James Coyne (who we last encountered in the sad story of Ellen Langer) writes:
I’m writing to you now about another matter about which I hope you will offer an opinion. Here is a critique of a study, as well as the original study that claimed to find an effect of group psychotherapy on time to recurrence and survival of early breast cancer patients. In the critique I note that confidence intervals for the odd ratio of raw events for both death and recurrence have P values between .3 and .5. The authors’ claims are based on dubious adjusted analyses. I’ve tried for a number of years to get the data for reanalysis, but the latest effort ended in the compliance officer for Ohio State University pleading that the data were the investigator’s intellectual property. The response apparently written by the investigator invoked you as a rationale for her analytic decisions. I wonder if you could comment on that.
Here is the author’s invoking of you:
In analyzing the data and writing the manuscript, Andersen et al. (2008) were fully aware of opinions and data regarding the use of covariates. See, for example, a recent discussion (2011) among investigators about this issue and the response of Andrew Gelman, an expert on applied Bayesian data analysis and hierarchical models. Gelman’s (2011) provided positive recommendations for covariate inclusion and are corroborated by studies examining covariate selection and entry, which appeared prior to and now following Gelman’s statement in 2011.
Here’s what Coyne sent me:
“Psychologic Intervention Improves Survival for Breast Cancer Patients: A Randomized Clinical Trial,” a 2008 article by Barbara Andersen, Hae-Chung Yang, William Farrar, Deanna Golden-Kreutz, Charles Emery, Lisa Thornton, Donn Young, and William Carson, which reported that a talk-therapy intervention reduced the risk of breast cancer recurrence and death from breast cancer, with a hazard rate of approximately 50% (that is, the instantaneous risk of recurrence, or of death, at any point was claimed to have been reduced by half).
“Finding What Is Not There: Unwarranted Claims of an Effect of Psychosocial Intervention on Recurrence and Survival,” a 2009 article by Michael Stefanek, Steven Palmer, Brett Thombs, and James Coyne, arguing that the claims in the aforementioned article were implausible on substantive grounds and could be explained by a combination of chance variation and opportunistic statistical analysis.
A report from Ohio State University ruling that Barbara Anderson, the lead researcher on the controversial study, was not required to share her raw data with Stefanek et al., as they had requested so they could perform an independent analysis.
I took a look and replied to Coyne as follows:
1. I noticed this bit in the Ohio State report:
“The data, if disclosed, would reveal pending research ideas and techniques. Consequently, the release of such information would put those using such data for research purposes in a substantial competitive disadvantage as competitors and researchers would have access to the unpublished intellectual property of the University and its faculty and students.”
I see what they’re saying but it still seems a bit creepy to me. Think of it from the point of view of the funders of the study, or the taxpayers, or the tuition-paying students. I can’t imagine that they all care so much about the competitive position of the university (or, as they put it, the “University”).
Also, if given that the article was published in 2008, how could it be that the data could “reveal pending research ideas and techniques” in 2014? I mean, sure, my research goes slowly too, but . . . 6 years???
I read the report you sent me, that has quotes from your comments along with the author’s responses. It looks like the committee did not make a judgment on this? They just seemed to report what you wrote, and what the authors wrote, without comments.
Regarding the more general points about preregistration, I have mixed feelings. On one hand, I agree that, because of the garden of forking paths, it’s hard to know what to make of the p-values that come out of a study that had flexible rules on data collection, multiple endpoints, and the like. On the other hand, I’ve never done a preregistered study myself. So I do feel that if a non-prereigstered study is analyzed _appropriately_, it should be possible to get useful inferences. For example, if there are multiple endpoints, it’s appropriate to analyze all the endpoints, not to just pick one. When a study has a data-dependent stopping rule, the information used in the stopping rule should be included in the analysis. And so on.
On a more specific point, you argues that the study in question used a power analysis that was too optimistic. You perhaps won’t be surprised to hear that I am inclined to believe you on that, given that all the incentives go in the direction of making optimistic assumptions about treatment effects. Looking at the details: “The trial was powered to detect a doubling of time to an endpoint . . . cancer recurrences.” Then in the report when they defend the power analysis, they talk about survival rates but I don’t see anything about time to an endpoint. They then retreat to a retrospective justification, that “we conducted the power analysis based on the best available data sources of the early 1990’s, and multiple funding agencies (DoD, NIH, ACS) evaluated and approved the validity of our study proposal and, most importantly, the power analysis for the trial.” So their defense here is ultimately procedural rather than substantive: Maybe their assumptions were too optimistic, but everyone was optimistic back then. This doesn’t much address the statistical concerns but it is relevant to implications of ethical malfeasance.
Regarding the reference to my work: Yes, I have recommended that, even in a randomized trial, it can make sense to control for relevant background variables. This is actually a continuing area of research in that I think that we should be using informative priors to stabilize these adjustments, to get something more reasonable than would be obtained by simple least squares. I do agree with you that it is appropriate to do an unadjusted analysis as well. Unfortunately researchers do not always realize this.
Regarding some of the details of the regression analysis: the discussion brings up various rules and guidelines, but really it depends on contexts. I agree with the report that it can be ok for the number of adjustment variables to exceed 1/10 of the number of data points. There’s also some discussion of backward elimination of predictors. I agree with you that this is in general a bad idea (and certainly the goal in such a setting should not be “to reach a parsimonious model” as claimed in this report). However, practical adjustment can involve adding and removing variables, and this can sometimes take the form of backward elimination. So it’s hard to say what’s right, just from this discussion. I went into the paper and they wrote, “By using a backward elimination procedure, any covariates with P < .25 with an endpoint remained in the final model for that endpoint.” This indeed is poor practice; regrettably, it may well be standard practice.
2. Now I was curious so I read all of the 2008 paper. I was surprised to hear that psychological intervention improves survival for breast cancer patients. It says that the intervention will “alter health behaviors, and maintain adherence to cancer treatment and care.” Sure, ok, but, still, it’s pretty hard to imagine that this will double the average time to recurrence. Doubling is a lot! Later in the paper they mention “smoking cessation” as one of the goals of the treatment. I assume that smoking cessation would reduce recurrence rates. But I don’t see any data on smoking in the paper, so I don’t know what to do with this.
I’m also puzzled because, in their response to your comments, the author or authors say that time-to-recurrence was the unambiguous primary endpoint, but in the abstract they don’t say anything about time-to-recurrence, instead giving proportion of recurrence and survival rates conditional on the time period of the study. Also, the title says Survival, not Time to Recurrence.
The estimated effect sizes (an approx 50% reduction in recurrence and 50% recurrence in death) are implausibly large, but of course this is what you get from the statistical significance filter. Given the size of the study, the reported effects would have to be just about this large, else they wouldn’t be statistically significant.
OK, now to the results: “With 11 years median follow-up, disease recurrence had occurred for 62 of 212 (29%) women, 29 in the Intervention arm and 33 in the Assessment–only arm.” Ummm, that’s 29/114 = 0.25 for the intervention group and 33/113 = 29% in the control group, a difference of 4 percentage points. So I don’t see how they can get those dramatic results shown in figure 3. To put it another way, in their dataset, the probability of recurrence-free survival was 75/114 = 66% in the treatment group and 65/113 = 58% in the control group. (Or, if you exclude the people who dropped out of the study, 75/109 = 69% in treatment group and 65/103 = 63% in control group). A 6 or 8 percentage point difference ain’t nothing, but Figure 3 shows much bigger effects. OK, I see, Figure 3 is just showing survival for the first 5 years. But, if differences are so dramatic after 5 years and then reduce in the following years, that’s interesting too. Overall I’m baffled by the way in which this article goes back and forth between different time durations.
3. Now time to read your paper with Stefanek et al. Hmmm, at one point you write, “There were no differences in unadjusted rates of recurrence or survival between the intervention and control groups.” But there were such differences, no? The 4% reported above? I agree that this difference is not statistically significant and can be explained by chance, but I wouldn’t call it “no difference.”
Overall, I am sympathetic with your critique, partly on general grounds and partly because, yes, there are lots of reasonable adjustments that could be done to these data. The authors of the article in question spend lots of time saying that the treatment and control groups are similar on their pre-treatment variables—but then it turns out that the adjustment for pre-treatment variables is necessary for their findings. This does seem like a “garden of forking paths” situation to me. And the response of the author or authors is, sadly, consistent with what I’ve seen in other settings: a high level of defensiveness coupled with a seeming lack of interest in doing anything better.
I am glad that it was possible for you to publish this critique. Sometimes it seems that this sort of criticism faces a high hurdle to reach publication.
I sent the above to Coyne, who added this:
For me it’s a matter of not only scientific integrity, but what we can reasonably tell cancer patients about what will extend their lives. They are vulnerable and predisposed to grab at anything they can, but also to feel responsible when their cancer progresses in the face of information that should be controllable by positive thinking or take advantage of some psychological intervention. I happen to believe in support groups as an opportunity for cancer patients to find support and the rewards of offering support to others in the same predicament. If patients want those experiences, they should go to readily available support groups. However they should not go with the illusion that it is prolonging their life or that not going is shortening it.
I have done a rather extensive and thorough systematic review and analysis of the literature I can find no evidence that in clinical trials in which survival was in a priori outcome, was an advantage found for psychological interventions.