Is there a way to fit a Cox model for a competing risk analysis? Wouldn’t it be inferior to perform a Cox regression instead of a competing risk regression and estimate the sub-distribution hazard? My understanding is that once we are fitting a cox model in presence of competing risks, we are pushing the competing events (e.g. deaths for failures) to cumulative censoring. Therefore, the relative ratio of the cumulative events to cumulative censoring will reduce and the study will be underpowered to calculate the treatment effect.
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if you censor the competing risks then youre estimating the cause specific hazard using cox regression. I recommend a paper by putter et al. SiM titled “Tutorial in biostatistics: Competing risks and multi-state models” it says the cause specific hazard is ok but we must be careful with interpretation, and maybe regression on cumulative incidence is preferred
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This is a great topic because I’ve been trying to understand competing risk analysis for 20 years. My current thinking is that it’s impossible for most people to understand, so I use discrete time state transition models for which all assumptions and all probabilities are out in the open, and they also handle recurrent events very well.
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yes, i’ve struggled with this. Reading the literature i see ambivalence. Eg re cause specific hazard:
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the SiM tutorial i link to above says it is the “logical choice” and it is “completely standard” … “but the interpretation requires caution”
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austin circ 2016: Introduction to the Analysis of Survival Data in the Presence of Competing Risks - PubMed “independent competing risks may be relatively rare in biomedical applications” … “even when the competing events are independent, censoring subjects at the time of the occurrence of a competing event may lead to incorrect conclusions because the event probability being estimated is interpreted as occurring in a setting where the censoring (eg, the competing events) does not occur”
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wolbers et al. ehj 2014: Competing risks analyses: objectives and approaches - PubMed "a cause-specific hazards model for an event of interest can be fitted using standard statistical software for Cox regression if competing events are treated as censored … “importantly, this approach is valid regardless whether different event types are independent of each other or not” [i guess this implies that you analyse all event types]
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he then says his own data example violates the assumption, it is clinically implausible in general, and cannot be tested: “The validity of this independence assumption cannot be statistically verified and is often clinically implausible. Specifically, in the ICD example, older subjects are more likely to die prior to an appropriate ICD therapy, i.e. they are ‘sicker’ than those who remain under follow-up, as we will show in the regression section below”
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I can’t help thinking this is all a reprise of the same problem Aalen & colleagues have explored [1,2], in which statistics’ customary high level of abstraction renders it incapable of achieving mechanistic causal explanation & understanding. Here’s a passage from the Conclusion of [2]:
I would propose that, as with the DAG, the abstractions you all are employing lack mechanistic precision. (It’s perhaps no accident that the element of time is so profoundly present in the present discussion as well.)
- Aalen OO, Frigessi A. What can Statistics Contribute to a Causal Understanding? Scand J Stat. 2007;34(1):155-168. doi:10.1111/j.1467-9469.2006.00549.x
- Aalen OO, Røysland K, Gran JM, Kouyos R, Lange T. Can we believe the DAGs? A comment on the relationship between causal DAGs and mechanisms. Stat Methods Med Res. 2016;25(5):2294-2314. doi:10.1177/0962280213520436 PMC5051601
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Great discussion. Here is an example to show why I think competing risk analysis is confusing. Suppose we have only two events: myocardial infarction (MI, fatal or nonfatal) and death not due to MI. First of all don’t we need to assume that MI is independent of death? What exactly does that mean? I assume it means that an impending risk of death does not alter your risk of MI. If so that is an unverifiable assumption. We can check whether a nonfatal MI alters your risk of all-cause death using a time-dependent covariate. But since death can be observed regarding of MI status one can compute a meaningful cumulative incidence of death with no assumption about MI.
The cumulative incidence of MI at 5y with non-MI death as a competing event is the probability of having an MI within 5y that preceeds death. What exactly does that mean? Can people interpret it?
Contrast that with a state transition model that gives rise to state occupancy probabilities. Note that we have to specify whether MI is an absorbing state or not. It has to be non-absorbing because a person can change for the state of “alive with MI” to dead. So in computing probabilities of MI you need to decide whether to compute the probability that a patient has ever had an MI or whether the patient currently is in status “MI”. State occupancy probabilities invite you to consider also the more simple quantity of the exacted number of MIs a patient has had within 5y, which is something you also get from the cumulative mean function in recurrent events analysis.
To have non-overlapping states, MI below means MI and alive. So we can compute
- P(death by time t)
- P(current MI at time t)
- P(MI or dead at time t)
- E(number of MIs before time t)
Aren’t these more interpretable?
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Interpretable in terms of what? The basic intuitions remain unexamined.
EDIT: Okay, I see it now. These probabilities are interpreted precisely in terms of the possible paths individuals may take through the states, with the careful observation that fewer of these states will be absorbing than one might casually realize. The state transition diagram establishes a set of canonical paths to represent the most relevant life-histories for discussion. These, in turn, might be compared according to the individual’s personal values. This is possible because these histories are more concrete than abstractions such as hazard ratios.
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A good place to start is this vignette by the great Terry Therneau using the R {survival} package:
Many seems to have issue with the Fine and Gray approach and how to interpret regression coefficients.
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That is a very nice explanation. Thank you Prof. Harrell. So you prefer a Markov multistate model instead of competing risk analysis. But what do you think of RMST and RMTL analysis where RMTL is basically the time lost secondary to competing risk and censoring??
I like “time in state”-like quantities; I just want to get them from state transition models and not from harder-to-interpret-and-less-flexible competing risk models.
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