This systematic review included a literature search and a write-up that were both carried out with respect to the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) 2020 statement [17]. The completed PRISMA 2020 expanded checklist is provided as Checklist 1. A narrative synthesis was performed in accordance with the Synthesis Without Meta-Analysis (SWiM) reporting guideline [18]. This type of analysis was chosen as significant clinical and statistical heterogeneity existed across included studies making statistical pooling and group analysis of studies unrealistic. The approach is consistent with the methodological guidance of the Cochrane Handbook for Systematic Reviews of Interventions [19]. Searches were additionally reported in accordance with the PRISMA-S extension for the reporting of literature searches in systematic reviews [20]. The review was not prospectively registered. However, an a priori protocol specifying the research question, eligibility criteria, databases, search strategy, data extraction variables, and planned synthesis approach was developed and followed throughout.

Eligible studies for analysis had to be original, peer-reviewed articles published in English, with a publication window between January 1, 2020, and September 15, 2025. Participants could be trainees at any stage of their training. This meant if participants of studies were medical students, residents, and fellows, the study was appropriate for inclusion.

On the intervention side, a clearly described augmented reality component was required. For the purposes of this review, AR was understood as technology that overlays digital content directly onto a person’s view of the real world. Since AR, VR, and MR tend to appear together frequently in the literature, screening by YA and MEA was agreed beforehand to be meticulous and deliberate in only including studies that clearly focused on independently analyzing AR only. Each study also needed to include a comparator condition, whether that entailed traditional instruction, conventional operative guidance, or a freehand approach. At least one objective measure of technical performance or skill acquisition had to be reported (Table 1).

Several categories of studies were excluded from the outset. Work published before 2020 was not considered, nor were non-original outputs such as reviews, editorials, or conference abstracts. Studies conducted exclusively with expert surgeons performing live clinical procedures fell outside the scope unless a formal training element was present. Where AR could not be disentangled from VR or MR, or where all reported outcomes were subjective in nature, studies were similarly excluded—as were those lacking any comparator.

The 2020 cutoff was a deliberate methodological choice rather than an arbitrary date. AR hardware and software underwent substantial development around 2018‐2019, and a good deal of earlier work was conducted using prototype or near-prototype systems that bear little resemblance to the tools in use today. Including that literature risked drawing conclusions that would not generalize meaningfully to contemporary training contexts, so it was excluded on those grounds. The 2020 cutoff marks the transition from prototype-based research to the use of enterprise-grade, high-fidelity hardware (eg, Microsoft HoloLens 2 and Magic Leap One). Including earlier data from low-resolution prototype systems would introduce technological bias and yield conclusions that do not generalize to contemporary surgical training environments.

Six electronic databases were searched: PubMed (MEDLINE), Ovid MEDLINE, Embase, IEEE Xplore, Scopus, and Web of Science. The selection was deliberate rather than exhaustive for its own sake. AR in surgical training sits at the intersection of clinical medicine and engineering, and no single database captures that breadth adequately—so the combination was chosen to reflect it. PubMed, Ovid MEDLINE, and Embase covered the biomedical literature, with Embase included specifically because its indexing patterns differ enough from PubMed to reduce the risk of missing relevant work, consistent with Cochrane Handbook recommendations on database selection [19]. IEEE Xplore addressed the engineering and technology side of the literature, where much of the platform development and human-computer interaction research is published. Scopus and Web of Science brought broader multidisciplinary coverage across both domains.

Google Scholar was not included in the primary database search. Reasons for this included the search base’s nontransparent indexing algorithm, inclusion of non–peer-reviewed sources, and absence of a reproducible search interface. These issues would result in the search falling short of the reproducibility standards required by PRISMA and the Cochrane Handbook, which we aimed for [19,21]. The search across all 6 databases was executed on April 24, 2026, with results filtered to the eligibility window of January 1, 2020, through September 15, 2025. Reference lists of relevant systematic reviews identified during screening were then hand-searched to capture any eligible work that database searching alone might have missed.

Our search strings were drafted by combining Medical Subject Headings (MeSH) terms with free-text keywords, referring to the PICO framework. We also reflected on guidance from Chapter 4 of the Cochrane Handbook [19]. There were 3 domains in particular that formed the backbone of the search strategy: the technology itself (augmented reality), the population and setting (surgical or procedural trainees), and the outcome domain (technical performance or skill acquisition). Boolean operators (AND, OR) were then used to combine terms within search strings. Truncation with wildcards was applied where database syntax allowed. The full PubMed search string is provided in Textbox 1.

This search strategy was adapted for the syntax and controlled vocabulary of each database. For IEEE Xplore, MeSH terms were replaced with IEEE Thesaurus terms if appropriate. For Scopus and Web of Science, equivalent field tags (TITLE-ABS-KEY) were used with the same conceptual terms. For Ovid MEDLINE and Embase, the Ovid MeSH explode function was used to capture all relevant subheadings. Full search strategies for all 6 databases are provided in Multimedia Appendix 1, reported in line with the PRISMA-S guideline [20].

A data restriction of January 1, 2020, to September 15, 2025, was applied across all databases. No language filter was applied at the search stage itself. We felt that by restricting the language at that point, we risked inadvertently suppressing relevant records before they could be assessed. Non-English records that did not come through were excluded at screening. Similarly, no publication type or study design filters were applied during the initial search. This was on the basis that this runs the risk of missing eligible studies that could be indexed or tagged inconsistently across databases.

All records retrieved from the 6 databases were imported into Rayyan (Qatar Computing Research Institute) for deduplication and screening. Rayyan automatically identified potential duplicates, which were manually verified and removed, leaving 1417 unique records for screening. Study selection was then conducted in 3 sequential stages by two independent reviewers (MEA and YA). In the first stage, titles of all 1417 unique records were screened against the prespecified eligibility criteria, reducing the pool to 101 records. In the second stage, the 101 records were reviewed through a detailed assessment of their abstracts against the full eligibility criteria to determine if they could pass onto the next stage. In the third stage, full texts of the 29 records were retrieved and assessed independently for final inclusion. Records for which full text could not be obtained via institutional access or interlibrary loan were pursued via direct author contact before being counted as inaccessible. Discrepancies at all stages were resolved through discussion and consensus between the two reviewers. If consensus could not be reached, a third senior reviewer (TY) acted as adjudicator. The reasons for exclusion at each stage are documented and reported in the PRISMA flow diagram.

Data extraction was carried out independently by two reviewers (MEA and YA) using a prestandardized form built in Microsoft Excel. Before the main extraction began, the form was piloted on two studies and adjusted where wording was ambiguous, or fields needed refinement. This was a small but useful step that avoided inconsistencies surfacing later in the process.

The form captured 7 categories of information: study identification details (first author, year, country, and journal); study design; participant characteristics, including specialty, training level, total sample size, and group allocation; details of the AR intervention, covering the specific platform and device used, what the AR content actually consisted of, and how it was delivered; comparator characteristics; the task or procedural scenario; and all reported outcomes measures including primary and secondary endpoints alongside their associated statistical results, including means (SDs), P values, and effect sizes if reported.

Responsibility for extraction was shared equally between MEA and YA. If the two reviewers disagreed on whether a data point should be included, they discussed this together with adjudication by a third reviewer (TY) if no consensus could be reached.

Risk of bias was assessed independently by two reviewers (MEA and YA) using a tool selection determined by the study design. Randomized controlled trials (RCTs) were assessed using the Cochrane Risk of Bias 2 (RoB 2) tool [22]. Nonrandomized prospective cohort studies were assessed using the Risk of Bias in Nonrandomized Studies of Interventions (ROBINS-I) tool [23]. Crossover randomized trials were assessed using the RoB 2 tool with the crossover extension, as crossover designs remain RCTs and ROBINS-I is not applicable to them. Disagreements between reviewers were resolved by discussion; unresolved disagreements were adjudicated by the third reviewer (TY). Risk-of-bias findings are presented narratively in the Results section and considered in the interpretation of the overall body of evidence.

Given the substantial clinical heterogeneity across included studies in terms of AR platforms used, participant training levels, surgical specialties, comparator conditions, and outcome measures used, statistical pooling (meta-analysis) was not appropriate and was not performed. No standardized effect sizes (eg, Cohen d and standardized mean difference) were reported by included studies in a sufficiently consistent form to enable pooling; where individual studies reported effect sizes, these are noted in the narrative synthesis. Findings were synthesized narratively following the SWiM reporting guideline [18]. Studies were grouped according to five prespecified thematic outcome domains derived during the protocol stage: (1) technical accuracy and procedural performance, (2) error reduction and procedural safety, (3) learning trajectory and skill acquisition, (4) cognitive load and gaze efficiency, and (5) operational efficiency and procedure time. Within each domain, consistency and heterogeneity of findings across studies were assessed narratively, and the direction and magnitude of effects were described in relation to methodological quality.

The systematic search returned 4596 records across the 6 databases (Scopus: 1640; Web of Science: 1039; IEEE Xplore: 790; Embase: 638; Ovid MEDLINE: 438; PubMed: 51). A further 203 records came from reference list checking and gray literature searching, bringing the total to 4799. Rayyan automatically identified 3382 potential duplicates, which were manually verified and removed, leaving 1417 unique records for screening.

MEA and YA independently screened all 1417 records by title, excluding 1316. The most common reasons were: no AR component or AR not separable from VR/MR (n≈478), no objective performance outcome (n≈369), not involving surgical or procedural trainees (n≈210), not an interventional study design (n≈171), no comparator group (n≈85), and non-English language (n≈3). Disagreements were resolved by consensus. The remaining 101 records proceeded to a detailed abstract review.

Both reviewers independently assessed all 101 abstracts, excluding 72. The main reasons were technology development or validation studies with no trainee performance outcomes (n=26), no clearly defined novice or trainee population (n=18), outside scope (n=14), non-original research formats including systematic reviews and editorials (n=8), and nontrainee participants (n=6). Where the two reviewers could not reach agreement through discussion, TY adjudicated. Twenty-nine records were then retrieved for full-text assessment.

At full-text review, again conducted independently by MEA and YA, 18 articles were excluded. Reasons were: AR present in the setting but not functioning as the instructional component (n=5); usability or feasibility assessment only, with no objective performance outcomes (n=4); AR inseparable from a VR or MR environment (n=3); no comparator or control condition (n=3); anatomy identification study without any surgical skill training component (n=2); and full text inaccessible despite institutional access attempts, an interlibrary loan request, and direct contact with the authors (n=1). Disagreements were again resolved by discussion, with TY available for adjudication where needed. Eleven studies met all prespecified eligibility criteria and were included in the final narrative synthesis. The full selection process is shown in the PRISMA 2020 flow diagram (Figure 2).

The 11 included studies span 2021 to 2025 and together enrolled 347 participants. Nine were RCTs—5 parallel-group [3,5,6,8,9], 3 crossover [1,4,7], and 1 three-arm [11], with the remaining 2 being prospective cohort comparisons [2,10]. Sample sizes ranged from 8 (Liu et al [2]) to 60 (Wild et al [7]). Across all studies, participants had no or very limited prior experience in the procedure being trained. Seven specialties featured in the included work: minimally invasive and laparoscopic surgery (n=4), open and basic surgical skills (n=2), neurosurgery (n=2), neurovascular and cerebrovascular surgery (n=1), otology (n=1), and spine surgery (n=1). Full characteristics of each included study are provided in Table 2.

The Microsoft HoloLens (versions 1 and 2) was the most commonly used AR platform, applied in 5 of the 11 included studies [1,6,8,9,11]. The HoloLens is an optical see-through HMD capable of projecting holographic content into the user’s visual field while preserving contact with the physical environment. Three studies used the iSurgeon telestration system, a laparoscopic screen-based AR device that projects a real-time feed of the instructor’s hand gestures onto the operative monitor [3,4,7]. The Magic Leap One combined with the Brainlab Mixed Reality Viewer and intraoperative heads-up display was used in one neurosurgical study [2]. The Vuzix M300XL smart glasses were evaluated in one suturing study [5]. Kong et al [10] used the HoloLens 2 in combination with custom surgical guides and the Vuforia 3D registration software for spinal navigation, and Dodier et al [11] used the HoloLens 1 to deliver holographic finite-element simulation of aneurysm clipping.

Risk of bias assessment findings are summarized narratively below. Among the 9 RCTs, 6 were assessed as having some concerns regarding randomization or blinding processes [1,3,4,7,9,11]; full blinding of participants and instructors to group allocation is inherently unfeasible in AR training studies, representing a structural limitation of all trials in this field. The remaining 3 RCTs [5,6,8] were assessed as low risk across all domains. The 2 nonrandomized studies [2,10] were assessed using ROBINS-I and rated as moderate risk, reflecting their small sample sizes and lack of formal randomization, though both did use internal controls. Outcome assessment blinding was reported in 4 studies [5,6,8,9], which goes some way toward reducing detection bias. None of the included studies reported any long-term follow-up or skill retention data—a gap that runs consistently across the entire evidence base.

This systematic review synthesizes evidence from 11 contemporary studies (2021‐2025) evaluating AR’s impact on the objective technical performance of surgical trainees. The principal finding is that AR demonstrates a consistent, measurable positive effect on technical performance, most strongly in domains requiring visuospatial reasoning, spatial anatomical understanding, and procedural accuracy. Of the 11 studies, 9 reported at least one significant improvement in an objective technical performance metric. The 2 studies that did not demonstrate AR superiority [5,9] nonetheless showed noninferiority, with AR-trained groups performing equivalently to comparators on skill quality metrics while achieving time advantages in independent performance. The absence of superiority in lower-stakes basic skills tasks is not evidence of inefficacy; it may reflect a ceiling effect in tasks where traditional instruction is already adequate for novice performance.

Across the body of evidence, the most robust performance advantages were observed in tasks with a strong visuospatial or spatial navigation component: EVD placement [6], aneurysm localization [2], mastoidectomy drilling [8], and pedicle screw placement [10]. This pattern is theoretically coherent: AR’s capacity to render 3D anatomical structures in the trainee’s visual field directly addresses a fundamental cognitive challenge in procedural surgery: the mental reconstruction of volumetric anatomy from 2D imaging data.

The findings of this review are consistent with, and substantially extend, the conclusions of prior systematic reviews. Abu Halimah et al [15] and Xiong et al [16] identified broad potential for AR in surgical skills training, but their reviews included older studies with heterogeneous definitions of AR and outcomes. By restricting our scope to post-2020 studies with objective outcomes and clear AR definitions, we provide a more precise assessment applicable to current training environments. Importantly, this review positions AR and VR as complementary rather than competitive modalities, a distinction emphasized in the literature [11,24].

The observed expertise reversal pattern, AR providing the greatest benefit to novices with diminishing returns at higher levels of proficiency, is consistent with predictions from both cognitive load theory [12] and the expertise reversal effect [14]. In Kong et al [10], AR navigation essentially equalized the novice-expert performance gap. This pattern has direct implications for curriculum design: AR-assisted training may be most efficiently used during the early stages of procedural learning, with progressive withdrawal of AR guidance as competency develops, a strategy consistent with the scaffolding framework in educational theory [25,26].

The gaze-guidance mechanism elucidated by Felinska et al [4] provides the most direct experimental evidence for the cognitive mechanism underpinning AR’s training benefit. By demonstrating that AR telestration reduced gaze latency tenfold and aligned trainee gaze with expert gaze, this study demonstrates that AR’s error-reducing effect is mediated by directing visual attention to operationally relevant anatomical regions more efficiently than verbal instruction.

Dodier et al [11] finding that only the combined video-plus-AR cohort achieved a significant improvement in aneurysm occlusion rate (67% to 93%; P=.05) is particularly noteworthy. The holographic AR clipping simulation allowed residents to test different clipping strategies on the exact same patient-specific anatomy as the physical phantom, a form of deliberate practice that is impossible with traditional simulation.

Several limitations of the constituent studies and of this review must be acknowledged. The most fundamental limitation is heterogeneity: the 11 included studies span 7 surgical specialties, use 6 distinct AR platforms, and measure outcomes using a wide variety of instruments, precluding statistical synthesis. Sample sizes were consistently small (range: 8‐60 participants), limiting statistical power. Publication bias cannot be excluded.

None of the 11 included studies reported long-term follow-up of skill retention or assessed the transfer of AR-trained skills to the real operating room or clinical environment. This is perhaps the most significant gap in the current evidence base. Device-related limitations were noted across several studies, including physical discomfort associated with prolonged HMD use [6] and interface familiarization time across HoloLens-based studies. The risk of bias assessment found some concerns in 6 of 11 RCTs, predominantly related to allocation concealment and blinding, which is an inherent structural limitation of AR training trials rather than a correctable methodological weakness. The review was not prospectively registered, which is acknowledged as a limitation.

One study for which full text could not be obtained despite institutional access, interlibrary loan request, and direct author contact was excluded; this represents 1 of 29 full-text articles reviewed (3.4%) and, given the consistency of findings across the 11 included studies, is unlikely to materially alter the direction of the conclusions.

The current evidence points toward several concrete priorities for future work. Most pressing is the need for adequately powered multicenter randomized trials across the more promising AR platforms and specialty domains, using standardized outcome measures that would actually allow findings to be compared across studies—something the current literature makes difficult. Alongside this, longitudinal studies with skill-retention assessments at 3, 6, and 12 months posttraining are needed to establish whether the performance gains associated with AR hold over time or fade once the technology is removed. Transfer studies examining whether AR-trained skills translate meaningfully into clinical performance are a logical next step that the field has yet to take seriously. Finally, cost-effectiveness analyses will matter enormously for any health system considering curriculum-level adoption—the training benefit needs to be weighed against the real costs of hardware, software, and implementation, and that work has not yet been done.

This review found consistent evidence that AR improves technical performance in surgical novices—reduced procedural errors, better accuracy, faster progression along the learning curve, and lower cognitive load, particularly in tasks with high visuospatial demands. The expertise reversal pattern that emerged across multiple studies is worth taking seriously: AR appears to deliver its greatest benefit during the early, high-error phase of skill acquisition, with returns diminishing as experience accumulates. That finding has practical implications for how AR should be used—not as a permanent scaffold, but as a targeted intervention in early training, with guidance progressively withdrawn as competency develops.

What this review cannot claim is that the evidence is mature. Sample sizes are small, platforms vary enormously, outcome measures are inconsistent, and no study has yet examined whether skills are retained or transferred to real clinical settings. AR shows genuine promise as an adjunct within structured surgical curricula—not a replacement for expert mentorship or traditional teaching, but something that adds real value when used thoughtfully alongside them. Turning that promise into confident implementation guidance will require the kind of rigorous, large-scale, longitudinal work that the field has not yet produced.