Misleading systematic review of mindfulness studies used to promote Bensen Institute for Mind-Body Medicine services

A seriously flawed overview “systematic review “ of systematic reviews and meta-analyses of the effects of mindfulness on health and well-being alerts readers how they need to be skeptical of what they are told about the benefits of mindfulness.

Especially when the information comes those benefiting enormously from promoting the practice.

The glowing evaluation of the benefits of mindfulness presented in a PLOS One review is contradicted by a more comprehensive and systematic review which was cited but summarily dismissed. As we will see, the PLOS One article sidesteps substantial confirmation bias and untrustworthiness in the mindfulness literature.

The review was prepared by authors associated with the Benson-Henry Institute for Mind-Body Medicine, which is tied to Massachusetts General Hospital and Harvard Medical School. The institute directly markets mindfulness treatment to patients and training to professionals and organizations.  Its website provides links to research articles such as this one, which are used to market a wide range of programs –

being calm

Recently PLOS One published corrections to five articles from this group concerning previous statements about the authors having no conflicts of interest to declare. The corrections acknowledged extensive conflicts of interest.

The Competing Interests statement is incorrect. The correct Competing Interests statement is: The following authors hold or have held positions at the Benson-Henry Institute for Mind-Body Medicine at Massachusetts General Hospital, which is paid by patients and their insurers for running the SMART-3RP and related relaxation/mindfulness clinical programs, markets related products such as books, DVDs, CDs and the like, and holds a patent pending (PCT/US2012/049539 filed August 3, 2012) entitled “Quantitative Genomics of the Relaxation Response.”

While the review we will be discussing was not corrected, it should have been.

The same conflicts of interest should have been disclosed to readers evaluating the trustworthiness of what is being presented to them.

Probing this review will demonstrate just how hard it is to uncover the bias and distortions that routinely is provided by promoters of mindfulness wanting to demonstrate the evidence base for what they offer.

The article is

Gotink, R.A., Chu, P., Busschbach, J.J., Benson, H., Fricchione, G.L. and Hunink, M.M., 2015. Standardised mindfulness-based interventions in healthcare: an overview of systematic reviews and meta-analyses of RCTs. PLOS One, 10(4), p.e0124344.

The abstract offers the conclusion:

The evidence supports the use of MBSR and MBCT to alleviate symptoms, both mental and physical, in the adjunct treatment of cancer, cardiovascular disease, chronic pain, depression, anxiety disorders and in prevention in healthy adults and children.

This evaluation is more emphatically stated near the end of the article:

This review provides an overview of more trials than ever before and the intervention effect has thus been evaluated across a broad spectrum of target conditions, most of which are common chronic conditions. Study settings in many countries across the globe contributed to the analysis, further serving to increase the generalizability of the evidence. Beneficial effects were mostly seen in mental health outcomes: depression, anxiety, stress and quality of life improved significantly after training in MBSR or MBCT. These effects were seen both in patients with medical conditions and those with psychological disorders, compared with many types of control interventions (WL, TAU or AT). Further evidence for effectiveness was provided by the observed dose-response relationship: an increase in total minutes of practice and class attendance led to a larger reduction of stress and mood complaints in four reviews [18,20,37,54].

Are you impressed? “More than ever before”? “Generalizability of the evidence”? Really?

And in wrap up summary comments:

Although there is continued scepticism in the medical world towards MBSR and MBCT, the evidence indicates that MBSR and MBCT are associated with improvements in depressive symptoms, anxiety, stress, quality of life, and selected physical outcomes in the adjunct treatment of cancer, cardiovascular disease, chronic pain, chronic somatic diseases, depression, anxiety disorders, other mental disorders and in prevention in healthy adults and children.

Compare and contrast these conclusions with a more balanced and comprehensive review.

The US Agency for Healthcare Research and Quality (AHCRQ) commissioned a report from Johns Hopkins University Evidence-based Practice Center.

The 439 page report is publicly available:

Goyal M, Singh S, Sibinga EMS, Gould NF, Rowland-Seymour A, Sharma R, Berger Z, Sleicher D, Maron DD, Shihab HM, Ranasinghe PD, Linn S, Saha S, Bass EB, Haythornthwaite JA. Meditation Programs for Psychological Stress and Well-Being. Comparative Effectiveness Review No. 124. (Prepared by Johns Hopkins University Evidence-based Practice Center under Contract No. 290-2007-10061–I.) AHRQ Publication No. 13(14)-EHC116-EF. Rockville, MD: Agency for Healthcare Research and Quality; January 2014.

A companion, less detailed article was also published in JAMA: Internal Medicine:

Goyal, M., Singh, S., Sibinga, E.M., Gould, N.F., Rowland-Seymour, A., Sharma, R., Berger, Z., Sleicher, D., Maron, D.D., Shihab, H.M. and Ranasinghe, P.D., 2014. Meditation programs for psychological stress and well-being: a systematic review and meta-analysis. JAMA Internal Medicine, 174(3), pp.357-368.

Consider how conclusions of this article were characterized in the Bensen-Henry PLOS One article. The article is briefly mentioned without detailing its methods and conclusions.

Recently, Goyal et al. published a review of mindfulness interventions compared to active control and found significant improvements in depression and anxiety[7].


A recent review compared meditation to only active control groups, and although lower, also found a beneficial effect on depression, anxiety, stress and quality of life. This review was excluded in our study for its heterogeneity of interventions [7].

What the Goyal et JAMA: Internal Medicine actually said:

After reviewing 18 753 citations, we included 47 trials with 3515 participants. Mindfulness meditation programs had moderate evidence of improved anxiety (effect size, 0.38 [95% CI, 0.12-0.64] at 8 weeks and 0.22 [0.02-0.43] at 3-6 months), depression (0.30 [0.00-0.59] at 8 weeks and 0.23 [0.05-0.42] at 3-6 months), and pain (0.33 [0.03- 0.62]) and low evidence of improved stress/distress and mental health–related quality of life. We found low evidence of no effect or insufficient evidence of any effect of meditation programs on positive mood, attention, substance use, eating habits, sleep, and weight. We found no evidence that meditation programs were better than any active treatment (ie, drugs, exercise, and other behavioral therapies).

The review also notes that evidence of the effectiveness mindfulness interventions is largely limited to trials in which it is compared to no treatment, wait list, or a usually ill-defined treatment as usual (TAU).

In our comparative effectiveness analyses (Figure 1B), we found low evidence of no effect or insufficient evidence that any of the meditation programs were more effective than exercise, progressive muscle relaxation, cognitive-behavioral group therapy, or other specific comparators in changing any outcomes of interest. Few trials reported on potential harms of meditation programs. Of the 9 trials reporting this information, none reported any harms of the intervention.

This solid JAMA: Internal Medicine review explains why its conclusions may differ from past reviews:

Reviews to date report a small to moderate effect of mindfulness and mantra meditation techniques in reducing emotional symptoms (eg, anxiety, depression, and stress) and improving physical symptoms (eg, pain).7– 26 These reviews have largely included uncontrolled and controlled studies, and many of the controlled studies did not adequately control for placebo effects (eg, waiting list– or usual care–controlled studies). Observational studies have a high risk of bias owing to problems such as self-selection of interventions (people who believe in the benefits of meditation or who have prior experience with meditation are more likely to enroll in a meditation program and report that they benefited from one) and use of outcome measures that can be easily biased by participants’ beliefs in the benefits of meditation. Clinicians need to know whether meditation training has beneficial effects beyond self-selection biases and the nonspecific effects of time, attention, and expectations for improvement.27,28

Basically, this article insists that mindfulness be evaluated in a  head-to- head comparison to an active treatment. Failure to provide such a comparison means not being able to rule out that apparent effects of mindfulness are nonspecific, i.e.,  not due to any active ingredient of the practice.

An accompanying editorial commentary raised troubling issues about the state of the mindfulness literature. It noted that limiting inclusion to RCTs with an active control condition and a patient population experiencing mental or physical health problems left only 3% (47/18,753 of the citations that had been retrieved. Furthermore:

The modest benefit found in the study by Goyal et al begs the question of why, in the absence of strong scientifically vetted evidence, meditation in particular and complementary measures in general have become so popular, especially among the influential and well educated…What role is being played by commercial interests? Are they taking advantage of the public’s anxieties to promote use of complementary measures that lack a base of scientific evidence? Do we need to require scientific evidence of efficacy and safety for these measures?

How did the Bensen-Henry review arrive at a more favorable assessment?

The issue that dominated the solid Goyal et al systematic review and meta analysis is not prominent in the Bensen-Henry review. The latter article hardly mentions the importance of whether mindfulness is compared to an active treatment. It doesn’t mention if any difference in effect size for mindfulness can be expected when the comparison is an active treatment.

The Bensen-Henry review stated that it excluded systematic reviews and meta analyses if they did not focus on MBCT or MBSR. One has to search the supplementary materials to find that Goyal et al was excluded because it did not calculate separate effect sizes for mindfulness-based stress reduction (MBSR).

However, Bensen-Henry review included narrative systematic reviews that did not calculate effect sizes at all. Furthermore, the excluded Goyal et al JAMA: Internal Medicine article summarized MBSR separate from other forms of meditation and the more comprehensive AHCQR report provided detailed forest plots of effect sizes for MBSR with specific outcomes and patient populations.

Hmm, keeping out evidence that does fit with the sell-job story?

We need to keep in mind the poor manner in which MBSR was specified, particularly in the early studies that dominate the reviews covered by the Bensen – Henry article. Many of the treatments were not standardized and certainly not manualized. They sometimes, but not always incorporate psychoeducation, other cognitive behavioral techniques, and varying types of yoga.

The Bensen-Henry authors claimed to have performed quality assessments  of the reviews  included using a checklist based on the validated PRISMA guidelines. However, PRISMA evaluates the quality of reporting in reviews, not the quality of how the review was done. The checklist used by the Bensen-Henry authors was highly selective in terms of which PRISMA items it chose to include, left unvalidated, and simply eccentric. For instance, one item evaluated a review favorably if it interpreted studies “independent of funding source.”

A lack of independence of a study from its funding source is generally considered a high risk of bias.  There is ample documentation of  industry-funded studies and reviews exaggerating the efficacy of interventions supported by industry.

Our group received the Bill Silverman Prize from the Cochrane Collaboration for our identifying funding source as an overlooked source of bias in many meta analyses and, in particular, in Cochrane reviews. The Bensen-Henry checklist scores a review ignoring funding source as a virtue, not a vice! These authors are letting trials and reviews from promoters of mindfulness off the hook for potential conflict of interest, including their own studies and this review.

Examination of the final sample of reviews included in the Bensen-Henry analysis reveals that some are narrative reviews and could not contribute effect sizes. Some are older reviews that depend on a less developed literature. While optimistic about the promise of mindfulness, authors of these reviews frequently complained about the limits on the quantity and quality of available studies, calling for larger and better quality studies. When integrated and summarized by the Bensen-Henry authors, these reviews were given a more positive glow than the original authors conveyed.

Despite claims of being an “overview of more trials than ever before”, Bensen-Henry excluded all but 23 reviews. Some of those included do not appear to be recent or rigorous, particularly when contrasted with the quality and rigor of the excluded Goyal et al:

MJ, Norris RL, Bauer-Wu SM (2006) Mindfulness meditation for oncology patients: A discussion and critical review. Integr Cancer Ther 5: 98–108. pmid:16685074

Shennan C, Payne S, Fenlon D (2011) What is the evidence for the use of mindfulness-based interventions in cancer care? A review. Psycho-Oncology 20: 681–697.

Veehof MM, Oskam MJ, Schreurs KMG, Bohlmeijer ET (2011) Acceptance-based interventions for the treatment of chronic pain: A systematic review and meta-analysis. Pain 152: 533–542

Coelho HF, Canter PH, Ernst E (2007) Mindfulness-Based Cognitive Therapy: Evaluating Current Evidence and Informing Future Research. J Consult Clin Psychol 75: 1000–1005.

Ledesma D, Kumano H (2009) Mindfulness-based stress reduction and cancer: A meta-analysis. Psycho-Oncology 18: 571–579.

Ott MJ, Norris RL, Bauer-Wu SM (2006) Mindfulness meditation for oncology patients: A discussion and critical review. Integr Cancer Ther 5: 98–108.

Burke CA (2009) Mindfulness-Based Approaches with Children and Adolescents: A Preliminary Review of Current Research in an Emergent Field. J Child Fam Stud.

Do we get the most authoritative reviews of mindfulness from  Holist Nurs Pract, Integr Cancer Ther, and Psycho-Oncology?

To cite just one example of the weakness of evidence being presented as strong, take the bold Bensen-Henry conclusion:

Further evidence for effectiveness was provided by the observed dose-response relationship: an increase in total minutes of practice and class attendance led to a larger reduction of stress and mood complaints in four reviews [18,20,37,54].

“Observed dose-response relationship”? This claim is  based [check out with respect to the citations just above] on Ott et al, 18, Smith et al 20, Burke 37 and Proulx 54, which makes the evidence neither recent nor systematic. I am confident that other examples will not hold up if scrutinized.

Further contradiction of the too perfect picture of mindfulness therapy conveyed by the Bensen – Henry review.

A more recent PLOS One review of mindfulness studies exposed the confirmation bias in the published mindfulness literature. It suggested a too perfect picture has been created of uniformly positive studies.

Coronado-Montoya, S., Levis, A.W., Kwakkenbos, L., Steele, R.J., Turner, E.H. and Thombs, B.D., 2016. Reporting of positive results in randomized controlled trials of mindfulness-based mental health interventions. PLOS One, 11(4), p.e0153220.

A systematic search yielded 124 RCTs of mindfulness-based treatments:

108 (87%) of 124 published trials reported >1 positive outcome in the abstract, and 109(88%) concluded that mindfulness-based therapy was effective, 1.6 times greater than the expected number of positive trials based on effect size d = 0.55 (expected number positivetrials = 65.7). Of 21 trial registrations, 13 (62%) remained unpublished 30 months post-trial completion.


None of the 21 registrations, however, adequately specified a single primary outcome (or multiple primary outcomes with an appropriate plan for statistical adjustment) and specified the outcome measure, the time of assessment, and the metric (e.g., continuous, dichotomous). When we removed the metric requirement, only 2 (10%) registrations were classified as adequate.

And finally:

There were only 3 trials that were presented unequivocally as negative trials without alternative interpretations or caveats to mitigate the negative results and suggest that the treatment might still be an effective treatment.

What we have is a picture of trials of mindfulness-based treatment having an excess of positive studies, given the study sample sizes. Selective reporting of positive outcomes likely contributed to this excess of published positive findings in the published literature. Most of the trials were not preregistered and so it’s unclear whether the positive outcomes that were reported were hypothesized to be the primary outcomes of interest. Most of the trials that were preregistered remained unpublished 30 months after the trials were completed.

The Goyal et al. study originally planned to conduct quantitative analyses of publication biases, but abandoned the effort when they couldn’t find sufficient numbers of the 47 studies that that reported most of the outcomes they evaluated.


 The Bensen-Henry review produces a glowing picture of the quality of RCTs evaluating MSBR and the consistency of positive findings across diverse outcomes and populations. This is consistent with the message that they want to promote in marketing their products to patients, clinicians, and institutions. In this blog post I’ve uncovered substantial problems in internal to the Bensen-Henry review in terms of the studies that were included and the manner in which they were evaluated. But now we have external evidence in two reviews without obvious conflicts of interest come into markedly different appraisals of a literature that lacks appropriate control groups and seems to be reporting findings with a distinct confirmation bias.

I could have gone further, but what I found about the Bensen-Henry review seems sufficient for a serious challenge to the validity of its conclusions.  Investigation of the claims made about dose-response relationships between amount of mindfulness practice and outcomes should encourage probing of other specific claims.

The larger issue is that we should not rely on promoters of MSBR products to provide unbiased estimates of their efficacy. This issue recalls very similar problems in the evaluation of Triple P Parenting Programs. Evaluations in which promoters were involved produce markedly more positive results than from independent evaluations. Exposure by my colleagues and me led to over 50 corrections and corrigendum to articles that previously had no conflicts of interest. But the process did not occur without fierce resistance from those whose livelihood was being challenged.

A correction to the Bensen-Henry PLOS One review is in order to clarify the obvious conflicts of interest of the authors. But the problem is not limited to reviews or original studies from Benson-Henry Institute for Mind-Body Medicine. It’s time that authors be required to answer more explicit questions about conflict of interest. Ruling out a conflict of interest should be based on authors having to endorse explicitly no conflicts, rather than on their basis of their not disclosing a conflict and then being able to claim it was an oversight that they did not report one.

Postscript Who was watching at PLOS One to keep out infomercials from promoters associated with Massachusetts General Hospital and Harvard Medical School? The Academic Editor was To avoid the appearance of  a conflict of interest,  should he have recused him from serving as editor?

This is another flawed paper for which I’d love to see the reviews.

eBook_Mindfulness_345x550I will soon be offering e-books providing skeptical looks at mindfulness and positive psychology, as well as scientific writing courses on the web as I have been doing face-to-face for almost a decade.

Sign up at my new website to get advance notice of the forthcoming e-books and web courses, as well as upcoming blog posts at this and other blog sites.  Get advance notice of forthcoming e-books and web courses. Lots to see at CoyneoftheRealm.com.


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