This is a continuation of a long topic, addressed by post number rather than by page. Start at post 1 · go to the accepted answer.
Post #29 describes the usual case. This is about the unusual one.
Multiplicity and multiple comparisons: if a trial tests many hypotheses, the chance of a false positive on at least one by random chance increases. This is why pre-specification of the primary endpoint matters and why secondary endpoints are weaker evidence.
The mechanism is plausible, which is not the same as established.
The first question about any trial is what it set out to estimate, not what it found. Once the estimand is on the table the rest of the discussion is tractable.
I am not the right person to answer the follow-up to this.
An open-label trial is not worthless and its subjective endpoints deserve more scepticism than its objective ones. That is a graded judgement rather than a verdict.
Confirming post #33 from a second method, which matters more than confirming it from a second person.
A comparator at less than its maximum licensed dose changes what a head-to-head result means. It does not invalidate the trial; it narrows the claim the trial supports.
Generalisability: the enrolled population was selected in ways that matter. Entry criteria, run-in periods, and the simple fact that people who agree to a multi-year trial differ from people who do not, all narrow the population. That is how internal validity is bought, at the cost of external validity.
The confident version of this sentence would be wrong, so here is the hedged one.
Population narrowness: most trials in this class enrolled fairly specific groups. Baseline body mass index ranges, exclusion of renal disease, exclusion of certain comorbidities, all narrow the population. Applying point estimates to someone well outside the range is an extrapolation.
I keep a log of this specifically because memory is unreliable about it.
Post #35 is right about the mechanism and I think understates the practical bit.
Absolute numbers, not just relative: a 30% relative reduction tells you the ratio but not the practical magnitude. The event rate in each arm and the difference between them tells you how many people benefit.
The answer changed when I changed how I was measuring, which was informative.
Risk of bias: structured appraisal of internal validity. Key things to assess: randomisation method (was it truly random or could someone predict the next assignment), concealment (could randomisation be subverted), blinding (who was blinded and why or why not), completeness of outcome reporting.
Post #38 answers the question as asked. The question underneath it is different.
Registration before enrolment, with the primary endpoint declared, is what makes outcome switching detectable. Checking the registry against the paper takes five minutes and is worth doing.
A treatment-policy estimand asks what happens to people assigned to a strategy, including those who abandon it. A hypothetical estimand asks what would have happened had everyone continued. Both are legitimate and they give different numbers.
Reading it back, the second half matters more than the first.
Following this. I have the same question and no better information than the first post.
A trial that answers a slightly different question from the one you have is the normal situation rather than a failure of the trial. The skill is describing the gap precisely.
This is the sort of thing that ought to be settled and apparently is not.
Post #42 is right about the mechanism and I think understates the practical bit.
Absolute and relative effects answer different questions. Write down the event rate in each arm and the difference between them; everything quotable is derived from those two numbers.
Coming back to post #44, because the follow-up matters more than the original answer.
Composite endpoints should be read component by component. A composite driven entirely by its softest component is a different finding from one where the components move together.
Trial duration determines what can be observed. A weight-change trajectory at 40 weeks and at 72 weeks are different observations and both get quoted as the result.
Absolute numbers, not just relative: a 30% relative reduction tells you the ratio but not the practical magnitude. The event rate in each arm and the difference between them tells you how many people benefit.
That is the practical version. The rigorous version is longer and says the same thing.
Confounding in observational data: a third variable can explain an apparent association. In a randomised trial, randomisation balances unknown confounders. In observational data, observed confounders can be adjusted for but unknown ones cannot.
I would not lead a decision with this, but I would not ignore it either.
The arithmetic in post #51 is right; the assumption feeding it is the part to check.
Intent-to-treat versus per-protocol: ITT includes everyone assigned regardless of whether they took the drug. Per-protocol includes only those who completed it as intended. The two can give substantially different results.
Noted, and thank you for writing it out rather than summarising it.
Risk of bias: structured appraisal of internal validity. Key things to assess: randomisation method (was it truly random or could someone predict the next assignment), concealment (could randomisation be subverted), blinding (who was blinded and why or why not), completeness of outcome reporting.
I would want the raw data before agreeing with my own summary of it.
Everything in post #51 holds. The case it does not cover is the one I have.
Effect sizes in a trial population reflect adherence achieved under trial conditions, which is generally better than adherence outside them.
Narrowing post #55, because the general version has more than one answer.
Safety findings from a trial powered for efficacy are underpowered by construction. Absence of a signal in that setting is weak evidence of absence.
Not a strong opinion, just a consistent one.
A treatment-policy estimand asks what happens to people assigned to a strategy, including those who abandon it. A hypothetical estimand asks what would have happened had everyone continued. Both are legitimate and they give different numbers.
I would rather post the uncertainty than round it away.
Absolute and relative effects answer different questions. Write down the event rate in each arm and the difference between them; everything quotable is derived from those two numbers.
Stating my assumptions rather than smuggling them in.
Reading the supplementary appendix is where most of the real information is, and it is where almost nobody goes. The baseline table alone answers half the generalisability questions asked here.
I have seen it go both ways, which is why I hedge.
Nothing in a trial report is medical advice about an individual, and the gap between a population estimate and a person is exactly where clinical judgement lives.
If anyone can point at the primary source I would be grateful.