Patients in the intensive care unit (ICU) often experience a series of physical, cognitive, and psychological impairments after discharge due to factors such as physiological dysfunction, surgical trauma, pain, and reduced social interaction [1]. In 2010, the Society of Critical Care Medicine first introduced the term “post-intensive care syndrome (PICS)” to define this phenomenon [2,3]. The manifestations commonly include weakness, pain, anxiety, sleep disturbances, and cognitive dysfunction, which can persist for months or even years. Studies indicate that 47.9% of patients still exhibit cognitive impairment 3‐6 months after transfer from the ICU [4]; 68% (355/523) report persistent pain after discharge, with pain intensity remaining at a moderate level even 1 year later [5]. Additionally, 55% of patients experience sleep disturbances within the first month after discharge [6]. Furthermore, 12.3% (98,530/799,645) of critically ill patients are diagnosed with depression or anxiety after discharge, and these patients demonstrate higher long-term mortality rates [7]. PICS severely compromises patients’ quality of life, reduces functional independence, and imposes a significant care burden on families and society [8].

To reduce long-term impairments after critical illness, the Society of Critical Care Medicine recommends that health care professionals assess patients and coordinate care strategies for injury management beginning at ICU admission [9]. As clinical treatment advances, early functional recovery has become a key focus for preventing PICS [10]. Early rehabilitation is generally initiated within 72 hours of ICU admission, following achievement of hemodynamic and respiratory stability (typically within 24‐48 h) [11,12]. It commonly includes early physical activity [13,14], neurocognitive stimulation [15,16], psychological intervention [17], and multimodal programs [18]. Existing meta-analyses confirm that routine early rehabilitation started within 72 hours may improve physical and cognitive function, help prevent PICS without increasing adverse events [19], and reduce the incidence of ICU-acquired weakness [20]. However, no differences have been found in cognitive-related delirium-free days or Hospital Anxiety and Depression Scale scores. Another meta-analysis on nurse-led early rehabilitation showed it significantly shortens ICU length of stay, although effects on functional outcomes, such as mobility, muscle strength, and mortality, were not significant [21]. These inconsistencies may relate to factors including the time-intensive nature of current measures, insufficient standardization in implementation, and low patient participation and adherence.

Virtual reality (VR), a term first introduced by computer scientist Jaron Lanier in 1989, refers to a simulation technology providing users with an immersive environmental experience [22]. VR technology integrates computer, electronic information, and simulation technologies to enable users to interact with the VR system and experience an immersive, tactile, visual, and multisensory environment via VR helmets, all-in-one devices, and other gadgets [23]. The system is known for its novelty, interactivity, and immersive qualities [24]. VR technology–based rehabilitation techniques have been widely adopted in clinical rehabilitation. There is evidence suggesting that these techniques can effectively improve cognitive function in patients with stroke [25], reduce pain levels in patients with chronic low back pain and neck pain [26,27], and alleviate anxiety and depression [28,29].

Virtual reality–based early rehabilitation intervention (VR-ERI) is an emerging ICU recovery strategy that is gaining attention and has shown preliminary application results. Using VR technology, it provides ICU patients with specific virtual environments, such as natural landscapes [30], meditation music [31], or virtual tasks (such as memory games [32]), and cognitive exercises like “catching coconuts” and “avoiding obstacles” [33]. This aims to enhance rehabilitation motivation, participation, and physiological and psychological function. Its interactive, immersive, and feedback-driven design makes VR-ERI a promising tool for personalized early rehabilitation in critically ill patients. However, current research findings are inconsistent. Some studies report that VR-ERI effectively reduces anxiety [32], while others show no significant difference [34,35]. Such discrepancies may affect the certainty and consistency of clinical decision-making, potentially hindering the technology’s wider adoption in ICU early rehabilitation.

To our knowledge, researchers [36] have explored the interventional effects of VR therapy on patients’ PICS through a meta-analysis, but its included population did not specifically focus on early rehabilitation strategies during the ICU period. This analysis pooled data from patients receiving VR therapy both within the ICU and during follow-up after discharge. Due to differences between these 2 populations in aspects such as intervention timing and environment, combining them in the analysis may introduce clinical heterogeneity, thereby weakening the credibility of the results. Another meta-analysis indicated that compared with traditional rehabilitation, VR-based early motor rehabilitation can improve balance, functional walking, and upper and lower limb motor function in critically ill patients [37]. However, this review only assessed motor function and did not comprehensively examine the effects on other early rehabilitation outcome indicators.

This systematic review and meta-analysis aim to (1) characterize the types and content of VR-ERI activities and analyze the feasibility and safety of VR technology implementation in critically ill patients; (2) systematically evaluate the effectiveness of VR-ERI on physiological, psychological, and cognitive outcomes during ICU treatment and at short-term follow-up (within 3 months post-ICU discharge); and (3) provide recommendations for future research.

The review protocol was registered in PROSPERO. This systematic review was conducted in accordance with the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) 2020 statement [38] to ensure transparency (Checklists 1-3).

During implementation, the search language was limited to Chinese and English to ensure assessment accuracy, and the search cutoff date was extended to October 5, 2025, to incorporate the latest evidence. Regarding statistical analysis, due to heterogeneity among the included studies, all analyses adopted the more conservative random-effects model. To enhance statistical robustness, the analysis was switched to the R language (version 4.4.1; R Core Team), and the Hartung-Knapp-Sidik-Jonkman method was applied to correct random-effects outcomes. This method provides more conservative CIs when the number of studies is small, reducing the risk of false-positive results in the presence of high heterogeneity. Apart from the above adjustments, all other procedures remained consistent with the original protocol.

Two independent researchers (FW and YW) conducted literature searches across 6 English-language and 4 Chinese-language databases. MEDLINE and Embase were searched simultaneously via the Ovid platform. The other English databases were searched on their respective platforms—PubMed (via National Center for Biotechnology Information), Web of Science (via Clarivate Analytics), the Cochrane Library, and PsycINFO (via ProQuest). The Chinese databases searched were China National Knowledge Infrastructure (CNKI), WanFang Data, VIP Database (VIP), and the SinoMed Service System (SinoMed). The search strategy combined Medical Subject Headings with free-text terms using Boolean operators. The search was performed in 2 stages. An initial search covered records from the inception of each database until May 11, 2025, and to incorporate the most recent evidence, the full search strategy was rerun on October 5, 2025, extending the cutoff date accordingly. All searches were limited to Chinese and English publications to align with the team’s language capabilities and ensure feasibility.

All search strategies were independently designed based on the research question and were peer-reviewed and refined by experts in evidence-based medicine and critical care medicine in accordance with the PRISMA-S (Preferred Reporting Items for Systematic reviews and Meta-Analyses literature search extension) checklist [39]. No published search filters were used, nor were search strategies from other systematic reviews adapted or reused. To cover the literature as comprehensively as possible, we also used the snowballing method to trace references and citations and attempted to obtain full-text articles by contacting librarians or the original authors. Furthermore, as this study focused on published efficacy evidence, we did not specifically search clinical trial registries or gray literature (including conference proceedings). The complete search strategies and procedures are detailed in Multimedia Appendix 1.

The rationale for formulating inclusion and exclusion criteria was based on the Population, Intervention, Comparison, Outcome, and Study Design (PICOS) framework, (1) population: adults aged ≥18 years receiving treatment during their ICU stay; (2) intervention: VR-ERI; (3) control: no treatment, usual care measures, or non–VR-based interventions; (4) outcomes: studies reporting at least 1 physical, psychological, or cognitive function outcome (such as cognition, pain, delirium, anxiety, depression, and sleep quality) or feasibility and safety outcomes during ICU treatment or after ICU transfer; and (5) study design: randomized controlled trials (RCTs) published in Chinese or English. The exclusion criteria were (1) studies that did not report original outcome measures and for which relevant outcome data could not be obtained after contacting the authors; (2) duplicate publications; and (3) case reports, letters, conference abstracts, and review articles.

In total, 2 independent researchers (FW and YW) conducted the literature screening and data extraction, followed by cross-checking. Any uncertainties were resolved by WC. First, duplicate records were automatically identified and removed using the built-in function of the EndNote X9 (Clarivate) reference management software, based on fields such as title, author, publication year, and journal name. Subsequently, the 2 researchers (FW and YW) independently examined the titles, authors, and other key information of the remaining records to further exclude any duplicates not detected by the software. Next, titles and abstracts were reviewed to exclude obviously irrelevant literature. Finally, full texts were retrieved and assessed against the eligibility criteria to determine the final set of included studies.

A total of 2 independent researchers (FW and YW) performed data extraction using a uniformly developed standardized form without using automated tools. The data that were systematically extracted were (1) general information, including first author, country, and publication year; (2) participant characteristics, including disease type, sample size, and baseline demographic and clinical characteristics; and (3) intervention characteristics, including specific type of VR, content of the VR-based intervention, content of the control group intervention, intervention duration, intervention frequency, outcome measures, measurement tools, time points of data collection and raw data (such as mean, SD, median, and IQR), for outcomes reported at baseline, post intervention, or follow-up for both groups.

To manage multiple data points objectively and consistently, we predefined selection criteria following the Cochrane Handbook [40]. The core principle was to prioritize data that best aligned with the review’s primary objective, had the highest validity, or greatest clinical representativeness. For multiple measures, we selected the tool that best matched the outcome definition or had the highest validity; for multiple intervention groups, we included the primary intervention group, the most clinically representative, or the largest in sample size; for multiple control groups, we chose the “most representative usual care” group. Where data were missing, unclear, or incomplete, we contacted corresponding authors by email for clarification or missing data. If no response was received after 2 attempts, we used recommended formulas to estimate means and SDs from available data (eg, based on sample size, median, and range) [41].

The second author (YW) and the third author (YX) independently assessed the risk of bias of the included studies using the revised Cochrane Risk of Bias tool (RoB 2) for randomized trials [42]. The RoB 2 tool assesses five domains for randomized trials, which are (1) bias arising from the randomization process, (2) bias due to deviations from the intended interventions, (3) bias due to missing outcome data, (4) bias in the measurement of the outcome, and (5) bias in the selection of the reported result. Each domain is judged against a series of signaling questions. The overall risk of bias for a study is categorized as “low,” “some concerns,” or “high.” A study is judged to have a low overall risk of bias if all domains are rated as “low.” An overall rating of “some concerns” is given if at least 1 domain is rated as having “some concerns” and no domain is rated as “high.” An overall “high” risk of bias is judged if any single domain is rated as “high” or if multiple domains are rated as having “some concerns.”

To ensure transparency in the data synthesis process, we followed a systematic decision-making procedure. First, all studies had to meet the predefined PICOS criteria and provide the raw data for the relevant outcome measures. Second, we established a rule that each study would contribute only a single data point for a given outcome. If a study contained multiple measurements or multiple group comparisons, a single dataset was selected for pooling according to the prespecified criteria, aiming to minimize heterogeneity as much as possible.

All analyses were performed using the R language (version 4.4.1) within the R Studio integrated development environment (version 2023.12). The metafor package was used for effect size pooling and forest plot generation [43], providing visual representations of each study’s effect size with its 95% CI, along with the pooled overall effect size. All included outcome measures were continuous variables. We conducted a meta-analysis using change scores (from baseline to postintervention or follow-up) in means and SDs for both groups. For studies reporting only pre- and postintervention means and SDs, the mean and SD of change scores were calculated as Mean_change=Mean_post−Mean_pre and SD__change= √ (SD__pre²+ SD__post² - 2 × r×SD__pre×SD__post), where r represents the correlation coefficient between pre- and postintervention values. When correlations were not reported in the original publications, they were calculated according to the Cochrane Handbook for Systematic Reviews of Interventions. To harmonize different assessment tools and ensure consistent direction of results, we reversed the scoring for subjective sleep quality assessed by the Pittsburgh Sleep Quality Index and cognitive scores assessed by the Perceived Deficits Questionnaire for Depression, following Cochrane Handbook guidelines [40]. Consequently, higher scores in the pooled results indicate better sleep quality and cognitive function in patients. Additionally, we categorized outcome measures by assessment time points, specifically divided into (1) during ICU treatment and (2) short-term follow-up (2 wk to 3 mo after ICU discharge).

Given the variability in assessment tools and the presence of clinical and methodological heterogeneity among the included studies, the standardized mean difference (SMD) was adopted as the effect size measure for meta-analysis outcomes. The adjusted Hedges g was used to estimate the effect sizes [44,45]. Absolute SMD values of 0.2, 0.5, and 0.8 were interpreted as small, medium, and large effect sizes, respectively [46]. A random-effects model was applied to derive more conservative effect estimates. To enhance the robustness of statistical inference, particularly in reducing the risk of false-positive results when the number of studies was limited, the Hartung-Knapp-Sidik-Jonkman adjustment was used during model fitting to estimate the pooled effect size and its 95% CI [47].

To quantify between-study heterogeneity and enhance the generalizability of the results in real-world settings, we used a comprehensive assessment strategy. First, absolute heterogeneity was quantified using τ² (between-study variance) and its square root τ (between-study SD) [48]. τ² provides an absolute measure of the variation between studies, while τ, being on the same scale as the effect size, facilitates clinical interpretation. Second, the Cochran Q test was used for the hypothesis testing of effect size homogeneity, supplemented by the I² statistic to quantify the relative extent of heterogeneity [49], with thresholds of 25%, 50%, and 75% used to define low, moderate, and high levels, respectively [50]. Finally, for outcome measures involving at least 3 studies, 95% prediction intervals (PIs) were calculated [51] to estimate the potential range of the true effect size in future similar interventions, thereby providing more clinically informative guidance for practice.

Subgroup analyses were performed to explore potential sources of heterogeneity. A leave-one-out sensitivity analysis was conducted to assess the robustness of the pooled results. For outcome measures with fewer than 2 included studies, descriptive analyses were performed. Additionally, to assess the potential for small-study effects (such as publication bias), we performed several checks for the anxiety outcome, which had the largest number of included studies (n=8). These included a visual inspection of funnel plot symmetry, the Egger test (regression test), and the Begg test (rank correlation test). Furthermore, the trim-and-fill method was used to estimate the potential number of missing studies and to compute an adjusted effect size, thereby evaluating the potential impact of small-study effects on the pooled result. The threshold for statistical significance was set at P≤.05.

To evaluate the reliability of the evidence, we used the Grading of Recommendations Assessment, Development, and Evaluation (GRADE) framework [52] to rate the certainty of evidence for each outcome. In addition, 2 independent raters (FW and YW) assessed the certainty of evidence using the official GRADE pro GDT software (Evidence Prime Inc), with any disagreements resolved by the corresponding author (RZ). The evidence was rated as very low, low, moderate, or high. Footnotes were provided to explain the reasons for any downgrading of the evidence, which included considerations of risk of bias, inconsistency, indirectness, imprecision, and publication bias.

This study used literature data and did not require approval from an ethics review committee or patient consent.

A total of 3737 studies were identified from 10 databases. After removing 243 duplicate articles, the titles and abstracts of the studies were initially screened, and 58 full-text manuscripts relevant to this study were identified. Following full-text reading and quality assessment, 16 RCTs [16,17,30,32-35,53-61] were ultimately included for analysis. The specific search and inclusion process is illustrated in Figure 1, and the excluded articles after rescreening, along with the reasons, are detailed in Multimedia Appendix 2.

Multimedia Appendix 3 summarizes the basic characteristics of the included studies. The 16 studies (published between 2020 and 2025) comprised a total of 1356 participants, with sample sizes ranging from 42 to 180. The studies originated from Brazil [53], Korea [30,54], France [17,35], Spain [16], Turkey [34], and China [32,33,55-61]. Patient conditions included cardiovascular diseases [30,35,53,55,60], postcraniotomy [33], postliver transplantation [61], postlaparoscopic sleeve gastrectomy [34], conventional oncologic surgery [32], severe respiratory diseases [58], and postmultiple fracture surgery [56], among others. The mean age of patients was generally between 60 and 70 years. Interventions were initiated within 24 hours after ICU admission in 3 studies [35,53,59], within 6 hours in 2 studies [32,34], and on the day of ICU admission once the patient’s condition was stabilized in the remaining 11 studies [16,17,30,33,54-58,60,61].

One study [16] used nonimmersive VR technology, while 15 studies [17,30,32-35,53-61] used fully immersive VR. The intervention directions included (1) early cognitive rehabilitation (training reaction and executive function through games or tasks) [16,33,55,57], (2) early motor rehabilitation (engaging in virtual activities, such as fruit cutting or cycling combined with motion capture) [53,56,58,59,61], (3) early delirium prevention (providing emotional support and cognitive training for multidimensional prevention) [32], (4) VR relaxation therapy (conducting physical and mental relaxation in natural scenes) [17,34,35], (5) VR meditation (improving sleep and mood by combining mindfulness) [30,54], and (6) VR preoperative visit (structured introduction to the ICU environment, treatment process, and rehabilitation) [60]. The intervention protocols were categorized into (1) single-session short-term intervention (15‐30 min at key clinical time points) [17,30,34,35,60], (2) high-frequency short-term intervention during ICU stay (approximately 20 min per session, 1‐3 times daily, lasting 3‐7 d) [16,32,54,55,57-59], (3) medium- to long-term structured intervention (30‐40 min per session, 5 d per wk, lasting 2 wk to 3 mo) [33,56,61], and (4) flexible individualized protocol (adjusted based on patient tolerance) [53]. The studies involved a total of 24 outcome measures, such as cognitive function, delirium, anxiety, depression, pain, sleep, and quality of life, although the assessment tools and observation windows varied across studies.

The overall risk of bias for the studies included in this review was high, with summary results presented in Figures 2 and 3, and detailed assessment results available in Multimedia Appendix 4. Furthermore, 1 study [58] was rated as “low,” 5 studies [17,32,34,54,55] raised “some concerns,” and 10 [16,30,33,35,53,56,57,59-61] were rated as “high.” In domain 1 (randomization process), 7 studies [33-35,53,56,60,61] did not describe allocation concealment, and 1 study [32] described neither the method for generating the random sequence nor allocation concealment; all were rated as “some concerns.” For domain 2 (deviations from intended interventions), 4 studies [16,32,55,57] were rated as “some concerns” due to lack of blinding of patients and implementers; 1 study [59] was rated as “high” because it lacked blinding and did not adhere to the intention-to-treat analysis principle. In domain 3 (missing outcome data), 2 studies [16,59] were rated as “high” due to a high rate of loss to follow-up and because the reasons for missing data were potentially related to health status. For domain 4 (measurement of the outcome), 11 studies [16,17,30,32,33,35,53,56,57,60,61] had issues with the lack of blinding of outcome assessors. Among these, 9 studies [16,30,33,35,53,56,57,60,61] were rated as “high” because they measured subjective patient-reported outcomes (eg, pain and anxiety), and 2 studies [17,32] were rated as “some concerns” as their outcome measures were relatively objective. In domain 5 (selection of the reported result), transparency was generally insufficient. Moreover, 4 studies [16,17,35,55] mentioned trial registration but lacked verifiable prespecified analysis descriptions for the reported results, while the remaining 11 studies [30,32-34,53,54,56,57,59-61] did not mention a preregistered protocol; consequently, all were rated as “some concerns.”

In total, 8 studies [16,17,35,53,55,57-59] reported on safety, 5 studies [16,55,57-59] confirmed the absence of serious adverse events but documented related reactions including dizziness [16,35,57], nausea [35,57], fatigue [16,17], anxiety [16,17], confusion [16,55], visual disturbance [17], headache or discomfort from wearing the headset [55], claustrophobia, agitated withdrawal, and dyspnea due to device displacement [17]. Furthermore, 1 study reported a significant drop in blood pressure during intervention in a patient [59], another reported a case of excessive drowsiness [16], and 1 noted that vital signs in all patients fluctuated within the normal range (±10%) during the intervention [58]. Regarding feasibility, 1 study reported a 78.3% patient recommendation rate and a 90% “good/excellent” experience rating [53]. Meanwhile, 2 studies reported that patients in the VR group demonstrated significantly better outcomes in terms of daily total exercise time, average daily out-of-bed activity time [58], and exercise adherence (with a high adherence rate of 71.74% vs 54.35% at 3 months) [56].

Among the included trials, due to the limited number of studies, we conducted meta-analyses on outcome indicators with at least 2 studies. The specific analysis results are as follows.

Although the number of included studies for all outcomes in this review did not meet the recommended threshold for conventional statistical tests of publication bias (≥10 studies), we still performed an exploratory analysis on the anxiety outcome, which had the largest number of included studies (n=8). This was done to preliminarily assess the potential impact of bias on the robustness of the conclusions.

The funnel plot (Figure 11) appeared approximately symmetrical by visual inspection. Statistical test results showed that the Egger linear regression test did not indicate significant small-study effects (t₆=−1.94; P=.10). However, the Begg rank correlation test suggested the possible presence of publication bias (z=−2.47, P=.01). To quantify the potential impact of missing studies on the pooled result, a trim-and-fill analysis was conducted. The analysis estimated that 1 potentially missing study needed to be imputed. The adjusted pooled effect size changed from the original SMD −0.862 (95% CI −1.853 to 0.129) to SMD −0.495 (95% CI −1.719 to 0.729), a change of 0.367. The decrease in the absolute value suggests that, if bias exists, its influence may have led to an overestimation of the intervention effect.

We fully acknowledge that with only 8 included studies [16,17,32,34,35,55,57,60] and substantial heterogeneity present, the statistical power of these tests is limited. Furthermore, heterogeneity itself can interfere with the interpretation of funnel plot asymmetry. Therefore, the above results should be considered exploratory. In summary, the current analysis, while suggesting that publication bias cannot be entirely ruled out, does not provide evidence from the Egger test supporting significant small-study effects. Moreover, the CI for the effect size adjusted by the trim-and-fill method remained wide and crossed the line of null effect. This indicates that, even if potential bias exists, the current conclusion regarding the anxiety outcome is stable. However, it serves as a reminder to interpret the magnitude of this effect size with caution in the future.

This review systematically assessed the feasibility, safety, and rehabilitation outcomes of VR-ERI in critically ill patients across 16 RCTs [16,17,30,32-35,53-61] (n=1356). VR-ERI was well-accepted and associated with high exercise adherence. Vital signs remained within acceptable ranges during use, and no serious adverse events were reported; however, mild dizziness, nausea, and fatigue occurred in some studies, underscoring the need for standardized safety monitoring. Regarding efficacy, VR-ERI improved balance during short-term follow-up, supported by low heterogeneity, narrow PIs, and moderate-certainty evidence, indicating robust and potentially generalizable benefit. VR-ERI also shows potential to improve in-ICU anxiety and subjective sleep quality, as well as short-term cognitive and motor function, particularly sleep, when assessed with the RCSQ. However, it did not significantly improve objective sleep parameters or in-ICU pain. For most outcomes, the certainty of evidence was low or very low due to implementation bias (eg, lack of blinding), study inconsistency, and imprecision in pooled estimates. Thus, results should be interpreted cautiously, and current evidence remains insufficient for definitive conclusions. Some outcomes could not be pooled due to limited studies. Further high-quality trials are needed to confirm these findings and clarify the clinical value of VR-ERI in critical care.

VR-ERI may reduce anxiety in critically ill patients, a finding consistent with recent reviews in both critical care [36] and elective surgery [62], suggesting VR could broadly mitigate hospital-related anxiety. Stress recovery theory [63] offers a possible explanation, proposing that exposure to natural landscapes can activate the parasympathetic nervous system and promote emotional relaxation. Research confirms that biophilic elements aid stress recovery [64]. Most VR-ERI scenarios in the included studies incorporated natural views (eg, mountains and rivers), which may help block typical ICU stressors, such as constant light, noise, and isolation. However, the pooled effect in this analysis was not statistically significant, and the 95% PI crossed zero, indicating instability in the estimate. The included studies also had a high risk of bias, with substantial inconsistency and imprecision, yielding very low certainty of evidence. Thus, future rigorous RCTs with adequate sample sizes and transparent reporting are needed to clarify VR’s effect on anxiety in this population.

VR-ERI shows potential in improving ICU patients’ subjective sleep quality, likely due to its intervention design—2 protocols [30,54] used VR meditation and hypnosis modules to promote relaxation and distraction, enhancing perceived sleep quality [30,54]. However, objective parameters measured with smart wristbands (eg, TST and sleep efficiency) did not improve concurrently, suggesting VR may modulate sleep perception rather than alter sleep physiology. A recent network meta-analysis [65] found that simple interventions like eye masks and earplugs offer more consistent sleep benefits in critically ill patients, while the effect of VR meditation remains unestablished, underscoring VR’s uncertain role in sleep intervention. Subgroup analysis indicated positive effects only when sleep was assessed with the RCSQ, not with other subjective scales. This highlights how tool selection influences outcomes, possibly because the RCSQ focuses more on immediate sleep depth and is designed specifically for critically ill patients. Future research should use standardized, population-specific sleep assessment tools to accurately capture intervention effects. Current evidence is limited by low certainty. Future studies should develop standardized VR sleep protocols, clarify optimal dosage, and incorporate objective measures, such as polysomnography or validated wearable monitoring, to systematically evaluate VR’s impact on sleep architecture, thereby building a more reliable evidence base for practice.

We also observed that VR-ERI can improve balance (measured by Berg Balance Scale) and limb motor function (measured by Fugl-Meyer Assessment) in critically ill patients during short-term follow-up. This finding is consistent with the review by He et al [37] on VR for early motor intervention in this population. By providing an immersive environment, VR compensates for the sensory and interaction deficits resulting from prolonged immobilization and isolation. It enhances sensorimotor pathways and balance-related neuroplasticity through visual-vestibular-proprioceptive integration [66]. Furthermore, VR-ERI engages both cognitive and motor functions simultaneously [67] and promotes cortical activation via feedback-driven learning and task-specific adaptation [68,69]. The engaging and gamified design of VR-ERI may also improve patient adherence to exercise, which could explain its advantage over traditional motor rehabilitation. Improvement in balance is supported by moderate-quality evidence and relatively narrow PIs, suggesting that standardized VR-ERI motor activities could be implemented early in critical care rehabilitation, with attention to personalized parameters and long-term effect tracking. However, evidence for limb motor improvement remains low in certainty and requires further rigorous validation.

However, VR-ERI did not demonstrate a statistically significant effect on reducing pain in critically ill patients during ICU treatment, a result that may be associated with several factors. The pain experience of critically ill patients is particularly complex, as frequent threats to psychological and physical integrity make their pain difficult to manage effectively [70]. Neuroimaging studies have shown that receiving VR intervention during painful stimuli can significantly reduce excitability in brain regions associated with pain processing, with a higher level of VR immersion correlating with stronger inhibitory effects [71]. Concurrently, immersive VR devices can divert attention away from nociceptive stimuli by isolating patients’ audiovisual connection to the external environment [72]. Nevertheless, in this study, the reported pain scores were relatively low in both groups, which might be related to insufficient immersion of the VR experience, inadequate intervention dosage, or the widespread use of analgesic medications. This warrants further investigation in future studies.

VR-ERI shows a potential trend for improving cognitive function in short-term follow-up, although the 95% PI crosses the null effect line, indicating unstable results. This may stem from several factors. First, the pathophysiology of post-ICU cognitive impairment is complex (eg, neuroinflammation and blood-brain barrier disruption) [73]; for instance, underlying neural damage in conditions like posterior cortical atrophy may limit response to conventional interventions [74], highlighting the need for more targeted programs. Second, widely used screening tools, such as the Mini-Mental State Examination and MoCA, may lack sensitivity to detect subtle, clinically meaningful improvements in critically ill patients. The Mini-Mental State Examination, although brief and simple, has a ceiling effect and inadequately assesses executive function and complex attention [75]. The MoCA is more sensitive to mild impairment but remains a broad screening tool that may miss specific post-ICU executive deficits (eg, inhibitory control and cognitive flexibility) [76]. Therefore, future studies should develop VR modules tailored to ICU-related cognitive impairment and consider longer intervention duration. A multilevel assessment strategy is recommended, combining screening scales with computerized neuropsychological tests (eg, flanker tasks) for objective, quantitative data [77]. Integrating VR with other rehabilitation methods into a multidimensional intervention may also help achieve meaningful cognitive gains. Given the low certainty of current evidence, these findings should be interpreted with caution.

This systematic review is the first to focus on VR intervention studies conducted during the early ICU rehabilitation phase. By systematically searching ten Chinese and English databases and implementing independent dual-reviewer screening and data extraction, it strictly adhered to the PRISMA 2020 guidelines, ensuring a transparent process and reproducible results. The review comprehensively used the Cochrane RoB 2.0 tool for risk of bias assessment and the GRADE framework for evidence grading, supplemented by sensitivity analyses to verify the robustness of the findings. It summarizes and analyzes the safety and clinical feasibility of VR intervention in critically ill patients, while systematically elucidating the efficacy profile of VR on relevant outcomes during both the ICU stay and at short-term follow-up. This provides an important reference for advancing the translational application of VR technology in this patient population.

Several limitations should be acknowledged. First, the literature search was restricted to Chinese and English publications and excluded trial registries and gray literature, potentially introducing omission and language bias. Second, the limited number of studies and small total sample size reduce statistical power, which may affect the robustness and generalizability of the pooled results. Third, substantial clinical and methodological heterogeneity existed across studies, including variations in VR immersion levels, protocol design, dosage, and outcome measures, contributing to high statistical heterogeneity. Inadequate reporting of precise dosage parameters also limited dose-response analyses. Fourth, most included studies had a high risk of bias due to issues such as unclear allocation concealment, lack of assessor blinding, and inherent challenges in blinding participants and personnel. Consequently, the certainty of evidence for most outcomes was low or very low, necessitating cautious interpretation. Finally, some outcomes were supported by only a few studies, resulting in meta-analyses with limited sample sizes and potentially unstable effect estimates. In summary, further well-designed, large-scale studies are required to validate these findings.

At the clinical level, VR-ERI can supplement traditional early rehabilitation, but widespread adoption faces systematic challenges. First, cost remains a key barrier. Although commercial VR prices are falling, expenses may still burden some institutions or patients, with VR for early pain management costing approximately €47.48 (approximately US $51.30) per patient [78]. Policymakers should thus consider including VR in insurance reimbursement or supporting it via dedicated funding. Second, patient vulnerability limits generalizability [79]. Those who are older adults, or have vestibular dysfunction, severe cognitive impairment, or complex life-support needs may be unable to tolerate VR. Health care institutions should form multidisciplinary teams to create standardized screening protocols—focusing on vestibular and cognitive function—and implement a safety system covering pre-, intra-, and postsession phases. Implementation should be phased and individualized—starting at low intensity and adjusted gradually under therapist supervision, while training ward staff and patients in device use. Finally, before broader promotion, safety and feasibility must be validated in heterogeneous critically ill populations [14].

At the policy level, relevant departments should establish a comprehensive support framework by developing evidence-based clinical guidelines for VR rehabilitation that specify indications, contraindications, and protocols, and implementing unified device certification and quality control systems to ensure safe and standardized application. Future research should adopt a phased strategy—priorities include conducting large-scale, rigorous pragmatic trials using blinded outcome assessment, diverse control groups, objective monitoring, and long-term follow-up to minimize bias; creating personalized interventions for specific patient groups, defining a core outcome set, and using objective, standardized assessment tools; and enhancing implementation science to identify optimal rollout pathways across different resource settings—beginning with pilot projects at regional medical centers before scaling to primary care. Concurrently, interdisciplinary collaboration among engineering, rehabilitation medicine, and critical care nursing should be strengthened to jointly advance technology innovation and support the development of a more integrated early rehabilitation system for critically ill patients.

This review is the first to examine VR rehabilitation effectiveness specifically during early intervention in the ICU. Unlike previous reviews, we focused strictly on the in-ICU early rehabilitation period to establish an evidence base for initiating such care and to minimize the clinical heterogeneity from combining interventions across different care settings. Evidence was synthesized across physiological, psychological, and cognitive domains. Results indicate that VR-ERI shows considerable potential for improving anxiety and subjective sleep quality during ICU treatment, as well as balance, limb motor function, and cognitive function in short-term follow-up. However, effects on pain and objective sleep quality in the ICU remain unclear. Given the high risk of bias in included studies, substantial heterogeneity, and imprecise pooled effect estimates, the evidence certainty for most outcomes is low, and conclusions should be interpreted cautiously. Additionally, establishing a comprehensive safety monitoring system is essential for future clinical translation. This review offers a new perspective on early ICU rehabilitation, suggesting VR technology could serve as a nonpharmacological adjunct in this phase. However, the current evidence is insufficient to support widespread implementation. Clinical translation requires careful consideration of cost and patient suitability, and long-term benefits need validation through large-scale and rigorous research.