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The identification of confounders in case-control studies
J Chron Dis Vol. 36. No. 4. pp. 309-310. 19X3 Printed
in Great
Br~tam.
THE
All rights
OOZI-9681/83/040309-02!ZQ3.00/0 Copyright 0 1983 Pergamon Press Ltd
reserved
IDENTIFICATION OF CONFOUNDERS CASE-CONTROL STUDIES
IN
HARLAND AUSTIN Department
of Epidemiology,
University of Alabama in Birmingham, 202 Tidwell Hall, Birmingham, AL 35294. U.S.A.
THE SELECTION of a control group for a case-control study is probably the most important and most difficult decision confronting an investigator. Although there are a number of sources from which controls may be obtained, they are usually chosen either from among other patients at the hospital where the cases are identified (hospital-based) or from among healthy members of the same communities in which the cases reside (population-based). In the preceding paper Stavraky and Clarke report a recent case-control study which used both hospital and population-based controls. The authors compare these two control groups in the hope of clarifying some of the issues involved in choosing between them. However, the study is limited and does not appreciably add to our understanding of the issues involved in choosing between hospital and population-based controls. The first limitation is that the hospital controls are from London (Ontario) while the neighborhood controls are from Ontario. Although each control group may be appropriate for its respective case series, there is no reason to believe that they are comparable to each other. Indeed, controls are usually selected from the same locale as cases because the prevalence of many exposures differs according to geographic area. The authors apparently recognize this problem, in fact, they explain some of the differences between the two control groups on this basis, but choose largely to ignore it. This is not one case-control study with two control groups, but rather two case-control studies each with its own control group. It is not relevant to the evaluation of the choice between hospital or population-based controls. The second limitation of the study is more subtle. It relates to case-control studies in general and to what issues are and are not important in selecting controls. However, to put the discussion in perspectives, I would like first to make a few general comments about case-control studies. Many scientists view case-control studies with extreme skepticism. This skepticism may arise because such studies are perceived as “unnatural” because they look back from effects to causes and because of the difficulties involved in obtaining unbiased estimates of the exposure frequencies of cases and controls. These aspects of case-control studies have led some to maintain that they are inherently non-scientific and that their validity can be enhanced by considering as their goal the duplication of the results of a randomized controlled trial. However, case-control studies differ from randomized controlled trials in that the latter are experimental whereas the former are non-experimental scientific investigations. The goal of a case-control study should be to obtain a valid estimate of the disease frequency among exposed persons relative to that among the non-exposed, not to mimic a randomized trial. This concern with their supposed unscientific nature has fostered a need to do something to enhance their validity and many epidemiologists believe that this need is fulfilled by controlling for many extraneous factors. In fact, the identification and control of confounding has become a preoccupation in case-control studies. However, although much is known about methods for controlling confounding, often little thought is given to what factors need to be controlled in case-control studies. 309
310
HARLAUD Ausrm
Miettinen and Cook recently described the properties of a confounder in a casecontrol study[l]. They maintain that a confounding factor must be a correlate of the exposure in the source population of cases and controls and that it must be a predictor of the disease or have different selection implications for cases and controls. For illustrative purposes they describe a case-control study of the effect of other than type 0 blood on the risk of coronary artery disease. They argue persuasively that since it is known, (I priori, that gender is unrelated to blood group in the source population of cases and controls. gender cannot be a confounder in this study. Thus, a control group consisting entirely of females would be suitable for a case series consisting entirely of males, at least insofar as the primary purpose of the study was concerned. This study would probably be dismissed out of hand by those who advocate the analogy to randomized trials because of the highly non-random distribution of gender (a strong risk factor for coronary artery disease) between the case and control series. These principles should be considered when selecting a control group. The choice of the control group depends crucially on both the disease and the exposure of interest. This brings up the second limitation of the paper by Stavraky and Clark. The “cases” in this study are women with cancer of the breast, ovary, lung or lymphopoietic system. The issues involved in selecting controls for a study of breast cancer are clearly not the same as those involved in selecting controls for a lung cancer study. It is not clear why the variables in their Tables 4 and 5 were selected for presentation. Do they suppose that they are all potential confounders? If so, what reasons do they have to suppose that age at menarche, the number of live births, the use of spray deoderants, etc. are related to the use of hair dyes among women in London or Toronto? Even if age at menarche were related to hair dye use, this is of no consequence to the assessment of the relationship between hair dyes and lung cancer because age at menarche has no selection implications for cases and controls in a study of lung cancer. The authors apparently hold the widespread view that control for a number of “confounders” in a case-control study enhances its validity. In Table 3 of their report they present risk ratios “adjusted by multiple logistic regression analysis for possible confounding variables”. However, they fail to mention what variables were controlled and why they believe that any of them are confounders. The problems of overadjustment in case-control studies have recently been discussed by Day et al. [Z]. These authors point out that adjustment for factors which are not confounders not only increases the variability of the estimate of the relative risk but, more importantly, may lead to bias in the risk estimate. Thus, in an attempt to enhance validity, the well-intentioned practitioner of case-control studies introduces bias into his study. It is not my purpose to diminish the importance of recognizing and controlling confounding in case-control studies. Nor do I imply that the selection of controls should be motivated solely by the intent to achieve efficient control of confounding. Rather, I wish to emphasize that in selecting controls and in analyzing the results of a case-control study, investigators should be more parsimonious in designating the factors that need to be controlled. Sometimes recognizing what is not important is just as important as recognizing what is. REFERENCES 1. 2.
Miettenen OS. Cook EF: Confounding: Essence and detection. Day NE. Byar. DP. Green SB: Overadjustment in case-control
Am J Epid 114: 593-603, 1981. Am J Epid 112: 696 706. 1980
studies.
in Great
Br~tam.
THE
All rights
OOZI-9681/83/040309-02!ZQ3.00/0 Copyright 0 1983 Pergamon Press Ltd
reserved
IDENTIFICATION OF CONFOUNDERS CASE-CONTROL STUDIES
IN
HARLAND AUSTIN Department
of Epidemiology,
University of Alabama in Birmingham, 202 Tidwell Hall, Birmingham, AL 35294. U.S.A.
THE SELECTION of a control group for a case-control study is probably the most important and most difficult decision confronting an investigator. Although there are a number of sources from which controls may be obtained, they are usually chosen either from among other patients at the hospital where the cases are identified (hospital-based) or from among healthy members of the same communities in which the cases reside (population-based). In the preceding paper Stavraky and Clarke report a recent case-control study which used both hospital and population-based controls. The authors compare these two control groups in the hope of clarifying some of the issues involved in choosing between them. However, the study is limited and does not appreciably add to our understanding of the issues involved in choosing between hospital and population-based controls. The first limitation is that the hospital controls are from London (Ontario) while the neighborhood controls are from Ontario. Although each control group may be appropriate for its respective case series, there is no reason to believe that they are comparable to each other. Indeed, controls are usually selected from the same locale as cases because the prevalence of many exposures differs according to geographic area. The authors apparently recognize this problem, in fact, they explain some of the differences between the two control groups on this basis, but choose largely to ignore it. This is not one case-control study with two control groups, but rather two case-control studies each with its own control group. It is not relevant to the evaluation of the choice between hospital or population-based controls. The second limitation of the study is more subtle. It relates to case-control studies in general and to what issues are and are not important in selecting controls. However, to put the discussion in perspectives, I would like first to make a few general comments about case-control studies. Many scientists view case-control studies with extreme skepticism. This skepticism may arise because such studies are perceived as “unnatural” because they look back from effects to causes and because of the difficulties involved in obtaining unbiased estimates of the exposure frequencies of cases and controls. These aspects of case-control studies have led some to maintain that they are inherently non-scientific and that their validity can be enhanced by considering as their goal the duplication of the results of a randomized controlled trial. However, case-control studies differ from randomized controlled trials in that the latter are experimental whereas the former are non-experimental scientific investigations. The goal of a case-control study should be to obtain a valid estimate of the disease frequency among exposed persons relative to that among the non-exposed, not to mimic a randomized trial. This concern with their supposed unscientific nature has fostered a need to do something to enhance their validity and many epidemiologists believe that this need is fulfilled by controlling for many extraneous factors. In fact, the identification and control of confounding has become a preoccupation in case-control studies. However, although much is known about methods for controlling confounding, often little thought is given to what factors need to be controlled in case-control studies. 309
310
HARLAUD Ausrm
Miettinen and Cook recently described the properties of a confounder in a casecontrol study[l]. They maintain that a confounding factor must be a correlate of the exposure in the source population of cases and controls and that it must be a predictor of the disease or have different selection implications for cases and controls. For illustrative purposes they describe a case-control study of the effect of other than type 0 blood on the risk of coronary artery disease. They argue persuasively that since it is known, (I priori, that gender is unrelated to blood group in the source population of cases and controls. gender cannot be a confounder in this study. Thus, a control group consisting entirely of females would be suitable for a case series consisting entirely of males, at least insofar as the primary purpose of the study was concerned. This study would probably be dismissed out of hand by those who advocate the analogy to randomized trials because of the highly non-random distribution of gender (a strong risk factor for coronary artery disease) between the case and control series. These principles should be considered when selecting a control group. The choice of the control group depends crucially on both the disease and the exposure of interest. This brings up the second limitation of the paper by Stavraky and Clark. The “cases” in this study are women with cancer of the breast, ovary, lung or lymphopoietic system. The issues involved in selecting controls for a study of breast cancer are clearly not the same as those involved in selecting controls for a lung cancer study. It is not clear why the variables in their Tables 4 and 5 were selected for presentation. Do they suppose that they are all potential confounders? If so, what reasons do they have to suppose that age at menarche, the number of live births, the use of spray deoderants, etc. are related to the use of hair dyes among women in London or Toronto? Even if age at menarche were related to hair dye use, this is of no consequence to the assessment of the relationship between hair dyes and lung cancer because age at menarche has no selection implications for cases and controls in a study of lung cancer. The authors apparently hold the widespread view that control for a number of “confounders” in a case-control study enhances its validity. In Table 3 of their report they present risk ratios “adjusted by multiple logistic regression analysis for possible confounding variables”. However, they fail to mention what variables were controlled and why they believe that any of them are confounders. The problems of overadjustment in case-control studies have recently been discussed by Day et al. [Z]. These authors point out that adjustment for factors which are not confounders not only increases the variability of the estimate of the relative risk but, more importantly, may lead to bias in the risk estimate. Thus, in an attempt to enhance validity, the well-intentioned practitioner of case-control studies introduces bias into his study. It is not my purpose to diminish the importance of recognizing and controlling confounding in case-control studies. Nor do I imply that the selection of controls should be motivated solely by the intent to achieve efficient control of confounding. Rather, I wish to emphasize that in selecting controls and in analyzing the results of a case-control study, investigators should be more parsimonious in designating the factors that need to be controlled. Sometimes recognizing what is not important is just as important as recognizing what is. REFERENCES 1. 2.
Miettenen OS. Cook EF: Confounding: Essence and detection. Day NE. Byar. DP. Green SB: Overadjustment in case-control
Am J Epid 114: 593-603, 1981. Am J Epid 112: 696 706. 1980
studies.