This is a continuation of a long topic, addressed by post number rather than by page. Start at post 1.
I read post #29 twice before replying, because I had assumed the opposite.
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.
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.
Two things before anyone answers the substance.
First, the context in the first post is clear and specific. Second, the question is framed so that an answer can actually address it. Both are the norm here and both matter more than they sound.
post #33 is right about the mechanism and I think understates the practical bit.
Open-label design: unblinded trials admit expectation effects. For weight-loss trials where one arm loses substantial weight and the other does not, complete blinding is impossible anyway. The unblinded nature is a limitation worth noting.
Coming back to post #33, because the follow-up matters more than the original answer.
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.
Picking up post #33: that is the part I would want checked first.
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 estimand: what the trial set out to estimate. Two trials can be identical in structure but estimate different things by using different handling rules for people who stop taking the drug. Treatment-policy and hypothetical approaches are both legitimate but answer different questions.
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.
Two things before anyone answers the substance.
First, the context in the first post is clear and specific. Second, the question is framed so that an answer can actually address it. Both are the norm here and both matter more than they sound.
Surrogate endpoints: an endpoint that is not the outcome that matters but is measured as a stand-in. HbA1c is a surrogate for long-term glucose control and the short-term complications it prevents. Weight loss is a surrogate for metabolic health and long-term outcomes. Surrogates are useful but not identical to the endpoint that matters.
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.
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.
Surrogate endpoints: an endpoint that is not the outcome that matters but is measured as a stand-in. HbA1c is a surrogate for long-term glucose control and the short-term complications it prevents. Weight loss is a surrogate for metabolic health and long-term outcomes. Surrogates are useful but not identical to the endpoint that matters.
On post #40 — agreed on the reasoning, with one qualification.
Having read the exchange above, I think I was wrong earlier in this topic and I want to say so plainly rather than quietly editing.
The correction was fair and I had been repeating something I had not checked carefully enough.
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.
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.
post #46 is right about the mechanism and I think understates the practical bit.
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.
Worth separating two things that post #44 runs together.
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.
Picking up post #46: that is the part I would want checked first.
I disagree with the reply above, and I think the disagreement is substantive rather than terminological.
The distinction being drawn does not survive when you look at the published data for this specific question. I would be glad to be shown wrong on this, because the version I am arguing against is more convenient.
Coming back to post #48, because the follow-up matters more than the original answer.
The estimand: what the trial set out to estimate. Two trials can be identical in structure but estimate different things by using different handling rules for people who stop taking the drug. Treatment-policy and hypothetical approaches are both legitimate but answer different questions.
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.
Coming back to post #51, because the follow-up matters more than the original answer.
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.
Picking up post #51: that is the part I would want checked first.
Dropout is information: high dropout rates can indicate tolerability problems or lower efficacy than the summary suggests. Where the analysis handled dropouts matters. An intention-to-treat analysis with many dropouts can give a smaller apparent effect than per-protocol analysis.
Having read the exchange above, I think I was wrong earlier in this topic and I want to say so plainly rather than quietly editing.
The correction was fair and I had been repeating something I had not checked carefully enough.
Open-label design: unblinded trials admit expectation effects. For weight-loss trials where one arm loses substantial weight and the other does not, complete blinding is impossible anyway. The unblinded nature is a limitation worth noting.
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.
This follows post #55 rather than contradicting it.
Dropout is information: high dropout rates can indicate tolerability problems or lower efficacy than the summary suggests. Where the analysis handled dropouts matters. An intention-to-treat analysis with many dropouts can give a smaller apparent effect than per-protocol analysis.
On post #55 — agreed on the reasoning, with one qualification.
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.
post #59 answers the question as asked. The question underneath it is different.
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.