Clinicians routinely evaluate clinical trials by asking whether the study population resembles their patients, whether the endpoint is clinically meaningful, whether the comparator is appropriate, and whether the confidence intervals support the conclusions.

An artificial-intelligence (AI) study deserves the same scrutiny, plus a few additional questions. AI models can appear impressive on paper while ultimately failing because of biased labels, data leakage, narrow patient populations, unstable performance, or workflows that are not clinically realistic.

Reviewing an AI paper does not require expertise in data science. The following eight questions provide a practical framework for evaluating AI studies.

1. Is this a real clinical problem, and does AI add anything useful? Begin by considering the model architecture, the AUC, or the heatmap. A clinically useful AI study should clearly define its intended use: Which patients is the model designed for? At what point in the care pathway will it be used? What data does it rely on? Which clinical decision is it intended to support?

Consider a model designed to identify hypothyroidism from demographic and laboratory data while excluding thyroid-stimulating hormone (TSH). That may be reasonable as a population-screening or pre-laboratory triage tool in a setting where TSH is unavailable or underused. However, if TSH testing is already routinely available in the intended practice setting, the model should demonstrate a meaningful advantage over simply measuring TSH.

Reviewers should also ask whether the study contributes something genuinely new. A new convolutional neural network architecture that predicts thyroid malignancy is not, by itself, a novel clinical contribution. The paper should show at least one of the following: 

• A clinically important new use case. 

• A better or more representative dataset. 

• A meaningful comparison against standard care. 

• Improved external performance. 

• Better calibration or clinical utility. 

• Evidence that the model changes a decision or outcome. 

The first question is not, “Can AI predict this?” It is, “Should we use AI for this problem at all?” 

2. Does the population resemble the patients and practice setting where the model would be used? Every model reflects the data on which it was trained.

A thyroid nodule classifier trained exclusively on images from a tertiary referral center may have seen a high malignancy prevalence, advanced ultrasound equipment, expert sonographers, and a pathology-enriched population. Its performance may fall substantially when used in a community endocrine clinic, where disease prevalence, image quality, referral patterns, and operator experience differ. 

Reviewers should look for: 

• Data source and participating sites. 

• Recruitment dates and length of the study period. 

• Inclusion and exclusion criteria. 

• Patient demographics and disease prevalence. 

• Disease severity and case mix. 

• Imaging platforms, laboratory assays, or electronic health record systems. 

• Missing-data patterns. 

• The unit of analysis: image, lesion, nodule, encounter, or patient. 

For endocrine imaging studies, the unit of analysis matters greatly. A dataset may contain multiple ultrasound images from the same thyroid nodule, multiple nodules from the same patient, or serial examinations over time. These related observations must remain together during model development and testing. Splitting images rather than patients allows information from the same patient to appear in both training and test sets, producing overly optimistic performance estimates.

A model should also be evaluated across clinically relevant groups. Depending on the application, these may include age, sex, race and ethnicity, BMI, diabetes phenotype, thyroid histology, disease severity, imaging equipment, geography, and care setting. 

A strong paper does not merely state that its cohort was “diverse.” It shows who was included, who was excluded, and whether the model worked consistently across those groups. 

3. Can the labels be trusted? A model is only as reliable as the reference standard used to train and evaluate it. 

Ask how the outcome was defined. Was thyroid malignancy determined by surgical histopathology, cytopathology, longitudinal surveillance, or a mixture of methods? Was hypothyroidism identified by laboratory criteria or merely by a billing code? Was diabetic retinopathy graded by one reader, multiple readers, or an adjudicated expert panel? 

Not all labels are equally trustworthy. For example, a thyroid ultrasound study that labels every surgically resected nodule as the ground truth may be highly accurate for pathology-confirmed disease, but it may also suffer from verification bias. Nodules that undergo surgery are not representative of all nodules seen in endocrine practice. They are often larger, more suspicious, symptomatic, cytologically indeterminate, or associated with patient preference. 

Important reviewer questions include: 

• Was the reference standard clinically appropriate? 

• Was it applied consistently across all patients? 

• Were labelers blinded to the model output? 

• Was inter-reader agreement reported? 

• Were uncertain, indeterminate, or discordant cases handled transparently? 

• Was the same outcome definition used in development and test cohorts? 

For thyroid cancer studies, reviewers should also inspect the histologic composition. A model trained predominantly on papillary thyroid carcinoma (PTC) may perform well for classic PTC while being less reliable for follicular-pattern malignancies, medullary thyroid carcinoma, or uncommon histologic subtypes. A model can be technically accurate while learning a narrow version of the disease. 

4. Was the model tested on data that were truly protected from development? This is the central methodological question. A model should not be evaluated on the same data used to train it. More subtly, the final test set should also be protected from all development decisions. That includes feature selection, image preprocessing, imputation, hyperparameter tuning, threshold selection, calibration, model selection, and error-driven revisions. 

A useful rule is simple: The final test set should be seen once, at the end. Internal cross-validation is useful during model development, but it does not establish that the model will generalize outside the original dataset. A later time period from the same institution is stronger than random splitting, and an independent institution is stronger still. 

External evaluation may be: 

• Temporal: tested in patients from a later time period. 

• Geographic: tested at a different hospital or health system. 

• Technical: tested using different devices, scanners, laboratory platforms, or electronic health record systems. 

• Clinical: tested in a different care setting or patient spectrum. 

An early developmental study may reasonably report internal validation, but its claims should remain limited. Research should not imply broad clinical readiness or generalizability without a genuinely independent evaluation cohort. 

Reviewers should be especially alert to data leakage, which occurs when information from the test set, or information unavailable at the intended decision point, enters model development. 

Examples include: 

• Images from the same patient appearing in both training and test sets. 

• Serial visits from the same patient split across datasets. 

• Using post-diagnosis laboratory tests to predict a diagnosis. 

• Including medication orders, pathology codes, procedure orders, or referral patterns that already reveal the outcome. 

• Normalizing or imputing the entire dataset before splitting into training and test cohorts. 

• Selecting the final classification threshold after examining the test-set results.

An unusually high AUC should prompt an audit for leakage, label artifacts, spectrum restriction, or an overly easy test population. An AUC of 0.99 is not automatically wrong, but it should be explained. 

5. Are the performance metrics clinically complete and statistically honest? AUC is useful, but it is not enough. A model may discriminate well between patients with and without disease while still being poorly calibrated, unstable across subgroups, or incapable of meaningfully guiding clinical decision-making.

Reviewers should expect the following:

Discrimination. For classification models, report measures such as: 

• Area under the receiver operating characteristic curve. 

• Sensitivity and specificity. 

• Positive and negative predictive values. 

• Likelihood ratios, when relevant. 

• Precision-recall performance for rare outcomes. 

For prognosis or continuous prediction, the relevant metric may differ. The key question is whether the metric matches the clinical task. 

Threshold-specific performance. A model should report sensitivity, specificity, positive predictive value, negative predictive value, and false-positive and false-negative consequences at the threshold intended for use. The threshold should be selected in a development or validation cohort, then locked before evaluation in the final test cohort. 

A model designed to reduce unnecessary fine-needle aspirations should not be judged only by AUC. It should show how many fine-needle aspiration (FNAs) might be avoided, how many malignancies might be delayed or missed, and whether that tradeoff is acceptable. 

Calibration. Calibration asks whether predicted probabilities correspond to observed risk. When a model reports a 20% risk of disease, approximately 20% should actually have the disease. A model can have an excellent AUC and still provide poorly calibrated risk estimates. 

Look for: 

• Calibration plots. 

• Calibration slope. 

• Brier score or another proper scoring rule. 

• Recalibration methods, when appropriate. 

Precision and uncertainty. Performance estimates should include confidence intervals. A model with an AUC of 0.88 based on 30 cancers is not equivalent to a model with the same AUC based on 3,000 cancers. Ask how many outcome events occurred in each dataset and whether confidence intervals are sufficiently narrow to support the authors’ conclusions. 

Subgroups and robustness.  Average performance can conceal clinically important failures. 

Look for model performance across: 

• Age groups. 

• Sex. 

• Race and ethnicity. 

• Disease prevalence strata. 

• Histologic or phenotypic subgroups. 

• Sites and geographic regions. 

• Ultrasound machines, scanners, laboratory platforms, or EHR systems. 

• Image quality and incomplete-data scenarios. 

For an endocrine AI tool, poor performance in one subgroup may matter more than a strong average result. 

6. Does the model improve clinical decisions, workflow, or patient outcomes? A model can be accurate and still be useless. The clinically important question is not whether the model predicts an outcome. It is whether using the model improves a decision compared with current practice. 

Ask what the model was compared against: 

• Standard clinical assessment. 

• Existing guideline-based risk stratification. 

• A validated clinical score. 

• A conventional statistical model. 

• The unaided endocrinologist. 

• The endocrinologist using the AI system. 

The comparator should be fair. A model that uses laboratory values, imaging, demographics, and longitudinal notes should not be compared with a clinician restricted to one ultrasound image. 

For thyroid nodule tools, meaningful outcomes may include: 

• Reduced unnecessary FNA. 

• Reduced unnecessary surgery. 

• Maintained sensitivity for clinically significant cancer. 

• Better selection for molecular testing. 

• Reduced interobserver variability. 

• Improved patient counseling. 

For diabetes tools, meaningful outcomes may include: 

• Reduced hypoglycemia. 

• Improved time in range. 

• Better risk stratification. 

• More timely treatment intensification. 

• Fewer preventable admissions. 

Decision-curve analysis can help estimate net benefit across clinically relevant thresholds, but it should not be treated as a substitute for real-world evaluation. 

The strongest studies move through a sequence: 

1. Retrospective development. 

2. Independent evaluation. 

3. Prospective validation. 

4. Clinical workflow evaluation. 

5. Comparative impact study or randomized trial. 

A model that has never left the retrospective sandbox may be promising; however, it has not yet earned the right to change patient care. 

7. Can the work be audited, reproduced, and safely maintained? Trustworthy AI requires more than an impressive result. Reviewers should look for enough detail to understand what was built, how it was evaluated, and whether another group could test it independently. 

Useful elements include: 

• A clearly defined clinical objective and intended use. 

• Complete cohort and label definitions. 

• Transparent preprocessing and feature-engineering methods. 

• A description of missing data handling. 

• Versioned model architecture and software environment. 

• Hyperparameter selection procedures. 

• Random seeds or enough detail to reproduce model development. 

• Access to code, model weights, data dictionaries, or a secure independent evaluation pathway. 

• Full disclosure of funding, conflicts of interest, and the role of commercial partners. 

Public code and data are valuable, but they are not always possible because of privacy, licensing, or regulatory constraints. When data cannot be shared, authors should still provide enough methodological detail for an independent investigator to understand and evaluate the work. 

Explainability claims also deserve scrutiny. A saliency map or heatmap can be visually persuasive, but it is not proof that the model used clinically valid reasoning. Ask whether the explanation method was itself evaluated, whether it highlights plausible anatomy or features, and whether it remains stable when the image is perturbed. 

For large language model studies, reviewers should additionally request: 

• Exact model name and version. 

• Date of model access. 

• Prompt design and system instructions. 

• Temperature and inference settings. 

• Retrieval sources, if retrieval-augmented generation was used. 

• Evaluation dataset and ground truth. 

• Hallucination, safety, and failure mode analysis. 

Finally, ask what happens after deployment. Models can drift as patient populations, imaging devices, laboratory assays, clinical guidelines, and documentation practices change. A clinically deployable model should have a plan for monitoring, recalibration, version control, and safe retirement when performance deteriorates. 

Endocrinology-Specific Red Flags 

Thyroid ultrasound AI 

• Images rather than patients are split into training and test sets. 

• Only surgical pathology is used as the reference standard. 

• The dataset is enriched for papillary thyroid carcinoma. 

• Benign nodules have inadequate follow-up. 

• Ultrasound machine vendor, probe type, and image-acquisition protocol are not reported. 

• Performance is reported per image but not per nodule or per patient. 

• The model is compared with radiologists or endocrinologists using an unfair information advantage. 

EHR and laboratory-based models 

• Predictors are collected after the intended clinical decision point. 

• Medication orders or referrals reveal the diagnosis. 

• Missingness is ignored, even though it may reflect clinician behavior or disease severity. 

• Billing codes are treated as definitive disease labels. 

• Temporal validation is absent despite changing practice patterns. 

Diabetes and CGM models 

• Sequential data from the same patient appear in both training and test sets. 

• The prediction horizon is poorly defined. 

• Insulin doses, carbohydrate entries, and glucose values are misaligned in time. 

• The model is evaluated only during stable outpatient periods and not during illness, exercise, pregnancy, hospitalization, or device failure. 

• Performance is reported without assessing hypoglycemia safety. 

8. Finally, are there any reporting requirements? A recurring challenge in peer review of medical AI is deciding which standard a manuscript should be measured against. The reporting guideline that applies depends on the clinical question the study asks and the stage of evaluation it represents, not simply on whether artificial intelligence is involved. These guidelines are not bureaucratic checklists; each defines the minimum information a reader needs to judge whether a model's reported performance is credible, reproducible, and free of the failure modes. The table below depicts these reporting guidelines. The authors are supposed to mention which guidelines they are adhering to and fill out the appropriate form as supplementary material.  

The Reviewer’s Toolkit at a Glance 

The Bottom Line 

Critically evaluating an AI study does not require a data science degree. The same clinical reasoning used to assess trials, diagnostic tests, and prediction models can be applied to AI studies, with additional attention to data provenance, label validity, data leakage, calibration, robustness, clinical workflow, and reproducibility.

Keep these questions nearby: 

1. Is this a real problem that AI can improve? 

2. Does the population match the intended use? 

3. Can I trust the labels? 

4. Was the model tested on genuinely protected data? 

5. Are the performance claims clinically complete and statistically honest? 

6. Does the model improve a decision or outcome that matters? 

7. Can the work be audited, reproduced, and safely maintained? 

8. Did the authors follow the appropriate reporting guideline for the study?

This framework will help distinguish a model that is merely technically interesting from one that may eventually deserve a place in endocrine practice.