse, from the point of view of whoever funded the trial, a protocol that works on our score would very likely work on a competitor's score, or on thresholds applied to raw vital signs with no model underneath at all. The funder would be handing the result to the field.

Mortality is an inheritance, not a choice.

Mortality was never selected as the endpoint for heart rate characteristics monitoring. It was a secondary outcome that cleared significance narrowly, in a trial whose primary outcome did not, and without correction for multiple testing. Fifteen years on, the field treats it as the benchmark a new trial would have to meet.

That creates a bind with no comfortable exit. The only effect estimate available for a sample size calculation is the one from 2011, and effect sizes that just cross the significance threshold tend to be overstated, so powering on it risks a study underpowered for the true effect. Powering instead for something smaller and more plausible pushes the sample size past anything realistically assembled.

Six obstacles, which multiply rather than add.

Nothing forbids this trial, nothing rewards it, and nobody is responsible for it. Those are three separate problems, and the value of writing the series has been learning to see them separately. The same applies to the obstacles themselves, which had been sitting in one undifferentiated sense that the thing is too hard.

• Prediction performance is adequate, not commanding. Our AUC sits in the band this field converges on, and the precision figure is the one set out in Episode 04. A high false positive rate makes the question of the accompanying action more pressing, not less.
• Nobody knows what the right action is at the moment the alarm fires. That was Episode 06, and it remains the honest gap at the centre of the series.
• There is no funder, for the structural reasons set out above.
• The model was built on one hospital's population, which is small and unrepresentative in ways a multicentre study would expose.
• External validation is likely to reduce performance. A recent comparative study of late-onset sepsis prediction models across multiple clinical environments addresses exactly this (Peng et al. 2025).
• The track record for assembling trials at this scale is thin, which is a statement about capacity rather than about intent.