Virtual reality for stroke rehabilitation the Cochrane verdict.

Why did the conclusion reverse between 2017 and 2025?

Cochrane reviews get updated as evidence accumulates, and this one has been updated four times since its protocol in 2010. The 2017 version pooled 72 trials with 2,470 participants and found that VR was not significantly better than conventional therapy for upper limb function: SMD 0.07, with a confidence interval crossing zero.

The June 2025 update pooled 190 trials and 7,188 participants, adding 119 new trials, and found SMD 0.20 (95% CI 0.12 to 0.28), which does not cross zero. The authors state plainly that this contrasts with the previous version and that the change in direction carries practical implications for clinicians.

Two methodological changes matter alongside the extra evidence. The 2025 version included only randomized trials, dropping the quasi-randomized studies the 2017 version allowed, which raises the floor on study quality. It also dropped the word “immersed” from its definition of VR, widening what counted.

What did the 2025 review actually find?

The review runs two separate comparisons, and conflating them is the most common error in reporting on it. The first asks whether VR replaces conventional therapy better than the alternative at the same dose. The second asks whether VR added on top of usual care helps, which necessarily means more total therapy time.

Comparison 1: VR instead of an alternative therapy

Comparison 2: VR added to usual care

For scale, the authors treat standardized mean differences of 0.2 to 0.5 as small, 0.5 to 0.8 as medium, and above 0.8 as large. Almost everything here sits in the small band, with balance in the adjunct comparison being the exception.

What is the catch in the headline finding?

The sensitivity analysis. When the authors restricted the main upper limb comparison to the studies that were not at unclear or high risk of bias in two or more domains, only 17 studies remained, and the effect fell to SMD 0.04 (95% CI −0.09 to 0.16). That interval includes zero, meaning the superiority result rests substantially on weaker trials.

The risk-of-bias picture across the whole review explains why. Adequate random sequence generation was reported in 64% of trials and adequate allocation concealment in 51%. Outcome assessors were blinded in 72%. And no trial was able to blind participants or personnel, which is inherent to the intervention: you cannot hide from someone that they are wearing a headset.

That last point matters for interpreting every VR rehabilitation trial. When participants know they are getting the novel, engaging treatment and the outcome partly depends on their effort, expectation is baked into the result. It is not a flaw the researchers could design away, but it does mean small effects should be read cautiously.

The review also notes an atypical funnel plot for the main analysis, though the authors say it was not clear whether publication bias explained it. Heterogeneity was substantial: I² of 68% for upper limb function and 85% for balance. Only 19% of trials had more than 50 participants, and the largest recruited 152.

Is the active ingredient the VR, or the extra therapy time?

This is the review's most interesting thread, and the authors lean into it. Within the first comparison, trials delivering 15 or more hours of therapy showed SMD 0.30 (0.20 to 0.41), while those under 15 hours showed 0.13 (0.01 to 0.24), a statistically significant subgroup difference (p = 0.03). In the 2017 version, that dose relationship was only a non-significant trend. More evidence hardened it.

Their proposed mechanism is refreshingly unglamorous: benefits may arise partly from the gamification of therapy, which increases motivation, adherence, and participation. Not neural rewiring unique to virtual environments, just people doing more repetitions because the task holds their attention.

The comparison of hardware supports that reading. Sixty-six of the 190 trials (35%) used off-the-shelf gaming consoles, mostly Nintendo Wii and Microsoft Kinect, and customised programmes did not significantly outperform them in either comparison (p = 0.32 and p = 0.58). The authors conclude their analyses gave no clear direction on which VR programmes are superior.

One finding runs the other way and deserves careful handling. A new subgroup analysis found immersive systems outperforming non-immersive ones (SMD 0.68 versus 0.20, p = 0.01). That is directionally interesting for the argument in our commentary on VR versus videogames, but the authors immediately caution that very few included studies were immersive and that no conclusions can currently be drawn about immersive VR. It is a hypothesis for future trials, not a result.

Does it matter how long ago the stroke happened?

In the adjunct comparison, yes, and strikingly. Trials recruiting people in the chronic phase showed SMD 0.77 (0.50 to 1.04), while trials recruiting within six months of stroke showed SMD 0.20 (−0.01 to 0.40), which does not exclude zero. The difference between those groups was significant at p < 0.001. In the first comparison, no such difference appeared.

Read cautiously, since this is a subgroup finding rather than a designed comparison. But it fits a sensible story: in the first months after a stroke, spontaneous recovery and intensive standard rehabilitation are already driving change, so an add-on has less room to show an effect. Later, when formal therapy has ended and improvement has plateaued, adding engaging practice has more to contribute.

That pattern echoes the clinic-to-home HEAD pilot, where tele-monitored home VR in chronic stroke helped maintain function that the usual-care group lost over six months.

What should a patient or clinician take from this?

Three things, stated at the strength the evidence supports:

• As an add-on, VR looks worthwhile. Moderate-certainty evidence supports better upper limb function and daily living activity when VR is added to usual care. This is the review's most defensible claim.
• As a replacement, the case is weak. Low-certainty evidence, a small effect, and a sensitivity analysis that erases it. Nothing here justifies swapping out conventional rehabilitation.
• Dose may matter more than the device. Fifteen or more hours outperformed less, and expensive purpose-built systems did not beat consumer consoles.

On safety, the review is reassuring: of 59 studies monitoring adverse events, 46 reported none that were major, and the events that did occur were mild, limited to dizziness, headaches, and pain.

Does any of this apply to chronic pain?

Not directly, and the distinction should be kept sharp. This review is about motor recovery after stroke: rebuilding movement in a limb affected by brain injury, measured with upper limb function scales, balance tests, and gait speed. Chronic pain is a different problem with different mechanisms and different outcome measures.

What does carry over is methodological. The dose finding, the difficulty of blinding anyone to a headset, and the gap between a headline effect and what survives a sensitivity analysis are all live issues for evaluating VR in any condition, chronic pain included. Those are the standards we try to hold our own evidence to in how the program works.

Where the mechanisms genuinely overlap is visual feedback and embodiment, which is the territory of mirror therapy and its own Cochrane review, and of the mechanism studies we cover on mirror feedback in the brain and VR-guided motor imagery.