Video Games and Cognitive Skills: Two Meta-Analyses, Same Journal, Opposite Answers

In 2018, Psychological Bulletin published a meta-analysis concluding that action video game training improves cognitive skills. In the next issue, it published a meta-analysis concluding that video game training does not enhance cognitive ability.

Bediou and colleagues, 144(1), pages 77-110. Sala, Tatlidil and Gobet, 144(2), pages 111-139. Consecutive issues. Consecutive page ranges. Opposite conclusions about the same literature.

That is not a failure of peer review. It is the clearest possible signal that the answer depends on a decision the popular coverage never mentions - and the decision is knowable.

The founding study is very small

Green and Bavelier (2003), in Nature, is where this begins: five experiments, four comparing habitual action-game players against non-players, plus one training study using Tetris as an active control.

We are not printing its sample sizes, because we could not read the paper. An independent source characterising it reports eight participants per group. We treat that as second-hand and unverified.

What matters more than the exact N is the design. Four of the five experiments are cross-sectional - comparing people who already play against people who do not. That is the design the field’s own critics identify as the problem.

The critique, and its own failure

Boot, Blakely and Simons (2011), in Frontiers in Psychology, made the argument that has shaped the field since. Verbatim:

“Many studies recruit experts through advertisements explicitly seeking people with game experience, thereby violating a core principle of experimental design and introducing the potential for differential demand characteristics.”

And: “If gamers are recruited to a study because of their gaming experience, they might expect to perform well because of their expertise, and a belief that you should perform well can influence performance.”

It is a strong argument. It has also now failed two direct tests, which is a fact critics of this literature rarely report.

Tsai and colleagues (2018), in the Journal of Applied Research in Memory and Cognition, manipulated expectancy directly with N = 122 across four arms. Training worked - F(1,116) = 52.25, p < .001, η²p = .31 on the trained task. Expectancy did nothing: no main effect, F(1,116) = 1.42, p = .236, and no interaction, F(1,116) = .02, p > .250. Their conclusion is that positive expectations are “neither necessary nor sufficient.” That study used n-back training, not games.

Gonçalves and colleagues (2026), in the Journal of Cognitive Enhancement, tested it on action games directly: N = 140, Solomon four-group design, expectancy manipulated by video framing. The manipulation induced different expectations and produced no group differences on the visual-attention outcome. The authors conclude the findings “do not support previous investigations in the literature claiming that an expectancy effect may account for attentional gains.”

So the standard critique of the pro-gaming literature is itself not well supported. Both sides of this argument have a problem.

The two meta-analyses

Bediou and colleagues (2018), the pro side:

Design	Effect	k/m
Cross-sectional	g ≈ 0.55, 95% CI [0.42, 0.68]	k = 194, m = 89
Intervention	g ≈ 0.34, 95% CI [0.09, 0.59]	k = 90, m = 22

Publication bias was significant on Egger’s test; trim-and-fill imputed 29 studies and corrected the estimate to about 0.48, which the authors describe as “28% smaller than the unadjusted effect.”

Sala, Tatlidil and Gobet (2018), the sceptical side, ran three models:

Model	Raw	After trim-and-fill
Correlational (k = 310, N = 8,141)	r̄ = .07 [.05, .09]	r̄ = .05 [.03, .08]
Players vs non-players (k = 315, N = 6,166)	ḡ = 0.33 [0.28, 0.39]	ḡ = 0.18 [0.12, 0.24]
Training interventions (k = 359, N = 3,286)	ḡ = 0.07 [0.02, 0.12]	ḡ = -0.01 [-0.06, 0.05]

Their closing line: “Video game training thus represents no exception to the general difficulty of obtaining far transfer.”

Why they disagree

Bediou and colleagues answered this directly in a later paper, and the answer is specific.

Sala and colleagues found “a Hedges’ g = 0.40 for action video games in cross-sectional studies but only a marginal effect in intervention studies contrasting an experimental group trained with an action video game and a control group trained with a control video game training (g = 0.10, p = 0.068).” Bediou’s explanation is that Sala’s “definition of action video game in this latter work was considerably more expansive.”

So the honest comparison, on action games with active controls, is Sala’s g = 0.10 (p = .068, non-significant) against Bediou’s g = 0.30.

That is a real disagreement. It is not the chasm implied by “0.07 versus 0.34,” and it turns on which games get counted.

The current best estimate

Bediou and colleagues (2023), in Technology, Mind, and Behavior, is the most recent synthesis and it was preregistered.

• 105 observational studies (221 effect sizes); 28 randomised trials (91 effect sizes)
• Cross-sectional: g = 0.64, 95% CI [0.53, 0.74]
• Intervention: g = 0.30, 95% CI [0.11, 0.50], k = 83, p = .004 - all with active controls playing commercial non-action games

By domain in the intervention studies: top-down attention 0.52, multitasking 0.41, perception and spatial cognition around 0.23-0.26, and verbal cognition 0.01.

The publication-bias result is the single most useful fact in this area. Bias was present in the cross-sectional literature (Egger’s β = 2.10, SE = 0.59, p = .002; bias-corrected g = 0.48-0.53) and not detected in the intervention studies (Egger’s β = 2.12, SE = 1.11, p = .17).

In other words: the inflated half of this field is the half that compares gamers to non-gamers, and the randomised half looks clean.

The nulls

Murphy and Spencer (2009), in the Journal of Articles in Support of the Null Hypothesis, tested 61 males (32 players, 29 non-players) across four attention paradigms:

• Useful Field of View accuracy: no group difference, F(1,57) = .262, p = .611
• Inattentional blindness: χ²(1,61) = .007, p = .931
• Repetition blindness: F(1,57) = .266, p = .608
• Attentional blink: a player advantage only at the 100 ms interval, t(58) = -2.19, p = .032, absent at 200-500 ms

Players were faster overall, F(1,57) = 4.28, p = .043, which the authors attribute to a speed-accuracy trade-off rather than better attention.

And a structural null worth stating plainly: twenty-three years after the founding study, there is still no large preregistered action-video-game training trial and no registered replication of Green and Bavelier (2003). The only preregistration we located in this literature is a meta-analysis protocol.

The disclosure

This belongs in the record and it is disclosed in the papers themselves.

The 2018 meta-analysis carries: “Daphne Bavelier declares she is a member of the scientific advisory board of Akili Interactive, Boston.”

The 2023 meta-analysis carries: “Daphne Bavelier is a founder and scientific advisor to Akili Interactive Inc. Boston.”

Akili Interactive commercialises a video-game-based cognitive therapeutic. The senior author of both pro-gaming meta-analyses has a direct financial interest in the proposition that games train cognition, and the disclosure escalates from advisory board member to founder between the two papers.

Both meta-analytic programmes are also substantially funded by the US Office of Naval Research, across all three of Bavelier, Green and Mayer.

None of this makes the work wrong. Both facts were disclosed properly. A reader deciding what to believe should have them.

What this leaves you with

Something real is happening, and it is narrow. Action games appear to move perception, spatial cognition, top-down attention and multitasking. Verbal cognition sits at g = 0.01.

The randomised estimate is around g = 0.30, and it may be closer to 0.10. That is a small effect either way, and roughly half what the twenty-year-old cross-sectional literature advertises.

The cross-sectional literature is demonstrably biased and the intervention literature is not. If you read one number from this article, make it that one.

Neither side’s methodological story is clean. The pro-gaming evidence has publication bias and a commercially interested senior author. The sceptical critique’s central mechanism - expectation effects - has now failed two direct tests.

This is a different question from commercial brain training. That has its own evidence base, its own regulatory record, and a worse answer; see does Lumosity work.

For a study technique that survives testing and one that does not, see spaced repetition and Sans Forgetica.

Limitations of this article

The 2018 pro-gaming meta-analysis has a published correction which we could not read. We have therefore relied on the 2023 preregistered meta-analysis by the same group for the current estimate, and we flag that any figure quoted from the 2018 paper should be checked against that correction before reuse.

We could not verify the exact k and m partition in the 2018 meta-analysis. Two reads of the same PDF returned different accountings, almost certainly because they describe different subsets. We print the young-adult intervention figures and flag the uncertainty.

We could not read Green and Bavelier (2003) and have printed no sample size for it.

We verified Sala’s action-game subgroup figure (g = 0.10, p = .068) only as quoted by the opposing authors, not in Sala’s own text. That is a real weakness in the central comparison of this article and we would rather say so than hide it.

We could not locate a funding statement for Sala, Tatlidil and Gobet (2018).

The expectancy null from 2018 used n-back and general-knowledge training, not video games. Only the 2026 study tested expectancy on action games directly, and it is not preregistered.