The Need for Validity
Epidemiology aims at providing an understanding of the disease experience in populations. In particular, it can be used to obtain insight into the occupational causes of ill health. This knowledge comes from studies conducted on groups of people having a disease by comparing them to people without that disease. Another approach is to examine what diseases people who work in certain jobs with particular exposures acquire and to compare these disease patterns to those of people not similarly exposed. These studies provide estimates of risk of disease for specific exposures. For information from such studies to be used for establishing prevention programmes, for the recognition of occupational diseases, and for those workers affected by exposures to be appropriately compensated, these studies must be valid.
Validity can be defined as the ability of a study to reflect the true state of affairs. A valid study is therefore one which measures correctly the association (either positive, negative or absent) between an exposure and a disease. It describes the direction and magnitude of a true risk. Two types of validity are distinguished: internal and external validity. Internal validity is a study’s ability to reflect what really happened among the study subjects; external validity reflects what could occur in the population.
Validity relates to the truthfulness of a measurement. Validity must be distinguished from precision of the measurement, which is a function of the size of the study and the efficiency of the study design.
A study is said to be internally valid when it is free from biases and therefore truly reflects the association between exposure and disease which exists among the study participants. An observed risk of disease in association with an exposure may indeed result from a real association and therefore be valid, but it may also reflect the influence of biases. A bias will give a distorted image of reality.
Three major types of biases, also called systematic errors, are usually distinguished:
- selection bias
- information or observation bias
They will be presented briefly below, using examples from the occupational health setting.
Selection bias will occur when the entry into the study is influenced by knowledge of the exposure status of the potential study participant. This problem is therefore encountered only when the disease has already taken place by the time (before) the person enters the study. Typically, in the epidemiological setting, this will happen in case-control studies or in retrospective cohort studies. This means that a person will be more likely to be considered a case if it is known that he or she has been exposed. Three sets of circumstances may lead to such an event, which will also depend on the severity of the disease.
This can occur when people who know they have been exposed to known or believed harmful products in the past and who are convinced their disease is the result of the exposure will consult a physician for symptoms which other people, not so exposed, might have ignored. This is particularly likely to happen for diseases which have few noticeable symptoms. An example may be early pregnancy loss or spontaneous abortion among female nurses handling drugs used for cancer treatment. These women are more aware than most of reproductive physiology and, by being concerned about their ability to have children, may be more likely to recognize or label as a spontaneous abortion what other women would only consider as a delay in the onset of menstruation. Another example from a retrospective cohort study, cited by Rothman (1986), involves a Centers for Disease Control study of leukaemia among troops who had been present during a US atomic test in Nevada. Of the troops present on the test site, 76% were traced and constituted the cohort. Of these, 82% were found by the investigators, but an additional 18% contacted the investigators themselves after hearing publicity about the study. Four cases of leukaemia were present among the 82% traced by CDC and four cases were present among the self-referred 18%. This strongly suggests that the investigators’ ability to identify exposed persons was linked to leukaemia risk.
This will occur when the doctors are more likely to diagnose a given disease once they know to what the patient has been previously exposed. For example, when most paints were lead-based, a symptom of disease of the peripheral nerves called peripheral neuritis with paralysis was also known as painters’ “wrist drop”. Knowing the occupation of the patient made it easier to diagnose the disease even in its early stages, whereas the identification of the causal agent would be much more difficult in research participants not known to be occupationally exposed to lead.
Bias resulting from refusal to participate in a study
When people, either healthy or sick, are asked to participate in a study, several factors play a role in determining whether or not they will agree. Willingness to answer variably lengthy questionnaires, which at times inquire about sensitive issues, and even more so to give blood or other biological samples, may be determined by the degree of self-interest held by the person. Someone who is aware of past potential exposure may be ready to comply with this inquiry in the hope that it will help to find the cause of the disease, whereas someone who considers that they have not been exposed to anything dangerous, or who is not interested in knowing, may decline the invitation to participate in the study. This can lead to a selection of those people who will finally be the study participants as compared to all those who might have been.
This is also called observation bias and concerns disease outcome in follow-up studies and exposure assessment in case-control studies.
Differential outcome assessment in prospective follow-up (cohort) studies
Two groups are defined at the start of the study: an exposed group and an unexposed group. Problems of diagnostic bias will arise if the search for cases differs between these two groups. For example, consider a cohort of people exposed to an accidental release of dioxin in a given industry. For the highly exposed group, an active follow-up system is set up with medical examinations and biological monitoring at regular intervals, whereas the rest of the working population receives only routine care. It is highly likely that more disease will be identified in the group under close surveillance, which would lead to a potential over-estimation of risk.
Differential losses in retrospective cohort studies
The reverse mechanism to that described in the preceding paragraph may occur in retrospective cohort studies. In these studies, the usual way of proceeding is to start with the files of all the people who have been employed in a given industry in the past, and to assess disease or mortality subsequent to employment. Unfortunately, in almost all studies files are incomplete, and the fact that a person is missing may be related either to exposure status or to disease status or to both. For example, in a recent study conducted in the chemical industry in workers exposed to aromatic amines, eight tumours were found in a group of 777 workers who had undergone cytological screening for urinary tumours. Altogether, only 34 records were found missing, corresponding to a 4.4% loss from the exposure assessment file, but for bladder cancer cases, exposure data were missing for two cases out of eight, or 25%. This shows that the files of people who became cases were more likely to become lost than the files of other workers. This may occur because of more frequent job changes within the company (which may be linked to exposure effects), resignation, dismissal or mere chance.
Differential assessment of exposure in case-control studies
In case-control studies, the disease has already occurred at the start of the study, and information will be sought on exposures in the past. Bias may result either from the interviewer’s or study participant’s attitude to the investigation. Information is usually collected by trained interviewers who may or may not be aware of the hypothesis underlying the research. For example, in a population-based case-control study of bladder cancer conducted in a highly industrialized region, study staff may well be aware of the fact that certain chemicals, such as aromatic amines, are risk factors for bladder cancer. If they also know who has developed the disease and who has not, they may be likely to conduct more in-depth interviews with the participants who have bladder cancer than with the controls. They may insist on more detailed information of past occupations, searching systematically for exposure to aromatic amines, whereas for controls they may record occupations in a more routine way. The resulting bias is known as exposure suspicion bias.
The participants themselves may also be responsible for such bias. This is called recall bias to distinguish it from interviewer bias. Both have exposure suspicion as the mechanism for the bias. Persons who are sick may suspect an occupational origin to their disease and therefore will try to remember as accurately as possible all the dangerous agents to which they may have been exposed. In the case of handling undefined products, they may be inclined to recall the names of precise chemicals, particularly if a list of suspected products is made available to them. By contrast, controls may be less likely to go through the same thought process.
Confounding exists when the association observed between exposure and disease is in part the result of a mixing of the effect of the exposure under study and another factor. Let us say, for example, that we are finding an increased risk of lung cancer among welders. We are tempted to conclude immediately that there is a causal association between exposure to welding fumes and lung cancer. However, we also know that smoking is by far the main risk factor for lung cancer. Therefore, if information is available, we begin checking the smoking status of welders and other study participants. We may find that welders are more likely to smoke than non-welders. In that situation, smoking is known to be associated with lung cancer and, at the same time, in our study smoking is also found to be associated with being a welder. In epidemiological terms, this means that smoking, linked both to lung cancer and to welding, is confounding the association between welding and lung cancer.
Interaction or effect modification
In contrast to all the issues listed above, namely selection, information and confounding, which are biases, interaction is not a bias due to problems in study design or analysis, but reflects reality and its complexity. An example of this phenomenon is the following: exposure to radon is a risk factor for lung cancer, as is smoking. In addition, smoking and radon exposure have different effects on lung cancer risk depending on whether they act together or in isolation. Most of the occupational studies on this topic have been conducted among underground miners and at times have provided conflicting results. Overall, there seem to be arguments in favour of an interaction of smoking and radon exposure in producing lung cancer. This means that lung cancer risk is increased by exposure to radon, even in non-smokers, but that the size of the risk increase from radon is much greater among smokers than among non-smokers. In epidemiological terms, we say that the effect is multiplicative. In contrast to confounding, described above, interaction needs to be carefully analysed and described in the analysis rather than simply controlled, as it reflects what is happening at the biological level and is not merely a consequence of poor study design. Its explanation leads to a more valid interpretation of the findings from a study.
This issue can be addressed only after ensuring that internal validity is secured. If we are convinced that the results observed in the study reflect associations which are real, we can ask ourselves whether or not we can extrapolate these results to the larger population from which the study participants themselves were drawn, or even to other populations which are identical or at least very similar. The most common question is whether results obtained for men also apply to women. For years, studies and, in particular, occupational epidemiological investigations have been conducted exclusively among men. Studies among chemists carried out in the 1960s and 1970s in the United States, United Kingdom and Sweden all found increased risks of specific cancers—namely leukaemia, lymphoma and pancreatic cancer. Based on what we knew of the effects of exposure to solvents and some other chemicals, we could already have deduced at the time that laboratory work also entailed carcinogenic risk for women. This in fact was shown to be the case when the first study among women chemists was finally published in the mid-1980s, which found results similar to those among men. It is worth noting that other excess cancers found were tumours of the breast and ovary, traditionally considered as being related only to endogenous factors or reproduction, but for which newly suspected environmental factors such as pesticides may play a role. Much more work needs to be done on occupational determinants of female cancers.
Strategies for a Valid Study
A perfectly valid study can never exist, but it is incumbent upon the researcher to try to avoid, or at least to minimize, as many biases as possible. This can often best be done at the study design stage, but can also be carried out during analysis.
Selection and information bias can be avoided only through the careful design of an epidemiological study and the scrupulous implementation of all the ensuing day-to-day guidelines, including meticulous attention to quality assurance, for the conduct of the study in field conditions. Confounding may be dealt with either at the design or analysis stage.
Criteria for considering a participant as a case must be explicitly defined. One cannot, or at least should not, attempt to study ill-defined clinical conditions. A way of minimizing the impact that knowledge of the exposure may have on disease assessment is to include only severe cases which would have been diagnosed irrespective of any information on the history of the patient. In the field of cancer, studies often will be limited to cases with histological proof of the disease to avoid the inclusion of borderline lesions. This also will mean that groups under study are well defined. For example, it is well-known in cancer epidemiology that cancers of different histological types within a given organ may have dissimilar risk factors. If the number of cases is sufficient, it is better to separate adenocarcinoma of the lung from squamous cell carcinoma of the lung. Whatever the final criteria for entry into the study, they should always be clearly defined and described. For example, the exact code of the disease should be indicated using the International Classification of Diseases (ICD) and also, for cancer, the International Classification of Diseases-Oncology (ICD-O).
Efforts should be made once the criteria are specified to maximize participation in the study. The decision to refuse to participate is hardly ever made at random and therefore leads to bias. Studies should first of all be presented to the clinicians who are seeing the patients. Their approval is needed to approach patients, and therefore they will have to be convinced to support the study. One argument that is often persuasive is that the study is in the interest of the public health. However, at this stage it is better not to discuss the exact hypothesis being evaluated in order to avoid unduly influencing the clinicians involved. Physicians should not be asked to take on supplementary duties; it is easier to convince health personnel to lend their support to a study if means are provided by the study investigators to carry out any additional tasks, over and above routine care, necessitated by the study. Interviewers and data abstractors ought to be unaware of the disease status of their patients.
Similar attention should be paid to the information provided to participants. The goal of the study must be described in broad, neutral terms, but must also be convincing and persuasive. It is important that issues of confidentiality and interest for public health be fully understood while avoiding medical jargon. In most settings, use of financial or other incentives is not considered appropriate, although compensation should be provided for any expense a participant may incur. Last, but not least, the general population should be sufficiently scientifically literate to understand the importance of such research. Both the benefits and the risks of participation must be explained to each prospective participant where they need to complete questionnaires and/or to provide biological samples for storage and/or analysis. No coercion should be applied in obtaining prior and fully informed consent. Where studies are exclusively records-based, prior approval of the agencies responsible for ensuring the confidentiality of such records must be secured. In these instances, individual participant consent usually can be waived. Instead, approval of union and government officers will suffice. Epidemiological investigations are not a threat to an individual’s private life, but are a potential aid to improve the health of the population. The approval of an institutional review board (or ethics review committee) will be needed prior to the conduct of a study, and much of what is stated above will be expected by them for their review.
In prospective follow-up studies, means for assessment of the disease or mortality status must be identical for exposed and non-exposed participants. In particular, different sources should not be used, such as only checking in a central mortality register for non-exposed participants and using intensive active surveillance for exposed participants. Similarly, the cause of death must be obtained in strictly comparable ways. This means that if a system is used to gain access to official documents for the unexposed population, which is often the general population, one should never plan to get even more precise information through medical records or interviews on the participants themselves or on their families for the exposed subgroup.
In retrospective cohort studies, efforts should be made to determine how closely the population under study is compared to the population of interest. One should beware of potential differential losses in exposed and non-exposed groups by using various sources concerning the composition of the population. For example, it may be useful to compare payroll lists with union membership lists or other professional listings. Discrepancies must be reconciled and the protocol adopted for the study must be closely followed.
In case-control studies, other options exist to avoid biases. Interviewers, study staff and study participants need not be aware of the precise hypothesis under study. If they do not know the association being tested, they are less likely to try to provide the expected answer. Keeping study personnel in the dark as to the research hypothesis is in fact often very impractical. The interviewer will almost always know the exposures of greatest potential interest as well as who is a case and who is a control. We therefore have to rely on their honesty and also on their training in basic research methodology, which should be a part of their professional background; objectivity is the hallmark at all stages in science.
It is easier not to inform the study participants of the exact object of the research. Good, basic explanations on the need to collect data in order to have a better understanding of health and disease are usually sufficient and will satisfy the needs of ethics review.
Confounding is the only bias which can be dealt with either at the study design stage or, provided adequate information is available, at the analysis stage. If, for example, age is considered to be a potential confounder of the association of interest because age is associated with the risk of disease (i.e., cancer becomes more frequent in older age) and also with exposure (conditions of exposure vary with age or with factors related to age such as qualification, job position and duration of employment), several solutions exist. The simplest is to limit the study to a specified age range—for example, enrol only Caucasian men aged 40 to 50. This will provide elements for a simple analysis, but will also have the drawback of limiting the application of the results to a single sex age/racial group. Another solution is matching on age. This means that for each case, a referent of the same age is needed. This is an attractive idea, but one has to keep in mind the possible difficulty of fulfilling this requirement as the number of matching factors increases. In addition, once a factor has been matched on, it becomes impossible to evaluate its role in the occurrence of disease. The last solution is to have sufficient information on potential confounders in the study database in order to check for them in the analysis. This can be done either through a simple stratified analysis, or with more sophisticated tools such as multivariate analysis. However, it should be remembered that analysis will never be able to compensate for a poorly designed or conducted study.
The potential for biases to occur in epidemiological research is long established. This was not too much of a concern when the associations being studied were strong (as is the case for smoking and lung cancer) and therefore some inaccuracy did not cause too severe a problem. However, now that the time has come to evaluate weaker risk factors, the need for better tools becomes paramount. This includes the need for excellent study designs and the possibility of combining the advantages of various traditional designs such as the case-control or cohort studies with more innovative approaches such as case-control studies nested within a cohort. Also, the use of biomarkers may provide the means of obtaining more accurate assessments of current and possibly past exposures, as well as for the early stages of disease.