What I have: SURMOUNT-1 · headache · 5 mg.
I can parse the result. I am less sure what it licenses me to conclude.
I have deliberately not looked at anyone else’s interpretation yet.
Which parts of this are informative and which are decoration?
Only what the 5 mg arm reported, and the denominator is that arm rather than the trial. Adverse-event tables are published per arm, so the 5 mg incidence of headache has its own numerator and its own denominator, and pooling it with the other arms produces a figure that describes nobody. Two further deductions before you use it. Subtract the placebo arm — headache occurs in people who received nothing, and the difference is the part attributable to the drug. And check whether SURMOUNT-1 counted events or counted participants: one participant with six episodes is one row in a participant count and six in an event count, and the two get quoted interchangeably. Nothing here is medical advice.
The honest answer here is that the published evidence supports part of the claim and is silent on the rest, and it is worth being precise about which part is which.
Confidence intervals matter more than point estimates when two trials disagree. Two studies reporting fifteen and twenty per cent whose intervals overlap heavily have not disagreed about anything.
| Quantity | Value | Derivation |
|---|---|---|
| Control-arm event rate | 8.0 % | From the trial table, not the abstract |
| Hazard ratio | 0.80 | Reported |
| Treated event rate | 6.4 % | 8.0 × 0.80 |
| Absolute risk reduction | 1.6 pp | 8.0 − 6.4 |
| Number needed to treat | 63 | 1 ÷ 0.016 |
| Relative risk reduction | 20 % | 1 − 0.80 |
The last two rows describe the same finding. Only one of them is used in headlines.
To be exact about it, trial populations are selected. Exclusion criteria in this class routinely remove people with significant renal impairment, prior pancreatitis and unstable psychiatric illness, which is exactly the population the results are then quoted for.
The cardiovascular outcome programme in this class runs to several large randomised trials — LEADER for liraglutide, SUSTAIN-6 and SELECT for semaglutide, REWIND for dulaglutide — and they are the reason the class is discussed as more than a weight intervention.
The caveat is that trial evidence is about licensed product administered under supervision. None of it transfers automatically to research-grade material of unverified content.
When two sources disagree, the answer is almost always in the methods section of the one you have not read.
edited 22 Jul 2025 by Dr_Tomas_Kral — tightened the wording; no substantive change
Aggregated, published test results and vendor ratings built from submitted batches. Methodology stated, dataset browsable, no listing fees.
Browse resultsThe short version: the effect is real, the magnitude depends on the population, and the population is usually the part that gets dropped when a result is quoted second-hand.
Duration decides what can be seen. A 68-week trial can measure weight and glycaemia; it cannot measure anything whose event rate is one per cent per year without enrolling tens of thousands.
Placebo arms in this class are not nothing. Lifestyle-intervention placebo arms in the major obesity trials commonly lose two to three per cent of body weight, so an active-arm figure quoted without its comparator overstates the drug effect by roughly that much.
If a claim cannot be traced to a named trial with a named endpoint, treat it as a claim rather than as evidence.
Concretely, this is answerable from the published record, but only if you take the placebo arm seriously rather than reading the active arm alone.
A composite endpoint is only as informative as its least serious component. Where a cardiovascular composite combines death, infarction and stroke, ask which component moved, because they are not interchangeable outcomes.
More usefully, non-inferiority and superiority designs are not interchangeable. A non-inferiority result says the new agent is not meaningfully worse against a pre-specified margin — it does not say it is as good, and it certainly does not say it is better.
One qualification: absence of a signal in a trial of this size is not evidence of absence for a rare event. It is evidence that the event is rarer than the trial could detect.
The short version: check the endpoint, check the comparator, check who was excluded, then look at the number.
In practice, a trial establishes what happened to a defined group under a defined protocol. Extending it beyond that group is inference, and inference is allowed as long as it is labelled.
Intention-to-treat and per-protocol analyses answer different questions. ITT asks what happens if you offer the treatment; per-protocol asks what happens if it is taken as directed. The gap between the two is a measure of how tolerable the protocol was.
Registry entries at ClinicalTrials.gov carry the pre-specified primary endpoint with a timestamp, which is the cheapest available check on whether an endpoint was changed after the data were seen.
Quote the interval alongside the estimate and half the disagreements on this site would not start.
Answer first: read the primary endpoint, the comparator and the population before you read the effect size. Almost every argument on this site about a trial is really an argument about one of those three.
Open-label extensions are not the same evidence as the randomised phase. Once everyone knows what they are taking, the reported outcomes acquire a bias that no analysis fully removes.
Read the protocol and the statistical analysis plan if the result matters to you. Both are usually published alongside.
Ask PeptideStack is a static archive. Posting is closed, but the norms are worth stating: answer the question that was asked, show your working, cite the trial or the certificate, and say plainly where the evidence runs out.