A gold-standard brain training study?
Not without some alchemy
A HI-BAR (Had I Been A Reviewer) of:
Corbett, A., Owen, A., Hampshire, A., Grahn, J., Stenton, R., Dajani, S., Burns, A., Howard, R., Williams, N., Williams, G., & Ballard, C. (2015). The effect of an online cognitive training package in healthy older adults: An online randomized controlled trial. JAMDA, 16(11), 990-997.
Edit 12-3-15: The planned sample was ~1 order of magnitude larger than the actual one, not 2. (HT Matthew Hutson in the comments)
A recent large-scale brain training study, published in the Journal of the American Medical Directors Association (JAMDA), has garnered a lot of attention. A press release was picked up by major media outlets, and a blog post by Tom Stafford on the popular Mind Hacks blog called it “a gold-standard study on brain training” and noted that “this kind of research is what ‘brain training’ needs.”*
Tom applied the label “gold standard” because of the study’s design: It was a large, randomized, controlled trial with an active control group and blinding to condition assignment. From the gold-standard monicker, though, people might infer that the research methods and results provide solid evidence for brain training benefits. They do not.
Tom's post identified several limitations of the study, such as differential attrition across conditions and the use of a self-report primary outcome measure. Below I discuss why these and other analysis and reporting problems undermine the claims of brain training benefits.
Tom's post identified several limitations of the study, such as differential attrition across conditions and the use of a self-report primary outcome measure. Below I discuss why these and other analysis and reporting problems undermine the claims of brain training benefits.
Problems that undermine interpretability of the study
Differential Attrition
The analysis was based on the 6-month testing point, but the study was missing data from about 70% of the participants due to attrition. To address this problem, the authors carried forward data from the final completed testing session for each participant and treated it as if it were from the 6-month point. Critically, the control group had substantially greater attrition than the intervention groups—more of their scores were carried forward from earlier points in the intervention.
For the control group, only 27% of the data for the primary outcome and 17% of the data for the secondary outcomes came from participants who actually completed their testing at 6 months. For the Reasoning group, those numbers were 42% and 40%. For the General Cognition group, they were 40% and 30%.
The extent of the differential attrition and rates of carrying forward results from earlier sessions were only discoverable by inspecting the Consort diagram. This analysis choice and its implications were not fully discussed, and the paper did not report analyses of participants with comparable durations of training. This analysis approach introduces a major confound that could entirely account for any differential benefits.
Unclear sample sizes and means
The Ns listed in the tables also are inconsistent with the information provided in the Consort diagram. In a few cases, the Tables list a larger N than the consort diagram, meaning that there were more subjects in the analysis than in the study.
I emailed the corresponding author (on Nov. 10 and Nov. 23) to ask about the each of these issues, but I received no response. I also emailed the second author. His assistant noted that the corresponding author's team was "was responsible for that part of the study" and said the second author "can be of no help with this." I’m hoping this post will prompt an explanation for the values in the tables.
For me, those reporting and analysis issues are show stoppers, but the paper has other issues.
Other issues
Limitations of the pre-registration
The study was pre-registered, meaning that the recruiting, testing methods, and analysis plans were specified in advance. Such pre-registrations are required for clinical trials, but they have been relatively uncommon in the brain training literature. Have a pre-registered plan is ideal because it eliminates much of the flexibility that otherwise can undermine the interpretability of findings. The use of pre-registration is laudable. But, the registration was underspecified and the reported study deviated from it in important ways.
For example, the protocol called for 75,000 - 100,000 participants, but the reported study recruited fewer than 7000. That’s still a great sample, but it’s2 orders an order of magnitude smaller than the planned sample. Are there more studies resulting from this larger sample that just aren’t mentioned in the pre-registration?
The study also called for a year of testing, but it had to be cut short at 6 months and more than 2/3 of the participants did not undergo even 6 months of training. The pre-registration did not include analysis scripts, and the data from the study do not appear to have been posted publicly.
For example, the protocol called for 75,000 - 100,000 participants, but the reported study recruited fewer than 7000. That’s still a great sample, but it’s
The study also called for a year of testing, but it had to be cut short at 6 months and more than 2/3 of the participants did not undergo even 6 months of training. The pre-registration did not include analysis scripts, and the data from the study do not appear to have been posted publicly.
The pre-registered hypotheses predicted greater improvements in the reasoning training group than the general cognition group and it predicted that the general cognition group would not outperform the control group. The paper reports no tests of this predicted difference.
Underreporting for the primary measure (IADL)
The primary outcome measure consisted of self-reports of performance in daily activities (known as the Instrumental Activities of Daily Living or IADL). As Tom's post noted, such self-reports are subject to demand characteristics — people expect to do better following training, so they report having done better. The study did not test for different expectations across the training and control groups, so the benefits could be due to such demands or to a differential placebo effect (e.g., the control group might have found the study less worthwhile).
The reported benefits for IADLs were small, and the data provide little evidence for any benefit of training. The study reported statistically significant benefits for both training groups relative to the control group, but statistical significance is not the same as evidence. With samples this large, we should expect a substantially lower p-value than .05 when an effect actually is present in the population. If the Ns and means reported in the table were consistent with the method description, it might be possible to compute a Bayes Factor for these analyses. My bet is that the difference between the training groups and the control group would provide weak evidence at best for a meaningful training benefit (relative to the null).
The paper provides no information about baseline scores on the primary outcome measure (IADL). Although the analyses control for baseline scores, training papers must provide the pre-test scores and post-test scores. Without doing so, it is impossible to evaluate whether apparent training benefits resulted in part from baseline differences.
The paper also states that “Data from interim time points also show significant benefit to IADL at 3 months, particularly in the GCT group, although this difference was not significant.” I take this to mean both training groups outperformed the control group at 3 months, but they did not differ significantly from each other. No statistical evidence is provided in support of this claim.
Limited evidence from the secondary measures
Underreporting for the primary measure (IADL)
The primary outcome measure consisted of self-reports of performance in daily activities (known as the Instrumental Activities of Daily Living or IADL). As Tom's post noted, such self-reports are subject to demand characteristics — people expect to do better following training, so they report having done better. The study did not test for different expectations across the training and control groups, so the benefits could be due to such demands or to a differential placebo effect (e.g., the control group might have found the study less worthwhile).
The reported benefits for IADLs were small, and the data provide little evidence for any benefit of training. The study reported statistically significant benefits for both training groups relative to the control group, but statistical significance is not the same as evidence. With samples this large, we should expect a substantially lower p-value than .05 when an effect actually is present in the population. If the Ns and means reported in the table were consistent with the method description, it might be possible to compute a Bayes Factor for these analyses. My bet is that the difference between the training groups and the control group would provide weak evidence at best for a meaningful training benefit (relative to the null).
The paper provides no information about baseline scores on the primary outcome measure (IADL). Although the analyses control for baseline scores, training papers must provide the pre-test scores and post-test scores. Without doing so, it is impossible to evaluate whether apparent training benefits resulted in part from baseline differences.
The paper also states that “Data from interim time points also show significant benefit to IADL at 3 months, particularly in the GCT group, although this difference was not significant.” I take this to mean both training groups outperformed the control group at 3 months, but they did not differ significantly from each other. No statistical evidence is provided in support of this claim.
Limited evidence from the secondary measures
Only one of the secondary cognitive outcome measures (a reasoning measure) showed a training benefit. The paper refers to it as “the key secondary measure,” but that designation does not appear in the pre-registration (http://www.isrctn.com/ISRCTN72895114). Moreover, the pre-registration predicts better performance for reasoning training than general cognition training or the control group, but the paper found improvements for both interventions. A few other measures showed significant effects, but given the large sample sizes, the high p-values might well be more consistent with the absence of a training benefit than the presence of one.
Despite providing no statistical evidence of differential benefits for Reasoning training and General Cognition training, the paper claims that “Taken together, these findings indicate that the ReaCT package confers a more generalized cognitive benefit than the GCT at 6 months. That claim appears to come from finding no effect on a digit secondary task in the Reasoning group and a decline in the General cognition group. However, a difference in significance is not a significant difference.
Almost all of the measures showed declining performance from the pre-test to the post-test. That is, participants were not getting better. They just declined less than the control participants. It is unclear why we should see such a pattern of declining performance over a short time window with relatively young participants. Although cognitive performance does decline with age, presumably those declines should be minimal over 1-6 months, and they should be swamped by the benefits of taking the test twice. One explanation might be differential attrition -- those subjects who did worse initially were more likely to drop out early.
* Thanks to Tom Stafford for emailing a copy of the paper. The journal is obscure enough that the University of Illinois library did not have access to it.
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