Paper presented at the 3rd Academy of Medicine of Malaysia Scientific Meeting and International Congress of Medicine held 1-4 November at the Shangri-La Hotel, Kuala Lumpur, MALAYSIA by Prof Dr Omar Hasan Kasule MB ChB (MUK), MPH, DrPH (Harvard), Deputy Dean, Faculty of Medicine, UIA Kuantan Malaysia E-M: omarkasule@yahoo.com


The case-control methodology has been popularly used for decades as preliminary evaluation of causal relations using small numbers of study subjects. It has also been used, inappropriately and extravagantly, for large-scale confirmatory studies. It is destined to become even more popular for cheap and rapid identification of causal relations that can be confirmed later by molecular and other laboratory studies. It is essentially a comparison of exposure in diseased and non-diseased subjects. The cases, all incident or newly diagnosed, are from the same population base as the controls to ensure comparability. Results of a case control study are set out in the familiar 2 x 2 table The exposure odds ratio, Pr (E+/D+) / Pr (E+/D-) is computed as ad/bc with 95% confidence bounds. The case-control study design has the following advantages that explain its popularity: easy estimation of the risk ratio using the odds ratio; economy, few subjects are adequate to answer epidemiological questions in a short time; compression of time, exposure information is obtained from history or records; and convenience, study subjects are seen only once with no need for follow-up. The case-control design suffers from the following disadvantages whose alleviation and resolution is increasing the popularity of the study design: an approximate parameter, OR, rather the real one, RR; inversion of the probability of exposure among the diseased, Pr (E+/D+), to get the probability of disease among the exposed, Pr (D+/E+), which is the real interest of etiological studies; sampling and design constraints that do not allow direct estimate of incidence or prevalence; the time sequence between exposure and disease is not certain; vulnerability to bias: misclassification, selection, and confounding; inability to study multiple outcomes from the same exposure;  historical information about exposures used in case-control studies can not be validated.

Key words: case-control, etiology, bias, confounding


1.0 INTRODUCTION           


Case control studies are also called case referent, case compeer, and trohoc studies. The term retrospective studies used to refer to case-control studies is misleading and is not specific since follow-up studies can also be retrospective. Developments over the past 2-3 decades have led to recognition of several variants of the case-control design each with its own technical name: case-base, case-cohort, and cross-over (Rothman et al. 1998). The term case-control is used here in a generic sense to refer to all the different variants. Epidemiologists and non-epidemiologists have sometimes argued with one another about properties of case-control studies with apparent discord. They might all be right but each is talking about a different variant of the case-control design.



The case-control study has been and continues to be popular because or its low cost, rapid results, and flexibility. Testimony to the importance of the case-control methodology is given by a Harvard Professor of Epidemiology Brian MacMahon recognized as the father of chronic disease epidemiology in North America when he wrote: ‘Case-control studies have contributed more than any other approach to the flourishing of epidemiology during the last few decades. Methodological advances allow case-control studies to address virtually all problems that cohort studies can address, excepting the evaluation of exposures that can affect disease risk factors, which, in turn can influence these exposures. However, case-control studies require more attention and subtlety for the avoidance of selection and information bias than the more straightforward cohort studies’ (MacMahon et al. 1996 p. 302). The main growth area in epidemiology over the past half-century has been in the field of chronic diseases. The case-control methodology has helped chronic disease epidemiology grow into a major discipline because it has enabled undertaking thousands of studies in the past half-century rapidly and cheaply. Several causal relations were first discovered through case control studies: cigarette smoking and lung cancer, Reye’s syndrome and aspirin use, absorbent tampons and the toxic shock syndrome. The studies of the smoking-lung cancer relation by Wynder et al. in 1950 and Doll et al. in 1952 led to a renaissance in epidemiology and gave prominence to the case-control design. They classical route of using the case case-control study to identify a potential relationship, published by Doll in 1953, Doll et al. in 1952, 1953, and 1954, and then using a follow-up study for confirmation, published by Doll et al. in 1956, 1964, and 1976 (MacMahon et al. 1996). 


The main attraction of the methodology has been the evaluation of exposures using a small number of subjects, a couple of hundreds, and within a short time frame measured in months. This is a considerable advantage when compared to experimental intervention studies or cohort follow-up studies which involve following thousands of subjects for periods of 3-5 years. The low-cost of the case-control design is illustrated by the study of the causal relation between exposure to DES in utero and clear cell vaginal carcinoma in teenagers. In 1971 Herbst et al. reported important and momentous results from one of the smallest studies in history. Eight cases of carcinoma were diagnosed in teenagers in Boston. Seven of the teenagers had been exposed to DES in uteri. None of the 32 controls had been similarly exposed. Similar results were obtained in an even smaller study in New York involving 5 cases and 8 controls. On the basis of these findings the Federal Drug Administration contra-indicated DES in pregnancy (Weiss 1997).


In addition to cost-efficiency and speed, case-control studies have attractive features when compared to their two closest competitors in epidemiological studies, the experimental and follow-up studies. Case-control studies are the only alternative available to evaluate exposures that cannot be investigated by randomized experimental trials because of logistic and ethical considerations. Advances in exposure and confounding covariate information measurement have enabled case-control studies mimic control of experimental conditions. Unlike case-control studies, cohort studies are not appropriate for rare diseases, short-induction diseases, or sporadic exposures. One variant of the case-control design, the case-cohort, has essentially the same features as a cohort follow-up study without the disadvantages of inability to study rare diseases, short induction diseases, or sporadic exposures. A series of valid case-control studies may be considered as strong as a follow-up study.


The conceptual problems of the case-control methodology, reversal of the cause-effect relation, and the higher potential for bias (classification, selection, and confounding) did not dampen enthusiasm for the method because public health interventions do not anyway wait for perfect elucidation of causal relations. They are instituted when preliminary studies point in the direction of the cause. Effective measures against cholera were undertaken decades before the causative bacterium was isolated and a century before the mechanisms of increased intestinal cell secretion in diarrhea was worked out. Anti-smoking measures against lung cancer were undertaken before isolation of the tobacco component responsible for lung carcinogenesis and before the molecular mechanisms were clarified. Measures to prevent DES exposure in utero were undertaken before its mechanism of action in embryological development was understood. Consistent findings of a couple of several case-control studies are sufficient for purposes of public health intervention but do not satisfy the arm-chair scientist who wants all details worked out and the verdict returned without any reasonable doubt before undertaking any practical measures.


Although originally introduced for study of rare and chronic diseases, the case-control methodology has been found useful even in more common epidemic and infectious diseases. It, however, is not suitable for study of very rare or very common exposures. The case-control methodology has also been extended to non-disease situations in which interest is cantered on causal associations. It is therefore now used outside medicine and public health.



The main objective of a case-control study is to compare exposure in cases with disease compared to exposure in controls who are non-diseased individuals. Controls in this situation reflect the general population exposure distribution. A causal exposure-disease relation is then inferred by inversion of the disease-exposure relation. The case control study is thus not as intuitive as the experimental or follow-up study. It, in essence, is a reversal of the familiar experimental model of cause preceding effect. The reversal has both conceptual and practical problems.



Case control studies were supposed to be preliminary exploratory studies because their design and associated bias potential could not allow definitive conclusions about causal relations. The case control study was supposed to identify potential causal relations that would be confirmed in a follow-up study. A good example was the investigation of the relation between smoking and lung cancer. Fifteen case control studies were published before the first cohort follow-up study was published in 1954 (MacMahon et al. 1996, p. 80). The popularity of case-control studies over the past 50 years, due to cheap and rapid results from evaluation of a small number of people in as much time as it takes to select the sample and administer a questionnaire, has led to their use in all types of investigations sometimes inappropriately. Case-control studies have moved far beyond their humble beginnings. They are now designed as definitive explanatory studies, a source of conceptual controversy among epidemiologists. The economic advantage of small studies has also disappeared with the introduction of large-scale case control studies involving thousands of subjects.




Some of the conceptual controversies about the use of case-control study methodology could be resolved if it is appreciated that there are several variants; each variant being suited to particular study situations. There are basically four major variants recognized at the moment: the case-base, the case-cohort, the case-only, and the crossover designs. Further sub-divisions of the above three categories can be based on the methodology of sampling, 1-stage or 2-stage, and use of incident or prevalent cases.



The case-base design is the predominant form. It is essentially choosing cases as all diseased individuals in the population and controls as a random sample of disease-free individuals in the same base population. The case-base design can use the primary base population or the secondary base population. Using the primary base, involving painstaking and laborious identification of all cases of disease in the population, is easier to design but difficult to execute perfectly. Using the secondary base is resorted to when all cases in the population cannot be identified easily. The restricted case selection then dictates that a secondary base population, a sub-set of the general population, be used as the source of controls to make sure that cases and controls arise from the same sub-population. The case-base design will yield unbiased odds ratios in the comparison of disease in exposed and unexposed people but its rate ratios will be biased because the fraction of sampling from the population is not known. The incidence rate of disease can be computed if the study is based on the primary base. No such computation is possible if the secondary base was employed.



The case-cohort design, involving efficient sampling from a cohort (closed or open), integrates the case-control and follow-up study designs since it has features of both. This variant can conceptually be used for definitive etiological studies and computation of true incidence rates. It has the further advantage, originally thought confined to follow-up studies, of evaluating several exposures using the same control series. Case-cohort studies are divided into 2 groups depending on whether they are based on open cohorts or are based on closed cohorts.


The open-cohort design is conceptualized as a case-control study nested in a cohort. All cases of disease that arise are included in the case series. The procedures of risk-set sampling or incidence density sampling are used for control selection. As each case is identified, 1 or more controls are randomly selected from the members of the cohort who remain hitherto disease-free. This design takes into account the person-time of follow-up and therefore provides an unbiased estimate of the risk ratio, the incidence rate ratio comparing disease in exposed and unexposed, without the necessity to invoke a rare disease assumption. The odds ratio, like in the case-base design, is unbiased.


The closed cohort design, also called the cumulative case-control study, is based on a closed cohort (confined to original members with no new entries or exits). It is widely used in epidemic diseases in which case and control selection start after the end of the epidemic. A cohort of a fixed number of people is conceptualized to have been disease-free at the start of the epidemic. By the end of the epidemic some of them contract the disease while the rest remain disease-free. Those with disease, either active or cured, constitute the case series. A sample of the disease-free is selected as controls. Analysis is based on cumulative incidence. Because time is not taken into account, the risk ratio, incidence rate ratio, cannot be determined. It is approximated by the odds ratio under the rare disease assumption, i.e. cumulative incidence is low.



The case-only design is used in genetic studies in which the control exposure distribution can be worked out theoretically. For example in the study of the relation between the ABO blood group and a given disease, it is only necessary to determine the ABO distribution in the case series. The ABO distribution of the general population is known and there is no need to draw a random sample as controls from the general population.



The crossover design is used in situations in which exposure is sporadic and its impact lasts a short time such as study of the relation between coitus, as exposure, and myocardial infarction, as disease. A subject who experiences a myocardial infarction on one day is included in the case series and contributes information on the exposure, i.e. coitus. The same person could be selected as a control the next month when he is disease-free, i.e. not in an episode of myocardial infarction, and will be asked about the exposure, coitus. The same individual can serve as a case or as a control several times without any prejudice to the study.





The results of a case-base study as shown in the diagram below:



Disease +

Disease -


Exposure +




Exposure -





The marginal totals, a+b and c+d, are fixed by design before data collection. This restricts use of the case control study to compute prevalence rates because the investigator fixes the number of controls sometimes guided by available budget and logistic considerations and not scientific criteria.



Source population for cases: The source population for cases and controls must be the same and is called the study base or the target population. As explained before the primary base is the whole population. The secondary base is restricted by the realities of case selection when it is impossible to identify every case in the population.




The following are sources of cases: clinical records, hospital discharge records, disease registries, data from surveillance programs, employment records, and death certificates.



Cases are either all cases of a disease or a sample thereof. The sampling must not in any way be influenced by the exposure status. Before starting any case selection the following must be ascertained for proper case definition: diagnostic criteria, inclusion criteria, and exclusion criteria. A trade-off is involved with regard to specificity and sensitivity of diagnostic criteria. Very stringent specificity criteria will exclude true cases include false controls. Very loose criteria will include false cases and exclude true controls.



Cases are selected as all persons diagnosed with the disease of interest in the population or the facility such as a hospital. Cases should, as far as possible, be from a homogenous diagnostic category. Only incident cases are selected. The definition of an incident case must be rigorous by defining a uniform selection time for example we can choose the date of the confirmatory histological report, the date of clinical diagnosis, or the date of recruitment into the study. In some cases there is no alternative but to use prevalent cases because the date of disease onset in not ascertainable as in HIV/AIDS. Prevalent cases are used with caution because exposure measurement is likely to be biased since disease status may change recollection of exposure. Disease status may even cause a change in exposure status.


Care must be taken to avoid bias in case selection. It is not a requirement that all available cases of disease be included in the study. No bias arises from missing some cases from the case series. Detection bias arises when some cases are missed in a systematic way. Selection bias arises if case selection is dictated by exposure status or when information is missing in a systematic way related to exposure status. Refusal to participate can be a cause of bias if it is related either directly or indirectly to exposure status.




Controls must be selected from an explicitly defined population. The general rule is that controls must be from the same population base as the cases since controls represent the general population. The criteria for case selection are used to define this population more systematically such that the source population for both cases and controls is the same. The guiding criterion is that controls must be like cases in everything except having the disease being studied. In practical terms this means that both controls must arise from the same population such that a person selected as a control would have readily been a case if they had the disease of interest. Subjects initially selected as controls and later develop disease have to be included in both the case and control series for purposes of analysis. There is no problem due to duplication if a subject is included more than once in the control series as a result of sampling with replacement. This is because exposure and covariate information changes every time and thus the duplication introduces no redundancy.



Criteria for control selection are determined partly by the criteria for case selection; the latter define precisely the source population from which controls ought to be sought. This is done to ensure that controls are from the same population base as the cases. The inclusion and exclusion criteria must be set before the start of the study. Care must be taken to exclude from the control series those who have no opportunity to be exposed to the risk factor being studied for example women who had total hysterectomy are excluded from the control series of a study of cervical cancer.


The selection of controls must not be affected by the exposure status since this will give rise to bias.  A general rule that has stood the test of time is that controls should be like cases in everything except the having disease being studied. Controls must be similar to cases in factors that determine likelihood of exposure. The controls must also be similar to cases in factors that, independent of exposure, determine the occurrence of disease. There must be comparability of information between cases and controls to avoid information bias; the measurement of exposure must be of the same level of accuracy between cases and controls. If controls are selected properly they will reflect the exposure status of the population.



Sampling: In rare cases when the whole population data is pre-recorded regarding the exposures and co-factors of interest, there may be no need for special sampling to obtain a study group. However in most practical cases a sample is selected as controls to provide data on exposure and other covariates. Sampling may be random or systematic. Controls are sourced from hospitals, hospital controls, or the general community, community controls. It is recommended to select controls from both hospital and community sources though this is associated with more logistic and analytic problems. The problem of confounding can be dealt with at the design stage by stratification or matching or at the analysis stage by suitable statistical procedures.


Hospital controls: Hospital controls, patients or workers, are readily accessible and are usually cooperative. Controls may be selected as all or a sample of those admitted for chronic diseases that are known to have no etiological relation to the exposure being studied. It is preferable to constitute the control series from a range of diagnostic categories rather than rely on one category or a narrow range of categories. Controls may also be selected from those who screened negative for the disease of interest (provided screening is not confined only to those with the exposure of interest). Hospital controls have the following advantages. They are easy to get being a captive group with time at their hands to participate in the study. Patients are motivated to participate in studies of diseases and therefore have minimal recall bias. Hospital controls have disadvantages that may nullify the advantages. The Berkson fallacy, explained elsewhere, is a type of selection bias that operates when hospital controls are used. It is difficult to blind the interviewer about the case or control status because the hospital environment easily suggests the diagnosis. Effect measures will be under-estimated if the diseases of the hospitalized controls are etiologically similar to the disease being studied in the cases. Bias also arises when the cause of death of the hospitalized controls is associated with the exposure. The source population for hospital controls is more difficult to define when referral patterns are complex.


Community controls: Community sources could be co-workers, classmates, friends, neighbors, associates, and relatives. Community controls have the advantage of a lower selection bias, the results are more easily generalizable, and control for confounding factors is convenient. The disadvantages of community controls are: the selection process is time-consuming and expensive with low participation rates and higher recall bias. The following measures can be adopted to prevent selection bias: random digit dialing, sampling from birth records, sampling from insurance records where insurance cover is universal, sampling from disease registers for eligible diseases, and sampling from the voters’ list.


Other types of controls are neighborhood, friend, dead, and relative controls. Neighborhood controls are used often in matched studies. Friend controls are a type of individual matching which may cause bias because cases and their friends are likely to share the same life-style and therefore have the same exposures. Dead controls for dead cases to ensure information comparability but could be a cause of bias if the exposure being studied is related to the death of the controls. Relative controls are difficult to use because environmental, hereditary, and exposure factors become inter-twined.


Case: control ratio: The decision on how many controls per case generally depends on the costs involved. There is little gain in efficiency beyond 1:2 unless control data is obtained at no cost.




Stratification is used to control confounding. Pre-stratification is restricting control selection by level of suspected confounding factor at the stage of design. Post-stratification carried out at the analysis stage after data collection is less desirable. Pre-stratification does not automatically imply ignoring adjustment for stratification at the analysis stage.



The purpose of matching is to control confounding factors by making sure that each case has a control similar to it on some aspects like gender, SES, age such that those aspects need not be considered further in the analysis. Matching attempts but can not guarantee that cases and controls will be similar in everything except the disease status. When matching is done stratified analysis or modeling must be done to take matching into account. Two types of matching are possible: pair wise matching and frequency matching. In pair-wise or individual matching one case is matched against 1 or more controls as individuals. In frequency matching the control source is selected so that the overall distribution of matching factors parallels the distribution in cases. The sources of matches are existing records like the voters’ list, telephone lists, census data etc. Using broader matching criteria is better than the more restrictive ones. There are three conditions for validity of matching: (a) The matching variable must be strongly related to both disease and exposure (b) information on the matching variable can be obtained cheaply (c) Information on exposure is obtainable cheaply.


Matching has the following advantages. It conforms well to situations of natural pairing. It enables control for confounding factors like SES that are otherwise difficult to measure and control for. Matching alone does not eliminate all confounding. There are good statistical reasons that justify adjusting for the matching for controlling for the matching factor in the analysis in order to remove residual confounding. Matching improves statistical precision for small samples; this advantage is lost for large samples. Matching enhances validity of the study. Results of a matched study are intuitively easy to interpret. Matching has the following disadvantages. Where too many confounding variables are involved, it becomes difficult to find suitable matches. Overmatching results into under-estimate of the effect measures. Matching may increase the cost of the study. A disadvantage of matching that is sometimes cited is that the main effects of the matching variable factor cannot be studied. It is however possible to study interactive effects.


Overmatching is a disadvantage of matching but is discussed here separately because of its importance. Overmatching is a situation in which cases and controls are artificially made to resemble one another more than the real situation in nature rendering invalid any comparisons between the two series. It occurs when the matching variable is strongly related either to disease to exposure and not to both. This situation occurs when the matching factor is part of the causal pathway and is thus related to disease. It also occurs when the matching variable, independent of the disease is strongly related to the exposure.




The same questionnaire and methods of data collection are used to obtain exposure information for both cases and controls in order to avoid bias. Exposure information can be obtained in the following ways: interview of study subjects or their relatives, hospital records, pharmacy records, vital records (birth and death certificates), disease registry employment records, environmental data, genetic determinants, biomarker, physical measurements, and laboratory measurements (hormones, micro-nutrients, infectious agents). Medical records are more reliable than interviews but may be incomplete. Recall bias is a disadvantage in interviewing. A nested case-control study can be carried out within a follow-up study. The blood and other biological specimens collected from the cohort at the start can be analyzed for exposure information when cases of disease appear.



Information on covariates must be collected for purposes of studying confounding, effect modification, or interactive effects. Methods of data collection must be standardized and must be comparable between cases and controls.



Validity of case control findings is benchmarked on comparability of information quality between the case and control series. This requirement is sometimes carried to extremes that may seem comic to the un-initiated. If the case in a matched study dies before being interviewed about exposure, a proxy like a wife or other close relative can be interviewed instead. For comparability the wife of the living control will have to be interviewed even in the presence of the control who may be in good health and capable of answering with perhaps better quality information than the proxy. Among the practical measures undertaken to ensure information comparability are: blinding the interviewer or record abstractor to the case/control status, and using records on exposure made before awareness of the diagnosis or the start of the study. Even with the best procedures for assuring information comparability, it is still necessary to carry out statistical evaluations of whether information is actually comparable. Comparative tabulations of lengths of interviews, time and place of the interview, as well as report of attributes not related to the exposure of interest etc may be carried comparing cases and controls.




The case-control study design has the following strengths/advantages. First: The odds ratio, easily computed as ad/bc, approximates the cohort follow up risk ratio, the real parameter of interest for causal studies. The odds ratio, though less intuitive than the risk ratio, has nice mathematical properties and can be manipulated or used in advanced mathematical operations. Effect estimates in the popular logistic regression analysis are also based on the odds ratio. Second:  Case-control studies are economical with small numbers being adequate to answer epidemiological questions; rare diseases can be studied at low cost by use of a high control to case ratio. Third: The case control design enables compression of time by obtaining exposure information from history or records in contract to cohort studies in which an exposed subject will have to be followed for a long time in order to observe the disease outcome. Thus only case control studies are feasible for rare diseases and diseases with a long induction period; they however are not feasible for study of rare exposures. Fourth: The case control design is convenient for study subjects because they are seen only once and do not have to return for any follow-up.



The case-control design suffers from the following disadvantages. First: The case control design cannot give the risk ratio, RR, but provides its approximation, the odds ratio, OR.  Second: The case control study gives the probability of exposure among the diseased, Pr (E+/D+), but real interest is the probability of disease among the exposed, Pr (D+/E+). Three: With the exception of cohort-based designs with defined sampling ratios, it is not possible to obtain a direct estimate of the incidence rate or the prevalence ratio from a case-control design because the marginals are fixed by design. Fourth: The time sequence between exposure and disease outcome is not clear in a case-control study since it is not possible to tell that the exposure preceded the disease. For example an elevated level of HBV antibodies or antigens in a case of hepatocellular carcinoma may precede disease when HBV is the cause or may follow disease due to disease-induced immuno-suppression that facilitates viral infection. Fifth: Case-control studies are very vulnerable to 3 types of bias: misclassification, selection bias, and confounding bias. Sixth: Unlike follow up studies and case-cohort designs, case-base studies cannot be employed to study multiple outcomes from the same exposure. Seventh: case-control studies are not precise in evaluation of exposures that are extremely rare or those that are extremely common. Eight: Historical information about exposures used in case-control studies is not readily validated. Human memory, whether of controls or cases, is not always perfect. There is differential recall of exposure between cases and controls due to the stress and anxiety engendered by disease. Memory deficiencies are not a problem in studies based on biological specimens collected and stored before disease diagnosis. Some of the biological markers do not change even after a long time for example the dentine lead levels tend to be constant. Memory is also not a problem if the exposure is measured as permanent traits such as genetic markers like the ABO blood groups. Information from records written before start of the study may be more reliable than memory. Ninth: Relevant confounding factors are difficult to control in case-control studies because they may not be known or anticipated. Even if suspected, their measurement and control are not always perfect.



Kenneth J Rothman and Sander Greenland: Case-Control Studies, in: Rothman et al. (ed) Modern Epidemiology, Lippincourt-Raven, Philadelphia, PA 1998


Noel S Weiss. Case-control Studies in: Oxford Text Book of Epidemiology Vol 3. Oxford medical Publications, New York 1997


Brian MacMahon and Dimitrios Trichopoulos. Epidemiology: Principles and Methods. 2nd edition. Little, Brown, and Company. Boston 1996



‘Case-control studies have contributed more than any other approach to the flourishing of epidemiology during the last few decades. Methodological advances allow case-control studies to address virtually all problems that cohort studies can address, excepting the evaluation of exposures that can affect disease risk factors, which, in turn can influence these exposures. However, case-control studies require more attention and subtlety for the avoidance of selection and information bias than the more straightforward cohort studies’ (MacMahon et al. 1996 p. 302)



Disease +

Disease -


Exposure +





Exposure –














Low Cost


Rapid Results




Non-medical and non-health studies


Reversal Of The Exposure-Disease Relation


Potential For Bias


Exploratory vs. Definitive Studies





Primary base

Secondary base



open-cohort design

closed cohort design





























Information On Exposure

Information On Covariates

Comparability Of Information



Odds ratio easy to compute.

Economical with small numbers

Compression of time

Convenient for study subjects



OR is not the same as RR

Pr (E+/D+) but not Pr (D+/E+)

No estimate of Incidence rate or prevalence

Exposure-Disease time sequence not clear

Bias: misclassification, selection, and confounding

Case-base cannot study multiple outcomes

Imprecise for rare / common exposures

Historical information difficult to validate

Confounding difficult to control

Professor Omar Hasan Kasule, Sr November 2000