Diagnostic accuracy of smartphone and artificial intelligence tools for diabetic foot screening

INTRODUCTION

Diabetic foot ulcers are the most frequent pathway to diabetes-related lower-limb amputation, and their prevention depends on recognizing the foot at risk before the skin breaks down. Around 18.6 million people develop a diabetic foot ulcer each year worldwide, and up to one third of people with diabetes will experience one during their lifetime.(1,2) Ulceration recurs in about 40% of patients within one year and in 65% within five years, and the five-year mortality after an ulcer rivals that of several cancers.(2) A meta-analysis of 26 studies estimated the global prevalence of diabetic foot ulceration at 6.3% of people with diabetes, with wide variation across regions and income settings.(3) Foot disease affects roughly 6% of people with diabetes at any time, a burden that rises when neuropathy, peripheral arterial disease and deformity coincide.(4) Diabetes accounts for more than one million lower-limb amputations each year, and the large majority of those amputations are preceded by an ulcer that might have been detected earlier.(1) These figures matter because ulceration is preventable, and prevention is cheaper than the amputation that follows neglect.

The clinical answer to this burden is structured screening followed by risk stratification. Guidelines recommend an annual examination of the foot for loss of protective sensation, peripheral arterial disease, deformity and previous ulceration, after which each patient is assigned to a risk category that determines the frequency and intensity of follow-up.(5,6) The examination itself combines several measurements that a photograph could plausibly reproduce. Loss of protective sensation is tested with a monofilament, peripheral arterial disease by palpation of pulses or the ankle-brachial index, deformity by inspection, and previous ulceration from history, and these components are then combined into the risk categories defined by the International Working Group on the Diabetic Foot.(5,6) A camera cannot yet replace the monofilament or the Doppler probe, but it can capture the visible consequences of neuropathy and ischemia, namely deformity, callus, skin breaks and established ulceration, which is precisely the information that a photograph carries. The proportion of people with diabetes who actually receive this examination each year remains below guideline targets in most health systems, and the prevalence of the foot at risk identified when it is performed is substantial.(7) Where specialist expertise is scarce, detection is postponed until ulceration or infection is already established, and the opportunity for early intervention is lost.(4) The clinical examination is inexpensive, but its reach is limited by the number of trained examiners, and this is the constraint that a camera-based tool could relax. The stakes of getting this right are concrete: an ulcer detected at the earliest stage is usually managed with offloading and local wound care, whereas a missed ulcer can progress to infection, hospitalization and amputation within weeks. The practical question is therefore not whether screening works, but whether it can be extended beyond the clinic wall with the devices that patients already carry.

Smartphone cameras and artificial intelligence could move part of this assessment to the patient or to non-specialist staff, and the technology has matured quickly. Deep learning already matches specialist performance in image-based diagnosis in neighbouring fields, as in dermatology where a convolutional network classified skin lesions at dermatologist level.(8) Public image datasets for the diabetic foot, above all the diabetic foot ulcer challenge collections, have allowed dozens of models to be trained and compared on a common benchmark.(9) Several systematic reviews now report that deep learning achieves high accuracy for ulcer detection and classification, with summarized estimates that frequently exceed 90%.(10-14) A recent meta-analysis of deep learning for ulcer screening reported high pooled accuracy but also marked between-study inconsistency, and reviews of computer vision for wound care and of home-based monitoring describe a field moving from laboratory benchmarks toward mobile applications and remote follow-up while noting that most models were never tested prospectively in clinical populations.(11,15,16) Those reviews nevertheless combine tasks that differ in kind, including detection, segmentation and clinical risk prediction, and most stop before the most recent mobile deployments or do not separate smartphone-based tools from laboratory models. The accuracy that a clinician can expect from a smartphone system at the point of care therefore remains unclear, and this is the gap that the present review addresses. It does so by asking the question separately for smartphone tools and for laboratory models, because the two carry different deployment promises and different risks, and by reporting the task and the reference that each accuracy value describes.

The term diagnostic accuracy deserves precision in this field. A model that detects an ulcer in a curated image archive answers a different question from a tool that screens consecutive patients for the first sign of ulceration, and the two are frequently conflated in the primary studies. Sensitivity and specificity are the measures that a clinician needs to estimate the consequences of using a tool, yet most published models report accuracy or the F1 score instead, which depend on the prevalence of ulcers in the training collection.(17) The distinction matters because the same accuracy can hide a very different balance of missed ulcers and false alarms, and this is why the review recorded the measure that each study actually reported rather than converting one measure into another.

The objective was to synthesize the diagnostic accuracy of smartphone-based and artificial intelligence tools for diabetic foot screening relative to clinical assessment. Three questions guided the review. P1: how accurately do smartphone-based tools detect diabetic foot ulcers or high-risk feet compared with clinical judgement? P2: how accurately do artificial intelligence models applied to foot images classify ulcers and related tissue states? P3: which sources of heterogeneity explain the differences in accuracy reported across studies?

METHODS

The review followed PRISMA 2020(18) and, for the reporting of searches, PRISMA-S.(19)

Eligibility was defined with a PICOS framework and mapped to the questions. For P1 the index test was a smartphone-based tool, including mobile photography and mobile applications, and for P2 it was an artificial intelligence model such as a deep learning, machine learning or computer vision system applied to foot images. The population comprised people with diabetes mellitus at risk of, or already presenting, diabetic foot ulcers. The reference standard was clinical assessment by a specialist or an expert-labeled image dataset, and the outcome was sensitivity, specificity, accuracy, the area under the receiver operating characteristic curve, or an equivalent per-class measure. Original studies published between 2018 and 2026 in English were eligible, so that the window matched the bibliographic rules of the target journal. Reviews, editorials, protocols and conference abstracts without accuracy data were excluded. Tools whose index test relied on thermal or hyperspectral imaging were also excluded, because infrared thermography of the diabetic foot is covered by a separate review, and models that predicted ulcer risk from clinical variables alone, without image analysis, were excluded as a different class of test. The thermography exclusion was applied even when the thermal signal was fused with visible-light images, because the contribution of the thermal component could not be separated from the contribution of the photographic component in those reports. This last exclusion kept P2 focused on image-based tools rather than on tabular risk scores, and both exclusions were applied at the stage of title and abstract screening.

The bibliographic databases consulted were: Scopus, Pubmed, Google Scholar, Open Alex and Crossref.

For each included study the design, country, sample, index test, reference standard and accuracy estimates were extracted together with their location in the abstract or full text. Missing fields were not completed by assumption, and where a study did not report a given measure it was recorded as not reported. When several accuracy values were available, the value reported by the authors as the primary result was preferred, and the task and the class definition were recorded alongside it. Sensitivity and specificity were extracted when reported, and otherwise the reported accuracy, F1 score, area under the curve or mean average precision was recorded as the available measure. Where a study reported per-class values, the class-specific values were preserved rather than averaged, because the clinical questions behind ischemia, infection and depth are distinct. The same reviewer performed the extraction, and no second extractor was available to cross-check the values.

Risk of bias and applicability were assessed with QUADAS-2(20) across four domains: patient selection, index test, reference standard, and flow and timing. Each domain was rated as low, high or unclear using the signaling questions of the tool, and studies for which only the abstract was available were rated unclear in the domains that could not be inspected. Patient selection was judged against the presence of consecutive or random enrolment and the avoidance of inappropriate exclusions, and most image collections failed this test because they were assembled for model training rather than for diagnostic evaluation. The index test was judged against the prespecification of thresholds, and the reference standard against its independence from the index test and its ability to classify the target condition. Flow and timing captured whether the same reference was applied to all images and whether cross-validation respected patient-level independence, which matters in this literature because several authors reported image-level rather than patient-level splitting. The same assessment supported the interpretation of P1 and P2, because the pattern of risk did not differ systematically between the two groups of tools.

Accuracy estimates were tabulated separately for P1 and P2, and the reported values were compared within each question in ascending order of the magnitude of the primary estimate. Pooling was not attempted because the studies used different datasets, tasks, class definitions and metrics, and this heterogeneity was described narratively for P3 rather than quantified. A meta-analysis was judged inappropriate because the same accuracy value denoted different tasks in different studies, and a pooled estimate would have combined binary ulcer detection with four-class classification and severity grading, which would have produced a summary without a clinical meaning. The narrative synthesis therefore presents each study with its own task and reference, and the comparisons between studies are qualitative rather than statistical.

RESULTS

Study selection

The searches identified 963 records, and 316 duplicates were removed, leaving 647 records for screening (Figure 1). After title and abstract screening, 582 records were excluded and 65 reports were sought for retrieval. Full text was not retrievable for 43 reports. Of the 22 reports assessed for eligibility, 3 were excluded and 19 studies were included in the review. Five of the included studies were assessed from their abstract because the full text was not openly accessible. The exclusions at title and abstract were dominated by reviews and by tools that were not image-based, and the three exclusions at full text corresponded to two reviews, one non-imaging prediction model and one infrared thermography study. The search was deliberately broad, which explains why the majority of records were discarded at screening and why the final set of 19 studies is small relative to the number of records identified. Nineteen studies were ultimately included.

DISCUSSION

The question that opened this review was whether smartphone and artificial intelligence tools can screen the diabetic foot accurately enough to substitute or extend clinical judgement. The answer is qualified: the tools reach high accuracy, but the evidence rests on retrospective image datasets rather than on prospective clinical verification. This distinction is the central finding, and it reappears under each of the three research questions.

With respect to P1, smartphone-based tools detected ulcers and high-risk feet with sensitivity and specificity that approached expert judgement in the single prospective evaluation, where a smartphone system reached 91.6% sensitivity and 88.6% specificity in 81 patients.(35) This aligns with the telemedicine literature, in which smartphone photography for wound assessment reproduces specialist decisions in most cases, and with the high sensitivity reported for smartphone-based retinal screening in diabetes.(40) Conversely, the remaining smartphone studies reported localization or component-level measures rather than patient-level sensitivity, which limits the confidence that can be placed in the headline values beyond the single clinical cohort.(21,22) The gap between 85.2% external accuracy for a deformity application and 99.9% accuracy in a clinician-audited model illustrates how much the deployment setting changes the estimate.(34,38) The component-level pattern is also informative, because the SINBAD application classified infection and area well but depth poorly, which indicates that the tools reproduce the visible parts of the assessment and struggle with the parts that require tissue-level judgement.(36) The high agreement among clinicians on the adequacy of the smartphone system is itself notable, because it indicates that the automated judgement was intelligible to the specialists who would have to act on it, an aspect of diagnostic tools that accuracy alone does not capture.(35) The clinical value of P1 therefore rests on one well-conducted study, and the remaining mobile tools are better described as promising than as validated.

As for P2, artificial intelligence models reached accuracy values from 78.3% to 99.9%, with the higher values concentrated in binary or curated tasks and the lower value in the four-class challenge task.(27,28) This range is consistent with previous systematic reviews, which summarized deep learning accuracy for ulcer detection and classification as high but heterogeneous, and with the broader diagnostic accuracy of deep learning in medical imaging.(11,12,41) The near-perfect estimates reported in several of the included models, such as an area under the curve of 1.000 in one comparative architecture, are unlikely to generalize because image-level cross-validation can leak information from the same patient across folds.(37) The same concern was raised explicitly by the authors of that study, and it is reinforced by the QUADAS-2 finding that flow and timing was at high risk in 14 studies. Conversely, the models that incorporated an external clinician audit or a real-world image set reported more modest but more credible values, which suggests that architecture choice matters less than the evaluation design.(34) Reviews of deep learning for segmentation and for computer vision in ulcer care draw the same conclusion, namely that reported accuracy exceeds what would be expected once models face uncurated images.(15,42) The four-class result of 78.3% is arguably the most realistic benchmark, because it reflects the diagnostic categories that a clinician actually distinguishes rather than a simplified ulcer versus normal contrast. Its per-class pattern is also clinically instructive: ischemia was the class most often misclassified, which is exactly the distinction that carries the greatest prognostic weight in the diabetic foot and the one that monofilament and Doppler assessment are designed to capture.(27)

A comparison with the wider machine learning literature places these numbers in perspective. In a systematic review of deep learning against health-care professionals across medical imaging, the diagnostic performance of algorithms was on average similar to that of clinicians, but the underlying studies rarely met the reporting standards of diagnostic accuracy research, and few were prospective.(41) The same pattern is visible here: the included models rival the accuracy of specialist readers on their own test sets, yet the evaluations would not satisfy a strict diagnostic accuracy framework, and the estimates are therefore best read as upper bounds on what a deployed system would achieve.(17) This does not diminish the engineering progress, but it changes what the numbers are evidence for.

Regarding P3, heterogeneity was driven by dataset, task and reference standard rather than by the model family. Models evaluated on the 2020 challenge performed differently from those on the 2021 multi-class set, and tasks as different as ulcer detection, infection classification and severity grading cannot be pooled into a single estimate without obscuring these differences.(9,13) This explains why the earlier reviews reached different summary figures, and why the present review chose narrative synthesis over meta-analysis.(10,14) A further source of variability is the absence of a common clinical reference, since expert image labels are not the same standard as an in-person specialist examination, and the two were rarely compared directly.(20) Home-based monitoring reviews reach a parallel conclusion, in that feasibility is often demonstrated while diagnostic agreement with a clinician is not.(16) Until a shared reference and a shared task definition are adopted, each new model will continue to report against a different yardstick, and between-study comparisons will remain descriptive.

The reliance on a small number of public benchmark datasets is itself a structural weakness. When most of the included models are trained and tested on the 2020 and 2021 diabetic foot ulcer challenge collections, the reported accuracy describes performance on those collections more than performance in the clinic, and successive models may overfit the idiosyncrasies of the benchmark rather than the disease.(9) The systematic reviews of deep learning in medical imaging warn that few of these studies are prospective, which means the published scores overstate what a deployed system would achieve.(41) A healthier evaluation culture would combine the benchmark with a small prospective clinical cohort, as the single clinical study and the clinician-audited models already do, so that every new architecture is measured against patients rather than only against pixels.(34,35)

The implications for low-resource settings, where structured screening is least available, cut in both directions. On one hand, a smartphone tool that reaches 91.6% sensitivity against expert judgement is precisely the kind of support that a non-specialist health worker or a patient at home could use between clinic visits, and the cloud and mobile deployments reviewed here show that the computation is no longer the bottleneck.(22,35) On the other hand, the same settings are where a false-negative result carries the greatest cost, because there is no specialist to catch the error, and the prevalence-dependent accuracy measures that dominate this literature do not answer the question of how many ulcers would be missed in a real screening cascade.(1) The external validation of the deformity application, which fell from 91.1% to 85.2% when moved to new participants, is a concrete warning that performance decays exactly when a tool leaves the environment in which it was trained.(38) Any deployment in routine screening should therefore include a mechanism for clinician review of negative results and a plan for measuring downstream outcomes, not only image-level accuracy.

The strengths of this review are the separation of smartphone tools from laboratory models, the question-driven structure, and the restriction to studies that reported an accuracy measure against a reference standard. The question-driven organization also tied each finding to the question it answers, which reduces the temptation to generalize from a curated benchmark to the clinic. The limitations are substantial and each carries a recommendation. Most included studies were retrospective image classification exercises, so estimates should be re-examined in prospective cohorts that enrol consecutive patients. Five studies were assessed from abstracts because the full text was not openly accessible, and their domains were rated unclear; future updates should retrieve those full texts. The absence of reported sensitivity and specificity in most studies forced the synthesis to rely on accuracy and related measures, which are prevalence-dependent and cannot be compared directly across samples. Publication and selective reporting are plausible, because the models that reached the highest internal accuracy may be precisely those most likely to be written up, and the review could not test for this.

For practice, the evidence supports using smartphone and artificial intelligence tools as an adjunct to, rather than a replacement for, structured clinical examination. The single prospective study and the clinician-audited models indicate that the technology is close to deployable, but the absence of standardized reporting and external validation means that local verification should precede routine use, and that verification should be reported in a way that lets others judge whether the local population resembles the one in which the tool was trained.(43) A cautious deployment would begin with ulcer detection as a triage aid in services that already perform structured screening, where the tool can shorten the queue rather than replace the examiner, and would expand only after its sensitivity and specificity are measured in that local population.(5) For research, the priority is a prospective comparison of the same tools against the same clinical reference, reported with sensitivity, specificity and confidence intervals in line with diagnostic accuracy standards.(17) The reporting of the included studies rarely followed such standards, and the field would benefit from adopting them before further benchmark proliferation. A shared checklist for reporting the reference labels, the splitting strategy and the target condition would cost little, would make the next generation of studies directly comparable with one another, and would spare clinicians the task of guessing how a reported accuracy value was produced. What remains open is whether the accuracy observed on images translates into earlier detection, fewer amputations and cost-effective screening when the tools are placed in the hands of patients and non-specialist staff, and no included study answered that question. Answering it will require a study design that follows patients over time rather than measuring a single image-level judgement, and that longitudinal design, with patient outcomes rather than image pixels as the endpoint, is the natural next step for this field of research.

CONCLUSIONS

Smartphone-based tools detected diabetic foot ulcers with high sensitivity in a prospective clinical evaluation, although most supporting evidence remained retrospective. Artificial intelligence models classified ulcer and tissue states with accuracy that ranged from 78.3% to 99.9% depending on dataset, task and reference standard. The observed heterogeneity indicates that prospective external validation against a common clinical reference is required before these tools enter routine screening.

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