I want to thank everyone who contributed to my request for help in evaluating the adequacy of Andersen et al's (2008) paper on psychological intevention improving survival after breast cancer. After considering the replies and some additional digging, my thinking has evolved. First, a few replies:
On 27 Nov 2008 at 22:05, Christopher D. Green wrote: I do know, however, that chi-square is not a very powerful > test, and that it is is extra-lousy when the contignecy table it badly > skewed, as it is here (you did include the non-occurrences (of death), > right?). I'm not as confident about this as Chris is. It seems to me that chi- square is the standard test for the kind of data I provided, namely a test of two proportions with substantial numbers in each cell (how many died in each group). But I now am persuaded that the Cox proportional hazards analysis may be a more sensitive test for the kind of data Andersen reported (more below) than a chi-square. That is why it is conventional medical research (where most > conditions are rare and, therefore, most contingency tables are badly > skewed) to use odd ratios. There is no significance test I know of > associated with odds ratios (but apparently there isn't one associated > with Cox either). In this case, the odds ratio for cancer death would be: > The Cox analysis does have have a significance test, which is used to test for a difference between the two survival curves. This is what Andersen did for her two groups, one receiving assessment alone (control), and the other receiving group therapy as well. The main problem that the Cox analysis overcomes (or so I understand) is that of "censored data". In the Andersen study, not everyone entered the study at the same time, and fortunately, not everyone died by its end (median of 11 years follow-up, which is impressive). A subject, for example, might be alive at least five years from enrolment up until the end of the study, but could be alive much longer. The termination of the study "censors" this data to five years. As I now understand it, my chi-square analysis of the data at the end of the study is fine as far as it goes, but it considers only one particular point along the curve, and throws away additional information which is exploited by a survival analysis, which considers the entire curve. So a chi-square may fail to reject the null while a survival analysis of the same experiment is able to reject it. My specific hang-up about Andersen was that my chi-square was a test of mortality while her survival analysis was about, well, survival. Yet she and her co-authors also made claims about reduced mortality, and these were the most striking part of her results. This seemed unjustified. But I now think the resolution is that the Cox analysis provides a statistic called a "hazard ratio", which is a kind of relative risk measure but based on all points on the two curves, not just on a selected point, as in my analysis. This is the mortality statistic. It was right there in her abstract, but I didn't understand its significance. As many (most?) medical trials seem to be suitable for the Cox analysis, I would have liked to have heard from Gigerenzer on this issue. Yet he considers only chi-square type data, and doesn't seem to mention survival time analysis. > > However, do not fret. I note that in their description of the aims of > therapy was included the phrase, "maintain adherence to cancer > treatment." Now, if that was even partly accomplished by the therapy > (that some people who would have otherwise quit conventional medical > treatment were persuaded to continue to instead) then you have your > answer without having to resort to spooky mind-over-matter claims. Yes, it was a big package, and without further dismantling studies, not possible to determine which of its many features were the most important for their results. If it promoted increased compliance with continuing treatment (say the women faithfully taking their hormone-blocking pills), that alone could perhaps account for the difference. Andersen et al prefer to focus on the ability of their package to reduce stress, and have an extended discussion, including other sources of evidence, of its possible role in the positive outcomes they reported. But whatever it was, their group therapy helped. So, although an implicit associations test would likely show I still don't believe it deep down, on the basis of this study I'm going to have to stop rolling my eyes whenever anyone asserts that psychological intervention can improve outcomes for at least one type of cancer. I'll say instead, trying not to wince, that well, gosh darn it, you betcha there is one study just published which does lend support to that conclusion... Stephen Some sources which led to my change of mind, although I can't say I understood more than a smattering (and we know how dangerous that is): Glantz, S. (2002). Primer of Biostatistics, 5th ed. Doesn't discuss Cox but does have a chapter on survival analysis. Spruance, S. et al (2004). Minireview; hazard ratio in clinical trials. _Antimicrobial Agents and Chemotherapy_, 48, 2787-2792. [free pdf at http://aac.asm.org/cgi/reprint/48/8/2787 ] [not a journal I get to very often] Also there's an essay, part of some medical course apparently, on "Hazard Ratios: An Overview" which I found helpful. It's tricky to specify where it is: First go here: http://www.bioquest.org/NumbersCount/freshman_seminar_files/week13/ Then click on the Shore2007 file, which will open a file called "Hazard Ratios simplifed.doc" in Word. [simplified is what I want] ----------------------------------------------------------------- Stephen L. Black, Ph.D. Professor of Psychology, Emeritus Bishop's University e-mail: [EMAIL PROTECTED] 2600 College St. Sherbrooke QC J1M 1Z7 Canada Subscribe to discussion list (TIPS) for the teaching of psychology at http://flightline.highline.edu/sfrantz/tips/ ----------------------------------------------------------------------- --- To make changes to your subscription contact: Bill Southerly ([EMAIL PROTECTED])
