This systematic review was conducted following the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) 2020 guidelines (Checklist 1). The review was not prospectively registered due to time constraints. A detailed protocol was developed a priori and is available from the corresponding author upon request.

This systematic review analyzed published data without direct human interaction. Therefore, institutional review board approval was not required per standard guidelines.

We searched 4 electronic databases on November 24, 2025: PubMed/MEDLINE (via the National Center for Biotechnology Information interface), Scopus (via the Elsevier platform), IEEE Xplore (via the IEEE platform), and Web of Science Core Collection (via the Clarivate platform). Gray literature, trial registers, and preprint servers were not searched. Neither backward citation searching nor forward citation searching was performed.

Search strategies combined 4 concept blocks using Boolean AND operators: (1) AI or ML technology terms (eg, “artificial intelligence,” “machine learning,” “deep learning,” “neural networks,” and “computer vision”); (2) clinical decision support terms (eg, “decision support,” “clinical decision support,” “CDSS,” “computer-aided detection,” and “diagnostic aids”); (3) medical imaging modality terms (eg, “ultrasound,” “dermoscopy,” “fundus imaging,” “microscopy,” “x-ray,” and “clinical photography”); and (4) point-of-care context terms (eg, “point-of-care,” “POCUS,” “bedside,” “handheld,” “portable,” “mobile health,” and “telemedicine”). No language restrictions were applied to the database searches, although only English-language reports were eligible for inclusion. Searches were limited to studies published from January 2018 onward to capture the recent era of deep learning applications in medical imaging. The search strategy was adapted to each database’s syntax requirements, with PubMed incorporating MeSH (Medical Subject Headings) terms combined with title or abstract keywords, Scopus using TITLE-ABS-KEY field tags, IEEE Xplore using explicit singular or plural forms, and Web of Science using topic search field tags. Complete search strategies for all databases, including exact queries and filters, are provided in Multimedia Appendix 1.

Screening and selection followed a 2-stage process. Search results were imported into Zotero (Corporation for Digital Scholarship) for deduplication and reference management. A total of 2 reviewers independently screened titles and abstracts using Rayyan (Rayyan Systems Inc) software with anonymous dual review. Studies meeting the inclusion criteria or with uncertain eligibility proceeded to full-text review. A total of 2 reviewers independently assessed full texts, with disagreements resolved through discussion. No automation tools were used to support title or abstract screening or full-text assessment; human reviewers made all screening decisions. When multiple exclusion criteria were applied to a single study, the primary reason for exclusion was recorded following a prespecified hierarchy: first, study type, language, date, and availability issues; then, population characteristics; and finally, intervention criteria.

A representative sample of excluded studies, along with the reasons for exclusion, is provided in Multimedia Appendix 2.

A total of 2 reviewers independently extracted data from each included study using a standardized form encompassing 18 prespecified sections: (1) study registry, (2) study design, (3) population, (4) point-of-care setting, (5) operator characteristics, (6) AI system, (7) AI output, (8) imaging, (9) reference standard, (10) diagnostic performance, (11) comparator, (12) explainability, (13) clinical outcomes, (14) limitations, (15) task-shifting, (16) integration, (17) QUADAS-2 summary, and (18) derived metrics (Multimedia Appendix 3). Disagreements were resolved through discussion. No automation tools were used in the data extraction process. Study authors were not contacted to obtain or confirm missing or unclear data. Unreported items were coded as “not reported,” and strict anti-inference rules prohibited any imputation or assumption of unreported data.

Data extracted from the 18 prespecified sections of the standardized form were organized for synthesis into thematic domains encompassing study characteristics, point-of-care context, AI system features, diagnostic performance, and clinical impact.

Extracted variables encompassed study characteristics (author, year, country, setting, design, sample size, condition, and prevalence), point-of-care context (facility type, geographic setting, and World Bank income classification), operator characteristics (profession, experience, and training), and AI system features (architecture, regulatory status, modality, device type, and processing capability).

Primary outcomes were sensitivity and specificity; secondary outcomes included area under the receiver operating characteristic curve (AUC), positive predictive value (PPV), and negative predictive value (NPV), with 95% CIs where reported. For studies reporting multiple thresholds, we extracted values at the author-identified optimal threshold. No amendments were made to outcome definitions from the a priori protocol.

Additional items included comparator characteristics, explainability assessment (technique, user presentation, understanding, and decision impact), clinical outcomes (workflow, referrals, time, cost, and patient outcomes), task-shifting demonstrations, and training requirements.

Methodological quality was assessed using QUADAS-2 across 4 domains: patient selection, index test, reference standard, and flow and timing. Overall risk of bias (RoB) was synthesized using predefined criteria: low (all domains low), low-moderate (1 unclear), moderate (1 high or multiple unclear), high (2 or more high), or very high (3 or more high or critical flaws). A total of 2 reviewers independently assessed each study, with disagreements resolved through discussion. Study authors were not contacted; no automation tools were used.

The results are presented in descriptive tables and figures including a PRISMA flow diagram, geographic distribution map, task-shifting illustration, forest plots grouped by condition, XAI cascade and clinical impact pyramid distributions, and QUADAS-2 visualizations.

A total of 2 frameworks were developed to systematically characterize evidence gaps not captured by standard diagnostic accuracy reporting. The first framework, an XAI implementation cascade (levels 0‐5), categorizes the depth of explainability implementation from nonmention through clinical user exposure to evaluation of whether explanations influenced clinical decisions. The second framework, a clinical impact pyramid (levels 0‐5), categorizes the maturity of clinical evidence from technical validation toward demonstration of health benefit. Diagnostic accuracy (level 0) is positioned at the pyramid’s base because, while foundational to any AI diagnostic system, it represents the least mature form of clinical evidence—demonstrating that a system works technically without establishing whether it improves patient outcomes. Process outcomes such as workflow efficiency and time to diagnosis occupy level 1. Clinical actions documented based on AI recommendations constitute level 2. Patient outcomes measured represent level 3, health system impact represents level 4, and population health outcomes represent level 5. These frameworks enabled systematic identification of evidence gaps and regulatory alignment assessment.

Reporting bias was assessed qualitatively, given the narrative synthesis approach and substantial heterogeneity that precluded meta-analysis. The assessment examined (1) literature search comprehensiveness, including gray literature coverage; (2) patterns potentially indicating publication bias, including commercial system predominance and small-study effects; and (3) selective outcome reporting completeness for diagnostic accuracy metrics (sensitivity, specificity, AUC, PPV, and NPV) and precision estimates (95% CIs). Formal statistical methods for detecting publication bias (eg, Deeks funnel plot asymmetry testing) were not feasible; however, a qualitative assessment was conducted to characterize potential biases that may have affected the evidence base. A total of 2 reviewers independently assessed the reporting bias, with disagreements resolved through discussion.

The certainty of evidence was assessed using the GRADE (Grading of Recommendations, Assessment, Development, and Evaluation) framework, adapted for diagnostic test accuracy studies. Following GRADE guidance, diagnostic accuracy studies are initiated at a high level of certainty. They are rated down across 5 domains: RoB (informed by QUADAS-2 assessments), indirectness (applicability and heterogeneity), inconsistency (variation in diagnostic performance), imprecision (CI width and sample size), and publication bias (completeness of literature search and selective reporting). Each domain was rated as no serious concern (no downgrade), serious concern (downgrade by 1 level), or grave concern (downgrade by 2 levels). Overall certainty was determined by summing downgrades across domains, with final ratings of high (⊕⊕⊕⊕), moderate (⊕⊕⊕◯), low (⊕⊕◯◯), or very low (⊕◯◯◯). A total of 2 reviewers independently assessed the certainty of evidence for each outcome, with disagreements resolved through discussion.

The systematic search yielded 2113 records across 4 databases: Scopus (n=993), Web of Science (n=422), IEEE Xplore (n=408), and PubMed (n=290). After removing 707 duplicates, 1406 unique records underwent title and abstract screening.

Title and abstract screening excluded 1245 records. The most frequent exclusion reasons were wrong study type (n=319, including reviews and editorials), wrong imaging modality (n=224, such as computed tomography or magnetic resonance imaging), lack of clinical validation (n=181), absence of point-of-care setting validation (n=153), and publication before 2018 (n=144). Additional exclusions included studies without an AI or ML component (n=70), retrospective designs (n=59), device development studies only (n=40), studies without clinical decision support output (n=37), nonhuman studies (n=14), and studies with missing abstracts (n=4).

All 161 records identified for full-text review were successfully retrieved; no potentially eligible reports were unretrievable. Full-text assessment excluded 141 studies, primarily due to the lack of point-of-care setting validation (n=40), device development without clinical implementation (n=35), and retrospective designs (n=33). Other exclusions included no clinical decision support output (n=7), unavailable full text (n=7), lack of clinical validation (n=7), wrong imaging modality (n=5), wrong study type (n=3), pre-2018 publication (n=2), nonhuman participants (n=1), and no AI or ML component (n=1). Twenty studies met all inclusion criteria and were included in the final synthesis (Figure 1). Human reviewers made all screening and selection decisions without the use of automation tools.

A representative sample of 30 borderline cases excluded at full-text review is provided in Multimedia Appendix 2. These studies met many criteria but failed to meet specific requirements, most commonly due to a retrospective design with AI applied to historical data (10/30, 33.3%) and the development of algorithms without subsequent clinical implementation (8/30, 26.7%). Other reasons included aspirational point-of-care claims without demonstrated deployment (5/30, 16.7%), specialist settings (3/30, 10%), and validation at a tertiary center only (2/30, 6.7%).

The 20 included studies enrolled approximately 78,000 patients across 15 countries (Table 1). The temporal distribution demonstrated an accelerating research trajectory, with 85% (17/20) of studies published in 2023 or later.

The geographic distribution spanned 4 continents, with Asia and Europe each contributing 30% (6/20) of the studies, followed by Africa and North America, each at 20% (4/20; Figure 2). India 15% (3/20), China 10% (2/20), Mexico 10% (2/20), and the United Kingdom 10% (2/20) contributed multiple studies; single studies originated from 11 additional countries. Notably, no studies were conducted in South America or Oceania.

World Bank income classification (Table 2) revealed substantial research activity in resource-limited settings, with 60% (12/20) of studies conducted outside HICs, including 2 in LICs (Sudan and Madagascar).

Sample sizes ranged from 32 to 30,405 participants (median 375, IQR 158-2879). The most extensive studies by sample size were Heydon et al [15] (n=30,405) evaluating diabetic retinopathy in the United Kingdom screening program, Jayaraman et al [18] (n=25,598) evaluating tuberculosis in Indian mobile units, and Marquez et al [22] (n=5740) evaluating tuberculosis in the Philippines. The clinical domains were diverse, including tuberculosis (5/20, 25%), breast cancer (3/20, 15%), deep vein thrombosis (DVT) (2/20, 10%), and diabetic retinopathy (2/20, 10%). Single studies addressed cardiac pathology, cervical cancer, developmental hip dysplasia, malaria, ophthalmic emergencies, parasitic infections, pressure ulcers, and melanoma. Disease prevalence ranged from 2% (hip dysplasia) to 70% (helminthiases).

Point-of-care settings varied substantially across the 20 studies, reflecting the versatility of AI-assisted imaging (Table 2). Primary care facilities predominated (6/20, 30%), followed by community screening programs (4/20, 20%), general hospitals (3/20, 15%), emergency departments (2/20, 10%), and mixed settings (2/20, 10%). Deployments also included mobile diagnostic units [18], home care [14], and remote rural villages [27], demonstrating adaptability to decentralized health care delivery. Geographic settings, where reported, revealed that 25% (5/20) of studies were conducted in rural areas, 5% (1/20) in urban settings, and 70% (14/20) did not specify a geographic context.

A central finding of this review is evidence for task-shifting enabled by AI-assisted imaging (Figure 3). A total of 13 (13/20, 65%) studies explicitly demonstrated task-shifting from specialists to nonspecialist health care workers, transferring tasks traditionally performed by radiologists, cardiologists, dermatologists, and ophthalmologists to primary care physicians, nurses, community health workers, and medical students. The operator types included primary care physicians (n=4), nurses or community health workers (n=4), health care workers without prior imaging experience (n=4), x-ray technicians (n=3), and medical students (n=2). Further, 7 studies did not specify the primary operator. Notably, most task-shifted operators had no prior experience with the specific imaging modality before training.

Training requirements varied across studies reporting training details (13/20, 65%). Among studies reporting training details, the duration ranged remarkably from 30 minutes to 6 months (median 1 h; n=6 studies reporting specific numeric durations); IQR was not calculated due to the small number of studies and extreme right skew of the distribution. A total of 6 of 13 (46%) studies achieved acceptable diagnostic performance with training programs of 1 hour or less. Training formats included brief PowerPoint (Microsoft Corp) presentations (n=4), app-based training (n=2), in-person demonstrations (n=3), hands-on supervised practice (n=4), and online training sessions (n=2).

No clear dose-response relationship emerged between training duration and diagnostic performance. Studies with 30‐60 minutes of training achieved sensitivities of 100%, comparable to or exceeding those with longer programs. Love et al [20] reported a medical student achieving 100% sensitivity and specificity for breast mass classification after 30 minutes of PowerPoint training. Avgerinos et al [10] demonstrated that nonultrasound-trained providers achieved 100% sensitivity and 95.7% specificity for DVT after 1 hour of app training. Similarly, Nothnagel and Aslam [24] found that health care professionals without ultrasound training achieved 100% sensitivity and 90.6% specificity for DVT after 1 hour. Berg et al [11] reported that research coordinators achieved 86% sensitivity for breast cancer triage after 30 minutes of training, although specificity was lower (33%) with portable devices.

Among studies where task-shifted performance was explicitly compared to specialists or predefined thresholds, 62% (8/13) demonstrated performance comparable to specialists, 31% (4/13) met predefined acceptable thresholds, and only 8% (1/13) showed performance below acceptable levels.

Having characterized this study’s settings and operators, we next examined the AI systems themselves. The 20 studies evaluated 18 distinct AI systems (Table 3): commercial products (12/20, 60%), research prototypes (7/20, 35%), and 1 open-source system (Kankanet). Commercial systems included ThinkSono Guidance, Koios DS, EyeArt, MEDO-Hip, Genki, Breast AI, qXR, Dermalyser, and SELENA+.

Deep learning architectures dominated (18/20, 90%), with 1 hybrid system combining deep learning and gradient boosting (EE-Explorer), and 1 study not reporting its architecture. No studies used traditional ML approaches alone. Specific architectures included convolutional neural networks of unspecified type (n=7), U-Net or UNet-like architectures for segmentation tasks (n=3), Inception-v3 for classification (n=2), and individual studies using DenseNet, EfficientNet, ResNet-101, SSD with MobileNet, and Faster R-CNN.

Regulatory status was largely unreported, representing a critical gap. Only 25% (5/20) of studies reported any regulatory approval: FDA clearance for MEDO-Hip [17], CE (conformité européenne) marking for ThinkSono Guidance (Class IIb [10] and Class I [24]) and EyeArt [15], and South African SAHPRA (South African Health Products Regulatory Authority) approval for Breast AI [21]. The remaining 75% (15/20) either did not report their regulatory status or used unapproved systems.

Imaging modalities reflected in point-of-care contexts included ultrasound (7/20, 35%), chest x-ray (5/20, 25%), smartphone photography (3/20, 15%), fundus photography (2/20, 10%), microscopy (2/20, 10%), and dermoscopy (1/20, 5%). Device types emphasized portability, with mobile phone-based devices (6/20, 30%), handheld devices (5/20, 25%), cart-based devices (3/20, 15%), and portable units (2/20, 10%) being the most prevalent; device type was not reported for 20% (4/20) of studies. Real-time processing was reported in 70% (14/20) of studies, and offline capability—critical for settings with unreliable connectivity—was confirmed in 30% (6/20) of the studies.

Beyond diagnostic accuracy, we examined the implementation of explainability features using a proposed cascade framework (Table 6), assessing progression from no mention through clinical evaluation of decision impact. The cascade revealed a progressive drop-off (Figure 5): 75% (15/20) of studies did not mention explainability at all (level 0). A total of 3 studies (3/20, 15%) implemented XAI during development but did not provide explanations to clinical users (level 1): Chen et al [13] used Grad-CAM (Gradient-weighted Class Activation Mapping) and SHAP (Shapley Additive Explanation) values, Nath et al [23] used heatmaps and attention mechanisms, and Poli et al [26] used Grad-CAM. Only 2 of 10 (10%) studies provided explanations to clinical users (level 2): Jayaraman et al [18] displayed heatmaps to radiologists, and Yang et al [27] showed bounding boxes with confidence scores to health care workers. Critically, no studies assessed whether clinicians understood the explanations (level 3) or evaluated whether XAI influenced clinical decisions (levels 4‐5), representing a complete drop-off above level 2.

Among studies mentioning XAI, the techniques included Grad-CAM activation maps (n=2), heatmaps (n=2), attention mechanisms (n=2), bounding boxes with confidence scores (n=1), and SHAP values (n=1); no studies implemented Local Interpretable Model-Agnostic Explanations.

A second critical finding is the evidence gap between technical validation and clinical impact. Applying the clinical impact pyramid framework (Table 7), the distribution revealed (Figure 6): 15% (3/20) of studies reported technical accuracy only (level 0: Kazemzadeh et al [19], Love et al [20], Yang et al [27]); 65% (13/20) reported process outcomes such as time to diagnosis and workflow efficiency (level 1); and 20% (4/20) documented clinical actions based on AI recommendations (level 2: Chen et al [13], Iacob et al [16], Jaremko et al [17], and Malherbe [21]). Critically, no studies measured patient-level health outcomes (level 3) or health system impact (levels 4‐5). Specific outcomes reported included workflow efficiency (10/20, 50%), time to diagnosis (9/20, 45%; AI processing typically <1 min), referral documentation (6/20, 30%), and cost analysis (5/20, 25%; projection-based rather than measured savings). The absence of patient outcome data is notable, given that several studies enrolled thousands of patients in operational settings (Heydon et al, n=30,405 [15]; Jayaraman et al, n=25,598 [18]; Marquez et al, n=5740 [22]), where outcome tracking was feasible.

We assessed methodological quality using the QUADAS-2 tool. Assessment revealed substantial methodological concerns (Table 8; Figures 7 and 8 [10-29]; detailed justifications for each judgment are provided in Multimedia Appendix 4). Thus, 70% (14/20) of the evidence base carries high or very high RoB, substantially limiting confidence in reported performance estimates.

Domain-level assessment revealed that the index test domain (domain 2) was the strongest, with 50% (10/20) of studies classified as being at low risk, reflecting reduced bias from automated AI interpretation. Patient selection (domain 1) revealed a 50% (10/20) unclear risk due to inadequate enrollment reporting, with high-risk studies relying on convenience sampling or case-control designs. The reference standard (domain 3) indicated a 55% (11/20) high risk, primarily due to differential verification bias; notably, Malherbe [21] did not have a reference standard. Flow and timing (domain 4) showed a 60% (12/20) high-risk rating, reflecting substantial exclusions and inadequate patient accounting.

Applicability concerns were generally low across all domains: patient selection 100% (20/20), index test 100% (20/20), and reference standard 80% (16/20) low concern, suggesting that, despite concerns about RoB, the studied populations and AI systems are relevant to the review question.

The most common methodological issues were verification bias (14/20, 70%) of studies, where only positive cases received the reference standard or substantial proportions were unverified; selection bias (10/20, 50%), involving nonconsecutive or convenience sampling; post hoc threshold optimization (6/20, 30%), potentially inflating performance estimates; and high exclusion rates (6/20, 30%), with some studies excluding over 20% of enrolled patients.

Given that 70% (14/20) of studies were rated as having a high or very high RoB, we conducted a sensitivity analysis restricted to studies with a low-to-moderate RoB (6/20, 30%; detailed in Multimedia Appendix 5). Sensitivity ranges narrowed from 62.5%-100% to 87%-100% (median 93.6%, IQR 87%-98% vs 90%, IQR 88%-95.7%), and specificity ranges narrowed from 28.1%-100% to 54%-96.5% (median 90.6%, IQR 74.5%-96.7% vs 85%, IQR 62%-93.5%). Median AUC remained stable at 0.91 (IQR 0.82-0.96) for the full cohort versus 0.91 (IQR 0.86-0.96) for the quality-restricted subset. These narrower ranges reflected elimination of outliers rather than systematic inflation in lower-quality studies, suggesting primary diagnostic accuracy conclusions are robust to quality concerns.

A qualitative assessment of reporting bias revealed several limitations (Multimedia Appendix 6). The comprehensiveness of the literature search was moderate: while 4 major databases (PubMed, Scopus, IEEE Xplore, and Web of Science) were systematically searched, gray literature, conference proceedings, preprint servers, and trial registries were not included, potentially missing unpublished studies with null or negative findings. Language restrictions to English-only studies may have excluded relevant evidence from non-English sources.

Publication bias indicators suggested moderate concern. Commercial AI systems predominated (12/20, 60%), potentially introducing bias in favor of favorable results from vendor-sponsored research. Small-study effects were evident: small studies (n<200, 5/20, 25%) demonstrated narrower and higher performance ranges (sensitivity 85.7%‐100%, specificity 71.1%‐100%) compared to extensive studies (n>1000, 8/20, 40%; sensitivity 62.5%‐98%, specificity 28.1%‐97.6%), consistent with preferential publication of favorable results from smaller studies.

Selective outcome reporting was moderate. Core sensitivity and specificity metrics were well reported (18/20, 90%, and 17/20, 85% of studies, respectively), but secondary metrics showed substantial gaps: AUC (10/20, 50%), PPV (10/20, 50%), NPV (10/20, 50%), sensitivity 95% CI (13/20, 65%), and specificity 95% CI (12/20, 60%). A total of 1 study reported no diagnostic performance metrics. However, the narrative synthesis approach and substantial heterogeneity limit the impact of these biases on review conclusions compared to meta-analytic approaches.

GRADE assessment revealed very low certainty in diagnostic accuracy estimates (Table 9). Starting from a high certainty level per GRADE guidance, the evidence was downgraded to 6 levels across all domains. The RoB was rated as of grave concern (2-level downgrade), given that 70% (14/20) of studies were at high or very high risk, with verification bias (14/20, 70%), selection bias (10/20, 50%), and post hoc threshold optimization (6/20, 30%) being the predominant concerns. Indirectness was rated as a serious concern (1-level downgrade) due to heterogeneity across 12 conditions, 6 modalities, and 18 AI systems. Inconsistency was rated as a serious concern, given the wide performance variation (sensitivity: 62.5%‐100%, specificity: 28.1%‐100%); even tuberculosis studies showed specificity ranging from 28.1% to 96.9%. Imprecision was rated a serious concern because 30% (6/20) of studies lacked CIs, and 25% (5/20) were small (n<200). Publication bias was rated as a serious concern due to the predominance of commercial systems (12/20, 60%) and small-study effects.

The very low certainty rating suggests that the proper diagnostic performance may differ substantially from the reported estimates. While median sensitivity (93.6%, IQR 87%-98%) and specificity (90.6%, IQR 74.5%-96.7%) appear promising, decision-makers should interpret these values cautiously, recognizing that real-world performance is likely to differ from the published results. Local validation remains essential before clinical adoption, and current evidence supports pilot implementation rather than widespread deployment without addressing methodological and heterogeneity concerns.

This systematic review of 20 studies evaluating AI in point-of-care imaging for clinical decision support reveals a rapidly evolving field, with 85% (17/20) of studies published since 2023 and approximately 78,000 patients enrolled across 15 countries. Five principal findings emerge with distinct implications for research, practice, and policy: (1) AI enables meaningful task-shifting from specialists to nonspecialist health care workers; (2) training requirements are remarkably minimal; (3) a profound gap exists between regulatory expectations for AI transparency and actual explainability implementation; (4) no studies measured patient-level health outcomes; and (5) the absence of cross-context validation undermines claims of global applicability.

This review provides the first systematic evidence synthesis demonstrating that AI enables meaningful task-shifting from specialists to nonspecialist health care workers across diverse point-of-care imaging applications. A total of 13 (65%) studies, 13/20 explicitly evaluated task-shifting, consistently showing that nonspecialists with AI assistance achieved diagnostic performance comparable to specialists. Key exemplars include Love et al [20] (100% sensitivity or specificity after 30 min of training), Avgerinos et al [10] and Nothnagel and Aslam [24] (100% DVT sensitivity with 1 hour training), and Nath et al [23] (technicians outperforming radiologists for tuberculosis detection). The consistency of this finding across diverse conditions—including deep vein thrombosis, breast masses, tuberculosis, and hip dysplasia—suggests the generalizability of the task-shifting paradigm, with policy implications for workforce planning, revision of training curricula, and regulatory frameworks for nonspecialist AI-assisted diagnostics.

This review also quantifies remarkably minimal training requirements for practical AI-assisted point-of-care imaging. The median training duration was only 1 hour (range 30 minutes to 6 months), with several studies achieving excellent performance after 30 minutes. Critically, no dose-response relationship was observed between training duration and diagnostic performance. This finding challenges traditional assumptions about extensive training requirements for medical imaging interpretation. The AI effectively serves as an “expert in the pocket,” enabling rapid deployment of diagnostic capabilities. The implications for scalability are profound, particularly in LMIC and LIC contexts, where traditional imaging training programs requiring months or years may be unnecessary when AI provides real-time guidance.

A critical finding concerns the gap between regulatory expectations for AI transparency and actual implementation of explainability. The XAI cascade revealed a progressive drop-off from 75% (15/20) nonmentioning (level 0) to only 10% (2/20) user presentation (level 2), with no studies reaching levels 3‐5—a field-wide gap requiring urgent attention. The findings suggest XAI is being treated as a development tool rather than a clinical communication mechanism. Regulatory compliance with the European Union AI Act and FDA guidance, as well as establishing clinical trust and appropriate AI usage, both depend on addressing this gap.

These findings have direct implications for physician autonomy—the capacity of clinicians to exercise independent judgment over diagnosis and treatment. The near absence of clinician-facing explainability (only 10% of studies) limits physicians’ ability to evaluate AI recommendations critically. When AI functions as opaque, physicians cannot meaningfully integrate AI outputs with their clinical reasoning; as Grote and Berens [30] argue, this uncertainty potentially undermines the epistemic authority of clinicians, risking either uncritical deference to algorithmic outputs or dismissal of potentially valuable decision support. Similarly, AI-enabled task-shifting, while extending diagnostic capacity, reshapes traditional boundaries of professional responsibility; physicians retain accountability for patient outcomes even when nonspecialists perform AI-assisted imaging. Future research should explicitly assess how AI implementation affects physician autonomy, including whether XAI restores clinician control and how task-shifting protocols maintain appropriate oversight structures.

The clinical impact pyramid revealed a substantial disconnect between technical validation and clinical benefit. While 15% (3/20) of studies reported technical accuracy alone, 65% (13/20) of studies progressed to process outcomes such as time to diagnosis and workflow efficiency. Although 20% (4/20) of studies documented clinical actions based on AI recommendations, no studies measured patient-level health outcomes or assessed the impact on the health system. Decision-makers cannot currently determine whether AI-assisted point-of-care imaging improves patient outcomes or represents a sound investment in health care. This gap is particularly critical in LMIC contexts, where resource allocation decisions require evidence of outcomes. The focus on diagnostic accuracy metrics reflects methodological traditions of diagnostic test evaluation, but leaves the fundamental question unanswered: Does AI-assisted point-of-care imaging help patients?

While 35% (7/20) of studies were conducted in LMIC or LIC settings, no studies validated AI systems across different resource contexts. Performance in LMIC and LIC settings was slightly lower (median sensitivity 88% versus 95.2% in HICs), but the absence of cross-context validation prevents conclusions about true generalizability. Before scaling AI systems to underserved populations, multicountry validation is essential to address differences in disease prevalence, imaging equipment, image quality, and patient populations.

These promising findings must be interpreted in light of the substantial methodological concerns detailed in the “Limitations of the Included Evidence” section below. With 70% (14/20) of studies at high or very high RoB, real-world performance may be lower than reported, and the GRADE assessment of very low certainty reflects appropriate caution. These findings must be contextualized within the existing literature to assess their novelty and significance.

This review addresses gaps not covered by existing systematic reviews in this domain. Kossoff et al [1] examined automated lung ultrasound analysis for pneumothorax detection; yet, their review was limited to a single modality and condition, without requiring point-of-care validation. Cold et al [2] focused on AI in bronchoscopy within specialist procedural settings rather than point-of-care contexts. Rambabu et al [3] evaluated AI for papilloedema detection using fundus photography; however, the included studies were predominantly retrospective and lacked clinical outcome assessment. Sunny et al [4] reviewed biomarker-integrated cytopathology for oral lesion detection, a laboratory-based methodology fundamentally distinct from point-of-care imaging.

Our review extends beyond these prior works in several critical dimensions. First, we provide the first cross-modality synthesis encompassing ultrasound, chest radiography, photography, fundus imaging, microscopy, and dermoscopy within point-of-care settings. Second, we developed and applied proposed frameworks—the XAI implementation cascade and clinical impact pyramid—that enable systematic identification of evidence gaps not previously characterized. Third, we provide the first quantitative characterization of task-shifting success and training requirements across point-of-care imaging applications.

The XAI and patient outcome gaps we identified are consistent with broader patterns in medical AI literature. Previous reviews of AI in radiology and pathology have similarly noted the predominance of diagnostic accuracy studies without clinical outcome assessment, suggesting this represents a field-wide methodological pattern requiring systematic attention rather than an isolated finding within point-of-care imaging.

These findings carry important implications for clinical practice, research priorities, and health policy.

Clinicians considering AI-assisted point-of-care imaging should recognize both promise and limitations. Diagnostic accuracy data support cautious adoption for specific applications, particularly tuberculosis screening, for which multiple studies demonstrate consistent performance. However, local validation remains essential before deploying systems that have been validated in different contexts. Training programs should be competency-based rather than duration-based; evidence suggests that brief training can be sufficient when AI provides real-time guidance, but competency assessment remains essential. The AI serves as decision support rather than autonomous diagnostics, and clinical judgment remains critical, particularly when AI recommendations conflict with clinical findings. Health care organizations implementing AI-assisted imaging should document clinical actions and patient outcomes; real-world performance data will build the evidence base currently lacking and enable quality improvement.

Based on the identified evidence gaps, we make the following explicit recommendations for future research. XAI evaluation studies should assess not only implementation but also clinician understanding and the impact on decision-making, using mixed methods that include cognitive task analysis and decision quality metrics. Implementation research with patient outcomes as primary end points, using cluster-randomized trials to compare AI-assisted vs standard care pathways, is crucial for determining whether these systems enhance patient health. Multicountry and multicontext validation is needed before claims of global applicability can be substantiated, including sites across HIC, upper-middle-income country, LMIC, and LIC settings. Methodological improvements, including consecutive enrollment, complete verification, prespecified thresholds, and reporting per STARD-AI (Standards for Reporting of Diagnostic Accuracy Studies–Artificial Intelligence) guidelines, would substantially strengthen the evidence base. Additional priorities include cost-effectiveness analyses using standardized methods and health system perspectives, longitudinal monitoring frameworks for deployed systems that track performance drift and recalibration needs, and equity-focused analyses that explicitly address whether AI reduces or exacerbates health disparities.

Policy implications are equally substantial, with 5 key recommendations. First, regulatory frameworks should evolve beyond requiring XAI implementation to requiring evidence of XAI evaluation and effectiveness; approval pathways should assess whether explanations are understood and valuable rather than merely present. Second, funding agencies should shift priorities from additional diagnostic accuracy studies toward implementation research with patient outcome end points for conditions where technical performance is established. Third, health technology assessment bodies should require cross-context validation evidence before recommending the adoption of systems in settings different from those in which they were initially validated. Fourth, workforce policy should anticipate task-shifting implications, as evidence suggests nonspecialists can achieve specialist-level performance with minimal training, with implications for training curricula, scope of practice regulations, and workforce planning. Fifth, global health initiatives should invest in validation infrastructure for LMIC and LIC settings, where the current evidence base is insufficient to support confident deployment despite these settings having the greatest need.

This review has several methodological strengths. A comprehensive search across 4 databases (PubMed, Scopus, IEEE Xplore, and Web of Science) with rigorous dual-reviewer screening addressed the challenges inherent in identifying genuine point-of-care implementations amid aspirational claims. The strict requirement for actual point-of-care deployment or validation, rather than theoretical potential, ensures the included evidence reflects real-world implementation. Thorough QUADAS-2 quality assessment with prespecified synthesis rules, sensitivity analysis restricted to studies with low-to-moderate RoB (6/20), and GRADE certainty evaluation ensured transparent and reproducible evidence appraisal.

The evidence base has substantial limitations that temper interpretation of the generally favorable diagnostic accuracy findings. First, 70% (14/20) of studies carried a high or very high RoB, predominantly due to verification bias (14/20, 70%), where only screen-positive cases received reference standard confirmation, and selection bias (10/20, 50%), which involved convenience sampling rather than consecutive sampling. These methodological weaknesses likely inflate reported sensitivity and specificity estimates. Second, post hoc threshold optimization in 30% (6/20) of studies may have overfitted performance to specific datasets, limiting generalizability. Third, substantial clinical heterogeneity across 12 conditions, 6 imaging modalities, and 18 distinct AI systems limits the applicability of aggregate findings to any specific clinical scenario. Fourth, incomplete outcome reporting—with 30% (6/20) of studies lacking CIs and secondary metrics (AUC, PPV, and NPV) reported in only 50% (10/20) of the studies—impairs the precision of effect estimates. Fifth, the predominance of commercial systems (12/20, 60%) raises concerns about the selective publication of favorable results. Collectively, these evidence limitations suggest that actual diagnostic performance in routine clinical practice may be lower than reported estimates, and the GRADE assessment of very low certainty (⊕◯◯◯) reflects this uncertainty.

Several limitations of this review warrant consideration. First, restricting our search to English-language publications may have excluded relevant studies from non-English contexts; given that 35% (7/20) of included studies originated from LMIC/LIC settings where non-English publication is common, this restriction may have introduced selection bias that underrepresents the global evidence base. Second, excluding gray literature—including conference proceedings, preprints, and technical reports—may have introduced publication bias by omitting negative or null findings, though this decision prioritized peer-reviewed evidence quality for clinical decision-making. Third, encountering substantial heterogeneity across conditions, modalities, and AI systems precluded meta-analysis, limiting our ability to generate pooled effect estimates that would enable more precise conclusions. Fourth, concluding our search in November 2025 means that subsequently published studies are not captured, potentially missing recent methodological advances given the rapid evolution of this field.

AI-assisted point-of-care imaging demonstrates promising diagnostic accuracy (median sensitivity 93.6%, IQR 87%-98%; median specificity 90.6%, IQR 74.5%-96.7%) and enables meaningful task shifting to nonspecialist operators with minimal training. These findings support cautious optimism regarding AI’s potential to democratize diagnostic capabilities in specialist-scarce settings.

However, 4 critical evidence gaps preclude confident recommendations for widespread adoption. The explainability gap is profound, with 75% (15/20) of studies not mentioning XAI and none evaluating whether explanations influenced clinical decisions, creating misalignment with regulatory requirements. The patient outcome gap is equally concerning, as no studies measured whether AI-assisted imaging actually improves patient health. The cross-context validation gap prevents conclusions about global applicability, and methodological quality concerns—with 70% (14/20) of studies at high or very high RoB—suggest reported performance may be optimistic.

The field requires urgent reorientation toward implementation research with patient outcome end points, rigorous XAI evaluation demonstrating clinical utility, and multicontext validation. Regulatory frameworks should require evidence of explainability effectiveness, not merely its presence. Only by systematically addressing these gaps can the field transition from promising technology demonstration to evidence-based clinical adoption that demonstrably improves patient outcomes.