Contents
On this page
- Mapping of 122 studies and pooling of 9
- Effect of the unit of analysis on pooled results
- The requirement for a bivariate model
- Thresholds, continuous outputs and the limitations of AUC
- Internal versus external validation
- Heterogeneity and bias checks at realistic study counts
- Appraisal and reporting instruments for this review type
- Reporting accuracy results in a usable form
- Planning a review of this type
- Key points
- Application to your study
- Frequently asked questions
Academy · Research Data Analytics & AI · Cardiac imaging AI meta-analysis
Pooling AI Studies in Cardiovascular Imaging: Reasons for the Low Proportion of Poolable Studies
In the largest recent review of AI in non-invasive cardiovascular imaging, 122 studies were mapped and 9 were pooled. That ratio is the central fact about this field, and it reflects a reporting problem rather than a scarcity problem. Most AI imaging studies cannot enter a diagnostic accuracy meta-analysis because they do not report the data a bivariate model requires, or because their accuracy figures refer to a validation design that is not comparable with that of other studies.
In a meta-analysis of artificial intelligence in cardiovascular imaging, the principal constraint is not the size of the literature but the small proportion of it that can be pooled. Diagnostic accuracy synthesis requires paired sensitivity and specificity at a stated threshold, in a defined population, at a defined unit of analysis, with the counts needed to reconstruct a 2x2 table. A large majority of published AI imaging papers report an area under the curve and little else. This article sets out what a defensible synthesis requires and how to write the review when the evidence will not support one.
Learning objectives
- Why a diagnostic accuracy meta-analysis needs a bivariate or hierarchical model rather than two separate pooled estimates
- How the unit of analysis — patient, vessel or segment — changes the pooled result and what it answers
- Why an AUC without a threshold and a validation design is not a poolable result
- How the difference between internal and external validation affects reported accuracy
- Which heterogeneity and small-study-effect checks are usable at the study counts available in this field
- How to report a review transparently when only a small number of studies can be combined
Common misconceptions
- “Pool the sensitivities, then pool the specificities.” Reitsma and colleagues demonstrated why this approach is incorrect: the two are negatively correlated within studies because they move with the threshold, and ignoring that correlation misstates both the summary estimates and their uncertainty.
- “A higher AUC means a better algorithm.” In the cardiovascular review, patient-level AUC was 0.83 and vessel-level AUC 0.92 for the same task. The unit of analysis changed the figure more than most algorithm comparisons do.
- “AI beats clinicians at image interpretation.” Liu and colleagues, in The Lancet Digital Health, found that across the 14 studies comparing both in the same external-validation sample, deep learning gave pooled sensitivity 87.0% and specificity 92.5% against 86.4% and 90.5% for health-care professionals — a near-identical result, from a small fraction of the literature.
- “Heterogeneity statistics will tell me whether to pool.” Such statistics are descriptive. Higgins and Thompson proposed H, I-squared and R to describe heterogeneity independently of the effect metric and the number of studies, not to license a decision.
- “A funnel plot will reveal publication bias in this literature.” Sterne and colleagues advise against asymmetry tests below 10 studies, and most poolable AI imaging sets fall below that number.
Mapping of 122 studies and pooling of 9
Liu and colleagues’ systematic review and meta-analysis of AI in non-invasive cardiovascular imaging for coronary artery disease, in Frontiers in Cardiovascular Medicine, mapped 122 studies and pooled 9 of them, with 8 contributing patient-level and 6 vessel-level data 5. This yield is not unusual for the field, and the reasons for which the other studies were excluded warrant precise examination.
The recurring reasons are structural. Many studies report discrimination as an area under the curve with no threshold at which sensitivity and specificity were evaluated, so there is no 2x2 table to extract. Many report performance on a held-out split of the development dataset rather than on an independent sample, which is a different quantity from diagnostic accuracy in a new population 51. Many report at a unit of analysis — per segment, per vessel, per patient — that is not stated clearly or not comparable with the rest. Many others use a reference standard that differs from the others in the set, so the pooled estimate would be an average across different definitions of the target condition.
The practical consequence for a review protocol is that eligibility criteria must be written in terms of what is reportable rather than what is of interest. If the criteria require paired sensitivity and specificity at a stated threshold, on an independent sample, at a single stated unit of analysis, reviewers should expect a single-figure number of eligible studies from a literature of several hundred, and the protocol should state this in advance rather than the problem emerging at the synthesis stage.
Effect of the unit of analysis on pooled results
This point is most often lost when AI accuracy figures are cited. In the cardiovascular review, for detection of at least 50% coronary stenosis, patient-level pooled sensitivity was 0.94 (95% CI 0.84 to 0.98) with specificity 0.69 (0.60 to 0.76) and AUC 0.83 (0.79 to 0.86) 2,5,49. Vessel-level pooled sensitivity was 0.81 (0.69 to 0.89) with specificity 0.88 (0.84 to 0.91) and AUC 0.92 (0.89 to 0.94). The same review and the same task therefore yielded two quite different profiles.
The pattern is explicable. A patient is classified as positive if any vessel is classified as positive, so patient-level analysis aggregates upward: sensitivity rises because one true detection suffices, and specificity falls because a single false-positive vessel makes the whole patient a false positive. Vessel-level analysis distributes the same errors across more units, which raises apparent specificity. Neither approach is incorrect. They answer different clinical questions — whether this patient requires further investigation, as opposed to whether this vessel is the culprit — and they must not be pooled together.
Two rules follow. The unit of analysis should be stated in the eligibility criteria and each level analysed separately, as the cardiovascular review did with 8 patient-level and 6 vessel-level contributions. Multiple units within one study should be treated as a dependency rather than as additional studies, because the same patients generate both 51.
Pooled diagnostic accuracy for detection of at least 50% coronary stenosis, by unit of analysis. Patient-level sensitivity 0.94 (95% CI 0.84-0.98), specificity 0.69 (0.60-0.76), AUC 0.83 (0.79-0.86); vessel-level sensitivity 0.81 (0.69-0.89), specificity 0.88 (0.84-0.91), AUC 0.92 (0.89-0.94). Source: Liu B, Reis J, Sharma A, Wang W. Application of artificial intelligence in non-invasive cardiovascular imaging for coronary artery disease: a systematic review and meta-analysis. Frontiers in Cardiovascular Medicine 2025;12:1664183.
The requirement for a bivariate model
Sensitivity and specificity are not two independent outcomes. Within any single study they are linked by the threshold: moving the cut-off to detect more disease reduces specificity. Reitsma and colleagues, in the Journal of Clinical Epidemiology, set out the bivariate random-effects approach that models the two jointly, with a correlation parameter, producing summary estimates whose uncertainty reflects the real structure of the data 55. Harbord and colleagues, in Biostatistics, showed how the bivariate and hierarchical summary ROC formulations relate to one another, so the choice between them is largely a matter of what the reviewer wishes to report rather than a dispute about the model 53.
Pooling sensitivity and specificity in two separate univariate meta-analyses remains common and remains incorrect. It ignores the negative within-study correlation, understates the joint uncertainty, and produces a summary point that may not lie on any plausible ROC curve 55. Deeks, Macaskill and Irwig, also in the Journal of Clinical Epidemiology, extended this analysis to small-study effects in diagnostic reviews, where the standard funnel plot behaves differently from the intervention case 54.
The model therefore requires specific data: for each study, at one threshold, the counts of true positives, false positives, false negatives and true negatives, or enough to reconstruct them. An AUC cannot be converted into those counts, which is the principal reason AI imaging studies are excluded. The Pubrica quantitative extraction page describes how to design the extraction form so that this problem is identified at extraction rather than at analysis.
Synthesis models for diagnostic accuracy, and what each demands
| Approach | What it needs from each study | When it fails |
|---|---|---|
| Two separate univariate pooled estimates | Sensitivity and specificity, each with a standard error | Always, in principle: it ignores the within-study correlation between the two, so the joint uncertainty is misstated and the summary point may lie off any plausible ROC curve |
| Bivariate random-effects model Reitsma and colleagues | A 2x2 table at a single common threshold, or enough to reconstruct it | When studies report at different thresholds, or report only an AUC with no operating point |
| Hierarchical summary ROC Harbord and colleagues on the unified formulation | 2x2 tables across studies at differing thresholds | When study counts are very small, or when thresholds were optimised within each study’s own data |
| Narrative or mapping synthesis | Whatever each study reports, described consistently | Never fails, but produces no pooled estimate — which is the correct output when the set is not poolable |
Model requirements as set out in Reitsma and colleagues, Journal of Clinical Epidemiology 2005; Harbord and colleagues, Biostatistics 2007; and Deeks, Macaskill and Irwig, Journal of Clinical Epidemiology 2005 on small-study effects in diagnostic reviews.
Thresholds, continuous outputs and the limitations of AUC
An AI model typically emits a continuous score, and the operating threshold is chosen by the investigators. The reported sensitivity and specificity are therefore properties of a decision rule rather than of the algorithm, and a reported AUC is a summary across thresholds that includes regions in which no one would operate 22. Two models with the same AUC can behave entirely differently at the threshold a clinician would actually use.
For synthesis, this creates a difficult choice. If studies report at different thresholds, a bivariate model at a single common threshold is not available, and the hierarchical summary ROC formulation becomes the more appropriate target because it estimates a curve rather than a point 53. If thresholds were chosen to optimise performance in each study — a data-dependent choice — then the pooled estimate is optimistically biased in a way that no model corrects. For each study, the method of threshold selection should be recorded: pre-specified, taken from a previous study, or optimised in the same data. That field belongs on the extraction form and in the risk-of-bias table.
Internal versus external validation
Accuracy reported on a random split of the development dataset answers a question about the model’s fit. Accuracy reported on a separate sample, from a different site, scanner or population, answers the question a clinician has. The literature routinely conflates the two, and the AI imaging reviews that have separated them find that the difference is material 2,40.
Liu and colleagues’ review in The Lancet Digital Health provides the clearest demonstration. They restricted the head-to-head comparison to the 14 studies that compared deep learning against health-care professionals in the same external-validation sample. Pooled deep-learning sensitivity was 87.0% (95% CI 83.0 to 90.2) with specificity 92.5% (85.1 to 96.4), against 86.4% (79.9 to 91.0) and 90.5% (80.6 to 95.7) for the health-care professionals. The estimates overlap substantially 40. Notwithstanding claims of algorithmic superiority in image interpretation, the comparison on equal terms — same images, same sample, external validation — shows closely similar performance, and it was available in only 14 studies.
Because headline claims most often omit this distinction, it should be an eligibility criterion and a stratification variable, not a footnote. The Pubrica AI imaging hub covers the broader appraisal picture, and the CNN radiology page works through the same problem in lung nodule detection, where the gap between independent and all-validation estimates has been quantified.
Heterogeneity and bias checks at realistic study counts
With 9 studies in a pooled set, most of the standard diagnostic apparatus is out of range, and it is preferable to state this than to apply it regardless. Higgins and Thompson, in Statistics in Medicine, proposed three statistics — H, I-squared and R — to describe heterogeneity independently of the effect metric and the number of studies, illustrated on five datasets; in diagnostic reviews these describe variation in the summary estimates but do not resolve its source, and the source in AI imaging is usually evident from the study table rather than from a statistic. Typical sources are differences in scanners, disease prevalence, reference standards and thresholds.
Small-study-effect testing is the clearer case. Sterne and colleagues’ recommendations in the BMJ state that tests for funnel plot asymmetry should generally not be used when a meta-analysis contains fewer than 10 studies, and that the minimum may be substantially higher when heterogeneity is substantial 49. The underlying logic of the plot is that if no bias or heterogeneity is present, about 95% of studies should lie inside the triangle defined by the fixed-effect estimate plus or minus 1.96 standard errors — a statement about expected scatter that has no force at nine points 49. The absence of a usable test should be reported as a limitation, not as an absence of bias.
The uncertainty around the summary estimate warrants the same care. Veroniki and colleagues identified 15 confidence-interval methods for the random-effects summary effect and grouped them into seven categories; the method selected is a reportable choice, and in small sets it is a consequential one 60. The methodology walkthrough sets out how to pre-specify it.
Appraisal and reporting instruments for this review type
Three instruments are central, and none substitutes for another. QUADAS-2, published by Whiting and colleagues in the Annals of Internal Medicine, assesses risk of bias and applicability in diagnostic accuracy studies across patient selection, index test, reference standard, and flow and timing. For AI studies the index test domain carries most of the weight, because threshold selection, model version and whether the test was interpreted with knowledge of the reference standard are all assessed in that domain.
PRISMA-DTA, published by McInnes and colleagues in JAMA, is the reporting guideline for the review. It is not a method — see the Pubrica PRISMA definition page for why that distinction matters — but it specifies the items a reader of a diagnostic accuracy review needs, including the reference standard, the target condition and the unit of analysis 43.
CLAIM, the Checklist for Artificial Intelligence in Medical Imaging published by Mongan, Moy and Kahn in Radiology: Artificial Intelligence, covers the primary studies. It is the instrument to extract against when deciding whether an AI study is reportable enough to pool: data sources, ground truth definition, data partitions, model description and validation design 38. A study that fails CLAIM on its data partitions usually cannot be pooled, and recording this systematically converts a vague exclusion into a documented one.
Reporting accuracy results in a usable form
Most of the misinformation in this area arises from a correctly calculated number reported without the three facts that give it meaning: the threshold, the unit of analysis, and the validation design. The two versions below report the same finding from the same review.
The same pooled accuracy result, stated two ways
Unusable as reported
AI-based analysis of non-invasive cardiovascular imaging achieved an AUC of 0.92 for the detection of coronary artery disease, demonstrating high diagnostic accuracy.
Which unit of analysis? The same review reports AUC 0.92 at vessel level and 0.83 at patient level. The unqualified figure is the more favourable one.
What counts as the target condition? “Coronary artery disease” is not a threshold; the pooled estimates refer to at least 50% stenosis.
At what operating point? An AUC summarises across thresholds, including ones no clinician would use, so it does not state how the test performs in use.
Pooled from how many studies? Nine, out of 122 mapped — a fact that bears directly on how much the estimate should be trusted.
Specificity omitted entirely. At patient level it was 0.69, which is the number that determines how many unnecessary downstream investigations the tool generates.
Usable
In a meta-analysis of 9 studies drawn from 122 mapped, pooled AI performance for detection of at least 50% coronary stenosis differed by unit of analysis. At vessel level, from 6 contributing studies, sensitivity was 0.81 (95% CI 0.69 to 0.89), specificity 0.88 (0.84 to 0.91) and AUC 0.92 (0.89 to 0.94). At patient level, from 8 studies, sensitivity was 0.94 (0.84 to 0.98) but specificity only 0.69 (0.60 to 0.76), with AUC 0.83 (0.79 to 0.86). Because fewer than 10 studies were pooled, no test for funnel plot asymmetry was performed and small-study effects cannot be excluded.
Both units of analysis are reported, so the reader can see that the headline AUC depends on which one is chosen.
The target condition is defined by a stated stenosis threshold rather than a disease label.
Sensitivity and specificity are given as a pair with intervals, which is what the bivariate model actually estimates.
The denominator of the synthesis — 9 of 122 — is stated, so the reader can weigh the evidence base rather than the point estimate.
The unavailability of an asymmetry test below 10 studies is reported as a limitation instead of being silently omitted.
Both versions are numerically accurate. The first is unusable because it omits the three facts that fix the meaning of an accuracy figure — threshold, unit of analysis and the size of the evidence base — and it omits the specificity, which is where the clinical cost sits.
Planning a review of this type
Eligibility criteria should be written around reportability. They should require paired sensitivity and specificity at a stated threshold with reconstructable counts, a single stated unit of analysis per stratum, a reference standard from a pre-specified list, and external validation if the review’s question concerns clinical accuracy. The search is then run and the surviving studies counted. If fewer than 10 studies remain, the unavailable bias checks are known in advance, and the review can be designed accordingly rather than the limitation being acknowledged retrospectively 49.
Where the yield will not support pooling, the mapping review is the appropriate output and a genuinely useful one. Sengupta and colleagues’ account of the challenges for augmenting intelligence in cardiac imaging in The Lancet Digital Health, the American Heart Association scientific statement in Circulation by Armoundas and colleagues, and Mihan, Pandey and Van Spall’s paper on mitigating AI bias in cardiovascular care all point to the same gap: the field needs structured accounts of what has and has not been validated, in which populations, more than it needs another pooled AUC. The Pubrica meta-analysis service and biostatistics support pages describe how the bivariate and hierarchical models are fitted once a poolable set is available 12,13,18.
Key points
Key points
The binding constraint on meta-analysis of AI in cardiovascular imaging is reportability, not the size of the literature: one recent review mapped 122 studies and pooled 9. Sensitivity and specificity should be pooled jointly with a bivariate or hierarchical model, never as two separate univariate estimates, and each unit of analysis should be analysed separately — patient-level pooled sensitivity was 0.94 with specificity 0.69, whereas vessel-level values were 0.81 and 0.88 in the same review. External validation should be required if the question concerns clinical accuracy; where deep learning and clinicians were compared in the same external sample, across 14 studies the estimates were close to identical. With fewer than 10 studies, the absence of a usable asymmetry test should be reported as a limitation.
Application to your study
Application to your study
- Define eligibility criteria according to what is extractable. Paired sensitivity and specificity at a stated threshold, with counts from which a 2x2 table can be reconstructed — not “reports diagnostic performance”.
- Fix the unit of analysis in the protocol and stratify by it. Patient, vessel and segment results answer different questions and must never be pooled together.
- Record how each study’s threshold was set. Thresholds may be pre-specified, borrowed, or optimised in the same data; the third introduces an optimistic bias that no model removes.
- Make validation design an eligibility criterion, not a covariate. Held-out splits of the development data answer a different question from independent external samples.
- Specify a bivariate model, or hierarchical summary ROC where thresholds differ. The choice should be made before extraction, because it determines what the form must capture.
- Count the included studies before planning bias checks. With fewer than 10 studies, omit the funnel plot asymmetry test and state in the limitations that small-study effects cannot be excluded.
- Extract against CLAIM and appraise with QUADAS-2. CLAIM indicates whether an AI study is reported sufficiently to be pooled; QUADAS-2 indicates whether it is at risk of bias.
- Report according to PRISMA-DTA, and describe it as a reporting guideline rather than a conduct guideline. Target condition, reference standard and unit of analysis are items a reader of this review type needs explicitly.
Frequently asked questions
Because most do not report what a diagnostic accuracy model requires. Liu and colleagues, in Frontiers in Cardiovascular Medicine, mapped 122 studies and pooled 9, with 8 contributing patient-level and 6 vessel-level data. The recurring exclusions are structural: an AUC with no operating threshold, so no 2x2 table can be reconstructed; performance reported on a held-out split of the development dataset rather than an independent sample; an unstated or non-comparable unit of analysis; and reference standards that differ across studies so that the pooled estimate would average across different definitions of the target condition. These are reporting failures, not evidence gaps.
No. Within any study the two are linked by the decision threshold and are typically negatively correlated, so two separate univariate meta-analyses misstate the joint uncertainty and can produce a summary point that lies off any plausible ROC curve. Reitsma and colleagues, in the Journal of Clinical Epidemiology, set out the bivariate random-effects model that estimates both together with a correlation parameter. Harbord and colleagues, in Biostatistics, showed how that formulation relates to the hierarchical summary ROC approach, which is the better target when studies report at different thresholds.
Yes, and in this field it often changes it more than the choice of algorithm. In Liu and colleagues’ review, detection of at least 50% coronary stenosis gave patient-level pooled sensitivity 0.94 (95% CI 0.84-0.98) with specificity 0.69 (0.60-0.76) and AUC 0.83 (0.79-0.86), against vessel-level sensitivity 0.81 (0.69-0.89), specificity 0.88 (0.84-0.91) and AUC 0.92 (0.89-0.94). Patient-level analysis calls a patient positive if any vessel is positive, which raises sensitivity and lowers specificity. Both are legitimate; they answer different questions and must be analysed as separate strata.
The best available comparison indicates that the two perform similarly, and that very few studies support any comparison at all. Liu and colleagues, in The Lancet Digital Health, restricted their head-to-head analysis to the 14 studies that compared deep learning against health-care professionals in the same external-validation sample. Pooled deep-learning sensitivity was 87.0% (95% CI 83.0-90.2) with specificity 92.5% (85.1-96.4), against 86.4% (79.9-91.0) and 90.5% (80.6-95.7) for the professionals — substantially overlapping intervals. Claims of clear superiority generally rest on studies that did not make the comparison on equal footing.
Not for a bivariate or hierarchical accuracy model, because an AUC cannot be converted into the counts those models need. An AUC also summarises performance across all thresholds, including operating points no clinician would use, so two models with identical AUCs can behave very differently at a usable cut-off. If a study reports only an AUC, the options are to contact the authors for the operating-point data, to include the study in a descriptive synthesis only, or to exclude it; the methods should state which option was taken and how many studies it affected.
By stating that it cannot be assessed. Sterne and colleagues, in the BMJ, advise that tests for funnel plot asymmetry should generally not be used below 10 studies, and that the minimum may be substantially higher when heterogeneity is substantial. The plot’s underlying expectation — that with no bias or heterogeneity about 95% of studies fall inside the triangle defined by the fixed-effect estimate plus or minus 1.96 standard errors — carries no force at nine points. Deeks, Macaskill and Irwig have examined the diagnostic-review case specifically. The limitation should be reported; a non-significant test should not be presented as reassurance.
Three, with distinct jobs. QUADAS-2, from Whiting and colleagues in the Annals of Internal Medicine, appraises risk of bias and applicability in the included accuracy studies across patient selection, index test, reference standard, and flow and timing. CLAIM, from Mongan, Moy and Kahn in Radiology: Artificial Intelligence, covers what an AI imaging study should report — data sources, ground truth, data partitions, model and validation design — and is the practical screen for whether a study is poolable at all. PRISMA-DTA, from McInnes and colleagues in JAMA, governs how the review itself is reported.
A mapping review, explicitly identified as such. The review should describe what has been developed, on which populations and scanners, validated how, with what reference standard and at what unit of analysis, and present the reporting gaps as a finding rather than an inconvenience. The field’s own commentary supports this: Sengupta and colleagues on the challenges for augmenting intelligence in cardiac imaging in The Lancet Digital Health, the American Heart Association scientific statement in Circulation, and Mihan, Pandey and Van Spall on mitigating AI bias in cardiovascular care all identify unvalidated and unevenly reported performance as the limiting problem. A clear map is more useful than a pooled estimate built on four studies.
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Pubrica Academy. “Pooling AI Studies in Cardiovascular Imaging: Reasons for the Low Proportion of Poolable Studies.” Pubrica, 9 Oct. 2026, pubrica.com/academy/research/an-overview-of-meta-analysis-inthe-field-of-cardiovascular-imaging-using-artificial-intelligence/.
Pubrica Academy (2026) Pooling AI Studies in Cardiovascular Imaging: Reasons for the Low Proportion of Poolable Studies. Pubrica. Available at: https://pubrica.com/academy/research/an-overview-of-meta-analysis-inthe-field-of-cardiovascular-imaging-using-artificial-intelligence/ (Accessed: 15 October 2026).
Pubrica Academy. “Pooling AI Studies in Cardiovascular Imaging: Reasons for the Low Proportion of Poolable Studies.” Pubrica. October 9, 2026. https://pubrica.com/academy/research/an-overview-of-meta-analysis-inthe-field-of-cardiovascular-imaging-using-artificial-intelligence/
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author = {{Pubrica Academy}},
title = {Pooling AI Studies in Cardiovascular Imaging: Reasons for the Low Proportion of Poolable Studies},
howpublished = {Pubrica},
year = {2026},
month = {oct},
url = {https://pubrica.com/academy/research/an-overview-of-meta-analysis-inthe-field-of-cardiovascular-imaging-using-artificial-intelligence/},
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.
Eligibility and extraction stub for an AI imaging accuracy review
This stub should be completed before searching. It is designed to identify the exclusions that otherwise appear at the synthesis stage, when it is too late to change the question.
AI IMAGING DIAGNOSTIC ACCURACY REVIEW — PROTOCOL STUB
1. TARGET CONDITION (a threshold, not a disease label)
Condition and defining threshold: ______________________
e.g. "at least 50% stenosis on invasive coronary angiography"
Acceptable reference standards (list; anything else is excluded):
a) ______________________ b) ______________________
2. UNIT OF ANALYSIS (strata are analysed separately, never pooled)
[ ] Patient level [ ] Vessel level [ ] Segment level
Studies reporting more than one: handled as a dependency, not as
separate studies. Method: ______________________
3. REPORTABILITY REQUIREMENTS FOR INCLUSION
[ ] Sensitivity AND specificity reported as a pair
[ ] At a stated threshold / operating point
[ ] 2x2 counts given, or reconstructable (TP / FP / FN / TN)
[ ] Unit of analysis explicitly stated by the authors
Studies with AUC only: [ ] excluded [ ] descriptive synthesis only
[ ] authors contacted — log kept
4. VALIDATION DESIGN
[ ] External / out-of-sample validation REQUIRED for inclusion
[ ] Internal validation included, analysed as a separate stratum
Record per study: development cohort, validation cohort, whether
sites/scanners differ, and whether patients overlap.
5. THRESHOLD PROVENANCE (extract for every study)
[ ] Pre-specified before evaluation
[ ] Taken from an earlier study or vendor default
[ ] Optimised within the same data <-- optimistic bias; flag
6. SYNTHESIS MODEL (decide now, it determines the extraction form)
[ ] Bivariate random-effects (common threshold available)
[ ] Hierarchical summary ROC (thresholds differ)
[ ] Descriptive / mapping synthesis only
Confidence interval method, pre-specified: ______________________
7. BIAS AND HETEROGENEITY PLAN
Expected number of poolable studies: ____
[ ] If fewer than 10: NO funnel plot asymmetry test; limitation
stated explicitly in the discussion
Heterogeneity to be described by: ______________________
Pre-specified sources of heterogeneity to tabulate: scanner /
vendor / prevalence / reference standard / threshold / country
8. APPRAISAL AND REPORTING
[ ] QUADAS-2 applied to every included study, with supporting quotes
[ ] CLAIM used to record AI-specific reporting completeness
[ ] Review reported following PRISMA-DTA (reporting, not conduct) Pubrica AcademyWritten and maintained by Pubrica’s subject matter experts. Articles are revised when the underlying standards change, and each article states the date on which it was last reviewed.
How Pubrica can help
Pubrica writes the eligibility criteria for AI imaging accuracy reviews around what the literature reports, so that the poolable yield is known before the search rather than after extraction, and fits the bivariate or hierarchical model once the set exists. The team extracts against CLAIM and appraises with QUADAS-2, and where the evidence will not support pooling it constructs a mapping review and reports the reporting gaps as findings.