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Academy · Research Data Analytics & AI · EBM vs precision medicine

Evidence-Based Medicine and Precision Medicine: A Comparison of Their Limitations

Evidence-based medicine and precision medicine are not rival philosophies, and treating them as such obscures the weaknesses of each. Evidence-based medicine addresses average effects in defined populations and is weak with respect to the individual. Precision medicine addresses the individual and is weak in demonstrating that the individualised decision was the better one. Because these limitations are complementary, the defensible position is to use both and to state which is being relied upon.

Pubrica AcademyWritten by the medical writing and biostatistics teams Reviewed byPubrica biostatistics team Published9 October 2026 Last checked9 October 2026 Reading time15 minutes Sources65 peer-reviewed

Sackett, Rosenberg, Gray, Haynes and Richardson defined evidence-based medicine in the BMJ as the integration of the best available external evidence with clinical expertise and patient values, a definition that already incorporates the individual but is frequently neglected in favour of a caricature of rigid adherence to trial averages. Precision medicine, as set out by Collins and Varmus in the New England Journal of Medicine, proposes to stratify care by molecular and other individual-level characteristics. The central question is not which framework is correct, but what each cannot establish and how a claim can be formulated that respects the distinction.

Learning objectives

  • The claims each framework makes, as stated by its founders
  • Why average treatment effects and individual benefit diverge, and the appropriate methodological response
  • The criteria that make a subgroup or biomarker claim credible rather than suggestive
  • The respects in which the results of precision medicine have fallen short of its programme, as described by its critics
  • The genuine weaknesses of evidence-based medicine beyond the usual criticisms
  • The formulation of a stratified-medicine claim acceptable to a methodological reviewer

Common misconceptions

  • “Evidence-based medicine means following trial results regardless of the patient in front of you.” Sackett and colleagues defined it in the BMJ as integrating the best external evidence with clinical expertise and patient values, in a paper explicitly titled to address what it is and what it isn’t. The caricature is a straw man that makes precision medicine appear more novel than it is.
  • “Precision medicine replaces population evidence with individual data.” It cannot, because establishing that a stratified strategy is superior still requires a comparison in a population. Chow, Gallo and Busse argue in Precision Clinical Medicine that the two are complementary approaches to clinical decision-making, and Beckmann and Lew, in Genome Medicine, set out how they are reconciled rather than traded off.
  • “A positive subgroup finding identifies the patients who benefit.” In most cases it does not. Sun and colleagues examined the credibility of subgroup-effect claims in randomised trials in the BMJ, and, with Briel, Walter and Guyatt, set out updated criteria for judging whether a subgroup effect is credible. Most reported subgroup effects do not meet them.
  • “Molecularly matched therapy is established practice in oncology.” It is established in specific settings and contested as a general strategy. Prasad’s commentary in Nature is titled the precision oncology illusion; Tannock and Hickman set out limits to personalised cancer medicine in the New England Journal of Medicine; Schwaederle and colleagues’ meta-analysis in JAMA Oncology of biomarker-based treatment strategies in refractory malignant neoplasms provides the counterargument. The literature is internally divided, and a manuscript should acknowledge this rather than cite only one side.
  • “Artificial intelligence settles the individualisation problem.” Not on current evidence, and the deficit lies in comparison rather than computation. Liu and colleagues’ systematic review in The Lancet Digital Health found few studies presenting externally validated, same-sample comparisons; only 14 such comparisons were available for pooling. An individualised prediction that has not been compared fairly against current practice has not been shown to improve on it.

The claims of each framework in its own terms

Both frameworks have founding statements that merit reading in the original rather than in paraphrase, because the paraphrases have drifted from them.

The Evidence Based Medicine Working Group’s 1992 statement in JAMA described a new approach to teaching the practice of medicine, and Sackett and colleagues’ 1996 BMJ editorial defined the practice itself as integrating the best available external clinical evidence with clinical expertise and individual patient values 62,63. The hierarchy of evidence, which is what is most often meant by EBM, is an instrument within that definition rather than the definition itself. The movement also produced individual-level methods early: Guyatt and colleagues reported n-of-1 randomised controlled trials in the New England Journal of Medicine and then three years’ clinical experience of them in the Annals of Internal Medicine 64,65. Individualisation was never outside EBM’s scope; it was a minority technique within it.

Precision medicine’s programme was stated by Hamburg and Collins in the New England Journal of Medicine as the path to personalised medicine, and by Collins and Varmus in the same journal as a national initiative 51,58. Naithani and colleagues, in the Medical Journal Armed Forces India, and Goetz and Schork, in Fertility and Sterility, give accessible accounts of the concepts and tools. The claim is that individual-level features (genomic, molecular, environmental, behavioural) identify subsets of patients for whom the appropriate action differs from the population average.

Considered together, the two frameworks answer different questions 32,56. EBM asks what works, on average, in a defined population, and has a well-developed apparatus for answering that question. Precision medicine asks which patients should receive which intervention, and has a well-developed apparatus for generating hypotheses about it but a much weaker one for confirming them. Our pages on how EBP enables informed decisions and the role of AI in precision medicine cover each side in more depth.

Two frameworks, compared on what they can and cannot establish

Evidence-based medicinePrecision medicine
Founding statementEvidence Based Medicine Working Group, JAMA, 1992; Sackett and colleagues, BMJ, 1996Hamburg and Collins, New England Journal of Medicine, 2010; Collins and Varmus, same journal, 2015
Question it answers wellWhat works, on average, in a defined populationWhich individual-level features are associated with a different response
Unit of inferenceThe population or trial-eligible groupThe stratum, and ultimately the individual
Strongest evidence formRandomised trials and their synthesesMarker-defined randomised designs — basket, umbrella, platform — and n-of-1 trials
Characteristic weaknessAn average effect is compatible with many distributions of individual benefitHypotheses are generated far faster than they can be confirmed
Where it is most contestedApplicability to patients excluded from trials by comorbidity, age or pregnancyCommon complex disease, where the predictive ceiling is low and actionability is narrow
Where it is least contestedInterventions with large, consistent effects across settingsMonogenic and near-monogenic conditions, and rare disease
The failure mode to avoid in writingCiting a pooled estimate as though it applied uniformly to every patientReporting a subgroup difference without an interaction test or a pre-specified hypothesis

Compiled from the founding statements and from the critical literature cited in this article, including Kravitz, Duan and Braslow (The Milbank Quarterly), Sun and colleagues (BMJ), Prasad (Nature), Tannock and Hickman (New England Journal of Medicine), Sheridan and Julian (Journal of the American College of Cardiology) and Chow, Gallo and Busse (Precision Clinical Medicine).

The limitations of average treatment effects

The most incisive critique of trial-based evidence is not that trials are unrealistic. It is that an average treatment effect is compatible with many different distributions of individual benefit, including distributions in which most patients derive no benefit and a few derive substantial benefit.

Kravitz, Duan and Braslow made this argument in The Milbank Quarterly under a title that summarises the argument: heterogeneity of treatment effects and the trouble with averages 60. Dahabreh, Hayward and Kent, in the International Journal of Epidemiology, develop the methodological version: how group data can be used to treat individuals, and the conditions under which this is valid 49. The central distinction in that literature is between variation in observed outcomes, which is always present and mostly reflects baseline risk and noise, and variation in treatment effect, which is much rarer and considerably more difficult to demonstrate.

Most individualisation claims fail at this distinction. Patients at higher baseline risk gain more in absolute terms from a treatment with a constant relative effect; this is real and clinically important, but it is not effect modification. Risk-based stratification is therefore usually better supported than stratification based on effect modification, and the two are frequently conflated. Where a manuscript claims that a subgroup benefits differently, it should state clearly whether this refers to a different absolute benefit at the same relative effect, which follows from baseline risk alone, or to a genuinely different relative effect, which requires an interaction and the evidence standards described in the next section.

Criteria for credible subgroup and biomarker claims

Precision medicine generates subgroup claims faster than they can be confirmed, and there is an established literature on which of them are credible. Sun, Briel, Walter and Guyatt set out criteria in the BMJ for judging whether a subgroup effect is credible, and Sun and colleagues then systematically examined the credibility of subgroup-effect claims across randomised trials in the same journal 55,57.

These criteria also serve as a drafting checklist. Was the subgroup hypothesis specified before the data were seen, and was the direction of the expected effect also specified? Was the subgroup one of a small number examined, or one of many? Was a formal test for interaction performed and reported, rather than separate within-subgroup tests, which constitute the most common statistical error in this area? Is the effect consistent across related studies? Is there an independent biological or clinical rationale? Is the subgroup variable measured reliably and in the same way in all settings?

Two failures merit explicit mention. Reporting that a treatment was significant in one subgroup and not in another is not evidence of a differential effect; it represents two tests with different power, and the appropriate analysis is the test for interaction 57. In addition, a biomarker that predicts prognosis is not thereby a marker that predicts treatment benefit; prognostic and predictive are different properties and require different designs to establish. Biostatistics support and statistical review can identify these problems before a reviewer does.

Judging whether a subgroup or biomarker effect is believable

QuestionWhy it mattersThe weak version that should not be accepted
Was the hypothesis pre-specified, with a direction?A subgroup effect identified post hoc is a different claim from one predicted in advance“Exploratory subgroup analyses were performed” followed by a confident conclusion
How many subgroups were examined?The chance of a spurious finding rises with the number testedOne significant subgroup reported, with no statement of how many were looked at
Was a formal interaction test reported?Separate within-subgroup tests have different power and cannot establish a differential effect“Significant in group A (p=0.02) but not group B (p=0.21)”
Is the effect consistent across related studies?A real effect modifier should reappear; a chance finding should notA single-trial finding presented as established
Is there independent biological or clinical rationale?A plausible mechanism makes a statistical finding more credible, although it cannot substitute for oneA plausible mechanism offered in place of an interaction test
Is the subgroup variable measured reliably and identically everywhere?Measurement differences alone can create or destroy an apparent interactionNo statement of how the marker was assayed or classified
Is the marker prognostic or predictive?Predicting outcome and predicting treatment benefit are different properties needing different designsA prognostic marker used to select treatment

Criteria follow Sun X, Briel M, Walter SD, Guyatt GH. Is a subgroup effect believable? Updating criteria to evaluate the credibility of subgroup analyses. BMJ; and Sun X, Briel M, Busse JW, et al. Credibility of claims of subgroup effects in randomised controlled trials: systematic review. BMJ. The third column is our characterisation of the patterns observed in drafts.

A stratified-benefit claim in a results and discussion section

Subgroup finding as discovery

In the overall population the treatment effect did not reach statistical significance. However, in the biomarker-positive subgroup the treatment was associated with a significant improvement in the primary outcome (p = 0.03), whereas no effect was seen in biomarker-negative patients (p = 0.68). These findings indicate that the biomarker identifies the patients who benefit from this treatment and support its use to guide therapy.

Two within-subgroup p values presented as a differential effect. This is the most common statistical error in stratified-medicine writing; the relevant analysis is the test for interaction, and it is absent.

No statement of how many subgroups were examined. Without a known denominator, a single significant subgroup carries almost no information.

No indication of pre-specification. A hypothesis generated after the data were seen is a different claim from one stated in a protocol, and the reader cannot determine which applies here.

A null overall result rescued by a subgroup. This is the pattern that the credibility literature was developed to address, and reviewers recognise it immediately.

“Identifies the patients who benefit” asserts a predictive marker on evidence that at best suggests one, and makes no distinction between prognostic and predictive.

“Support its use to guide therapy” is a practice recommendation from an underpowered secondary analysis of a null trial.

Subgroup finding as hypothesis, correctly bounded

The treatment effect in the overall population was not statistically significant. The biomarker subgroup analysis was one of four pre-specified subgroup hypotheses, each with a pre-specified direction, and is reported here as a test for interaction rather than as separate within-subgroup tests: the interaction between biomarker status and treatment allocation was not statistically significant, although the point estimates differed in the direction hypothesised. Because the trial was not powered for interaction, this analysis cannot establish effect modification, and the difference between a significant within-subgroup result and a non-significant one reflects differing power as much as any differential effect. The biomarker was assayed centrally by a single method, with the classification threshold fixed before unblinding. We therefore treat this as a hypothesis for prospective testing in a biomarker-stratified randomised design, and we note that the biomarker’s prognostic value in this cohort does not by itself establish that it predicts treatment benefit.

The interaction test is the reported analysis, and the number of pre-specified subgroup hypotheses is stated, so the reader can weigh the finding.

The power limitation is stated explicitly, which anticipates the objection and demonstrates that the authors understand what their design can and cannot detect.

The difference in direction of effect is reported transparently as a pattern in point estimates rather than translated into a claim about which patients benefit.

Assay method and threshold timing are specified, removing the possibility that the classification was optimised after unblinding.

The distinction between prognostic and predictive markers is made explicitly; this is the distinction that most often breaks down in biomarker writing.

The conclusion is a design for the next study rather than a recommendation for practice, which is both transparent and considerably more likely to withstand peer review.

The second version makes a claim that a methodological reviewer can accept and a trialist can act on. The first makes a claim that will be rejected, and that would be harmful if it were accepted.

Shortfalls of precision medicine relative to its programme

The critical literature on precision medicine is substantial and authoritative, and a manuscript that ignores it appears promotional. The literature is also not unanimous, and that disagreement is itself a finding to report.

Prasad, in Nature, argues this position under the heading of the precision oncology illusion 48. Tannock and Hickman, in the New England Journal of Medicine, set out limits to personalised cancer medicine. Joyner, Paneth and Ioannidis ask in JAMA what happens when underperforming major ideas in research become entrenched. Ioannidis and Khoury, in Human Molecular Genetics, examine evidence-based medicine against big genomic data. Duffy, in Briefings in Bioinformatics, surveys the problems, challenges and promises together.

Against that, Schwaederle and colleagues’ meta-analysis in JAMA Oncology found biomarker-based treatment strategies associated with better response rates and progression-free survival in refractory malignant neoplasms, and Tsimberidou and colleagues, in Nature Reviews Clinical Oncology, describe molecular tumour boards as established infrastructure with current and future considerations rather than as an experiment 11,42. Might and Crouse argue in Cell Reports Medicine that rare disease is where the approach is least contestable, and the argument generalises: precision medicine is strongest where the biology is monogenic or near-monogenic, the effect is large, and no alternative treatment exists 19.

Four structural limitations recur irrespective of which position is considered more persuasive. Most phenotypes are not monogenic, so the predictive ceiling for common complex disease is low. Actionability is narrower than detectability: identifying a variant is not the same as having an intervention for it. Evidence generation is slow relative to marker discovery, so the ratio of claimed to confirmed markers continues to rise. Finally, the populations in which markers were discovered are not representative, which translates directly into inequitable performance; Ramaswami, Bayer and Galea develop that point from a public health perspective in the Annual Review of Public Health 35,39.

Genuine weaknesses of evidence-based medicine

The usual criticisms of EBM are weak, and its genuine limitations are specific. Sheridan and Julian survey its achievements and limitations in the Journal of the American College of Cardiology, and Fernandez and colleagues ask in Health Research Policy and Systems whether it is a bridge too far.

Four limitations hold up. The evidence base is not the evidence. What has been trialled reflects what was fundable and commercially attractive, so the absence of evidence is systematically non-random across questions. Trial populations are selected. Eligibility criteria exclude comorbidity, polypharmacy, age extremes and pregnancy, which characterise precisely the population in which most clinical decisions are made. Aggregation can obscure what matters to the individual. This is the point made by Kravitz and colleagues, and it is a genuine limitation of an average rather than a flaw in how averages are estimated. The patient’s values are the hardest element to operationalise. Bensing, in Patient Education and Counseling, describes the separate worlds of evidence-based and patient-centred medicine, and the gap she identified has narrowed in theory more than in practice 61.

Several common criticisms do not withstand scrutiny: that EBM ignores mechanism, that it cannot accommodate individual data, or that it is hostile to clinical judgement. The definition by Sackett and colleagues answers all three in advance. Where a manuscript criticises EBM, authors should verify which version is being criticised, because a reviewer familiar with the 1996 paper will notice.

Convergence of the two frameworks in implementation

The point at which these frameworks must be reconciled is the point of care, and pharmacogenomics is the most mature example, sufficiently mature to show where the difficulty lies.

Hoffman and colleagues, in the Journal of the American Medical Informatics Association, describe the Clinical Pharmacogenetics Implementation Consortium’s principles for developing knowledge resources, an explicit attempt to translate gene-drug evidence into actionable guidance 44. Bell and colleagues, in the same journal, report development and use of active clinical decision support for pre-emptive pharmacogenomics. Klein, Parvez and Shin set out the barriers and solutions in the Journal of Pharmaceutical Sciences, and Chambliss and Marzinke, in The Journal of Applied Laboratory Medicine, give an account of successes and setbacks that is unusually candid about the setbacks 30,38.

The scale of the available tooling indicates how early this field remains. Johnson and colleagues’ systematic review of genetically guided precision-medicine clinical decision support tools, in the same journal, found 41 primary articles describing 36 unique tools 5. That ratio, close to one article per tool, is informative: this is a field of individual implementations each described once, not a field of tools with accumulated independent evaluation 5. Any claim that genetically guided decision support improves outcomes must be interpreted in that light.

Milani, Leitsalu and Metspalu’s account of the Estonian experience in the Journal of Internal Medicine provides the national-scale perspective, and Day and colleagues’ cross-sectional analysis in the Journal of Medical Internet Research assessing the clinical robustness of digital health startups provides an assessment of the commercial sector. See steps for implementing EBP in healthcare and translating research into practice interventions for the implementation science side.

41primary articles identified
36unique decision support tools described

Close to one publication per tool: a field of single implementations rather than one with accumulated independent evaluation. Figures from Johnson D, Del Fiol G, Kawamoto K, et al. Genetically guided precision medicine clinical decision support tools: a systematic review. Journal of the American Medical Informatics Association.

Cost-effectiveness of individualised care

This question is raised less often than it should be in clinical manuscripts, yet it is raised consistently by those who decide whether a strategy is adopted. Two syntheses provide a starting point, and neither supports a confident general answer.

Vellekoop and colleagues, in Value in Health, conducted a systematic literature review and regression analysis of the net benefit of personalised medicine. Kasztura and colleagues, in the International Journal of Public Health, conducted a scoping review of the cost-effectiveness of precision medicine 26. A balanced summary of this body of work is that cost-effectiveness is strongly dependent on setting and strategy, that the favourable cases tend to involve avoiding an expensive or harmful treatment in patients who will not benefit, and that the unfavourable cases tend to involve testing many patients to identify few.

The implications for a manuscript are narrow but useful. A manuscript proposing a stratified strategy should state the test-to-treat ratio (the number of people tested to change one decision), because that number determines all downstream consequences and is usually calculable from data already available. It should state what happens to the patients the test excludes, since a strategy that withholds treatment from a marker-negative group must also be evaluated on their outcomes. It should also distinguish a cost-effectiveness claim from a clinical effectiveness claim, because they require different evidence and different expertise. Health economics support and cost-effectiveness modelling are where that analysis belongs.

Study designs and reporting of the comparison

The resolution of this debate is methodological rather than rhetorical, and the designs that resolve it already exist. Fountzilas, Tsimberidou, Vo and Kurzrock review clinical trial design in the era of precision medicine in Genome Medicine: basket, umbrella and platform designs test marker-defined hypotheses within a randomised framework, which is precisely the construction that makes a precision claim evidence-based rather than mechanistic 16. Guyatt and colleagues’ n-of-1 design is the individual-level version and has been available since the 1980s. Subbiah, in Nature Medicine, describes the next generation of evidence-based medicine as this synthesis rather than as its successor.

Real-world evidence is the other current route and requires careful handling. Van Spall and colleagues, in Nature Cardiovascular Research, discuss the role of early-phase trials and real-world evidence in drug development; Raphael, Gyawali and Booth, in Nature Reviews Clinical Oncology, examine real-world evidence and regulatory drug approval 10,22. The constraint is the one Msaouel names as the big data paradox in Cancer Investigation, namely that scale reduces variance but not bias, and that Verheij and colleagues document for routinely collected records in the Journal of Medical Internet Research.

Four rules apply to writing. The manuscript should state which question it answers: the average effect in a population, or a differential effect across strata. If the latter, it should report the interaction rather than within-subgroup tests and state whether the hypothesis was pre-specified. It should distinguish prognostic from predictive markers explicitly. Where the literature disagrees, as it does on precision oncology, it should cite both positions and state what evidence would resolve the disagreement. On the regulatory horizon, the EMA reflection paper on the use of artificial intelligence in the medicinal product lifecycle and Regulation (EU) 2024/1689, the Artificial Intelligence Act, now form part of the context for any individualised tool intended for use rather than publication; Lee and colleagues address the methodological and regulatory considerations for causal AI in drug development in npj Digital Medicine 1,2,9. See epidemiology designs for clinical trials and regulatory affairs and causal inference in machine learning.

Key points

Key points

Evidence-based medicine and precision medicine have complementary limitations. Sackett and colleagues’ definition of EBM already integrates external evidence with clinical expertise and patient values, so the caricature of rigid adherence to trial results is a straw man; its genuine limitations are a non-random evidence base, selected trial populations, and the fact that an average effect is compatible with many distributions of individual benefit, the point made by Kravitz, Duan and Braslow about “the trouble with averages”. Precision medicine addresses the individual but generates hypotheses far faster than it confirms them: the critical literature extends from Prasad’s precision oncology illusion to Tannock and Hickman’s limits to personalised cancer medicine, with Schwaederle and colleagues’ meta-analysis on the other side, and implementation remains at an early stage, with a systematic review of genetically guided decision support tools identifying 41 articles describing 36 unique tools, approximately one publication each. The reconciliation is methodological: marker-defined randomised designs, n-of-1 trials, interaction tests rather than within-subgroup comparisons, and an explicit distinction between prognostic and predictive markers. Artificial intelligence does not circumvent this requirement; only 14 externally validated same-sample comparisons were available for pooling in the review by Liu and colleagues.

Application to your study

Application to your study

  1. The question addressed by the paper should be stated. The question concerns either the average effect in a population or a differential effect across strata, and every claim in the discussion should correspond to the question named.
  2. Interaction tests, rather than within-subgroup tests, should be reported. Where a differential effect is claimed, the interaction test is the appropriate analysis. The number of subgroups examined, and which hypotheses were pre-specified with a direction, should be stated.
  3. Prognostic and predictive markers should be distinguished explicitly. A marker that predicts outcome is not thereby a marker that predicts treatment benefit, and the designs needed to establish each are different.
  4. Absolute and relative benefit should be distinguished when discussing which patients gain most. Higher baseline risk yields larger absolute gain at constant relative effect; that is risk stratification, not effect modification, and it is usually the better-supported claim.
  5. Both positions should be cited where the literature disagrees. This is the case for precision oncology. The disagreement should be named, the evidence that would resolve it identified, and selective citation in the discussion section avoided.
  6. The test-to-treat ratio should be reported for any proposed stratified strategy. The ratio indicates how many patients must be tested to change one decision, and the report should state what happens to the patients excluded by the test.

Frequently asked questions

They answer different questions. Evidence-based medicine, as Sackett and colleagues defined it in the BMJ, integrates the best available external evidence with clinical expertise and patient values, and its apparatus (randomised trials and their syntheses) is designed to establish what works on average in a defined population. Precision medicine, as set out by Hamburg and Collins and later by Collins and Varmus in the New England Journal of Medicine, asks which individual-level features identify patients for whom the appropriate action differs from that average. A useful way to reconcile them is Chow, Gallo and Busse’s framing in Precision Clinical Medicine: complementary approaches to clinical decision-making. A precision claim must still be demonstrated, and demonstrating it requires population-level comparison.

Four withstand scrutiny. The evidence base is not the evidence: what has been trialled reflects what was fundable and commercially attractive, so gaps are systematically non-random. Trial populations are selected, with eligibility criteria that commonly exclude comorbidity, polypharmacy, age extremes and pregnancy, which are the circumstances in which most decisions are actually made. An average treatment effect is compatible with many distributions of individual benefit, which is the point Kravitz, Duan and Braslow made in The Milbank Quarterly. Finally, patient values, although part of the original definition, remain the most difficult element to operationalise; Bensing wrote about the separate worlds of evidence-based and patient-centred medicine in Patient Education and Counseling and the gap has narrowed more in theory than in practice.

Four structural limitations apply, irrespective of which side of the debate is considered persuasive. Most phenotypes are not monogenic, so the predictive ceiling for common complex disease is low. Actionability is narrower than detectability: identifying a variant is not the same as having an intervention for it. Evidence generation is slow relative to marker discovery, so the ratio of claimed to confirmed markers continues to grow. Finally, discovery populations are unrepresentative, which translates directly into unequal performance, a point Ramaswami, Bayer and Galea develop in the Annual Review of Public Health. The critical literature (Prasad in Nature, Tannock and Hickman in the New England Journal of Medicine, Joyner, Paneth and Ioannidis in JAMA) merits direct engagement rather than avoidance.

The literature genuinely disagrees, and a manuscript should acknowledge this. On the critical side, Prasad’s commentary in Nature is titled the precision oncology illusion, and Tannock and Hickman set out limits to personalised cancer medicine in the New England Journal of Medicine. On the supportive side, Schwaederle and colleagues’ meta-analysis in JAMA Oncology found biomarker-based treatment strategies associated with better response rates and progression-free survival in refractory malignant neoplasms, and Tsimberidou and colleagues describe molecular tumour boards in Nature Reviews Clinical Oncology as working infrastructure. A defensible summary is that the approach is strongest where the alteration is a strong driver with a matched agent and no alternative treatment exists, and weakest as a general strategy applied across unselected advanced disease. Acknowledging the disagreement is more credible than resolving it through selective citation.

Because of how they are usually conducted and reported, not because stratification is unsound in principle. Three problems recur. The first is multiplicity: the more subgroups examined, the more likely a chance finding, and the number examined is frequently not stated. The second is post hoc specification: a hypothesis generated after the data were seen is a weaker claim than one stated in a protocol, and readers cannot determine which they are reading. The third is the wrong test: reporting that an effect was significant in one subgroup and not another represents two tests of differing power, not evidence of a differential effect; the interaction is the relevant analysis, and trials are rarely powered for it. Sun, Briel, Walter and Guyatt set out credibility criteria in the BMJ, and most published subgroup claims do not meet them.

A prognostic marker is associated with outcome regardless of treatment; it indicates how a patient is likely to fare. A predictive marker is associated with the size or direction of treatment benefit; it indicates whether a given treatment will help a particular patient more than it helps others. The two require different designs: prognosis can be established in a cohort, whereas prediction requires a comparison of treated and untreated patients within each marker stratum, which in practice means a randomised trial with a marker-by-treatment interaction. The conflation of this distinction is one of the most common errors in stratified-medicine manuscripts, and it has clinical consequences: using a prognostic marker to select treatment selects patients on the basis of disease severity, not likely benefit.

It depends heavily on the strategy and the setting, and the syntheses do not support a general answer. Vellekoop and colleagues conducted a systematic literature review and regression analysis of the net benefit of personalised medicine in Value in Health; Kasztura and colleagues conducted a scoping review of cost-effectiveness in the International Journal of Public Health. The pattern across that literature is that favourable cases usually involve avoiding an expensive or harmful treatment in patients who will not benefit, while unfavourable cases involve testing many people to change few decisions. The key quantity for any proposed strategy is the test-to-treat ratio (the number tested to alter one decision), together with the outcomes of the patients the test excludes, since those outcomes form part of the strategy’s effect.

Not yet demonstrably better than current practice, and the limiting factor is comparison rather than computation. Liu and colleagues’ systematic review in The Lancet Digital Health found few studies presenting externally validated, same-sample comparisons (only 14 such comparisons were available for pooling), so the evidence that an algorithmic decision outperforms a clinical one is limited even where accuracy figures are high. For observational data, a further constraint is the big data paradox that Msaouel describes in Cancer Investigation: scale reduces variance but leaves bias intact, so a large dataset yields a precise estimate that may nevertheless be incorrect. Subbiah, in Nature Medicine, frames the realistic path as a synthesis with evidence-based methods rather than a replacement for them.

References

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Pubrica Academy. (2026, October 9). Evidence-Based Medicine and Precision Medicine: A Comparison of Their Limitations. Pubrica. https://pubrica.com/academy/latest-topics/an-overview-of-evidence-based-medicine-vs-precision-medicine-in-comparison-with-their-limitations/

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Stratified-claim audit

This checklist should be applied to any manuscript that claims a subgroup, biomarker or individual-level effect. Its purpose is to make the claim as large as the evidence allows and no larger, which is what enables it to withstand peer review.

STRATIFIED / PRECISION CLAIM AUDIT

1. WHICH QUESTION AM I ANSWERING?
   [ ] Average effect in a defined population
   [ ] Differential effect across strata (effect modification)
   [ ] Differential ABSOLUTE benefit from differing baseline risk
       (note: this is risk stratification, NOT effect modification)
   My strongest supportable claim, one sentence:
   ______________________________________________________

2. PRE-SPECIFICATION
   Subgroup hypotheses pre-specified?      [ ] yes  [ ] no
   Number of subgroups examined in total:  ____
   Direction of expected effect specified? [ ] yes  [ ] no
   Where pre-specified (protocol/SAP, section): ______________
   [ ] Any post hoc subgroup is labelled post hoc in the text

3. THE RIGHT TEST
   [ ] Interaction test reported (not separate within-subgroup tests)
   Interaction estimate and interval: ______________________
   [ ] Trial powered for interaction?  If no, stated in the text [ ]
   [ ] No sentence of the form "significant in A but not in B"
       is used as evidence of a differential effect

4. THE MARKER
   Marker: ______________________
   Assay method: ______________________
   Classification threshold: ______  Fixed before unblinding? [ ]
   Measured identically at all sites/timepoints? [ ] yes [ ] no
   This marker is:  [ ] prognostic  [ ] predictive  [ ] both
     Evidence for predictive status: ______________________

5. CONSISTENCY AND RATIONALE
   Replicated in independent studies? [ ] yes [ ] no [ ] untested
   Independent biological/clinical rationale: ______________
   [ ] Rationale is offered IN ADDITION to, not INSTEAD of, a test

6. IF PROPOSING A STRATIFIED STRATEGY
   Number tested to change one decision (test-to-treat ratio): ____
   What happens to marker-negative patients: ______________
   Their outcomes reported?  [ ] yes  [ ] no
   Cost-effectiveness claim made?  [ ] yes - evidence: ______
                                   [ ] no

7. HOW THE LITERATURE STANDS
   Does the literature disagree on this question?  [ ] yes  [ ] no
     If yes, sources cited on BOTH sides: ______________________
     What evidence would settle it: ______________________

8. CONCLUSION WORDING
   [ ] Conclusion is a design for the next study, not a practice
       recommendation, unless the design supports a recommendation
   [ ] No use of "identifies the patients who benefit" without an
       interaction test and pre-specification
   [ ] Limitations name power, multiplicity and measurement explicitly

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

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