Journal of and Community Health 1990; 44: 179-186 J Epidemiol Community Health: first published as 10.1136/jech.44.3.179 on 1 September 1990. Downloaded from

REVIEW ARTICLE: Research methods in epidemiology, V

Bias in case-control studies. A review

Jacek A Kopec, John M Esdaile

It has been widely accepted that one reason for Greenland and Morgenstern, case-control studies inconsistent or contradictory results of are distinguished from cohort studies by their use epidemiologic studies is . Therefore, an of "outcome-selective ".1o Miettinen appreciation of potential sources of bias has rejects the case-control versus cohort duality become a critical issue in epidemiology. A large entirely. In his view, the "case-referent strategy" number of different sources and possible consists in: (1) identifying and classifying all ofthe mechanisms of bias have been described but a cases in the "study base"a, defined as the consistent terminology has not evolved. Different "population experience captured in a study", and authors have used different terms when referring (2) drawing a of the base to obtain to essentially the same type of bias. For example, information on the exposure. 12 A good illustration Kleinbaum et al' and Rothinan2 classify of this concept is a "nested", or "within cohort" into , information bias and case-control study, which can be regarded as an confounding. Sackett offered a more detailed efficient form ofthe cohort design, rather than an classification, with five major types of sampling entirely different type of study.'3 bias (eg, admission rate bias, membership bias) It may be noted that the two aspects (or "axes") and four types ofmeasurement bias (eg, diagnostic of the design, ie, order of measurement and suspicion bias, ).3 Feinstein method of sampling, are interdependent. The distinguishes, inter alia, among susceptibility bias, reason for determining exposure status for all performance bias, transfer bias and detection bias.4 subjects in most cohort studies is to obtain as valid Last's Dictionary of epidemiology5 gives information as possible for the relatively few definitions of 26 biases but fails to mention many cases-to-be. Therefore, in cohort studies all of the terms proposed by other authors. potential cases are classified as exposed or It is not our objective to provide a unexposed. The logic behind the case-control comprehensive list ofbiases, or to propose a new, method is to make the design more efficient by improved taxonomy. Our purpose is to review the classifying only the actual cases, since information most common threats to validity in the design of about the source population can be obtained by case-control studies-commonly regarded as sampling. This, however, implies a particular being particularly susceptible to bias-and to order of measurement (directionality), namely discuss some useful strategies in dealing with ascertaining the outcome first. Measuring these problems. Certain issues will not be exposure for all members of the study population http://jech.bmj.com/ addressed, notably methods of controlling after the cases have been ascertained is confounding, and the statistical analysis of case- unnecessary and impractical, if the disease is rare. control studies.

The RCT paradigm Defining a case-control study There seems to be current agreement that the

Traditionally, a case-control (case-referent) study methods of the randomised clinical trials may on October 1, 2021 by guest. Protected copyright. has been defined as an investigation into a serve as a useful paradigm in designing case- relationship between a given disease and one or control studies. Yet for many clinicians, the more causal or preventive factors, in which conceptual links between the randomised clinical persons selected because they have the disease trial model and the case-control design may not be Department of Epidemiology and (the cases) and suitably selected persons who do obvious. As an illustration, consider the famous Biostatistics, McGiil not have the disease (the controls) are compared in study of cholera in London, conducted by John University, Montreal, terms of their exposure to the factors under Snow in the mid-nineteenth century. 4 The study Canada J A Kopec study.'7 Case-control studies are usually has often been referred to as a "natural Department of considered to be an alternative to cohort studies, experiment",2 and was practically as valid as a Medicine, Montreal from which they are distinguished by two randomised controlled trial. However, its design General Hospital, features: McGill University, (1) sampling by disease as opposed to resembled a modem, nested case-control ("case- 1650 Cedar Avenue, sampling by exposure, and (2) investigative cohort") study, rather than a randomised Montreal, Canada movement from effect to cause as opposed to from controlled trial. Snow did not follow each member H3G 1A4 cause to effect. 1 6-8 Recently, Kramer and Boivin9 of the study cohort individually and, in fact, did J M Esdaile have postulated that the order of measurement Correspondence to: ("directionality"), rather than the method of Dr Esdaile a The term "study base" actually refers to population-time. 1 sampling, provides an "unconfounded" criterion Some authors also distinguish between a source population, for distinguishing between the two designs. This which includes prevalent cases, and a population at risk. The Accepted for publication term "study subjects" is used here to refer to the actual cases and April 1990 approach is not shared by other authors. For controls. 18080acek A Kopec, John M Esdaile J Epidemiol Community Health: first published as 10.1136/jech.44.3.179 on 1 September 1990. Downloaded from not know the source of drinking water for each precisely defined, eg, as the population of a household. In order to ascertain the exposure geographical area, employees in an industrial retrospectively, he visited those families in which plant etc, over a specified time period. fatal cases of cholera had occurred. Although Once the study population (study "base") has Snow obtained the overall number of households been defined, the validity ofthe study depends on supplied by each water company directly from the investigator's ability to obtain accurate their records, the proportion exposed in the study information on the outcome for all its members (as population could have been estimated by in a randomised controlled trial), and information measuring the quality ofwater in a random sample on the exposure and other relevant variables of all households. This example illustrates that (confounders, effect modifiers) for all ofthe cases, under optimal conditions, neither "backward" and a random sample of the base." It may be directionality nor sampling of the base make the noted that in a randomised controlled trial, case-control method inherently less valid, or exposure information is available for all scientifically inferior to other types of research in individuals. The selection of controls (referents) epidemiology. in population based studies should follow the The idea ofusing the experimental approach as principles of random sampling. Various methods a paradigm for observational research was of sampling have been proposed: (1) traditional strongly advocated by Hill"5 and, more recently, "cumulative" sampling, at the end of the by Horwitz and Feinstein.4 '6`9 Exactly how this observation period; (2) "case-base" or "case- paradigm should be implemented remains cohort" sampling, performed at the start of the problematic. According to Feinstein, special care observation period; (3) "incidence-density" in the conduct ofobservational research should be sampling, conducted throughout the period of devoted to the selection of subjects according to follow up.22 23 In order to adjust for confounding the same eligibility criteria that are commonly factors, the sampling is usually performed within applied in randomised controlled trials (eg, strata, formed by the categories of potential indications, contraindications), and the avoidance confounders. A useful strategy, especially when of susceptibility bias (confounding by the study population is "unstable", is to consider susceptibility), detection bias in ascertaining the time as one of the stratification variables.24 25 cases, protopathic bias (confusing cause and effect) and "transfer bias".4 Esdaile and HOSPITAL BASED STUDIES Horwitz20 used the randomised controlled trial In so called hospital based, or "case initiated" framework to develop a list of principles that case-control studies,26 the investigator starts with could be used as a check list for a scientific quality a case series, usually selected from a medical care ofan observational study. Miettinen21 pointed out facility, and compares it (in terms of exposure that the traditional outlook in case-control studies history) to an arbitrary control group, taken either is incompatible with the randomised controlled from the hospital (patients with other diseases) or trial paradigm, where the concern is always to from the community (eg, neighbours or relatives compare exposed and unexposed, rather than of the cases). The cases and controls are usually cases and "non-cases". He also emphasised the matched for a number ofpotentially confounding need to define appropriately not only exposure variables. The source population in these studies but also "non-exposure" (the reference level of is often described vaguely as those subjects who exposure), and the importance of restricting the are "at risk" ofboth exposure and disease,7 but no study population, in order to obtain a desired effort is made to delineate it with any rigour. As a distribution of exposure levels. result, two types of problems arise. First, the http://jech.bmj.com/ The usefulness of the randomised controlled investigator has to accept that the cases studied trial paradigm in elucidating potential sources of are only a fraction of all cases that might be bias stems primarily from its conceptual "eligible" for the study. A substantial and simplicity as a model for cause-effect research, potentially differential underdetection cannot be and the relatively advanced knowledge of the ruled out, but its extent can hardly be evaluated. methodological principles involved. In the Second, there is no "roster" from which to select a

following sections of the paper we will apply this population based control series. The resultant on October 1, 2021 by guest. Protected copyright. paradigm to examine common sources of bias in problem ofpotential "selection" biasa can be seen case-control research. Three broad issues will be as one of "incoherence" of the cases and controls discussed: (1) problems related to the definition of with respect to the population at risk they the study population; (2) measurement related represent.6 12 biases; and (3) bias due to non-participation. SECONDARY BASE Conceptually, some improvement in the design of Study population case initiated studies is possible by "turning the POPULATION BASED STUDIES argument around" and defining the study Experimental populations are "fixed" cohorts, population secondarily, as all those subjects who with membership defined automatically by the would have been included in the case series, had fact of "enrolment" into the study. In "case- they developed the disease of interest." Full case control within cohort" studies the population ascertainment is then achieved simply by which gives rise to the cases is an observational definition, and the previously mentioned cohort, and is defined in a similar way. Most of selection bias that arises in the case series is case-control studies are conducted within so apparently eliminated. However, since the called dynamic (open) populations, characterised a We try to avoid the term "selection bias" because of its by a constant influx and outflow of subjects. ambiguity and because it has been used in many different Nevertheless, a dynamic population can be contexts. Bias in case-control studies. A review 181 J Epidemiol Community Health: first published as 10.1136/jech.44.3.179 on 1 September 1990. Downloaded from membership in the population at risk is now ELIGIBILITY CRITERIA defined only conditionally on a hypothetical An internally valid clinical trial can be carried out event, it cannot be determined with certainty. in a very restricted population, eg, among Thus the problem of unbiased sampling of volunteers, or patients in a single hospital ward. controls remains unresolved. Moreover, the choice of appropriate "eligibility" The choice of an appropriate control group in criteria may significantly improve the study's case initiated (hospital based) studies has been the validity, for example by increasing compliance, subject of much controversy. One proposed minimising drop out rate, or enhancing the solution is to take cases ofother, carefully selected quality of measurement.35 The same principles diseases, from the same "source" as the original apply in case-control studies. Failure to apply case series. To avoid bias, the control disease must certain restrictions on admissibility may seriously not be related to the exposure at issue, and should limit the investigator's ability to control bias.'62' be subject to exactly the same surveillance and The specific admission criteria will usually differ detection procedures as the disease of interest. considerably in studies of therapy (most of which For many diseases, and some common exposures, are experimental) and studies ofaetiology (most of these conditions seem to be very difficult to which are observational). For example, in case- satisfy, and may actually conflict with each control studies on side effects of drugs and other other.7 27 28 Such factors as care seeking therapeutic manoeuvres, it does not matter behaviour, diagnostic accuracy, referral patterns whether the subject had or did not have or hospital catchment areas are likely to differ for indications for the therapy used, except when a different diseases.4 Using a "diagnostic roster", given indication can be considered a confounding (eg, a chest x ray file) as a source ofboth cases and variable or an effect modifier.2' Similarly, it is controls does not seem to be an improvement. irrelevant whether the subjects had the Although the "medical itinerary" ofthe cases (eg, "opportunity" for exposure or not.36 cases of lung cancer) and the controls (other lung Measurement accuracy is usually a greater diseases, etc) may be similar, they may often be problem in case-control studies than in related to the same exposure studied (eg, randomised controlled trials and, as will be smoking). The same objection applies to an discussed, restricting the source population is an extreme version of the above strategy, namely to important strategy in dealing with this problem. compare different histological subtypes of the In both types ofstudies it is reasonable to exclude same disease.29 Another common option in those subjects whose risk of developing the selecting the control group is to use "community disease of interest is known to be zero.' 1 25 controls". This approach can seldom be theoretically justified in case initiated studies.6 12 The use of neighbours, siblings or friends of the Measurement cases has more to do with controlling confounding MEASUREMENT OF OUTCOME (CASE (through matching), than it does with unbiased ASCERTAINMENT) sampling of the base. The amount of bias will By analogy with experimental research, it seems certainly be study specific, and it is difficult to useful to approach the problem of case estimate. Only limited attempts to study the identification in case-control studies from a problem empirically have been made.30 In one measurement point of view. In a large clinical study in which friends ofthe cases have been used trial, one would have an elaborate system ofactive

as controls,3' 32 the "friendly control bias" surveillance for all subjects in the study http://jech.bmj.com/ apparently increased the observed effect. In other population, perhaps involving periodic follow up studies it may act in the opposite direction. examinations. The out migrants would be traced, As an efficient alternative to the case initiated the subjects' personal physicians might be study some authors employed a "control contacted, and the records reviewed. The initiated" design,33 34 whereby the investigator diagnosis in each case would be verified by uses the same control series more than once, to independent, "blinded" reviewers, according to study different diseases and different exposures. standard, pre-established criteria, and using all This design has been used infrequently, and it pertinent information available.35 on October 1, 2021 by guest. Protected copyright. does not offer any advantage over the case Unfortunately, maintaining such a system for a initiated design in terms of validity.26 long period of time, even in a moderately large Because of these difficulties, many population, may be expensive and difficult epidemiologists (including the authors of this logistically, as the experience of some clinical review) believe that validity ofthe control group is trials and observational cohort studies suggest. most likely to be achieved, and easiest to evaluate, The alternative approach, commonly employed in when the case series can be linked to an case-control studies of rare diseases, is to replace identifiable source population. Unfortunately, these costly activities with routine recording of population based studies are expensive because of contacts between patients and the health system the difficulty in ascertaining all the cases. The (including deaths) as the primary source of data validity of a hospital (registry, etc) control group on the outcome. The measurement (case depends on the similarity between the control identification) thus becomes a multistage process, disease and the disease under investigation in largely beyond the investigator's control. For a terms of all factors bearing on the appearance of case to be properly identified, the following the cases in a particular "source", and the lack of activities must take place: (1) a person must association between the control disease and the receive medical attention; (2) he/she must be exposure at issue. Empirical data concerning properly diagnosed as having the disease of these properties of different case-control- interest; and (3) the record of the diagnosis must exposure combinations are scant. appear in the "source" of the case series (eg, a 182 2acek A Kopec, Jrohn M Esdaile J Epidemiol Community Health: first published as 10.1136/jech.44.3.179 on 1 September 1990. Downloaded from registry, a hospital, etc). The remaining members sources may significantly improve validity, of the base are, by default, regarded as "non- substantial and potentially differential cases". Since each missed case represents an underdetection may still remain. It is important instance ofmeasurement error (misclassification), to recognise that non-differential under- it becomes clear that the objective should always ascertainment of the cases will not bias the be to ascertain all incident cases that occur in the estimate ofthe rate ratio.38 Thus another strategy study population. For the purpose of analysis, a is to ensure, to the extent possible, that all random sample of the cases may sometimes be activities associated with case ascertainment are sufficient. In some studies there will also be performed with the same vigour among the persons without the disease, erroneously exposed and unexposed, and follow the same, diagnosed as cases ("false positives"). standard protocol. In randomised controlled trials Misclassification of subjects in terms of their this is achieved through blinding of the disease status, even if "non-differential" with manoeuvre (eg, a placebo) and blind assessment of respect to the exposure, will usually produce a the outcome. In case-control studies, exposure bias toward the null in the estimate of causal status is often unknown to the physician making effect. (An important exception from this rule will the diagnosis, and "unrealised" by the patient, be discussed later.) Differential misclassification which would make differential bias unlikely. This may produce bias in either direction. situation may be changing, The objective of complete however, as ascertainment of information about newly discovered, or only cases in the study base may be unrealistic. For suspected health many conditions the accuracy of hazards is increasingly medical considered a "hot topic" by the media. When diagnosis is imperfect. Increasingly, sophisticated reviewing medical records and specialised care is necessary to make the or verifying the diagnoses, the evaluators should be blind as to diagnosis. Even for conditions that almost whether invariably lead to serious symptoms and hospital the subject is exposed or not. admission, such as many cancers, the Another useful strategy is to restrict the study completeness of reporting seldom exceeds 95%, population to those who, because of their and may be much lower.37 Many relatively mild demographic profile (age, sex, ethnicity, disorders are never recorded simply because education, occupation, income) or some other medical attention is not sought. The incident characteristic specific to the problem studied (eg, cases of some chronic age related disorders, such being covered by a particular health plan, living as osteoarthritis, are very difficult to ascertain close to the study hospital), have a reasonable from medical records, even though these chance of appearing in the case series should they conditions produce significant morbidity and develop the disease under investigation. Then, of disability. In addition, hospital catchment areas course, those cases that do not meet the and referral patterns are often difficult to specify prespecified criteria must be excluded. As part of with precision. Thus, for most diseases, the task of the criteria for admission, it will often be identifying all cases in any large population may necessary to modify the definition of a case. For appear insurmountable. example, only serious cases with overt symptoms There are several strategies in the study design are accepted. The study population may have to that the investigator may employ to reduce be redefined once all potential sources of cases misclassification of the outcome status and avert have been determined and it turns out that certain segments ofthe population are not covered. Savitz bias. The diagnosis can often be verified in the http://jech.bmj.com/ cases, through the use of various auxiliary data and Pierce39 illustrate how these problems might sources, thus eliminating "false positives". In this be approached in the case of male infertility, a way, misclassification is reduced to under- condition with a very high degree of ascertainment ofthe cases, a situation that may be underascertainment. The study population easier to handle, as discussed below. Examining should be restricted to those men who (1) want to the controls to detect "false negatives" is have children and (2) are willing to seek medical recommended by some authors,4 but may be care when this desire is unfulfilled. Then, given difficult, especially when sophisticated that appropriate care is devoted to the on October 1, 2021 by guest. Protected copyright. technology, invasive tests or unpleasant identification of cases, a high degree of procedures are required to rule out a given ascertainment may.be achieved. At the same time, diagnosis. the selection ofa representative control group will When information is gathered prospectively, be possible, provided that such attributes as the investigator may consider various forms of "child seeking behaviour" can be validly active case ascertainment, similar to those used in measured (eg, by means of a ). In large experimental or observational cohorts. In practice, one could initially select a larger pool of some cases, a periodic ofall members ofthe potential controls from a "candidate" population base may be an option, especially in studies of and then eliminate those who do not qualify as relatively mild but selfevident illnesses (eg, minor members of the base ("child seekers"). With the accidents). In retrospective studies, multiple data above approach, the distinction between sources should be used to improve detection. For "primary base" and "secondary base" becomes example, to identify all cancers in a given somewhat artificial.39 The whole process of population over a specified time period, the designing a case-control study is in a sense investigator may review the death certificates, iterative. The challenge is to define the study hospital records, and pathology reports, in population in such a way that all its members addition to the data from a tumour registry.37 (over a specified time period) can be correctly Although diagnosis verification, active case classified as cases or "non-cases", using available ascertainment, and the use of all available data case detection procedures. Bias in case-control studies. A review 183 J Epidemiol Community Health: first published as 10.1136/jech.44.3.179 on 1 September 1990. Downloaded from MEASUREMENT OF EXPOSURE former the direction of bias in the estimate of In a laboratory experiment or, to a somewhat effect may be away from the null and may be lesser degree, in a randomised controlled trial, the difficult to predict.50 Differential report (recall) investigator has almost full control over the bias has been implicated mainly in studies on specific type ofagent being investigated, as well as pregnancy outcomes.5" There are also examples of the dose, timing and duration of exposure. None recall bias in psychiatric publications.52 The of these elements is controlled by the investigator suggestion that the apparent relationship of soft in a case-control study, in which the estimate of tissue sarcoma and malignant lymphoma to exposure is usually based on past records, made phenoxy acids may be due to recall bias has not for other purposes, or recall of past events by the been confirmed.53 Overall, the empirical evidence subjects. Even the very definition of exposure concerning the extent and frequency ofrecall bias may be a problem, let alone the measurement of is scant.54 Of two recently reported studies, one the dose.40 Of course, the specific techniques used failed to provide any evidence of biased reporting to obtain exposure data will depend on the type of of exposure during pregnancy,55 whereas the exposure studied. These issues are too complex to second study (using a somewhat different design) be discussed here, but excellent references are suggested the existence of substantial recall bias available (eg41). for some, but not all, exposure factors.56 In some case-control studies exposure is The most effective device the investigator can recorded before the onset of disease, or after the employ to ensure comparability of measurement onset of disease but before the assessment of is blind assessment of exposure. That is, neither disease status. However, it is ascertained by the the subject nor the investigator (or interviewer) investigator after the disease status has been should know who is a case and who is a control. assessed. Thus the possibility of differential This is analogous to double blinding, routinely misclassification of exposure, often referred to as employed in randomised controlled trials. "recall bias" when the assessment is based on self Despite its strong appeal this obvious precaution report, should always be taken into account. is sometimes ignored in case-control studies. If Another form of measurement related bias in blinding is not feasible, it is essential that the same case-control studies is protopathic (reverse standard measurement conditions and procedures causality) bias. Here, the ascertainment of are used for all subjects. In some instances this exposure is affected by disease related changes in approach may lead to a conflict between the the level of exposure.42 principle of maximum accuracy and that of Perhaps the most common method of data maximum comparability of measurement. For collection in case-control studies is self report. example, if data for the cases have been obtained The accuracy of recall in an has been through proxies, it may be advisable to obtain data studied extensively for a number of common for the controls in the same way, even if it may exposures, for example smoking, medication cause greater bias (but hopefully similar to that in associated with female reproduction, past history the cases) or less precision than questioning the ofchronic illness and hospital admission, diet, and controls directly.12 On the other hand, there is no many occupational exposures. A common finding evidence to support the need for using dead is that the quality of information depends on both controls for dead cases.57 the type of data sought and the methodological Although the use of some equivalent to a aspects of the assessment process.43-46 For placebo to simulate the disease (or death) among example, memory aids, such as pictorial displays, the controls is not feasible in most case-control http://jech.bmj.com/ food models, or wall calendars have been found studies, the investigator may select the controls useful in a number ofstudies.43 45 47 In a series of from subjects with other disorder(s). This method experiments on survey techniques, substantial is commonly used in hospital based studies. improvement in reporting, particularly for Disease controls may also be used as a second "sensitive" topics or "socially undesirable" control group in population based studies, if behaviours, was observed when the following comparability of information appears to be a techniques were used: (1) a mixture of long and significant problem.

short questions; (2) detailed respondent It should be emphasised that the methods of on October 1, 2021 by guest. Protected copyright. instructions; (3) feedback (following each controlling measurement bias in the analysis are question), informing the respondent how well he very limited. Predictors of measurement errors is performing; and (4) commitment technique, cannot, in general, be treated in the same way as consisting in asking the respondent to sign an confounders in the analysis, and improved agreement to respond conscientiously.48 The so measurement quality is always preferable to called cognitive approach to questionnaire design analytical adjustments.58 Nevertheless, it may has been extensively studied at the National sometimes be possible to correct algebraically for Centre for Health Statistics, and the preliminary measurement bias after the data have been results are encouraging.49 collected, if a validation substudy has been In many situations, despite the use of state of performed. Even then, for a wide range of the art measurement techniques, significant bias conditions, it may be more efficient to use the or imprecision in the estimate of exposure is optimal (but more expensive) method of difficult to avoid. If this occurs, an important measurement in all subjects, and enrol fewer consideration is whether these measurement subjects into the study.59 It has been also errors are likely to be different (in terms of suggested that a validity subscale be incorporated frequency, magnitude or direction) among the into the questionnaire, using "fake" exposures, cases and the controls. Differential errors are whose relation to the disease studied has been usually considered a greater threat to the study's ruled out.5' Alternatively, an additional, validity than non-differential ones, since in the "objective" source of information, such as 18484acek A Kopec, John M Esdaile J Epidemiol Community Health: first published as 10.1136/jech.44.3.179 on 1 September 1990. Downloaded from medical records, may be available for some should not occur if the exposures, but not for others; ifthe two exposures relevant information is obtained for all subjects are comparable in terms of validity of recall, the initially selected for the study, and all exclusions magnitude and direction of bias can be estimated, are based on a priori defined criteria (definition of and an appropriate correction factor can be the base). In practice, one should probably strive incorporated into the analysis. This approach for a participation level similar to that required in has a serious limitation as there is some other types of studies, ie, 80-900/ in both cases empirical evidence that different exposures tend and controls. This will sometimes call for the use to behave differently with respect to reporting of special techniques, developed by social bias44 45 56 scientists and large survey organisations. It has Sometimes, the best tactic to obtain good been found, for example, that availability of quality data is to restrict eligibility to those for potential respondents in a population survey whom valid information can be collected. This is depends on the timing and number of calls made somewhat analogous to checking the compliance by the interviewer, whereas refusals to participate of potential candidates for a randomised are related to, among other things, fear of crime controlled trial. Such restrictions should be made and concerns about confidentiality.6' When data a priori (or, at least, without reference to the are collected by means of a self administered outcome data collected in the study), and may questionnaire, the method known as "total design involve age, ability to communicate in a given method" may considerably improve the response language, mental abilities, educational level, rate.62 In some studies, the low response rate was occupational group, etc. For example, when due to such simple omissions in the planning of a occupation is used as a surrogate measure of study as the investigator's failure to print a exposure, the researcher conducting a case- sufficient number of for a second control study may select the occupational groups and third mailing.62 Whenever feasible, the with definitely high or low (plus, perhaps, subjects should be kept blind as to the hypothesis intermediate) exposure levels, and exclude all under investigation. Restricting the study cases and controls whose occupation is not a good population to those subjects who are likely to indicator of exposure. Such an approach participate in any study, regardless of the resembles in some respects a cohort study, and is hypothesis, may be a very useful strategy and consistent with the randomised controlled trial should be considered whenever such general paradigm. predictors of cooperation are known beforehand and are easy to measure. Participation In randomised clinical trials, any confounding Conclusions and recommendations potentially introduced by arbitrary exclusions/ It seems reasonable to argue that under optimal inclusions, refusal to participate, or other forces conditions, a case-control study is as valid as a operating prior to the moment ofrandomisation is randomised clinical trial. For many problems, a effectively prevented. However, exclusions, nested study provides evidence as strong as a withdrawals or losses to follow up occurring after corresponding cohort study, but may be much randomisation are a potential source of more efficient. This is particularly true when the "selection" bias.35 60 Differential losses can often information on exposure is obtained from past be prevented by true blinding with respect to the records. Ofcourse, confounding remains a critical exposure. If blinding is not possible, the success issue in observational research and neither careful http://jech.bmj.com/ with which the follow up is achieved becomes the subject selection nor measuring known basic measure of the quality of the study.8 Yet, confounders, followed by adjustment in the relatively little attention has been paid to high analysis, will ever provide the level of participation rate in evaluating the quality of comparability of the exposed and unexposed case-control studies.6 Even if we assumed that no groups that is attainable through randomisation. confounding by unknown factors was initially This weakness of the observational design in

present in the source population (as if studying certain behavioural interventions has on October 1, 2021 by guest. Protected copyright. randomisation had been performed), the been elegantly demonstrated by Grey-Donald possibility of"selection" bias due to missing data, and Kramer in their study of the relationship non-response, incompleteness ofmedical records, between formula supplementation in hospital and obvious errors in measurement, and other duration of breast feeding.63 uncontrollable factors should always be taken into In this review we have deliberately omitted the account. For example, cancer patients who are topic of confounding, and focused on other aware of having been exposed to a widely sources ofbias, particularly relevant in the context publicised risk factor may be more likely to of case-control studies. The ideas presented here participate than healthy or unexposed are not new, and have been discussed in a number individuals. A positive effect may then be found of recent texts and articles on methods in even if in fact there is no association between the epidemiology. Rather than emphasise differences disease and the exposure. This type of bias may between the authors, we have attempted to occur if the prospective participants (members of reconcile and bring together various seemingly the source population) are aware of the exposure divergent points of view. Our point of departure, and disease being investigated, and the response and a unifying theme, was the conceptual link rate is low. Exposure differential non- between a case-control study and a randomised participation among the controls will bias the clinical trial. A number of bias minimising estimate of the proportion exposed in the source strategies have been discussed and these are population. summarised below. Bias in case-control studies. A review 185 J Epidemiol Community Health: first published as 10.1136/jech.44.3.179 on 1 September 1990. Downloaded from (1) In all case-control studies, an attempt should 9 Kramer MS, Boivin J-F. Toward an unconfounded classification ofepidemiologic research design. J Chron Dis be made to define explicitly the source population 1987; 40: 683-8. for the cases. 10 Greenland S, Morgenstern H. Classification schemes for epidemiologic research design. J Clin Epidemiol 1988; 41: 715-6. (2) If the case series can be linked to an 11 Miettinen OS. Theoretical epidemiology. Principles of occurrence research in medicine. New York: John Wiley & identifiable source population, a valid control Sons, 1985. group can be obtained by random sampling. 12 Miettinen OS. The case-control study: valid selection of subjects. J Chron Dis 1985; 38: 543-8. 13 Mantel N. Synthetic retrospective studies and related topics. (3) If hospital (registry, etc) controls are used, Biometrics 1973; 29: 479-86. should be to the 14 Snow J. On the mode of communication of cholera. 2nd ed. the control disease(s) subject London: John Churchill, 1960. same case detection mechanisms/procedures as 15 Hill AB. Observation and experiment. N EnglI Med 1953; the disease ofinterest, and should not be related to 248: 995. 16 Horwitz RI, Feinstein AR. The application of therapeutic- the exposure at issue. trial principles to improve the design of epidemiologic research: a case-control study suggesting that anticoagulants reduce mortality in patients with myocardial (4) In population based studies, complete infarction. J Chron Dis 1981; 34: 575-83. ascertainment of all cases should be sought. This 17 Feinstein AR. Experimental requirements and scientific principles in case-control studies. J Chron Dis 1985; 38: can be facilitated by: (a) a suitable definition ofthe 127-33. outcome; (b) an extensive use of multiple data 18 Feinstein AR. Epidemiologic analyses of causation: the unlearned scientific lessons of randomized trials. J Clin sources and active case detection; and (c) Epidemiol 1989; 42: 481-9. restricting the source population to those 19 Horwitz RI. The experimental paradigm and observational studies of cause-effect relationship in clinical medicine. J presumably covered by the available Chron Dis 1987; 40: 91-9. ascertainment systems/procedures. 20 Esdaile JM, Horwitz RI. Observational studies of cause- effect relationships: an analysis of methodologic problems as illustrated by the conflicting data for the role of oral (5) Additional eligibility criteria can be applied, contraceptives in the etiology of rheumatoid arthritis. J in order to the ofinformation and Chron Dis 1986; 39: 841-52. improve quality 21 Miettinen OS. The clinical trial as a paradigm for prevent participation bias. epidemiologic research. J Clin Epidemiol 1989; 42: 491-6. 22 Kupper LL. McMichael AJ, Spirtas R. A hybrid epidemiologic study design useful in estimating relative (6) State of the art methods of measurement risk. J Am Stat Assoc 1975; 70: 524-8. should be used, including sophisticated 23 Miettinen OS. Design options in epidemiologic research. An update. Scand J Work Environ Health 1982; 8 (Suppl): questionnaire designs. 7-14. 24 Breslow N. Design and analysis of case-control studies. Annu Rev Public Health 1982; 3: 29-54. (7) Blind assessment is the best way to ensure 25 Greenland S, Thomas DC. On the need for the rare disease comparability of information in the cases and in assumption in case-control studies. Am J Epidemiol 1982; 116: 547-53. the controls. If blinding is not feasible, 26 Greenland S. Control-initiated case-control studies. Int J standardised, uniform data collection procedures Epidemiol 1985; 14: 130-4. 27 Axelsson 0. Comment. The "case-control" study: valid must be used in all subjects. selection of subjects. J Chron Dis 1985; 38: 553-5. 28 Axelsson 0, Flodin U, Hardell L. A comment on the reference series with regard to multiple exposure (8) The subjects and interviewers should not be evaluations in a case-reference study. Scand J Work informed about the hypothesis under study. Environ Health 1982; 8 (Suppl): 15-19. 29 Knottnerus JA. Letter to the Editors. Subject selection in Diagnosis verification should be done "blindly". hospital-based case-control studies. J Chron Dis 1987; 40: 183-5. 30 Stavraky KM, Clarke EA. Hospital or population controls? (9) High response rate among both cases and An unanswered question. J Chron Dis 1983; 36: 301-7. controls should be obtained. 31 Siemiatycki J, Colle S, Campbell S, Devar R, Belmonte MM. Case control study of insulin dependent (type I) http://jech.bmj.com/ diabetes mellitus. Diabetes Care 1989; 12: 209-16. 32 Siemiatycki J. Friendly control bias. J Clin Epidemiol 1989; 42: 687-8. The authors are grateful to Drs J-F Boivin, R I Horwitz 33 Weiss NS, Daling JR, Chow WH. Incidence ofcancer ofthe and A B Miller for their constructive criticism and large bowel in women in relation to reproductive and helpful comments on preliminary drafts of this hormonal factors. I Natl Cancer Inst 1981; 67: 57-60. 34 Harris NV, Weiss NS, Francis AM, Polissar L. Breast manuscript. However, the views expressed in the article cancer in relation to patterns oforal contraceptive use. AmJ are those ofthe authors and do not necessarily reflect the Epidemiol 1982; 116: 643-51. views of Drs Boivin, Horwitz, or Miller. 35 Peto R, Pike MC, Armnitage P, et al. Design and analysis of Dr Kopec is the recipient of a Fellowship from the randomized clinical trials requiring prolonged observation on October 1, 2021 by guest. Protected copyright. of each patient. I. Introduction and design. Br J Cancer National Health Research and Development Program of 1976; 34: 585-612. Canada. Dr Esdaile is a Senior Research Scholar of the 36 Poole C. Exposureopportunity in case-control studies. Amj Fonds de la recherche en sante du Quebec. Supported in Epidemiol 1986; 123: 352-8. from 37 Robles SC, Marrett LD, Clarke EA, Rish HA. An part by grants the Arthritis Society of Canada and application ofcapture-recapture methods to the estimation the Institut de recherche en sante et securite du travail. of completeness of cancer registration. J. Clin Epidemiol 1988; 41: 495-501. 38 Poole C. Exceptions to the rule about nondifferential misclassification (Abstract). AmJEpidemiol 1985; 122: 508. 1 Kleinbaum DG, Kupper LL, Morgenstern H. Epidemiologic 39 Savitz DA, Pearce N. Control selection with incomplete case research: principles and quantitative methods. Belmont: ascertainment. Am J Epidemiol 1988; 127: 1109-17. Wadsworth, 1982. 40 Matanoski GM. Issues in the measurement ofexposure. In: 2 Rothman KJ. Modern epidemiology. New York: Little, L Gordis, ed. Epidemiology and health risk assessment. Brown, 1986. Oxford: Oxford University Press, 1988. 3 Sackett DL. Bias in analytic research. Y Chron Dis 1979; 32: 41 Gordis L, ed. Epidemiology and health risk assessment. 51-63. Oxford: Oxford University Press, 1988. 4 Feinstein AR. Clinical epidemiology. The architecture of 42 Horwitz RI, Feinstein AR. Methodologic standards and clinical research. Philadelphia: WB Saunders, 1985. contradictory results in case-control studies. Am J Med 5 Last JM, ed. A dictionary of epidemiology, 2nd ed. Oxford: 1979; 66: 556-64. Oxford University Press, 1988. 43 Mitchell AA, Cottler AB, Shapiro S. Effect ofquestionnaire 6 Cole P. Introduction. In: Breslow NE, Day NE. Statistical design on recall of drug exposure in pregnancy. Am J methods in cancer research. Vol 1. The design and analysis of Epidemiol 1986; 123: 670-6. case-control studies. Lyon: IARC, 1980. 44 Harlow SD. Agreement between questionnaire data and 7 Schlesselman JJ. Case-control studies: design, conduct, medical records. The evidence for accuracy of recall. AmJ analysis. New York: Oxford University Press, 1982. Epidemiol 1989; 129: 233-48. 8 Breslow NE, Day NE. Statistical methods in cancer research. 45 Lee-Han H, McGuire V, Boyd NF. A review ofthe methods Vol2. The design andanalysisofcohort studies. Lyon: IARC, used by studies of dietary measurement. J Clin Epidemiol 1987. 1989; 42: 269-78. 186 Jacek A Kopec, John M Esdaile J Epidemiol Community Health: first published as 10.1136/jech.44.3.179 on 1 September 1990. Downloaded from 46 Jain M, Howe GR, Harrison L, Miller AB. A study of 56 Werler MM, Prober BR, Nelson K, Holmes LB. Reporting repeatability of dietary data over a seven year period. AmJ accuracy among mothers of malformed and nonmalformed Epidemiol 1989; 129: 422-9. infants. Am I Epidemiol 1989; 129: 415-21. 47 Beresford SAA, Coker AL. Pictorially assisted recall of past 57 Gordis L. Should dead cases be matched to dead controls? hormone use in case-control studies. Am3J Epidemiol 1989; AmJEpidemiol 1982; 115: 1-5. 130: 202-5. 58 Greenland S. Robins JM. Confounding and 48 Cannel CF, Miller PV, Oksenberg L. Research on misclassification. Am J Epidemiol 1985; 122: 496-506. interviewing techniques. In: Lainhard S, ed. Sociological 59 Greenland S. Statistical uncertainty due to misclassification: . San Francisco: Jossey-Blass, 1981. implications for validity substudies. J Clin Epidemiol 1988; 49 Jobe JB, Mingay DJ. Cognitive research improves 41: 1167-74. questionnaires. Am J Public Health 1989; 79: 1053-5. 60 Armitage P. Exclusions, losses to follow-up, and 50 Copeland KT, Checkoway H, McMichael AJ, Holbrook withdrawals in clinical trials. In: Shapiro SH, Louis TA, RH. Bias due to misclassification in the estimation of eds. Clinical trials. Issues and approaches. New York: relative risk. Am J Epidemiol 1977; 105: 488-95. Marcel Dekker, 1983. 51 Raphael K. Recall bias: a proposal for assessment and 61 Hawkins DF. Nonresponse in Detroit area study surveys: a control. Int J Epidemiol 1987; 16: 167-70. ten year analysis. Working papers in methodology No 8. 52 Wolkind S. Koleman EZ. Adult psychiatric disorder and Chapel Hill, N C: Institute for Research in Social Science, childhood experiences: the validity ofretrospective data. Br 1977. J Psychiatry 1983; 143: 188-91. 62 Dillman DA. Mail and other self-administered 53 Hardell L. Relation of soft tissue sarcoma, malignant questionnaires. In: Rossi PH, Wright JD, Anderson AB. lymphoma and colon cancer to phenoxy acids, Handbook of survey research. New York: Academic Press, chlorophenols and other agents. Scand Work Environ 1983. Health 1981; 7: 119-30. 63 Grey-Donald K, Kramer MS. Causality inference in 54 Lippman A, MacKenzie SG. What is recall bias and does it observational vs. experimental studies. An empirical exist? In: Marois M, ed. Progress in clinical and biological comparison. Am J Epidemiol 1988; 127: 885-92. research, vol 163. New York: Alan R Liss, 1985. 55 MacKenzie SG, Lippman A. An investigation of report bias in a case-control study of pregnancy outcome. Am Epidemiol 1989; 129: 65-75. http://jech.bmj.com/ on October 1, 2021 by guest. Protected copyright.