Critical appraisal of a matched case–control study
Abstract and Keywords
This chapter presents an example of the application of the scheme for critical appraisal: a small matched case-control study entitled ‘Increased risk of endometrial carcinoma among users of conjugated estrogens’, published in the New England Journal of Medicine in 1975. The study is the first publication showing an important relationship between a disease and a widely used drug. It was chosen because it is now of historical importance, and is a good example of an individually matched study with several issues of interpretation. In addition, it shows an interesting way of assessing confounding, which is valid although not usually used in current studies.
In this chapter, we review a small matched case–control study, which was the first publication showing an important relationship between a disease and a widely used drug. It has been chosen because it is now of historical importance, and is a good example of an individually matched study with several issues of interpretation. In addition, it shows an interesting way of assessing confounding, which is valid although not usually used in current studies. The abstract, methods, and results are reproduced here, with the permission of the first author and the journal (excerpted with permission from the publishers from the New England Journal of Medicine, 4 December 1975, 293, 1167–1170. Copyright 1975 Massachusetts Medical Society. All rights reserved).
The possibility that the use of conjugated estrogens increases the risk of endometrial carcinoma was investigated in patients and a twofold age-matched control series from the same population. Conjugated estrogens (principally sodium estrone sulfate) use was recorded for 57 per cent of 94 patients with endometrial carcinoma, and for 15 per cent of controls. The corresponding point estimate of the (instantaneous) risk ratio was 7.6 with a one-sided 95 per cent lower confidence limit of 4.7. The risk-ratio estimate increased with duration of exposure: from 5.6 for 1 to 4.9 years’ exposure to 13.9 for seven or more years. The estimated proportion of cases related to conjugated estrogens, the etiologic fraction, was 50 per cent with a one-sided 95 per cent lower confidence limit of 41 per cent. These data suggest that conjugated estrogens have an etiologic role in endometrial carcinoma.
(p.454) Subjects and Methods
Between July 1, 1970, and December 31, 1974, the diagnosis of endometrial cancer was made in 94 patients at the Kaiser Permanente Medical Center, Los Angeles, and reported to its tumour registry. The criterion for the definition of endometrial cancer was a pathological diagnosis of endometrial adenocarcinoma or adenocanthoma; mixed Müllerian sarcoma and choriocarcinoma were excluded.
Control subjects were selected in the following way. The membership files of the Southern Californian Kaiser Foundation Health Plan population were reviewed, and all members in the vicinity of the Los Angeles facility whose record designations ended in arbitrarily selected numbers were identified and listed. From the list, two control subjects were selected for each patient and matched for birth date within one year, area of residence by postal zip code, duration of Health Plan membership (each control subject had been a member at least as long as the associated patient), and potential for the development of endometrial cancer by the control subject’s having an intact uterus. The patient and the two control subjects thus constituted a matched triple.
The data source for the 94 matched triples was the clinic record. To avoid information bias that could result from the more probing clinical history taken after identification of the cancer, the following procedure was employed for each matched triple. A medical-records clerk requested all three records from the record room and reviewed those of the control subjects to determine whether they had an intact uterus. Subjects without an intact uterus were replaced by selection of others from the original list. The clerk determined the date of diagnosis for each patient, and then the date one year before that diagnosis (the reference date). The clerk concealed all information in the record after the reference date. For control subjects, information recorded during the same period was similarly concealed. The record was then given to an abstractor, who filled out the abstract form without knowing whether the record was that of a patient or a control.
For any given triple, there were six possible combinations of conjugated-estrogen use; all three were users; the patient and one of the control subjects were users; and so forth. The observed frequencies for each of the six possible combinations for each of the 94 triples are shown in Table 1. These data were used to estimate the risk ratio associated with the use of conjugated estrogens and the etiologic (p.455) fraction (the proportion of cases due to conjugated estrogens). The (maximum-likelihood) point estimate of the relative risk () is 7.6. The significance test statistic is 49 (P ≪ 10−8). The approximate 95 per cent one-sided lower confidence limit of the risk ratio (RR) is 4.7. The point estimate of the etiologic fraction () is 50 per cent. For this parameter, Miettinen’s proposed (test-based) computation of the 95 per cent one-sided lower confidence limit (EF) yields 41 per cent.
Data on the relative risk ratio to duration of exposure are given in Table 2. Even with only 1.0 to 4.9 years of use, the point estimate is 5.6, with a corresponding 95 per cent one-sided confidence limit of 2.7. For uses of less than one year’s duration, the data are too scanty to be informative.
A. Description of the evidence
1. What was the exposure or intervention?
2. What was the outcome?
3. What was the study design?
4. What was the study population?
5. What was the main result?
The exposure is the use of conjugated estrogenic drugs, as recorded in medical records up to 1 year before the date of diagnosis of the cases, or the equivalent time for the controls (we will use the American spelling in this chapter). The outcome is the pathologically confirmed diagnosis of endometrial adenocarcinoma or adenocanthoma. The design is an individually matched retrospective casestudy. The case subjects were diagnosed at the Kaiser Permanente Medical Centre between 1970 and 1974, and were reported to its tumour registry. For each case, two controls were chosen from the membership files of the health plan which operates this hospital, matched for birth date within 1 year, area of residence by postal code, duration of health plan membership, and possession of an intact uterus. The main result of the study was that estrogen use was recorded in 57 per cent of cases and in 15 per cent of controls, giving an odds ratio of 7.6 for ‘ever use’ (Ex. 14.1). The note at the end of this chapter explains how this is calculated.
B. Internal validity – consideration of non-causal explanations
6. Are the results likely to be affected by observation bias?
Since this is a case–control study, the major problems relate to the assessment of exposure. Assessment of disease status is straightforward. For the cases, this was (p.456)
The information on estrogen use is based on a medical record review done in a blind fashion. One clerk obtained the records for each set of cases and controls, and concealed all information recorded after a reference date 1 year before the date of diagnosis for the case, and a corresponding date for the controls. A different clerk abstracted the information from each record, without knowing whether the record belonged to a case or a control. Further information on the quality of the medical records would be helpful, in particular any independent assessment of the completeness and accuracy of drug recording. There could be substantial under-reporting of drug usage, as drugs might have been used that were not prescribed within this particular health plan, or were not recorded; also, some drugs prescribed may not have been used. Such errors, if randomly distributed amongst all subjects, would serve only to reduce the observed association. The crucial question is whether there is any likelihood of estrogen use being more completely recorded in those subjects who were later diagnosed as have endometrial cancer than in the control subjects. The blindness of the abstraction, and the exclusion of any material relating to the (p.457) period 1 year before diagnosis provides some protection. Could other factors affect this? Endometrial cancer is more common in the higher socio-economic groups. Might such patients have more completely recorded drug histories? This seems unlikely as all the study participants used the same health care system. Is it possible that patients who eventually were diagnosed with endometrial cancer had a more frequent history of gynaecological and related problems, resulting not only in a greater prescribing of these drugs but also a greater recording of such prescribing? For parity, obesity, and age at menopause, the data were more complete for the cases than for the controls. Could the information on estrogens also be more complete? Counter-arguments are that no excess was seen for several other drugs, an indication for the use of estrogens was recorded more frequently in the controls, and that the association was very strong (see below). It seems unwise to accept totally results based on review of one medical record, without independent verification, and the issue of observation bias cannot be dismissed.
7. Are the results likely to be affected by confounding?
The subjects were matched by age, area of residence (which probably gives some measure of socio-economic matching), and duration of health plan membership; a matched analysis has been performed. Potential confounding factors are those related both to the incidence of endometrial cancer and to the use of estrogenic drugs. The literature on endometrial cancer was reviewed in the paper; at that time there were several recognized risk factors such as high parity, obesity, and late age at menopause. For each of these, the authors used information from the medical records to assess the confounding effect by stratified analysis. Substantial data were missing on each of these topics. Rather than presenting unconfounded odds ratio estimates obtained from the stratified analysis, the authors have used a less familiar technique in calculating the ‘confounding risk ratio’, which is a measure of the extent to which the association is produced by confounding. An explanation of this method is given at the end of this chapter. The confounding effect for each of the three factors of parity, obesity, and age at menopause is very minor, but the analysis is limited by the missing data. No other confounding factors had been shown to have major associations. Some protection against the observed association being due to confounding is given by the strength of the association; the odds ratio is high compared with the odds ratio of 1.5–3 usually quoted for factors such as parity or obesity.
At the time this paper was published there was little written on the factors related to estrogen use. Of prime importance is the indication for estrogen usage, as the observed association with the drug could be disguising a true association with the indication for the drug. The indications for the use of (p.458) conjugated estrogens are unclear, and must reflect psychological and social as well as medical factors. The most frequently recorded indication was hot flashes. If the case patients used more estrogenic drugs, and if the indications for use of estrogens were the same in cases and controls, this implies that the case subjects suffered from hot flashes more frequently than did the controls, suffered from them more severely, sought treatment more readily, or for some other reason were given these drugs as treatment more readily. Thus there is a competing hypothesis that endometrial cancer could be related to hot flashes. A further possibility is that cases might have a high usage of drugs in general; this can be dismissed as the cases were recorded as using diazepam, reserpine, and thyroid drugs less commonly than were the controls. Thus there is protection against confounding by most of the major known risk factors for endometrial carcinoma. However, there is a viable alternative hypothesis to causation—that the disease is related not to the use of estrogens but to the indications for their use.
8. Are the results likely to be affected by chance variation?
The estimated odds ratio is 7.6, and the associated P-value is less than 10−8, giving 95 per cent two-sided confidence limits of 4.3 and 13.4. Thus chance variation can be excluded. The methods used in the statistical analysis are a little different from those presented in this text; a note on them is given at the end of this chapter. Some publications will use more complex methods than those described in this book, which may have particular advantages for that study. However, the results should differ greatly from those obtained by the methods described here. The reader might like to apply the methods for analysis of a matched case–control study that are presented in Appendix Table 6. These give an odds ratio of 8.2, and an associated χ2 statistic of 48.8.
Summary: non-causal explanations
Thus of the three non-causal explanations, we can effectively exclude chance, but must keep in mind the possibilities of observation bias and of confounding, particularly by the indication for drug usage.
C. Internal validity: consideration of positive features of causation
9. Is there a correct time relationship?
This study, as is common with case–control studies, is fairly weak with regard to time relationships. The method of data collection has the important feature (p.459) of excluding any information recorded in the year before clinical diagnosis, and therefore we can conclude that the drugs assessed were prescribed before the endometrial cancer was diagnosed. But could the disease or its precursor have been present even earlier, and have produced symptoms which led to the prescription for the drugs? We do not know if any of the case subjects had previous tests (e.g. a curettage) that would have detected the disease or a related state such as hyperplasia. The time relationship is not clear; no data for risk by time since first use of estrogens are given. As it is unlikely that the records go back many years, we assume that the risk is seen only a few years from first exposure. This appears inconsistent with a cancer initiator action, which typically takes decades; if the risk is causal, it shows a short-term action.
10. Is the association strong?
The relationship is strong, with a high odds ratio of 7.6. This odds ratio is greater than those associated with even extremes of parity, obesity, late menopause, and other recognized risk factors for endometrial carcinoma, making it unlikely that this association could be produced by confounding by such factors. However, it is no protection against the association being due to the indication for the drug rather than the usage of the drug, as the association between these two may be very close. To assess its relevance for observation bias, it is useful to go to the raw data, which show that estrogen use was recorded for 57 per cent of the case subjects compared with 15 per cent of the controls. Thus for the association to be totally due to observation bias would require, for example, that estrogen use was always recorded for the case subjects, but recorded on only about 25 per cent of occasions for the controls; this seems implausible. Thus the strength of the association protects against some aspects of confounding and against observation bias, but not against what is emerging as the chief competing hypothesis—an association with the indication rather than with the drug prescribed.
11. Is there a dose-response relationship?
Information on this is limited by the completeness of the records, but the data in Ex. 14.2 show the odds ratio increasing from shorter to longer exposures. While the odds ratios for each exposure category are significantly different from the unexposed, a test for trend is not included. This dose-response is not very helpful; it could occur if the relationship were produced by confounding by the indication for the drug, or even from observation bias. Information on the relationship between risk and time since first use or since last use might be of more help, but is not given.
13. Is there any specificity within the study?
The association shows some specificity, as no increased risks were seen with diazepam, reserpine, and thyroid drugs. This protects mainly against gross observation bias, i.e. the possibility that all drugs would be recorded more frequently for the cases. Beyond that, a separation of patients with different indications for the use of the estrogen drugs would be helpful, but this would probably need a special study rather than one using routine medical records. Separation of different estrogenic preparations would also help, but there is no information on the precise preparations used. An association with a particular drug is more convincing if no association is seen with other drugs used for the same indications.
Conclusions with regard to internal validity
The second part of our assessment of internal validity has not been particularly helpful, and this is often the situation in assessing a relatively small study. Larger studies give more opportunity to assess consistency between subgroups, dose-response relationships, and so on. Therefore the assessment of internal validity depends on the comparison of the causal hypothesis with the alternatives of bias and confounding. The main alternative hypothesis is that the association is not due to the drug itself, but to the symptoms for which the drug has been prescribed, which might be caused by the developing carcinoma, or be indications of an altered physiological state produced by mechanisms akin to (p.461) those producing the tumour. To assess this alternative we need information from other studies, as will be seen.
D. External validity: generalization of the results
14. Can the study results to applied to the eligible population?
The eligible population comprises the members of the Kaiser Foundation Health Plan, and there is little problem applying the results to them. If we accept that they would all attend this medical centre and that the tumour registry is efficient, all patients with a histological diagnosis during the stated time period were included, and medical records on all of them were obtained. The control subjects, apart from the appropriate matching criteria, should be representative of unaffected members of the plan, with the limitation that they include only women with an intact uterus. This is an appropriate criterion, both on the argument that women without a uterus are not at risk of developing endometrial cancer and therefore are not eligible as cases, and also because women who have had their uterus removed may be different in terms of estrogen usage.
15. Can the study results be applied to the source population?
The source and eligible populations in this study are essentially the same.
16. Can the study results be applied to other relevant populations?
The study was done on members of the Kaiser Foundation Health Plan diagnosed between 1970 and 1974 in Los Angeles. Are members of this health plan different from women in Los Angeles in general? Further information would be required, but we might assume that plan members are likely to be fairly affluent stable subjects, who can afford a comprehensive prepaid health plan. No information is given on racial origin. However, the representativeness of the subjects in the study is not the most important issue. The main question is: Is the association seen likely to apply to other women? If the true relationship is between the drug and the disease, the finding is likely to be widely applicable. In other populations, the value of the odds ratio may be considerably different, depending on the usual dosage and length of time the drugs are used. If the true association is with a specific type of drug, the association may not be seen in societies where other types are used. Even if the association is consistent, its importance will depend on the type, frequency, and dosage of the drugs used, and on the level of background incidence of endometrial (p.462) cancer, produced by other factors. In this study population, a strong association is seen with a drug used frequently—in 15 per cent of controls; the attributable proportion is 87 per cent in those exposed and 50 per cent in the population—if causal, estrogens are the main cause of the disease. (These calculations are shown at the end of this chapter.)
E. Comparison of the results with other evidence
17. Are the results consistent with other evidence, particularly evidence from studies of similar or more powerful study design?
This study was chosen because it was one of the first to suggest this association. In the same issue of the same journal another case–control study, from Seattle, was published, showing a similar association, and this strengthens the credibility of these results . However, if this other study is assessed, bearing in mind the conclusion we have reached on the present study, i.e. that the association is likely to be either causal or due to an association between the indication for the drug and endometrial cancer, we find that the same limitation applies to its interpretation. Because of the importance of the association suggested, these two papers were followed reasonably rapidly by several other case–control studies and some cohort studies. There have been randomized trials of estrogen use, but these have been too small to assess the outcome of endometrial cancer.
18. Does the total evidence suggest any specificity?
At the time this paper was published there was no relevant information. However, several later studies confirmed the association in the USA, where conjugated estrogens were used widely, whereas studies in some other countries showed no risk because the use of conjugated estrogens was much less. It appears that patients who would be treated with conjugated estrogens in the USA would be treated with a mixture of estrogens and progestogens in Europe, and this combination did not appear to confer a marked increased risk of endometrial cancer.
19. Are the results plausible in terms of a biological mechanism?
The authors review epidemiological and experimental evidence that estrogens may produce endometrial cancer, and the association seems biologically acceptable. The time issue is relevant. Cancer-initiating factors produce tumours only many years after exposure, but this association does not fit this pattern. Hormones in general are not initiators of cancer, but act as cancer promoters, and this action would be consistent with a short-term effect.
(p.463) 20. If a major effect is shown, is it coherent with the distribution of the exposure and the outcome?
This study does show a major effect, and the authors calculated that in this population approximately 50 per cent of endometrial cancer was caused by these drugs, if the association they have shown is causal. They also noted that the usage of these drugs quadrupled between 1962 and 1973, and therefore a noticeable increase in the incidence of endometrial carcinoma in the USA would be expected. They reviewed the literature available at that time, which did not show any such increase, but pointed out that an increase might be disguised by an increase in the prevalence of hysterectomy for non-cancer reasons. Subsequent work published some months later, using better information, did show a substantial rise in the incidence of endometrial cancer in the USA. Strong evidence of causality is given by the trends in the years after the publication of this and other studies; there was a reduction in the prescribing of these drugs, and a fairly rapid reduction in the incidence of this tumour [3,4]. As well as the time relationship, we would expect the excess incidence to occur in geographical areas, and in social groups, in which the usage of these estrogenic drugs was maximum, and the difference between American and European experience in this regard has already been mentioned.
Coherence is the item on which the two major hypotheses can be separated. If the association with the drug is merely indicating a true association with symptoms, the rapid rise in use of the drugs will not affect the incidence rate, while a direct effect of the magnitude given will have doubled the previous incidence in this population. Thus, given the size of the effect, there should be a close association between the use of these drugs and the incidence of endometrial cancer in terms of time, place, and person. If the real relationship is with the indication, no such associations will be found. Therefore the concordance of drug usage and disease subsequently shown between countries, social groups, and over time is crucial.
The study shows a large and important association, which is most likely to be due to one of two mechanisms; either a causal relationship between the use of these particular drugs and the development of endometrial cancer, or an association between the indications for those drugs and an increased risk of endometrial cancer (Ex. 14.3). There are other possibilities, that the result reflects other confounding factors, or that it is produced by observation bias with regard to the medical records on which the data on estrogen exposure were based, but these seem less likely. If the association is real, it is likely to (p.464) (p.465)
Thus, in assessing priorities for further investigation and for critical reading of subsequent results, we shall look particularly for studies that can differentiate between a direct effect of the drug and an effect of the indications for the drug. One piece of evidence that has already been noted is the secular variation in the incidence of the disease. Studies in other countries, where women presumably have the same sort of symptoms but may be treated differently, are helpful. Other than that, we look for studies using more reliable methods of assessing drug exposure, perhaps medical records supplemented by independent reviews or direct interviews, even though recall bias may then become an issue. Prospective studies of users of these drugs would be useful, and the ultimate would be a trial in which women regarded as eligible for treatment with conjugated estrogens were randomized either to receive such treatment or to receive a non-estrogen alternative. However, to mount such a study would be extremely difficult in terms of the number of women required, and also might be regarded as unethical. Randomized trials have been set up to look at the short-term effects of estrogens, such as the relief of symptoms, but are not large enough to look at cancer incidence.
This paper, and the other case–control study published simultaneously , provided the first information on an important relationship between estrogenic drugs and endometrial cancer. The studies raised much controversy and were vigorously criticized, primarily by gynaecologists who had used the drugs (p.466) clinically for many years and were reluctant to accept epidemiological evidence of a major hazard. In arguments reminiscent of the debate concerning smoking and lung cancer in the 1950s, some of the criticisms were along the lines that case–control studies could not demonstrate causation. One anonymous editorialist in a prominent journal (The Lancet) criticized the studies on the grounds that they were not prospective and randomized, without discussing the reality that a prospective randomized trial to answer this question would be logistically extremely difficult because of the numbers required, and of course ethically dubious . In response to this, the authors of one of the observational studies commented that if such rules of evidence were applied generally, even the cause of pregnancy could not be regarded as established .
The main more serious controversy related to the difficulty of separating an association with the drug itself from an association with the indications for the drug. Studies comparing patients with endometrial cancer with other patients attending the same gynaecological services who had had similar presenting symptoms, such as uterine bleeding, showed similar rates of estrogen usage and therefore no association. However, subsequent studies demonstrated that the most reasonable explanation for these results was that estrogenic drugs caused both benign hyperplasia leading to bleeding, and also endometrial cancer . Further work also established that if estrogenic preparations were used together with progestogens, the risk of endometrial cancer was no longer increased, thus providing a management plan that could avoid this problem. Endometrial cancer risk is increased approximately 10-fold after prolonged estrogen use. However, the tumours produced tend to be diagnosed earlier because they bleed easily, and are usually of low grade and stage with an excellent prognosis . With the benefit of hindsight, this association between endometrial cancer and estrogenic drugs represents an example of an important aetiological relationship being first demonstrated in retrospective case–control studies.
Thirty years on, the association of estrogen drugs with endometrial cancer is accepted, and use of estrogenic drugs alone is regarded as contraindicated in women with an intact uterus . A meta-analysis of 30 observational studies showed an overall relative risk estimate of 2.3 comparing users with non-users, rising to 9.5 after 10 years of use . A Cochrane systematic review of 15 randomized trials and a further meta-analysis of both trials and observational studies have been done [11,12], which showed that combined estrogen and progesterone therapy does not increase endometrial cancer risk. Although these drugs do control menopausal symptoms, their longer-term risks and benefits are still controversial.
The US Preventive Services Task Force has assessed the risks and benefits of this therapy. They concluded that, while both unopposed estrogen and (p.467) estrogen-progesterone combined therapy reduced the risk of fractures, both may increase the risk of stroke, dementia, and impaired cognitive function (all with ‘fair’ evidence using the Task Force’s classification, described in Chapter 9), and venous thromboembolism (good evidence for combined therapy, fair for estrogen alone). In addition, combined therapy increased breast cancer (good evidence) and may decrease colorectal cancer (fair evidence). Neither therapy confers any reduction in the risk of heart disease, despite earlier evidence. On the basis of all the evidence, the US Preventive Services Task Force recommends against the use of either combined or unopposed estrogen for the prevention of chronic conditions, at grade D (‘at least fair evidence that the intervention is ineffective or that harms outweigh benefits’) .
The analysis used in the paper by Ziel and Finkle
The basic data for this matched case–control study with two controls per case are given in Ex. 14.1. The formula shown in Appendix Table 6 gives an odds ratio of 8.2. This is rather different from the maximum likelihood point estimate calculated by the authors by a more complicated iterative procedure, which is 7.6, and such disparity is to be expected with these relatively small numbers. The chi-squared statistic, calculated by the variant of the Mantel–Haenszel procedure given in Appendix Table 6 is 48.8, identical with that given in the paper. A chi statistic of 6.98 is out of the range of most conventional tables; but using the function shown in Appendix Table 16 gives the corresponding two-sided P-value as <10−9.
The odds ratio calculated from an unmatched analysis can also be derived from Ex. 14.1, which gives a value of 7.4; the difference between this and the result of the matched paired analysis is small. In Ex. 14.2, where small numbers are subdivided by duration of exposure, unmatched analyses are used, and the appropriate chi-squared statistic can be derived by the usual formula for case–control studies given in Appendix Table 1; an exact test (Appendix Table 4) and a test for trend (Appendix Table 7) can also be applied.
The test-based confidence limits calculated in the paper use the test-based method shown in Ex. 7.7, incorporating the maximum likelihood point estimate of odds ratio derived by the authors and the chi statistic of 6.98.
Control of confounding
Briefly, the confounding risk ratio  is the odds ratio linking exposure to outcome, which is produced by the confounder; it can be thought of as the risk ratio which would be observed in the absence of any direct association. If there (p.468) is no confounding, it will be 1.0; if the crude association is totally due to confounding, the confounding risk ratio will equal the crude risk ratio. The crude risk ratio ORc, the confounding risk ratio ORf, and the unconfounded or standardized risk ratio ORs are simply related as follows:
ORc = ORf × ORs.
Thus controlling for parity gives a crude odds ratio (ORc) for estrogens and endometrial cancer of 6.71 (different from the risk for the whole study because of the missing data), and a confounding odds ratio ORf of 1.18 (showing very little confounding). The unconfounded odds ratio ORs is given by 6.71/1.18 = 5.69. The authors also calculate a ‘confounding effect’ relating the extent of confounding to the size of the unconfounded risk ratio, giving (1.18 − 1)/(5.69 − 1) = 4 per cent.
Using the formulae shown in Ex. 3.6, the overall odds ratio is 7.6 and the proportion p of controls exposed is 15 per cent (Ex. 14.1). The attributable proportion (= ‘aetiological fraction’) in those exposed is
(OR − 1)/OR = 87 per cent
and the attributable proportion in the population is
p(OR − 1)/(p(OR − 1) + 1) = 50 per cent.
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