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Academy · Research Data Analytics & AI · AI in precision medicine

Artificial Intelligence in Precision Medicine: Reported Promise and Deployed Evidence

Machine learning has produced substantive results in precision medicine, almost all of which are molecular rather than clinical: predicting the effect of a variant, inferring a biomarker from morphology, and ranking drug sensitivity in cell lines. The gap between these results and a treatment decision altered because of a model is wide and under-reported, and it is the appropriate subject of any review in this area.

Pubrica AcademyWritten by the medical writing and biostatistics teams Reviewed byPubrica biostatistics team Published9 October 2026 Last checked9 October 2026 Reading time15 minutes Sources53 peer-reviewed

Precision medicine and machine learning are complementary in principle: high-dimensional molecular data, small effect sizes and interactions too numerous to enumerate manually. Parts of the resulting work are substantial. What is consistently absent is the step from a molecular prediction to a clinical one, from “this variant is probably deleterious” or “this tumour probably carries that alteration” to “this patient should receive that drug, and did better because a model said so.” This article distinguishes what has been demonstrated from what has been proposed.

Learning objectives

  • The areas of genomics in which deep learning has produced durable results, and the reasons those results are molecular rather than clinical
  • What inference of molecular status from histology images does and does not establish
  • The reasons drug-response prediction is the most difficult problem in the field, and the findings of community benchmarks
  • The reproducibility lesson of the microarray era and its direct relevance to current multi-omic models
  • The reporting requirements for a precision-medicine model before a reviewer can appraise it
  • The claims in this area that lack deployed evidence, to support accurate reporting

Common misconceptions

  • “AI can already select treatments for individual patients.” Published work predicts molecular features and drug sensitivity in preclinical systems. Evidence that acting on such a prediction changes patient outcomes is scarce, and is a different kind of study.
  • “More omics layers means a better model.” Each layer adds dimensions faster than it adds patients. Integration is a statistical liability as much as an opportunity, and the characteristic failure is undetected overfitting.
  • “Predicting a mutation from histology replaces molecular testing.” It is a triage and research tool with a stated performance and a stated population. No published work supports substituting it for the assay without a clinical evaluation of that substitution.
  • “Polygenic prediction is ready for individual clinical use.” Scores are developed in particular ancestry groups and transport poorly outside them, and the clinical utility question — whether acting on the score helps — is largely untested.
  • “This is a new problem.” The microarray era produced a substantial literature on this failure: predictive signatures that did not reproduce. The methodological lessons were documented and are now being relearned.

Aims of precision medicine and the anticipated contribution of AI

Collins and Varmus, in the New England Journal of Medicine, set out the initiative that gave the field its current shape: prevention and treatment that take individual variability in genes, environment and lifestyle into account 47. Aronson and Rehm, in Nature, described what building the genomic foundation for that would require — interpretation infrastructure, curated variant knowledge, and clinical reporting that a non-geneticist can act on 48. Ritchie and colleagues, in Frontiers in Genetics, added the other half: linking those genomic data to electronic health records, without which the phenotypes are unavailable 49.

The role machine learning was expected to fill follows from that description. The data are high-dimensional relative to sample size — many features, relatively few patients. Effects are small and interact. Relevant signal resides in sequence contexts, image textures and expression patterns that cannot be specified in advance. Sboner and Elemento, in Briefings in Bioinformatics, gave an early account of the informatics this implies, and Karczewski and Snyder, in Nature Reviews Genetics, of the integrative-omics ambition.

Topol, in Nature Medicine, and He and colleagues, in the same journal, both reviewed the resulting field with the same reservation: the modelling has outpaced the implementation by a wide margin 28,34. That reservation is the organising claim of this article, and the sections below examine where it applies most strongly.

Genomic applications and molecular endpoints

The clearest successes are in predicting molecular properties of sequence. Zou and colleagues, in Nature Genetics, and Eraslan and colleagues, in Nature Reviews Genetics, review the territory: predicting the functional consequences of variants, regulatory element activity, splicing, chromatin state and transcription factor binding from sequence alone 26,27. These are well-posed problems with abundant labelled data, and the models perform well on them.

In each case the endpoint is molecular. The model predicts a molecular property — whether a variant disrupts splicing, whether a region is accessible — not a clinical one. This is not a criticism; it is the appropriate scope, and the field states it clearly. The confusion arises downstream, when a variant-effect prediction is interpreted as a diagnosis or a treatment indication. The chain from “probably disrupts function” to “causes this patient’s disease” to “indicates this therapy” involves two further inferential steps, each of which requires its own evidence and neither of which the sequence model provides.

Ching and colleagues, in the Journal of the Royal Society Interface, surveyed opportunities and obstacles for deep learning across biology and medicine and reached a conclusion that merits restating in substance: the technical obstacles are tractable and the evaluation obstacles are not, because clinical endpoints are scarce, expensive and slow to accrue in precisely the settings where the models have most data 39.

Transportability of polygenic and SNP-based prediction

Ho and colleagues, in Frontiers in Genetics, review machine learning approaches to SNP-based prediction for precision medicine, and the evidence indicates that the methods perform approximately as well as the data design permits 31. Two constraints dominate and both are design problems rather than algorithmic ones.

The first is dimensionality. The number of candidate variants vastly exceeds the number of patients in almost every study, which makes feature selection the dominant source of optimism — and makes any feature selection performed before data splitting a fundamental error rather than a minor one. The second is ancestry. Scores developed in one ancestry group transport poorly to others, which means that a model’s reported performance is a property of the population in which it was developed. A paper that does not describe the ancestry composition of its development and validation cohorts has not reported its principal limitation.

A further question lies beyond both, and the literature largely does not address it: clinical utility. Knowing that a score discriminates risk is not the same as knowing that acting on it improves outcomes, and the second is a causal claim requiring a comparison of management strategies rather than a validation study. This distinction is examined in detail in the article on why prediction is not causation, and it applies to every risk score in this section.

Inference of molecular status from images

One notable finding in this field is that molecular information is partly discernible in routine histology. Coudray and colleagues, in Nature Medicine, trained networks on non-small cell lung cancer slides to classify histology and predict mutation status from morphology 35. Kather and colleagues, in Nature Cancer, extended the idea to pan-cancer image-based detection of clinically actionable genetic alterations 24. Wang and colleagues, in Medical Image Analysis, show how transformer-based unsupervised contrastive learning can be applied to histopathological classification, reducing the annotation requirement.

These studies establish that morphology carries molecular signal — a genuine and unexpected scientific finding. They do not establish a clinical substitution. Using an image-based prediction in place of a molecular assay is a different claim, requiring the performance of the substitution to be evaluated against the assay in the intended population, with the consequences of error specified: a false negative in this context means that a patient does not receive a targeted therapy from which they would have benefited. No study in this reference pool evaluates that substitution prospectively.

The appraisal points are the same as for any imaging model: external cohorts, case mix, calibration, a pre-specified threshold, and a stated intended use. The AI in medical imaging hub covers them in detail, and the cardiac imaging AI meta-analysis and convolutional network radiology meta-analysis show how such studies behave in aggregate. Liu and colleagues’ meta-analysis in The Lancet Digital Health remains the cautionary benchmark: across the whole imaging AI literature, only a small subset of studies had compared algorithm and clinician on the same sample 25.

Drug response prediction and evidence from community benchmarks

Treatment selection is the central aim of precision medicine, and it is the weakest part of the evidence. Ali and Aittokallio, in Biophysical Reviews, review machine learning and feature selection for drug response prediction in precision oncology and are explicit about the structural difficulty: the number of candidate molecular features is enormous, the number of profiled samples with response data is small, and response itself is measured differently across studies 32.

The most informative evidence here is a community benchmark rather than a single study. Costello and colleagues, in Nature Biotechnology, organised a DREAM challenge in which many teams attempted drug sensitivity prediction on the same data under the same conditions 50. The value of that design is that it removes the selective reporting that makes single-team results difficult to interpret: every method is evaluated on the same held-out data, including the methods that did not perform. Challenge formats of this kind are among the few mechanisms in this field that generate a realistic picture of achievable performance.

Two further points belong in any discussion of this area. Most published drug-response modelling is performed in cell lines and other preclinical systems, and the transfer from preclinical sensitivity to patient response is itself a research question rather than a technicality. In addition, Huang and colleagues, in Cancer Letters, reviewing AI in cancer diagnosis and prognosis, make the point that prognostic and predictive claims are routinely conflated in this literature — a model identifying patients with worse outcomes is not identifying patients who will benefit from a particular drug 23.

Dimensionality and sample size in multi-omic integration

Integration across omic layers is the field’s standing ambition and its standing statistical hazard. Karczewski and Snyder, in Nature Reviews Genetics, set out the case for integrative omics in health and disease. Gao and colleagues, in Cell, give a substantial worked example in their integrated proteogenomic characterisation of hepatitis B virus-related hepatocellular carcinoma 29. Curtis and colleagues, in Nature, established with the METABRIC breast tumour cohort that joint genomic and transcriptomic architecture defines subgroups that neither layer identifies alone — a result that has held up and that shaped how the field thinks about molecular taxonomy 52.

The hazard is arithmetical. Every additional layer multiplies the feature space while the patient count remains fixed or falls, because fewer patients have complete data across all layers. This worsens the feature-selection problem, increases the number of defensible-looking analytic paths, and makes internal validation less informative. Subbiah, in Nature Medicine, argues for a reconstruction of evidence-based medicine around this kind of data, and that argument is strongest where it is most specific about the evidence standard required rather than the data volume available — a distinction developed in the article on evidence-based medicine and precision medicine 14.

Reproducibility lessons from the microarray era

The field has conducted this experiment before. Shi and colleagues’ MicroArray Quality Control (MAQC)-II study in Nature Biotechnology examined the common practices used to develop and validate microarray-based predictive models across many endpoints and many analysis teams, and it remains the most important methodological paper for researchers developing a multi-omic predictor today. Its findings were unwelcome at the time and have been borne out since: the properties of the endpoint mattered more than the choice of algorithm, and the analysis team’s practices — particularly how validation was handled — mattered more than the modelling technique 53.

The practical implication for a current project is direct. The architecture is unlikely to be the determining factor; the endpoint definition, the validation design and procedural discipline are. The model should be locked before the validation data are accessed, feature selection should remain inside the resampling loop, and all analyses attempted should be reported, not only those that succeeded. These are established lessons expressed in new terminology, and because they were documented a decade and a half ago in a journal widely read in this field, a reviewer is unlikely to accept their absence as an oversight.

The pipeline-level treatment of these issues — where leakage enters, how to split, how to validate — is set out step by step in the article on the fundamental steps in neural-network-based diagnosis.

The evidence gap between molecular and clinical claims

Kelly and colleagues, in BMC Medicine, identify the barriers to clinical impact from AI as predominantly matters of evaluation, integration and monitoring rather than model performance 30. He and colleagues, in Nature Medicine, review the practical implementation of AI technologies in medicine and describe the same bottleneck from the health-system side. Fountzilas and colleagues, in Genome Medicine, address the trial-design consequence: precision medicine questions do not fit comfortably into conventional parallel-group designs, and the basket, umbrella and adaptive designs that fit better bring their own inferential complications 17.

Taken together, the gap comprises four specific components, and identifying them is more informative than describing it in general terms.

  • Endpoint mismatch. Models are trained on molecular or surrogate endpoints because clinical endpoints are scarce; the claim is then made at the clinical level.
  • No evaluation of substitution. Where a model is proposed in place of an existing test, the substitution itself is almost never evaluated.
  • Prognostic read as predictive. Identifying worse-outcome patients is persistently conflated with identifying treatment-benefiting patients.
  • Utility untested. Validation studies establish discrimination; whether acting on the model improves outcomes is a separate causal question that requires comparing management strategies.

Each of these can be acknowledged in a discussion section in two sentences, and doing so is now closer to a publication requirement than a stylistic choice. Dart’s short piece in Nature Reviews Cancer and Quazi’s review of AI and machine learning in precision and genomic medicine both capture the field’s expectations; the discipline lies in separating expectation from result.

Four areas of AI in precision medicine: what is shown, and what is claimed beyond it

AreaWhat the published work establishesWhat is claimed beyond itWhat would close the gap
Variant and regulatory effect predictionMolecular properties of sequence can be predicted with useful accuracy from sequence aloneThat a predicted effect identifies disease causation or a therapeutic indicationEvidence for each further step: variant to phenotype, and phenotype to treatment benefit
Polygenic and SNP-based riskScores discriminate risk within the ancestry groups they were developed inIndividual clinical use, and transportability across populationsValidation in the target ancestry and setting, plus a comparison of management strategies
Molecular status from histologyMorphology carries molecular signal; alterations can be flagged from slidesSubstitution for molecular assays in clinical practiceProspective evaluation of the substitution against the assay, with error consequences specified
Drug response predictionSensitivity is partly predictable in preclinical systems, as community benchmarks have assessedTreatment selection for individual patientsTransfer from preclinical to patient response, then a trial of model-guided versus standard selection

Compiled from the reviews and primary studies in the reference list: Zou and colleagues and Eraslan and colleagues on genomics; Ho and colleagues on SNP-based prediction; Coudray and colleagues, Kather and colleagues and Wang and colleagues on inference from histology; Ali and Aittokallio and Costello and colleagues on drug response. The right-hand columns state design requirements, not findings; no performance figures are implied.

Reporting a precision-medicine model

The characteristic weak sentence in this literature describes a cohort by size and a model by accuracy and leaves unstated everything that makes either interpretable. The two versions below describe the same study. Only one can be appraised, reused in a meta-analysis, or defended on resubmission.

For the statistical design — dimensionality, feature selection inside resampling, validation sample size — see the biostatistics role hub; for the reporting items required of any prediction model, reporting guidelines.

The same precision-medicine study, written two ways

Unappraisable

Using a large multi-omic cohort, we trained a machine learning classifier that accurately predicted treatment response and identified a molecular signature with strong prognostic value, supporting the use of our model to guide therapy selection.

“Large multi-omic cohort” is not a description. No source, no period, no ancestry, no case mix — so the result cannot be transferred anywhere.

Who had complete data? Requiring all omic layers selects a subset, usually a healthier or better-documented one, and this is the main selection bias in multi-omic work.

“Accurately predicted” how? No metric, no interval, no threshold, and no statement of whether validation was internal.

Feature selection unspecified. With features outnumbering patients, selection outside the resampling loop can generate the entire result.

“Prognostic value” then “guide therapy” — two different claims, one of which was not studied at all.

Appraisable

Patients were drawn from a single institutional cohort treated between [years], with inclusion limited to those having complete transcriptomic and proteomic profiles and documented response assessment; [n] of [n] screened patients met both conditions, and we report how the [n] excluded differed in stage and treatment line. Ancestry composition is given in Table 1. Response was defined by [criteria] at [time point]. Feature selection was performed inside the cross-validation folds, the model and its threshold were locked before the external cohort was accessed, and we report discrimination with confidence intervals, calibration slope and intercept, and performance in the external cohort separately. The signature is prognostic in this cohort; whether selecting therapy on it improves outcomes is untested and would require a comparison of model-guided with standard selection.

Provenance, period and the complete-data cascade are stated, so the selection built into the cohort is visible and quantifiable.

Ancestry composition appears, which is the limitation on transportability that SNP- and expression-based models most often omit.

The response definition and time point are given, so the endpoint can be compared with other studies rather than assumed equivalent.

Feature selection is declared as inside the folds and the model locked before external access — the two procedural points MAQC-II identified as decisive.

The prognostic finding and the therapy-selection question are separated explicitly, with the study that would answer the second one named.

The second version concedes more and claims less, and it is the version that can be entered into a systematic review, replicated by another group or cited in a regulatory file. The bracketed placeholders denote the study’s own counts. The two procedural sentences — feature selection inside the folds, model locked before external access — are what the microarray-era literature identified as mattering more than the choice of algorithm, and each requires only one line.

Key points

Key points

The results of machine learning in precision medicine are substantive and almost entirely molecular: variant effects, regulatory activity, biomarker status inferred from morphology, and drug sensitivity in preclinical systems. The clinical claims built upon them usually involve one or two further inferential steps that have not been evidenced. Four recurring gaps account for most of this: training on surrogate endpoints and then claiming clinical ones, proposing a model in place of a test without evaluating the substitution, interpreting prognostic findings as predictive, and treating a validation study as evidence of utility. The microarray era documented the procedural remedies: locking the model before validation, keeping feature selection inside resampling, and reporting ancestry and case mix. Acknowledging the gap in the discussion is now expected rather than optional.

Application to your study

Application to your study

  1. Specify the endpoint and whether it is molecular, surrogate or clinical, and confirm that every sentence in the abstract makes a claim at that level and no higher.
  2. Report the complete-data cascade. State how many patients were screened, how many had every omic layer, and how the excluded patients differed. Requiring complete multi-omic data is a selection step, not an administrative one.
  3. State the ancestry composition of development and validation cohorts. For any variant- or expression-based model, this is the principal limit on transportability, and its absence is likely to be among the first concerns raised by a reviewer.
  4. Perform feature selection inside the cross-validation folds and state this in the methods. When features outnumber patients, selection outside the loop can generate the entire result.
  5. Lock the model and its threshold before accessing the external cohort, and report that this was done. MAQC-II identified this procedural discipline as more important than the choice of algorithm.
  6. Separate prognostic from predictive explicitly. A finding that identifies patients with worse outcomes should be reported as such and not presented as a statement about who benefits from a treatment.
  7. Where replacement of an assay is proposed, evaluate the replacement. Report performance against the assay in the intended population and state the consequences of a false negative for the patient.
  8. Conclude the discussion by stating the utility question. A single sentence should state that whether acting on the model improves outcomes is untested, and identify the design that would test it.

Frequently asked questions

Predominantly molecular prediction, performed well. Zou and colleagues, in Nature Genetics, and Eraslan and colleagues, in Nature Reviews Genetics, review deep learning that predicts variant effects, regulatory activity, splicing and chromatin state from sequence. Coudray and colleagues, in Nature Medicine, and Kather and colleagues, in Nature Cancer, showed that clinically actionable alterations can be flagged from routine histology. Curtis and colleagues established molecular subgroups from joint genomic and transcriptomic data in Nature. What is largely missing is the clinical layer: evidence that a treatment decision taken on a model’s output produced a better outcome than the decision that would otherwise have been made.

Not reliably at the individual patient level on current published evidence. Ali and Aittokallio, in Biophysical Reviews, set out why: candidate molecular features vastly outnumber profiled samples with response data, and response is defined inconsistently across studies. Costello and colleagues’ DREAM challenge in Nature Biotechnology is the most informative evidence because many teams were evaluated on the same held-out data, which removes selective reporting. Most of this work is also performed in cell lines and other preclinical systems, and transfer from preclinical sensitivity to patient response is itself an open research question rather than an implementation detail.

Because each added layer multiplies the feature space while the number of patients with complete data stays fixed or falls, which makes feature selection the dominant source of optimism and multiplies the number of defensible-looking analytic paths. Shi and colleagues’ MAQC-II study in Nature Biotechnology examined this directly across many endpoints and analysis teams and found that the endpoint’s properties and the team’s procedural practices — especially how validation was handled — mattered more than the algorithm. The remedies are procedural: keep feature selection inside the resampling loop, lock the model before the validation data are accessed, report the complete-data cascade, and report all analyses attempted rather than only those that succeeded.

No published study in this area supports that substitution. Coudray and colleagues and Kather and colleagues established something scientifically important — that morphology carries molecular signal and that actionable alterations can be flagged from slides — which is a different claim from replacing an assay in clinical use. Evaluating a substitution requires measuring the image-based prediction against the assay in the population in which it would be used, with the error consequences stated: a false negative means that a patient does not receive a targeted therapy from which they would have benefited. Until that study exists, the appropriate framing is triage or research prioritisation, not replacement.

The clinical utility question is largely unanswered, and two limits dominate the literature Ho and colleagues review in Frontiers in Genetics. First, candidate variants vastly outnumber patients, so feature selection drives apparent performance and any selection performed before data splitting invalidates the estimate. Second, scores developed in one ancestry group transport poorly to others, which makes reported performance a property of the development population rather than of the score. Beyond both, discriminating risk is not the same as improving outcomes: establishing that acting on a score helps requires comparing management strategies, which is a causal question and a different study design.

A prognostic marker identifies patients with a different expected outcome regardless of treatment. A predictive marker identifies patients who will respond differently to a specific treatment. The two require different designs: predictive claims need a treatment-by-marker interaction, which means patients who did and did not receive the treatment. Huang and colleagues, in Cancer Letters, note that the distinction is persistently blurred in this literature. In machine learning papers the conflation is easily made, because a model trained on outcome in a treated cohort appears to predict response when it is in fact predicting prognosis. If a cohort was uniformly treated, the finding is prognostic.

With sufficient detail for a reader to judge selection and transportability: source institutions and period; the screening and complete-data cascade with counts, because requiring every omic layer selects a subset; how excluded patients differed; ancestry composition; stage, treatment line and prior therapy; and the endpoint definition and the time point at which it was assessed. These should be followed by the procedural statements: feature selection inside the resampling folds, the model and threshold locked before the external cohort was accessed, and both discrimination and calibration reported. This amounts to six or seven sentences, and it distinguishes a study that can be entered into a systematic review from one that cannot.

The tension is genuine, and the sources disagree about how to resolve it. Subbiah, in Nature Medicine, argues for a next generation of evidence-based medicine reconstructed around high-dimensional individual data, on the grounds that population-average trial estimates answer the wrong question for an individual patient. Fountzilas and colleagues, in Genome Medicine, take the more conservative route of adapting trial design — basket, umbrella and adaptive structures — while keeping randomised inference where it can be had. The disagreement is about method rather than principle: both accept that a claim about individual benefit needs evidence about individual benefit. Where that evidence comes from is unsettled.

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Every source above is a peer-reviewed article, a publisher’s record of one, or a standard issued by the body that owns it. Each carries the date it was last read. Where a standard moves, this article is revised rather than left up with a note.

How to cite this article

Pick your referencing style and copy it. Your university or target journal may vary the punctuation — check its guide if it has one.

Pubrica Academy. (2026, October 9). Artificial Intelligence in Precision Medicine: Reported Promise and Deployed Evidence. Pubrica. https://pubrica.com/academy/medical-writing/role-of-artificial-intelligence-in-precision-medicine/

This article is written to be learned from. Cite it if you are referring to what it says; if you are using the evidence behind it, cite the sources listed above instead.

Reporting checklist for a precision-medicine model paper

Written against the failure modes in this literature rather than as a general prediction-model checklist. Complete it before drafting the abstract, since most of the items change what the abstract is allowed to say.

PRECISION MEDICINE MODEL -- REPORTING CHECKLIST
Study / manuscript: ______________________   Date: ______________

1. ENDPOINT LEVEL           (this governs every claim in the paper)
   My outcome is:  molecular / surrogate / clinical
   My abstract claims at the level of:  molecular / surrogate / clinical
   Do these match?                                        yes / no
   If no, rewrite the abstract to the measured level.

2. COHORT AND SELECTION
   Source institutions: _____________________________________________
   Period: ______________________
   Screened: ______   With complete data across all layers: ______
   How the excluded differed (stage, line, performance status):
     _______________________________________________________________
   Ancestry composition reported?                         yes / no
   Stage, treatment line, prior therapy reported?         yes / no
   Uniformly treated cohort?                              yes / no
     -> if yes, any marker finding is PROGNOSTIC, not predictive

3. ENDPOINT DEFINITION
   Outcome definition: _____________________________________________
   Criteria and time point: ________________________________________
   Same definition as the comparison literature?          yes / no

4. DIMENSIONALITY DISCIPLINE
   Number of candidate features: ______   Patients: ______
   [ ] Feature selection performed INSIDE the resampling folds
   [ ] Hyperparameters chosen on a training-validation partition only
   [ ] Model AND threshold locked before external cohort accessed
   [ ] Number of model configurations tried is reported
   [ ] Batch / site / platform effects assessed and handled inside folds

5. PERFORMANCE REPORTING
   [ ] Discrimination with confidence intervals
   [ ] Calibration slope and intercept, with plot
   [ ] Internal and external results reported separately
   [ ] Performance by ancestry group and by site
   [ ] Negative and null results from other configurations reported

6. CLAIM SEPARATION          (one line each -- do not merge them)
   Prognostic finding: _____________________________________________
   Predictive finding, if any, and the interaction that supports it:
     _______________________________________________________________
   Proposed substitution for an existing test?            yes / no
     If yes: performance against that test in the intended population
     reported?                                            yes / no
     Consequence of a false negative for the patient: _______________

7. UTILITY STATEMENT         (required closing sentence)
   "Whether selecting [decision] on this model improves [outcome] is
    untested and would require [design]."
   Drafted?                                               yes / no

8. WHAT I AM NOT CLAIMING    (write these out, then check the abstract)
   [ ] Not claiming clinical benefit from a molecular endpoint
   [ ] Not claiming assay replacement without a substitution study
   [ ] Not claiming treatment selection from a prognostic model
   [ ] Not claiming transportability outside the ancestry studied

Pubrica AcademyWritten and maintained by Pubrica’s subject matter experts. Articles are revised when the underlying standards change, and each article states the date on which it was last reviewed.

How Pubrica can help

Pubrica’s bioinformatics and biostatistics teams address the elements of a precision-medicine manuscript that determine whether it replicates: the complete-data cascade, feature selection inside resampling, batch and platform effects, locking the model before external validation, and ancestry-stratified reporting. Pubrica’s medical writers then distinguish the prognostic finding from the predictive claim so that the abstract reports only what the study demonstrated.

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