Hi, I have a cohort of patients with a rare type of tumor. These patients have received two different therapies, A and B, and there are currently no clinical trials comparing them. After reading Datamethods I am convinced that the Bayesian analysis is the best approach. Therefore, I chose a bayesian AFT log-normal survival model (multivariable). However, I have some doubts about how I should proceed, and I wanted to ask you about the best strategy.
There is no historical information for prior distributions, but clinicians have differing views on the differential effect. Therefore, I thought to analyze the data according to the proposal by Spiegelhalter et al for interim analysis (with non-informative, skeptical or enthusiastic priors). Since my data are observational I wanted to ask if extrapolation is wise.
The idea could be to report the probability that A is equivalent or not to B (e.g., estimate 0 +/- 0.1), according to the a posteriori distribution.
I am not sure about applying the informative prior only to the main variable, or I should also do it with the rest of covariates, or even on the rest of the parameters of AFT models. For example, with Weibull models I would have two parameters (shape/scale), with the lognormal, only one.
Finally, I have read (Fayers & Parmar) that the variance of normal priors can be surprisingly 4/ number of events. However, my feeling is that this variance is a very small number that dwarfs the likelihood and makes the prior effect predominate by far. What do you think?
That’s not the variance of a prior. That’s the approximate variance of the log hazard ratio, so with a normal approximation it goes into the data likelihood.
It’s a good idea to be using Bayesian methods in observational comparisons. In this setting, more skepticism (encoded by the variance of a prior centered at zero, for example) is warranted than usual because of incomplete confounding control. As for the priors on model shape and scale parameters you might find something here in the Andrew Gelman/Columbia University “prior wiki”. For adjustment covariates, I think the same considerations for priors for predictive model covariates comes into play. You can use normal priors with a little skepticism to affect some shrinkage, to avoid overfitting/over adjustment.
Two analyses, the skeptical and the optimistic that most experts would support. The reason for the double analysis is that there are no previous data, but the most prevalent opinion is that B is possibly slightly better than A (about 15%). So the true coefficient should be somewhere between 0 and log(1.15)
In our database, the frequentist lognormal model finds a coefficient of 0.18 (B increases PFS with time ratio 1.19, 95% CI, 0.97-1.47).
To select the skeptical prior, one could use the prior N(0,0.1) where 0.1 is the SD. In this case, the bayesian model yields a coefficiente of 0.08.
To select the prior according to the expert opinion, I could also apply N(0.139,0.1), where 0.139 is log(1.15). In this case the coefficient is 0.16.
Finally, the posterior probability that A and B are equivalent in practical terms (i.e., +/- 10%) could be calculated in both scenarios.
Now I get the issue. You’re trying to get an approximate posterior distribution from another study to use as a prior (hopefully with discounting) in a new study. Yes that makes sense. Note though that 4/n is always needlessly simplified. The variance of a log hazard ratio is closer to the sum of the reciprocals of the number of events in each of the two exposure groups.
Yes, it was to learn how to apply in practical terms the Bayesian philosophy on updating prior knowledge. I find it tremendously attractive. For the study I have unfortunately there are no historical data yet.
Are you implying that findings from observational studies can not be extrapolated (i.e. generalized, transported) to individuals other than those who were included in your study? If your findings are valid, then they should apply to any patient with this tumor, unless there is a biological, physiological, or pharmacological reason to expect a different effect of A/B in those patients, assuming that A/B could be administered in the same way they were administered to the patients in your study.
On the other hand, I think it is a good idea of presenting results from the skeptical and optimistic analyses. However, I wonder how helpful would this be, because physicians that are already inclined one way or the other, would most likely stick to their previous belief, if presented with the two options. What about a third analysis reflecting the overall uncertainty about the problem?
No, I didn’t mean exactly that. The issue is that the proposal to use a skeptical prior and an optimistic prior at the same time, as far as I humbly know, comes from the field of interim analysis. In this case you can rely on the hypotheses of the study, to define those priors. For example, the optimistic approach would be that compatible with the optimistic hypothesis. Thus, in an interim analysis you can discern to what extent data, up to that specific point, are compatible or not with the null and alternative hypotheses, and make decisions. I was referring to whether it makes sense to extrapolate that analytical approach to the field of inference based on observational data. I imagined that basically, it might be relatively similar. My intuition was that with this I could evaluate if my data were probable under the prism of the alternative hypothesis of a possible clinical trial.
Would this have any practical utility? My colleagues in Spain believe that not much.
I don’t know if anyone has any opinion about it.
Ideally we should have a prior for the steepness of the curve if it’s linear, and a more skeptical prior for the nonlinear effects. There are scaling issues in forming those priors. More recent work (that I need to read about to understand) thinks of nonlinear terms as random effects and Bayes can tell you how many degrees of freedom to devote to them.