Does the 2026 Meta-Analysis Show Cognitive-Training Transfer to IQ Tests?

What did the 2026 review actually find?

The 2026 review, “The effects of computerized cognitive training on cognitive function in patients with mild cognitive impairment: a systematic review and meta-analysis,” reports that computerized cognitive training (CCT) was associated with better overall cognition across the included randomized trials. Its abstract says the authors searched four databases through February 2026 and included 30 randomized controlled trials with 2,056 participants described as having mild cognitive impairment (MCI). The pooled overall-cognition estimate was a standardized mean difference (SMD) of 0.62, with a 95% confidence interval from 0.43 to 0.81. The reported heterogeneity was I²=73%. This is a positive average result: the confidence interval reported in the abstract excludes zero, while the heterogeneity indicates that trial results varied materially around the pooled estimate. The finding therefore deserves to be treated as evidence of a group-level cognitive difference in this review, rather than dismissed because it does not answer every question about intelligence. The point estimate is the review’s pooled summary, and the interval describes uncertainty around that pooled estimate under its analysis; neither interval is a range of likely gains for a single person. I² describes inconsistency in the observed study estimates, not the percentage of participants who benefited.

An SMD expresses a between-group difference in standardized units, making outcomes measured on different scales combinable under the review’s analysis. It is not a count of questions answered correctly, a number of IQ points, or an estimate of how much any one participant should gain. The “overall cognition” label is the outcome the abstract reports for the pool. It does not name an intelligence-test composite or report a separate pooled intelligence-test result. The accessible abstract is not enough to inspect which instruments and outcomes each trial contributed, how those outcomes were grouped, or whether any trial included an intelligence measure. The full text is subscription restricted according to the source record, so this section cannot verify those trial-level details.

The careful conclusion is consequently two-part: the review reports a statistically significant favorable pooled result for overall cognition in its MCI trial sample, and the accessible report does not establish transfer to intelligence-test performance or a change in general intelligence. That second point is a limit on what can be concluded from the reported outcome, not evidence that none of the 30 trials used any intelligence test. The same distinction applies to the population wording. The abstract describes participants as having MCI; from the abstract alone, it does not establish that every participant was an older adult. A reader can acknowledge the positive pooled evidence while keeping the claim attached to the measure actually named and the sample actually described, rather than silently converting either into a broader claim about older adults’ IQ.

Sources: The effects of computerized cognitive training on cognitive function in patients with mild cognitive impairment: a systematic review and meta-analysis

What does the pooled number mean for one person?

The pooled SMD cannot be read as IQ points, as a personal forecast, or as proof of clinically meaningful change. It is a standardized summary of the average difference between the training and comparison groups on the outcomes combined by the review. Standardization removes the outcomes’ original units for the purpose of pooling; it does not transform their underlying tests into an IQ scale. To express a result in the units of a particular test, one would need the actual instrument and score scale, along with the relevant spread of scores and the specific group contrast. The abstract’s pooled number alone supplies none of those ingredients for an IQ-point conversion.

A simple invented arithmetic illustration shows why. Suppose two groups differ by 6 points on a hypothetical task, and the scores’ standard deviation is 12 points. The standardized difference would be 6 divided by 12, or 0.5 standard deviations. If the task instead had a 3-point group difference and a 6-point standard deviation, it would also yield 0.5 standard deviations. Those equal standardized values do not mean either task uses an IQ scale, nor that either group gained half an IQ point—or any fixed number of IQ points. The figures here are only arithmetic examples, not results from the Guan review or observations about its participants. A standardized summary preserves a relative group contrast while leaving the original score units behind.

Nor does a pooled group contrast say what will happen to a particular person. The group estimate averages across the trials and participants included under the review’s methods; individuals can have different starting scores, responses, and outcomes. The SMD does not report a personal probability of improvement, a reliable-change threshold, or whether a change matters in daily functioning. Those questions require evidence tied to the relevant instrument, population, comparison, and outcome—not just a pooled magnitude.

Statistical significance and the size of a standardized estimate answer different questions from transfer and individual benefit. A nonzero average difference can be a meaningful finding for comparing the groups in the review, yet it does not show that training improved an untrained intelligence test or that an individual’s general intelligence changed. To make that further claim, the outcome itself would need to be identified and the evidence would need to support that interpretation for the studied population.

Why do two 2026 reviews give different-looking results?

The separate network meta-analysis qualifies the broad positive result by asking a different question with a different outcome structure. “Efficacy of different computerized cognitive training modalities in improving global cognitive function in patients with mild cognitive impairment: a network meta-analysis” brings together 23 randomized trials, then analyzes the Mini-Mental State Examination (MMSE) and Montreal Cognitive Assessment (MoCA) in separate networks. That is not a second estimate of precisely the same pool as the Guan review’s overall-cognition summary. Network analyses compare several intervention types through direct and indirect evidence, while a broad pooled outcome summarizes the contrasts selected for that analysis. Differences in trials, measures, comparators, and synthesis method mean the reviews can look different without functioning as conflicting replications.

In the MMSE network, the review reports substantial heterogeneity: results varied across studies enough to make a single ordering of training modalities unreliable. Its estimated comparisons and rankings therefore do not establish one modality as a dependable winner across settings. This is not equivalent to finding that every intervention had no effect. Rather, the network does not support a stable hierarchy for this outcome given the variation and uncertainty in its contributing evidence. A reader considering the broad positive pooled result should therefore avoid turning it into a claim that a particular computerized format reliably produces the largest cognitive gain.

The MoCA network gives a more qualified positive picture. Selected intervention-package comparisons favored training, so it would be inaccurate to summarize this review as wholly null. But those favorable contrasts do not remove the review’s uncertainty: the authors rate the evidence from low to very low certainty and describe the rankings as exploratory. A network ranking is conditional on the included evidence and its assumptions; it is not automatically a secure treatment league table. The distinction matters because apparent benefit can depend on which cognitive measure is used and which intervention contrasts the analysis can estimate. A result on the MoCA cannot simply be substituted for an MMSE result, and neither outcome structure turns the underlying evidence into an intelligence-test score.

Taken together, the reviews illustrate why “cognitive training works” is too compressed to guide an intelligence claim. One analysis reports a favorable overall-cognition pool; the network analysis separates two named screening measures and finds a heterogeneous MMSE network alongside selected, uncertain MoCA advantages. The comparison changes the resolution of the question: broad pooling asks about an average across outcomes or contrasts, whereas separate networks expose outcome-specific differences and uncertainty in relative modality rankings. This is a synthesis of the reviews’ designs and reported findings, not evidence that one analysis invalidates the other.

For a reader evaluating a training claim, the practical test is to ask what outcome produced the result and how directly it answers the claimed question. Evidence that one package compares favorably on a MoCA network can support a bounded statement about that comparison and outcome, with its low-to-very-low certainty attached. It cannot by itself establish that the same package improves a different cognitive measure, produces a durable individual benefit, or raises IQ. Conversely, the heterogeneous MMSE network does not erase the separate favorable findings. The outcome and comparison structure shape what the evidence can say; an intelligence-test interpretation would require a direct measure and evidence supporting that specific use.

Sources: Efficacy of different computerized cognitive training modalities in improving global cognitive function in patients with mild cognitive impairment: a network meta-analysis

What evidence would justify calling an outcome an IQ result?

A cognitive outcome supports an IQ interpretation only when evidence connects the actual score, the people tested, and the proposed use. The “Standards for Educational and Psychological Testing” frame validity around interpretations and uses, not as a generic property that attaches to any test or positive finding. For this question, that means identifying the construct an outcome is intended to represent, the instrument and score actually used, the population for which evidence is relevant, and the inference someone wants to draw. Calling a pooled outcome “global cognition” does not, on its own, establish that it measures general intelligence or that its changes can be read as IQ changes.

Those details matter because similar-sounding labels can conceal different measurement jobs. A screening measure of broad cognitive status, a task measuring one reasoning operation, and a composite designed to support an intelligence interpretation are not interchangeable merely because all involve cognition. Nor does a standardized group difference solve the problem: standardization expresses a contrast in units of variability, not in IQ points. To justify the stronger interpretation, the evidence would need to show that the named measure and score support it for the relevant participants and purpose, with limitations in precision or coverage accounted for. The standards supply this rule for responsible interpretation; they do not independently determine what any trial measured.

Here, the accessible abstract for “The effects of computerized cognitive training on cognitive function in patients with mild cognitive impairment: a systematic review and meta-analysis” reports a pooled overall-cognition outcome but does not name every trial’s instruments or outcomes. That leaves a specific empirical question open: study-level data or accessible full text would be needed to check whether any included trial used an intelligence measure and, if so, what score and interpretation it supports. The absence of those details in the abstract is not evidence that no relevant measure appeared. It also does not license calling the review’s pooled result an IQ result. Both a categorical denial and a positive IQ-transfer claim would outrun the available measure-level record.

A defensible reading therefore stays at the level established by the source: the review reports a favorable pooled result for overall cognition among its included participants. Whether that result bears on intelligence-test performance depends on the particular measures, their intended score meanings, the population, and the analysis connecting them. Until those links are documented, the IQ interpretation remains unsubstantiated rather than disproved. This distinction preserves the value of a broad cognitive finding while reserving an intelligence claim for evidence designed and reported to support that inference.

Sources: Standards for Educational and Psychological Testing; The effects of computerized cognitive training on cognitive function in patients with mild cognitive impairment: a systematic review and meta-analysis

How far does training transfer beyond the practiced task?

The broad review “Near and Far Transfer in Cognitive Training: A Second-Order Meta-Analysis” draws a useful distinction: near transfer means improvement on tasks similar to the trained activity, while far transfer means performance change in more distant domains. Its synthesis found evidence of near transfer from working-memory training, with the estimated size varying by population. For far transfer, including outcomes such as reasoning, language, and cognitive control, the review describes effects as small or null. Its conclusion is therefore not that practice never changes another task, but that improvement becomes less dependable as the measured outcome shares fewer features with the training. A gain on a familiar exercise is the closest outcome; a different task using related processes is farther away; a broad ability claim is farther still and needs correspondingly direct evidence.

The second-order review tested how analysis choices affected the far-transfer estimate rather than treating every positive study contrast as equivalent. It compared the full sets of experimental-control contrasts with subsets using active controls: comparison activities designed to be engaging and cognitively demanding. Such controls help account for effects that may arise from taking part in a structured activity, expectation, or attention from researchers, instead of the distinctive training operation. The review also incorporated publication-bias-adjusted estimates. This matters because published positive findings can be easier to locate than null results; if that imbalance inflates the input estimates, a synthesis of unadjusted estimates can make transfer appear larger than it is.

Across working-memory training analyses, the far-transfer estimate was nearly zero when placebo-related differences and publication bias were addressed. The review reported a similar pattern across its broader set of programs, including video-game, music, chess, and exergame training: small unadjusted signals did not remain as clear evidence of far transfer after those adjustments. This is a method-sensitive finding from the meta-analyses available to that review, not a direct estimate for people with mild cognitive impairment and not a 2026 update of the MCI trials. The authors also note that some component meta-analyses contained relatively few studies, which limits precision and the power of bias checks. The result should be read as a reason for restraint, not as proof that every training method, population, or distant outcome must show exactly no effect.

For an intelligence claim, the practical implication is to inspect the distance between the exercise and the outcome actually tested. If training and assessment share item formats, content, or operations, better performance may indicate useful learning on related tasks, but it does not alone demonstrate change in a distinct reasoning ability or intelligence-test composite. Active comparisons and adjustment for selective publication make a claimed transfer effect more demanding to establish because they test whether it survives plausible alternative explanations. Transfer distance is therefore an empirical question about the tasks, controls, and accumulated evidence. A favorable broad-cognition score cannot be labeled far transfer merely because its name sounds general; the particular outcome and study design must show that the measured change extends beyond what was practiced.

Sources: Near and Far Transfer in Cognitive Training: A Second-Order Meta-Analysis

What can healthy older-adult training research add—and not add?

A separate review focused on working-memory training in healthy older adults offers adjacent context, not an answer to the MCI intelligence question. “Reviewing Working Memory Training Gains in Healthy Older Adults: A Meta-Analytic Review of Transfer for Cognitive Outcomes” included 27 experiments and 1,130 participants. It assessed near and far transfer using short-term memory, working-memory, and reasoning measures. The abstract reports small, significant, long-lasting transfer gains on working-memory tasks. It describes the reasoning effects as very small and marginal. This pattern is consistent with the broad distinction above: the clearest reported transfer concerned outcomes close to the trained domain, while the evidence for a more distant reasoning outcome was much weaker.

The population boundary matters. These experiments concerned healthy older adults; the 2026 review at the center of this article concerns trials enrolling people described as having mild cognitive impairment. A healthy sample cannot stand in for a clinical group whose baseline function, needs, and response to training may differ. Nor can the two bodies of evidence simply be combined into a larger estimate: they address different populations and the reviews use different inclusion criteria and outcome groupings. The older-adult review supplies context for how transfer has been studied, but it does not fill in the 2026 review’s unavailable trial-level account of which measures were used or establish what its MCI results imply for intelligence-test scores.

Outcome labels also set a firm boundary. A reasoning task measures performance on that task; a small, marginal pooled reasoning effect does not automatically represent an IQ composite or a change in general intelligence. Its modest status is not proof of zero effect, and the abstract-level report does not warrant erasing the possibility of limited reasoning transfer. But it cannot support a broad claim that working-memory training raises IQ among healthy older adults, much less among older adults with MCI. The defensible use of this adjacent evidence is narrower: it shows that some sustained transfer may be detected on working-memory outcomes, while evidence on reasoning was much less conclusive. Direct, well-described intelligence outcomes in the relevant MCI population would be needed to resolve the article’s specific question.

Sources: Reviewing Working Memory Training Gains in Healthy Older Adults: A Meta-Analytic Review of Transfer for Cognitive Outcomes

Could a later test score rise because the test is familiar?

Yes. A higher score on a later administration can reflect a retest effect, which makes a simple before-and-after comparison ambiguous. “Retest effects in cognitive ability tests: A meta-analysis” synthesized 174 samples from 122 studies, covering 786 outcomes and 153,185 participants. Its abstract reports significant score gains associated with repeat administration and says the gains did not continue after the third administration. This is evidence that scores can change when cognitive-ability tests are repeated across the research literature; it does not establish that every person improves, that every test produces the same change, or that a particular training program caused an observed increase.

The key distinction is between observing that a score rose and identifying why it rose. If participants complete an assessment before and after a training period, the second score follows both the intervention and another exposure to testing. A pre/post difference alone therefore cannot assign the change to training. The retest meta-analysis makes that a material design concern because it found average gains associated with repeated testing, but its abstract does not identify the cause of each gain or say that retesting accounts for any particular intervention result. A study needs a comparison condition and an analysis suited to distinguish change associated with training from change that could also occur under repeat assessment.

The review also reports that retest effects varied with operation and content, form equivalence, interval between administrations, and age. These are moderators: features associated with differences in the observed retest effect across the included evidence. They give a reader concrete questions to ask when comparing a study with a claimed score gain. Did participants see the same or equivalent forms? How similar was the content and cognitive operation? How long elapsed between administrations? What ages were represented? Those details affect how closely a study's retest conditions match the evidence summarized by the meta-analysis; they do not provide a formula for correcting an individual score or a guarantee that an equivalent form eliminates change.

This matters especially when the outcome resembles the practiced material. Repeated assessment may alter the comparison even when a study does not claim to train the test itself, while overlap between training and assessment raises a separate question about the distance of the measured outcome. The available abstract supports attention to content and operation as moderators, but it does not establish a specific familiarity mechanism for every result. Keeping those claims separate avoids treating a possible explanation as a demonstrated cause. A credible training design should describe assessment forms, timing, and outcomes, and use an adequate comparison group exposed to the same testing schedule. Then the relevant contrast is whether the trained group changes more than a comparable group facing repeat assessment, not simply whether its own later score exceeds its earlier one.

Retest evidence does not explain every gain or show that practice-related change is the only alternative to a training effect. It identifies a source of ambiguity that pre/post designs must address. For readers assessing an intelligence-test claim, the practical standard is therefore design-level: look for the retest schedule, form relationship, interval, age range, and comparison that help separate repeated measurement from the intervention. Without that information, an observed increase is a score change whose cause remains unresolved; it is not, by itself, evidence that cognitive training transferred to intelligence-test performance.

Sources: Retest effects in cognitive ability tests: A meta-analysis

What does a single controlled study reveal about trained-task gains?

A small controlled study can illustrate why a gain on an exercised activity and a change on a broader outcome are different findings. “Cognitive change is more positively associated with an active lifestyle than with training interventions in older adults at risk of dementia: a controlled interventional clinical trial” enrolled 65 older adults at risk of dementia; 54 participants were analyzed. The study compared physical training, cognitive training, and a wait-list condition over ten weeks and included a three-month follow-up. Those details define a bounded example in older adults at risk of dementia. The study was not an IQ test study, and its population description does not make it a direct replication restricted to people with mild cognitive impairment.

The outcome comparison is the central point. The paper reports that neither training condition improved global cognition relative to the control condition, with p=.08 for the reported comparison. That finding differs from asking whether participants got better at an activity they practiced: a study can observe task-specific progress while separately testing whether a broader measure changes relative to a comparison group. Here, the reported global-cognition contrast did not meet the conventional threshold for statistical significance. It should not be rewritten as proof that no participant changed, nor converted into a claim about intelligence-test performance, because the study did not test IQ as its outcome.

The result also has to be read alongside the study's design and scale. Fifty-four analyzed participants provide a small study, and the ten-week intervention plus follow-up is one particular test of these training conditions and this broader outcome. A non-significant training-versus-control result does not establish that all cognitive training is ineffective, just as a score increase within one condition would not establish a training effect without the relevant between-group comparison. The point is narrower: the study distinguishes its intervention arms from control on global cognition and reports no statistically significant advantage for either training arm. The available evidence does not justify treating that contrast as an intelligence score or as a general verdict on other training programs.

The paper also describes associations between a more active lifestyle and cognitive change. That finding is separate from the intervention comparison. Lifestyle was not experimentally assigned as the contrast in that association, so the relationship cannot show that adopting a more active lifestyle caused the cognitive change. Participants who report different levels of activity may also differ in other ways relevant to cognition; the study's association does not isolate those possibilities. It is reasonable to report the observed relationship as an association, but not to present it as a causal benefit or to use it to rescue an intervention result that was not significant against control.

This example does not overturn the positive pooled result from the 2026 review: it is one small study with different intervention conditions, population framing, and methods. Nor does the pooled result erase the design lesson the study offers. A reader should ask what changed, on which outcome, and against which comparator. Improvement on a trained task and improvement on a broader cognitive measure are not interchangeable; neither should be relabeled as an IQ gain without a direct, supported intelligence-test interpretation. The trial is useful as an illustration of outcome and comparison distinctions, not as a direct answer about transfer to IQ among older adults with MCI.

Sources: Cognitive change is more positively associated with an active lifestyle than with training interventions in older adults at risk of dementia: a controlled interventional clinical trial

Which uncertainties are specific to older adults with MCI?

The accessible abstract of “The effects of computerized cognitive training on cognitive function in patients with mild cognitive impairment: a systematic review and meta-analysis” identifies participants as people with mild cognitive impairment, but it does not establish the age composition of every included trial. That distinction matters: MCI is a diagnostic description, while “older adults with MCI” is a narrower population claim. The abstract also does not list every outcome by trial, so it cannot show whether a direct intelligence measure appeared anywhere in the evidence base. These are limits of what the accessible abstract reports; the review’s full text or study-level records may resolve them. Until those records are examined, readers should neither assume every participant was older nor conclude that no included trial measured intelligence-test performance.

The same abstract reports substantial heterogeneity in the overall-cognition synthesis. A pooled average can remain positive while underlying trial estimates vary, so it summarizes the included evidence rather than promising a uniform response across people, programs, or settings. The review reports no statistically significant differences in its subgroup analyses. That result does not establish that the subgroups are equivalent: a failure to detect a difference can reflect limited information as well as genuinely similar effects, and equivalence requires a design and analysis capable of testing a prespecified margin. The abstract-level subgroup result therefore does not settle whether age, training format, or another trial feature changes the effect. It leaves those comparisons uncertain while preserving the pooled average as informative evidence about the studies combined.

Duration is another unresolved question. The review authors call for larger randomized controlled trials with longer follow-up. An outcome measured at the end of a training period describes performance at that assessment point; by itself, it does not show that any change persists after training stops. Longer controlled follow-up would be needed to distinguish a lasting difference from one that fades, changes with further assessment, or depends on continued activity. The abstract’s recommendation signals that the current evidence does not settle durability; it is not evidence that benefits necessarily disappear.

A more specific conclusion about older adults with MCI and intelligence-test outcomes would require trial-level reporting that links participant ages to the actual tests and scores used, alongside controlled follow-up of those direct outcomes. Such evidence could show whether the relevant trials included older participants, whether any intelligence measure was administered, and whether a group difference endured beyond the immediate endpoint. Until then, the review supports a positive average finding for its reported overall-cognition outcome, while age composition, direct intelligence-test generalization, and persistence remain open. Those uncertainties narrow the claim that can responsibly be made; they do not erase the pooled result the review reports.

Sources: The effects of computerized cognitive training on cognitive function in patients with mild cognitive impairment: a systematic review and meta-analysis

What should a reader do with this finding?

For low-stakes curiosity or practice, try challenging reasoning problems and review their worked answers; that can be worthwhile without treating a score as a diagnosis. Test IQ Free offers a free 50-question reasoning test, but its displayed estimated IQ range is provisional: it comes from an unvalidated conversion with no validated adult reference population. It is not a confidence interval or an established comparison with the population. The result can support reflection on performance across the test’s reasoning tasks, but should not be used to label ability or predict how someone will perform in another setting. Reviewing solutions can show how particular operations work and suggest what to practice next; it does not establish that practice raises general intelligence. Use it for practice, not as evidence of a clinical change. The optional $9 report adds explanation and a practice plan, not validity or greater accuracy. If a score will inform a consequential education, clinical, or other high-stakes decision, consult a qualified professional for an appropriate assessment. The 2026 review reports an average overall-cognition effect in MCI trials, but does not establish improvement on intelligence tests or a lasting IQ gain.

Sources: Standards for Educational and Psychological Testing

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