Prototype Results
Status: demonstrated — the complete findings of the 2026 synthetic prototype.
This article is the evidence backbone of the documentation: every findings table from the synthetic prototype, every miss accounted for, and the limits of what the numbers mean. The authoritative result is the full-population grid — 3,250 phenotype patients × 5 models = 16,250 forced continuations, with zero errors.
The verdict
The method works decisively on the controlled synthetic world — the verdict is stated in full in the overview; this page holds the numbers behind it, every residual miss and false fire explained mechanically rather than hand-waved.
That proves the mechanism can work when an analogous precursor pattern exists. It does not prove that real conditions have such patterns, nor that the method survives messy real data — see what this does not prove before quoting any number below.
How to read the tables
A model "fires" when the string CPT-82197 — the screening TEST of the fabricated condition Primary Veladrin Excess — appears anywhere in its forced continuation (EOS banned, ~1,536 tokens, ten-plus rows). The read is binary, a string match against a code that exists in zero base patients by construction.
The prototype has no hold-out set. Every example trained exactly one pool's model and is out-of-distribution (OOD) for the other four — so the four models that never saw a patient are the decision-relevant read, and the in-distribution (IN) model is shown only for contrast. Tables below lead with OOD throughout.
The four example kinds, and what a fire on each one measures:
| kind | patients | the prompt contains | a fire measures |
|---|---|---|---|
| GOOD | 250 | the SIGNAL lead-up of a caught-in-time arc | sensitivity |
| BAD | 750 | SIGNAL plus accrued IMPACT, cut shortly before the late TEST | sensitivity |
| FAKE | 750 | the same BAD history cut ~20 rows earlier — before the TEST ever occurred | earliness |
| NOPE | 1,500 | an ordinary history whose bare TEST nothing in the record legitimately predicts | a false positive |
Sensitivity, specificity, earliness
The full-population grid, as executed and captured:
| kind | patients | OOD fire% | IN fire% | avg fire row |
|---|---|---|---|---|
| GOOD | 250 | 100.0 | 100.0 | 1.10 |
| BAD | 750 | 99.8 | 100.0 | 1.11 |
| FAKE | 750 | 90.0 | 95.0 | 1.24 |
| NOPE | 1,500 | 1.5 | 0.7 | 5.24 |
Three readings, in order of importance. First, OOD tracks in-distribution across the board — the phenotype transfers between pools as a real, learnable pattern, not a memorized cohort. This is the core claim of the whole experiment. Second, sensitivity on GOOD and BAD is at or near 100%, while NOPE — the specificity control — sits near 1%; and the rare NOPE fires land late in the continuation (average row ~5, versus row 1 for true fires), the signature of drift during forced generation rather than confident recognition. Third, FAKE is the earliness result: a FAKE prompt ends before the point where the TEST ever occurred, so firing on it means surfacing the screening earlier than the data did. FAKE fires 90.0% OOD, and the gap from 100% is almost entirely a construction artifact, explained row by row below.
Consensus
Single-model rates are not the unit of evidence — agreement across independent models is. Per patient, how many of the five models fired:
| kind | unanimous fire (5/5) | unanimous silent (0/5) | notable |
|---|---|---|---|
| GOOD | 250 / 250 | 0 | every early-caught patient, all five models |
| BAD | 744 / 750 | 1 | 5 split; the one silence is a cut artifact (below) |
| FAKE | 656 / 750 | 63 | the 63 silences are zero-precursor FAKEs — correct |
| NOPE | — | 1,425 / 1,500 | exactly one NOPE patient reached 5/5 |
Consensus is a noise filter, and the NOPE column shows it directly. Per model, the NOPE false-fire rate is about 1.4%. Require agreement before treating a fire as a flag, and it collapses:
| decision rule | NOPE false-positive rate |
|---|---|
| any single model | ~1.4% |
| ≥ 4 of 5 agree | 0.13% (2 / 1,500) |
| all 5 agree | 0.07% (1 / 1,500) |
The single design choice that mattered most — voting across independently trained models — is exactly what crushes the false positives. Out of 1,500 controls built so that nothing in the record could predict the TEST, precisely one drew a unanimous vote.
The steering baseline: adapter off
Is the firing behavior the base models' fluency, or the secondary steering adapters? Replaying the same sample of prompts with the adapter disabled — leaving the pure primary model — answers it:
| kind | adapter ON | adapter OFF |
|---|---|---|
| GOOD | 100% | 0.3% |
| BAD | 99.7% | 1.3% |
| FAKE | 94% | 0.7% |
| NOPE | 1.0% | 0.0% |
Unsteered, the models fired 7 times in 1,200 runs — essentially never. Everything in the tables above is attributable to the secondary steering round, not to base-model behavior.
The strip ablation: remove the signal, get silence
The experiment's stated win-condition had a mirror: if the models learned the injected pattern and nothing else, then stripping the injected rows from a carrier's history — leaving an ordinary background timeline, indistinguishable from a non-carrier — must return them to silence. On a 180-patient sample:
| kind | as-is fire% | stripped fire% | drop |
|---|---|---|---|
| GOOD (IN) | 100.0 | 0.0 | −100.0 |
| GOOD (OOD) | 100.0 | 1.7 | −98.3 |
| BAD (OOD) | 99.6 | 0.8 | −98.8 |
| FAKE (OOD) | 93.8 | 1.7 | −92.1 |
The first row is the punchline. In-distribution GOOD — the model shown a patient it trained on, minus the signal — fired 0 of 60. A model that had memorized its patients would recognize them anyway; it cannot, because it learned the pattern, not the patient. This is as clean as the win-condition gets.
Every miss explained
One rule holds across the entire dataset: the model fires if and only if the prompt contains at least one precursor (SIGNAL or IMPACT) row. Every apparent miss among the signal-bearing kinds traces to the prompt window containing no precursor — never to a model failing to recognize one that was there.
The 63 unanimously silent FAKEs are the bulk of it. The FAKE construction cuts a BAD history roughly 30 rows before its TEST, and for these 63 patients that cut lands before any SIGNAL or IMPACT exists — the prompt is already pure background. The ensemble's silence on them is correct behavior scored against a label with no signal in it. Conditioned on a precursor actually being present in the prompt, FAKE sensitivity is ~98–100%, in line with GOOD and BAD.
The single silent BAD is the same mechanism from the other side. That carrier has a full precursor set — six SIGNAL and two IMPACT rows — but the BAD cut placed every one of them beyond the prompt boundary, leaving a signal-free prompt. All five models were correctly silent.
So the causal chain closes tight: unsteered, the models essentially never fire; steered with a precursor present, they essentially always fire; steered with the signal stripped, they fall silent again. Fire ⟺ steered AND at least one precursor in the prompt. There are no unexplained failures on either side of that rule.
Dose-response: one row is a switch
How much of the precursor cascade does a model actually need? Holding a GOOD patient's background fixed and including 0, 1, 2, 3, or all of its SIGNAL rows (50 patients):
| signal rows in prompt | fire% | avg fire row |
|---|---|---|
| 0 (background only) | 1.6 | — |
| 1 | 90.8 | 1.83 |
| 2 | 98.8 | 1.33 |
| 3 | 100.0 | 1.14 |
| all | 100.0 | 1.06 |
Firing is a switch on presence, not a dose ramp: going from zero rows to one takes the rate from ~2% to ~91%. Additional rows do not change whether the ensemble fires; they sharpen how confidently — the fire moves toward row 1, and consensus tightens (at a single row, 37 of 50 patients are already unanimous 5-of-5). The implication for messy real data is the most encouraging shape this result could have taken: the mechanism degrades gracefully, surviving the loss of nearly the entire precursor cascade so long as one recognizable event remains in the history.
What this does not prove
The data is synthetic and deliberately clean. The signal is isolated by construction — that is the whole point, because it makes a positive result attributable to the method and nothing else — but it also means every rate on this page is an upper bound, not a forecast of real-world performance.
The prototype proves the method works given an analogous precursor pattern. It does not establish that real conditions leave such patterns in claims data, or how strong and learnable they are. That is the explicit leap of faith the experiment was always honest about, and it is tested next: real claims data, primary and secondary training per pool, retrospective evaluation, then a pilot with suggestions to physicians.
Two smaller cautions. The sub-analyses run on smaller samples (dose-response: 50 patients; strip ablation: 180) and are directional; the full-population grid is the robust result. And single-model behavior is noisy by design — only the cross-pool consensus counts as evidence, here and everywhere in PRISM.