# Statistical power in randomized clinical trials versus observational studies with identical questions

Hi, in Spain we wish to replicate this randomized clinical trial with an observational registry of cancer:

The original RCT compared DCF vs CF in stomach cancer. The authors specified a sample size of 230 patients per arm, for 95% power.
In our observational registry we already have more events and patients per category (238 DCF + 1139 CF).
However, we need to fit a multivariable Cox model with at least 8 confounding factors selected by experience, a few missing data (low rate in same covariables), and I have to test several key interactions.
Can we assume the same statistical power as in the RCT? How can I estimate my statistical power in such a setting? Since I only have to fit the Cox regression with our current dataset to see if we had enough statistical power or not, and I will have residual bias, is my question utterly stupid?

In already-collected data, power is not the issue. I would concentrate on the precision (e.g., half-width of confidence/compatibility interval) of key parameter estimates.

It is a bit unusual to do the observational study second. Normally we validate results of observational studies with RCTs.

The big question here is bias, more than power or even precision. And doing a sensitivity analysis for possible effects of unmeasured confounders will help.

1 Like

Ummm, indeed, the reason why we find the analysis interesting is because at that time (2006) there was not so much awareness that stomach cancer is actually several different pathologies. Thus, we would like to check the heterogeneity of effects according to histology and other criteria that have been seen to be important.
It may also make sense to check what happens in the real world, since DCF is a fairly toxic treatment, and probably in daily practice is applied to patients older and with a worse general situation than those included in the original trial.
The data are already collected, but we had been waiting to have at least the same patients with DCF as in the original study.
So I understand that in the statistics section of the hypothetical future article it would not make sense to allude to sample size except to briefly explain why this isnâ€™t important. However, then in results some commentary or reference should be made about the amplitude of the confidence intervals obtained, but without pretending to control their size beforehand. Is that it?

To better control the issue of bias, what I had thought was to do a Bayesian analysis with brms package, introducing the result of the randomized trial as prior. My idea was to analyze the heterogeneity of effects assuming that prior that indicated the superiority of DCF. I had thought that could be beautifuly effective at controlling bias there, because if despite a prior in favor of the existence of an effect, and despite the residual bias possibly in favor of DCF, it turns out that the hazard ratio = 1 in some histology, possibly this would be convincing. But this analysis is hard!

Yes. Once the sample size is fixed, aim at discussing the yield of that sample.

An interesting idea. But it may work against how the result will be perceived re: â€śindependentâ€ť replication.