Contents
On this page
- Step 1: Definition of the clinical question and intended use before data collection
- Step 2: Data assembly and documentation of record provenance
- Step 3: Definition of the reference standard and labelling against it
- Step 4: Data partitioning at the boundary where leakage may occur
- Step 5: Model training and documentation of analytical choices
- Step 6: External validation and the expected decline in performance
- Step 7: Calibration and threshold selection as a clinical decision
- Step 8: Attribution methods as debugging tools rather than assurance
- Step 9: Deployment within a monitoring plan
- Key points
- Application to your study
- Frequently asked questions
Academy · Research Data Analytics & AI · Steps in ANN diagnosis
Fundamental Steps in Artificial Neural Network-Based Medical Diagnosis: From Clinical Question to Deployment
A diagnostic neural network is built in a fixed sequence, and most published failures can be traced to a specific step in that sequence rather than to the architecture. This article describes the pipeline (question, data, labels, partitioning, training, validation, calibration and deployment) as an auditable process, identifying the decision that must be recorded at each stage and the consequence of failing to record it.
The architecture of a diagnostic model is the component that papers describe in most detail and that has the least influence on performance. Whether a model performs adequately outside the development setting depends on the decisions taken before and after training: which patients entered the dataset, who produced the labels, where the split boundary was drawn, whether the operating threshold was fixed before the test set was accessed, and whether calibration was assessed. This article presents these decisions in sequence, to support both transparent reporting and the audit of published models.
Learning objectives
- The nine steps in sequence, and the decision that must be recorded at each
- The routes by which data leakage enters a pipeline, of which there are at least five, four of them not apparent in the results
- The reasons a patient-level split is the minimum requirement and a site-level or temporal split is usually necessary
- The required content of an external validation study, according to the BMJ guidance on evaluating prediction models
- The reasons internal validation systematically overestimates performance, and the approximate extent of the overestimation
- The description of a dataset in sufficient detail for a reader to judge transportability rather than accepting “a large cohort” without evidence
Common misconceptions
- “The train/test split constitutes validation.” A random split of one dataset estimates performance on that dataset. Any information learned from site, scanner, period or local case mix is present on both sides of the split, so the estimate reflects reproducibility rather than generalisability.
- “Preprocessing before the split is merely data cleaning.” Normalisation, imputation, feature selection or harmonisation across the whole dataset transfers test-set information into training. Every such step belongs within the resampling loop.
- “Hyperparameters may be tuned on the test set and the best run reported.” Hyperparameters are selected on a validation partition. A test set used more than once ceases to be a test set, and the figure reported from it is a maximum rather than an estimate.
- “Labels constitute ground truth.” Labels are a measurement subject to error, produced by people under defined conditions. The model cannot exceed the reference standard, and label noise is inherited rather than averaged out.
- “Deployment marks the end of the project.” Deployment marks the beginning of the obligation to monitor. Input distributions, case mix and clinician behaviour all change after a model enters use, and the model itself does not report such changes.
Step 1: Definition of the clinical question and intended use before data collection
The first step produces no code. It produces three sentences, which constrain every subsequent step: the clinical decision the model output will inform, current practice in the absence of the model, and the comparator. A model developed to triage a reporting worklist and a model developed to remove studies from human review have different acceptable error profiles, different validation requirements and different sample size requirements, even if the architecture is identical.
At this stage, the prediction time point — the exact moment in the clinical pathway at which the model will run — should be recorded, and only the variables genuinely available at that moment should be listed. This discipline alone prevents the most common structural error in diagnostic modelling, namely training on features recorded after the decision the model is intended to inform.
Our companion page on what artificial neural networks actually do in medical diagnosis addresses the conceptual aspects: what a network is, which roles it can plausibly occupy and what it cannot be made to do. The present page assumes that these questions have been settled and that development is under way.
Step 2: Data assembly and documentation of record provenance
Data assembly is the step most likely to determine the result and least likely to be described adequately. What must be recorded is not the dataset size but its provenance: the sources and sites, the date range, whether sampling was consecutive or selected, the inclusion and exclusion criteria with a count at each step, and the case mix by age, sex, disease stage and acquisition device. A reader cannot judge whether the model will transfer to another population without this information, and an “N = 14,000 multicentre cohort” on its own conveys nothing beyond scale.
Two assembly decisions require particular attention. The first is enrichment. A case–control sample with a deliberately raised proportion of cases is efficient for training but changes every prevalence-dependent metric, so it cannot be used to estimate performance in a screening population without explicit recalibration. The second is multi-site heterogeneity, which is usually treated as a nuisance to be removed but is in fact the property that makes the model portable. Dinsdale and colleagues, in NeuroImage, demonstrated a deep learning approach to unlearning dataset bias for MRI harmonisation and confound removal. The approach is useful, but its implication should be noted: if scanner identity must be actively unlearned, it was learnable, and an unharmonised pipeline would have learned it 26.
Preprocessing belongs to this step only in the sense that it is planned here. Zhang and colleagues, in Diagnostics, describe informative frame selection for video-derived data, and Pinckaers and colleagues, in IEEE Transactions on Pattern Analysis and Machine Intelligence, address the different problem of training end-to-end on multi-megapixel images that will not fit in memory 14,33. Both are legitimate pipeline components, and both must be fitted within the training partition only.
The same dataset, described two ways
Unauditable
The model was developed using a large multicentre cohort of retrospectively collected imaging studies with confirmed diagnoses, which was randomly divided into training, validation and test sets.
How large, and from where? “Large multicentre” cannot be compared with any other study or transferred to any population.
Who was left out? Without exclusion counts, selection bias cannot be assessed, and exclusions are where it most often arises.
What counted as a confirmed diagnosis? The reference standard sets the upper limit of model performance, and it is not stated.
What was the prevalence? Without it, every accuracy, predictive value and calibration claim is uninterpretable.
Randomly divided at what level? If the split was at image level, the performance figures are invalid; the sentence does not specify the level.
Auditable
Studies were drawn consecutively from three hospitals between January 2017 and December 2020. Of [n] studies screened, [n] were excluded for incomplete acquisition, [n] for absent reference-standard confirmation and [n] for prior treatment, leaving [n] studies from [n] patients. Cases were confirmed by biopsy; non-cases required at least twelve months of imaging follow-up. Case mix by age, sex, disease stage, scanner vendor and site is given in Table 1, together with disease prevalence overall and separately for each of the three sites. Splitting was at patient level, with the third hospital held out entirely as an external set and the remaining two split temporally rather than at random.
Provenance and date range allow readers to judge whether the equipment and practice resemble their own.
The exclusion cascade makes selection bias visible and quantifiable rather than concealed.
The reference standard is named for cases and for non-cases, including the follow-up rule that defines a true negative.
Prevalence is given overall and by site, so prevalence-dependent metrics can be recalculated for another setting. The bracketed counts are placeholders for the study’s own cascade; the structure, not these figures, is the point.
The split is at patient level, with one site held out and the remainder split temporally, so the paper tests transportability rather than reproducibility.
The second version is six sentences and one table reference longer. It converts a claim that must be taken on trust into one that a reader can check, recalculate for another population and reject on specific grounds. It also fixes the dataset description in a form that can be reused verbatim in the validation paper, the regulatory file and any later meta-analysis, none of which can use the first version.
Step 3: Definition of the reference standard and labelling against it
The quality of the labels sets the upper limit of model performance, so the labelling protocol is a methods subsection, not a footnote. Authors should record who labelled the data, their expertise, how many labellers assessed each case, the adjudication rule for disagreement, whether labellers were blinded to other information, and the measured agreement between them. Where inter-rater agreement is poor, the model’s apparent error includes the raters’ disagreement, and the reported performance has an upper bound that no amount of training can raise.
The annotation granularity is a design decision with costs and consequences. Sirinukunwattana and colleagues, in Medical Image Analysis, describe the GlaS gland segmentation challenge, in which pixel-level annotation constitutes the costly part of the work and comparability between entrants depends entirely on it; Graham and colleagues’ HoVer-Net, in the same journal, performs simultaneous nuclear segmentation and classification, which requires annotation at a finer level still 35,44. At the other extreme, Lu and colleagues, in Nature Biomedical Engineering, show data-efficient and weakly supervised approaches that learn from slide-level labels alone, and Krishnan and colleagues, in the same journal, review self-supervised learning, which reduces the labelled requirement by learning representations from unlabelled data first 23,25.
Each of these choices changes the claims for which the model can be held accountable. A slide-level model trained on weak labels should not be reported with lesion-level claims, and a model trained on labels derived from a downstream outcome — as in Kim and colleagues’ preoperative CT model for disease-free survival in Radiology, or Gamble and colleagues’ work on biomarker status in Communications Medicine — is predicting that outcome, not reproducing a diagnosis 27,32.
Step 4: Data partitioning at the boundary where leakage may occur
Splitting is an arithmetic operation that encodes an assumption, and an incorrect split invalidates the result without any visible sign. The minimum requirement is a patient-level split: every image, slide, frame or episode from one patient falls entirely on one side. A split at the image level, in which two slices of the same study are assigned to the training and test sets, produces performance figures that are close to meaningless, yet such splits are still regularly published.
Beyond this, the split should break whatever dimension the model is claimed to generalise across. If the claim is that the model works at other hospitals, a hospital should be held out. If the claim is that it will work in future, a time period should be held out — a temporal split, which also detects drift in practice patterns and equipment. If the claim is that it works on a different scanner, a scanner should be held out. A random split breaks none of these dimensions and therefore tests none of them.
Leakage commonly enters by five routes, which merit particular attention because four of them leave no trace in the results: splitting below patient level; fitting any preprocessing, normalisation, imputation or harmonisation step on the full dataset; selecting features using the whole dataset before splitting; choosing hyperparameters or an operating threshold on the test set; and including a variable that encodes the outcome or the clinical response to it 22. The table below sets out where each enters and what it does to the reported figure.
Where leakage enters the pipeline, and what it does to the reported figure
| Route | Step it enters at | Effect on reported performance | Visible in the results? |
|---|---|---|---|
| Split below patient level slices or frames of one study on both sides | Splitting | Large upward bias; the model partly recognises the patient | No — only in the methods, if the unit of splitting is stated |
| Preprocessing fitted on all data normalisation, imputation, harmonisation | Assembly / preprocessing | Modest to large upward bias depending on the statistic used | No |
| Feature selection before splitting | Assembly | Upward bias, worst where features greatly outnumber cases | No |
| Tuning or thresholding on the test set | Training / calibration | Reported figure becomes a maximum rather than an estimate | No — unless the number of configurations tried is reported |
| Outcome-adjacent variable included records the decision the model should inform | Question framing | Very large upward bias; performance collapses on deployment | Sometimes, as implausibly high performance |
| Random instead of site or temporal split | Splitting | No bias for the dataset; overstates transportability | No |
Routes compiled from the pipeline requirements set out by Collins and colleagues and Riley and colleagues in BMJ on developing and externally validating clinical prediction models, and from the harmonisation and confound-removal problem described by Dinsdale and colleagues in NeuroImage. The magnitudes are directional, not quantitative; no effect sizes are implied.
Step 5: Model training and documentation of analytical choices
Papers commonly over-report and under-document the training step simultaneously. A reader requires reproducible detail: the architecture and its source, whether weights were initialised from a pretrained model and from which dataset, the loss function and any class weighting, the optimiser and learning rate schedule, the augmentation applied, the stopping criterion, and — the item most often missing — the number of configurations tried and the partition on which they were compared.
Transfer learning warrants an explicit statement rather than a passing mention. Abu and colleagues, in Diagnostics, analysed transfer learning optimisation for visual field defect classification and showed the extent to which the result depends on which layers are frozen, which are fine-tuned and how the learning rate is scheduled — decisions that form part of the method rather than implementation detail 17. Where a pretrained backbone is used, the pretraining dataset becomes part of the data provenance.
Hyperparameter selection is governed by one rule: it takes place on a validation partition derived from the training data, never on the test set. If computational constraints necessitated repeated use of a single held-out set, this should be stated and the reported figure described as optimistic. Nuvoli and colleagues, in Diagnostics, illustrate the corresponding good practice in a small-data setting, comparing automated classifiers for differentiating Alzheimer disease from mild cognitive impairment on FDG PET/CT with the comparison specified rather than discovered; Ding and colleagues’ deep learning model for Alzheimer diagnosis on FDG PET in Radiology provides a useful contrast in scale 20,39.
Step 6: External validation and the expected decline in performance
Internal validation estimates how well the model reproduces its own dataset. It overstates performance for structural reasons rather than through malpractice: the model has been fitted to the idiosyncrasies of that data source, every shortcut available in training is available in the held-out split, and the analyst’s decisions were informed by inspection of the data. The question is not whether internal validation is optimistic but to what extent, and that cannot be answered from within the dataset.
Collins and colleagues, in BMJ, set out the path from development to external validation for clinical prediction models, and Riley and colleagues, in the companion BMJ paper, specify how to undertake an external validation study 10,11. Read together, they specify the content that a credible validation requires: a population defined independently of the development data, with its own case mix and prevalence described; a pre-specified analysis; discrimination and calibration both reported, with calibration slope and intercept rather than a visual impression; sufficient sample size in the validation set to estimate performance precisely, a calculation that most papers omit entirely; and performance reported by subgroup rather than pooled only 10,11.
External validation is also where the principal reporting problems of the field are concentrated. Liu and colleagues, in The Lancet Digital Health, could pool deep learning performance against health-care professionals only for the handful of studies that had tested both on identical samples; pooled sensitivity was 87.0% and pooled specificity 92.5% in that subset. The far larger remainder of the literature did not meet that condition 34. For the appropriate synthesis of such studies, as opposed to simple averaging, see Pubrica’s pages on the meta-analysis of convolutional networks in radiology and the cardiac imaging AI meta-analysis, and the wider AI in medical imaging hub.
Pooled estimates restricted to studies that evaluated algorithms and health-care professionals on identical samples; the wider literature did not meet that condition. Source: Liu X, Faes L, Kale AU, et al. A comparison of deep learning performance against health-care professionals in detecting diseases from medical imaging: a systematic review and meta-analysis. The Lancet Digital Health.
Step 7: Calibration and threshold selection as a clinical decision
Discrimination and calibration are different properties and a model can have one without the other. Discrimination asks whether the model ranks patients correctly; calibration asks whether a predicted probability of 0.2 corresponds to about a one-in-five chance in reality. Almost all clinical use of a model occurs at a threshold, and at a threshold it is calibration that determines whether the output is meaningful. A model with an excellent area under the curve but a calibration slope far from one will systematically over- or under-treat at every operating point.
The calibration plot should be reported with slope and intercept, and the model should be recalibrated rather than retrained when it is transferred to a population with different prevalence 11. The threshold should then be treated as a decision about the relative cost of a false negative and a false positive in the specific intended use. The assumed costs should be stated, the threshold fixed before the test set is accessed, and performance reported at that threshold rather than at the threshold that appeared best afterwards. Where the intended use is rule-out, the tolerance analysis for missed cases also belongs in this step.
Step 8: Attribution methods as debugging tools rather than assurance
Attribution methods have a legitimate and limited role in this pipeline. Bach and colleagues, in PLOS ONE, introduced layer-wise relevance propagation as a pixel-wise explanation of non-linear classifier decisions; Eitel and colleagues, in NeuroImage: Clinical, applied it to convolutional networks diagnosing multiple sclerosis on conventional MRI, and Böhle and colleagues, in Frontiers in Aging Neuroscience, to MRI-based Alzheimer classification 36,38,45. Faust and colleagues, in BMC Bioinformatics, took a different route, using non-linear dimensionality reduction of the feature space to visualise histopathologic classification and detect anomalies 42.
These methods provide a debugging instrument. If the relevance concentrates on a text marker, an image border, a support device or the background, a shortcut has been identified, and the finding is actionable. They do not, however, provide assurance: a model exploiting an artefact can still produce a plausible map over the lesion, and no attribution method establishes that the features used are clinically valid 13. They should be used to look for problems, and the findings should be reported. They should not be presented as evidence that the model is trustworthy; that case is made by the validation design.
Step 9: Deployment within a monitoring plan
Most published diagnostic models never reach prospective evaluation, and the gap between a validated model and a deployed one constitutes a project in itself. Before deployment, three elements should exist in writing: a prospective evaluation design appropriate to the intended use, a monitoring plan, and a stopping rule.
Monitoring involves tracking the input distribution as well as the output — case mix, acquisition devices, missing-data rates, and the proportion of inputs unlike any the model has previously encountered — because the model will not report that its population has changed. It also involves monitoring human factors: clinicians adapt to a model’s outputs, which changes the data the model subsequently receives and can invalidate the original validation without obvious signs. The degree of drift that triggers recalibration, revalidation or withdrawal, and the person responsible for acting on it, should be defined in advance.
Where the model is intended as a regulated product, the evidentiary and change-control requirements constitute a separate subject, addressed on the page on causal inference and the regulation of machine-learning tools. For the statistical side of the pipeline — validation sample size, calibration analysis, subgroup reporting — see the biostatistics role hub and statistical review.
Key points
Key points
The pipeline, rather than the architecture, determines whether a diagnostic model performs adequately at a second hospital. The clinical question, the prediction time point and the intended use should be defined before data are accessed; provenance, exclusions, case mix and prevalence should be recorded; labels should be treated as a measurement subject to error, with their source stated; data should be split at patient level and across every dimension over which generalisation is claimed; every preprocessing step should be fitted within the training partition only; external validation should follow the guidance of Collins and Riley in BMJ, with calibration reported as well as discrimination; the threshold should be fixed before the test set is accessed; and deployment should occur only within a monitoring plan that includes a stopping rule. Each step involves one decision that must be documented, and this documentation is what makes the model auditable.
Application to your study
Application to your study
- Write the three framing sentences first. These sentences should state the decision the output informs, the situation without the model, and the comparator. Only the variables available at that prediction time point should then be listed.
- Construct the exclusion cascade before any modelling, with a count at every step. Reviewers commonly request this figure, and it is the most difficult to reconstruct retrospectively.
- Write the labelling protocol as a methods subsection. The protocol should state who labelled the data, the number of labellers per case, the adjudication rule, blinding and measured agreement. Without a measure of agreement, the error estimate includes inter-rater disagreement.
- Set the split boundary according to the intended claim. A claim of generalisation to another hospital requires a hospital to be held out; a claim of generalisation to a later period requires a time period to be held out. Random splitting tests neither.
- Place every preprocessing step within the resampling loop, including normalisation, imputation, harmonisation and feature selection. A decline in performance on re-analysis indicates the extent of the previous leakage.
- Record the number of configurations tested and the partition on which each was evaluated. If the test set was used more than once, the reported figure should be described as optimistic in the main text as well as in the limitations.
- Produce a calibration plot with slope and intercept in addition to an ROC (receiver operating characteristic) curve, and recalibrate rather than retrain when prevalence changes.
- Fix the operating threshold before the test set is accessed and state the assumed relative costs of a false negative and a false positive on which the choice was based.
- Prepare the monitoring plan before claiming readiness for deployment. The plan should specify what is monitored, the degree of drift that triggers action, who is responsible for acting, and the conditions under which the model is withdrawn.
Frequently asked questions
In order: define the clinical question, prediction time point and intended use; assemble the data and record provenance, exclusions, case mix and prevalence; define the reference standard and label against it with measured agreement; split at patient level and across every dimension over which generalisation is claimed; train, documenting architecture, pretraining source, loss, augmentation and the number of configurations tried; validate externally with both discrimination and calibration; calibrate and then fix an operating threshold as a clinical cost decision; use attribution methods for debugging rather than assurance; and deploy only within a monitoring plan with a stopping rule. Each step involves one decision that must be documented, and the documentation is what makes the model auditable.
Leakage is any route by which information from the test set, or from the outcome, reaches the model during training. There are five common routes: splitting below patient level, so slices or frames of one study fall on both sides; fitting normalisation, imputation or harmonisation on the whole dataset; selecting features before splitting; tuning hyperparameters or the operating threshold on the test set; and including a variable that records the clinical response to the outcome. Four of these are not apparent in the results, so they cannot be detected by inspecting performance. The only reliable check is to re-read the pipeline code for the order of operations, move every fitted step inside the resampling loop, and determine whether performance falls.
Because internal validation measures something narrower than most readers assume. The model has been fitted to one data source, including features of that source — scanner, protocol, local case mix, practice era — that are present in the held-out split as well, so they inflate both. The analyst’s choices were also informed by inspection of that data. Collins and colleagues and Riley and colleagues, in their paired BMJ papers on evaluating prediction models, treat this as structural rather than as a flaw to be fixed: the realistic expectation is that performance will fall in a genuinely independent population, and the purpose of the external study is to determine by how much and to recalibrate accordingly.
At patient level as an absolute minimum — every image, slide, frame or episode from one patient on one side only. Beyond that, the split should follow every dimension across which generalisation is claimed. If the claim is that the model works at other hospitals, a hospital should be held out entirely. If the claim is that it will work prospectively, the split should be temporal, which also detects drift in equipment and practice. If the claim concerns a different scanner or assay, that scanner or assay should be held out. A random split breaks none of these dimensions, so it estimates reproducibility within the dataset rather than transportability, and should be described as such in the paper.
Discrimination asks whether the model ranks patients in the correct order and is usually summarised by the area under the ROC curve. Calibration asks whether the predicted probabilities are numerically accurate — whether a prediction of 0.2 corresponds to approximately a one-in-five chance in that population. Clinical use nearly always occurs at a threshold, and at a threshold it is calibration that determines whether the output supports the decision. A model can discriminate well and still systematically over- or under-treat at every operating point. The calibration plot should be reported with slope and intercept, and the model recalibrated rather than retrained when it is transferred to a population with different prevalence.
It depends on the claims to be made. Pixel-level annotation of the kind used in the GlaS challenge described by Sirinukunwattana and colleagues, or required by Graham and colleagues’ HoVer-Net for simultaneous nuclear segmentation and classification, supports localisation claims and is expensive. Lu and colleagues, in Nature Biomedical Engineering, show data-efficient weakly supervised approaches learning from slide-level labels, and Krishnan and colleagues review self-supervised pretraining that reduces the labelled requirement further. The rule is that the claim must match the label granularity: a model trained on slide-level labels should not be reported with lesion-level performance, however convincing its attribution maps appear.
This is a calculation rather than a convention, and it is the step most commonly omitted. The requirement depends on the number of events rather than the number of records, on the precision required in estimating calibration as well as discrimination, and on whether subgroup performance is to be reported, which multiplies the requirement. Riley and colleagues’ BMJ paper on undertaking an external validation study sets out the approach. The common practice of holding out a fixed percentage, reporting a point estimate with wide confidence intervals and discussing it as though it were precise should be avoided. If the validation set is small, this should be stated and the interval presented prominently.
No. Attribution methods such as the layer-wise relevance propagation introduced by Bach and colleagues in PLOS ONE, and applied to MRI by Eitel and colleagues and by Böhle and colleagues, show where the output is most sensitive to changes in the input. A model exploiting an acquisition artefact or a support device can still produce a plausible map over the lesion. Their principal value is diagnostic: if relevance concentrates on a text marker, an image border or the background, a shortcut has been identified and should be reported. Assurance derives from external validation, subgroup performance and monitoring, not from visualisation.
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Pubrica Academy (2026) Fundamental Steps in Artificial Neural Network-Based Medical Diagnosis: From Clinical Question to Deployment. Pubrica. Available at: https://pubrica.com/academy/medical-writing/fundamental-steps-in-artificial-neural-networks-based-medical-diagnosis/ (Accessed: 15 October 2026).
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@misc{fundamental_steps_in_artificial_neural_2026,
author = {{Pubrica Academy}},
title = {Fundamental Steps in Artificial Neural Network-Based Medical Diagnosis: From Clinical Question to Deployment},
howpublished = {Pubrica},
year = {2026},
month = {oct},
url = {https://pubrica.com/academy/medical-writing/fundamental-steps-in-artificial-neural-networks-based-medical-diagnosis/},
note = {Accessed: <span data-cite-acc="iso">2026-10-15</span>}
}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.
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DIAGNOSTIC MODEL -- PIPELINE RECORD
Model / project: ______________________ Version: ______ Date: ________
1. QUESTION AND INTENDED USE
Clinical decision the output feeds: ________________________________
Current pathway without the model: ________________________________
Comparator: _______________________________________________________
Prediction time point: ____________________________________________
Variables available at that time point only? yes / no
2. DATA PROVENANCE
Sources and sites: ________________________________________________
Date range: __________________ Consecutive / selected: __________
Screened: ______ Excluded: ______ (reasons and counts below)
______________________________________ n = ______
______________________________________ n = ______
Final: ______ studies from ______ patients
Prevalence overall: ______% Range across sites: ______ to ______%
Case mix table prepared? yes / no
Enriched or case-control sampling? yes / no
3. REFERENCE STANDARD AND LABELS
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Definition of a non-case (incl. follow-up rule): __________________
Labellers: ______ Expertise: ______________ Per case: ______
Adjudication rule: ________________________________________________
Blinded to model output and to each other? yes / no
Measured agreement: ______________________
Label granularity: pixel / region / slide / patient / outcome-derived
4. SPLITTING
Unit of splitting: patient / study / image (patient = minimum)
Design: random / temporal / site-held-out / scanner-held-out
Dimension the paper claims generalisation across: _________________
Does the split break that dimension? yes / no
5. LEAKAGE AUDIT
[ ] No patient appears on both sides
[ ] Normalisation fitted inside training partition only
[ ] Imputation fitted inside training partition only
[ ] Harmonisation fitted inside training partition only
[ ] Feature selection inside training partition only
[ ] No outcome-adjacent variable included
[ ] Test set opened once
6. TRAINING
Architecture and source: __________________________________________
Pretrained weights from: __________________________________________
Loss / class weighting: ___________________________________________
Augmentation: _____________________________________________________
Optimiser and schedule: ___________________________________________
Stopping criterion: _______________________________________________
Configurations tried: ______ Compared on: training-validation split
7. VALIDATION
Internal: random / temporal Sample size justified? yes / no
External: site ______ / scanner ______ / population ______
Discrimination (with CI): _________________________________________
Calibration slope: ________ Intercept: ________ Plot? yes / no
Subgroup performance reported: ____________________________________
8. THRESHOLD
Fixed before test set opened? yes / no
Assumed cost ratio, false negative : false positive: ______ : ______
Threshold: ________ Sensitivity: ______ Specificity: ______
Rule-out use? If so, tolerance analysis for missed cases: yes / no
9. ATTRIBUTION / DEBUGGING
Method used: ______________________________________________________
Shortcuts found: __________________________________________________
Masking or lesion-removal test performed? yes / no
10. DEPLOYMENT AND MONITORING
Prospective evaluation design: ____________________________________
Inputs monitored: _________________________________________________
Drift threshold triggering recalibration: _________________________
Owner of the monitoring plan: _____________________________________
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