REWIND was built to answer the stopping question, and it did

The Journal has read all three of the relevant reports in full, and the most striking feature of the coverage they generated is how much of it treated the results as a scandal rather than as an answer. That a treatment for a chronic condition stops working when it is stopped is not a finding about the treatment. It is a finding about the condition, and it places these drugs in the same category as antihypertensives, statins and inhaled corticosteroids, none of which anybody expects to work after they are discontinued.

What a randomised withdrawal design does

A randomised withdrawal design begins with an open-label lead-in during which all participants receive the active drug and escalate to a target dose. Those who tolerate it and complete the lead-in are then randomised, usually two to one or one to one, to continue the drug or to receive matching placebo, and both arms are followed for a defined period with weight as the primary endpoint.

The design has two properties worth naming. Because randomisation occurs after the response, it isolates the effect of continuing from the effect of having lost weight, which a conventional parallel-group trial cannot do. And because the population has been selected for tolerating the drug, the withdrawal arm is not a general population — it is an enriched one, which makes the arm comparison internally valid and limits how far the absolute figures generalise.

Regulators favour the design for chronic-use products precisely because it answers the duration question. Its cost is ethical rather than statistical: participants who have achieved a substantial benefit are randomised to lose it, which is defensible only where the question is genuinely open and the follow-up is bounded. The Journal notes that all three withdrawal designs in this class published their regain data in full, which is more than can be said for several older obesity programmes.

The STEP 1 extension: two-thirds back within a year

The pivotal semaglutide obesity trial ran for sixty-eight weeks with a mean weight reduction of approximately 14.9 per cent on 2.4 mg weekly against 2.4 per cent on placebo.¹ An extension followed a subset of participants for a further fifty-two weeks after both the drug and the lifestyle intervention were withdrawn, which makes it an off-treatment observation rather than a randomised withdrawal.

By week 120 — a year after stopping — participants who had received semaglutide had regained approximately two-thirds of the weight they had lost, finishing on average around 5.6 per cent below their original baseline against approximately 0.1 per cent for the former placebo group.² Improvements in glycaemic parameters, blood pressure and lipids reverted broadly in step with the weight.

Two details are consistently dropped from summaries. The residual benefit was real: a mean 5.6 per cent reduction sustained a year after stopping is not nothing, and it is more than most non-pharmacological interventions achieve while they are still being delivered. And the lifestyle support was withdrawn at the same time as the drug, so the extension describes the removal of an entire intervention package rather than of a molecule.

STEP 4: the randomised switch to placebo

STEP 4 is the cleanest test of continuation in the semaglutide programme. All participants took semaglutide through a twenty-week escalation to 2.4 mg weekly, achieving a mean reduction of approximately 10.6 per cent. They were then randomised two to one to continue semaglutide or to switch to placebo for a further forty-eight weeks, with lifestyle support maintained in both arms.³

Those who continued lost a further 7.9 per cent, reaching roughly 17.4 per cent below their original baseline at week 68. Those switched to placebo regained approximately 6.9 per cent, ending near 5 per cent below baseline. The between-group difference of about fifteen percentage points is the effect of continuing treatment for a year, measured in a population that had already demonstrated a response.

The design detail that matters most is that lifestyle support continued in the placebo arm. This is not a comparison of drug against nothing; it is a comparison of drug plus support against support alone, in people who had lost weight on the drug. The regain observed is therefore what happens with the behavioural intervention still running, which makes it a more conservative estimate of the drug contribution rather than a less one.

SURMOUNT-4 and the steeper curve

SURMOUNT-4 applied the same architecture to tirzepatide with a longer lead-in. Participants escalated over thirty-six weeks of open-label treatment to their maximum tolerated dose of 10 or 15 mg weekly, achieving a mean reduction of approximately 20.9 per cent, and were then randomised one to one to continue or to switch to placebo for fifty-two weeks.⁴

Continuation produced a further mean reduction of about 5.5 per cent, for a total near 25.3 per cent at week 88. Withdrawal produced a mean regain of about 14 per cent of body weight, leaving that arm approximately 9.9 per cent below original baseline. The between-arm difference of roughly fifteen percentage points is similar in magnitude to STEP 4 despite the much larger initial loss.

The steeper regain in absolute terms is the expected consequence of a larger loss rather than evidence of anything peculiar to the agent. It is nonetheless the figure most often quoted without its denominator, and a fourteen-point regain from a twenty-one-point loss is a materially different statement from a fourteen-point regain from a ten-point loss. Both arms in this trial ended below where they began, and the arm that stopped ended roughly where the continued arm of the semaglutide programme did.

What the three designs agree on

The parent programmes establish the losses from which the withdrawal arms fall: approximately 14.9 per cent at sixty-eight weeks for semaglutide 2.4 mg in adults without diabetes, approximately 20.9 per cent at seventy-two weeks for tirzepatide 15 mg, and — the only continuous two-year comparator anybody has — approximately 15.2 per cent sustained at week 104 with treatment maintained throughout.⁵⁶

Read together, the withdrawal evidence supports four statements and does not support a fifth. Regain begins promptly after cessation, within weeks rather than months. It proceeds at a decelerating rate, with the steepest portion in the first three to six months. It does not, within twelve months of follow-up, return participants fully to their original baseline; residual reductions of roughly five to ten per cent persist at one year in all three datasets. And continued treatment maintains and usually extends the loss, with the extension diminishing as the plateau is approached.

The statement not supported is that the drugs cause weight regain, or that stopping leaves a person worse off than never having started. Nothing in these datasets shows overshoot above the original baseline at a group level. Every arm that stopped remained below where it began at the end of follow-up.

The Journal makes this point repeatedly because the contrary claim circulates widely and is often accompanied by a mechanistic story about metabolic damage. The withdrawal trials are the direct test of that claim and they do not support it. What they do support is the unremarkable proposition that a treatment for a chronic condition works while it is being taken.

What comes back, and in what proportion

The composition of regained weight is the thinnest part of this literature. None of the three withdrawal designs measured body composition after cessation. The concern most often voiced — that weight lost in a favourable fat-to-lean ratio returns in a less favourable one, so that repeated cycles progressively worsen composition — is physiologically plausible and, in this drug class, entirely unmeasured.

What exists comes from the dietary weight-cycling literature, where the picture is mixed rather than alarming: several studies find that regained weight is disproportionately fat, several find no such asymmetry, and the meta-analytic position is that weight cycling has not been shown to produce a cumulative composition penalty in humans. The Journal regards that as genuinely unresolved rather than as reassurance.

One dataset does bear on it indirectly. In the maintenance trial that randomised exercise, a GLP-1 receptor agonist, both or neither after a diet-induced loss, composition was tracked throughout, and the arms that trained retained a more favourable composition through the maintenance year.⁷ That is a statement about maintenance rather than about regain after withdrawal, and it is the closest thing to relevant evidence anybody has.

When the indication is not weight

The withdrawal question changes shape when the drug was prescribed for something other than weight. In the cardiovascular outcome trial of semaglutide in overweight and obesity without diabetes, the reduction in major adverse cardiovascular events emerged over years of continued treatment, and the trial provides no information about what happens to that benefit on cessation.⁸ The same applies to the renal outcome data in chronic kidney disease with type 2 diabetes, where the effect on kidney disease progression was measured over a median of several years of treatment.⁹

There is no reason to expect an outcome benefit that accrues over years to persist after the exposure ends, and no trial has tested it. For a person taking the drug for glycaemic control, stopping has an immediate and measurable consequence in HbA1c over the following three months. For a person taking it for cardiovascular or renal risk, stopping has no measurable short-term consequence at all, which makes the decision harder rather than easier.

This is the situation in which the Journal thinks the withdrawal-trial coverage has done the most damage. Framing discontinuation as a weight question invites a person taking the drug for kidney disease to reason about it in the wrong currency entirely.

The lifestyle intervention is a confound in both directions

Every trial in this class delivers a behavioural intervention alongside the drug: energy-restriction targets, activity targets, and regular contact with a study team. That contact is itself an intervention of measurable effect, which is why placebo arms in these programmes lose two to three per cent of body weight rather than nothing. Where the behavioural component was deliberately intensified, the placebo arm lost around 5.7 per cent over sixty-eight weeks, which is a useful upper bound on what contact and counselling alone achieved in these populations.¹⁰

It matters for the withdrawal question in a way that is usually elided. The semaglutide off-treatment extension withdrew the drug and the lifestyle support together, so its regain figure describes the removal of a package.² The STEP 4 and SURMOUNT-4 withdrawal arms kept the lifestyle component running, so their regain figures describe the removal of a molecule with support maintained.³⁴ Those are different experiments and the second is the more conservative.

Anybody comparing regain figures across the three should therefore expect the extension to look worse, and it does. The Journal states which withdrawal design a figure comes from every time it quotes one, because the alternative is pooling two different experiments into a single number that describes neither. The same caution applies to the frequent comparison with dietary weight-loss regain, where the behavioural intervention is the whole of the treatment.

What would settle the maintenance question

The Journal’s position is that three trials would resolve almost everything currently argued about in this area, and that all three are straightforward. The first is a dose-reduction design: after a lead-in to target, randomise to full dose, one step down, two steps down, or placebo, and follow for a year with weight as the primary endpoint. It would establish the shape of the descending dose-response curve and would cost a fraction of a pivotal programme.

The second is an interval design: after a lead-in, randomise to weekly, fortnightly and three-weekly administration at the same nominal dose. It would answer the intermittent-schedule question directly and would settle whether the exposure pattern matters independently of average exposure.

The third is a taper design: randomise abrupt cessation against a stepped reduction over twelve weeks, with appetite, eating behaviour and weight measured for a year afterwards. It would test the only argument for tapering that is worth testing.

None of the three is under way as far as the Journal can establish. Readers who know otherwise should write to letters@compoundjournal.com; a registered protocol for any of them would be news in this department.

How the Journal reports a regain figure

Four things accompany every regain number in these pages. Which withdrawal design it comes from, because an off-treatment extension and a randomised placebo switch are different experiments. Whether the lifestyle intervention continued in the arm being described. What the denominator is — regain as a percentage of body weight, as a percentage of the weight lost, or as a final position relative to original baseline, three quantities that are routinely quoted interchangeably. And the follow-up duration, because the regain curve decelerates and a figure at six months is not a figure at a year.

The third of those is where most of the misreporting happens. A statement that participants regained two-thirds is a proportion of loss; a statement that they regained eleven per cent is a proportion of body weight; a statement that they finished 5.6 per cent below baseline is a final position. All three can describe the same arm and they are not interchangeable.

Where a source we are quoting has not stated its denominator, we say that rather than inferring it. Readers who find a regain figure in these pages without its design and its denominator have found an error, and the standards desk would like to hear about it at standards@compoundjournal.com.

What this piece is not

This is reporting on a body of trial evidence and it is not advice about whether or how to stop taking a medicine. The decision to discontinue an agent prescribed for glycaemic control, cardiovascular risk or kidney disease is materially different from the decision to discontinue one prescribed for weight, and in every case it belongs with a clinician who has seen the person and knows why the drug was started.

Two further notes. Compounds sold for research use only are not approved for human use in any jurisdiction, and nothing here should be read as guidance about using them or about stopping their use. And where this piece describes what clinicians report doing about maintenance dosing, that is description of practice and not a schedule anybody should adopt from a magazine.

The Journal takes correspondence on this subject at letters@compoundjournal.com and factual challenges at standards@compoundjournal.com. Letters describing a personal experience of stopping are read with attention and are published, where they are published, as accounts rather than as evidence — a distinction this department tries hard to preserve in both directions.

The correspondence this department receives on stopping divides almost evenly between people frightened by regain figures they have seen quoted without denominators and people who stopped without difficulty and cannot understand the alarm. Both groups are reading the same trials. The difference is almost entirely a matter of which number was quoted to them and whether anybody explained what it was a proportion of.