Artificial intelligence for imaging-based detection of gallbladder cancer: A systematic review and diagnostic test accuracy meta-analysis

Abstract

BACKGROUND

Early diagnosis of gallbladder cancer (GBC) remains challenging because malignant lesions can mimic benign inflammatory or polypoid gallbladder disease. Artificial intelligence (AI) imaging models have been reported for ultrasound-, computed tomography-, and radiomics-based diagnosis; however, the evidence often conflates clinical validation cohorts with image-level model-development experiments.

AIM

To evaluate the diagnostic test accuracy (DTA) of AI-assisted imaging for detecting GBC and to distinguish patient-level clinical validation evidence from technical benchmark studies.

METHODS

Reporting followed PRISMA 2020 and the PRISMA-DTA extension. Risk of bias and applicability were assessed with a Quality Assessment of Diagnostic Accuracy Studies-2 framework tailored to AI imaging. The primary synthesis used a Reitsma bivariate random-effects model. Robustness was examined using a generalized linear mixed model following the meta-analysis of DTA implementation, leave-one-out analyses, exclusion of internal validation, modality/model subgroup analyses, and Hartung-Knapp random-effects diagnostic odds ratio analysis.

RESULTS

Of 485 records, 32 studies met the inclusion criteria and five patient-level validation datasets suitable for 2 × 2 reconstruction, including four independent, external, or prospective validation settings and one internal non-training validation cohort, comprising 615 patients/cases, were meta-analyzed. In these five validation datasets, AI-assisted imaging was associated with pooled sensitivity of 0.888 (95% confidence interval: 0.834-0.927) and moderate-to-high specificity of 0.838 (95% confidence interval: 0.717-0.914), with a summary receiver operating characteristic area under the curve of 0.921. Prediction intervals were wider for specificity than sensitivity (0.529-0.959 vs 0.785-0.946), indicating less stable false-positive performance across settings. Because only five datasets were available, these estimates should be interpreted as preliminary and context-dependent.

CONCLUSION

AI-assisted imaging showed promising sensitivity and moderate-to-high specificity for GBC detection in a small set of patient-level validation datasets. However, the quantitative evidence rested on only five datasets, included heterogeneous modalities, target contrasts, models, thresholds, and validation designs, and showed greater uncertainty for specificity than sensitivity. Current evidence is most consistent with AI as a triage or second-reader adjunct requiring further external and prospective validation, not as a stand-alone diagnostic replacement.

Key Words: Gallbladder cancer; Artificial intelligence; Deep learning; Radiomics; Diagnostic accuracy; Meta-analysis; Summary receiver operating characteristic

Core Tip: Early diagnosis of gallbladder cancer remains challenging because malignant lesions often mimic benign gallbladder diseases. This study provides the first diagnostic test accuracy meta-analysis focused exclusively on patient-level validation evidence for artificial intelligence-based imaging diagnosis of gallbladder cancer. By separating clinical validation cohorts from image-level development studies, we found that only five datasets were suitable for quantitative synthesis despite 32 eligible publications. Artificial intelligence-assisted imaging achieved high diagnostic performance and may serve as an effective adjunct for lesion triage and radiological decision support, although robust prospective multicenter validation is still required before routine clinical implementation.

INTRODUCTION

Gallbladder cancer (GBC) is an uncommon yet aggressive biliary tract malignancy. Its clinical relevance stems less from its incidence than from delayed presentation, anatomic complexity, limited therapeutic options, and the narrow window for curative resection[1]. Recent mechanistic evidence also links perineural invasion to extracellular vesicle-mediated neuronal necroptosis, reinforcing the aggressive biology of GBC[2]. Early-stage disease is frequently subtle, and malignant gallbladder wall thickening or small masses can be difficult to differentiate from chronic cholecystitis, adenomyomatosis, gallbladder polyps and xanthogranulomatous cholecystitis (XGC)[3].

Imaging plays a central role in the diagnostic pathway for GBC. Ultrasound is typically the first-line imaging modality for gallbladder symptoms or incidental lesions, whereas contrast-enhanced computed tomography (CT) and magnetic resonance imaging (MRI) assist in lesion characterization, staging and surgical planning. However, the imaging appearance depends on lesion morphology, acquisition quality and reader expertise. Even conventional CT and MRI have limited accuracy for certain GBC-related tasks, such as nodal staging, underscoring the need for more reproducible imaging decision support[4].

Artificial intelligence (AI)-based image analysis may improve the consistency of image interpretation by extracting quantitative patterns that are not readily captured by visual assessment. Deep-learning classifiers, transformer models, weakly supervised detection methods, and radiomics-based machine-learning pipelines have been applied to various imaging modalities, including ultrasound, CT, endoscopic ultrasound, and video data. Across medical imaging, however, systematic reviews have indicated that high reported performance frequently stems from internal validation, publicly available image datasets, or non-independent testing rather than from clinically representative external validation[5].

This distinction is particularly critical in GBC. The available literature includes not only prospective clinical studies, but also a substantial number of image-level experiments, overlapping public datasets, segmentation studies, polyp-classification studies, and staging or prognostic analyses among already diagnosed GBC cases. Although valuable for method development, these studies do not provide patient-level diagnostic test accuracy (DTA) evidence. Therefore, a DTA meta-analysis intended for publication must predefine the target condition, index test, reference standard, and unit of analysis prior to data pooling.

Accordingly, the objective of this systematic review was to evaluate the diagnostic accuracy of AI-assisted imaging for the detection of GBC. The primary quantitative synthesis was restricted to independent patient-level validation data or patient-level data that could be reconstructed from the published literature. Secondary objectives were to describe the broader evidence base for AI-based imaging in GBC, examine the robustness of pooled accuracy estimates, and identify methodological requirements for future clinical validation studies.

MATERIALS AND METHODS

Protocol and reporting

The review was registered in the International Prospective Register of Systematic Reviews (CRD42024605966). Reporting followed the PRISMA 2020 statement and the PRISMA-DTA extension for DTA reviews[6-9]. The search was reported in accordance with PRISMA-S[10]. Risk of bias and applicability were assessed with Quality Assessment of Diagnostic Accuracy Studies-2 (QUADAS-2)[11]. Data extraction was informed by Standards for Reporting Diagnostic Accuracy Studies 2015 and the Checklist for Artificial Intelligence in Medical Imaging and its 2024 update, with emphasis on patient spectrum, reference standard, validation independence, threshold selection, and model reporting[12-15]. A Measurement Tool to Assess Systematic Reviews 2 was used only as an internal quality-control framework for the review process, not as a reporting guideline for this DTA review[16].

Clinical question and eligibility criteria

Eligibility criteria were defined according to the participants, index test, reference standard, and target condition framework. The participant inclusion criteria encompassed patients or image datasets evaluated for suspected GBC, gallbladder masses, malignant gallbladder lesions, or clinically relevant differential diagnoses involving GBC. The index test was defined as any AI-assisted image analysis method, including deep learning, radiomics combined with machine learning, computer-aided diagnosis, transformer-based models, or hybrid imaging AI. Eligible imaging modalities included ultrasound, endoscopic ultrasound, CT, MRI, and imaging-video inputs, provided that the target condition was GBC detection.

The target condition for the primary meta-analysis was GBC. Acceptable reference standards included histopathology, cytology, biopsy, surgical pathology, or clearly defined clinical follow-up for benign/non-malignant diagnoses. Studies were eligible for quantitative synthesis only if they reported, or permitted reconstruction of, the numbers of true positives, false positives, false negatives, and true negatives [true positive (TP), false positive (FP), false negative (FN), true negative (TN)] from an independent test set, a prospective clinical test cohort, an external validation cohort, or a clearly separated internal non-training patient-level validation cohort. We did not describe all included datasets as independent external validation, because one eligible dataset was internal rather than external or prospective.

Studies were retained for qualitative synthesis but excluded from the primary meta-analysis if they were reviews, editorials, conference abstracts without extractable primary data, studies limited to segmentation or grading tasks, staging or prognostic studies conducted among patients already diagnosed with GBC, experiments using publicly available image-level datasets without patient-level validation data, polyp-only studies not directly targeting GBC detection, or studies lacking extractable 2 × 2 contingency table data. When multiple algorithms were tested on the same patient cohort, we selected one model to avoid double counting. Priority was given to the prespecified primary validation model, the model most clearly intended as the index imaging test, or the most clinically relevant imaging-only model. Selection was not based solely on the most favorable accuracy estimate. When a study reported data from multiple non-overlapping external cohorts, the cohorts were combined prior to synthesis if the study-level estimate was the intended unit of analysis.

Search strategy and study selection

MEDLINE (via PubMed), EMBASE and Web of Science were searched from database inception to 12 May 2026. The search strategy combined terms for GBC or gallbladder neoplasms, AI or machine learning methods, and diagnostic imaging modalities. The database-specific search strategies are provided in Supplementary Table 1. In addition, reference lists of relevant reviews and included studies were manually screened.

Duplicate records were removed prior to screening. Two reviewers independently screened titles and abstracts, followed by the full texts of potentially eligible reports. Disagreements were resolved through consensus, and when necessary, the full text was re-evaluated against the the participants, index test, reference standard, and target condition eligibility criteria. At the full-text review stage, eligibility was assessed at two levels: Eligibility for qualitative synthesis and eligibility for the more stringent patient-level DTA meta-analysis.

This two-stage process was prespecified as the AI imaging literature frequently reports image-level accuracy in the absence of an independent clinical validation cohort. When potential dataset reuse was identified, only independent patient-level clinical validation data were considered for primary meta-analysis.

Data extraction

Two reviewers independently extracted data using a standardized data extraction form. The extracted variables included first author, publication year, country/setting, study design, validation design and independence, imaging modality, target contrast, algorithm type, split of training/validation/test sets, threshold source and handling, sample size, reference standard, radiologist comparator, availability of TP/FP/FN/TN counts, whether the reported index test was a stand-alone imaging AI model or a combined clinical-imaging model, and reported diagnostic accuracy metrics. For studies included in the meta-analysis, TP, FP, FN, TN, sensitivity, specificity, diagnostic odds ratio (DOR) and area under the curve (AUC) were extracted directly or reconstructed from denominators and reported sensitivity/specificity when unambiguous. When only sensitivity or specificity and the corresponding disease-positive or disease-negative denominator were reported, TP and TN were calculated by rounding sensitivity × disease-positive denominator and specificity × disease-negative denominator to the nearest integer; FN and FP were then derived from the remaining denominators. Reconstructed counts were retained only when they reproduced the published estimates within the reported rounding precision, and all reconstructed 2 × 2 tables were independently checked by two reviewers with disagreements resolved by consensus.

The patient or case was considered as the preferred unit of analysis. Results at the image, slice, lesion, or frame level were not pooled with patient-level data as multiple images from the same patient could artificially inflate precision. When both a stand-alone imaging AI model and a combined clinical-imaging nomogram were reported, the stand-alone imaging AI model was preferred unless the combined model was explicitly presented as the intended index test. For each included dataset, we extracted the threshold used to generate the reported or reconstructed TP, FP, FN, and TN counts. Thresholds were classified as prespecified, internally optimized, externally validated, or unclear when reporting was insufficient. We did not attempt to standardize thresholds across studies, and threshold heterogeneity was considered a source of between-study variability, particularly for specificity. Reconstruction, model-selection, and threshold-handling decisions were documented in Supplementary Table 2.

Risk of bias and applicability

Two reviewers independently assessed risk of bias and applicability using QUADAS-2. The tool was tailored for AI-based imaging studies before assessment. In addition to the standard domains, the index test domain considered independence of the validation data from the training and tuning sets, possible data leakage, post-hoc threshold selection, model multiplicity, and whether patient-level performance was reported. The tailoring rules are provided in Supplementary Table 3. The reporting-guideline mapping is provided in Supplementary Table 4.

Applicability concerns were assessed independently of the risk of bias assessment. Studies restricted to differentiating GBC from XGC were considered clinically relevant to a challenging surgical differential diagnosis but they were considered less directly applicable to the broader population of patients undergoing first-line imaging for indeterminate gallbladder lesions.

Statistical analysis

The primary analysis employed a Reitsma bivariate random-effects DTA model estimated using restricted maximum likelihood in R version 4.2.1 with the R package mada package (version 0.5.11)[17,18]. The model jointly synthesizes the logit-transformed sensitivity and false-positive rate, thereby preserving the correlation between sensitivity and specificity that can arise from study-level thresholds. Exact binomial confidence intervals (CIs) were calculated for the sensitivity and specificity of each individual study.

From the bivariate model, we derived pooled estimates of sensitivity and specificity, LR+, LR-, DOR, summary receiver operating characteristic (SROC) AUC, 95%CIs and 95% prediction intervals. The SROC curve and AUC were derived from the fitted Reitsma model. Particular emphasis was placed on prediction intervals, as they indicate the expected range of diagnostic performance in a new validation setting.

None of the primary 2 × 2 tables contained zero cells; therefore, continuity correction was not required for the bivariate model. For study-level DOR calculations, a 0.5 continuity correction was prespecified only in the presence of a zero cell. Robustness analyses comprised a bivariate generalized linear mixed model fitted with the lme4 package (version 1.1-32), following the MetaDTA implementation, leave-one-out analyses, exclusion of internal validation, deep-learning-only analysis, ultrasound-only analysis, and a random-effects DOR model with Hartung-Knapp adjustment fitted using the metafor package (version 3.8-1)[19]. Subgroup analyses were considered exploratory because of the small number of datasets and were used to describe patterns rather than support definitive modality- or architecture-specific comparisons.

Threshold effects were explored by examining the correlation between logit-transformed sensitivity and the logit false-positive rate. Formal assessment of publication bias or small-study effects was not undertaken, as fewer than 10 studies were available. Formal GRADE-DTA certainty rating was not performed for the same reason and because the included studies were heterogeneous with respect to validation design and target contrast; considerations regarding the certainty of evidence are therefore discussed narratively[20]. No post-search update was performed after 12 May 2026.

Clinical impact analysis

To facilitate clinical interpretation of the pooled estimates, post-test consequences were projected across a range of illustrative pre-test probabilities. For each assumed prevalence, the expected numbers of false negatives and false positives, along with the positive predictive value and negative predictive value, per 1000 tested patients were calculated from the pooled sensitivity and specificity. These scenarios were intended to show how false-positive and false-negative consequences may vary across plausible referral or diagnostic settings; they should not be interpreted as prevalence estimates for screening populations, general surgical practice, or tertiary hepatobiliary referral cohorts, and they do not substitute for prospective decision-curve analysis.

RESULTS

Study selection

The search identified 485 records: 84 from EMBASE, 85 from PubMed, and 316 from Web of Science. After removing 47 duplicates, 438 records underwent title and abstract screening and 373 were excluded, leaving 65 full-text articles for detailed assessment.

Of these, 33 full-text articles were excluded: Six were abstract-only reports, five did not use medical imaging, 13 did not evaluate GBC or a relevant gallbladder neoplasm endpoint, and nine did not evaluate an AI model. Consequently, 32 studies were retained for qualitative synthesis. Of these, 27 were excluded from the primary quantitative synthesis because they lacked independent patient-level 2 × 2 data, used image-level public datasets, addressed adjacent endpoints, or represented reviews/editorials rather than primary diagnostic validation studies. Five studies met the stricter criteria for the primary DTA meta-analysis. The study-selection process is shown in Figure 1.

Figure 1 Study selection flow. The diagram follows PRISMA 2020 flow-logic and distinguishes qualitative inclusion from quantitative diagnostic test accuracy eligibility. DTA: Diagnostic test accuracy; GBC: Gallbladder cancer; AI: Artificial intelligence.

Study characteristics

The qualitative evidence showed a rapidly expanding but methodologically heterogeneous field. Ultrasound was the most common imaging modality, followed by CT; other studies used mixed imaging, endoscopic ultrasound, high-resolution ultrasound, or ultrasound video. Methods ranged from convolutional neural networks, transformer-based classifiers, weakly supervised detection and object-detection pipelines to radiomics with XGBoost or other machine-learning classifiers and hybrid clinical-imaging models.

The five studies contributing to the primary synthesis included 615 patients/cases[21-25]; the corresponding patient-level diagnostic accuracy data are summarized in Table 1. Two studies used computed tomography and three used ultrasonography. Four evaluated deep-learning models and one evaluated an ultrasound radiomics/machine-learning model. Validation designs comprised one prospective clinical test cohort, two external validation settings, one independent test set, and one internal non-training validation cohort; therefore, the quantitative evidence should not be characterized uniformly as independent external validation. Target contrasts included GBC vs benign gallbladder lesions, GBC vs non-GBC, GBC vs XGC, and gallbladder carcinoma vs benign gallbladder masses. These target contrasts differ clinically: XGC-focused studies address a difficult mimic of GBC, whereas broader benign-versus-malignant or GBC-versus-non-GBC contrasts may better approximate initial diagnostic imaging populations.

Table 1 Patient-level diagnostic accuracy data included in the primary meta-analysis.

Ref.	Country/design	Index test	Target/reference	Validation	N	TP/FN	TN/FP	Sensitivity	Specificity
Xiang et al[21], 2024	China; retrospective	CT ResNet50	GBC vs benign lesions; pathology	Internal non-training validation	84	28/5	39/12	0.848 (0.681-0.949)	0.765 (0.625-0.872)
Gupta et al[22], 2024	India; prospective	US deep learning	GBC vs non-GBC; pathology/cytology/biopsy/follow-up	Prospective test	273	169/14	67/23	0.923 (0.875-0.958)	0.744 (0.642-0.831)
Zhang et al[23], 2024	China; retrospective external validation	CT FCovResNet18	GBC vs XGC; pathology	External validation	74	48/4	18/4	0.923 (0.815-0.979)	0.818 (0.597-0.948)
Gupta et al[24], 2024	India; prospective independent test	US RadFormer	GBC vs XGC; pathology/cytology	Independent test	80	48/7	21/4	0.873 (0.755-0.947)	0.840 (0.639-0.955)
Wang et al[25], 2023	China; prospective multi-institutional	US XGBoost radiomics	GBC vs benign masses; pathology	External validation	104	18/4	79/3	0.818 (0.597-0.948)	0.963 (0.897-0.992)

Sensitivity and specificity are shown as point estimate (95% confidence interval). Extended model-selection rationale, threshold handling, validation design, and target-contrast details are provided in Supplementary Table 2. TP: True positive; FN: False negative; TN: True negative; FP: False positive; CT: Computed tomography; US: Ultrasonography; GBC: Gallbladder cancer; XGC: Xanthogranulomatous cholecystitis.

Restricting the meta-analysis to these five datasets reduced apparent breadth but improved clinical interpretability. Several excluded studies reported high image-level accuracy, but many used the same public GBC ultrasound dataset or analyzed multiple images from the same patient. Pooling those studies with patient-level clinical cohorts would have treated technical benchmarks as independent clinical evidence and artificially narrowed CIs.

In brief, most AI imaging studies were not pooled because they did not provide independent patient-level 2 × 2 diagnostic data, used public image-level benchmark datasets, addressed adjacent segmentation, staging, prognostic, or polyp-classification endpoints, or lacked a clinically interpretable validation cohort.

Risk of bias

Concerns about risk of bias were concentrated in patient selection and index test reporting. Patient selection was judged to be at high risk of bias or to raise some concerns when studies used enriched case-control contrasts, narrow differential diagnoses, or internal validation cohorts that may not reflect the full clinical spectrum of suspected GBC. Concerns about the index test arose when threshold selection, model selection, or tuning procedures were insufficiently transparent.

Concerns about the reference standard were generally lower because most quantitative studies used pathology, cytology, biopsy, or clinically established follow-up. Applicability varied by clinical question. Prospective ultrasound studies of suspected gallbladder lesions were more directly applicable to triage. Studies enriched for XGC were clinically important because XGC is a challenging inflammatory mimic of GBC, but they may not represent the full spectrum of patients undergoing initial gallbladder imaging. Applicability to broader benign, malignant, and incidental gallbladder lesion populations therefore remains uncertain.

Judgements are domain-level QUADAS-2 ratings. Applicability was judged against broad imaging-based GBC detection; studies limited to GBC vs XGC were clinically relevant but less applicable to unselected gallbladder-lesion populations. AI-specific tailoring rules, including validation independence, threshold handling, and model-selection transparency, are provided in Supplementary Table 3. The study-level judgements are summarized in Table 2.

Table 2 Quality Assessment of Diagnostic Accuracy Studies-2 risk-of-bias and applicability summary for the five quantitative studies.

Ref.	Patient selection	Index test	Reference standard	Flow/timing	Applicability concern
Xiang et al[21], 2024	High	Unclear	Low	Low	Some concerns
Gupta et al[22], 2024	Low	Low	Low	Low	Low
Zhang et al[23], 2024	High	Low	Low	Low	High
Gupta et al[24], 2024	Some concerns	Low	Low	Low	High
Wang et al[25], 2023	Low	Unclear	Low	Low	Low

Primary diagnostic accuracy

The bivariate model estimated a pooled sensitivity of 0.888 (95%CI: 0.834-0.927) and a pooled specificity of 0.838 (95%CI: 0.717-0.914). In the available datasets, AI-assisted imaging identified most GBC-positive cases while maintaining moderate-to-high specificity. However, these estimates are preliminary because they were derived from only five heterogeneous validation datasets. The 95% prediction interval was narrower for sensitivity (0.785-0.946) than for specificity (0.529-0.959), indicating greater between-study variation in false-positive performance. Study-level and pooled sensitivity and specificity estimates are shown in Figure 2A.

Figure 2 Forest plots of diagnostic test performance. A: Forest plot of sensitivity and specificity. Individual-study intervals are exact binomial 95% confidence intervals. The pooled estimate was derived from the Reitsma bivariate random-effects model based on five datasets; B: Diagnostic odds ratio (DOR) forest plot. Estimates are shown on a logarithmic scale. The pooled DOR was derived from the bivariate summary-point simulation; the dashed reference line represents DOR = 1. US: Ultrasonography; CT: Computed tomography; XGC: Xanthogranulomatous cholecystitis.

At the study level, sensitivity ranged from 0.818 to 0.923 and specificity ranged from 0.744 to 0.963. The highest specificity was observed in the external ultrasound radiomics study, whereas the prospective ultrasound deep-learning test cohort had the largest sample size and contributed substantially to the clinical representativeness of the pooled estimate. The CT studies showed high sensitivity but differed in validation design and target contrast.

The pooled positive likelihood ratio was 5.760 (95%CI: 3.220-9.940), indicating that a positive AI result increased the post-test odds of GBC by approximately sixfold. The pooled negative likelihood ratio was 0.136 (95%CI: 0.093-0.190), indicating that a negative AI result substantially reduced, but did not eliminate, the probability of GBC. The pooled DOR was 43.200 (95%CI: 22.700-74.800), and the Hartung-Knapp DOR sensitivity analysis yielded a similar estimate of 36.882 (95%CI: 18.618-73.064). The study-level and pooled diagnostic odds ratio estimates are shown in Figure 2B.

The SROC AUC was 0.921, suggesting good discrimination within the available validation datasets, but with uncertainty due to the small number of studies and heterogeneous clinical settings. Study points clustered in the high-sensitivity region; model uncertainty is therefore reported through prediction intervals in the text rather than drawn as contours. The estimated random-effects correlation was not emphasized because it was derived from only five datasets and may be unstable. The corresponding summary receiver operating characteristic curve is shown in Figure 3.

Figure 3 Summary receiver operating characteristic curve from the Reitsma bivariate model. Model uncertainty is reported in the text rather than drawn as contours because k = 5. Study points are plotted in receiver operating characteristic space, and the summary point is shown as a red diamond. Confidence and prediction contours were omitted to avoid overinterpreting model-based uncertainty from five datasets. CT: Computed tomography.

Robustness analyses

A MetaDTA-style generalized linear mixed model produced concordant point estimates: Sensitivity 0.892 (95%CI: 0.839-0.929) and specificity 0.846 (95%CI: 0.734-0.917). The model fit was singular, as expected when a hierarchical DTA model is estimated from very few studies and the random-effects correlation approaches the boundary. Therefore, concordance between models should be interpreted as descriptive support for the primary estimates rather than evidence of stable variance-covariance estimation.

Excluding the internal validation study yielded sensitivity 0.891 (95%CI: 0.825-0.935) and specificity 0.860 (95%CI: 0.708-0.940). This did not materially change the point estimates, but the sensitivity analysis remains underpowered and should not be interpreted as proving robustness. The deep-learning-only analysis produced sensitivity 0.902 (95%CI: 0.859-0.933) and specificity 0.771 (95%CI: 0.703-0.827), and the ultrasound subgroup produced sensitivity 0.881 (95%CI: 0.788-0.937) and specificity 0.876 (95%CI: 0.668-0.961). These subgroup estimates are presented descriptively; the small number of datasets precludes reliable inference about modality- or model-specific performance. These robustness analyses are summarized in Figure 4.

Figure 4 Robustness analyses. Pooled sensitivity and specificity are shown after leave-one-out exclusions and selected dataset restrictions. Numbers indicate contributing datasets; vertical orange lines mark the primary pooled estimates.

The exploratory threshold-effect analysis, measured as the correlation between logit sensitivity and logit false-positive rate, yielded Spearman’s ρ = 0.700 (P = 0.188). This result is compatible with a threshold effect, but the analysis was underpowered. Formal tests for publication bias or small-study effects were not performed because only five studies were included.

Clinical impact

Using the pooled point estimates in illustrative scenarios, projected false negatives per 1000 tested patients increased from 6.0 at a 5% pre-test probability to 56.0 at a 50% pre-test probability, whereas false positives decreased from 154.0 to 81.0. Negative predictive value remained high in lower-prevalence scenarios, whereas positive predictive value increased as pre-test probability rose. These calculations show the expected direction of clinical consequences under selected assumptions rather than setting-specific screening or referral prevalence. The projected clinical consequences are shown in Figure 5.

Figure 5 Clinical impact projection. False negatives, false positives, positive predictive value, and negative predictive value per 1000 tested patients are shown across illustrative pre-test probabilities. Shaded ranges use marginal 95% confidence intervals; scenarios are illustrative and are not prevalence estimates.

These projections frame AI as a context-dependent decision aid. In low-prevalence or screening-like settings, a negative AI result may support prioritization, but false positives could still increase downstream imaging and referral burden. In enriched specialist settings, a positive AI result carries greater post-test weight, while false negatives have greater clinical consequences. AI outputs should therefore be interpreted alongside clinical context, conventional imaging features, and multidisciplinary review.

DISCUSSION

Principal findings

This systematic review found that AI-assisted imaging had promising sensitivity for GBC detection when the synthesis was restricted to patient-level validation data suitable for 2 × 2 diagnostic reconstruction. A central limitation is that the evidence base narrowed from 32 eligible studies to only five patient-level datasets, underscoring that the pooled estimates reflect a small and selected validation evidence base. The low negative likelihood ratio and SROC AUC support a potential role in triage or second-reader workflows, particularly in pathways where missed GBC has serious consequences, but the evidence remains preliminary.

The pooled specificity was also moderate-to-high, but it was less stable than sensitivity. This is important because false-positive AI outputs can lead to additional cross-sectional imaging, repeat ultrasound, invasive diagnostic procedures, surgical referral, patient anxiety, and healthcare resource utilization. The wide prediction interval for specificity indicates that future validation studies may yield substantially different false-positive rates, particularly if case mix, lesion spectrum, imaging acquisition, or reference standards differ from those of the included studies.

Interpretation in relation to similar evidence

The pattern of findings is consistent with recent DTA meta-analyses of AI imaging. Comprehensive reviews of medical imaging AI have shown that deep-learning systems can achieve high diagnostic accuracy but that external validation, patient-level reporting, and transparent threshold selection are often limited[5]. Ultrasound-based AI reviews in ovarian tumors and lymph node diagnosis similarly emphasize the need to separate training and internal validation from independent test data and to report the numbers of TP, FP, FN and TN in a clinically interpretable manner[26,27].

The hepatobiliary context adds two further considerations. First, radiomics and AI studies in intrahepatic cholangiocarcinoma show that quantitative imaging biomarkers can be diagnostically informative, but performance depends on segmentation, imaging modality, model design and validation quality[28]. Second, a conventional imaging meta-analysis in GBC demonstrates that even established CT and MRI pathways have limitations in specific diagnostic tasks[4]. Against that background, AI should be viewed not as a replacement for expert radiology, but as a candidate method for improving consistency, triage and reader support.

Why the evidence base narrows from 32 to 5 studies

A central contribution of this review is the explicit separation of AI method development from patient-level diagnostic validation. Thirty-two studies were relevant to AI in gallbladder imaging, but only five provided data suitable for the primary patient-level DTA meta-analysis. This narrowing protects against overstating certainty from image-level or development-set results, but it also means that the pooled estimates should be considered preliminary and hypothesis-generating. Image-level experiments, public-dataset benchmarks, and model-development studies can advance technical progress, but they do not carry the same evidentiary weight as prospective, external, or otherwise clearly separated patient-level validation.

The distinction also affects the interpretation of model performance. Public image datasets can enable reproducible algorithm comparisons, yet they may contain curated images, repeated patients, standardized acquisitions, and a limited disease spectrum. Prospective or external clinical cohorts instead capture real-world variability, imperfect image quality, and heterogeneous benign mimics. Diagnostic performance intended for clinical deployment must therefore be demonstrated in those settings.

Clinical implications

The most defensible near-term role for AI is adjunctive rather than autonomous. In first-line ultrasound, AI may help flag suspicious gallbladder lesions for expert review or cross-sectional imaging. In CT-based characterization, AI may assist in distinguishing GBC from inflammatory mimics such as XGC. In multidisciplinary pathways, AI outputs should be incorporated as one component of structured imaging assessment rather than treated as a final diagnosis. These use cases should be evaluated separately because ultrasound triage, CT-based mimic differentiation, and specialist multidisciplinary review involve different case mixes, downstream actions, and acceptable sensitivity-specificity trade-offs.

Clinical deployment should be guided by local disease prevalence and intended use. A high-sensitivity tool may be useful for triage when missed cancer carries severe consequences, but the acceptable specificity threshold depends on downstream diagnostic capacity and the harms of false-positive workup. A tool intended to support surgical decision-making must demonstrate reliable specificity and calibration in populations with a high pre-test probability of disease. The current evidence justifies further validation of these use cases but does not establish readiness for stand-alone clinical deployment.

Implications for future research

Future studies should be designed as diagnostic accuracy studies rather than as model-development reports alone. At a minimum, reporting should include patient-level denominators, TP, FP, FN, TN, along with CIs, prespecified operating thresholds, methods for handling missing data, reference standard definitions, and information on whether validation images or patients were independent from training and tuning. Studies should avoid reporting only accuracy or AUC because these metrics do not show the clinical trade-off between missed cancers and false positives.

The next generation of evidence should include multicenter prospective validation, external validation across scanners and institutions, predefined subgroup analyses by modality and lesion spectrum, calibration assessment, decision-curve or clinical impact analysis, and comparison with radiologists or standard-of-care pathways. Reporting should align with PRISMA-DTA, Standards for Reporting Diagnostic Accuracy Studies, Checklist for Artificial Intelligence in Medical Imaging, and QUADAS-2 principles[8,9,11-15]. When feasible, model weights, code, inference thresholds, and de-identified validation protocols should be shared to enhance reproducibility.

Limitations

This article has several limitations. First, only five patient-level validation datasets were eligible for quantitative synthesis, including one internal non-training validation cohort. This limited precision, widened prediction intervals, and precluded reliable meta-regression or formal testing for publication bias. The pooled estimates should therefore be interpreted as preliminary, hypothesis-generating evidence rather than definitive clinical diagnostic performance. Second, some contingency tables were reconstructed from reported denominators and diagnostic accuracy measures rather than extracted directly from published confusion matrices. Although reconstruction was only performed when the data permitted unambiguous derivation, direct reporting would be preferable. Third, the included studies varied in imaging modality, target contrast, AI architecture, threshold handling, validation design, and clinical setting. In particular, XGC-focused comparisons address a different use case from broader benign-versus-malignant or GBC-versus-non-GBC diagnostic imaging populations. The pooled estimate should therefore be interpreted as an overall summary of current patient-level evidence, not as a single expected performance value for every clinical scenario. Fourth, the available data did not allow robust comparison with radiologist performance, combined reader-AI performance, or standard diagnostic pathways. Fifth, publication and selective-reporting bias could not be excluded because small, high-performing AI studies may be more likely to be published. Finally, the search was current to 12 May 2026 and was not updated afterward; very recent external validation studies published after that date may not have been captured.

Finally, the qualitative synthesis was broader in scope than the quantitative evidence. Several studies addressed gallbladder polyp classification, image segmentation, serosal involvement, or general gallbladder disease classification. These studies were relevant to the field but were not directly aligned with the primary GBC diagnostic endpoint. Their exclusion from pooling reduces the statistical power of the quantitative analysis but improves clinical coherence.

CONCLUSION

Overall, AI-assisted imaging showed promising diagnostic performance for GBC in limited patient-level validation datasets, but the evidence remains preliminary. Heterogeneity in modality, target contrast, model type, threshold handling, and validation design limits generalizability. Current evidence supports further external and prospective validation and suggests a potential adjunctive role in triage or second reading, particularly in ultrasound-first pathways and difficult benign-malignant differentials, but it does not justify stand-alone clinical deployment.