Artificial Neural Networks in Medical Diagnosis: Function, Evidence and Limitations

Most papers describing a diagnostic neural network report a single accuracy figure from a held-out split of the dataset on which the network was trained, and most readers treat that figure as a property of the model. It is instead a joint property of the model, the dataset, the reference standard and the split, and it almost always declines when any one of these changes. This article describes what a network is, where it fits in a diagnostic pathway, what the comparative evidence does and does not establish, and which claims warrant scepticism.

Definition of an artificial neural network

In essence, an artificial neural network is a long chain of weighted sums passed through simple non-linear functions, with the weights chosen numerically so that the outputs match a set of labelled training examples as closely as a chosen loss function allows. Amato and colleagues, in the Journal of Applied Biomedicine, described the architecture in precisely these terms before the deep learning era, and subsequent developments have not altered that description; only the depth of the networks, the volume of data and the available hardware have changed 43.

Two consequences follow from this definition, and they govern the remainder of this page.

First, the network has learned a mapping from inputs to labels, not a theory of the disease. It has no representation of pathophysiology, cannot be interrogated about a differential diagnosis, and cannot distinguish a feature that causes the label from one that is merely associated with it in the training data. Second, the mapping is meaningfully defined only over the distribution to which it was fitted. Nothing in the computation signals that an input differs from the training data; the network returns an apparently confident value regardless. Both are properties of the method rather than defects of a particular implementation, and additional data do not remove them.

The construction pipeline, as distinct from the concept (how the data are assembled, labelled, split, trained, validated and calibrated), is the subject of the companion page on the fundamental steps in neural-network-based diagnosis. The present page addresses what a neural network is and where it belongs in the diagnostic pathway.

Common network architectures and their inputs

Diagnostic papers use a small number of recurring designs, and identifying the design indicates what the input was and therefore what could have leaked into it. Zacharia and colleagues, in the proceedings of the first International Electronic Conference on Chemical Sensors and Analytical Chemistry, and Kamal and colleagues, in their review of deep learning for medical image analysis, both survey the same families 12,22.

The distinction most important for appraisal is between classification (one label per image or per patient), detection (a label plus a location, as in Mao and colleagues’ work in Diagnostics on locating endotracheal tubes and the carina on supine chest radiographs) and segmentation (a label per pixel, surveyed by Huang and colleagues in Diagnostics) 17,19. These tasks are not interchangeable and do not share evaluation metrics. A segmentation network reported with a classification accuracy figure has been assessed against an inappropriate criterion.

Whole-slide pathology merits particular mention because the input is too large to be processed directly. Campanella and colleagues, in Nature Medicine, showed that clinical-grade performance was achievable with weak supervision at the slide level rather than exhaustive pixel annotation, which alters both the labelling cost and the failure modes 33.

Position of a network in the diagnostic pathway

“Diagnosis” is not a single task, and a network cannot be evaluated until its task has been specified. The plausible roles are narrow, and each implies a different acceptable error profile.

• Triage or pre-read: reordering a worklist so that studies likely to be abnormal are reviewed first. Errors cost time rather than diagnoses, provided that nothing is removed from the queue.
• Rule-out: removing studies from human review. This requires very high sensitivity and a tolerance analysis for the cases that will be missed, because by design no one reviews them again.
• Second reader: providing an independent opinion alongside a clinician. Here the relevant question is not the accuracy of the model but that of the combined clinician-and-model system, which is a different measurement.
• Quantification: measuring a quantity that humans measure poorly or slowly, such as a volume, a count or an ordinal grade.

De Fauw and colleagues, in Nature Medicine, provide a useful example of a stated role: their retinal optical coherence tomography (OCT) system was built to produce a referral decision, with the clinical pathway specified in advance, rather than a disease label in the abstract 38. A statement of the role before evaluation is the most informative sentence in a diagnostic AI paper, and it is the sentence most often absent. Topol’s review in Nature Medicine makes the same point across specialties: the principal constraint in this field has not been model performance but the absence of a defined decision that the model is intended to support 35.

Comparative evidence against clinicians

The most frequently cited synthesis in this area is the systematic review and meta-analysis by Liu and colleagues in The Lancet Digital Health, comparing deep learning with health-care professionals in detecting disease from medical imaging. Its most important result is not a performance figure but a restriction: of the entire literature screened, only 14 studies had compared an algorithm and clinicians on the same sample. Within those 14, pooled sensitivity was 87.0% for deep learning against 86.4% for the health-care professionals, and pooled specificity 92.5% against 90.5% 32. Interpreted carefully, this is a finding of approximate equivalence in the best-designed subset of studies, and a criticism of the remainder, which compared the performance of an algorithm on one dataset with the performance of clinicians reported elsewhere 32.

Well-designed studies can produce strong results. Bulten and colleagues, in Nature Medicine, conducted the PANDA challenge with 1,290 developers and 10,616 digitised prostate biopsies, and then tested the leading algorithms on independent cohorts 16. Agreement with expert uropathologists reached a quadratically weighted kappa of 0.862 (95% CI 0.840–0.884) on the US external validation set and 0.868 (95% CI 0.835–0.900) on the European one 16. The credibility of this result derives from independent external cohorts, an expert reference standard and an agreement statistic suited to an ordinal grade rather than a bare accuracy figure 16.

In contrast, Nagendran and colleagues, in BMJ, reviewed the design and reporting of deep learning studies making clinician-comparable claims and found that methodological and reporting standards were weak and that the claims were routinely stronger than the designs could support 26. Fleuren and colleagues, in Intensive Care Medicine, reached a related conclusion for machine learning prediction of sepsis: substantial heterogeneity between studies in definitions, prediction windows and reference standards, which makes pooled estimates difficult to interpret and cross-study comparison largely uninformative 31. A fair summary of the field is that the best studies show parity with clinicians on narrow tasks, and that most studies are not among the best.

Shortcut learning: correct outputs for incorrect reasons

A network minimises training loss by any available route, including routes unrelated to the disease. DeGrave and colleagues, in Nature Machine Intelligence, demonstrated this directly for radiographic COVID-19 detection: models trained on assembled public datasets achieved strong apparent performance while relying on acquisition-related features and dataset provenance rather than lung pathology 21. The networks were not malfunctioning. They were solving the problem they had in fact been given, which was to distinguish one source dataset from another.

This failure mode cannot be detected by internal validation, because the shortcut is also present in the held-out split. It can be detected by three methods, and a paper that has applied none of them has not examined the possibility: external validation on data from a different site and scanner; a deliberate test on inputs with the lesion removed or masked, to determine whether performance is maintained; and a case mix table sufficiently detailed to show whether cases and controls differ in any respect other than the disease.

Shortcut learning is also the main reason that internal validation overstates performance so consistently. The same reasoning applies to imaging AI generally; the Academy AI in medical imaging hub and the meta-analysis of convolutional networks in radiology describe how such studies can be pooled without inheriting their optimism.

Distinction between diagnostic accuracy and clinical impact

A diagnostic network changes patient care indirectly, through a clinician or a pathway, and whether it does so is an empirical question that accuracy cannot answer. Three study designs in the reference list below illustrate the difference.

Kiani and colleagues, in npj Digital Medicine, tested a deep learning assistant for histopathologic classification of liver cancer and reported the effect on pathologists’ accuracy when the assistant was available, including cases in which the model’s error propagated into the human decision 28. This is an interaction effect, and it cannot be inferred from the standalone performance of the model. McKinney and colleagues, in Nature, evaluated a breast screening system across two national datasets and simulated reader workflows, which approaches the operational question more closely but is still not a prospective evaluation 29. Lin and colleagues, in EClinicalMedicine, went furthest: a multicentre randomised controlled trial of an AI platform for childhood cataracts in eye clinics, assessing both diagnostic efficacy and therapeutic decision-making 34.

Randomised and prospective evaluations of diagnostic networks remain rare. Most published models never undergo one, which means that the central claim of the field, that these tools improve care, rests on considerably less evidence than its accuracy literature suggests. Authors describing a model should state at which of these three levels their evidence lies, and those appraising a model should establish it.

Reporting a diagnostic network for critical appraisal

Hernandez-Boussard and colleagues, in the Journal of the American Medical Informatics Association, proposed MINIMAR as a minimum information set for medical AI reporting because papers in the field were omitting information that readers require: the source population, the cohort characteristics, how the model was built and how it is intended to be used 30. The underlying problem is that an accuracy figure is compact, impressive and almost uninterpretable on its own, whereas the information that makes it interpretable is unremarkable and requires four additional sentences.

Those four sentences should be written in full, because the difference between the two versions below is not one of writing quality but of whether a reviewer can determine what was measured.

Inherent limitations of neural networks

Some limitations are not engineering problems awaiting a solution, and they should be stated explicitly in the discussion section rather than left for a reviewer to raise.

A network has no out-of-distribution guarantee. It will produce an output for an input from a scanner, a population or a disease stage that it has never encountered, and that output carries the same apparent confidence as any other. It has no causal content: it predicts the label, so if treatment decisions in the training data depended on features visible to the network, it has learned clinicians’ behaviour as much as the biology, a problem examined in detail in why prediction is not causation. It also inherits every property of its labels: the CAMELYON16 analysis by Bejnordi and colleagues in JAMA is instructive in this respect, because the reference standard against which the algorithms were scored was itself produced by pathologists working under defined conditions 41.

Interpretability does not resolve these limitations. Durán and Jongsma, in the Journal of Medical Ethics, argue that the question of whether to trust a medical algorithm is settled not by opening the black box but by the epistemic and ethical grounds for relying on its outputs, which derive from validation design rather than from visualisation 23. Coudray and colleagues, in Nature Medicine, showed that networks trained on lung histopathology could predict mutation status from morphology; this is a notable result concerning the information that images contain, but it does not constitute an explanation 37.

Kelly and colleagues, in BMC Medicine, set out the practical consequence: the barriers to clinical impact from AI are predominantly matters of evaluation, integration and monitoring rather than model performance. A candid account of limitations does not weaken a paper; it is the section that reviewers in this field are now trained to examine.

Key points

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Frequently asked questions

@misc{overview_of_artificial_neural_network__2026,
  author       = {{Pubrica Academy}},
  title        = {Artificial Neural Networks in Medical Diagnosis: Function, Evidence and Limitations},
  howpublished = {Pubrica},
  year         = {2026},
  month        = {oct},
  url          = {https://pubrica.com/academy/medical-writing/overview-of-artificial-neural-network-in-medical-diagnosis/},
  note         = {Accessed: <span data-cite-acc="iso">2026-10-15</span>}
}

DIAGNOSTIC NEURAL NETWORK -- APPRAISAL SHEET
Paper / manuscript: ______________________________

1. INTENDED USE
   [ ] Named role: triage / rule-out / second reader / quantification / other
   [ ] The clinical decision it feeds is stated
   [ ] The comparator is the current pathway, not an abstract baseline
   Acceptable error profile for that role: ______________________

2. DATA PROVENANCE
   [ ] Sources, sites and date range given
   [ ] Consecutive or selected sampling stated
   [ ] Inclusions and exclusions listed with numbers at each step
   [ ] Case mix table present (age, sex, site, scanner, disease stage)
   [ ] Prevalence in each evaluation set stated

3. REFERENCE STANDARD
   [ ] What counted as the truth, and who produced it
   [ ] Number of labellers and their expertise
   [ ] Agreement between labellers reported
   [ ] Labellers blinded to the model output

4. VALIDATION DESIGN            (circle one)
       internal random split  /  internal temporal  /  external  /  prospective
   [ ] External set differs in site AND scanner or assay
   [ ] Validation sample size justified, not just "held out"

5. METRICS
   [ ] Metric matches the task (segmentation NOT scored as accuracy)
   [ ] Discrimination with confidence intervals
   [ ] Calibration plot, with slope and intercept
   [ ] Operating threshold fixed BEFORE testing -- stated in methods
   [ ] Performance reported by subgroup, not pooled only

6. SHORTCUT CHECKS
   [ ] Anything other than disease that differs between cases and controls
   [ ] Masking or lesion-removal test performed
   [ ] Performance on data from a different acquisition source

7. CLINICIAN COMPARISON  (if claimed)
   [ ] Same sample, same time, readers blinded to model output
   [ ] Reader experience and number stated
   [ ] Clinician-plus-model measured, not only model alone

8. CLINICAL IMPACT
   [ ] Any patient outcome measured?  yes / no
   [ ] If no: stated in the discussion that clinical effect is unknown

9. FAILURE AND MONITORING
   [ ] Error analysis on the misclassified cases
   [ ] What happens when input is out of distribution
   [ ] Drift monitoring plan if deployment is proposed

10. CLAIMS
   [ ] Abstract conclusion does not exceed the validation design
   [ ] Limitations name case mix, external validity and labelling
   [ ] No comparator performance borrowed from another study