There is much debate on the role of statistics in epidemiological research on causal relationships. In epidemiology, statistics is primarily a collection of methods for assessing data based on human (and also on animal) populations. In particular, statistics is a technique for the quantification and measurement of uncertain phenomena. All the scientific investigations which deal with non-deterministic, variable aspects of reality could benefit from statistical methodology. In epidemiology, variability is intrinsic to the unit of observation—a person is not a deterministic entity. While experimental designs would be improved in terms of better meeting the assumptions of statistics in terms of random variation, for ethical and practical reasons this approach is not too common. Instead, epidemiology is engaged in observational research which has associated with it both random and other sources of variability.

Statistical theory is concerned with how to control unstructured variability in the data in order to make valid inferences from empirical observations. Lacking any explanation for the variable behaviour of the phenomenon studied, statistics assumes it as random—that is, non-systematic deviations from some average state of nature (see Greenland 1990 for a criticism of these assumptions).

Science relies on empirical evidence to demonstrate whether its theoretical models of natural events have any validity. Indeed, the methods used from statistical theory determine the degree to which observations in the real world conform to the scientists’ view, in mathematical model form, of a phenomenon. Statistical methods, based in mathematics, have therefore to be carefully selected; there are plenty of examples about “how to lie with statistics”. Therefore, epidemiologists should be aware of the appropriateness of the techniques they apply to measure the risk of disease. In particular, great care is needed when interpreting both statistically significant and statistically non-significant results.

The first meaning of the word statistics relates to any summary quantity computed on a set of values. Descriptive indices or statistics such as the arithmetic average, the median or the mode, are widely used to summarize the information in a series of observations. Historically, these summary descriptors were used for administrative purposes by states, and therefore they were named statistics. In epidemiology, statistics that are commonly seen derive from the comparisons inherent to the nature of epidemiology, which asks questions such as: “Is one population at greater risk of disease than another?” In making such comparisons, the relative risk is a popular measure of the strength of association between an individual characteristic and the probability of becoming ill, and it is most commonly applied in aetiological research; attributable risk is also a measure of association between individual characteristics and disease occurrence, but it emphasizes the gain in terms of number of cases spared by an intervention which removes the factor in question—it is mostly applied in public health and preventive medicine.

The second meaning of the word statistics relates to the collection of techniques and the underlying theory of statistical inference. This is a particular form of inductive logic which specifies the rules for obtaining a valid generalization from a particular set of empirical observations. This generalization would be valid provided some assumptions are met. This is the second way in which an uneducated use of statistics can deceive us: in observational epidemiology, it is very difficult to be sure of the assumptions implied by statistical techniques. Therefore, sensitivity analysis and robust estimators should be companions of any correctly conducted data analysis. Final conclusions also should be based on overall knowledge, and they should not rely exclusively on the findings from statistical hypothesis testing.

Definitions

A statistical unit is the element on which the empirical observations are made. It could be a person, a biological specimen or a piece of raw material to be analysed. Usually the statistical units are independently chosen by the researcher, but sometimes more complex designs can be set up. For example, in longitudinal studies, a series of determinations is made on a collection of persons over time; the statistical units in this study are the set of determinations, which are not independent, but structured by their respective connections to each person being studied. Lack of independence or correlation among statistical units deserves special attention in statistical analysis.

A variable is an individual characteristic measured on a given statistical unit. It should be contrasted with a constant, a fixed individual characteristic—for example, in a study on human beings, having a head or a thorax are constants, while the gender of a single member of the study is a variable.

Variables are evaluated using different scales of measurement. The first distinction is between qualitative and quantitative scales. Qualitative variables provide different modalities or categories. If each modality cannot be ranked or ordered in relation to others—for example, hair colour, or gender modalities—we denote the variable as nominal. If the categories can be ordered—like degree of severity of an illness—the variable is called ordinal. When a variable consists of a numeric value, we say that the scale is quantitative. A discrete scale denotes that the variable can assume only some definite values—for example, integer values for the number of cases of disease. A continuous scale is used for those measures which result in real numbers. Continuous scales are said to be interval scales when the null value has a purely conventional meaning. That is, a value of zero does not mean zero quantity—for example, a temperature of zero degrees Celsius does not mean zero thermal energy. In this instance, only differences among values make sense (this is the reason for the term “interval” scale). A real null value denotes a ratio scale. For a variable measured on that scale, ratios of values also make sense: indeed, a twofold ratio means double the quantity. For example, to say that a body has a temperature two times greater than a second body means that it has two times the thermal energy of the second body, provided that the temperature is measured on a ratio scale (e.g., in Kelvin degrees). The set of permissible values for a given variable is called the domain of the variable.

Statistical Paradigms

Statistics deals with the way to generalize from a set of particular observations. This set of empirical measurements is called a sample. From a sample, we calculate some descriptive statistics in order to summarize the information collected.

The basic information that is generally required in order to characterize a set of measures relates to its central tendency and to its variability. The choice between several alternatives depends on the scale used to measure a phenomenon and on the purposes for which the statistics are computed. In table 1 different measures of central tendency and variability (or, dispersion) are described and associated with the appropriate scale of measurement.

Table 1. Indices of central tendency and dispersion by scale of measurement

The descriptive statistics computed are called estimates when we use them as a substitute for the analogous quantity of the population from which the sample has been selected. The population counterparts of the estimates are constants called parameters. Estimates of the same parameter can be obtained using different statistical methods. An estimate should be both valid and precise.

The population-sample paradigm implies that validity can be assured by the way the sample is selected from the population. Random or probabilistic sampling is the usual strategy: if each member of the population has the same probability of being included in the sample, then, on average, our sample should be representative of the population and, moreover, any deviation from our expectation could be explained by chance. The probability of a given deviation from our expectation also can be computed, provided that random sampling has been performed. The same kind of reasoning applies to the estimates calculated for our sample with regard to the population parameters. We take, for example, the arithmetic average from our sample as an estimate of the mean value for the population. Any difference, if it exists, between the sample average and the population mean is attributed to random fluctuations in the process of selection of the members included in the sample. We can calculate the probability of any value of this difference, provided the sample was randomly selected. If the deviation between the sample estimate and the population parameter cannot be explained by chance, the estimate is said to be biased. The design of the observation or experiment provides validity to the estimates and the fundamental statistical paradigm is that of random sampling.

In medicine, a second paradigm is adopted when a comparison among different groups is the aim of the study. A typical example is the controlled clinical trial: a set of patients with similar characteristics is selected on the basis of pre-defined criteria. No concern for representativeness is made at this stage. Each patient enrolled in the trial is assigned by a random procedure to the treatment group—which will receive standard therapy plus the new drug to be evaluated—or to the control group—receiving the standard therapy and a placebo. In this design, the random allocation of the patients to each group replaces the random selection of members of the sample. The estimate of the difference between the two groups can be assessed statistically because, under the hypothesis of no efficacy of the new drug, we can calculate the probability of any non-zero difference.

In epidemiology, we lack the possibility of assembling randomly exposed and non-exposed groups of people. In this case, we still can use statistical methods, as if the groups analysed had been randomly selected or allocated. The correctness of this assumption relies mainly on the study design. This point is particularly important and underscores the importance of epidemiological study design over statistical techniques in biomedical research.

Signal and Noise

The term random variable refers to a variable for which a defined probability is associated with each value it can assume. The theoretical models for the distribution of the probability of a random variable are population models. The sample counterparts are represented by the sample frequency distribution. This is a useful way to report a set of data; it consists of a Cartesian plane with the variable of interest along the horizontal axis and the frequency or relative frequency along the vertical axis. A graphic display allows us to readily see what is (are) the most frequent value(s) and how the distribution is concentrated around certain central values like the arithmetic average.

For the random variables and their probability distributions, we use the terms parameters, mean expected value (instead of arithmetic average) and variance. These theoretical models describe the variability in a given phenomenon. In information theory, the signal is represented by the central tendency (for example, the mean value), while the noise is measured by a dispersion index (such as the variance).

To illustrate statistical inference, we will use the binomial model. In the sections which follow, the concepts of point estimates and confidence intervals, tests of hypotheses and probability of erroneous decisions, and power of a study will be introduced.

Table 2. Possible outcomes of a binomial experiment (yes = 1, no = 0) and their probabilities (n = 3)

An Example: The Binomial Distribution

In biomedical research and epidemiology, the most important model of stochastic variation is the binomial distribution. It relies on the fact that most phenomena behave as a nominal variable with only two categories: for example, the presence/absence of disease: alive/dead, or recovered/ill. In such circumstances, we are interested in the probability of success—that is, in the event of interest (e.g., presence of disease, alive or recovery)—and in the factors or variables that can alter it. Let us consider n = 3 workers, and suppose that we are interested in the probability, p, of having a visual impairment (yes/no). The result of our observation could be the possible outcomes in table 2.

Table 3. Possible outcomes of a binomial experiment (yes = 1, no = 0) and their probabilities (n = 3)

The probability of any of these event combinations is easily obtained by considering p, the (individual) probability of success, constant for each subject and independent from other outcomes. Since we are interested in the total number of successes and not in a specific ordered sequence, we can rearrange the table as follows (see table 3) and, in general, express the probability of x successes P(x) as:

where x is the number of successes and the notation x! denotes the factorial of x, i.e., x! = x×(x–1)×(x–2)…×1.

When we consider the event “being/not being ill”, the individual probability, refers to the state in which the subject is presumed; in epidemiology, this probability is called “prevalence”. To estimate p, we use the sample proportion:

p = x/n

with variance:

In an hypothetical infinite series of replicated samples of the same size n, we would obtain different sample proportions p = x/n, with probabilities given by the binomial formula. The “true” value of  is estimated by each sample proportion, and a confidence interval for p, that is, the set of likely values for p, given the observed data and a pre-defined level of confidence (say 95%), is estimated from the binomial distribution as the set of values for p which gives a probability of x greater than a pre-specified value (say 2.5%). For a hypothetical experiment in which we observed x = 15 successes in n = 30 trials, the estimated probability of success is:

p = x/n = 15/30 = 0.5 

Table 4. Binomial distribution. Probabilities for different values of  for x = 15 successes in n = 30 trials

The 95% confidence interval for p, obtained from table 4, is 0.334 – 0.666. Each entry of the table shows the probability of x = 15 successes in n = 30 trials computed with the binomial formula; for example, for = 0.30, we obtain from:

For n large and p close to 0.5 we can use an approximation based on the Gaussian distribution:

where z_{a /2} denotes the value of the standard Gaussian distribution for a probability

P (|z| ³ z_{a /2}) = a/2;

1 – a being the chosen confidence level. For the example considered, = 15/30 = 0.5; n = 30 and from the standard Gaussian table z_0.025 = 1.96. The 95% confidence interval results in the set of values 0.321 – 0.679, obtained by substituting p = 0.5, n = 30, and z_0.025 = 1.96 into the above equation for the Gaussian distribution. Note that these values are close to the exact values computed before.

Statistical tests of hypotheses comprise a decision procedure about the value of a population parameter. Suppose, in the previous example, that we want to address the proposition that there is an elevated risk of visual impairment among workers of a given plant. The scientific hypothesis to be tested by our empirical observations then is “there is an elevated risk of visual impairment among workers of a given plant”. Statisticians demonstrate such hypotheses by falsifying the complementary hypothesis “there is no elevation of the risk of visual impairment”. This follows the mathematical demonstration per absurdum and, instead of verifying an assertion, empirical evidence is used only to falsify it. The statistical hypothesis is called the null hypothesis. The second step involves specifying a value for the parameter of that probability distribution used to model the variability in the observations. In our examples, since the phenomenon is binary (i.e., presence/absence of visual impairment), we choose the binomial distribution with parameter p, the probability of visual impairment. The null hypothesis asserts that = 0.25, say. This value is chosen from the collection of knowledge about the topic and a priori knowledge of the usual prevalence of visual impairment in non-exposed (i.e., non-worker) populations. Suppose our data produced an estimate = 0.50, from the 30 workers examined.

Can we reject the null hypothesis?

If yes, in favour of what alternative hypothesis?

We specify an alternative hypothesis as a candidate should the evidence dictate that the null hypothesis be rejected. Non-directional (two-sided) alternative hypotheses state that the population parameter is different from the value stated in the null hypothesis; directional (one-sided) alternative hypotheses state that the population parameter is greater (or lesser) than the null value.

Table 5. Binomial distribution. Probabilities of success for  = 0.25 in n = 30 trials

Under the null hypothesis, we can calculate the probability distribution of the results of our example. Table 5 shows, for = 0.25 and n = 30, the probabilities (see equation (1)) and the cumulative probabilities:

From this table, we obtain the probability of having x ³15 workers with visual impairment

P(x ³15) = 1 – P(x <15) = 1 – 0.9992 = 0.0008

This means that it is highly improbable that we would observe 15 or more workers with visual impairment if they experienced the prevalence of disease of the non-exposed populations. Therefore, we could reject the null hypothesis and affirm that there is a higher prevalence of visual impairment in the population of workers that was studied.

When n×p ³ 5 and n×(1-) ³ 5, we can use the Gaussian approximation:

From the table of the standard Gaussian distribution we obtain:

P(|z|>2.95) = 0.0008

in close agreement with the exact results. From this approximation we can see that the basic structure of a statistical test of hypothesis consists of the ratio of signal to noise. In our case, the signal is (p–), the observed deviation from the null hypothesis, while the noise is the standard deviation of P:

The greater the ratio, the lesser the probability of the null value.

In making decisions about statistical hypotheses, we can incur two kinds of errors: a type I error, rejection of the null hypothesis when it is true; or a type II error, acceptance of the null hypothesis when it is false. The probability level, or p-value, is the probability of a type I error, denoted by the Greek letter a. This is calculated from the probability distribution of the observations under the null hypothesis. It is customary to predefine an a-error level (e.g., 5%, 1%) and reject the null hypothesis when the result of our observation has a probability equal to or less than this so-called critical level.

The probability of a type II error is denoted by the Greek letter β. To calculate it, we need to specify, in the alternative hypothesis, α value for the parameter to be tested (in our example, α value for ). Generic alternative hypotheses (different from, greater than, less than) are not useful. In practice, the β-value for a set of alternative hypotheses is of interest, or its complement, which is called the statistical power of the test. For example, fixing the α-error value at 5%, from table 5, we find:

P(x ³12) <0.05

under the null hypothesis = 0.25. If we were to observe at least x = 12 successes, we would reject the null hypothesis. The corresponding β values and the power for x = 12 are given by table 6. 

Table 6. Type II error and power for x = 12, n = 30, α = 0.05

In this case our data cannot discriminate whether is greater than the null value of 0.25 but less than 0.50, because the power of the study is too low (<80%) for those values of <0.50—that is, the sensitivity of our study is 8% for = 0.3, 22% for = 0.35,…, 64% for = 0.45.

The only way to achieve a lower β, or a higher level of power, would be to increase the size of the study. For example, in table 7 we report β and power for n = 40; as expected, we should be able to detect a  value greater than 0.40. 

Table 7. Type II error and power for x = 12, n = 40, α = 0.05

Study design is based on careful scrutiny of the set of alternative hypotheses which deserve consideration and guarantee power to the study providing an adequate sample size.

In the epidemiological literature, the relevance of providing reliable risk estimates has been emphasized. Therefore, it is more important to report confidence intervals (either 95% or 90%) than a p-value of a test of a hypothesis. Following the same kind of reasoning, attention should be given to the interpretation of results from small-sized studies: because of low power, even intermediate effects could be undetected and, on the other hand, effects of great magnitude might not be replicated subsequently.

Advanced Methods

The degree of complexity of the statistical methods used in the occupational medicine context has been growing over the last few years. Major developments can be found in the area of statistical modelling. The Nelder and Wedderburn family of non-Gaussian models (Generalized Linear Models) has been one of the most striking contributions to the increase of knowledge in areas such as occupational epidemiology, where the relevant response variables are binary (e.g., survival/death) or counts (e.g., number of industrial accidents).

This was the starting point for an extensive application of regression models as an alternative to the more traditional types of analysis based on contingency tables (simple and stratified analysis). Poisson, Cox and logistic regression are now routinely used for the analysis of longitudinal and case-control studies, respectively. These models are the counterpart of linear regression for categorical response variables and have the elegant feature of providing directly the relevant epidemiological measure of association. For example, the coefficients of Poisson regression are the logarithm of the rate ratios, while those of logistic regression are the log of the odds ratios.

Taking this as a benchmark, further developments in the area of statistical modelling have taken two main directions: models for repeated categorical measures and models which extend the Generalized Linear Models (Generalized Additive Models). In both instances, the aims are focused on increasing the flexibility of the statistical tools in order to cope with more complex problems arising from reality. Repeated measures models are needed in many occupational studies where the units of analysis are at the sub-individual level. For example:

1. The study of the effect of working conditions on carpal tunnel syndrome has to consider both hands of a person, which are not independent from one other.
2. The analysis of time trends of environmental pollutants and their effect on children’s respiratory systems can be evaluated using extremely flexible models since the exact functional form of the dose-response relationship is difficult to obtain.

A parallel and probably faster development has been seen in the context of Bayesian statistics. The practical barrier of using Bayesian methods collapsed after the introduction of computer-intensive methods. Monte Carlo procedures such as Gibbs sampling schemes have allowed us to avoid the need for numerical integration for computing the posterior distributions which represented the most challenging feature of Bayesian methods. The number of applications of Bayesian models in real and complex problems have found increasing space in applied journals. For example, geographical analyses and ecological correlations at the small area level and AIDS prediction models are more and more often tackled using Bayesian approaches. These developments are welcomed because they represent not only an increase in the number of alternative statistical solutions which could be employed in the analysis of epidemiological data, but also because the Bayesian approach can be considered a more sound strategy.

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Errors in exposure measurement may have different impacts on the exposure-disease relationship being studied, depending on how the errors are distributed. If an epidemiological study has been conducted blindly (i.e., measurements have been taken with no knowledge of the disease or health status of the study participants) we expect that measurement error will be evenly distributed across the strata of disease or health status.

Table 1 provides an example: suppose we recruit a cohort of people exposed at work to a toxicant, in order to investigate a frequent disease. We determine the exposure status only at recruitment (T₀), and not at any further points in time during follow-up. However, let us say that a number of individuals do, in fact, change their exposure status in the following year: at time T₁, 250 of the original 1,200 exposed people have ceased being exposed, while 150 of the original 750 non-exposed people have started to be exposed to the toxicant. Therefore, at time T₁, 1,100 individuals are exposed and 850 are not exposed. As a consequence, we have “misclassification” of exposure, based on our initial measurement of exposure status at time T₀. These individuals are then traced after 20 years (at time T₂) and the cumulative risk of disease is evaluated. (The assumption being made in the example is that only exposure of more than one year is a concern.)

Table 1. Hypothetical cohort of 1950 individuals (exposed and unexposed at work), recruited at time T₀ and whose disease status is ascertained at time T₂

Exposed workers                                1200      250 quit exposure       1100 (1200-250+150)

Cases of disease at time T₂ = 220 among exposed workers

Non-exposed workers                         750        150 start exposure      850 (750-150+250)

Cases of disease at time T₂ = 85 among non-exposed workers

The true risk of disease at time T₂ is 20% among exposed workers (220/1100),
and 10% in non-exposed workers (85/850) (risk ratio = 2.0).

Estimated risk at T₂ of disease among those classified as exposed at T₀: 20%
(i.e., true risk in those exposed) ´ 950 (i.e., 1200-250)+ 10%
(i.e., true risk in non-exposed) ´ 250 = (190+25)/1200 = 17.9%

Estimated risk at T₂ of disease among those classified as non-exposed at
T₀: 20% (i.e., true risk in those exposed) ´ 150 +10%
(i.e., true risk innon-exposed) ´ 600 (i.e., 750-150) = (30+60)/750 = 12%

Estimated risk ratio = 17.9% / 12% = 1.49

Misclassification depends, in this example, on the study design and the characteristics of the population, rather than on technical limitations of the exposure measurement. The effect of misclassification is such that the “true” ratio of 2.0 between the cumulative risk among exposed people and non-exposed people becomes an “observed” ratio of 1.49 (table 1). This underestimation of the risk ratio arises from a “blurring” of the relationship between exposure and disease, which occurs when the misclassification of exposure, as in this case, is evenly distributed according to the disease or health status (i.e., the exposure measurement is not influenced by whether or not the person suffered from the disease that we are studying).

By contrast, either underestimation or overestimation of the association of interest may occur when exposure misclassification is not evenly distributed across the outcome of interest. In the example, we may have bias, and not only a blurring of the aetiologic relationship, if classification of exposure depends on the disease or health status among the workers. This could arise, for example, if we decide to collect biological samples from a group of exposed workers and from a group of unexposed workers, in order to identify early changes related to exposure at work. Samples from the exposed workers might then be analysed in a more accurate way than samples from those unexposed; scientific curiosity might lead the researcher to measure additional biomarkers among the exposed people (including, e.g., DNA adducts in lymphocytes or urinary markers of oxidative damage to DNA), on the assumption that these people are scientifically “more interesting”. This is a rather common attitude which, however, could lead to serious bias.

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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.

Internal Validity

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
• confounding

They will be presented briefly below, using examples from the occupational health setting.

Selection bias

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.

Self-selection bias

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.

Diagnostic bias

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.

Information bias

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

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.

External Validity

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.

Study design

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.

Selection

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.

Information

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

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.

Conclusion

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.

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Epidemiology involves measuring the occurrence of disease and quantifying associations between diseases and exposures.

Measures of Disease Occurrence

Disease occurrence can be measured by frequencies (counts) but is better described by rates, which are composed of three elements: the number of people affected (numerator), the number of people in the source or base population (i.e., the population at risk) from which the affected persons come, and the time period covered. The denominator of the rate is the total person-time experienced by the source population. Rates allow more informative comparisons between populations of different sizes than counts alone. Risk, the probability of an individual developing disease within a specified time period, is a proportion, ranging from 0 to 1, and is not a rate per se. Attack rate, the proportion of people in a population who are affected within a specified time period, is technically a measure of risk, not a rate.

Disease-specific morbidity includes incidence, which refers to the number of persons who are newly diagnosed with the disease of interest. Prevalence refers to the number of existing cases. Mortality refers to the number of persons who die.

Incidence is defined as the number of newly diagnosed cases within a specified time period, whereas the incidence rate is this number divided by the total person-time experienced by the source population (table 1). For cancer, rates are usually expressed as annual rates per 100,000 people. Rates for other more common diseases may be expressed per a smaller number of people. For example, birth defect rates are usually expressed per 1,000 live births. Cumulative incidence, the proportion of people who become cases within a specified time period, is a measure of average risk for a population. 

Table 1. Measures of disease occurrence: Hypothetical population observed for a five-year period

*To simplify the calculations, this example assumes that all deaths occurred at the end of the five-year period so that all 100 persons in the population were alive for the full five years.

Prevalence includes point prevalence, the number of cases of disease at a point in time, and period prevalence, the total number of cases of a disease known to have existed at some time during a specified period.

Mortality, which concerns deaths rather than newly diagnosed cases of disease, reflects factors that cause disease as well as factors related to the quality of medical care, such as screening, access to medical care, and availability of effective treatments. Consequently, hypothesis-generating efforts and aetiological research may be more informative and easier to interpret when based on incidence rather than on mortality data. However, mortality data are often more readily available on large populations than incidence data.

The term death rate is generally accepted to mean the rate for deaths from all causes combined, whereas mortality rate is the rate of death from one specific cause. For a given disease, the case-fatality rate (technically a proportion, not a rate) is the number of persons dying from the disease during a specified time period divided by the number of persons with the disease. The complement of the case-fatality rate is the survival rate. The five-year survival rate is a common benchmark for chronic diseases such as cancer.

The occurrence of a disease may vary across subgroups of the population or over time. A disease measure for an entire population, without consideration of any subgroups, is called a crude rate. For example, an incidence rate for all age groups combined is a crude rate. The rates for the individual age groups are the age-specific rates. To compare two or more populations with different age distributions, age-adjusted (or, age-standardized) rates should be calculated for each population by multiplying each age-specific rate by the per cent of the standard population (e.g., one of the populations under study, the 1970 US population) in that age group, then summing over all age groups to produce an overall age-adjusted rate. Rates can be adjusted for factors other than age, such as race, gender or smoking status, if the category-specific rates are known.

Surveillance and evaluation of descriptive data can provide clues to disease aetiology, identify high-risk subgroups that may be suitable for intervention or screening programmes, and provide data on the effectiveness of such programmes. Sources of information that have been used for surveillance activities include death certificates, medical records, cancer registries, other disease registries (e.g., birth defects registries, end-stage renal disease registries), occupational exposure registries, health or disability insurance records and workmen’s compensation records.

Measures of Association

Epidemiology attempts to identify and quantify factors that influence disease. In the simplest approach, the occurrence of disease among persons exposed to a suspect factor is compared to the occurrence among persons unexposed. The magnitude of an association between exposure and disease can be expressed in either absolute or relative terms. (See also "Case Study: Measures").

Absolute effects are measured by rate differences and risk differences (table 2). A rate difference is one rate minus a second rate. For example, if the incidence rate of leukaemia among workers exposed to benzene is 72 per 100,000 person-years and the rate among non-exposed workers is 12 per 100,000 person-years, then the rate difference is 60 per 100,000 person-years. A risk difference is a difference in risks or cumulative incidence and can range from -1 to 1. 

Table 2. Measures of association for a cohort study

Rate Difference (RD) = 500/100,000 - 250/100,000

= 250/100,000 per year

(146.06/100,000 - 353.94/100,000)*

Rate ratio (or relative risk) (RR) =  

Attributable risk in the exposed (AR_e) = 100/20,000 - 200/80,000

= 250/100,000 per year

Attributable risk per cent in the exposed (AR_e%) =

 Population attributable risk (PAR) = 300/100,000 - 200/80,000

= 50/100,000 per year

Population attributable risk per cent (PAR%) =

 * In parentheses 95% confidence intervals computed using the formulas in the boxes.

Relative effects are based on ratios of rates or risk measures, instead of differences. A rate ratio is the ratio of a rate in one population to the rate in another. The rate ratio has also been called the risk ratio, relative risk, relative rate, and incidence (or mortality) rate ratio. The measure is dimensionless and ranges from 0 to infinity. When the rate in two groups is similar (i.e., there is no effect from the exposure), the rate ratio is equal to unity (1). An exposure that increased risk would yield a rate ratio greater than unity, while a protective factor would yield a ratio between 0 and 1. The excess relative risk is the relative risk minus 1. For example, a relative risk of 1.4 may also be expressed as an excess relative risk of 40%.

In case-control studies (also called case-referent studies), persons with disease are identified (cases) and persons without disease are identified (controls or referents). Past exposures of the two groups are compared. The odds of being an exposed case is compared to the odds of being an exposed control. Complete counts of the source populations of exposed and unexposed persons are not available, so disease rates cannot be calculated. Instead, the exposed cases can be compared to the exposed controls by calculation of relative odds, or the odds ratio (table 3). 

Table 3. Measures of association for case-control studies: Exposure to wood dust and adenocarcinoma of the nasal cavity and paranasal sinues

Relative odds (odds ratio) (OR) =

Attributable risk per cent in the exposed () =

Population attributable risk per cent (PAR%) =

where = proportion of exposed controls = 55/195 = 0.28

* In parentheses 95% confidence intervals computed using the formulas in the box overleaf.

Source: Adapted from Hayes et al. 1986.

Relative measures of effect are used more frequently than absolute measures to report the strength of an association. Absolute measures, however, may provide a better indication of the public health impact of an association. A small relative increase in a common disease, such as heart disease, may affect more persons (large risk difference) and have more of an impact on public health than a large relative increase (but small absolute difference) in a rare disease, such as angiosarcoma of the liver.

Significance Testing

Testing for statistical significance is often performed on measures of effect to evaluate the likelihood that the effect observed differs from the null hypothesis (i.e., no effect). While many studies, particularly in other areas of biomedical research, may express significance by p-values, epidemiological studies typically present confidence intervals (CI) (also called confidence limits). A 95% confidence interval, for example, is a range of values for the effect measure that includes the estimated measure obtained from the study data and that which has 95% probability of including the true value. Values outside the interval are deemed to be unlikely to include the true measure of effect. If the CI for a rate ratio includes unity, then there is no statistically significant difference between the groups being compared.

Confidence intervals are more informative than p-values alone. A p-value’s size is determined by either or both of two reasons. Either the measure of association (e.g., rate ratio, risk difference) is large or the populations under study are large. For example, a small difference in disease rates observed in a large population may yield a highly significant p-value. The reasons for the large p-value cannot be identified from the p-value alone. Confidence intervals, however, allow us to disentangle the two factors. First, the magnitude of the effect is discernible by the values of the effect measure and the numbers encompassed by the interval. Larger risk ratios, for example, indicate a stronger effect. Second, the size of the population affects the width of the confidence interval. Small populations with statistically unstable estimates generate wider confidence intervals than larger populations.

The level of confidence chosen to express the variability of the results (the “statistical significance”) is arbitrary, but has traditionally been 95%, which corresponds to a p-value of 0.05. A 95% confidence interval has a 95% probability of containing the true measure of the effect. Other levels of confidence, such as 90%, are occasionally used.

Exposures can be dichotomous (e.g., exposed and unexposed), or may involve many levels of exposure. Effect measures (i.e., response) can vary by level of exposure. Evaluating exposure-response relationships is an important part of interpreting epidemiological data. The analogue to exposure-response in animal studies is “dose-response”. If the response increases with exposure level, an association is more likely to be causal than if no trend is observed. Statistical tests to evaluate exposure-response relationships include the Mantel extension test and the chi-square trend test.

Standardization

To take into account factors other than the primary exposure of interest and the disease, measures of association may be standardized through stratification or regression techniques. Stratification means dividing the populations into homogenous groups with respect to the factor (e.g., gender groups, age groups, smoking groups). Risk ratios or odds ratios are calculated for each stratum and overall weighted averages of the risk ratios or odds ratios are calculated. These overall values reflect the association between the primary exposure and disease, adjusted for the stratification factor, i.e., the association with the effects of the stratification factor removed.

A standardized rate ratio (SRR) is the ratio of two standardized rates. In other words, an SRR is a weighted average of stratum-specific rate ratios where the weights for each stratum are the person-time distribution of the non-exposed, or referent, group. SRRs for two or more groups may be compared if the same weights are used. Confidence intervals can be constructed for SRRs as for rate ratios.

The standardized mortality ratio (SMR) is a weighted average of age-specific rate ratios where the weights (e.g., person-time at risk) come from the group under study and the rates come from the referent population, the opposite of the situation in a SRR. The usual referent population is the general population, whose mortality rates may be readily available and based on large numbers and thus are more stable than using rates from a non-exposed cohort or subgroup of the occupational population under study. Using the weights from the cohort instead of the referent population is called indirect standardization. The SMR is the ratio of the observed number of deaths in the cohort to the expected number, based on the rates from the referent population (the ratio is typically multiplied by 100 for presentation). If no association exists, the SMR equals 100. It should be noted that because the rates come from the referent population and the weights come from the study group, two or more SMRs tend not to be comparable. This non-comparability is often forgotten in the interpretation of epidemiological data, and erroneous conclusions can be drawn.

Healthy Worker Effect

It is very common for occupational cohorts to have lower total mortality than the general population, even if the workers are at increased risk for selected causes of death from workplace exposures. This phenomenon, called the healthy worker effect, reflects the fact that any group of employed persons is likely to be healthier, on average, than the general population, which includes workers and persons unable to work due to illnesses and disabilities. The overall mortality rate in the general population tends to be higher than the rate in workers. The effect varies in strength by cause of death. For example, it appears to be less important for cancer in general than for chronic obstructive lung disease. One reason for this is that it is likely that most cancers would not have developed out of any predisposition towards cancer underlying job/career selection at a younger age. The healthy worker effect in a given group of workers tends to diminish over time.

Proportional Mortality

Sometimes a complete tabulation of a cohort (i.e., person-time at risk) is not available and there is information only on the deaths or some subset of deaths experienced by the cohort (e.g., deaths among retirees and active employees, but not among workers who left employment before becoming eligible for a pension). Computation of person-years requires special methods to deal with person-time assessment, including life-table methods. Without total person-time information on all cohort members, regardless of disease status, SMRs and SRRs cannot be calculated. Instead, proportional mortality ratios (PMRs) can be used. A PMR is the ratio of the observed number of deaths due to a specific cause in comparison to the expected number, based on the proportion of total deaths due to the specific cause in the referent population, multiplied by the number of total deaths in the study group, multiplied by 100.

Because the proportion of deaths from all causes combined must equal 1 (PMR=100), some PMRs may appear to be in excess, but are actually artificially inflated due to real deficits in other causes of death. Similarly, some apparent deficits may merely reflect real excesses of other causes of death. For example, if aerial pesticide applicators have a large real excess of deaths due to accidents, the mathematical requirement that the PMR for all causes combined equal 100 may cause some one or other causes of death to appear deficient even if the mortality is excessive. To ameliorate this potential problem, researchers interested primarily in cancer can calculate proportionate cancer mortality ratios (PCMRs). PCMRs compare the observed number of cancer deaths to the number expected based on the proportion of total cancer deaths (rather than all deaths) for the cancer of interest in the referent population multiplied by the total number of cancer deaths in the study group, multiplied by 100. Thus, the PCMR will not be affected by an aberration (excess or deficit) in a non-cancer cause of death, such as accidents, heart disease or non-malignant lung disease.

PMR studies can better be analysed using mortality odds ratios (MORs), in essence analysing the data as if they were from a case-control study. The “controls” are the deaths from a subset of all deaths that are thought to be unrelated to the exposure under study. For example, if the main interest of the study were cancer, mortality odds ratios could be calculated comparing exposure among the cancer deaths to exposure among the cardiovascular deaths. This approach, like the PCMR, avoids the problems with the PMR which arise when a fluctuation in one cause of death affects the apparent risk of another simply because the overall PMR must equal 100. The choice of the control causes of death is critical, however. As mentioned above, they must not be related to the exposure, but the possible relationship between exposure and disease may not be known for many potential control diseases.

Attributable Risk

There are measures available which express the amount of disease that would be attributable to an exposure if the observed association between the exposure and disease were causal. The attributable risk in the exposed (AR_e) is the disease rate in the exposed minus the rate in the unexposed. Because disease rates cannot be measured directly in case-control studies, the AR_e is calculable only for cohort studies. A related, more intuitive, measure, the attributable risk percent in the exposed (AR_e%), can be obtained from either study design. The AR_e% is the proportion of cases arising in the exposed population that is attributable to the exposure (see table 2 and table 3 for formula). The AR_e% is the rate ratio (or the odds ratio) minus 1, divided by the rate ratio (or odds ratio), multiplied by 100.

The population attributable risk (PAR) and the population attributable risk per cent (PAR%), or aetiological fraction, express the amount of disease in the total population, which is comprised of exposed and unexposed persons, that is due to the exposure if the observed association is causal. The PAR can be obtained from cohort studies (table 28.3 ) and the PAR% can be calculated in both cohort and case-control studies (table 2 and table 3).

Representativeness

There are several measures of risk that have been described. Each assumes underlying methods for counting events and in the representatives of these events to a defined group. When results are compared across studies, an understanding of the methods used is essential for explaining any observed differences.

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