What the evidence does not support.
We are an applied institute, not a research one.
We teach methods that have been studied. We do not conduct our own research and we do not claim to. Nothing on this site is “our research”, because there is none.
This page sets out what the published evidence supports, where it is weak, where it points the other way, and what we therefore will not tell you. It is the longest page on this site and the one we would most like you to read before you spend anything.
The people we admit are professional sceptics. A claim we cannot defend is worth less to us than no claim at all — which is why the section on what the evidence does not support is longer than the section on what it does.
What the evidence supports.
Four claims we think the literature will bear, each stated at the size the literature will bear it — which is smaller than this industry usually implies.
Attention training produces small but real gains in measured attention.
The best available meta-analysis puts the effect at roughly a quarter of a standard deviation — Hedges' g ≈ 0.29 across 109 effect sizes from 40 intervention studies (Verhaeghen, 2021, Mindfulness). That is a genuine, replicated effect. It is not a transformation, and it is an effect on laboratory attention tasks. Whether it appears in a meeting or a board decision has not been demonstrated, and we do not claim it has.
The strongest applied finding is protection against degradation, not enhancement.
Work with high-demand populations shows that periods of extreme load degrade attention and working memory, and that attention training attenuates that decline (Jha et al., 2015, PLOS ONE; Jha et al., 2020, Cognitive Therapy and Research). The value is in what does not fall away. That is a less dramatic claim and a more useful one — and it is the closest thing in this literature to what we actually sell.
Both studies are small. The 2015 study was quasi-experimental, allocated by unit rather than by individual, with nineteen people in one of its four arms, and the protective effect appeared only in the group that actually practised — the arm that received instruction without practice degraded like the untrained control. In the 2020 randomised trial both arms declined; the trained arm declined less. Neither is a study of our programme.
Decentering is measurable, and as a mechanism it is plausible rather than demonstrated.
The capacity to observe a thought as a thought rather than as a fact about the world can be measured with validated self-report instruments, and it shifts with practice. That is a psychometric finding, not a causal one: validating an instrument establishes that a construct can be measured consistently, not that it produces anything downstream. We work with decentering because it is coherent and measurable, not because it has been shown to be the mechanism.
Psychological flexibility is associated with occupational outcomes — and it is our weakest construct.
Acceptance-based methods have a more developed research base in workplace settings than most contemplative research does. But the meta-analysts who looked specifically at work performance declined to draw a conclusion (Bartlett et al., 2019, Journal of Occupational Health Psychology), and the instrument the field relies on has documented measurement problems of its own — see What we measure. We report this as the weakest of the four capacities we teach, because it is.
What the evidence does not support.
Most organisations selling this kind of work do not publish this section. That is the whole reason we do.
Superiority over an active alternative is not established.
The largest meta-analysis of mindfulness-based programmes in non-clinical adults — 136 randomised trials, 11,605 participants (Galante et al., 2021, PLOS Medicine) — found benefits against passive controls, but no statistically significant superiority over specific active comparison conditions on any primary outcome. Against non-specific active controls the only significant effect was on depression (SMD −0.46). The authors record that all 136 included trials were at high risk of bias.
Read plainly: compared against doing nothing, effects appear. Compared against another structured activity that occupies the same hours with the same expectation of benefit, they largely do not. Anyone who omits this is not describing the literature accurately.
Neuroimaging claims are routinely overstated, and we will not use them.
Findings in this area are heterogeneous, frequently drawn from small samples, and habitually over-interpreted once they leave the journal. “Rewiring the brain” is not a claim we will make, not in a brochure, not in a conversation, and not in a room where somebody is deciding whether to spend a five-figure sum. We do not use brain images to sell a programme.
The field has been criticised from inside, and we think the criticism is largely fair.
A 2018 review in Perspectives on Psychological Science (Van Dam et al., 13(1), 36–61) documented conceptual imprecision, methodological weakness and systematic overstatement across the mindfulness literature. It was written by people inside the field, about the field. We do not treat it as an attack to be managed. We treat it as an accurate description of the ground we are standing on.
Transfer to real-world decision quality is the weakest link in the chain.
The single result most often used to sell training like ours reported that a brief mindfulness induction reduced sunk-cost bias (Hafenbrack, Kinias & Barsade, 2014, Psychological Science). It failed direct replication — twice, in the same paper (Williams & Polito, 2022: p = 0.315 and p = 0.577). We name it here precisely because we sell attention training to people who make consequential decisions, and because the best-known evidence that it improves decisions did not hold.
We have no outcome data of our own.
The Institute was established in 2026. We have run no cohorts under this brand, we have no alumni figures, no completion statistics and no outcome data. We will collect pre- and post-measures with validated instruments from the first cohort onward and give every participant their own result — and we will not present that data as evidence that the programme works. The reason is in What we measure, and it is not modesty.
A range you can check is worth more than a reassurance you cannot.
Risk. The honest numbers.
Intensive contemplative practice is not risk-free, and the published figures are larger than this field usually admits. They are also inconsistent with one another, for reasons that are themselves informative.
The 2025 figures come from the only approximately representative sample in this literature — 886 US adults, quota-matched to population age, gender and race or ethnicity. That is what makes them the ones we lead with, and the finding that matters most to us is not the headline percentage but the predictor: residential retreat attendance was the most robust predictor of functional impairment. Intensive residential formats are the higher-risk end of this work, and saying so out loud is inconvenient for anyone selling them.
It is also the reason we do not run one. None of our three programmes is a residential retreat. The cohort is remote and participants stay at home and at work; the individual programme is one-to-one; the institutional programme runs at the client’s own premises and over secure video. We designed around this finding rather than publishing it and hoping you would not connect it to us.
The 2021 trial figures are higher than the survey figures for a specific and important reason: the researchers used independent assessors and a 44-item structured interview instead of waiting for participants to volunteer that something had gone wrong. When you ask properly, you find more. The Farias review makes the same point from the other direction — a ninefold gap between the rate reported in trials and the rate reported in observational studies is not evidence that trials are safer. It is evidence that trials mostly do not ask. That review also concluded that adverse events occur in people with no previous history of mental health problems.
One citation we are careful with. Lindahl et al. (2017, PLOS ONE 12(5):e0176239) is the study most often quoted in this area, and it is frequently quoted wrongly. We cite it for two things only: its taxonomy of 59 categories of meditation-related difficulty across seven domains, and the finding that 72% of the difficulties described arose during or immediately after a retreat. We do not cite it for prevalence. It used deviant-case sampling — it deliberately sought out people who had had difficulties — and reports no prevalence rate at all. Anyone presenting a percentage from that paper as “how often this happens” has misread it. It describes the range of difficulty, not its frequency.
These are studies of other people's programmes and of meditators in general. They are not studies of ours. They may overstate what happens here, or understate it. We do not know, because we have not measured it and we do not claim to have. We publish them because a range you can check is worth more than a reassurance you cannot.
What we do about it
Every applicant completes a health and history screening and speaks with a member of our teaching team before a decision. We decline against written criteria rather than at discretion.
What screening cannot do
Screening reduces risk. It does not remove it. If we admit you, that is not a statement that this will be safe for you — it is a statement that we found nothing telling us it would not be.
You may stop at any time
You may leave any practice, shorten it, sit out, decline to speak, or leave a programme entirely, at any point, without explanation. Stopping is never treated as resistance or lack of commitment.
Declining costs you nothing
If we decline you, or if you disclose something that means we cannot admit you, everything you have paid is refunded in full, including the deposit. Nobody should have a financial reason to conceal anything.
What we measure, and what the measurements cannot tell you.
Validated instruments, administered before a programme and after it. Results go to the participant, with an interpretation, including where nothing changed.
| Instrument | What it measures | What it does not tell you |
|---|---|---|
| Experiences Questionnaire | Decentering | Self-report. A movement in the score records a change in how you describe your relationship to thought, not a demonstrated change in behaviour. |
| Cognitive Fusion Questionnaire | Fusion with thought content | Self-report, and sensitive to acquired vocabulary — people trained in a construct get better at recognising it in a questionnaire. |
| Mindful Attention Awareness Scale | Dispositional attentional awareness | A disposition measure, not a performance measure. It cannot distinguish improved attention from improved noticing of inattention. |
| Acceptance and Action Questionnaire II | Psychological flexibility | Documented discriminant-validity problems. It functions substantially as a general distress measure rather than a flexibility measure, and we report it as a distress index, not a flexibility score. |
| Perceived Stress Scale | Subjective stress load | A subjective self-report at a moment in time. We do not present a movement in it as a health outcome, because it is not one. |
| Sustained attention task | Objective attentional performance | Indexes a speed–accuracy trade-off as much as attentional lapse. We report and control for that, and improvement on a laboratory task has not been shown to transfer to work. |
We will not publish aggregate pre-and-post results as evidence that our programmes work.
Uncontrolled before-and-after data cannot support a causal claim. Everyone in the sample chose the programme, paid a significant sum for it, expected it to help, and answered the same questionnaire twice. Regression to the mean, demand characteristics, expectancy and simple attrition all push the second number in the same direction, and none of them are the training. Publishing that chart as proof would be exactly the overstatement the rest of this page criticises.
Each participant receives their own results, with an honest interpretation, including where nothing moved. If we ever run properly controlled research, we will publish it as research — with a methods section, named investigators and a pre-registered analysis — and it will be judged as research.
Our claims policy.
“We describe what we teach and what we measure. We do not describe what will happen to you.”
No medical claims
We make no medical or psychiatric claims of any kind. We do not treat, reduce, relieve or address any condition. Our programmes are education, not medical care, psychotherapy, counselling or psychiatric treatment, and not a substitute for any of them.
No figures we have not measured
We publish no result figures we have not measured. No completion statistics, no satisfaction scores, no alumni numbers, no countries served. We were established in 2026 and we say so.
No testimonials of improvement
We use no testimonials describing medical or psychological improvement, and no client logos. We publish no participant names.
No accreditation, no degrees
We are not accredited, we award no degrees or academic credit, and we are not affiliated with any university. “Institute” is descriptive. A certificate of completion records attendance and nothing more.
Never “evidence-based”
We do not use the phrases “evidence-based”, “clinically proven”, “proven” or “verifiable outcomes”. The term we use is evidence-informed, and it means only that our design draws on published research by other people.
Never “our research”
We conduct no research, publish no findings, and do not describe ourselves as a research organisation. We are a training company that reads the literature carefully.
Every citation on this page, in full.
With the design, the sample and the limitation, because a citation without those is decoration. Two of these are here because they did not hold.
Effects of attention training
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Verhaeghen, P. (2021). Mindfulness, 12(3), 564–581. doi.org/10.1007/s12671-020-01532-1
Meta-analysis. Hedges' g = 0.29 across 109 effect sizes from 40 intervention studies. Limitation: the outcomes are objective laboratory attention tasks. Transfer to working life is not tested.
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Jha, A. P., Morrison, A. B., Dainer-Best, J., Parker, S., Rostrup, N., & Stanley, E. A. (2015). PLOS ONE, 10(2), e0116889. doi.org/10.1371/journal.pone.0116889
Quasi-experimental, N = 134 across four arms, allocation by unit rather than by individual, one arm n = 19. Attention degraded under high load in untrained participants; the protective effect appeared only in the practice-focused arm. The arm that received instruction without practice degraded like the untrained control.
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Jha, A. P., Zanesco, A. P., Denkova, E., Rooks, J., Morrison, A. B., & Stanley, E. A. (2020). Cognitive Therapy and Research, 44(2), 311–326. doi.org/10.1007/s10608-020-10076-6
Randomised trial, N = 80 US Army soldiers, two active arms, no passive control. Both arms declined from first to second measurement; the mindfulness arm declined significantly less.
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Bartlett, L., et al. (2019). Journal of Occupational Health Psychology, 24(1), 108–126.
Meta-analysis of workplace mindfulness programmes. The authors explicitly declined to draw a conclusion on work performance.
What the evidence does not support
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Galante, J., Friedrich, C., Dawson, A. F., Modrego-Alarcón, M., Gebbing, P., Delgado-Suárez, I., Gupta, R., Dean, L., Dalgleish, T., White, I. R., & Jones, P. B. (2021). PLOS Medicine, 18(1), e1003481. doi.org/10.1371/journal.pmed.1003481
136 randomised trials, 11,605 participants. Benefits against passive controls. No statistically significant superiority over specific active controls on any primary outcome. Against non-specific active controls the only significant effect was on depression (SMD −0.46, 95% CI −0.81 to −0.10, p = 0.012). All 136 included trials were at high risk of bias; GRADE confidence moderate to very low.
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Van Dam, N. T., van Vugt, M. K., Vago, D. R., et al. (2018). Mind the hype: a critical evaluation and prescriptive agenda for research on mindfulness and meditation. Perspectives on Psychological Science, 13(1), 36–61. doi.org/10.1177/1745691617709589
Critical review from inside the field. Documents conceptual imprecision, methodological weakness and systematic overstatement. Not to be confused with Van Dam et al. (2025), the adverse-effects prevalence study, which shares a first author and nothing else.
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Hafenbrack, A. C., Kinias, Z., & Barsade, S. G. (2014). Psychological Science, 25(2), 369–376. doi.org/10.1177/0956797613503853
Brief mindfulness induction reported to reduce sunk-cost bias. Listed here because it failed replication — see the next entry. Do not read this entry without it.
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Williams, A. L., & Polito, V. (2022). Frontiers in Psychology, 13, 747983.
Two direct replication attempts of the Hafenbrack sunk-cost finding. Both null: Experiment 1 p = 0.315, Experiment 2 p = 0.577.
Risk and adverse effects
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Van Dam, N. T., Targett, J., Davies, J. N., Burger, A., & Galante, J. (2025). Clinical Psychological Science, 13(3). journals.sagepub.com/doi/10.1177/21677026241298269
Cross-sectional survey of 886 US adults, quota-matched to population age, gender and race or ethnicity — the only approximately representative sample in this literature. 58.4% reported an adverse effect, 31.4% a challenging, difficult or distressing experience, 9.1% functional impairment. Residential-retreat attendance was the most robust predictor of functional impairment.
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Britton, W. B., Lindahl, J. R., Cooper, D. J., Canby, N. K., & Palitsky, R. (2021). Clinical Psychological Science, 9(6), 1185–1204. journals.sagepub.com/doi/abs/10.1177/2167702621996340
Randomised trial of an eight-week mindfulness-based programme, using a 44-item structured interview administered by independent assessors rather than spontaneous reporting. 83% reported at least one side effect, 37% a negative impact on functioning, and 6–14% effects lasting a month or longer.
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Farias, M., Maraldi, E., Wallenkampf, K. C., & Lucchetti, G. (2020). Acta Psychiatrica Scandinavica, 142(5), 374–393. onlinelibrary.wiley.com/doi/10.1111/acps.13225
Systematic review, 83 studies, 6,703 participants. Overall adverse-event prevalence 8.3% — but 3.7% in experimental studies against 33.2% in observational studies, because trials mostly do not ask. Adverse events occur in people with no previous history of mental health problems.
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Lindahl, J. R., Fisher, N. E., Cooper, D. J., Rosen, R. K., & Britton, W. B. (2017). PLOS ONE, 12(5), e0176239. journals.plos.org/plosone/article?id=10.1371/journal.pone.0176239
Qualitative mixed-methods study of 60 practitioners and 32 teachers. 59 categories of meditation-related difficulty across seven domains; 72% arose during or immediately after a retreat; durations from one day to more than twenty-five years. This study used deviant-case sampling and reports no prevalence rate. We cite it for its taxonomy and for the 72% figure only, and never as a frequency source.