Stratum Collapse: When Language Models Turn a Subtype Finding into a Disease Fact

Patients with the same diagnosis often differ at the molecular level. A gene can be switched on in one subgroup of patients and switched off in another. In atrial fibrillation, for example, AKT3 moves up in some patients and down in others (Vanhoutte et al.). A language model that reads such a result and reports "AKT3 is upregulated in atrial fibrillation" has said something fluent, plausible, and wrong. We call this error stratum collapse: the model takes a finding that holds only in one molecular subgroup (a "stratum") and asserts it for the whole disease, or for a subgroup where it is false. This proposal builds a benchmark whose ground truth is computed directly from cancer omics data rather than from expert opinion. We use it to ask a sharp question: does pre-training a model on biomedical literature reduce stratum collapse, or does it make it worse, because papers mostly report headline, cohort-level findings?

In two sentences: we turn real between-subtype divergences in The Cancer Genome Atlas (TCGA) into natural-language inference items where the correct answer depends on keeping the subtype qualifier. We then measure, under matched compute, whether biomedical pre-training changes how often open models drop that qualifier, and whether the internal "task vector" the model builds from in-context examples explains and can repair the error.

Core Claim

Our first claim is that stratum collapse is a distinct, measurable hallucination. It is more common than ordinary reading errors on the same inputs. It is also hidden by existing clinical faithfulness benchmarks, which test cohort-level statements about trials rather than patient-level molecular divergence. The hallucination survey by Zhang et al. sorts errors into input-conflicting, context-conflicting, and fact-conflicting types. Stratum collapse is a specific input-conflicting failure in which the source says "in subtype A," and the generated claim drops or swaps the condition. Kather et al. motivate this from the applied side: when matching patients carrying biomarkers such as KRAS to trials, they found that dense embeddings could not separate "small cell" from "non-small cell" lung cancer. That is the retrieval-level analogue of collapsing a qualifier.

Our second claim is a falsifiable hypothesis, and we do not know its sign in advance. Domain pre-training is usually credited with better grounding. BioBART continually pre-trains BART on PubMed and improves biomedical generation, and MonoCoder shows a small domain model beating much larger general ones. But literature priors may push a model toward the pooled conclusion that papers typically state. If so, domain pre-training would raise stratum collapse even as it improves standard biomedical scores. Either outcome bears directly on the open tension the file documents. On one side, the Edinburgh team argue that open 7B models must be fine-tuned, and that zero-shot GPT-4 still beats them on clinical inference (Gema et al.).

Our third claim concerns mechanism. Geva et al. showed that a model compresses its few-shot examples into a "task vector": an intermediate-layer activation at the final example token that, when patched into a run without examples, recovers 80–90% of in-context accuracy. We hypothesize that stratum collapse appears when the subtype condition fails to enter this vector. If that is right, collapsed and correct runs should be separable along a direction in the task vector, and patching should repair some errors. Geva et al. studied single-token outputs only. Our classification items also have single-token label outputs, so we stay inside the regime where their method is known to work.

Research Program

Building the benchmark (SubtypeNLI). We start from the TCGA RNA-seq and continuous copy-number data. Abbasi et al. identify these modalities as the most reliable for subtyping. We use established cancer subtypes, with normal-tissue references from GTEx as in BulkRNABert, via the multiomics-open-research resource.

For each cancer type, we compute per-gene effect sizes and confidence intervals separately within each subtype. We keep "divergent" genes, whose direction differs between subtypes with confidence, and "concordant" genes, whose direction is the same in all subtypes, as controls.

Each item pairs a premise with a hypothesis, following the NLI4CT format. The premise is a short subgroup-results summary with sample sizes and effect sizes. Each hypothesis is one of five types:

  • a correct within-subtype claim;
  • a pooled claim about the whole disease, which is unsupported when the gene diverges;
  • a cross-subtype transfer claim;
  • a numeric claim, to probe the quantitative weakness reported by PubMedQA and Saama;
  • a pooled claim about a concordant gene, which is actually entailed.

That last type matters. It ensures a model cannot score well by refusing every pooled claim.

Because the labels come from the statistics, a simple calculator can solve every item. Any model error is therefore a reading or generation error, not genuine ambiguity. This sidesteps the weak agreement between automatic metrics and expert judgment noted by Zhang et al..

We add NLI4CT-style interventions to test whether models are consistent:

  • swapping the subtype labels in the premise;
  • paraphrasing the subtype names;
  • reordering the subgroups.

We also include a generation track: the model summarizes the premise, and an automatic checker extracts each atomic claim and scores it against the computed facts. A harder in-context track replaces the summary with a few patient-level profiles labelled by subtype. To answer, the model must infer the subtype-specific pattern from the examples themselves. Here in-context learning over molecular data meets the heterogeneity question directly. SynerGPT did few-shot learning over cell lines, but it removed all molecular features and all text, so it never measured this.

Controlled domain pre-training. To isolate the effect of pre-training, we take one open 7B base model, of the Mistral family used by Gema et al. We continue pre-training it under identical token budgets on two corpora: PubMed abstracts, as in BioBART, and a general-text control matched in size. A third arm uses PubMed filtered to passages that report subgroup analyses. This arm tests whether the content of the domain corpus matters, not just its domain. Existing biomedical models serve as a secondary check that the findings are not an artifact of our own training.

Mechanistic analysis. We extract task vectors from the in-context and summary prompts, sweeping layers because Geva et al. find a sharp best layer. We then test two things. First, can a linear probe on the task vector predict whether the run will collapse? Second, does patching a vector taken from a correctly answered prompt of the same subtype fix collapsed runs? Two controls pin down what any repair means: patching a random vector of matched norm, and patching a vector from a pooled-cohort prompt.

Baselines

The naive reference points are a majority-label classifier and a hypothesis-only model, a fine-tuned classifier that never sees the premise. If the hypothesis-only model scores well, the templates leak the answer, and we will rewrite them until it falls to chance.

The calculator reference is a rule applied directly to the premise numbers. Its near-perfect accuracy shows that the items are unambiguous. It also bounds what tool use could achieve.

The prompting baselines run the base 7B model three ways: zero-shot, with one or two examples, and with chain-of-thought. A further variant adds an explicit instruction to restrict claims to the stated subtype. This instructed prompt is the cheapest competitor to the mechanistic repair. Chain-of-thought gets its own test because Gema et al. report that it improves faithfulness while lowering F1.

The strongest open-model baseline is parameter-efficient fine-tuning with merged adapters, combining a language-modelling adapter with a triplet-loss adapter, as in Gema et al.. On NLI4CT, their MistralLite-7B with merged adapters reached an average score of 0.7862. We first reproduce this on NLI4CT, to confirm our pipeline matches theirs. We then train it on SubtypeNLI with the same training items, base model, and hyperparameter-search budget as every other trained arm. Evaluation uses held-out cancer types.

The strongest overall reference is zero-shot GPT-4. Gema et al. report an average score of 0.8328 and faithfulness of 0.9479 for it on NLI4CT. We run it on the public-data portion of SubtypeNLI only, because Kather et al. note that real patient data raise privacy concerns with hosted models. We found no reported result on Lacuna for any model on subtype-conditional inference, so every number on SubtypeNLI will be new.

The key ablations are the matched general-text pre-training arm, which isolates domain pre-training, and the random-vector and pooled-vector patches, which isolate the task-vector repair. "Beating" a baseline is defined as follows: a lower collapse rate on divergent genes, with no loss on the concordant pooled controls, with a 95% bootstrap interval excluding zero. The concordant-control condition guards against a model that wins simply by refusing pooled claims.

Why not just…?

Why not just tell the model to respect the subtype? This is the most direct threat to the mechanistic part of the proposal. Gema et al. found that 7B–13B models often fail to follow structured clinical instructions when prompted alone. In Geva et al.'s conflict tests, an injected task vector overrode the literal prompt. Both point toward instructions being insufficient, but neither is direct evidence on our task, so we test it head on. If the instructed prompt closes most of the collapse gap, we drop patching as a repair method and keep it only as a diagnostic.

Why not just fine-tune on subtype-conditional examples? This is a real threat, and it may well work in distribution. What we test is whether it transfers to cancer types, genes, and phrasings it never saw, and whether it holds up under the label-swap interventions. Chen et al. report that fine-tuning GPT-3.5 sometimes reduced consistency on guideline questions, which gives some reason to doubt robustness. But if fine-tuning generalizes, we will report that, and the paper's contribution becomes the benchmark plus the pre-training diagnosis.

Why not just let a tool compute the statistics, or use an SVM? For classifying patients by subtype, SVMs are strong; Abbasi et al. found SVM had the best overall mean macro-accuracy. But stratum collapse happens when a model writes language about results, not when it computes them. The generation track checks whether models collapse even when the correct numbers sit in their context. The calculator reference reports what tool routing could achieve.

Why not just use GPT-4? We include it. It still hallucinated 46.8% of the references it generated in Agrawal et al., and it cannot be used freely with patient data. The question of how open models should be trained remains whatever GPT-4 scores.

Decisive Checks

We will judge the project by three pre-registered outcomes.

  1. Collapse is real. The error rate on pooled and cross-subtype claims about divergent genes must clearly exceed the error rate on matched within-subtype claims. If it does not, there is no distinct phenomenon.
  2. Domain pre-training has a measurable effect. Under matched compute, the PubMed-pretrained model's collapse rate must differ from the general-text control's, in either direction. We will also check whether the subgroup-filtered PubMed arm moves the rate. That would show the content of the corpus matters, not just its domain.
  3. Patching does more than add noise. Same-subtype patching must repair substantially more collapsed runs than random-vector patches do. It must also outperform the instructed prompt at an equal number of extra forward passes.

A null result on the first check ends the project. A null on the third reduces the work to a benchmark and a pre-training study, which is still informative.