University of Wisconsin Medical School, Department of Population Health Sciences, 610 Walnut Street, 707C WARF Madison, WI 53705-2397, USA. E-mail: fjnieto{at}wisc.edu
When Mervyn Susser wrote his 1989 commentary Epidemiology today: A thought-tormented world1 he probably did not realize how prophetic his words would be. During the ensuing decade, epidemiology journals were inundated by self-critiques and soul-searching commentaries. For Susser, epidemiology had abandoned its substantive-oriented nature to become a technique-oriented discipline, more concerned with its analytical methods than with its primary goals of guiding disease prevention and public health. Further elaborations of these criticisms urged a renewed emphasis on the population and societal perspectives of epidemiology.25
From an entirely different perspective, however, there were those who claimed that epidemiology was already too involved with public health.69 According to these critics, epidemiologists had become data torturers with an agenda of social agitation and constantly made exaggerated recommendations aimed at promoting costly and invasive public policy interventions. For these authors, epidemiology is not a real science but a mere collection of inductive tools useful to the astute biologist (the real scientist) to make predictions about population health.7
And then there was Taubers 1995 critique of current epidemiology practice in (of all places!) the journal Science.10 This journalistic article was largely based on quotes from leaders in the field criticizing the sin of overinterpreting small effects found in observational studies, particularly when this information made it to the mass media and the general public. Commentaries and debates then flooded epidemiology journals and seminar series in academic institutions: Who are we?, where are we coming from?, where are we going?, ... are we real scientists?
Now, it appears, it is the turn of the subspecialties. According to Beaglehole and Magnus provocative commentary in this issue of the International Journal of Epidemiology,11 the claim that more research on emerging coronary heart disease (CHD) risk factors is needed, is just the epidemiologists own occupational therapy. For these authors, we already know all that there is to know about the determinants of CHD: high serum cholesterol, high blood pressure, cigarette smoking, and physical inactivity explain 75% or more of the CHD incidence,12 and not just 50% as conveniently quoted by epidemiologists trying to justify their occupation and research portfolios. For Beaglehole and Magnus, the proponents of the old-fashioned risk factor approach are only distracting attention and resources that would be better used for implementing public health interventions and, if anything, on research on upstream determinants.
While it is hard to disagree with the authors argument that translating what we currently know about CHD risk factors into effective prevention policies at the population level should be a high priority, I take issue with the assertion that there is nothing new to be learned with regard to CHD risk factorsthat I found presumptuous and blatantly unscientific.
The data that Beaglehole and Magnus use to support their attributable risk estimates are largely derived from studies of adult individuals in Western societies, with CHD clinical events or CHD deaths as outcomes. But atherosclerosis is practically universal in adult individuals in our society13,14 and thus these studies can only inform us of the predictors and correlates of the late phases of the disease natural history. There is absolutely no proof that a causative model that explains 75% of the clinical events (even assuming that this is a correct estimate) would also explain the same amount of variance in the incidence (initiation) of the atherosclerotic process itself, the true target for primary prevention.
For Beaglehole and Magnus, research on emerging risk factors (thrombotic/biochemical factors, infectious agents, early life exposures, multiple genes, oestrogen deficiency, psychosocial environment) is irrelevant because these factors fail to pass the public health test of causality. The origins and rationale for this new causality paradigm are unclear. Moreover, even though up to five criteria are listed (including risk factor prevalence and opportunities for prevention), the application of this test to the above listed risk factors appears to be almost entirely based on whether each of them is consistently (and independently) associated with clinical CHD incidence in observational epidemiological studies.
For example, a largely negative meta-analysis of studies of chronic Chlamydia pneumoniae infection is cited as reliabl[y] exclud[ing] any strong associations.11 It is important to recognize, however, that the studies included in this meta-analysis, each with its own strengths and unique characteristics, all share a potentially fatal limitation: they are all based on one single serological measure of C. pneumoniae antibodies at one point in time in adult individuals who were followed for clinical CHD events. Since practically all of the participants in these studies (like all adults in our society) were already affected by the underlying disease (i.e. atherosclerosis) and had been exposed to this highly prevalent infectious agent,15 how can these data be so confidently used to dismiss the potential causal role of infections in earlier phases of the natural history of atherosclerosis? This would be like concluding that smokingis not a risk factor for lung cancer solely on the basis of studies of individuals with subclinical lung cancer (almost all of them smokers) that found that smoking status was not associated with the occurrence of clinically manifest lung cancer.
The risks of overinterpretation of meta-analyses of observational evidence when they replace critical assessment of the limitations of the source literature have been previously emphasized.16,17 The exclusive and uncritical attention to the meta-analysis results not only ignores the potentially serious flaws of the source studies, but also fails to consider even the most fundamental and well known aspects of the natural history of the disease as well as the extraordinarily large body of pathology, laboratory, and experimental evidence that strongly suggests a role of certain infections in atherosclerosis.1820 Just to cite a few examples, experimental infection of monocytes with C. pneumoniae induces the formation of foam cells and the oxidation of cholesterol;21,22 and experimental infection induces atherosclerosis in rabbits and rats only when combined with a high cholesterol diet.23,24 Thus, could it be that infections and cholesterol are mutually contributing factors involved in the early build-up of the atherosclerosis plaque? Apparently, Beaglehole and Magnus already know the answer to this question.
Similar issues could be raised with regard to the other risk factors discussed in the commentary, such as, for example, homocysteine, for which the inconsistent results of observational studies25 contrast with other types of evidence.26
Research on new risk factors is not only aimed at adding predictive power, but also at providing new clues for the understanding of the pathophysiology of the disease, which in turn may suggest mechanisms of action of upstream factors (including both traditional individual risk factors and social determinants). In this regard, considerable attention has been paid in recent years to the possibility that atherosclerosis is actually an inflammatory27,28 or an autoimmune disease.29 Apparently, these are utterly superfluous areas of research for Beaglehole and Magnus, who seem to be certain that the causes of CHD are diets high in saturated fat and low in antioxidants (where is the evidence for this, by the way?) along with some other contributing factors (smoking, lack of physical activity, high blood pressure)factors which act synergistically and are determined by the social, economic, and cultural contexts where populations live. Inflammation does not meet the public health criteria for causality, i.e. epidemiologists have so far been unable to consistently demonstrate an association between serum levels of inflammatory markers and CHD events or mortality. But could it be that measuring serum levels of one of these chemicals in isolation might not be a meaningful approach to address an extremely complex pathophysiological question? Cytokines and other molecules interact with each other and with cellular components at the blood-endothelial interface in extremely complex ways which we are only beginning to understand. The effect of certain molecules may go in different directions depending on the homeostatic balance at any given moment. Thus, a simplistic toxicological-type analytical approach of measuring serum levels of an isolated marker and expecting that their (dose-response) association with a certain outcome will establish or rule out the importance of a given chemical or mechanisms might be utterly irrelevant in this case.
I would argue that epidemiology should keep (or rather, recover) its broad scientific basis ranging from molecular biology to social sciences. This multidisciplinary approach to the understanding of disease causation and prevention is, to me, the essence of epidemiology. Ignoring everything outside the realm of so-called epidemiologic studies results in a narrow understanding of the scope of the discipline; it results in bad epidemiology. Ultimately, a public health test of causality that ignores the extraordinary complexity of disease pathogenesis and ignores non-epidemiological evidence is a step backwards and will not help advance our understanding of disease aetiology and its determinants. In my opinion, this approach is no less reductionistic than a strict biomedical understanding of disease processes so severely criticized by some.5
Contrary to Beaglehole and Magnus belief, many, including myself, still think that some of the lines of research that they consider worthless could reveal important clues for the understanding of atherogenesis that could eventually help in developing new primary and secondary prevention strategies. These would have important implications for the development of both population-based and high-risk preventive strategies, which, as Geoffrey Rose emphasized, are to be considered complementary rather than mutually exclusive strategies.30
It is interesting to note that, in contrast to their lack of interest in the role of the six groups of emergent risk factors discussed in their commentary, Beaglehole and Magnus conclude that there is a need for improving the understanding of the social and economic determinants of the major risk factors and overall population health status.11 It seems to me that the argument against risk factor epidemiology could also be extended to research on known socioeconomic determinants of known risk factors. Dont we also know enough about poverty being a bad thing? Being poor is clearly bad for your health (among other things). Wouldnt this type of argument support those who question whether we really need to do more research on social and economic determinants of risk factors and disease?31 Why dont we spend that money and time on acting against poverty?
For Beaglehole and Magnus, research on possible risk factors and unresolved issues is at best only moderately promising.11 The problem is that if one applies the same high standards of evidence to studies of the efficacy of cardiovascular disease prevention interventions, the results will be similarly weak if not weaker.3234 Are we then surprised when someone claims that no more CHD prevention research should be conducted?35
The authors blame the public health research community for their reluctance to act fully on the available evidence on the causes of CHD.11 Tobacco control and the reduction of salt content in manufactured foods are cited as examples of successful public health policies. The argument is that we need to do more stuff like this; for example, we need to work toward modifying the environmental determinants of physical inactivity and the resulting obesity. What is lacking in Beaglehole and Magnus commentary, however, is a discussion of concrete and specific ways for addressing the cultural and political determinants underlying these upstream conditions. If we continue their line of reasoning and arguments against emergent risk factor epidemiology, we might also conclude, for example, that we already know enough about how to prevent sedentary lifestyles and obesity. Dont we have enough evidence already regarding the influence on sedentarism and obesity prevalence of the public transportation infrastructure of cities, the patterns of TV-viewing in children, and accessibility to recreational facilities? The question is, then, what can we do about these problems?
Thus, perhaps the next line of the argument would be for public health researchers to quit applying for grants from the National Heart Lung and Blood Institute and become public policy activists or lobbyists. Should then cardiovascular epidemiologists quit their academic positions and devote the rest of their careers to trying to convince legislators to ignore car manufacturers and oil companies lobbying efforts and raise gasoline taxes, reduce parking facilities in cities, increase public transportation services, and limit the number of hours of cartoons that a TV channel can offer per day? How do we address the high saturated fat diet in the population? Would Beaglehole and Magnus recommend nutritionists abandon their research projects on lipoprotein metabolism and become advocates for the cause of outlawing the fast-food industry?
Ultimately, the question is what is the responsibility of the public health research community relative to other sectors of society with regard to convincing the government and the public at large of the desirability (and feasibility?) of these efforts?
I am certainly not against epidemiologists becoming public health activists and advocates. Quite the contrary. Moreover, I must recognize that I agree with the premise that there is currently an imbalance in the funding of aetiological and preventive research. However, I believe that this should be discussed in a wider social and political context. Blaming research epidemiologists for doing what they are funded to do after going through a highly competitive scientific review process is simply a rhetorical and not particularly constructive exercise.
I have a hard time thinking of another scientific discipline so prone to self-criticism. No one seems to be questioning the work of entomologists or botanists studying the ecology of rare species in the rain forests, archaeologists investigating lost cultures, or astronomers studying stars billions of light-years away. Epidemiologists for some reason seem intent on questioning their own worthiness. I just wonder how much of the energy spent on self-deprecating efforts would be better used in actually working together with all the other experts involved (including biologists, social scientists and policy advocates) on improving the understanding of the distribution, determinants, and (yes, of course) trying to figure out ways to improve the health of the population. That is, actually doing our jobs.
Acknowledgments
The author thanks Marion Ceraso and Karen Cruickshanks for their thoughtful and critical review of a previous version of this commentary.
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