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THE GREAT DEBATE |
From the School of Medicine and Social Medicine, Harvard Medical School, Cambridge, MA.
Address reprint requests to: Arnold S. Relman, MD, 13 Ellery Square, Cambridge, MA 02138-4227. Email: arelman{at}rics.bwh.harvard.edu
NEGATIVE SPEAKER 1: Dr. Relman
Ladies and gentleman, Dr. Angell and I are not interested in a general debate about the "mind-body connection." Mind is obviously a function of the brain and brain is obviously an integral part of the body. The interactions among brain, mind, and body are numerous and our understanding of these mechanisms increases almost daily. The mechanisms by which brain and mind interact with the body may be debatable, but the fact of the connection is established and we do not doubt that.
The question that we want to discuss is: Given the fact of the mind-body connection, is there any good clinical evidence that psychological and social interventions can directly change the course of serious organic disease? By directly, we mean through some direct effect on the biological process itself rather than through changes in compliance with treatment or some change in behavior such as diet or exercise that might well affect the course of the illness.
Our position is not that significant direct effects of this kind are impossible, but simply that as yet there is no good clinical evidence to reject the null hypothesis. On the other hand, we do not challenge the likely proposition that some psychosocial interventions in some diseases may make some patients feel better and more able to tolerate the symptoms and disabilities of their disease, and therefore, they may be useful for that reason.
Whether, in fact, psychosocial intervention can directly change the pathology and clinical course of the disease itself is a question that can only be answered by a critical examination of the evidence. We, therefore, asked Drs. Schneiderman and Williams to select any reasonable number of published studies that they consider to be good evidence that psychosocial intervention can improve the pathological course of organic disease. They sent 21 articles, to which we added two more (with advance notice to our opponents), making a total of 23. It is this evidence on which we focus our discussion. We have already heard reference to articles that were not in that list of 23, and I object to this deviation from the agreed-upon format of the debate because we have not had an opportunity to examine those additional citations. We looked at 23 papers, which we presumed were among the very best that they could find, and that is what we want to talk about.
How good is the evidence in those 23 articles? After examining them carefully, it is our contention that none of them provides good strong evidence. Most of them, in fact, are so flawed as to be uninterpretable. At best, a few can be described as only suggestive, but worthy of attempts at replication with larger and better designed studies. Dr. Angell and I divide the discussion of these articles between us; I will critique the 11 that describe the results of psychosocial interventions. She will critique the others that describe simply a statistical association of psychosocial factors with disease.
The diseases studied in the 11 interventional studies are cancer, heart disease, infection, hypertension, and psoriasis (1–11). Only four of this group of interventional studies are going to get specific comment from me because of time limitations. It is much more important to discuss a few key studies in detail than to cover a larger number more superficially without critically examining the design and the data. No conclusions can be drawn without careful consideration of the evidence in detail. Everything depends on the quality of the evidence.
1. First, there is the study by Fawzi et al. (1) on malignant melanoma, which you already heard Dr. Schneiderman talk about. Dr. Angell and I believe it is fatally flawed because the analysis is not by the intent-to-treat method, which should be standard epidemiologic practice. The authors did not report the results on all their randomized subjects, which would have been the proper, "intent-to-treat" procedure. The number of exclusions and losses to follow-up after randomization could easily have affected the outcome critically since their groups were relatively small and they report a relatively small number of deaths or recurrences. So, I believe that any critical and experienced epidemiologist would consider that study invalid. You have to analyze by intent to treat, and there were enough cases lost to have totally changed the results and the conclusions, depending on their outcome. You simply cannot find out what happened to a lot of missing patients in this study, so you cannot have much confidence in the conclusions.
2. The much cited study by Spiegel et al. (2) on the effect of 1 year of group therapy in patients with metastatic breast cancer is weakened seriously by the lack of data on possible differences between control and experimental groups in lifestyle, treatment, diet, and compliance during the years after randomization and intervention. Without such information, we do not even know which patients got more treatment after they were randomized, we do not know what kind of diet they followed, and so on. Without more information on the treatment after the initial intervention, it is difficult to draw conclusions about the direct effect of the initial treatment on survival.
Also, the observed survival curves are very mysterious. For the first 20 months, the treated patients do not do quite as well as the untreated; more of them died. The difference was not very large, but clearly more treated patients died during the first 20 months of follow-up. Then the curves cross and for the remainder of the time the patients who have been counseled survive longer. That is very odd. It is also interesting that Spiegel et al. (2) confirm the earlier observation of Cassileth et al. (12) that there is no correlation between baseline personality characteristics and survival time in advanced cancer, which by itself raises doubts about the putative effects of counseling. So, I would classify this study of uncertain significance, but worthy of replication with a larger cohort and better follow-up data. I am glad to know that that is what Dr. Spiegel is doing. But as of now, I think it is fair to say that an effect of psychological intervention on survival with metastatic breast cancer has not yet been established.
While these remarks were being prepared for publication, a study on "The Effect of Group Psychosocial Support on Survival in Metatastic Breast Cancer" by Goodwin et al. appeared in the New England Journal of Medicine 2001;345:1719–26. This rigorously conducted trial showed that supportive group therapy made patients feel better, but did not prolong survival. In an editorial in that same issue, Spiegel attributes the result to the general improvement in the medical and psychological management of all breast cancer patients during the period since his original paper was published. Whatever the explanation, it now seems clear that his initial claims for the life-prolonging effects of psychological treatment in breast cancer are not likely to be confirmed.
Another much discussed study is that of Kabat-Zinn and colleagues in Psychosomatic Medicine (3), which has to do with meditation and the rate of healing of psoriatic lesions. My detailed critique of that study has just appeared in Advances in Mind-Body Medicine (13).
Comment by Debate Monitor: That article was inserted and Dr. Williams and Dr. Schneiderman were made aware that it was going to be discussed, but it was not on their original list.
Comment by Dr. Relman: Okay, but they saw it, and they had a chance to study the article. In contrast, we have not had a chance to examine several of the articles they have cited here this morning.
As I point out in my critique, the Kabat-Zinn et al. (3) article is a small study. It is further weakened by subjectivity and lack of blinding for most of the observations, and by inadequate correction for possible confounding factors. They only corrected for two such factors and there certainly were more. The authors themselves describe their conclusions as "preliminary and tentative," and they add that the results must be interpreted cautiously considering the small numbers. To which Dr. Angell and I would simply say "Amen." And yet, this study is widely cited as evidence supporting the biological therapeutic effect of psychological intervention.
4. The last in this quartet of interventional studies is the 1986 report by Friedman et al. (4) on the therapeutic alteration of type A behavior, which you have heard discussed already. Setting aside the fact that not everybody confirms what Friedman and co-workers (4) claim, this study is considerably weakened by the fact that the alleged beneficial long-term affects of counseling could all be due to unmeasured, indirect effects (such as subsequent changes in lifestyle, including diet, exercise), or to differences in compliance with medical treatment. The authors give us no information about that. Now, you can say that counseling helped patients lead a more healthful life, but that does not prove that counseling directly affects the pathology and natural history of coronary artery disease. Nevertheless, we concede it is possible that control of hostile behavior reduces sympathetic nervous system discharges and may thereby reduce morbidity and mortality in coronary artery disease. Clearly, more and better data are needed and I am glad to see that the National Heart, Lung and Blood Institute is currently conducting a big study that may give us some answers. In the meantime, I endorse the views of the American Heart Association, which were quoted in the New York Times a few days ago (March 7, 2001). The AHA says that "the available data do not yet support" the use of stress management as a proven therapy for cardiovascular disease. The same article quotes the noted cardiologist, Dr. Eugene Braunwald, as saying that after review of the data for the past four decades, he is "not very impressed with firm evidence for stress-related progression of coronary disease." I usually prefer to cite published evidence rather than authority, but could not resist quoting the AHA and a world-famous cardiologist in this case.
These four articles are the best of the interventional studies I reviewed. The others I have no time to discuss, but I will be glad to respond to any questions about them from Dr. Schneiderman and Dr. Williams. In my opinion, however, they are all much weaker than the ones that I have just cited.
There remains the article that was published in the New England Journal of Medicine on the association between a history of stress and the response to experimental inoculation of normal volunteers with various types of cold viruses (7). This study did show a small effect of past stress on the replication of virus in the subjects, but not on cold symptoms. The effect is modest; the odds ratio is a little over 3, and the confidence limits are wide. All that one can say is that the study seemed carefully carried out, and the results provocative enough to warrant publication in New England Journal of Medicine. When this manuscript was first submitted, I was Editor-in-Chief and Dr. Angell was Executive Editor. We did not share the rhapsodic enthusiasm with which some commentators greeted this study, and we certainly did not think that it was the last word on this subject. It was basically just a preliminary study, but it opened the field to additional exploration, and we hoped it would lead to other and even more definitive studies. One very small study published subsequently has partly confirmed this work (14), but much more and better evidence will be needed to settle this question.
In conclusion we say: Where are the data? Where is the evidence? Examine each paper on its merits. Dr. Angell and I have done just that for most of our professional life, and we think we know how to distinguish convincing epidemiologic studies from those that are not. In our judgment, none of the interventional studies we examined was convincing. In judging by the published studies we have seen, there is as yet no substantial evidence that psychosocial intervention can directly improve the pathological processes in organic disease. Thank you very much.
NEGATIVE SPEAKER 2: Dr. Angell
In my 1985 editorial (15), which was titled "Disease as a Reflection of the Psyche," I wrote "the literature contains very few scientifically sound studies of the relation, if there is one, between mental state and disease." I made it clear that I was not referring to the effect of mood on our sense of physical well being, or to psychological health as a worthy goal in itself. What I was talking about was the view that mental state can directly cause or substantially modify organic disease independent of personal habits such as smoking, drinking alcohol, or overeating. I am afraid my assessment of the literature has not changed very much in the 16 years since I wrote that. You sent us 23 articles on the subject, all but one of which was published after 1985. We assume you chose to send us the very best evidence you could find.
Dr. Relman discussed the 11 articles you sent concerning interventions to modify mental state and thereby change the course of physical disease. I will discuss the remaining 12 papers—all observational epidemiologic studies on the relationship between mental health and disease.
Observational epidemiologic studies are fraught with difficulties, and these articles exemplify most of them. The most serious are: 1) failure to deal adequately with possible confounding variables, 2) failure to distinguish cause from effect, 3) data dredging, and 4) biased interpretation. I will consider these problems one by one.
Confounders
The articles were studies of weak effects, not strong ones, and dealing adequately with confounders is especially crucial in these types of studies. By confounders I mean a variable that is related causally both to the risk or prognostic factor and to the outcome. By weak effects, I mean a relative risk, or odds ratio, of no more than 3 or 4. For comparison, remember that the relative risk of lung cancer in cigarette smokers is over 20; that is a very strong effect. The reason weak effects are so difficult to study is that they are easily swamped by effects of confounding variables, either known ones or unknown. For example, a study of smog as a risk factor for lung cancer could easily be swamped by differences in cigarette smoking between the smog-exposed group and the unexposed group. Even very careful attempts to adjust for cigarette smoking, right down to the number of cigarettes smoked per day, would probable be inadequate and certainly it would be inadequate simply to classify people as nonsmokers or current smokers. That is because smoking would be so strong a confounder compared with the likely effects of smog, that to adjust for it completely would require such information as how deeply subjects inhaled and how much of each cigarette they smoked. For that reason, such a study should look only at nonsmokers. Unknown confounders can also be a threat to studies of weak effects. Indeed, many eminent epidemiologists do not accept any conclusions based on a single study with a relative risk of less than 3. I refer to a 1995 article in Science (16).
I am going through this in some detail because only in two of the observational studies you sent Dr. Relman and me (17, 18) was the relative risk of an outcome more than 3. Yet, failure to describe exactly how confounding variables were handled was a major problem in nearly all these studies, even when the confounders were extremely strong. For example, in the study of the effect of hostility on coronary artery calcification (17), it would be essential to adjust very, very finely for important factors that would be related both to hostility and to coronary artery calcification—for example, cigarette smoking, alcohol consumption, education, and income. In fact, to be on the safe side, a good study of this question would enroll only nonsmokers, nondrinkers, and people with the same income, same education and so forth; as much as possible the people in the study should differ only in their hostility scores. Yet in this study, confounders were measured only coarsely—for example, the percentage of current smokers in each hostility group.
Dealing with confounders is especially important in studies of mental state and disease, because one of the important questions here is whether the effects of mental state are direct or mediated through behavior such as smoking. In the studies we were sent, most of the confounders varied in the direction that would create a spurious connection between mental state and disease, particularly when the confounders were added together. For example, in the study of hostility and coronary artery calcification (17), hostility was ranked in quartiles, and the percentage of current smokers ranged from less than 8% in the lowest hostility quartile to 39% in the highest hostility quartile. That is a major confounder. Remember, statistical significance says nothing about the adequacy of controlling for confounding variables or for that matter about other forms of bias. Nor does it speak to the magnitude of the results or the clinical significance.
Failure to Distinguish Cause From Effect
Observational epidemiologic studies are meant to find risk factors or causes of disease, and they often do that. But they need to be carefully designed to rule out the reverse (ie, that the disease causes the risk factor). In several of these studies, the designs permitted either interpretation. For example, in the study of mental state and survival in breast cancer (19), the psychological testing to determine mental state was performed 1 to 3 months after diagnosis. That lag time allowed for women to learn something about their prognosis, and to feel differently because of that. So, the conclusion that "helplessness/hopelessness" increased the risk of relapse or death could have been backward. More serious disease could have caused feelings of helplessness and hopelessness, and not the reverse.
Data Dredging
Observational studies virtually invite data dredging (ie, combing through a large number of findings and slicing and dicing them in various ways until finally one of them turns out to be statistically significant, probably by chance). If you measure enough things, on average, 1 in 20 of them will be abnormal. For example, in the study that I just mentioned (19), it was concluded that a high "helplessness/hopelessness" score (and maybe depression) increased the risk of relapse or death at 5 years. But these two positive findings were culled from 24 findings, all the rest of which were negative. That association could easily happen by chance alone.
Biased Interpretation
Finally, by this, I mean making more of a finding than it is worth and perhaps downplaying others. The Watson study (19), is a good example. Bias is also shown by exaggerating the clinical significance of a result. For example, finding an association between mental state and herpes simplex virus (HSV-2) antibodies or serum cortisol says nothing about the effect of mental state on disease. One link in the presumed chain of causation is not enough to complete the chain. Along the same lines, one problem with some of the cardiovascular studies we were given is the possible confusion between physiologic effects, which are very important in cardiovascular disease, and the disease itself. For example, the Jonas study (20) could easily have been affected by the well-known fact that anxiety increases blood pressure. Yet, the implication was that anxiety causes essential hypertension with all its complications. The conclusion of scientific papers should follow from the data and not go beyond the data, and it should be the only conclusion that follows from the data. You cannot just pick the conclusion you like from among many possible ones.
To summarize, these studies are of variable, but generally poor quality. I have discussed only a few of them specifically, but the others suffer from similar deficiencies (21–27). Only a few are solid enough to generate a hypothesis that should be studied in larger and better-designed studies. In those cases, that should certainly be done. I am all for that, but most of these articles are uninterpretable, as Dr. Relman said, for one or more of the reasons that I outlined. I remain unconvinced that there is good evidence for the proposition that mental state directly causes or substantially modifies organic disease. I have spent the last 21 years reviewing and editing many scientific papers, and it strikes me that the literature on psychosomatic interventions and associations is unusually poor. In general, papers on this subject are not as rigorous as those in other areas. There seems to be a double standard. I wonder whether that reflects a universal human desire to find that we have some control over the course of serious illness. I would like that to be the case as much as anyone else, but wishes are no substitute for evidence, and the evidence must meet the same standards as in any other field.
Of course there is a mind-body connection, and to suggest that Dr. Relman and I do not recognize that sets up a straw man. What is at issue is whether the mind has dominion over the body, and I think that we humans need to be a little bit more humble about our mental powers and certainly a lot more humble about the state of our knowledge.
Received for publication September 10, 2001.
Revision received September 27, 2001.
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