The evidence library

Caveat on this rating: With 34 participants the study is underpowered to detect small true effects, and the authors' own Bayesian analysis in the successfully blinded subgroup was inconclusive rather than clearly negative.

Caveat on this rating: The meta-analytic estimates rest on very little randomised data — two parallel RCTs (three comparisons, n=117) for efficacy and two RCTs (n=109) for adverse events — so the confidence intervals are wide and the review is better read as demonstrating absence of evidence than proving absence of effect. Several authors are affiliated with psychedelic research centres and one is chief medical officer of a psychedelics company (disclosed), so the null result is not coming from sceptics.

Caveat on this rating: Participants sourced and weighed their own material, so actual doses were unverified, and the sample was self-selected enthusiasts rather than people with a diagnosed condition. The authors are based at Imperial College's Centre for Psychedelic Research with a co-author from the Beckley Foundation, both proponents of psychedelic research — which cuts against, not toward, a bias explanation for this null result.

Caveat on this rating: Uncontrolled and unblinded: participants knew they were dosing, sourced their own substances, and were self-selected enthusiasts, so nothing here can separate drug effect from expectation. The authors say as much and explicitly call for dose- controlled research.

Caveat on this rating: Open-label by necessity (neither ketamine nor ECT can be masked), so subjective outcomes may favor the treatment patients preferred; population excluded psychotic depression, where ECT performs best.

Caveat on this rating: This umbrella review's STRONG tier reflects its independent, systematic method — its actual conclusion is that the underlying MDMA evidence is weak. Read the tier as confidence in the review, not in MDMA.

Caveat on this rating: The declarations of interest read literally: "KH has previously acted as a temporary consultant for Pfizer (manufacturers of sildenafil). MT has been paid to lecture and received travel expenses from Bristol-Myers Squibb (manufacturers of buspirone) and Otsuka; his spouse is an employee of GlaxoSmithKline (manufacturers of bupropion)." Two of the six authors therefore have financial ties to the makers of the two drugs the review endorses, which is why independence is scored false despite the funding being public. The reviewers also warn that partial reporting of subscale results in the source trials could bias the effect estimates upward.

Caveat on this rating: A regulatory label change is a precautionary act on a safety signal, not proof of incidence, causation, or permanence. The evidence base the PRAC weighed was EudraVigilance reports, literature, social media, and manufacturer reviews. Clomipramine and vortioxetine were part of the same signal assessment but were explicitly not covered by the labelling recommendation. US FDA labelling does not carry equivalent wording.

Caveat on this rating: The authors state that including open-label studies and pooling across different sexual-function scales "could reduce the significance of our findings," so the 25.8-80.3% band is wide partly because the source studies were not uniform. No funding statement or conflict-of-interest disclosure was accessible for this paper.

Caveat on this rating: The high trust score reflects the review's method, funding, and journal, not the strength of the underlying trials: 398 men across 11 studies, several from the 1970s and 1980s, with waitlist controls and confidence intervals touching 1.0. The single trial claiming group therapy outperformed sildenafil alone (WMD -12.40 on the IIEF) had 20 participants and was run by one of the review's own authors, which is a direct conflict on the review's most eye-catching result.

Caveat on this rating: The high trust score reflects the quality of this meta-analysis as a piece of evidence synthesis, not the strength of the effect it found. The pooled benefit rests on a subjective, dichotomised outcome in six trials with demonstrated publication bias, and the authors' own conclusion is the hedged "valerian might improve sleep quality," followed by a call for better studies. Twenty years on, those studies have largely not materialised.

Caveat on this rating: This review reaches the opposite conclusion to Bent 2006 from overlapping trials, and the difference is instructive: Taibi weighted trial quality and recency, and found that the better and newer the study, the smaller the effect. That pattern is the signature of a treatment whose apparent benefit comes from weak methods.

Caveat on this rating: Dated: the search closed 31 December 2011 and the review has not been updated, so it predates the trauma-focused work of the last decade. Its conclusion applies to brief generic counselling as trialled up to 2011 and should not be read as evidence against structured psychological treatment for post-loss PTSD, depression, or complicated grief.

Caveat on this rating: These are screening-instrument prevalences drawn largely from cross-sectional studies with substantial heterogeneity, so they measure symptom burden rather than diagnosed disorder, and the pooled percentages are sensitive to which scales and cut-offs the contributing studies used.

Caveat on this rating: The control groups were not uniform — they mixed live births, difficult live births, and non-pregnant community samples — and "perinatal loss" spans early miscarriage through stillbirth, so the pooled risk ratios blur real differences between very different experiences.

Caveat on this rating: Only psychiatric conditions severe enough to require hospitalisation were captured, so ordinary depression and anxiety treated in primary care are invisible here — the absolute risks are small and the affective-disorder result should not be read as evidence that unsuccessful treatment protects against depression.

Caveat on this rating: The pregnancy-rate result is the weak half of this paper: the pooled studies were heterogeneous, not all randomised, and the finding directly contradicts the larger and better-controlled Boivin 2011 BMJ meta-analysis showing distress does not affect cycle outcome. Read this study as evidence that psychological support reduces distress, not as evidence that it makes you pregnant.

Caveat on this rating: Attrition was substantial and grew over follow-up: 67% of the loss cohort completed the one-month questionnaire, 58% at three months, and 46% at nine months, so the later percentages rest on a shrinking and possibly non-representative subgroup. These are validated screening thresholds, not clinical diagnoses.

Caveat on this rating: The declarations of interest read literally: "KH has previously acted as a temporary consultant for Pfizer (manufacturers of sildenafil). MT has been paid to lecture and received travel expenses from Bristol-Myers Squibb (manufacturers of buspirone) and Otsuka; his spouse is an employee of GlaxoSmithKline (manufacturers of bupropion)." Two of the six authors therefore have financial ties to the makers of the two drugs the review endorses, which is why independence is scored false despite the funding being public. The reviewers also warn that partial reporting of subscale results in the source trials could bias the effect estimates upward.

Caveat on this rating: A regulatory label change is a precautionary act on a safety signal, not proof of incidence, causation, or permanence. The evidence base the PRAC weighed was EudraVigilance reports, literature, social media, and manufacturer reviews. Clomipramine and vortioxetine were part of the same signal assessment but were explicitly not covered by the labelling recommendation. US FDA labelling does not carry equivalent wording.

Caveat on this rating: The authors state that including open-label studies and pooling across different sexual-function scales "could reduce the significance of our findings," so the 25.8-80.3% band is wide partly because the source studies were not uniform. No funding statement or conflict-of-interest disclosure was accessible for this paper.

Caveat on this rating: The high trust score reflects the review's method, funding, and journal, not the strength of the underlying trials: 398 men across 11 studies, several from the 1970s and 1980s, with waitlist controls and confidence intervals touching 1.0. The single trial claiming group therapy outperformed sildenafil alone (WMD -12.40 on the IIEF) had 20 participants and was run by one of the review's own authors, which is a direct conflict on the review's most eye-catching result.

Caveat on this rating: Both arms improved similarly on the primary desire and arousal outcomes, so this trial does not show that mindfulness specifically works — it shows that eight weeks of structured group attention works. There was no no-treatment or waitlist arm, so regression to the mean and expectancy effects cannot be separated out. All 148 participants were cisgender women, and the authors note the need to diversify samples.

Caveat on this rating: Every pooled effect is against a waitlist, not an active or placebo control, so attention and expectancy are baked into the d = 0.58 figure. The search ends at 2009, predating the internet-delivered treatments that now dominate access. No total participant count is reported in the abstract, and the MEDLINE record lists the publication type "Research Support, Non-U.S. Gov't", indicating unnamed external support.

Caveat on this rating: Confidence in these numbers is low by the authors' own grading: 1 of 218 studies met the Cochrane criteria for low risk of bias, and CINeMA confidence was low for walking or jogging and very low for every other modality. The credible intervals for the five modalities overlap heavily, so the order above is not an established ranking and must not be read as one. The authors name the blinding problem themselves and call for future trials to blind participants and staff. Results did appear robust to publication bias. A correction was published (BMJ 2024;385:q1024) and is logged as unverified - the BMJ site refuses automated fetch - but nothing quoted here depends on a precise ranking. Effect sizes drawn from different literatures are not directly comparable, so this row deliberately does not set these numbers against antidepressant trial results.

Caveat on this rating: Observational. The correlations are small - 0.05 within persons, 0.08 between - and the authors state plainly that the practical effect is comparable to other everyday activities. People who move more may differ from people who move less in many ways this design cannot adjust away. The association runs in both directions, so "exercise lifts mood" is only half of what was measured: feeling better also predicts moving next. Considerable heterogeneity across individuals, only partly explained by sociodemographic moderators, means the average says little about any one person. The negative association with calmness is a real finding rather than a nuance to skip - activity tracked energetic arousal most strongly, so someone seeking calm may not find it here.

Caveat on this rating: Read this as absence of evidence, not evidence of absence - the body says so and the authors insist on it: "Contrary to expectations, nature-based interventions did not significantly outperform controls. However, this finding should be interpreted cautiously... studies in this group were small, at moderate-to-high risk of bias and conceptually diverse... This conceptual heterogeneity probably diluted the pooled effect estimate and limits interpretability." The abstract adds that the evidence "was limited by conceptual and methodological heterogeneity". Across the 183 trials risk of bias was "frequently moderate to high" and funnel asymmetry suggested publication bias, though sensitivity analyses held. Separately: the field's most-cited experiment, Bratman et al. 2015 PNAS (38 people), did not hold exercise constant - its nature route climbed 155m and its urban route 4m over the same 5.3km - and its brain finding has never been replicated.

Caveat on this rating: Strong design, still not causal, and the authors say so: "Despite the strong longitudinal design of our study, our risk estimates fundamentally only show correlations." Three limits they name: residential choice may be genetically confounded; unmeasured socioeconomic factors such as green-space quality and crime rates may remain; and NDVI "provides no information about the use of green space", so a child who only sees a park scores the same as one who plays in it daily. Our own added critique: there is no sibling or within-family analysis, so families who move somewhere greener are never compared with their own relatives. The 55% figure is the paper's "up to" across various disorders, not a single headline estimate.

Caveat on this rating: THE WIDELY-QUOTED VERSION OF THIS FINDING IS RETRACTED. Gu et al. 2019 (Br J Psychiatry 215(2):456-467, doi 10.1192/bjp.2018.295), the source of the much-repeated "19% higher depression risk per 10 ug/m3 PM2.5", was retracted - confirmed three ways on 2026-08-28: the PubMed record for PMID 30719959 is flagged RETRACTED ARTICLE; a separate retraction notice exists at PMID 32349797 / doi 10.1192/bjp.2020.87; and Crossref carries a type-retraction update-to relation from both the publisher and Retraction Watch. The published notice gives no reason we could read, so none is asserted here. Do not use the 19% figure; 1.102 [1.023-1.189] is the surviving estimate. It rests on five observational studies with, in the authors' words, "heterogeneous outcome definitions, exposure assessment, and residual confounding" - and poverty tracks bad air, so the inversion is about consistency, not about proof.

Caveat on this rating: The famous number is far weaker than its fame. The threshold was not pre-specified - it emerged from cutting the data into 60-minute blocks - and the curve is not a staircase: adjusted odds for good health run 1.59 [1.31-1.92] at 120-179 minutes, then FALL to 1.44 at 180-239, rise to 1.55, and fall again to 1.33 at 300+, with overlapping confidence intervals throughout. The data cannot distinguish two hours from five. The authors call the threshold and peak "more as a starting points for discussion and further investigation, than clearly established findings", report that nature time explained "approx. 1%" of variance, and state they "are unable to rule out the possibility that the association is, at least in part, due to healthier, happier people spending more time in nature."

Caveat on this rating: Contested, and symmetrically - both reviews have published critiques. Jauhar and Hayes argue Davies and Read inverted the evidence hierarchy, giving most weight to self-selected online surveys of people already experiencing withdrawal, without registering inclusion criteria in advance and excluding low-incidence studies after the fact; on that reading 56% is not a population rate and cannot be attributed to the drug's pharmacology. Henssler and colleagues' placebo-controlled estimate drew five published comment letters in Lancet Psychiatry and carries a published erratum; the authors themselves report substantial heterogeneity and note that residual or re-emerging illness has to be considered when reading their figure. What neither paper disputes is that withdrawal is real, that it was underestimated for years, and that abrupt discontinuation is the avoidable part. The headline percentage is unsettled in both directions.

Caveat on this rating: Population and construct, both load-bearing. These are 476 consecutive adults already referred to a national specialist autism service - people who had passed a referring clinician's judgement - so the predictive values are conditioned on that population and do not describe someone completing the questionnaire at home, where the proportion who are autistic is different and unknown. Sensitivity and specificity are properties of the instrument against a clinical reference standard, not verdicts on any individual score. The finding replicates in the wider literature rather than standing alone: Sizoo et al. 2015 concluded that none of the common self-report instruments has sufficient validity to predict an autism diagnosis in outpatient settings, and Wigham et al.'s 2019 systematic review found questionnaires perform markedly worse in referral streams than in samples of already-diagnosed people.

Caveat on this rating: Genre limits, from the studies' own limitation sections, and they bind the numbers next to them. This is top-video sampling of one hashtag at one time point: there is no denominator, and it does not reproduce what any individual's feed shows. "Accurate" is rater-defined and the definitions differ between studies, so these percentages are not comparable with accuracy figures published for other conditions or platforms. Cross-sectional content ratings measure content, not harm - no study here follows viewers to any outcome. Rater agreement is itself imperfect: in a study of the same genre, expert raters reached only moderate agreement. Nothing in this literature measures how many people self-identify because of social media, or whether any of them are right; both are separately verified absences. The later adult-diagnosis study is Brennan et al. 2025 (doi:10.1007/s10803-025-07123-0).

Caveat on this rating: Citation provenance, stated plainly. The anchor is Volkmar and McPartland's peer-reviewed history of the autism diagnostic concept, which is the house-citable route for the DSM-III-to-DSM-5 timeline because DSM edition text is paywalled and the publisher's history page does not resolve. The quoted sentence is not from that review: it is verbatim from the American Psychiatric Association's own "Highlights of Changes from DSM-IV-TR to DSM-5" document, held on file and verified 2026-08-26, and it is attributed to the manual in the body rather than to the review. Diagnostic criteria are a definition, not a finding, so nothing here is evidence about causes, prevalence or what any individual has. The manual also states that people with a well-established earlier diagnosis keep it under the new category, which is why the 2013 change did not remove existing diagnoses.

Caveat on this rating: Design limits, stated because they are the whole caveat. This is a cross-sectional online survey of a self-selected convenience sample recruited through a national campaign, not a random population sample - the same methodological objection Jauhar and Hayes raise against this research group's withdrawal-incidence work applies here, and it is why no national disclosure rate can be read off this row. Recall of a past consultation is also self-reported and unverified against the record: some prescribers may have mentioned withdrawal without the patient retaining it, which the study cannot separate from non-disclosure. What the figure supports is that the conversation is frequently absent or not memorable, not that a precise percentage of prescribers omit it. The 752-participant UK figure is Read, Gee, Diggle and Butler 2019 (doi:10.1016/j.addbeh.2018.08.021), carried in prose and subject to the same sampling limit.

Caveat on this rating: The denominator is the whole caveat and it is stated in the body rather than hidden here. The paper's own words: "We find one out of five STM articles suffering from reference rot" and "When only considering STM articles that contain references to web resources, this fraction increases to seven out of ten." One in five is of ALL science, technology and medicine articles in their corpus - not of all scholarship, and not of web references. Dropping the denominator is the standard misquotation of this paper and would make our own figure the kind of claim this trail exists to warn about. The figure describes scholarly citation, not government websites; it is offered as context for why link rot is normal, never as a measurement of federal pages.

Caveat on this rating: Two pairings are mandatory. On the evidence: educational meetings do change practice at moderate certainty (Cochrane CD003030.pub3, 2021, 215 studies), and physician-industry interaction is associated with prescribing (Brax, PLoS One 2017, pooled OR 2.52, 95% CI 1.82-3.50, moderate quality) - but only TWO studies in that review examined industry-funded CME specifically, one at high risk of bias, published 1988 and 1992, neither measuring clinical outcomes; the most-cited (Orlowski, Chest 1992) measured prescribing after physicians were flown on "all-expenses-paid trips to popular sunbelt vacation sites", conduct Standard 4.1.c now prohibits. On the accreditor: the review most often quoted for "no evidence of bias" (Cervero and Gaines 2014) was commissioned and funded by the ACCME, as its own cover states, and its finding is symmetrical - no data-based article supports OR refutes the assertion. The register is disclosure, never accusation: you should know who pays.

Caveat on this rating: The domain label is load-bearing, per the verified record: the primary-sourced pressure case here (the Annals advertising pullback) is a MEDICAL-JOURNAL case, not a consumer-news case, and the body says so in those words. No news-side adjudicated case exists; no "pharma funds X% of TV news" figure has any federal or peer-reviewed basis (the viral personalization is fact-checked False, PolitiFact 2023); and the pharma advertising-revenue-to-coverage causal literature is absent. The absences print as content - presenting the journal case as a news-media case would be the overreach this row exists to avoid.

Caveat on this rating: What is measured versus what is asserted, per the framing rule in the verified record: these three studies measure coverage QUALITY - benefits inflated, harms omitted, conflicts undisclosed - and none of them measures why. No robust empirical literature links pharmaceutical advertising revenue at an outlet to that outlet's drug-safety coverage decisions (the classic ad-revenue studies are about tobacco, a different industry, and are not presented as pharma evidence). This row presents the measured record and asserts no cause; "media buries drug harms because pharma pays them" publishes beyond the evidence and is on the do-not-publish list.

Caveat on this rating: The built-in rebuttal is structural, per the verified record: BOTH directions print together, always. A brand-name request quintupled prescribing where antidepressants are not clearly indicated (55% vs 10%) AND requests cut undertreatment of real depression (minimally acceptable care 56% without a request, 90-98% with one) - the authors' conclusion is that DTC advertising "may have competing effects on quality, potentially both averting underuse and promoting overuse". The chain also stays explicit: Kravitz tests requests, not ads; the ads-to-requests link is the review tier (Mintzes 2012). "Ads make doctors prescribe" is on the do-not-publish list.

Caveat on this rating: The mandatory rebuttal, printed beside the guidance annotation per the verified record: Rosenthal et al., NEJM 2002 (doi:10.1056/NEJMsa012075) - "the initial surge in direct-to-consumer advertising preceded the 1997 FDA guidelines... and thus the 1997 guidelines may not have been the most important reason" for the increase. The 1997 draft and 1999 final guidance are rendered as annotations ("the rules changed here"), never as the asserted cause of the spend curve - and DTC advertising was never illegal, so "legalized" appears nowhere in this row.