CLINICAL STUDIES

Methodologic Standards and Contradictory Results in Case-Control Research

RALPH I. HORWITZ, M.D. ALVAN R. FEINSTEIN, M.D. New Haven, Connecticut

From the Departments of Medicine and Epidemiology and the Robert Wood Johnson Clinical Scholar Program, Yale University School of Medicine, New Haven, Connecticut. This investigation was supported in part by Grant ROl HS 00408-07 from the National Center for Health Services Research, HRA. Requests for reprints should be addressed to Dr. Ralph Horwitz, Clinical Scholar Program, Yale University School of Medicine, 333 Cedar Street, New Haven, Connecticut 06510. Manuscript accepted October 30.1978.

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Despite a reversal of the customary direction of the cause + effect reasoning used in prospective (cohort) studies, the retrospective case-control method for the study of disease etiology has become epidemiologically popular and sanctioned by authorities who claim that it rarely produces contradictory results. Nevertheless, we have found at least 17 topics in which conflicts were noted in conclusions that arose either among case-control studies or between case-control and cohort studies of the same topic. The 17 topics include the etiologic relationships of myocardial infarction to coffee-drinking and aspirin, and of various neoplastic diseases to reserpine, estrogens, coffee-drinking, herpesvirus, oral contraceptives, appendectomy, tonsillectomy, prenatal irradiation, benign prostatic hyperplasia, asthma, circumcision, early age of menarche and tuberculosis. The 85 case-control investigations of these topics were each evaluated for the fulfillment of 11 methodologic standards that would enhance scientific quality in the research. The standards include a predetermined method of patient selection, clear specification of the risk agent, unbiased collection of data, efforts to provide anamnestic equivalence, avoidance of constrained selection for cases and controls, equal diagnostic examination, equal prehospital surveillance, equal demographic and clinical susceptibility, and avoidance of protopathic bias in the compared groups. These standards, which were commonly violated in the 85 reviewed investigations, should not be used to provide a general summary score for individual studies, since the impact of each type of violation depends on the topic under investigation and must be appraised separately for that topic. Certain scientific problems of case-control studies are inherent in the research architecture, but others can be eliminated or reduced by better attention to the quality of the conventional research procedures and by special new methods of sampling and analysis. The cited standards can help readers to evaluate the results of casecontrol research and can help designers of future studies to improve their scientific structure and credibility. Retrospective case-control research has become a popular activity, with widespread acceptance in the medical community. The general approval of this relatively new form of research has been aided by assurances from epidemiologic authorities that case-control results are usually correct [1,2]. These assurances have been offered despite the

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reasonably well-known existence of errors in two old etiologic claims-that tuberculosis protected against cancer and that circumcision protected against cervical cancer-in which the initial results of case-control studies were later refuted. Another outstanding conflict recently became evident when suspicions that reserpine causes breast cancer were originally supported by three case-control studies [3-51 and later contradicted by eight [6-131.

The prominence of these opposing contentions made us wonder about possible conflicts emerging from other case-control investigations. Excluding studies of oral contraceptive agents, which we plan to discuss in a separate report, a nonexhaustive search of the literature led to 14 additional topics in which the results of one case-control study had been contradicted either by another case-control study or by cohort research. While contemplating those 17 sets of conflicting results, we began to analyze the possible methodologic reasons for the conflicts. We then developed a set of standards for evaluating scientific quality in case-control research, and we applied those standards to each of the reports that had been involved in the conflicts. This paper contains a listing of the conflicts, a description of the methodologic standards that were developed and examples of their application to the papers under review. Choice of Topics and Studies. We identified a topic as being a suspected relationship between a particular agent and a particular disease. For example, the relationships of tuberculosis-cancer, circumcision-cervical cancer or reserpine-breast cancer would be regarded as topics. Each topic also contained a specific hypothesis in which the selected agent was suspected of having either a causal role or a protective role with respect to the disease. When the topic was investigated, the hypothesis was either supported or not supported by the direction of the results. Two investigations of the same topic were regarded as contradictory if their results had opposite directions. A particular topic was selected for inclusion in this review if it had been investigated in at least one casecontrol study and if the directional results of the relationship (as supportive or non-supportive) were later contradicted by at least one other study. The contradictory study could have been performed either with case-control or cohort research. When such contradictions were encountered, all of the associated studies we could find for that topic were included for review. To ease the review process, we restricted the candidate studies to those that had been published in the English language. With this approach, we found a total of 17 topics, investigated in 95 studies of which 85 were of the case-control type, and 10 were cohorts.

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Establishment and Application of Methodologic Standards. After these directional conflicts were noted, we developed a separate set of 12 methodologic standards for case-control research. Since our concern was with the methodologic problems of casecontrol rather than cohort studies, we confined the remainder of our analysis to an evaluation of the way those standards had been attended in each of the 85 studies that were performed using case-control methods. For each study, compliance with each methodologic standard was rated according to five possible scores. A + indicates that the investigators complied with the standard: a 0, that the standard was violated. In some circumstances the standard did not receive full compliance, but no reasonable resulting bias could be inferred. In these instances a f was scored. A f was also used when the descriptive accounts of the research methods were too incomplete or ambiguous to allow a definite rating. The standard was marked not applicable (NA) in circumstances in which it did not pertain. For example, if exposure to the causal agent was assessed with objective technology, as in herpesvirus and cervical cancer, certain standards about interview methods for ascertainment would not be pertinent. Finally, certain standards, although pertinent were marked not evaluable (NE] when the necessary criteria for evaluation did not exist. For example, because clinical risk factors for breast cancer have not been unequivocally established, the question of equal clinical susceptibility was not evaluated in the groups compared for the occurrence of breast cancer. A description of each methodologic standard is presented in the section that follows, together with its rationale, examples of its application and the summary results for that standard in the 85 case-control studies. RESULTS In Table I we have listed the topics and the case-control and cohort studies under review. For each topic and hypothesis we have specified the span of years from the first published paper on the topic to the most recent paper in our analysis. For each case-control or cohort investigation, the directional results of the relationship were determined from the conclusions drawn by the investigators. If the investigators did not arrive at specific conclusions, we classified the direction of the report as supportive or nonsupportive of the stated hypothesis, according to the values noted in the various risk or odds ratios. To be considered supportive the results required an odds ratio in the data substantially greater than 1.0 for a causal hypothesis, and substantially smaller than 1.0for a protective hypothesis. Otherwise the results

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TABLE I

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Case-Control and Cohort Studies of 17 Topics Numberof StudiesThat Did or Did Not Supporl Hypothesis Years Spanned Sup by Sludles porlive

Topic and Hypothesis 1. 2. 3. 4. 5. 6. 7. 6. 9. 10. 11. 12. 13. 14. 15. 16. 17. l

Tuberculosis and cancer (protective) Normal lactation and breast cancer (protective) Circumcision and cervical cancer (protective) Prenatal irradiation and childhood leukemia (causal) Allergy and malignancy (protective) Appendectomy and neoplasia (causal) Early age at menarche and breast cancer (causal) Herpesvirus and cervical cancer (causal) Oral contraceptive pills and benign breast disease (protective) Coffee drinking and bladder cancer (causal) Tonsillectomy and Hodgkins disease (causal) Coffee drinking and myocardial infarction (causal) Benign prostatic hyperplasia and carcinoma of prostate (causal) Aspirin and myocardial infarction (protective) Risk factors and cleft lip and palate (causal) Reserpine and breast cancer (causal) Estrogens and endometrial cancer

Refers to a study that used cohort rather than case-control

Table II contains a summary of the results for the application of the 12 methodologic standards to the studies of each topic in our analysis. (The extensive tabulation of individual scores for each of the 85 studies will be made available to interested readers on request.) The remainder of this section is devoted to a separate discussion of the individual methodologic standards. Predetermined method of selection: The first methodologic standard is a predetermined method of selecting patients for the research. Regardless of how the investigators choose cases and controls, the method should be established before the research data are obtained and analyzed. The scientific purpose of this standard is obvious: to prevent the manipulation of the odds ratio, after the results have been analyzed, by altering the composition of the case or control groups. An example of the violation of this standard occurred when Armstrong et al. [4], studying the reserpine-breast cancer relationship, found that they could attain statistical significance only by discarding the original control group and creating a new one. In the summary of the 85 studies shown in Table II, compliance with this standard was scored as positive in 66 studies, negative in four studies and uncertain or unknown in 15.

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would be considered as nonsupportive. The number of such supportive and nonsupportive studies for each topic are shown in Table I, together with the specific reference identifications for each study.

1.

1929 1931-70 1954-67 1956-68 1958-75 1964-74 1956-71 1969-71 1971-76 1968-75 1971-75 1972-76 1974 7974-75 1975 7974-77 1967-77

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2. Specification of the causal agent: The next three methodologic standards are all concerned with ascertainment of the suspected causal agent. The first of these ascertainment standards requires a precise specification of what is meant by exposure to the chosen agent. The main purpose of this standard is to enable the work to be reproduced when other investigators explore the same topic. The specificational criteria should also preferably be established before the data are analyzed so that the investigator will not be tempted afterward to redefine “exposure” in a way that partitions the data most favorably for the research hypothesis. An example of violation of this standard occurred when Heinonen et al. [5], studying the association between reserpine and breast cancer, did not cite specific criteria for the pharmaceutical dosage or duration that would designate a patient as a “reserpine user.” By contrast, O’Fallon et al. [7], investigating the same topic, specified a reserpine user as having a “prescription (compliance assumed] for any concentration of the drug at any time more than six months before the defining diagnosis.” Table II indicates that compliance with this standard was noted as positive in 29 studies, negative in 18 studies and uncertain or unknown in 38. 3. Unbiased data collection: This standard is the case-control counterpart of double-blind observation in experimental cohort research. The standard is needed to avoid bias when investigators collect the information that designates

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TABLE II

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Compliance with the 12 Methodologic Crlterla in 85 Studies

ulethoddogic Crtterta

NumberotStudies inWhich Compliancewss Uncertain Positive Negative (*) (0) (+)

NotApplkXbte (NA) or Not Evstwbte(NE)

1. Predetermined method

66

4

15

0

2. Specification of the agent

29

18

36

0

3. Unbiased data collection

10

17

56

2

4. Anamnestic eauivalence

31

36

13

5

5. Avoidance of constrained cases

51

3

31

0

6. Avoidance of constrained controls

47

10

26

0

7. Equal diagnostic examination

12

61

10

2

8. Equal diagnostic surveillance

4

36

0

45

71

12

2

0

10. Equal clinical susceptibility

7

9

0

69

11. Avoidance of protopathic bias

1

15

1

68

31

54

0

0

9. Equal demographic susceptibility

12. “Community control” for Berkson’s bias

groups as exposed or not exposed to the alleged causal agent. The person who performs the data collection should be kept unaware of both the hypothesis being tested and the identity of the subject as acaseor control. An example of potentially biased data collection occurred when Mack et al. [8], investigating the association between reserpine and breast cancer, noted that the process of abstracting data from medical records “could not be kept blind.” Consequently, the data collectors would have had the opportunity to record the information in a manner favorable to the hypothesis of the investigators. As summarized in Table II, this criterion was scored as positive in 10 studies, negative in 17 studies, uncertain in 56 studies and not applicable in two. Anamnestic equivalence: Anamnestic equivalence is needed not to avoid bias in the interviewer, but to avoid bias in the patient’s memories. The purpose of this standard is to minimize inequalities among cases and controls in the patient’s ability or incentive to recall previous exposure to the allegedly causal agent. For example, in contrast to the mother of a normal child, the distressed mother of a leukemic child is more likely to have contemplated all the drugs, roentgenograms and illnesses that occurred during the associated pregnancy. Consequently, when an interviewer inquired about prenatal irradiation, the mothers of leukemic children may have remembered an exposure that mothers of normal children might have forgotten. 4.

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As summarized in Table II, this criterion was scored as positive in 31 studies, negative in 36, uncertain in 13 and not applicable in five. 5. Avoidance of constrained cases and 6. Avoidance of constrained controls: These two standards are intended to prevent the constraints that may create bias during arbitrary decisions about the selection of cases and controls. In excluding certain kinds of patients from the potential candidates for either the case or control groups, the investigator may inadvertently eliminate people with particularly high or low rates of exposure to the suspected causal agent. Consequently, the proportionate rate of exposure to that agent may be falsely lowered or raised for the people who remain as the cases or controls. To help avoid this problem, whenever the investigators decide to study a particular subset of the available population, the constraint should be applied equally to the selection of the cases and controls. An example of constrained controls occurred in the reserpine-breast cancer topic when patients with thyrotoxicosis, renal disease or cardiovascular disease were excluded from the control groups [3,5]. Since patients with such diseases are particularly likely to be receiving reserpine, their exclusion would probably decrease the exposure rate to reserpine among the controls and would artificially elevate the odds ratio, As summarized in Table II, the criterion for avoidance of constrained cases received positive compliance in 51

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studies. The criterion for avoidance controls was positive in 47 studies.

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of constrained

7. Equal diagnostic examination: The seventh and eighth methodologic standards deal with problems in detection of the target disease. Equal diagnostic examination is needed to check that in both cases and controls similar procedures and criteria have been utilized for the diagnosis of the disease. The purpose of this standard is to ensure that members of the control group are free of the disease being studied. Fulfillment of this standard is particularly important when the target disease is an ailment, such as cancer, that can occur in an asymptomatic form, allowing the disease to escape detection unless specifically sought. An example of this problem occurred in one of the reserpine and breast cancer studies [3], when the controls were selected from among women hospitalized for cataracts, dental disease or hemorrhoids. Patients admitted to the hospital with these conditions may undergo either no examination of the breasts or examinations that are too perfunctory to detect an asymptomatic breast lesion. Even if the diagnostic test were performed for all members of the case and control groups, however, diagnostic examination bias can still occur if the findings were not interpreted with the same criteria for all patients. For example, in the histologic interpretation of endometrial curettings of uterine tissues, most gynecologic pathologists might agree on the diagnosis of poorly differentiated, advanced-stage adenocarcinoma of the endometrium, but the diagnosis of well-differentiated, noninvasive lesions is troublesome. In fact, the distinction between atypical adenomatous hyperplasia and w8lLdifferentiated, stage 1 cancer of the uterus is challenging even to the most skilled pathofogists. Faced with this uncertainty, pathologists may select from among diagnostic alternatives the decision that offers the patient the greatest benefit. The uncertainty between benign hyperplasia and well-differentiated stage 1 cancer might thus be resolved by designating the lesion as malignant. If the pathologist interpreting the slides knows that the patient was taking estrogens, he may feel even more justified in diagnosing cancer since the hormones have long been suspected of encouraging the growth of neoplasia. To avoid these potential sources of bias in the performance and interpretation of diagnostic tests, similar examination procedures should have been utilized in cases and controls. The tissue retrieved from these procedures should be interpreted with similar diagnostic criteria by a pathologist who is preferably unaware of the patient’s history of exposure to estrogens. As summarized in Table II, this criterion ‘was scored as positive in 12studies, negative in 61 studies, uncertain in 10and not applicable in two.

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Equal prehospital surveillance: This important principle refers to events that occur before a person is assigned to a case or control group. The issue is not [as in the previous methodologic standard] equal care and criteria for performance of the diagnostic examination that distinguished a “case” from a “control.” The issue here is whether an examination was made before hospitalization to allow the exposed or unexposed people an equal chance to become detected as cases. For example, in the relationship of reserpine and breast cancer, patients taking reserpine are under: regular medical surveillance. They are, thereby, more likely to have an asymptomatic breast lesion detected because their breasts are more likely to be examined than patients who are not taking reserpine and are not under medical surveillance. Since these “screening” tests usually are performed before a patient enters a hospital to become a “case,” a check for equality in the intensity of previous diagnostic surveillance cannot be performed merely by examining the hospitalized patients in the case and control groups. A separate, special strategy is needed. If exposure to the etiologic agent can also lead to an increased intensity or frequency of the examination procedures that detect asymptomatic or subclinical disease, a separate control group should be sought from among people who received similar diagnostic surveillance. One way to achieve this equal diagnostic surveillance is to insist that the appropriate diagnostic test be utilized in both the cases and controls, and to stratify the analyses according to whether the disease was previously suspected, so that the patient was referred to the hospital specifically to receive that test. Again, using the topic of reserpine and breast cancer as an example, we might suspect that patients taking reserpine, in contrast to general population controls, are more likely to have the necessary examination that would disclose an otherwise asymptomatic breast cancer. Consequently, to achieve more comparable rates of diagnostic surveillance among cases and controls, we might use as our sampling frame all patients who undergo mammography or surgery for breast lumps. Cases and controls would emerge naturally from this group as the disease or absence of disease is determined at the time of the procedure. This choice of sampling frame would help to equalize the rates of diagnostic surveillance among the cases and controls. As summarized in Table II, this criterion was applicable in 40 studies, of which only four were positive for fulfillment of the standard.

8.

9. Equal demographic susceptibility: This standard is needed to check that the patients in both groups (cases and controls) are similar in age, gender and other variables that might affect the development of the target disease in exposed and nonexposed people. As shown in Table II, this standard was met in 71 studies.

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10. Equal clinical susceptibility: In the relatively few circumstances in which pertinent clinical features are known to be risk factors that predispose people to the development of a disease, this standard would be required to check whether the patients in these groups were clinically similar in their proportionate susceptibility to the development of the target disease. Examples of such factors are elevated cholesterol levels and hypertension as risk factors for the development of myocardial infarction. Since the clinical “risk” factors for most cancers are either uncertain or controversial, we applied this standard only for topics in which the clinical “risk” factors have been clearly identified and generally accepted. Among the 16 studies in which the standard of equal clinical susceptibility could be evaluated, the standard was fulfilled in seven [Table II). 11. Avoidance of protopathic bias: This unusual form of bias needs a special name. Suppose the target disease has already developed in a patient but its existence has not yet been suspected or diagnosed. Suppose also that the disease has an early [or protopathic) manifestation which becomes the stimulus that influences the prescription (or cessation] of the alleged etiologic agent. For example, hormonal therapy may be prescribed in an effort to control the bleeding of a postmenopausal woman with metrorrhagia and no abnormalities in the routine pelvic examination and cervical pap smear. If the, bleeding happens to be the earliest manifestation of an endometrial cancer, however, the cancer may later be detected with the same or with other diagnostic tests. After detection, the cancer may then be falsely ascribed to the hormonal therapy although it actually antedated the treatment. If such protopathic manifestations lead to the preferential prescription of a pharmaceutical agent, the subsequent association between disease and agent will obviously be biased. Perhaps the best way to avoid this bias in case-control research is to determine why the etiologic agent was prescribed for each patient in the case and control groups, and to analyze the data according to appropriate strata of the manifestations that evoked prescription. This standard was applicable whenever a protopathic relationship could be suspected of having existed between a target disease and a suspected pharmaceutical agent. An example of this problem occurs in the topic of oral contraceptives and benign breast disease, because benign breast disease may present clinically with the development of painful, tender breasts, long before biopsy evidence is obtained to support the diagnosis. In the patients with this symptom, however, the physician may promptly discontinue the use of oral contraceptive agents or never prescribe them at all, and a biopsy procedure may not be performed until many months

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later when a prominent lump is noted. When such a patient is entered into the case-control study, she is assigned to the case group and is recorded as an oralcontraceptive nonuser. Because of the protopathic discontinuation or avoidance of the pharmaceutical agent, patients with benign breast disease may thus have a falsely low rate of oral contraceptive usage, leading to the erroneous conclusion that the agent is protective

@31. As shown in Table II, among the 17 studies in which this standard was applicable, one was positive, 15 were negative, and one was uncertain. 12. Avoidance of Berkson’s bias: An optional standard: An additional source of bias can arise in casecontrol research because the people who are both exposed and diseased are more likely to be admitted to the hospital than are other groups of people. The mathematical basis for this bias was first described theoretically by Berkson [94] and was later demonstrated empirically by Roberts et al. [%I. We have regarded this standard as optional because the customary procedure recommended for avoidance of Berkson’s bias is actually ineffective. The customary recommendation is to choose the control group from a community population, rather than from other hospitalized patients. (As shown in Table II, a control group was chosen from a community population in 31 of the case-control studies under review.) Since Be&son’s bias arises in the “case” group, because of increased hospitalization for the subpopulation that is both exposed and diseased, a change in the control group from a hospital to a community source will not eliminate the problem. Berkson’s bias could be removed only if the cases and controls were selected from the same community roster-a tactic that is rarely possible. CONCLUSIONS Because the papers and topics included in this report were selected for their contradictory features, the results do not necessarily represent the spectrum of case-control research. We have not intentionally selected bad or good studies, nor have we intentionally excluded research that complied with the methodologic standards. Our goal was to find methodologic principles that could provide explanations for the contradictions, and when appropriate, many of the conflicting papers could be used as examples in which the standards were violated. Because of the diverse ways in which bias can be introduced into case-control research, the array of positive or negative ratings for these methodologic standards cannot be added together to form a single “score” for each study. An investigation that fulfills all but one of the standards might receive a high total “score,” but might nevertheless produce erroneous results if the

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remaining standard is violated in a way that creates a crucial source of bias for that topic. Conversely, an investigation with relatively low scores may still reach correct conclusions if the standards that were violated are not critically important for the topic under study. For this reason, the methodologic standards that have been noted here should be used as guides rather than grades. The relative importance of each standard will depend on the particular topic and particular association that is under investigation. Some of the defects in case-control research are entirely produced by the investigative procedures and can be eliminated with better attention to the quality of conventional research strategies. Among such procedures are the use of a predetermined method for choosing patients, the avoidance of constraints in the choices of cases and controls, and improved technics for ascertaining exposure to the causal agent. Other defects, however, are not

so readily amenable to the investigator’s jurisdiction. They include sources of protopathic bias, differences in clinical susceptibility and inequalities in prehospital surveillance among community members who are exposed or nonexposed to the causal agent. To correct these sources of bias will require special new methods of sampling and analysis. Case-control studies can be an important research tool in the study of chronic diseases in which cohort investigations are not feasible. To achieve this importance, however, the methods of case-control research require major scientific improvements to help remove or avoid bias in the groups selected for study and in the data collected. The 11methodologic standards compiled in this review offer useful guidelines for the evaluation of case-control research and can help to improve quality in its design.

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Volume 66

Methodologic standards and contradictory results in case-control research.

CLINICAL STUDIES Methodologic Standards and Contradictory Results in Case-Control Research RALPH I. HORWITZ, M.D. ALVAN R. FEINSTEIN, M.D. New Haven...
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