Artificial Intelligence in Fracture Detection: A Systematic Review and Meta-Analysis


Artificial intelligence is noninferior to clinicians in terms of diagnostic performance in fracture detection, showing promise as a useful diagnostic tool.

Key Results

  • ■ In a systematic review and meta-analysis of 42 studies (37 studies with radiography and five studies with CT), the pooled diagnostic performance from the use of artificial intelligence (AI) to detect fractures had a sensitivity of 92% and 91% and specificity of 91% and 91%, on internal and external validation, respectively.

  • ■ Clinician performance had comparable performance to AI in fracture detection (sensitivity 91%, 92%; specificity 94%, 94%).

  • ■ Only 13 studies externally validated results, and only one study evaluated AI performance in a prospective clinical trial.


Fractures have an incidence of between 733 and 4017 per 100 000 patient-years (13). In the financial year April 2019 to April 2020, 1.2 million patients presented to an emergency department in the United Kingdom with an acute fracture or dislocation, an increase of 23% from the year before (4). Missed or delayed diagnosis of fractures on radiographs is a common diagnostic error, ranging from 3% to 10% (57). There is an inverse relationship between clinician experience and rate of fracture misdiagnosis, but timely access to expert opinion is not widely available (6). Growth in imaging volumes continues to outpace radiologist recruitment: A Canadian study (8) from 2019 found an increase in radiologist workloads of 26% over 12 years, whereas a study from the American College of Radiologists found a 30% increase in job openings from 2017 to 2018 (9). Strategies (6,10) to reduce rates of fracture misdiagnosis and to streamline patient pathways are crucial to maintain high standards of patient care.

Artificial intelligence (AI) is a branch of computer science in which algorithms perform tasks traditionally assigned to humans. Machine learning is a term that refers to a group of techniques in the field of AI that allow algorithms to learn from data, iteratively improving their own performance without the need for explicit programming. Deep learning is a term often used interchangeably with machine learning but refers to algorithms that use multiple processing layers to extract high level information from any input. Health care, and in particular, radiologic image classification, has been identified as a key sector in which AI could streamline pathways, acting as a triage or screening service, as a decision aid, or as second-reader support for radiologists (10).

Recent narrative reviews have reported high accuracy for deep learning in fracture detection and classification. Smets et al (11) summarized 32 studies, finding a wide range of accuracy (78%–99%) similar to Langerhuizen et al (12), who found a range of 77%–90% accuracy across 10 studies. Recent studies reported higher accuracy estimates (93%–99%) (1214). Yang et al (14) performed a meta-analysis of nine studies with a pooled sensitivity and specificity of 87% and 91%, respectively.

Our study is a systematic review and meta-analysis of 42 studies, comparing the diagnostic performance in fracture detection between AI and clinicians in peer-reviewed publications and in the gray literature (ie, articles published on preprint repositories) on radiographs or CT images. We described study methods, adherence to reporting guidelines, and we performed a detailed assessment of risk of bias and study applicability.

Materials and Methods

Protocol and Registration

This systematic review was prospectively registered with PROSPERO (CRD42020186641). Our study was prepared by using guidelines from the Preferred Reporting Items for a Systematic Review and Meta-analysis of Diagnostic Test Accuracy Studies (15,16). All stages of the review (title and abstract screening, full-text screening, data extraction, assessment of adherence to reporting guidelines, bias, and applicability) were performed in duplicate by two independent reviewers (R.Y.L.K. and either C.H., T.A.C., B.J., A.F., D.C., or M.S.), and disagreements were resolved by discussion with a third independent reviewer (G.S.C. or D.F.).

Search Strategy and Study Selection

A search was performed to identify studies that developed and/or validated an AI algorithm for the purposes of fracture detection. A search strategy was developed with an information specialist, including variations of the terms artificial intelligence and diagnostic imaging. The full search strategy is included in Appendix E1 (online) and Tables E1 and E2 (online). We searched the following electronic databases for English language peer-reviewed and gray literature between January 2018 and July 2020 (updated in June 2021): Ovid Medline, Ovid Embase, EBSCO Cumulative Index to Nursing and Allied Health Literature, Web of Science, Cochrane Central, Institute of Electrical and Electronics Engineers and Institution of Engineering and Technology Xplore, Association for Computing Machinery Digital Library, arXiv, medRxiv, and bioRxiv. The reference lists of all included articles were screened to identify relevant publications that were missed from our search.

We included all articles that fulfilled the following inclusion criteria: primary research studies that developed and/or validated a deep learning algorithm for fracture detection or classification in any user-independent imaging modality, English language, and human subjects. We applied the following exclusion criteria to our search: conference abstracts, letters to the editor, review articles, and studies that performed purely segmentation tasks or radiomics analysis. We excluded duplicates by using Endnote ×9, following the method described by Falconer (15). We did not place any limits on the target population, study setting, or comparator group.

Data Extraction

Titles and abstracts were screened before full-text screening. Data were extracted by using a predefined data extraction sheet. A list of excluded studies, including the reason for exclusion, was recorded in a Preferred Reporting Items for Systematic Reviews and Meta-Analyses flow diagram. Any further papers identified through reference lists underwent the same process of screening and data extraction in duplicate.

We extracted information from each study including peer-review status, study design, target condition, sample size, comparator groups, and results. Where possible, we extracted diagnostic performance information to construct contingency tables for each model and used them to calculate sensitivity and specificity. When studies included more than one contingency table, they were included in the analysis.

Statistical Analysis

We estimated the diagnostic performance of the deep learning algorithms and clinicians by carrying out a meta-analysis of studies providing contingency tables at both internal and external validation. We planned to perform a meta-analysis if at least five studies were eligible for inclusion, recommended for random-effects meta-analysis (16). We used the contingency tables to construct hierarchical summary receiver operating characteristic curves and to calculate pooled sensitivities and specificities, anticipating a high level of heterogeneity (17). We constructed a visual representation of between-study heterogeneity by using a 95% prediction region in the hierarchical summary receiver operating characteristic curves. We performed a meta-regression analysis to identify sources of between-studies heterogeneity by introducing level of bias; study and fracture type; the reference standard; peer-review status; and whether the algorithm used single or multiple radiologic views, data augmentation, or transfer learning as covariates. Statistical significance was indicated at a P value of .05. All calculations were performed by using statistical software (Stata version 14.2, Midas and Metandi modules; StataCorp) (18,19).

Quality Assessment

We assessed studies for adherence to reporting guidelines by using the Transparent Reporting of a Multivariable Prediction Model for Individual Prognosis or Diagnosis (TRIPOD) checklist, which is a 22-item list of recommendations to aid transparent reporting of studies that develop and/or validate prediction models (20). We used a modified version of TRIPOD (Appendix E2, Table E3 [online]), as we considered that not all items on the checklist were informative for deep learning studies; for example, reporting follow-up time is irrelevant for diagnostic accuracy studies. The checklist therefore is limited in granular discrimination between studies, but instead acts as a general indicator of reporting standards.

We used the Prediction Model Study Risk of Bias Assessment Tool, or PROBAST, checklist to assess papers for bias and applicability (Appendix E2, Table E4 [online]) (21). This tool uses signaling questions in four domains (participants, predictors, outcomes, and analysis) to provide both an overall and a granular assessment. We considered both the images used to develop algorithms, and the patient population or populations the models were tested on, to assess bias and applicability in the first domain. We did not include an assessment of bias or applicability for predictors. The diagnostic performance of both AI and clinicians at internal and external validation was examined separately in studies assessed at low risk of bias.

Publication Bias

We minimized the effect of publication bias by searching preprint servers and hand-searching the reference lists of included studies. We performed a formal assessment of publication bias through a regression analysis by using diagnostic log odds ratios and testing for asymmetry (22).


Study Selection and Characteristics

We identified 8783 peer-reviewed studies, of which 1981 were duplicates. A further 149 studies were identified through preprint servers and citation searching. After full-text screening, 42 studies were included in the review, of which 35 were peer-reviewed publications and seven were preprint publications (Fig 1). Thirty-seven studies identified fractures on radiographs, of which 18 focused on lower limb, 15 on upper limb, and four on other fractures (Tables 13) (2358). Five studies identified fractures on CT images (5963). All studies performed their analyses with a computer, with retrospectively collected data, by using a supervised learning approach; and one study also performed a prospective nonrandomized clinical trial (34). Thirty-six studies developed and internally validated an algorithm, and nine of these studies also externally validated their algorithm (23,24,2630,32,33,3555,5759,6163). Six studies externally validated or made an incremental change to a previously developed algorithm (25,31,34,56,60,63). Twenty-three studies restricted their analysis to a single radiologic view (25,27,2935,37,38,4043,4648,5053,58).

Figure 1: Preferred Reporting Items for Systematic Reviews and Meta-Analyses flowchart shows studies selected for review. ACM = Association for Computing Machinery, AI = artificial intelligence, CENTRAL = Central Register of Controlled Trials, CINAHL = Cumulative Index to Nursing and Allied Health Literature, IEEE = Institute of Electrical and Electronics Engineers and Institution of Engineering and Technology.

Table 1: Characteristics of Studies, Developing and Internally Validating Algorithms

Table 1:

Table 2: Characteristics of Studies Developing, Internally and Externally Validating Algorithms

Table 2:

Table 3: Characteristics of Studies Making Incremental Changes, or Externally Validating Algorithms

Table 3:

Sixteen studies compared the performance of AI with expert clinicians, seven compared AI to experts and nonexperts, and one compared AI to nonexperts only (24,2631,3339,42,43,46,50,51,5355,58,59). Six studies included clinician performance with and without AI assistance as a comparison group (2931,34,54,59). The size of comparison groups ranged from three to 58 (median, six groups; interquartile range, 4–15). Three studies compared their algorithm against other algorithms and 16 studies did not include a comparison group (23,25,32,40,41,4449,52,56,57,6064).

To generate a reference standard for image labeling, 18 studies used expert consensus, six relied on the opinion of a single expert reader, seven used pre-existing radiologic reports or other imaging modalities, five studies used mixed methods, and one defined their reference standard as surgically confirmation fractures (23,24,2632,3439,4163). Three studies did not report how their reference standard was generated (25,33,40).

Study Participants

The number of participants represented by each data set ranged widely (median, 1169; range 65–21,456; interquartile range, 425–2417; Appendix E3, Table E5 [online]). The proportion of participants with a fracture in each data set also ranged widely (median, 50%; interquartile range, 40%–64%). Seventeen studies did not include the proportion of study participants who were men or women, and 15 studies did not include information about participant age (23,25,27,3437,41,46,54,56,57,58,6063).

Algorithm Development and Model Output

The size of training (median, 1898; interquartile range, 784–7646), tuning (median, 739; interquartile range, 142–980) and test (median, 306; interquartile range, 233–1111) data sets at the patient level varied widely (Tables 13). Five of 33 (15.2%) studies that developed an algorithm did not report the size of each data set separately (24,28,32,33,40). In studies that performed external validation of an algorithm, the median size of the data set was 511 (range, 100–1696). Thirty studies used data augmentation, and 30 studies used transfer learning (2330,32,33,3544,46,4859,61,62). Twenty-six studies used random split sample validation as a method of internal validation, five used stratified split sampling, and four used a resampling method (Table E6 [online]) (2331,33,3555,57,58,61,62).

Twenty-two studies included localization of fractures in model output to improve end-user interpretability (23,24,3039,41,42,44,48,49,52,54,57,60,64). Metrics used to evaluate model performance varied widely, including sensitivity and specificity (38 studies); area under the receiver operating characteristic curve and Youden index (23 studies); accuracy (22 studies); positive and negative predictive values (nine studies); and F1, precision, and recall (nine studies).

Quality Assessment

Adherence to TRIPOD reporting standards was variable (Fig 2). Four items were poorly reported (<50% adherence): clarity of study title and abstract (19% and 17% adherence, respectively), sample size calculation (2.4%), discussion and attempt to improve model interpretability (43%), and a statement about supplementary code or data availability (19%).

Summary of study adherence to Transparent Reporting of a Multivariable                         Prediction Model for Individual Prognosis or Diagnosis (TRIPOD) reporting                         guidelines.

Figure 2: Summary of study adherence to Transparent Reporting of a Multivariable Prediction Model for Individual Prognosis or Diagnosis (TRIPOD) reporting guidelines.

Prediction Model Study Risk of Bias Assessment Tool, or PROBAST, led to an overall rating of 22 (52%) and 21 (50%) studies as high risk of bias and concerns regarding applicability, respectively (Fig 3). The main contributing factors to this assessment were studies that did not perform external validation, or internally validated models with small sample sizes. Fifteen (36%) studies were judged to be at high risk of bias and 18 (43%) at high concern for applicability in participant selection because of inclusion and exclusion criteria. In general, studies were at low concern for bias (six; 14% high concern) and applicability (nine; 21% high concern) in specifying outcomes and in analysis (nine; 21% high concern).

Summary of Prediction Model Study Risk of Bias Assessment Tool                         (PROBAST) risk of bias and concern about generalizability scores.

Figure 3: Summary of Prediction Model Study Risk of Bias Assessment Tool (PROBAST) risk of bias and concern about generalizability scores.


We extracted 115 contingency tables from 32 studies (55 061 images) that provided sufficient information to calculate contingency tables for binary fracture detection (Tables E7, E8 [online]) (2325,2740,42,43,45,4749,51,53,5558,60,61,63). Thirty-seven contingency tables from 26 studies were extracted for reported algorithm performance on internal validation, and 15 were extracted from seven studies on external validation. Thirty-six contingency tables from 12 studies were extracted for human performance on the same internal validation test sets, and 23 contingency tables from seven studies were extracted for performance on the same external validation test sets (24,27,30,31,3339,42,43,51,53,55). Four contingency tables were extracted from four studies for human performance with AI assistance (2931,34).

Hierarchical summary receiver operating characteristic curves from the studies evaluating AI and clinician performance on internal validation test sets are included in Figure 4. The pooled sensitivity was 92% (95% CI: 88, 94) for AI and 91% (95% CI: 85, 95) for clinicians. The pooled specificity was 91% (95% CI: 88, 93) for AI and 92% (95% CI: 89, 95) for clinicians. At external validation, the pooled sensitivity was 91% (95% CI: 84, 95) for AI and 94% (95% CI: 90, 96) for clinicians on matched test sets (Fig 5). The pooled specificity was 91% (95% CI: 82, 96) for AI and 94% (95% CI: 91, 95) for clinicians. When clinicians were provided with AI assistance, the pooled sensitivity and specificity were 97% (95% CI: 83, 99) and 92% (95% CI: 88, 95), respectively.

Hierarchical summary receiver operating characteristic (HSROC) curves                         for (A) fracture detection algorithms and (B) clinicians with internal                         validation test sets. The 95% prediction region is a visual representation                         of between-study heterogeneity.

Figure 4: Hierarchical summary receiver operating characteristic (HSROC) curves for (A) fracture detection algorithms and (B) clinicians with internal validation test sets. The 95% prediction region is a visual representation of between-study heterogeneity.

Hierarchical summary receiver operating characteristic (HSROC) curves                         for (A) fracture detection algorithms and (B) clinicians with external                         validation test sets. The 95% prediction region is a visual representation                         of between-study heterogeneity.

Figure 5: Hierarchical summary receiver operating characteristic (HSROC) curves for (A) fracture detection algorithms and (B) clinicians with external validation test sets. The 95% prediction region is a visual representation of between-study heterogeneity.

Meta-regression of all studies showed that lower model specificity was associated with lower risk of bias (89%; 95% CI: 87, 91; P , .01), use of data augmentation (92%; 95% CI: 90, 93; P , .01), and transfer learning (91%; 95% CI: 90, 93; P , .01). Higher model sensitivity was associated with algorithms focusing on lower limb fractures (95%; 95% CI: 93, 97; P , .01) and use of resampling methods (97%; 95% CI: 94, 100; P , .01). We performed a sensitivity analysis, separately evaluating studies with low risk of bias. We found that all performance metrics were lower, although only the reduction in area under the curve in studies assessing the performance of algorithms at external validation reached statistical significance (96%; 95% CI: 94, 98; P , .01; Table 4, Fig 6). We report findings of sensitivity analyses for other covariates in Figure E1, Appendix E4, and Tables E9–E13 (online).

Table 4: Pooled Sensitivities, Specificities, and Areas Under the Curve for Artificial Intelligence Algorithms and Clinicians

Table 4:
Summary of pooled sensitivity, specificity, and area under the curve                         (AUC) of algorithms and clinicians comparing all studies versus low-bias                         studies with 95% CIs.

Figure 6: Summary of pooled sensitivity, specificity, and area under the curve (AUC) of algorithms and clinicians comparing all studies versus low-bias studies with 95% CIs.

Publication Bias

We assessed publication bias by using a regression analysis to quantify funnel plot asymmetry (Fig E2 [online]) (22). We found that the slope coefficient was –5.4 (95% CI: –13.7, 2.77; P = .19), suggesting a low risk of publication bias.


An increasing number of studies are investigating the potential for artificial intelligence (AI) as a diagnostic adjunct in fracture diagnosis. We performed a systematic review of the methods, results, reporting standards, and quality of studies in assessing deep learning in fracture detection tasks. We performed a meta-analysis of diagnostic performance, grouped into internal and external validation results, and compared with clinician performance. Our review highlighted four principal findings. First, AI had high reported diagnostic accuracy, with a pooled sensitivity of 91% (95% CI: 84, 85) and specificity of 91% (95% CI: 81, 95). Second, AI and clinicians had comparable performance (pooled sensitivity, 94% [95% CI: 90, 96]; and specificity, 94% [95% CI: 91, 95]) at external validation. The addition of AI assistance improved clinician performance further (pooled sensitivity, 97% [95% CI: 83, 99]; and specificity, 92% [95% CI: 88, 95]), and one study found that clinicians reached a diagnosis in a shorter time with AI assistance (2931, 34). Third, there were significant flaws in study methods that may limit the real-world applicability of study findings. For example, it is likely that clinician performance was underestimated: Only one study provided clinicians with background clinical information. Half of the studies that had a clinician comparison group used small groups (ie, less than five) at high risk of interrater variation. All studies performed experiments on a computer or via computer simulation, and only one evaluated human-algorithm performance in a prospective clinical trial. Fourth, there was high heterogeneity across studies, partly attributable to variations in study methods. Heterogeneity in sensitivity and specificity was higher when methodologic choices, such as internal validation methods or reference standards, were used. There was a wide range of study sample size, but only one study (63) performed a sample size calculation.

Previous narrative reviews have reported a wide range of AI accuracy (1113). However, the use of accuracy as an outcome metric in image classification tasks can be misleading (65). For example, in a data set consisting of 82% fracture and 18% unfractured radiographs, an AI that always predicts a fracture will have a reported accuracy of 82%, despite being deeply flawed (30). A meta-analysis of nine studies by Yang et al (14) reported a pooled sensitivity and specificity of 87% (95% CI: 78, 93) and 91% (95% CI: 85, 95), respectively. This is consistent with the findings of our meta-analysis of 32 studies. We provided further granularity of results, reporting pooled sensitivity and specificity separately for internal (sensitivity, 92% [95% CI: 88, 94]; and specificity, 91% [95% CI: 88, 93]) and external (sensitivity, 91% [95% CI: 84, 95]; and specificity, 91% [95% CI: 81, 95]) validation.

Our study had limitations. First, we only included studies in the English language that were published after 2018, excluding other potentially eligible studies. Second, we were only able to extract contingency tables from 32 studies. Third, many studies had methodologic flaws and half were classified as high concern for bias and applicability, limiting the conclusions that could be drawn from the meta-analysis because studies with high risk of bias consistently overestimated algorithm performance. Fourth, although adherence to TRIPOD items was generally fair, many manuscripts omitted vital information such as the size of training, tuning, and test sets.

The results from this meta-analysis cautiously suggest that AI is noninferior to clinicians in terms of diagnostic performance in fracture detection, showing promise as a useful diagnostic tool. Many studies have limited real-world applicability because of flawed methods or unrepresentative data sets. Future research must prioritize pragmatic algorithm development. For example, imaging views may be concatenated, and databases should mirror the target population (eg, in fracture prevalence, and age and sex of patients). It is crucial that studies include an objective assessment of sample size adequacy as a guide to readers (66). Data and code sharing across centers may spread the burden of generating large and precisely labeled data sets, and this is encouraged to improve research reproducibility and transparency (67,68). Transparency of study methods and clear presentation of results is necessary for accurate critical appraisal. Machine learning extensions to TRIPOD, or TRIPOD-ML, and Standards for Reporting of Diagnostic Accuracy Studies, or STARD-AI, guidelines are currently being developed and may improve conduct and reporting of deep learning studies (6971).

Future research should seek to externally validate algorithms in prospective clinical settings and provide a fair comparison with relevant clinicians: for example, providing clinicians with routine clinical detail. External validation and evaluation of algorithms in prospective randomized clinical trials is a necessary next step toward clinical deployment. Current artificial intelligence (AI) is designed as a diagnostic adjunct and may improve workflow through screening or prioritizing images on worklists and highlighting regions of interest for a reporting radiologist. AI may also improve diagnostic certainty through acting as a “second reader” for clinicians or as an interim report prior to radiologist interpretation. However, it is not a replacement for the clinical workflow, and clinicians must understand AI performance and exercise judgement in interpreting algorithm output. We advocate for transparent reporting of study methods and results as crucial to AI integration. By addressing these areas for development, deep learning has potential to streamline fracture diagnosis in a way that is safe and sustainable for patients and health care systems.

Disclosures of conflicts of interest: R.Y.L.K. No relevant relationships. C.H. No relevant relationships. T.A.C. No relevant relationships. B.J. No relevant relationships. A.F. No relevant relationships. D.C. No relevant relationships. M.S. No relevant relationships. G.S.C. No relevant relationships. D.F. Chair, British Society for Surgery of the Hand Research Committee; member, British Association of Plastic, Reconstructive, and Aesthetic Surgeons Research Committee; member, British Lymphology Society Research Committee; chair, Scientific Advisory Committee Restore Research; Trustee, British Dupuytren Society.


We thank Eli Harriss, BA, MS, Bodleian Libraries Outreach Librarian for the Bodleian Health Care Libraries, who formulated the search strategies and ran the database searches.

Author Contributions

Author contributions: Guarantors of integrity of entire study, R.Y.L.K., D.F.; study concepts/study design or data acquisition or data analysis/interpretation, all authors; manuscript drafting or manuscript revision for important intellectual content, all authors; approval of final version of submitted manuscript, all authors; agrees to ensure any questions related to the work are appropriately resolved, all authors; literature research, R.Y.L.K., C.H., T.A.C., B.J., A.F., D.C., D.F.; statistical analysis, R.Y.L.K., D.C., G.S.C.; and manuscript editing, R.Y.L.K., C.H., B.J., A.F., D.C., M.S., G.S.C., D.F.

R.K. supported by a National Institute for Health Research (NIHR) Academic Clinical Fellowship. C.H. supported by a NIHR Doctoral Research Fellowship (NIHR300684). D.F. supported by the Oxford NIHR Biomedical Research Centre. This publication presents independent research funded by the NIHR.

Data sharing: All data generated or analyzed during the study are included in the published paper.


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