R. Heller · Date: 2026-07-26 · Last changed: 2026-11-09
NoteAt a glance
Guiding question: Which findings support measurement quality, and which support better care?
For: clinicians preparing a journal club, members of committees that decide on clinical software, doctoral researchers and peer reviewers · Prerequisites:Chapter 5 (validation designs) and Chapter 6 (2 × 2 table, calibration, thresholds)
The committee for clinical decision support of a fictitious hospital meets in two weeks. On the agenda is a request to switch on a sepsis warning that comes with the hospital’s electronic health record and, according to the supplier, is used in many hospitals. A resident who runs the internal medicine journal club is asked to prepare a one-page brief. The committee wants to know two things: how well does the score recognise sepsis, and does its use lead to better care for patients? The resident finds one independent external validation of a widely implemented proprietary sepsis model, a set of reporting guidelines with unfamiliar acronyms and a supplier brochure. The recommendation — switch on, pilot under observation, or decline — will change the work of every ward. A brief that confuses accuracy with benefit could commit the hospital to thousands of alerts without any evidence that patients gain.
7.2 Core reading
Core reading · required for W2 · about 11 minutes · ends before ‘Lab’
A ladder of evidence. Studies of medical tests and models answer questions at different levels. Fryback and Thornbury described a hierarchy for diagnostic imaging that still serves well: technical quality, diagnostic accuracy, effect on the clinician’s diagnostic thinking, effect on management, effect on patient outcomes, and societal costs and benefits. Evidence at a lower level is necessary but not sufficient for a claim at a higher level (Fryback and Thornbury 1991). An AI system climbs the same ladder. A reader study or diagnostic accuracy study compares the system’s output with a reference standard. An external validation applies a prediction model to patients from another place or time and measures discrimination and calibration there (Chapter 6). An early clinical evaluation places the system into a real workflow on a small scale and asks how clinicians use it, when they override it and what goes wrong. Only a comparative study, ideally randomised, can show whether patients are better off with the system than without it.
The higher rungs are sparsely populated. A systematic review of deep learning studies in medical imaging that compared algorithms with clinicians found only 10 records of randomised trials, two of them published; of 81 non-randomised studies only nine were prospective, 58 were at high risk of bias, and 61 stated in their abstract that the algorithm performed at least as well as clinicians (Nagendran et al. 2020). Claims in abstracts can therefore run ahead of the design.
Four tools, four tasks. Reporting guidelines list what a paper must report so that a reader can judge it; an appraisal tool guides the judgement itself. Table 7.1 assigns each of the four AI-specific tools to one concrete check. The item numbers refer to the published checklists.
Table 7.1: Four tools for four questions about clinical AI. For randomised trials of AI interventions, CONSORT-AI adds 14 items to CONSORT 2010 (Liu et al. 2020).
Study type and question
Tool
One concrete check
What the study cannot show
Diagnostic accuracy: does the output agree with the reference standard?
How were the data partitioned into training, validation and test sets (item 15b), and does the test set represent the target condition and population (items 25, 28)?
Whether clinicians decide differently or patients do better
Prediction model development or evaluation: how well does the model discriminate and calibrate?
Are all measures for discrimination, calibration and clinical utility specified (item 12e) and reported with confidence intervals, including key subgroups (item 23a)?
Whether acting on the prediction changes outcomes
Same studies, appraised: can the result be trusted and does it apply here?
PROBAST+AI, quality, risk of bias and applicability (Moons et al. 2025)
Model evaluation, domain 4: was data leakage avoided (4.5), were all development steps repeated in resampling (4.6), were calibration, discrimination and net benefit evaluated (4.7)?
Anything beyond the population and setting of the evaluation
Early clinical evaluation in live use: how is the system used, and is it safe?
Is user agreement reported, with instances of and reasons for variation from the recommendation (item 12), and are errors and risks to patient safety listed (item 13)?
Comparative effectiveness
A missing item is not a verdict. It is a question to the authors, the supplier or the local team. If a paper on a prediction model reports an AUC but no calibration, the right response is “How do predicted and observed risks compare in your test set?”, not silent acceptance or silent rejection. Such questions can go to the authors through the journal, to the supplier as part of procurement, or to the local team as the first item of a plan for a silent evaluation in the hospital’s own patients. The answer may change the verdict in either direction.
Five questions for the journal club. Whatever the study type, five questions organise the reading, and the lab turns them into a card. Recruitment: who was included, from where and when, and who was left out? A test set collected from patients with clear-cut disease and clear-cut health tends to overstate accuracy for the mixed patients of everyday care. Reference: how was the target condition or outcome established, by whom, and without knowledge of the model’s output? Discharge codes, for example, capture only episodes that were documented and coded. Analysis: were tuning, model choice and testing kept apart (Chapter 5), and are discrimination, calibration and a threshold reported with denominators (Chapter 6)? Generalisation: does the evaluation population resemble the patients on whom the model would be used here — case mix, measurement devices, time, care pathway? Decision: does the conclusion stay at the level the design reached, or does an accuracy study recommend implementation “to improve outcomes”? Each question can be answered from the paper, from a supplement, or not at all; the last answer is itself a finding.
One statement, checked against its source. The committee brief will contain numbers, and each number needs a source that can be checked. Here is one statement, traced to its origin.
Table 7.2: A checked statement: claim, original, locator, unit and verdict. Numbers are published(Wong et al. 2021).
Element
Content
Statement in the brief
In an independent external validation, the sepsis model discriminated poorly (AUC 0.63) and missed two thirds of sepsis cases while alerting in almost one in five hospitalisations.
Original study
Wong et al. (2021), retrospective cohort at one US academic health system, December 2018 to October 2019
Locator
Abstract, “Results”: AUC 0.63 (95% CI 0.62–0.64) at hospitalisation level; the model “did not identify 1709 patients with sepsis (67%) despite generating alerts for an ESM score of 6 or higher for 6971 of all 38 455 hospitalized patients (18%)”
Unit and denominator
38,455 hospitalisations of 27,697 patients; 2,552 with sepsis (7%)
Data status
published; abstract read in PubMed, DOI checked against Crossref; the article carries a correction (2 August 2021) of the number needed to evaluate in Table 2 and the Results, so only the corrected version may be quoted for that number
Verdict
Supported for measurement quality at this centre. Not evidence about patient outcomes, nor about other hospitals or later versions of the model
The lab reconstructs the 2 × 2 table behind this statement: a sensitivity of about 33%, a positive predictive value of about 12%, and roughly 8 hospitalisations with an alert for each hospitalisation with sepsis that the alert caught. The study also compared the score with contemporary care: it identified 183 of the 2,552 patients with sepsis (7%) who did not receive timely antibiotics. The authors read this as low sensitivity compared with contemporary clinical practice: the score seldom flagged sepsis that clinicians had not already treated in time. That is a question one level above accuracy on the Fryback–Thornbury ladder — whether the information changes what clinicians do.
The most important assumption when reading any AI study is that a study supports only the claim its design can answer: accuracy in a test population is not evidence of better care, and better care in one hospital is not evidence for another. The supplier’s statement that the model is “used in many hospitals” is evidence of dissemination, not of benefit.
Question for the workshop: The committee asks for a single sentence. Write one sentence about the sepsis warning that is fully supported by Table 7.2, and one sentence that the brochure might contain but that the study cannot support. Which study type would be needed for the second sentence?
7.3 Lab
7.3.1 Part A · Reconstruct the 2 × 2 table from the published abstract
All inputs are published counts from the abstract of Wong et al. (2021). Combining them into one table rests on an assumption that must be stated: the counts refer to the same unit (hospitalisation), the same alert threshold (score 6 or higher) and the same time window. The abstract places them in one sentence but does not say this explicitly; the full text (Table 2, corrected version) is where a reader would confirm it.
n_hosp <-38455# hospitalisations analysed (published)n_sepsis <-2552# hospitalisations with sepsis (published)missed <-1709# sepsis not identified by the alert (published, 67%)alerted <-6971# hospitalisations with an alert, score >= 6 (published, 18%)tp <- n_sepsis - missed # sepsis with alertfp <- alerted - tp # alert without sepsisfn <- missed # sepsis without alerttn <- n_hosp - n_sepsis - fp # neithersens <- tp / n_sepsisspec <- tn / (n_hosp - n_sepsis)ppv <- tp / alertednpv <- tn / (tn + fn)alerts_per_case <- alerted / tp # alerts per sepsis case caught# Consistency with the percentages printed in the abstractstopifnot(tp + fp + fn + tn == n_hosp,round(100* missed / n_sepsis) ==67, round(100* alerted / n_hosp) ==18,round(100* n_sepsis / n_hosp) ==7, tp ==843)round(c(sensitivity = sens, specificity = spec, ppv = ppv, npv = npv,alerts_per_case = alerts_per_case), 3)
Table 7.3: Reconstructed 2 × 2 table for the sepsis alert (score ≥ 6) at the hospitalisation level, from the published abstract of Wong et al. (2021). Unit: hospitalisation; n = 38,455 from 27,697 patients; counts derived from published figures under the stated assumption.
Sepsis
No sepsis
Total
Alert (score ≥ 6)
843
6,128
6,971
No alert
1,709
29,775
31,484
Total
2,552
35,903
38,455
Read the result as a committee member would. Of 1,000 hospitalisations, about 181 receive an alert; about 22 of these involve sepsis and about 159 do not; about 44 hospitalisations with sepsis receive no alert. The unit matters: 38,455 hospitalisations come from 27,697 patients, so some patients contribute more than one hospitalisation, and the hospitalisations are not fully independent observations (Chapter 19).
7.3.2 Part B · A journal-club card for a fictitious abstract
The second exercise uses a synthetic abstract written for this book. It describes no real study, product or hospital.
Fictitious abstract.Machine learning predicts postoperative delirium after hip fracture. We developed a gradient-boosting model using 46 routinely collected variables from 2,140 admissions of patients aged 65 or older at two hospitals (2019–2023). Delirium was identified from discharge diagnosis codes. Admissions were randomly split 80 : 20 into training and test sets; hyperparameters were optimised on the test set. The model achieved an AUC of 0.89 (95% CI 0.86–0.92) and outperformed a clinical points rule (AUC 0.71). Feature importance identified postoperative opioid dose, age and dementia as the strongest predictors. The model reliably identifies patients at risk and should be implemented to reduce delirium.
The card has five rows — recruitment, reference (here: outcome definition), analysis, generalisation and decision. Each row names the tool item it draws on and turns a missing or doubtful item into a question.
card <-data.frame(domain =c("Recruitment", "Reference / outcome", "Analysis", "Analysis", "Generalisation", "Decision"),abstract_says =c("2,140 admissions, two hospitals, 2019-2023","delirium from discharge diagnosis codes","random 80:20 split of admissions","hyperparameters optimised on the test set; AUC only","test set from the same two hospitals and period","'should be implemented to reduce delirium'"),item =c("PROBAST+AI 1.3 (representative inclusions)","PROBAST+AI 3.1 (outcome defined and assessed appropriately)","PROBAST+AI 4.5 (data leakage avoided); 2.4 (predictors available at prediction time)","TRIPOD+AI 12c, 12e; PROBAST+AI 4.7 (calibration, net benefit)","STARD-AI 28 / TRIPOD+AI 23a (target population, subgroups)","DECIDE-AI; CONSORT-AI (impact needs live use and comparison)"),rating =c("unclear", "doubtful", "doubtful", "not reported", "not reported", "not supported"))card$question <-ifelse(card$rating =="reported", "",c("How many eligible admissions were excluded, and why?","How sensitive are discharge codes for delirium compared with a structured bedside assessment?","Were repeat admissions of the same patient kept on one side of the split? Was the postoperative opioid dose known at the time of prediction?","What was the performance on data not used for tuning, and how well calibrated are the predicted risks?","How does the model perform in another hospital, a later period and in key subgroups?","Which study showed that acting on the model reduces delirium?"))n_questions <-sum(card$question !="")stopifnot(n_questions ==nrow(card)) # every row of this abstract triggers a questionknitr::kable(card, col.names =c("Domain", "Abstract says", "Tool item", "Rating", "Question to the authors"),row.names =FALSE)
Table 7.4: Journal-club card for the fictitious delirium abstract. Every row rated other than ‘reported’ produces a question to the authors.
Domain
Abstract says
Tool item
Rating
Question to the authors
Recruitment
2,140 admissions, two hospitals, 2019-2023
PROBAST+AI 1.3 (representative inclusions)
unclear
How many eligible admissions were excluded, and why?
Reference / outcome
delirium from discharge diagnosis codes
PROBAST+AI 3.1 (outcome defined and assessed appropriately)
doubtful
How sensitive are discharge codes for delirium compared with a structured bedside assessment?
Analysis
random 80:20 split of admissions
PROBAST+AI 4.5 (data leakage avoided); 2.4 (predictors available at prediction time)
doubtful
Were repeat admissions of the same patient kept on one side of the split? Was the postoperative opioid dose known at the time of prediction?
Analysis
hyperparameters optimised on the test set; AUC only
TRIPOD+AI 12c, 12e; PROBAST+AI 4.7 (calibration, net benefit)
not reported
What was the performance on data not used for tuning, and how well calibrated are the predicted risks?
How does the model perform in another hospital, a later period and in key subgroups?
Decision
‘should be implemented to reduce delirium’
DECIDE-AI; CONSORT-AI (impact needs live use and comparison)
not supported
Which study showed that acting on the model reduces delirium?
Two findings stand out. Tuning on the test set removes the independence of the test, so the AUC of 0.89 is an optimistic estimate (Chapter 5). And postoperative opioid dose cannot be known on the first morning after admission: if the model is meant to trigger prevention before surgery, one of its strongest predictors is not available at the time of use (PROBAST+AI, signalling question 2.4). The concluding sentence makes an impact claim from an accuracy study.
7.4 Counter-check
Change the target population. Suppose the committee considers the alert only for an intensive care unit, where sepsis is far more common — say 20% of stays instead of 7% (assumption).
Before you compute, predict: With the published sensitivity and specificity, does the positive predictive value rise or fall? And what happens to the number of alerts per sepsis case caught?
ppv_at <-function(prev, se = sens, sp = spec) se * prev / (se * prev + (1- sp) * (1- prev))prevalences <-c(published = n_sepsis / n_hosp, icu_assumed =0.20)cc <-data.frame(setting =names(prevalences), prevalence = prevalences,ppv =ppv_at(prevalences), alerts_per_case =1/ppv_at(prevalences))stopifnot(abs(cc$ppv[1] - ppv) <1e-9, cc$ppv[2] > cc$ppv[1])knitr::kable(cc, digits =3, row.names =FALSE,col.names =c("Setting", "Prevalence", "PPV", "Alerts per case caught"),caption ="Counter-check: published sensitivity and specificity applied to an assumed higher prevalence.")
Counter-check: published sensitivity and specificity applied to an assumed higher prevalence.
Setting
Prevalence
PPV
Alerts per case caught
published
0.066
0.121
8.269
icu_assumed
0.200
0.326
3.067
The positive predictive value rises to about 33% and the alerts per case caught fall to about 3.1. The calculation, however, assumes that sensitivity and specificity carry over unchanged to intensive care. That is rarely true: patients there are sicker, measured more often and treated earlier, so the score’s behaviour can change in either direction. The counter-check therefore yields a hypothesis for a local evaluation, not a result (Methods in R: Predictive Values and Prevalence).
7.5 Consequences for patients and operations
Patients. Two harms sit on either side of a sepsis alert. A missed case may delay treatment, although clinicians often recognise sepsis without the alert, as the comparison with timely antibiotics in Wong et al. (2021) shows. A false alert can lead to unnecessary tests, antibiotics and interruptions, and many false alerts teach staff to ignore all of them. Which harm dominates depends on how the alert is embedded in the workflow — a question for an early clinical evaluation (DECIDE-AI), not for the accuracy study.
Operations. A brief for the committee should give the expected number of alerts per ward and day, the person who responds to an alert, and the rule for stopping the pilot (Chapter 20). Local data from a silent, non-alerting phase can show discrimination and calibration in the hospital’s own population before any alert reaches a clinician.
Regulation. Software intended to support the diagnosis of sepsis in individual patients is typically assessed as medical device software under the Medical Device Regulation (European Parliament and Council of the European Union 2017); the qualification guidance MDCG 2019-11 Rev. 1 is orientation, not binding law (Medical Device Coordination Group 2025). Under Article 6(1) of the AI Act (European Parliament and Council of the European Union 2024), an AI system is high-risk if it is a safety component of a product, or itself a product, covered by the legislation listed in Annex I — which includes the Medical Device Regulation — and that product has to undergo a third-party conformity assessment. After the amendment by Regulation (EU) 2026/1744 (European Parliament and Council of the European Union 2026), which entered into force on 27 July 2026, Chapter III, Sections 1 to 3 apply to such systems from 2 August 2028 (Article 113, as amended; read on EUR-Lex in the English text of the amendment; status: November 2026). Whether a particular warning function is a medical device, and who is its manufacturer, depends on its intended purpose and is a question for the hospital’s regulatory function (open; Chapter 22).
Data protection. A local validation uses patient data for a purpose other than treatment. Its legal basis, minimisation and access rules must be settled before data are extracted (Chapter 23, Chapter 26).
7.6 Look up and transfer
Reviewer question: “For each claim in your abstract, which result in which table supports it, at which level of evidence — accuracy, effect on decisions, or effect on patient outcomes — and in which population?”
Self-test: A paper reports that after an AI fracture-detection tool was introduced in an emergency department, the rate of missed fractures in the following six months was lower than in the six months before. The authors conclude that the tool improves patient outcomes. Which level of evidence does the study reach, and what is the main alternative explanation?
TipAnswer
It is an uncontrolled before–after comparison of a process measure (missed fractures), so it sits between accuracy and effect on management, and it does not measure patient outcomes such as complications or function. The main alternative explanations are secular trends and co-interventions (new staff, training, awareness after the introduction), and changes in how missed fractures were detected or recorded. A concurrent comparison — ideally a cluster-randomised or stepped-wedge design reported according to CONSORT-AI — and a patient-relevant outcome would be needed. An early clinical evaluation reported according to DECIDE-AI would describe how clinicians used the tool.
Annotated sources:
Fryback and Thornbury (1991) defines the hierarchy of diagnostic efficacy that structures the core reading.
Nagendran et al. (2020) documents how few prospective and randomised studies exist for deep learning in imaging and how often abstracts claim parity with clinicians.
Sounderajah et al. (2025) (STARD-AI; an author correction of July 2026 concerns only the consortium list), Collins et al. (2024) (TRIPOD+AI), Moons et al. (2025) (PROBAST+AI) and Vasey et al. (2022) (DECIDE-AI) are the four tools assigned to concrete checks in Table 7.1.
Liu et al. (2020) is the reporting extension for randomised trials of AI interventions, the top rung of the ladder.
Wong et al. (2021) is the external validation from which the checked statement and the reconstructed 2 × 2 table come.
Collins, Gary S., Karel G. M. Moons, Paula Dhiman, et al. 2024. “TRIPOD+AI Statement: Updated Guidance for Reporting Clinical Prediction Models That Use Regression or Machine Learning Methods.”BMJ 385: e078378. https://doi.org/10.1136/bmj-2023-078378.
European Parliament and Council of the European Union. 2024. Regulation (EU) 2024/1689 Laying down Harmonised Rules on Artificial Intelligence (Artificial Intelligence Act). https://eur-lex.europa.eu/eli/reg/2024/1689/oj.
European Parliament and Council of the European Union. 2026. Regulation (EU) 2026/1744 Amending Regulation (EU) 2024/1689 (Digital Omnibus on AI). https://eur-lex.europa.eu/eli/reg/2026/1744/oj.
Fryback, Dennis G., and John R. Thornbury. 1991. “The Efficacy of Diagnostic Imaging.”Medical Decision Making 11 (2): 88–94. https://doi.org/10.1177/0272989X9101100203.
Liu, Xiaoxuan, Samantha Cruz Rivera, David Moher, et al. 2020. “Reporting Guidelines for Clinical Trial Reports for Interventions Involving Artificial Intelligence: The CONSORT-AI Extension.”Nature Medicine 26 (9): 1364–74. https://doi.org/10.1038/s41591-020-1034-x.
Moons, Karel G. M., Johanna A. A. Damen, Tabea Kaul, et al. 2025. “PROBAST+AI: An Updated Quality, Risk of Bias, and Applicability Assessment Tool for Prediction Models Using Regression or Artificial Intelligence Methods.”BMJ 388: e082505. https://doi.org/10.1136/bmj-2024-082505.
Nagendran, Myura, Yang Chen, Christopher A. Lovejoy, et al. 2020. “Artificial Intelligence Versus Clinicians: Systematic Review of Design, Reporting Standards, and Claims of Deep Learning Studies.”BMJ 368: m689. https://doi.org/10.1136/bmj.m689.
Sounderajah, Viknesh, Ahmad Guni, Xiaoxuan Liu, et al. 2025. “The STARD-AI Reporting Guideline for Diagnostic Accuracy Studies Using Artificial Intelligence.”Nature Medicine 31: 3283–89. https://doi.org/10.1038/s41591-025-03953-8.
Vasey, Baptiste, Myura Nagendran, Bruce Campbell, et al. 2022. “Reporting Guideline for the Early Stage Clinical Evaluation of Decision Support Systems Driven by Artificial Intelligence: DECIDE-AI.”BMJ 377: e070904. https://doi.org/10.1136/bmj-2022-070904.
Wong, Andrew, Erkin Otles, John P. Donnelly, et al. 2021. “External Validation of a Widely Implemented Proprietary Sepsis Prediction Model in Hospitalized Patients.”JAMA Internal Medicine 181 (8): 1065–70. https://doi.org/10.1001/jamainternmed.2021.2626.