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In my data I have $n_1$ people who had an "event" and $n_2$ people who did not. Cases (those with an event) were oversampled substantially (the true prevalence is probably more like 1 in 10000). If it matters, $n_1 = 70$ and $n_2 = 250$. For all of those who had an event, I also know how long it took from baseline for the event to occur.

I also have a quantitative predictor measured on each person.

I want to see how that the quantitative predictor is related to the "survival time". I know if case-control status were based on something other than the variable that generates the survival time, it could just be treated as a binary predictor. But, that's not the case here. Given the wild oversampling of cases (and thus a biased sample of survival times), I feel there's something not quite right about doing survival analysis as though this were a random sample of survival time/covariate pairs.

Ignoring times and only focusing on the binary indicator of whether or not you had an event, I do know that logistic regression is still OK in this case for estimating Odds Ratios. Is that the best I can do in this case? If so, that is OK, I just don't want to look stupid for not doing survival analysis if it's feasible to do so.

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  • $\begingroup$ Much of what you're asking seems to be covered by this thread. Please look that over and refocus your question on issues not covered there. Note that in any case/control or case/cohort study, there will only be (uncensored) events in the cases. $\endgroup$ – EdM Jan 19 '17 at 19:26
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It wouldn't be advised. The hazard ratio becomes biased when the null is not true. This is because in the exposure group having higher risk of event, the person-year follow-up time is less than would be expected in a prospective study. Similarly, the unexposed groups are followed up more than would be expected. This is because inclusion as a control in the study is defined by not having experienced an event over a time frame. This is called lead time bias. A biased estimator is acceptable in some circumstances, but the resulting test may be anticonservative.

There are proposed methods for handling these scenarios. The simplest and most readily approachable was proposed by Scott and Wild for logistic models and extended to survival models later by (I think) Miguel Hernan and Tyler VanderWheele--citation forthcoming. The basic idea is to weight the cases and controls according to the expected prevalence of outcome in the sample using external epidemiologic data, provided it's available.

The other alternative is to analyze data via a nested case cohort design. This is discussed in the book Applied Survival Analysis by Hosmer Lemeshow and May.

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I thought about this a little bit. Here is my answer. Not certain it is correct.

I think it is clear that the survival function

$$ S(t) = P(T > t) $$

would be estimated incorrectly. In this data setting, $S(0) = 70/320$, which is way off the population estimate (which should be around .0001). Therefore, the hazard function, $\lambda(t) = S'(t)/S(t)$, which is the baseline value for the cox proportional hazards model is wrong, so the covariate effects, which enter in the form $\lambda(t) \cdot e^{X \beta}$, would also be wrong.

My only hesitance is that the baseline value is incorrectly estimated in case control analysis in logistic regression also, yet the other coefficients are estimated wrong. Maybe that's the case here too?

Edit: Actually, I think this is wrong, because $\lambda(t)$ is never estimated in Cox regression. I'm starting to think it's actually OK to use this approach with prospective case control data and the logic seems very similar to the reason you can use logistic regression.

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