How to Read Gender Medicine Research

How to judge gender medicine studies: designs, GRADE, biased samples, lost follow-up, confounding, relative risk, outcome switching and spin, on both sides.

Overview

Almost every argument about gender medicine ends up as an argument about studies. One side cites a survey of 27,000 trans adults, the other a survey of 100 detransitioners. One side says "gender-affirming care reduces depression by 60%", the other says "suicide is 19 times higher after surgery". Both figures come from real, peer-reviewed papers. Neither means what it is usually taken to mean.

This page is a practical guide to reading that research. It explains the main study designs and how they rank, how evidence certainty is graded, and the recurring weaknesses that decide how much a study can tell you: convenience samples, loss to follow-up, short follow-up, confounding, outcome switching and press-release spin. Each point is illustrated with studies from the study archive, including well-known studies cited by both sides of the debate.

It is a companion to two existing pages. Evidence reviews covers what national reviews in England, Sweden, Finland, Norway, the US and elsewhere concluded. Suicide statistics explains how suicide figures are measured and misused. This page does not repeat their findings. It gives you the tools to check any study yourself, including ones that support what you already believe.

The most common problems in gender medicine research are not fraud or bad faith. They are design limits: no comparison group, samples recruited from one community, many participants lost before the end, and follow-up too short to see long-term outcomes such as regret. These limits apply to studies cited by trans advocates and by detransitioners alike, and a fair reader applies the same test to both.

Study designs and the evidence hierarchy

What each design can show

Research designs differ in one main way: how well they rule out explanations other than the treatment. The table below lists the designs that appear most often in this field, roughly from strongest to weakest for questions about whether a treatment works.

DesignWhat it doesWhat it can showExamples in gender medicine
Systematic review and meta-analysisSearches for every study on a question using pre-set rules, rates their quality, and (in a meta-analysis) combines their results statisticallyThe overall weight of evidence. Only as good as the studies it includesYork reviews for the Cass Review; Miroshnychenko et al. 2025; Baker et al. 2021
Randomised controlled trial (RCT)Assigns people to treatment or comparison by chanceCause and effect, because chance balances the groups on everything elseNone comparing blockers or hormones with no medical treatment. The only randomised trial in Baker's review compared testosterone doses
Prospective cohort with a comparison groupFollows treated and untreated people forward in timeAssociation. Can suggest cause if groups are similar and most people are followedTordoff et al. 2022
Register (registry) cohortUses national health records to follow whole populationsLarge numbers and long follow-up for deaths and hospital care. Weak on why people sought careDhejne et al. 2011; Bränström & Pachankis 2020
Before-and-after study (uncontrolled cohort)Measures the same treated people before and afterWhether people changed, but not whether the treatment caused the changede Vries et al. 2011; Carmichael et al. 2021; Olson-Kennedy et al. 2025
Cross-sectional surveyAsks a group of people questions at one point in timeHow common something is in that group, and associations. Usually cannot show order of events or causeUS Transgender Survey; Littman 2021; Vandenbussche 2022
Case series, case reports, qualitative interviewsDescribe individual patients or explore experiences in depthWhat can happen and how people experience it. Not how oftenLomax & Butler 2025
Expert opinion and consensusClinicians agree on recommendationsWhat experts currently believeWPATH SOC8 (voting rounds)

The hierarchy is a rule of thumb, not a law. A large, well-run register study can be more informative than a small, badly run trial. But the order reflects a real principle: the further down the table, the more ways there are for something other than the treatment to explain the result.

The missing comparison group

The single most common weakness in youth gender medicine studies is that there is no comparison group. Before-and-after studies measure treated young people at the start and again a year or two later. If they feel better, that might be the treatment. It might also be:

  • Growing up. Adolescent mood and behaviour change a lot between 12 and 18.
  • Regression to the mean. People often seek treatment when they feel worst, and many feel better later whatever is done.
  • Other care. Most treated young people also received therapy, family support or psychiatric medication.
  • Expectation. People who wanted a treatment, and fought to get it, may report feeling better on it.

The founding Dutch study shows how much weight rests on this design. De Vries and colleagues followed 70 carefully screened adolescents on puberty blockers. Mood and behaviour improved, but gender distress and body image, the problems the drugs were meant to ease, did not change. There was no comparison group, and every teen received psychological support at the same time (de Vries et al. 2011). It became a cornerstone of international guidelines even though England's evidence review rated it very low certainty.

The English replication found something different. The Tavistock's study of 44 children aged 12 to 15 found no change in psychological distress, self-harm or gender distress, and 98% went on to cross-sex hormones (Carmichael et al. 2021). Neither study can say what would have happened without the drugs.

GRADE and evidence certainty

Systematic reviews increasingly rate evidence using GRADE (Grading of Recommendations, Assessment, Development and Evaluation). The four certainty levels, from high to very low, are explained on the evidence reviews page. What follows is how a rating is reached, so you can see why most of this field ends up at the bottom.

Under GRADE, evidence from randomised trials starts at high certainty and evidence from observational studies starts at low. Reviewers then move it down for five kinds of problem (GRADE handbook):

  1. Risk of bias: flaws in how studies were run, such as no comparison group, missing data or unmeasured confounding.
  2. Inconsistency: studies point in different directions.
  3. Indirectness: the studied population or outcome differs from the one you care about, for example evidence from adults applied to teenagers, or from screened childhood-onset cases applied to today's mostly adolescent-onset referrals.
  4. Imprecision: too few people or events, giving wide confidence intervals (the range in which the true value plausibly lies).
  5. Publication bias: studies with favourable results are more likely to be published.

Evidence can also be moved up if an effect is very large, if there is a dose-response pattern, or if all plausible biases would work against the effect seen.

Youth gender medicine studies typically start low (all are observational) and lose more for bias, indirectness and imprecision. That is why the McMaster reviews rated nearly every mental health outcome for puberty blockers and hormones as very low certainty (Miroshnychenko et al. 2025a; 2025b). In some of their pooled analyses, results came from as few as 6 to 26 people.

Two points are often missed:

  • Very low certainty is not proof of no effect. It means the true effect could be substantially different from the estimate, in either direction. A claim that "studies show blockers don't work" goes as far beyond the evidence as a claim that they do.
  • Not every review uses GRADE the same way. The York reviews behind the Cass Review rated individual studies with an adapted checklist, combined only moderate- and high-quality studies, and did not give a formal certainty rating for each outcome (Cass 2024). Critics argue this made benefits and harms harder to weigh. The McMaster reviews used standard GRADE and reached the same overall conclusion. When two methods agree, that is more reassuring than either alone.

Convenience samples and online surveys

What a convenience sample is

A convenience sample is a group recruited wherever researchers can find willing participants, often through online networks, rather than at random from the whole population. It can tell you a lot about the people who took part. It cannot tell you how common anything is in the wider population, because people who take part differ from those who don't.

The key question to ask of any survey is who was invited, who was able to answer, and who was screened out. This applies with full force to surveys on both sides.

The US Transgender Survey

The 2015 US Transgender Survey (USTS) had 27,715 respondents, the largest survey of trans-identified people at the time (James et al. 2016). It was recruited through more than 400 trans community and advocacy groups, and its respondents were younger, better educated and more often white than people in random samples (Turban et al. 2021). Its sheer size is often mistaken for representativeness, but a large convenience sample is still a convenience sample.

Two widely cited papers drew on it:

  • Detransition. Turban and colleagues found that 13% of respondents who had transitioned had "ever detransitioned", mostly citing outside pressures such as family or stigma (Turban et al. 2021). But the survey only included people who currently identified as trans. Anyone who had detransitioned and no longer identified as trans was, by design, not there. The study can describe people who paused and resumed transition. It cannot describe detransitioners as this site uses the term, and it cannot give a detransition rate.
  • Puberty blockers and suicidal thoughts. Another analysis reported that trans adults who had received puberty blockers had lower odds of lifetime suicidal ideation (adjusted odds ratio 0.3) than those who had wanted but not received them (Turban et al. 2020). Only 89 respondents had received blockers. "Lifetime" ideation includes thoughts before any treatment, the data relied on adults' recall, and young people who got blockers in the US at that time likely differed in family support and access to care.

Many detransitioners describe the same screening problem from the other side:

I was once invited to participate in a survey about detransition. I made it through all the pre-qualification questions until it asked if I had returned to my birth sex. I said yes, and the system told me "Thanks anyway." —OtterWithKids, detrans male

The 2022 survey grew to over 92,000 respondents and its authors describe it as a non-probability sample (Herman et al. 2026). Its suicide figures, and why they cannot be read as death rates, are covered on the suicide statistics page.

Detransitioner surveys

Surveys of detransitioners are also convenience samples, recruited from the communities most likely to hold strong views about transition. Their limits are real and should be stated as plainly as the USTS's.

  • Littman 2018 (parents). This survey of 256 parents, which introduced the term "rapid-onset gender dysphoria", was recruited through three websites that the paper itself describes as cautious or critical about youth transition. To take part, parents had to report a sudden onset, so the sample was selected for the pattern it described. No young people or clinicians were asked, and 76.5% of parents believed their child was wrong to think they were transgender (Littman 2018). It can show that such cases exist and need study. It cannot show how common they are. The wider debate is on the rapid-onset gender dysphoria page.
  • Littman 2021 (100 detransitioners). Recruited mostly through detransition blogs, forums and social media, 90% white and mostly American. Nothing could be checked against records, and there was no comparison group of people who continued transition (Littman 2021).
  • Littman et al. 2024 (78 young adults). About 45% were recruited via r/detrans. People had to have stopped identifying as trans for at least six months, which excludes those who later retransitioned and may favour people who are doing well after detransition (Littman et al. 2024).
  • Vandenbussche 2022 (237 detransitioners). Recruited through detransitioner networks, including female-only groups; 92% were female, so males could not be analysed separately. Inclusion was broad: 31% had transitioned socially only (Vandenbussche 2022).

These surveys are valuable for what they show: reasons for detransition, unmet care needs, and the fact that only about a quarter of participants had told their clinicians (Littman 2021; Littman et al. 2024). They cannot tell you what share of all transitioners detransition, or what share of detransitioners feel as their respondents do.

Trans commenters often make a version of this criticism, focusing on who counts as a detransitioner:

I am not trying to ruffle any feathers, but imo a lot of this is because the definition of a 'detransitioner' is very broad. It could mean someone went by different pronouns online or it could mean they went for everything available to them. —bugatti420, trans man (FTM)

That point has substance: Vandenbussche's sample did mix social-only and medical detransition. The same reasoning cuts the other way too, because Turban's broad definition of "detransition" included briefly presenting as one's birth sex when visiting family. Some detransitioners apply the same scepticism to studies that favour their own view:

I don't think this is generalisable - not because of the sample size, but because of sample bias. The participants are a particular subgroup of detransitioners who are more likely to seek out participation in such studies. —Upset-Elderberry3723, desisted male

Clinic samples are selected too

Clinic and research cohorts are not free of selection. Families in the US TransYouth Project, which reported that 94% of socially transitioned children still identified as trans five years later, signed up through community networks; 66% earned over $75,000 a year and 68% were white (Olson et al. 2022). The early Dutch cohort was screened for mental stability and supportive families (de Vries et al. 2011). Results from these groups may not apply to the young people now referred to gender services, many of whom are adolescent females with co-occurring mental health problems.

Loss to follow-up and short follow-up

Who disappears from the data

Loss to follow-up means participants drop out of a study before it ends, or patients stop attending a clinic so their outcome is never recorded. It matters most when the people who leave differ from those who stay, which is almost always the case.

Examples from both directions:

  • Tordoff et al. 2022. Of 104 young people at a Seattle gender clinic, 65 completed the 12-month survey. By study end, 69 had received blockers or hormones and 35 had not. According to the paper's supplementary tables, as analysed by journalist Jesse Singal, 28 of the 35 untreated youths left the study, against 12 of the 69 treated, so the untreated comparison at 12 months rested on seven people (Tordoff et al. 2022; Singal 2022).
  • Olson-Kennedy et al. 2025. In this US study of 94 young people starting puberty blockers, 37% had no depression data at two years, and the statistical method used to fill the gaps assumes dropouts are random (Olson-Kennedy et al. 2025).
  • Carmichael et al. 2021. Of 44 children, data were available for 24 at two years and 14 at three, and the children's own questionnaires for 15 and 6 (Carmichael et al. 2021).
  • Wiepjes et al. 2018. The Amsterdam study that is the main source of the "under 1% regret" figure reported that 36% of patients stopped coming to the clinic after several years of treatment (Wiepjes et al. 2018).
  • de Vries et al. 2014. The Dutch follow-up into young adulthood reported that gender dysphoria had resolved and wellbeing matched peers. Of the original 70, 55 took part and 40 had complete data. One participant who died of necrotising fasciitis (a severe infection) after vaginoplasty was among those not included in the outcome data (de Vries et al. 2014).

In detransition research, loss to follow-up is not random noise. People who stop treatment are the people most likely to stop attending. Only 24% of Littman's detransitioners had told their clinicians (Littman 2021), and a UK adult clinic found 22% of discharged patients had simply stopped attending (Hall et al. 2021). Clinic-based detransition counts will therefore tend to be too low. Detransitioners often describe this directly:

I also signed papers that mean I'm included in some study but I'm pretty sure they don't put me in as a detrans person now. So I'm unsure how real these studies can be. So many detrans people just ghost their clinics because they have trauma associated with them and don't want to go back to them. —ClydeFallon, detrans female

The evidence reviews page covers how national reviews dealt with this gap, including the Cass Review's blocked data linkage study.

Follow-up that ends too soon

Short follow-up is a separate problem. Even if nobody drops out, a study cannot record events that happen after it ends.

In the Amsterdam data, regret appeared on average about 11 years after starting hormones, with a range of about 4 to 22 years (Wiepjes et al. 2018). Swedish data put typical times to regret at about 7.5 to 8 years (Cohn 2023). Yet most studies of youth outcomes follow people for one to three years. A Dutch study reporting that 98% of young people who took blockers then hormones were still on hormones measured them at a typical age of about 19 or 20 (van der Loos et al. 2022). A regret review combining 27 studies found follow-up ranging from under 1 year to 9 years, and none met a standard of following at least 85% of patients for 8 years or more (Bustos et al. 2021; Cohn 2023).

Short follow-up can also make treatments look better than they are if early effects fade. Some detransitioners describe an initial lift that they later reinterpreted:

For example, Testosterone does have a moderate anti-depressant effect even in men who take it for low testosterone levels. It can decrease fatigue. So a woman who is depressed, fatigued, may feel initially "better" but that doesn't mean "this is proof my brain is a man brain" cause any one taking testosterone replacement will notice some effects on mood. —throwawayeffoff, detrans female

Short follow-up cuts both ways too. Studies reporting high rates of stopping hormones, such as the roughly 30% in US military records within four years, were also short and uneven, and could not say why people stopped (Roberts et al. 2022).

Prescriptions are not outcomes

Several studies use whether people keep filling hormone prescriptions as a stand-in for satisfaction or regret. The Dutch figure of 98% continuing (van der Loos et al. 2022) and the US military figure of about 30% stopping (Roberts et al. 2022) both measure refills, not wellbeing.

The measure misleads in both directions. People who have had their ovaries or testes removed need hormones for life for bone health, so a continuing prescription does not show they still support their transition. People who stop may be detransitioning, but may also have moved, lost insurance or switched to an unrecorded source. Neither figure is a detransition rate.

Confounding

What confounding is

Confounding happens when a third factor influences both who gets a treatment and how they do afterwards, making the treatment look more or less effective than it is. Gender medicine has several strong confounders:

  • Concurrent psychiatric care. Young people on blockers or hormones are usually also receiving therapy, antidepressants or other support. All 70 teens in the first Dutch study received ongoing psychological support (de Vries et al. 2011); regular psychological support was required in the Tavistock study (Carmichael et al. 2021); and in the Johns Hopkins review of hormones, counselling was often required alongside treatment (Baker et al. 2021). If people improve, the drug's share of the credit cannot be separated out.
  • Pre-existing mental illness. People with severe psychiatric problems may be less likely to be approved for treatment, so treated groups start healthier. People referred to gender services carry much more psychiatric illness than the general population, which affects any comparison with it. How adjusting for this changes suicide figures is covered on the suicide statistics page.
  • Family support and income. Families who support and can access treatment differ in many ways from those who don't.

Bränström 2019 and its correction

The Swedish study by Bränström and Pachankis, published in 2019 in the American Journal of Psychiatry, is the clearest case of confounding and correction in this field. Using Sweden's national registers, it found that among 2,679 people diagnosed with gender incongruence, each year since surgery was linked to 8% lower odds of being treated for depression or anxiety in 2015. It presented this as evidence of a long-term benefit of surgery (Bränström & Pachankis 2020).

Seven published letters pointed out problems. The study measured treatment only in one year, comparing different people at different times since surgery, rather than following the same people. People with better mental health may be approved for surgery sooner. People who had died, including by suicide, were left out. When the authors compared those who had surgery with those who had not, surgery showed no advantage on any measure, and the journal's August 2020 correction said the original conclusion was too strong (Bränström & Pachankis 2020; SEGM 2020).

The correction itself has limits. The surgery-versus-no-surgery comparison was added after the fact, and the no-surgery group included many people who never wanted surgery. So "no difference" is not strong proof that surgery has no benefit either (SEGM 2020). The fair reading is that this study, in either version, cannot show whether surgery improves mental health.

Dhejne 2011: one study, two misreadings

The Swedish surgery cohort by Dhejne and colleagues is cited by both sides, often wrongly. It followed all 324 people who had sex reassignment surgery in Sweden from 1973 to 2003 and compared them with matched people from the general population. Deaths were about three times higher and suicides about 19 times higher (Dhejne et al. 2011).

  • The misreading against transition: that surgery causes suicide. The comparison was with the general public, not with people with gender dysphoria who did not have surgery, so the study cannot say whether surgery made things better or worse. The authors say so themselves.
  • The misreading for transition: that the later cohort (1989–2003) shows the problem was fixed. For that group, the extra deaths and suicide attempts could have been chance, but with so few events that is a lack of evidence either way, and psychiatric hospital stays were still about 2.5 times higher.

The study adjusted only for earlier psychiatric hospital stays and immigrant status, so outpatient mental illness, substance use and poverty were not taken into account. What it does show is that serious psychiatric and mortality risks persisted after surgery and that long-term care is needed.

Detransitioners on r/detrans sometimes apply this reasoning to studies that seem to support their own view. Commenting on a study reporting more depression after surgery, one wrote:

Looking at the methodology, that's not really what they found. They found that those who had surgery had double the rates of depression of those who didn't have it. But there is no data on them before surgery. They could have been more depressed from before surgery in the first place —recursive-regret, detrans male

Relative risk vs absolute risk

A relative figure says how many times more (or less) often something happens in one group than another: "six times as likely", "60% lower odds". An absolute figure says how often it happens at all: "8 in 1,000". Headlines favour relative figures because they are larger. Decisions need both. The suicide statistics page works through Dhejne's suicide figure in detail; three other examples follow.

  • Bränström. Diagnosed people were 6.8 times as likely as the general population to be hospitalised after a suicide attempt in 2015. In absolute terms, that was 0.8% against 0.1%, resting on 22 people (Bränström & Pachankis 2020).
  • Straub et al. 2024. US health records showed recorded suicide attempts about 12 times higher among adults with past gender surgery than among other emergency patients (3.47% vs 0.29%). Against a matched group of sterilisation patients, the figure fell to about 5 times. The headline 12-times figure was the unmatched one (Straub et al. 2024). The size of a relative risk depends heavily on who you compare with.
  • Miroshnychenko 2025b. In one records study, 3.9% of females on testosterone (151 of 3,875) had a heart or blood vessel event over 7 months to 9 years. That is an absolute frequency with no comparison group: it shows how often events happened, not whether testosterone caused them (Miroshnychenko et al. 2025b).

Odds are not risks

Many studies report odds ratios rather than risk ratios. When an outcome is common, as depression is in gender clinic samples, an odds ratio exaggerates the difference compared with a risk ratio. Tordoff and colleagues reported an adjusted odds ratio of 0.40 for moderate-to-severe depression in treated versus untreated youth (Tordoff et al. 2022). That became "60% lower odds of depression" in the university's news release and "60% reduction in depression" in some coverage. Those are different claims. The second sounds like 60% of depressed young people got better. In the treated group, moderate-to-severe depression went from about 59% at the start to about 56% at 12 months (Singal 2022). The difference between groups came mainly from comparison with a shrinking untreated group, not from improvement among the treated.

Outcome switching

What it is

Outcome switching means reporting different outcomes from the ones a study planned to measure, or changing how an outcome is measured partway through, without explaining why. It matters because if researchers measure many things and report the ones that turned out well (or badly), chance findings look like real effects. The safeguard is pre-registration: publishing a study's planned outcomes before results are known, then checking the paper against that plan.

Examples

  • Olson-Kennedy et al. 2025. This NIH-funded study's progress report expected improvements in depression, anxiety, trauma symptoms, self-harm, suicidal thoughts, body image and quality of life. None of the reported mental health measures improved. Critics noted that the preprint reported different measures from the planned ones on gender distress, anxiety, trauma and body image without explanation, and that gender distress itself was not reported. The authors concluded that blockers "likely" prevent deterioration, which the study had no comparison group to test (Olson-Kennedy et al. 2025). The delay in publishing is covered on the Olson-Kennedy NIH study page.
  • de Vries et al. 2014. The gender dysphoria questionnaire used (the Utrecht Gender Dysphoria Scale) has separate male and female versions with mostly different items. Participants filled in the version for their birth sex before and during treatment, and the version for their identified gender after surgery (de Vries et al. 2014). A change in score therefore partly reflects a change of questionnaire, which weakens the study's headline finding that gender dysphoria had resolved.
  • Bränström and Pachankis. The original paper emphasised an analysis of hormones and of time since surgery. When the hormone analysis showed nothing, the surgery analysis carried the conclusion; when a new comparison was run, that conclusion was corrected (Bränström & Pachankis 2020). Post-hoc analyses, decided after seeing the data, should be read as hypotheses in either direction.

A related problem is reliance on proxy outcomes: measuring something easy (prescription refills, clinic visits, treatment use) instead of what matters (wellbeing, regret, function). Proxies are not worthless, but a study that measured a proxy should not be described as having measured the real thing.

Systematic reviews vs clinical guidelines

Different jobs

A systematic review asks what the evidence shows. A clinical guideline tells clinicians what to do. Good guidelines are built on systematic reviews, rate the certainty of evidence behind each recommendation, manage conflicts of interest, and are checked by people outside the group that wrote them. Guideline quality is usually assessed with the AGREE II checklist, which scores how rigorously and independently a guideline was developed.

When the University of York appraised 23 youth gender guidelines for the Cass Review, most scored poorly for rigour and independence. WPATH's 2022 guideline scored 35% for rigour and the Endocrine Society's 2017 guideline 42%; only Sweden's and Finland's scored above 50% and were recommended by all three raters (Taylor et al. 2024). WPATH and Endocrine Society guidance formed the basis of most other national guidance, and the two groups are linked through joint sponsorship, so guidelines partly vouched for each other.

Two specific problems stand out:

  • Strong advice on weak evidence. The Endocrine Society guideline rates the evidence behind every adolescent recommendation as low or very low quality, yet words some as strong recommendations, such as puberty blockers at the first signs of puberty. Its two commissioned evidence reviews covered heart, cholesterol and bone effects, not whether treatment eases distress (Hembree et al. 2017).
  • No evidence rating at all. WPATH SOC8's recommendations were agreed by voting rounds and labelled only "recommend" or "suggest", without saying how strong the evidence was. Its adolescent chapter states that a systematic review of outcomes "is not possible" (Coleman et al. 2022). The story of the evidence reviews WPATH commissioned and then restricted is on the WPATH files page; the Endocrine Society's links to WPATH are on the Endocrine Society page.

The fact that many medical associations endorse a guideline does not make it a systematic review. Endorsement measures agreement among professionals, not the strength of the underlying studies.

Reviews have weaknesses too

Systematic reviews are not automatically neutral. Their conclusions depend on search dates, inclusion rules and quality ratings, and both sides have reviews with declared interests:

  • The Johns Hopkins review of hormones was funded by WPATH. It linked hormones to better mood and quality of life, but rated all its evidence low quality and found nothing firm on suicide. Its closing statement that hormones are "essential" goes beyond its own ratings (Baker et al. 2021).
  • The McMaster reviews were commissioned and funded by the Society for Evidence-Based Gender Medicine (SEGM), a group that argues for caution, and SEGM members helped shape the question (Miroshnychenko et al. 2025a; 2025b).
  • The 2026 AGREE II appraisal of WPATH SOC8, which rated it low on rigour and independence, was also SEGM-funded, and raters had to agree to an attitude screening statement (Zhang et al. 2026).
  • The York reviews were rated at high risk of bias by Noone and colleagues, a critique the Cass team and others dispute; the US HHS review was ordered by an executive order and its authors were at first unnamed (HHS 2025). Both debates are covered on the evidence reviews page.

Funding does not make a review wrong. It is a reason to check the methods. Here the reviews' bottom lines are strikingly similar: Baker (WPATH-funded) and Miroshnychenko (SEGM-funded) both rated the mental health evidence as low or very low certainty. Where opposing funders reach the same rating, that rating is probably sound. Where they differ is in what they think should follow from it.

Press-release spin

How spin happens

Most people never read a study. They read a university news release, a headline or a social media post. Spin is reporting that makes a study look stronger, more causal or more relevant than its own results support. It often starts with the authors or their institution, not with journalists.

Examples from both directions

  • Tordoff et al. 2022. The University of Washington's news release reported "60% lower odds of depression" among treated youth, and the version emailed to journalists was headlined "Gender-affirming care dramatically reduces depression for transgender teens" (Singal 2022). The study was observational, the paper's authors stated that causal claims cannot be made, and the treated group did not significantly improve. The newsroom page later carried an editor's note saying its language had been revised to match the study more closely (UW Newsroom).
  • Turban et al. 2020. Coverage of the USTS blocker analysis ran headlines such as "Puberty blockers linked to lower suicide risk" (NBC News). The study measured lifetime suicidal thoughts in a convenience sample, not suicide risk, and rested on 89 people who had received blockers (Turban et al. 2020).
  • Bränström and Pachankis 2019. The original "reduction in mental health treatment" finding was widely reported. The 2020 correction received far less attention, and the uncorrected conclusion is still cited as evidence that surgery improves mental health (Bränström & Pachankis 2020).
  • Littman 2018. Brown University promoted the parent survey with a news release, then withdrew it five days later after the journal announced a post-publication review (Brown Daily Herald). The corrected paper, republished in 2019, kept its results but rewrote its framing to stress that rapid-onset gender dysphoria is not a formal diagnosis (Littman 2018). Supporters saw the withdrawal as giving in to activists. Critics pointed to the paper's sampling and design. Both can be true: the institution's handling was unusual, and the paper's limits were real.
  • Straub et al. 2024. This US records study originally described surgery itself as linked to higher suicide-attempt risk. In June 2024 the journal's editors corrected its summary and conclusions to say instead that patients who have had surgery are at higher risk (Straub et al. 2024). The study compared surgery patients with non-trans patients, so it could not show what surgery caused.

Reading past the headline

When you meet a striking claim about a study, look for:

  • Causal verbs ("reduces", "causes", "prevents", "saves lives") attached to observational studies. The study's own limitations section usually says it cannot show cause.
  • Relative figures without absolute ones, and odds ratios presented as percentage reductions.
  • Which comparison is reported. A treated-versus-untreated difference is not the same as treated people improving.
  • Corrections and later letters. Search the journal page for corrections, comments and replies before quoting a paper.
  • Who is promoting it. Universities, advocacy groups and campaigners on both sides have an interest in favourable coverage.

How to read a study: a checklist

Before relying on a study, from any side, ask:

  1. What design is it? Is there a comparison group? Was anyone randomised? A before-and-after study cannot show cause.
  2. Who was in the sample, and how were they found? A clinic, a community network, an advocacy website, a national register? Who was screened out?
  3. How many people were followed to the end? If more than about a fifth were lost, ask who left and why.
  4. How long was follow-up? Regret and detransition often take years to appear. One or two years cannot measure them.
  5. What else was happening? Therapy, medication, family support, growing up. Were these measured or adjusted for?
  6. Which outcome, and was it planned? Is the reported outcome the one that matters, or a proxy such as refills or clinic visits? Does it match the study's registration or stated aims?
  7. Relative or absolute? How many events does the headline figure rest on? How wide is the confidence interval?
  8. Has it been corrected or criticised? Check the journal page for corrections, letters and replies.
  9. What do systematic reviews say? A single study rarely settles anything. See how it was rated in reviews such as York, McMaster or NICE.
  10. Would I accept this design if the result went the other way? This is the hardest question and the most useful one.

What this means

The research on gender medicine is not worthless, but most of it can answer narrower questions than the ones it is used to settle. Surveys can describe the people who answered them. Before-and-after studies can show whether treated people changed. Register studies can show whether risks persist after treatment. Very few studies can show whether a treatment caused an outcome, and almost none followed people long enough, or completely enough, to measure regret and detransition.

For detransitioners, that gap is personal. Clinics and surveys built around people who continue transition tend not to see people who stop, which is why statements that detransition is rare rest on weak foundations. The same standards also apply to the surveys detransitioners rely on. Littman's and Vandenbussche's work documents real experiences and needs, but it cannot give rates. Holding both kinds of study to the same test is the most convincing way to show that the evidence is uncertain. Peer-reviewed studies on these questions are collected in the study archive.

References
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