Working Memory Training Programs: What the Evidence Says
A family arrives at your intake with a printout. They have been told that twenty-five sessions of a computerised working memory training program will lift their daughter's reading, and they want to know whether to spend the next five weeks on it instead of on the intervention you were about to recommend.
You are not being asked a research question. You are being asked to arbitrate between a company's evidence page and something you half-remember reading.
So here is the useful thing to know before you answer. The people who argue about working memory training programs do not actually disagree about the data. They agree, remarkably closely, on what the studies found. What they disagree about is how far an improvement has to travel before it counts — and about what a control group has to be doing while it travels.
That is a question you can adjudicate yourself, in about ten minutes, on any study a family puts in front of you. This piece is a map of the published record and a method for reading the next study that lands in your inbox.
The one thing every side agrees on
Start with the agreement, because it is larger than the argument and it gets lost.
Working memory training improves working memory tasks. Nobody contests this. It is the single most replicated finding in the area, it appears in every meta-analysis including the most sceptical ones, and it appears in the vendors' own documentation.
Melby-Lervåg, Redick and Hulme's 2016 meta-analysis, published in Perspectives on Psychological Science and indexed here, is the most widely cited sceptical review in the field. It opens its own abstract with the agreement: "Immediately following training there were reliable improvements on measures of intermediate transfer (verbal and visuospatial working memory)."
Aksayli, Sala and Gobet's 2019 meta-analysis of Cogmed, published in Educational Research Review, found the same thing and put a number on it. Across 50 studies and 637 effect sizes, the overall near-transfer effect was a Hedges' g of 0.444.
The argument in this field has never been about whether the programs do something. It is about where that something stops.
Transfer is a distance, and the distance is measurable
The word doing all the work here is transfer. Practitioners tend to hear it as a binary — either the training carries over or it does not. The literature treats it as a continuum, and the Cogmed meta-analysis split that continuum into bands and measured each one separately.
That split is the most practically useful thing in the whole literature, so it is worth having in front of you.
Very near transfer
Outcome tasks that closely resemble the trained tasks. In Aksayli and colleagues' analysis the overall effect here was g = 0.566 (95% CI 0.472 to 0.660). This is a solid, real, replicated effect.
Lesser near transfer
Memory tasks that still share the general domain but not the specific format. The effect drops to g = 0.246 (95% CI 0.102 to 0.391) — less than half.
Far transfer
Cognitive ability, attention, reasoning, language ability, mathematics. The overall effect was g = 0.048, with a confidence interval of −0.017 to 0.113 that comfortably includes zero, at p = .135.
And at follow-up
Far transfer at follow-up was g = 0.051, confidence interval −0.018 to 0.119. No different from immediate post-test, which rules out the hypothesis that generalisation simply needs time to appear.
The authors' own summary of the pattern is the cleanest statement of it anywhere: "Transfer thus appears to be a function of the degree of overlap between trained tasks and outcome tasks."
Read that sentence as a measurement rule, not a verdict. It tells you what to check on any study: how similar is the outcome task to the training task? The closer they look, the larger the effect, in a relationship so orderly that the meta-analysis found essentially no unexplained variation left over once overlap was accounted for.
The same gradient appears in a completely different population
If the pattern were an artefact of how children's studies are run, it should not reproduce in adults. It does, and the numbers are almost the same shape.
Sala and colleagues' comprehensive meta-analysis of working memory training in older adults, in Intelligence in 2019 and available in full from the University of Liverpool repository, pooled 43 studies, 698 effect sizes and 2,140 participants.
The trained tasks improved a lot: g = 0.877. Near transfer was modest at g = 0.274. Far transfer was g = 0.121 — and here is the line worth memorising:
"Moreover, when active control groups were implemented, the far-transfer effects were null (g = −0.008)."
Same gradient, different decade of life, different research groups. A finding that reproduces this cleanly across populations is not a null result. It is a positive finding about how narrow transfer is.
The bench and the kitchen, one level further out
This is the same measurement problem that runs through the whole executive function literature, and the scope-of-practice map we published on where five professional bodies actually put executive function quotes Adele Diamond's version of it: executive functions have historically been assessed "on arbitrary laboratory-based tests far removed from the real world," while self-regulation has been assessed through adult ratings of behaviour at home and school.
One tradition measures on a bench. The other measures in a kitchen.
Working memory training lives entirely on the bench. The training task is a bench task, and so is the very-near-transfer outcome. The far-transfer outcomes — a reading comprehension score, an arithmetic score, a teacher's rating of attention — are kitchen measures.
So "far transfer" is not a vague term of art. It is the specific claim that a bench exercise changes a kitchen outcome. That is precisely the claim a family is being sold, and precisely the claim the meta-analyses were built to test.
This is also why the instrument you use to check afterwards matters so much. Rating scales and performance tests do not measure the same construct, and a program evaluated on one will look different when evaluated on the other.
What exactly is being trained
It helps to be precise about the target, because the marketing is not.
The dominant account of executive function, Adele Diamond's 2013 review in the Annual Review of Psychology, states it plainly: "There is general agreement that there are three core EFs ... inhibition ..., working memory (WM), and cognitive flexibility ... From these, higher-order EFs are built such as reasoning, problem solving, and planning."
Planning is not a core executive function in that account. It is built from the other three. A program that trains a working memory task and advertises better planning is therefore making a two-step claim, and the second step is exactly the step the meta-analyses keep failing to find.
The three-factor structure comes from Miyake and colleagues' 2000 latent-variable analysis in Cognitive Psychology, which is the paper most of this vocabulary descends from.
The World Health Organization's ICF files the whole cluster under code b164, "higher-level cognitive functions," with executive functions as the alias rather than the primary label — a detail that matters when three different professions describe the same territory in three different vocabularies.
None of this settles whether training works. It settles what a claim about "executive function training" is actually asserting, which is the first thing to establish before you evaluate it.
An early review that named the problem before the meta-analyses did
Worth knowing about, because it was written in 2012 and its list of concerns reads like a summary of everything found since. Shipstead, Redick and Engle's review in Psychological Bulletin flagged four things: defining change to an ability using a single task, inconsistent use of valid working memory tasks, no-contact control groups, and subjective measurement of change.
Every one of those four is still the right question to ask about a study published this year.
What the far-transfer analyses actually found
Melby-Lervåg, Redick and Hulme, 2016
The largest general review. It covers 87 publications and 145 experimental comparisons, all with a pretest–posttest design and a control group.
Its conclusion, verbatim: "working memory training programs appear to produce short-term, specific training effects that do not generalize to measures of 'real-world' cognitive skills."
Three details from that paper matter more to a practitioner than the headline.
First, the two apparent exceptions did not survive inspection. Reading comprehension showed a small significant effect against treated controls, g = 0.15. When the authors excluded comparisons in which the control group's scores fell between pretest and posttest — a pattern that inflates effect sizes and is not expected on a stable construct — the effect became "trivial (g = 0.08)."
Second, the mechanism did not check out. If training produces far transfer by increasing working memory capacity, then studies with bigger working memory gains should show bigger far-transfer gains. The meta-regressions "revealed no evidence for any mediated relationships." The authors call this a finding that "undermine[s] the rationale for working memory training studies."
Third, sample size decided the answer. Among studies with treated controls that met minimum recommended sample sizes, the effect was g = 0.01. Among the smaller studies it was significant. That is the signature of underpowered research, not of a real effect.
The full text is open access through Oxford's research archive if you want to read the moderator analyses yourself.
Aksayli, Sala and Gobet, 2019
The Cogmed-specific analysis, open access in full from the LSE repository. Its most striking result is not the near-zero effect but the absence of variation around it: the far-transfer models showed no true heterogeneity at all once baseline differences were controlled, which the authors describe as "consistent with a nonphenomenon: no generalized effects occurred regardless of any potential moderator."
That has a direct consequence for caseload decisions. The common hope that a program will work better for the students who need it most — the ones with the lowest working memory — was tested and not supported.
Gobet and Sala, 2023
A review of the meta-analyses themselves, in Perspectives on Psychological Science — full text from the LSE repository, indexed here — stating the position bluntly: "The overall effect of far transfer is null, and there is little to no true variability between the types of cognitive training."
Their recommendation is the part worth carrying into practice: "research efforts should be redirected to near transfer or other methods for improving cognition."
The evidence does not say the programs do nothing. It says the thing they do is the thing you trained.
The real argument is about the control group
Here is the fault line, and once you see it you can read almost any dispute in this area.
An untreated control group does nothing. A treated control group — often called an active control — does something else for the same number of sessions, with the same adult attention, on the same computer.
Melby-Lervåg and colleagues separated the two and found that far-transfer effects "are absent (nonverbal ability, verbal ability, word decoding, arithmetic) in studies using treated control groups." Their recommendation is unusually direct for a meta-analysis: "We recommend that investigators stop conducting working memory training studies with untreated control groups and that journals stop publishing them."
Simons and colleagues' 2016 review in Psychological Science in the Public Interest goes further and explains why an active control is not automatically an adequate one. A control condition should "place similar demands on the participants but should lack the critical ingredient thought to enhance performance." A non-adaptive version of the same task is a good control. Watching videos is not.
They add the harder problem underneath it: participants know which group they are in. Without equated expectations across groups, a difference between an exciting adaptive game and a dull filler task is not clean evidence about working memory.
This is why two honest readers can look at the same fifty studies and reach opposite conclusions. One counts waitlist comparisons as evidence. The other does not. The disagreement is methodological, it is stated openly in both camps, and you can settle it for yourself on any single study by looking at one line of the method section.
What the publishers themselves publish
Apply the house method here: read what the vendor actually says, in its own document, rather than what its critics say it says.
Cogmed, published by Pearson
Pearson publishes a document titled Cogmed Working Memory Training – Research Evidence for the Improvement of Working Memory and Attention. It is the clearest statement of the vendor case available, and it is more careful than the marketing around it.
Its central claims, in its own words: improvements "transfer to non-trained WM tasks, an effect equivalent of about 2 years of normal childhood development"; there are "more than 120 studies of CWMT, by independent research groups around the world"; and effects on attention are documented in children with ADHD, children treated for cancer, and adults after stroke. The program's own research page makes the same case in shorter form.
It also names its own limits, which is more than most such documents do. It declines to recommend the program where oppositional defiant disorder is part of the picture, citing the one large study that did not find the effect: "CWMT is more likely to succeed in individuals where the deficit in WM and attention is the main problem."
And it concedes the field's central methodological problem outright. To have an 80 percent chance of detecting its own effect, the document states, a study "needs to include at least 200 subjects (100 training and 100 control)," and to detect an effect of 0.3 it needs "around 350 subjects." Its own assessment of the literature: "most studies have been underpowered."
Put that next to Melby-Lervåg's finding that adequately powered studies with treated controls produced g = 0.01, and the two documents are not contradicting each other. They are agreeing about the power problem and disagreeing about what the adequately powered studies then showed.
One number in that document is worth checking yourself
The "0.7 standard deviations" figure is attributed to Spencer-Smith and Klingberg's 2015 meta-analysis in PLOS ONE. Two things about that source are on the public record and are worth knowing before you repeat the figure.
Its competing interests statement reads: "The authors have declared that no competing interests exist. TK was previously a consultant for Cogmed, but currently has no competing interests." TK is Torkel Klingberg, whose laboratory at the Karolinska Institutet produced the founding studies the program is built on.
And the paper carries a formal correction published in November 2016. Two values had been incorrectly coded. The corrected overall effects are a standardised mean difference of −0.37 for inattention in daily life, 0.62 for visuospatial working memory and 0.41 for verbal working memory.
We could not establish which of those the 0.7 figure refers to, and the Pearson document carries no date or version number, so we cannot tell whether it predates the correction. If that number is load-bearing for a decision you are making, read the correction notice yourself rather than relying on the summary.
A negative trial sits inside the vendor's own reference list
The reference list of that same Pearson document includes Roberts and colleagues, 2016, in JAMA Pediatrics. It is one of the largest and best-controlled trials in the field, and it is worth reading in full.
Academic Outcomes 2 Years After Working Memory Training for Children With Low Working Memory screened 1,723 first graders across 44 schools in Melbourne and randomised 452 children with low working memory. The intervention was Cogmed: 20 to 25 sessions of 45 minutes, delivered at school, with 90.3 percent of the intervention group completing at least 20 sessions. Retention was 90 percent at one year and 88 percent at two.
The result: one of four memory outcomes benefited at 6 months (effect size 0.43) and 12 months (0.49), but not at 24 months. There were no benefits to any other outcome. Mathematics scores in the intervention arm were worse at two years, by a mean difference of −3.0 (95% CI −5.4 to −0.7, p = .01).
The authors' conclusion, verbatim: "Given the loss of classroom time, cost, and lack of lasting benefit, we cannot recommend population-based delivery of Cogmed within a screening paradigm."
The MRC Cognition and Brain Sciences Unit, whose researchers were involved in the trial, summarised it as showing "no improvements in reading, spelling or mathematics ... one and two years after training."
Note what that trial is not. It is a population-screening trial, not a clinical trial of an individually selected caseload, and its conclusion is scoped to population-based delivery. That scope is stated in the paper and should be stated by anyone who cites it.
Fast ForWord, published by Scientific Learning Corporation
The one long-standing "cognitive skills" program with a full What Works Clearinghouse intervention record. It is reviewed in three topic areas, and the ratings are mixed rather than uniform.
The March 2013 Beginning Reading intervention report found positive effects on alphabetics, no discernible effects on reading fluency, and mixed effects on comprehension, across nine studies and 1,390 students. A separate August 2010 Adolescent Literacy report covers the older grade bands, and an English Language Learners report from 2006 covers a third.
Two things about that record deserve a practitioner's attention. First, the improvement index ranges are wide and cross zero — alphabetics runs from −21 to +19, comprehension from −12 to +21.
Second, of the studies meeting WWC standards in the Beginning Reading domain, most are authored by Scientific Learning Corporation itself. That is disclosed on the WWC page and it is not disqualifying. It is context you should have before you quote the rating.
And note what the WWC rated. It rated reading outcomes. It did not rate whether the program improved the cognitive skills its marketing describes.
Two open letters, and what they actually disputed
In 2014 this argument spilled into public view in a way that is still worth reading, because both documents are short and both are candid.
On 20 October 2014, the Stanford Center on Longevity and the Max Planck Institute for Human Development published A Consensus on the Brain Training Industry from the Scientific Community, signed by more than seventy scientists. The core sentence:
"We object to the claim that brain games offer consumers a scientifically grounded avenue to reduce or reverse cognitive decline when there is no compelling scientific evidence to date that they do."
The statement marks each signatory who holds a financial interest in the industry with an asterisk, which is a standard other documents in this area could usefully copy. The full statement is published separately from the summary.
A group of scientists and practitioners replied with an open letter disputing that it was a consensus at all. The interesting part of that letter is not the disagreement. It is the list of things it explicitly concedes. Verbatim, the signatories "strongly agree" that:
"No one should say or imply that products have scientific evidence where there is no or little evidence for those claims."
"Cognitive training programs should be evaluated in peer-reviewed, randomized, controlled trials."
"Evidence is stronger if run independently, funded independently, run at multiple sites, and if it evaluates program benefits by comparison with 'active' control activities."
"Many companies that claim to provide brain fitness have not subjected their exercises to peer-reviewed trials to show any efficacy."
"Claims promoting brain games are frequently exaggerated, and are often misleading."
The two letters agree on the standard. They disagree about whether the existing studies meet it.
The review commissioned to settle it
Simons and colleagues then reviewed every peer-reviewed intervention study cited on the websites of the leading brain-training companies — on the reasoning that "companies would not deliberately cite weak evidence if stronger evidence were available."
Their verdict is the most quotable thing in the literature, and it is deliberately not a verdict of failure:
"The Scottish legal system permits a verdict that eschews 'guilty' or 'not guilty' in favor of 'not proven.' ... In place of 'not proven,' we find the evidence of benefits from cognitive brain training to be 'inadequate.'"
They also report that "none of the cited studies conformed to all of the best practices we identify as essential to drawing clear conclusions about the benefits of brain training for everyday activities."
The review runs to eighty-odd pages and the Association for Psychological Science keeps a public summary page for it. It is indexed here. If you read one thing in this whole literature, read its best-practices section.
Where the regulators landed
Two federal enforcement actions in 2016 put a floor under what may be advertised. Neither is a scientific finding, and neither tells you whether a program works. Both tell you what a marketing claim must be backed by. Nothing here is legal advice, and questions about what you may say in your own advertising belong with an attorney.
On 5 January 2016 the Federal Trade Commission announced that Lumos Labs would pay $2 million to settle deceptive advertising charges over its Lumosity program, against a judgment of $50 million suspended on the basis of the company's financial condition.
The claims at issue included that the games would improve performance "in school, at work, and in athletics" and delay age-related cognitive decline. The Bureau of Consumer Protection's director at the time, Jessica Rich, said: "Lumosity simply did not have the science to back up its ads."
The case file carries the order itself.
On 18 May 2016 the FTC announced a settlement with LearningRx Franchise Corp., a one-to-one rather than computerised program, on a $4 million judgment suspended upon payment of $200,000. The order bars unsubstantiated claims about school grades, standardised test scores, everyday task performance and superiority to tutoring unless supported by human clinical testing. Its case file is here.
The operative phrase in both orders is "competent and reliable scientific evidence." That is the standard a company must meet before advertising a benefit. It is also, usefully, the standard you can hold yourself to when you describe a program to a family — and it is the same discipline that governs what you may accurately claim about your own practice.
What the evidence catalogues hold, and what they do not
This is an absence finding, and absences in this field are usually more informative than presences. We checked both catalogues on 23 September 2026.
The What Works Clearinghouse holds no intervention report for Cogmed, Lumosity, LearningRx, or any working memory training program. Its Find What Works catalogue carries reviews of individual working memory training studies, and one intervention record for Fast ForWord, but no product-level report on cognitive training as a category.
The only listed intervention whose description names working memory is Tools of the Mind, and that is an early childhood curriculum, not a cognitive training program — it sits in the territory covered by our comparison of executive function curricula.
The National Center on Intensive Intervention's Academic Intervention Tools Chart lists 60 programs, and not one of them is a cognitive or working memory training program. The chart is populated with reading, mathematics, writing and learning-strategy interventions: Cover Copy Compare, Incremental Rehearsal, the Learning Strategies Curriculum, SRSD for Writing Strategies, Math Recovery. Fast ForWord Language Series appears — charted for prereading and reading outcomes, not cognitive ones.
That absence is not a judgment by either body. Neither clearinghouse has reviewed and rejected cognitive training programs. The charts are populated by submission, and NCII publishes its review process so you can see what a submission has to survive.
The correct statement is narrower and more useful. As of today, if you are looking for a cognitive training program on the two charts practitioners actually consult for intensive intervention, it is not there. The same distinction matters throughout the question of what "evidence-based" means for this field, where six bodies use the phrase to mean six different things.
The best-designed study in the field, and why it is the most instructive
The Advanced Cognitive Training for Independent and Vital Elderly study — ACTIVE — is the largest cognitive training intervention conducted, and Simons and colleagues single it out for praise. Its reporting, they write, "is a model of clarity," with CONSORT diagrams, all primary outcomes reported in a single paper for the whole sample, and years of follow-up.
And here is what that exemplary design produced: "The results of this large study were clear in showing effectively no evidence of transfer of training from one skill to another; improvements were mostly limited to the trained activities."
The speed-of-processing arm showed the largest gains. Those gains were "limited to similar outcome measures of processing speed" and "diminished over time."
This is the most important thing in the whole literature for a practitioner, and it is easy to miss. The pattern is not that sloppy studies find effects and careful studies find nothing in a way that leaves the question open. It is that the more carefully a study is designed, the more precisely it localises the improvement to the trained task. The finding is consistent, not absent.
How to read a training study in ten minutes
Turn the best practices in Simons and colleagues' review into a checklist. This works on any intervention study, not just cognitive training, and it is the same discipline you would bring to a program's published dosage specification.
1. What did the control group do?
Nothing, or a waitlist, means the study cannot separate the training from attention, novelty and practice at being tested. If the control was active, was it matched on time, adult contact and difficulty, and did it lack only the ingredient under test?
2. How far apart are the training task and the outcome task?
Write both down side by side. If the outcome is a digit-span variant and the training was digit-span-like, you are looking at very near transfer. If the outcome is a reading comprehension score, you are looking at far transfer and the bar is much higher.
3. How many participants?
The vendor's own document says 200 for adequate power and 350 to detect a small effect. A study of 60 is not evidence of absence, but it is not evidence of presence either.
4. Were all outcomes reported?
Count the outcome measures. If nineteen are listed in the methods and three in the results, ask where the other sixteen went. Was the study preregistered, and does the registration list the same primary outcomes as the paper?
5. Is the Time × Group interaction reported?
A within-group improvement is not a finding. The trained group improving is expected. The question is whether it improved more than the control group, and that is a specific statistic.
6. Are these papers independent of each other?
One large trial reported across six papers is one trial. Check the sample descriptions.
7. Who followed up, and how long after?
Effects that vanish at six months are real findings about six months. The Melbourne trial's benefit was gone by 24 months. Ask what the follow-up interval was and whether the paper reports it.
8. Who conducted it, and who paid?
Developer involvement is not disqualifying and independent replication is the relevant test. But it is information, and it belongs in your summary to the family.
What you may accurately say to a family
This is where the professional obligations bite, and they are more specific than practitioners tend to assume.
The AET Code of Ethics, Revision #9 binds several clauses here. Note first that the Code never uses the phrase "executive function" at all, while the association's public fact sheet claims "all aspects of executive functioning" for the role.
I.I.B requires educational therapists to "provide professional services only within the boundaries of their competence based on their education, training, supervised and professional experience." I.II.A narrows it further: "provide only those professional services for which they have been adequately trained."
II.I.N requires you to "establish baseline data about the skills and needs of new clients and maintain accurate data for the purpose of decision making," and N.1 to "establish ways to measure and determine client progress towards those goals at regular intervals."
II.II.I is the clause almost nobody quotes and the one most relevant to this conversation: educational therapists "facilitate the understanding among parents/guardians, school personnel, and other professionals regarding the realistic limitations of each one's function and role."
Read those together and the position is clear. You are not obliged to have an opinion on the literature. You are obliged to represent the limits of what you are offering accurately, to measure what you do, and to help a family understand what any of it can realistically be expected to do.
The sequence, not the decision
Consistent with how we handle every instrument and program comparison, here is a decision sequence rather than a decision. Choosing an intervention for a particular student is your clinical judgment and nobody else's.
Name the outcome the family actually wants. Almost always it is an academic or functional one: reading, written output, homework completion, independence.
Ask what the direct route to that outcome is. The evidence base for teaching the skill you want to change is considerably stronger than the evidence for training a capacity you hope will produce it.
If the family is committed to a training program regardless, do not fight it. Set a measurement plan before it starts, with a baseline on the actual outcome of interest and a review date.
Choose the outcome measure before the program begins, not after. The progress monitoring system you use has its own decision rules, and switching mid-stream breaks the graph.
Write down what you will conclude from each possible result. This is what separates a measurement plan from a hope.
Refer where the question is not yours. AET II.II.J requires you to "facilitate referral to other appropriate professionals for services as needed," and a question about a diagnosis or a cognitive profile sits with the professionals whose report you are reading, not writing.
Can a training program tell you whether a student has a working memory impairment? No. A training program is not an assessment, and qualification levels for the instruments that do assess it are a separate question entirely.
Where this leaves a caseload
The uncomfortable part of this literature is not that it debunks something. It is that it points, consistently, back to the slow route.
Gobet and Sala's recommendation — redirect effort to near transfer or other methods — is not a counsel of despair. It is a statement that if you want a student to read better, the intervention with the strongest evidence is reading instruction. If you want better written output, it is writing instruction. The evidence attaches to the thing you taught.
That is exactly the shape of the record in every adjacent area this site has mapped: reading intervention programs, math intervention for dyscalculia, and dysgraphia and writing intervention tools all show the same pattern — specific instruction produces specific gains, and the gains do not spread as far as anyone would like.
It is also why the distinction between training a capacity and teaching a strategy keeps recurring. Simons and colleagues put the general point plainly: "Brain training is appealing in part because it seems to provide a quick way to enhance cognition relative to the sustained investment required by education and skill acquisition."
None of this makes the conversation with a family easy. It does make it honest, and honesty about limits is the thing that distinguishes this role from the roles it gets confused with.
Where the published record runs out
Every map should say where it stops. Here is where this one does.
We did not assess every program on the market. This piece covers the programs with published meta-analytic or clearinghouse records. Several programs marketed to educational therapists and learning specialists have no independent evidence base we could locate, and the honest statement about those is that we have not evaluated them — not that they do not work.
The Pearson claims document carries no date or version number, so we cannot say when it was last revised or whether it predates the 2016 correction to one of the meta-analyses it cites.
We could not determine which corrected effect size the "0.7 standard deviations" figure corresponds to. The correction notice revised three separate values. If that number matters to a decision, read the notice.
The WWC's Fast ForWord reports date from 2006, 2010 and 2013. They are the current published record, but they are not recent, and none of them addresses the program's cognitive-skills claims.
Neither clearinghouse has reviewed and rejected cognitive training programs. The finding is that the programs are not on the charts, which is a statement about what has been submitted and reviewed, not a rating.
We found no meta-analysis of working memory training conducted specifically within one-to-one educational therapy. The populations in this literature are school samples, clinical samples and older adults. The setting you work in has not been studied as a setting.
Frequently asked questions
Does working memory training improve working memory?
Yes, on working memory tasks, and the effect is larger the more the outcome task resembles the trained task. Aksayli, Sala and Gobet estimated g = 0.566 for very near transfer and g = 0.246 for memory tasks that share the domain but not the format.
Does it improve reading or mathematics?
The meta-analytic evidence says no. Melby-Lervåg, Redick and Hulme found no convincing far transfer against treated controls, and the Cogmed-specific meta-analysis estimated far transfer at g = 0.048 with a confidence interval including zero. The Melbourne randomised trial found no academic benefit at one or two years.
Why do some studies find positive effects?
Three reasons appear repeatedly in the reviews: untreated or waitlist control groups, which cannot separate training from attention and test practice; small samples, which produce unstable estimates; and outcome measures that resemble the trained tasks more closely than the label suggests.
What is the difference between near and far transfer?
Near transfer means improvement on tasks that resemble what was trained. Far transfer means improvement on tasks that do not — reasoning, attention in daily life, reading, arithmetic. The distance between training and outcome is the single best predictor of effect size in this literature.
Is it unethical to recommend a cognitive training program?
That is not a question this article can answer for you, and it depends on what you claim for it. AET I.I.B and I.II.A bind you to the boundaries of your training, and II.II.I obliges you to help families understand realistic limitations. Describing a program accurately, measuring the outcome that matters, and setting a review date is consistent with those clauses.
What should I tell a family who has already bought one?
Tell them what it is likely to do and what it has not been shown to do, both sourced. Then offer to set the baseline and the review date, so that in twelve weeks the family has data rather than an impression. That is a service only you are positioned to provide.
Working with families and practitioners on this
Illuminate Educational Therapy Group keeps a list of educational therapists, learning specialists and executive function coaches for student matching and referrals. If you would like to be on it, join the educator list.
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