Reading a trial's population section before its results posts 61–90
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.
On post #58 — agreed on the reasoning, with one qualification.
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.
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.
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.
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.
This follows post #64 rather than contradicting it.
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.
Practical note that does not fit anywhere else. Whatever you conclude from this topic, write down what you did and when. The single most useful thing in your own records is not any individual result; it is that they are dated and consecutive.
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.
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.
I read post #69 twice before replying, because I had assumed the opposite.
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.
For anyone arriving from a search: the marked solution above is the direct answer, and the replies underneath it add the caveats that make it safe to use.
post #73 is right about the mechanism and I think understates the practical bit.
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.
Collapsed as off-topic by two members at trust level 3 or above
Coming back to post #73, because the follow-up matters more than the original answer.
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.
Picking up post #73: that is the part I would want checked first.
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.
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.
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.
post #82 answers the question as asked. The question underneath it is different.
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.
On post #80 — agreed on the reasoning, with one qualification.
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.
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.
I read post #84 twice before replying, because I had assumed the opposite.
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.
post #86 is right about the mechanism and I think understates the practical bit.
Thank you for the correction. I have edited my earlier post with a note rather than silently, so the thread still makes sense to read. The error was mine and it was the kind that comes from remembering a figure instead of looking it up.
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.
Picking up post #86: 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.
Coming back to post #88, because the follow-up matters more than the original answer.
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.