What is the reported incidence of dizziness on cagrilintide in REDEFINE-1?

The specifics, since they change the answer: dizziness · cagrilintide · REDEFINE-1.

I have the document in front of me and I can read the numbers. What I cannot do is interpret them.

I am reasonably comfortable with statistics and completely uncomfortable with chromatography, or vice versa.

Which parts of this are informative and which are decoration?

Take it from the REDEFINE-1 adverse-event table by arm, and check the unit before you use it. An incidence can be the proportion of participants who reported the event at least once, or the count of events divided by exposure time, and the two differ by however many people had it repeatedly. Then subtract the placebo arm, because the untreated rate is not zero. And read the discontinuation column beside it: an event that made people leave the trial is under-counted at every later visit, so a low late-timepoint incidence can mean the event was severe rather than rare.

Start with what the trial was powered for. Everything else in the publication is secondary, exploratory, or a subgroup, and those three words mean three different things.

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.

Relative to absolute, worked

The last two rows describe the same finding. Only one of them is used in headlines.

Stated carefully, 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.

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.

Read the protocol and the statistical analysis plan if the result matters to you. Both are usually published alongside.

The relevant detail is that this is answerable from the published record, but only if you take the placebo arm seriously rather than reading the active arm alone.

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.

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.

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.

Be careful about generalising from a trial population to yourself. The exclusion criteria are usually the most informative page in the supplement.

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.

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.

In practice, 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.

I am not a clinician and this is not medical advice; it is a reading of a published protocol.

When two sources disagree, the answer is almost always in the methods section of the one you have not read.

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.

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.

Meta-analyses in this area are dominated by whichever trial contributed the most participants, so read the forest plot rather than the summary estimate.

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.

Look at the discontinuation rate alongside the efficacy figure. A large effect in the two thirds who stayed is a different result from a large effect in everyone.

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.

The caveat is the population. Trial participants were screened, monitored and supported; the effect size in an unmonitored setting is not the trial effect size, and it is not obvious in which direction the difference runs.

If a claim cannot be traced to a named trial with a named endpoint, treat it as a claim rather than as evidence.

edited 27 Feb 2026 by thabo_maseko — added the placebo-arm figures