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THE GREAT DEBATE |
From the Department of Psychiatry and Behavioral Science, Duke University Medical Center, Durham, NC
Address reprint requests to: Redford B. Williams, MD, Duke University Medical Center, Dept. of Psychiatry & Behavioral Sciences, Box 3926, Durham, NC 27710. Email: redfordw{at}acpub.duke.edu
Abbreviations: CHD = coronary heart disease; MI = myocardial infarction; BHAT = Beta-Blocker Heart Attack Trial; APS = American Psychosomatic Society
CLOSING ARGUMENTS—AFFIRMATIVE SIDE: Dr. Williams
Our opponents have advanced a broad range of arguments, and it is not easy to decide where to begin our response. To get things started, I will recall Dr. Relman’s statement that the Affirmative side "dropped a lot of names and threw a lot of conclusions up on the board..." and then he proceeded to drop a lot of names. He did not throw any conclusions on the board, but he did tell us, "The AHA said this..." and "Gene Braunwald said that..." Among our legal colleagues, it is said that when the facts are against you, argue the law; when the law is against you, argue the facts; and if the law and the facts are both against you, pound on the table. I would characterize Dr. Relman’s primary debating strategy thus far—appealing to authority as just noted, rather than arguing the facts—as pounding on the table. He did bring up an article by Kabat-Zinn et al. (1), which is surprising, because it was not among those we sent to Drs. Angell and Relman. We agree with Dr. Relman that the outcome in the Kabat-Zinn et al. study was based on ratings that could be characterized as subjective. That is why we used only studies with objective outcomes to document the Affirmative case. His bringing up the Kabat-Zinn et al. study, which we had not mentioned or even included in the packet to be considered in this debate, is yet another example of Dr. Relman’s table pounding.
Our opponents have raised the issue of double standards, maintaining that psychosocial interventions must meet the same standards as any biomedical intervention. We could not agree more! Indeed, we would be quite satisfied if Drs. Angell and Relman would only apply the same standard to psychosocial predictors, risk factors, and interventions that they apply to biomedical risk factors and interventions. Instead of doing this, however, Dr. Angell tells us that to control for smoking in studies of psychosocial risk factors and behavioral interventions, we must get information about how deeply people inhale! Otherwise, she maintains, the studies are too flawed to be interpretable. Surely Dr. Angell knows that the voluminous epidemiological research that has established smoking as a potent risk factor for CHD has not been labeled flawed because it failed to consider depth of inhalation. Therefore, Dr. Angell’s demand that behavioral researchers do something that was not required of researchers studying "physical" risk factors is a prime example of the Negative side using a double standard—or is it simply more table pounding?
We agree with our opponents that the behavioral intervention studies do have flaws and limitations and at this point, there is not a definitive, perfect study. The evidence we have reviewed thus far in this debate, however, does make a sound case for both the health-damaging impact of psychosocial risk factors and the potential benefits to be gained from behavioral interventions that target these factors. The position of the Affirmative side is that this case is sufficiently strong now to warrant doing the definitive, large-scale studies of behavioral interventions in organic disease that will enable us to conclude not only that psychosocial interventions can improve clinical outcome, but that such interventions do improve clinical outcomes.
We submit that the state of affairs concerning behavioral interventions in organic disease at present is similar to the situation with beta-blocker therapy for post-MI patients in the early 1980s, when some studies showed a positive effect on survival but others did not, and there was heated debate as to whether beta-blocker therapy post-MI was truly effective in improving prognosis in CHD. Then the large-scale Beta-Blocker Heart Attack Trial (2) randomized 3837 men and women with acute myocardial infarction to either propranolol therapy or placebo and documented a highly reliable 23% to 28% reduction in various manifestations of CHD over an average follow-up of 25 months, and now it is considered good clinical practice to treat all post-MI patients with beta-blockers. We believe the available evidence, reviewed by us in this debate, warrants the mounting of similar, large-scale behavioral intervention trials to establish, once and for all, whether psychosocial interventions actually do "improve objective clinical outcomes in organic disease," and we are pleased that our opponents in this debate seem to agree with us on this point.
AFFIRMATIVE SIDE: Dr. Schneiderman
I would like to recall that the title of this debate is "Psychosocial interventions can improve objective clinical outcomes in organic diseases." It is not about mind-body issues. In my opinion, there is no room for mind-body dualism in the 21st century.
When Dr. Markovitz asked Dr. Williams and me to argue the Affirmative position in this debate, I was delighted. It was only after the APS announcement went out, however, that I was informed that our worthy opponents did not wish the debate to include a discussion of lifestyle changes or medication-adherence training, which are two vitally important forms of behavioral intervention. In my opinion, psychosocial interventions involve important aspects of skills training, including teaching people how to decrease their distress and make lifestyle changes. We should not minimize the expertise needed to modify behavior so that patients can make appropriate lifestyle changes and/or adhere to medication regimens. In the intervention model my group uses in our research on HIV, we ask whether CBSM decreases HIV viral load and disease progression: a) directly through skills learning leading to improvement in medication adherence; b) indirectly through a decrease in distress that facilitates medication adherence; or c) through separate pathways involving both stress reduction and medication adherence. All of the above pathways involve behavioral intervention, and both b) and c) involve biological mediation—that’s the problem.
The arguments Drs. Relman and Angell use involve a double standard; one for their version of medicine and one for everybody else’s. We would not say that evaluation of a cancer treatment involves medication, but not surgery. Nor should we say studies should look only at medications working on bacterial but not viral agents. Similarly, all behavioral intervention effects cannot be divided into lifestyle vs. other biobehavioral factors. A variety of behavioral factors impact on disease outcomes. As McKinlay and McKinlay (3) have observed, the precipitous decline in infectious disease rates in the United States preceded the development of immunization and antibiotics by several decades. After analyzing the relevant data, they concluded that most of the decline was due to better nutrition and improved hygiene, both of which involve behavior. Only about 3.5% of the total decline in mortality since 1900 could be attributed to pharmacological interventions. It can be argued that changes in environmental conditions that involve learned behavior have played the preeminent role in improving health throughout the past century. Thus, it seems that psychosocial interventions have long been shown to play an important role in improving clinical outcomes in organic disease.
Drs. Angell and Relman have in part argued that the individual intervention studies that we presented are flawed because the findings are based on small numbers of subjects—albeit with large enough effect sizes to achieve statistical significance. Before this debate, our opponents argued that we should not use meta-analysis to help make our points, arguing that it is a flawed methodology and not scientific. Note that the argument was not about a particular meta-analysis, but about all meta-analyses. I would argue that in the development of science, positive results from a reasonable number of relatively small studies that have similar outcomes despite slightly different methodologies provide the basis for identifying needs for rigorously controlled clinical trials.
I would like to turn again to the issue of the double standard, since it was raised by our opponents. In 1985, the New England Journal of Medicine published an article by Barry Cassileth and colleagues (4) examining possible associations between psychosocial variables and either survival or relapse from advanced cancers. More than half of the subjects in this study had unresectable cancers, and the patients had life expectancies less than a year. The psychosocial questionnaire Cassileth and colleagues used was composed of questions about variables found to predict mortality in previous investigations conducted for the most part on healthier patients. Only one of the questionnaires that they used to develop their psychosocial instrument had been primarily used on patients with metastasized cancers. The result was an instrument that was not appropriately validated. Is it reasonable, for example, to ask terminally ill cancer patients to provide discriminatory information based on job satisfaction? They are certainly not working. Or is it appropriate to ask for a subjective view of the patient’s adult health? These people are all very sick.
In short, the paper by Cassileth et al. (4) was naive and arguably should not have been published in a rigorously reviewed scientific journal, much less the prestigious New England Journal of Medicine! This is true without even considering the paper’s other design flaws, including failure to evaluate moderating variables such as gender in considering job satisfaction (ie, most of the men in the study had a continuous work history, whereas this was less likely to be the case for women). The study also lumped together a large number of disparate cancers including viral- and hormonal-based cancers. There was no indication of when cancer diagnoses were made. I was interested when Dr. Angell brought up the timing of diagnoses. You cannot tell in the Cassileth study whether the assessments were made before or after the onset of adjuvant therapy; that would make a major difference. Nevertheless, Dr. Angell wrote a glowing editorial accompanying the Cassileth article whereby she described it as a careful, prospective study and concluded that "It is time to acknowledge that our belief in disease as direct reflection of mental state is largely folklore." Dr. Angell seems to be using a double standard of her own here, castigating the studies we have cited as flawed in multiple, even "fatal" ways, while heaping praise on the clearly flawed Cassileth study.
In presenting the Negative position in this debate, Drs. Angell and Relman have set out to show that the studies the Affirmative side presented have design flaws, although none of them could be nearly as flawed as the Cassileth article whose publication in the New England Journal of Medicine was overseen by our opponents. I would submit that all scientific studies in medicine are limited and almost all have possible confounds. The studies that we have cited, however, did not have fatal flaws. Instead, they collectively provide a preponderance of evidence that clearly justifies the initiation of large-scale clinical trials to examine the extent to which psychosocial interventions actually do improve clinical outcomes for specific clinical diseases. We certainly welcome the comments that Dr. Relman and Dr. Angell have made, indicating that we need more, better and larger studies. We believe that, given the current state of scientific knowledge, there is substantial need for the initiation of large-scale, rigorously conducted psychosocial clinical intervention trials in the areas of CHD, HIV/AIDS, and cancer.
NEGATIVE SIDE: Dr. Relman
Mea Culpa. I am guilty of citing authority, I could not resist. The article in the New York Times was there, I read it at the breakfast table, and thought we should mention it, but Drs. Schneiderman and Williams, your point is well taken. We should not care about authority. We do, in fact, recognize the primacy of objective evidence; and therefore, we should not have mentioned it. That is why I take serious issue with the charge that we use a double standard in reviewing manuscripts. We do not. We just look at the data. If you think that when we were editors of the New England Journal of Medicine, we were favoring papers reporting medical interventions over those reporting psychosocial interventions, talk to the 90% of authors whose papers on medical interventions we rejected. We were tough; we thought we were fair, and we were constantly asking the question "what is the evidence?" We did not care what the intervention was, or what the subject was, or who the author was. We were looking at the evidence, and therefore, I personally am affronted by the implication that we are somehow unfair in our evaluation of evidence. There is nothing to support that notion.
If you do a prospective study and you randomize a statistically sufficient number of people so that you are able to control for confounders, and you measure objective, clinically significant outcomes, then you are likely to get a useful result. If authors do those things, editors of rigorously reviewed journals will say "great." We simply have not yet seen such studies in the literature describing psychosocial interventions. Now, for Dr. Schneiderman’s point that although the intervention may not directly change the mechanisms of the disease, if it changes behavior and has some effect on outcome, then that is useful. We do not contest that; we agree. If psychosocial interventions will make people behave more sensibly and more able to deal with their disease, thus making them feel better, fine, use those interventions. But this does not prove that how you think, or what your emotional state is, or how stressful your environment is, or the counseling session you received really changed the pathological processes that account for your disease. That is what we are debating.
Turning now to the question of meta-analysis. We do not like meta-analyses because everything depends on the quality of each individual study, and most of the meta-analyses we saw included articles of varied quality and rigor. The New England Journal of Medicine was, I think, the first major journal to begin to publish clinical meta-analyses and methodological papers about meta-analyses, but we were always worried because you have to look at each and every paper upon which the meta-analysis is based, in the same way we have been looking at the papers that we are talking about today, to know whether the meta-analysis is sound.
I cannot overemphasize the importance of Dr. Angell’s point: You cannot strengthen your argument, Dr. Schneiderman, simply by accumulating a lot of studies that are not very good. A large number of weak studies do not add up to a strong conclusion. To argue that these papers we criticized, although not as good as one might like, did not have truly fatal flaws, and therefore in total ought to be considered as valid evidence—-that is not good science or even rational thinking. We must be driven by the evidence and the evidence must be credible. Therefore, Dr. Angell and I say, "tell us what you did, show us the numbers, deal with your data critically, get enough numbers, use appropriate controls, randomize where you can, and then we will follow the evidence." We are all for good studies of that sort in every field, and we are not biased against studies of psychosocial interventions, but they must be conducted rigorously.
NEGATIVE SIDE: Dr. Angell
In answer to Dr. Williams, I was not seriously suggesting that you look at how far down people smoke their cigarettes, or how deeply they inhale. I was simply underscoring the point that these studies should not have included smokers at all, because to include smokers was to introduce an overwhelmingly strong confounding variable while looking for a weak effect.
Since both Dr. Williams and Dr. Schneiderman have spoken about my writings, let me speak about theirs. Dr. Williams and his colleagues published a paper in 1992 called, "Prognostic importance of social and economic resources among medically treated patients with angiographically documented coronary artery disease" (5). They studied a sample of medically treated people with 75% or greater stenosis of at least one major coronary artery. They found that those with an income of $40,000 or more, as opposed to less, were more likely to survive, as were those who were married or had a confidante. We all know this: affluent, married people live longer than those who are impoverished and live alone. Williams and colleagues conclude that low levels of social and economic resources identify an important high-risk group among medically treated patients with coronary artery disease, independent of important medical prognostic factors. This study says nothing about mental state. The effect could be the result of the behaviors of these people. For example, it could be the result of smoking, because the only thing that the authors adjusted for was medical status—left ventricular dysfunction and the amount of coronary artery disease. They did not adjust for other confounding variables, not even the treatment. Then, Dr. Schneiderman and his colleagues, in a study published last year, found that marital stress but not job stress, predicted death after coronary artery disease in women (6). The numbers were small, and all of the baseline differences were in favor of those who did not have recurrent events. The authors made no attempt to determine whether the effect of marital stress was direct or due to differences in behavior. So, I am every bit as critical of their publications as they are of mine.
Received for publication September 26, 2001.
Revision received September 28, 2001.
REFERENCES
This article has been cited by other articles:
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  N. Schneiderman and R. B. Williams THE GREAT DEBATE EDITORIAL, REVISITED Psychosom Med, July 1, 2006; 68(4): 636 - 638. [Full Text] [PDF]
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K. E. Freedland, G. E. Miller, and D. S. Sheps The Great Debate, revisited. Psychosom Med, March 1, 2006; 68(2): 179 - 184. [Full Text] [PDF]
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