Can Meditation Be Too Much? On a Flawed Thesis!

/ Jan

A Real Signal, Wrapped in False Precision: A Second Look at “The Dark Side of Mindfulness”

The Atlantic has just published a long, well-reported piece on Willoughby Britton, the Brown University researcher turned Cheetah House founder, who has spent nearly two decades documenting the ways meditation can go wrong (“The Dark Side of Mindfulness,” theatlantic.com, September 2026). It is a good piece of journalism, and it tells a story worth taking seriously: some people who meditate, especially on intensive retreats, experience genuine and sometimes lasting psychological harm, and a teaching culture built on “it gets worse before it gets better” has not always handled that honestly.

That part of the story does not need defending against. What needs a closer look is the epidemiology the article leans on to make the harm sound as common and as well-quantified as it is presented. As someone who spent a career in drug development reading adverse-event data for a living, I read claims like “roughly 1 in 10 meditators experience an effect lasting more than a month, a rate that would qualify as very common for a drug” the way I would read a pharmacovigilance signal, and this one does not hold up as stated.

Confounding is the first problem, and it is a big one. A ten-day silent retreat is not a clean dose of “meditation.” It is meditation bundled with sleep restriction, caloric restriction, sensory deprivation, social isolation, and a demanding novel environment, stacked on top of each other. Every one of those factors is independently and robustly capable of triggering psychosis, mania, and dissociation in vulnerable people, on its own, with no meditation involved at all. The article even hands the reader this exact analogy (Inuit piblokto, a dissociative reaction linked to the sensory deprivation of Arctic winters) without following it to its conclusion. Nobody has run the retreat without the meditation, so nobody can say how much of the harm belongs to the sitting practice itself rather than the conditions it happens to be embedded in.

The second problem is the case definition. Buried in the foundational 2017 “Varieties of Contemplative Experience” study is this detail: 78 percent of the people counted as having an adverse effect reported “changes in motivation or goal.” But renunciation of ordinary striving is a stated aim of the contemplative traditions being studied, not a side effect of them. Counting the practice working as intended as harm, then folding that into the same aggregate figure as psychosis and suicidality, produces a single headline number that is not measuring one thing. In drug safety this is called a composite endpoint problem, and no regulator would accept “insomnia relief” and “myocardial infarction” pooled into one adverse-event rate for a sleeping pill. That is structurally what is happening here.

Third, there is no real denominator, and to its credit the article half admits this. The original study recruited people who already believed meditation had harmed them, which by design tells you nothing about prevalence in the general meditating population. Cheetah House’s own clients self-selected into a clinic built specifically to treat meditation-related distress. The later cross-sectional surveys (13 percent in one, a quarter in another) have no matched comparison group of non-meditators facing similar life stress, and no baseline rate for how often people report “unpleasant psychological experiences” after any demanding, introspective, identity-touching activity, whether that is psychotherapy, a strict fast, an ultramarathon, or a silent week with no meditation instruction whatsoever. Ask broadly enough about discomfort following any of those and you will find a nontrivial minority reporting it. Without the comparator, ten percent is not an effect size. It is an unadjusted background rate wearing an effect size’s clothes.

Fourth, once “meditation-induced psychosis” becomes a named, publicized clinical category with its own dedicated intake line, ascertainment bias runs in exactly the direction that inflates the finding. Clinicians and patients alike become more likely to pattern-match an ambiguous presentation onto the category once it exists and has a name. Pharmacovigilance has a well-documented version of this (sometimes called the Weber effect), where reporting of a suspected drug reaction spikes after media attention rather than after any real change in incidence. There is no reason contemplative-harm reporting would be exempt.

None of this erases the one finding in the piece that deserves real weight: more practice correlated with more reported difficulty. A genuine dose-response relationship is the strongest kind of evidence anyone in this article produces, and it is worth taking seriously precisely because it survives most of the objections above. But specificity is still poor (the retreat conditions alone would predict the same outcomes), the surveys share the same recruitment biases rather than replicating independently, and the underlying neuroscience (attentional overload, a prefrontal cortex “shutting off” emotional centers) is a plausible narrative applied after the fact, not a demonstrated mechanism.

So what should a practitioner actually take from this. Not that meditation is dangerous in any generic sense, and not that Britton is inventing a problem. Take instead the same lesson pharmacology insists on for any intervention: dose matters, context matters, and vulnerable people need more caution than the marketing around any practice usually allows for. An hour a day at home is not a ten-day silent retreat run on no sleep and no food. People with a personal or family history of psychosis, or anyone in the middle of an acute depressive episode, have specific reasons to be cautious with intensive, unsupervised concentration practice, and a teacher who tells someone mid-crisis to simply sit longer is not doing their job. That is a real and useful conclusion. “One in ten meditators are being harmed at a rate comparable to a common drug side effect” is not the conclusion the data support, and dressing an uncontrolled observational signal in that kind of precision does a disservice to a genuinely interesting question.

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