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BIAS & CONFOUNDING
M.Tevfik DORAK
Glossary of Bias: Delgado-Rodriguez & Llorca, 2004
Introduction
In epidemiologic research, it is essential to avoid bias, to control confounding and to undertake accurate
replication. Bias, confounding and random variation/chance are the non-causal reasons for an
association between an exposure and outcome. These major threats to internal validity of a study should
always be considered as alternative explanations in the interpretation. Bias is a mistake of the
researcher; confounding is not a mistake and when obvious, it can be controlled; replication is up to the
researcher.
Bias is defined as 'any systematic error in an epidemiologic study that results in an incorrect estimate of
the association between exposure and risk of disease.' Two major classes of bias are:
1. Selection bias
2. Observation/information (misclassification) bias
Selection bias is an important problem in case-control and retrospective cohort studies while it is unlikely
to occur in a prospective cohort study. The observation bias group include recall bias, interviewer bias,
follow-up bias and misclassification bias.
Confounding is sometimes referred to as the third major class of bias. It is a function of the complex
interrelationships between various exposures and disease. Confounding can be controlled in the design
(randomisation, restriction and matching) and in the analysis (stratification, multivariate analysis and
matching). The best that can be done about unknown confounders is to use a randomised design.
Bias and confounding are not affected by sample size but chance effect (random variation) diminishes as
sample size gets larger. A small P value and a narrow odds ratio/relative risk are reassuring signs
against chance effect but the same cannot be said for bias and confounding.
Types of bias
Chance findings are caused by random variation but bias is caused by systematic variation. Potential
sources of bias should be eliminated or minimised through rigorous design and meticulous conduct of a
study. Each analytic study design has particular types of bias to which it is most vulnerable. In casecontrol studies, selection bias (knowledge of exposure status influences the identification of diseased and
nondiseased study subjects) and recall bias (knowledge of disease status influences the determination of
exposure status) are most important. In cohort studies, bias due to loss to follow-up (attrition) would be
the greatest danger (and selection bias in retrospective studies). The potential for misclassification is
present in all types of epidemiologic studies. Despite all preventive efforts, bias should always be
considered among alternative explanations of a finding. It has to be remembered that bias may mask an
association or cause a spurious one; and it may cause over or underestimation of the effect size. A study
that suffers from bias lacks internal validity. The list presented below may help to consider potential
sources of bias in planning, executing, and interpreting a study.
Following the classic paper by Sackett (1979), biases are classified according to stages of research:
* Literature Review
- Foreign language exclusion bias
- Literature search bias
- One-sided reference bias
- Rhetoric bias
* Study Design
- Selection bias
- Sampling frame bias
Berkson (admission rate) bias
Centripetal bias
Diagnostic access bias
Diagnostic purity bias
Hospital access bias
Migrator bias
Prevalence-incidence (Neyman / selective survival; attrition) bias
Telephone sampling bias
- Nonrandom sampling bias
Autopsy series bias
Detection bias
Diagnostic work-up bias
Door-to-door solicitation bias
Previous opinion bias
Referral filter bias
Sampling bias
Self-selection bias
Unmasking bias
- Noncoverage bias
Early-comer bias
Illegal immigrant bias
Loss to follow-up (attrition) bias
Response bias
Withdrawal bias
- Noncomparability bias
Ecological (aggregation) bias
Healthy worker effect (HWE)
Lead-time bias
Length bias
Membership bias
Mimicry bias
Nonsimultaneous comparison bias
Sample size bias
* Study Execution
Bogus control bias
Contamination bias
Compliance bias
* Data Collection
- Instrument bias
Case definition bias
Diagnostic vogue bias
Forced choice bias
Framing bias
Insensitive measure bias
Juxtaposed scale bias
Laboratory data bias
Questionnaire bias
Scale format bias
Sensitive question bias
Stage bias
Unacceptability bias
Underlying/contributing cause of death bias
Voluntary reporting bias
- Data source bias
Competing death bias
Family history bias
Hospital discharge bias
Spatial bias
- Observer bias
Diagnostic suspicion bias
Exposure suspicion bias
Expectation bias
Interviewer bias
Therapeutic personality bias
- Subject bias
Apprehension bias
Attention bias (Hawthorne effect)
Culture bias
End-aversion bias (end-of-scale or central tendency bias)
Faking bad bias
Faking good bias
Family information bias
Interview setting bias
Obsequiousness bias
Positive satisfaction bias
Proxy respondent bias
- Recall bias
Reporting bias
Response fatigue bias
Unacceptable disease bias
Unacceptable exposure bias
Underlying cause (rumination bias)
Yes-saying bias
- Data handling bias
Data capture error
Data entry bias
Data merging error
Digit preference bias
Record linkage bias
* Analysis
- Confounding bias
Latency bias
Multiple exposure bias
Nonrandom sampling bias
Standard population bias
Spectrum bias
- Analysis strategy bias
Distribution assumption bias
Enquiry unit bias
Estimator bias
Missing data handling bias
Outlier handling bias
Overmatching bias
Scale degradation bias
- Post hoc analysis bias
Data dredging bias
Post hoc significance bias
Repeated peeks bias
* Interpretation of Results
Assumption bias
Cognitive dissonance bias
Correlation bias
Generalisation bias
Magnitude bias
Significance bias
Underexhaustion bias
* Publication
All's well literature bias
Positive result bias
Hot topic bias
Potential effects of sources of bias may be:
1. Positive bias: The observed measure of effect (eg, odds ratio) is larger than the true measure of effect
(applies to both protective and risk associations)
2. Negative bias: The observed measure of effect is smaller than the true measure of effect
3. Toward the null: The observed measure of effect is closer to 1.0 than the true measure of effect
4. Away from the null: The observed measure of effect is farther from 1.0 than the true measure of effect
Most important biases:
Prevalence-incidence bias: Selective survival may be important in some conditions. For these diseases
(such as cancer, HIV infection) the use of prevalent instead of incident cases usually distorts the
measure of effect. The frequency of glutathione S-transferase class mu (GSTM) deletion is for example
different in incident (newly and sequentially diagnosed) cases and prevalent (all patients at a point in
time) cases (Kelsey, 1997).
Berkson (admission rate) bias: Where cases/controls are recruited from among hospital patients, the
characteristics of these groups will be influenced by hospital admission rates.
Healthy Worker Effect (HWE): The overall mortality experience of an employed population is typically
better than that of the general population (in Western countries at least). Use of blood donors as controls
is a kind of HWE. Blood donors are self-selected on the basis of better life styles.
Detection bias: The risk factor investigated itself may lead to increased diagnostic investigations and
increase the probability that the disease is identified in that subset of persons. An example is women with
benign breast diseases who undergo detailed follow-up programs which would detect cancer at early
stages (Silber & Horwitz, 1986).
Recall bias: Recall bias is caused by differences in accuracy of recalling past events by cases and
controls. There is a tendency for diseased people (or their relatives) to recall past exposures more
efficiently than healthy people (selective recall). For example, because women with breast cancer are
more likely to remember a positive family history than control subjects, retrospective study designs are
likely to overestimate the effect size of family history as a risk factor. This bias is avoided by prospective
studies, and indeed the risk estimates from prospective cohorts are less than those for other types of
study. Another example is the mothers of leukaemic children who would remember even trivial
exposures.
Family information bias: Within a family, the flow of information about exposures and diseases is
stimulated by a family member who develops the disease. A person who develops a disease is more
likely than his or her unaffected siblings to know that a parent has a history of the disease.
Non-respondent bias: Non-respondents to a survey often differ from respondents. Volunteers also differ
from non-volunteers, late respondents from early respondents, and study dropouts from those who
complete the study.
Misclassification bias: This is systematic distortion of estimates resulting from inaccuracy in measurement
of classification of study variables. Non-differential misclassification generally dilutes the exposure effect
(toward to null effect) (Copeland, 1977). It is worse when the proportions of subjects misclassified differ
between the study groups (differential misclassification). Such a differential between cases and controls
may mask an association or cause one when there is none. This type of misclassification is rare when
exposures are recorded before the outcome is known. This bias usually results from deeper investigation
or surveillance of cases. Typical sources of misclassification/information bias are:
- variation among observers and among instruments
- variation in the underlying characteristic
- misunderstanding of questions by study subjects (interview or questionnaire)
- incomplete or inaccurate record data
Selection bias due to missing data: When there are a large number of variables, the regression
procedure excludes an entire observation if it is missing a value for any of the variables (listwise
deletion). This may result in exclusion of a considerable percentage of observations and induce selection
bias.
Regression to mean: This is an example of how random variability can lead to systematic error (Davis,
1976). An example would be a follow-up study of people with highly elevated cholesterol levels. During
follow-up, part of reduction in cholesterol levels would be due to regression to the mean rather than drug
of life modification effects. Because the initial very high level was partly because of a large positive
random component (and of course, some were truly very high). This is an information bias mainly
concerning cohort studies.
End-aversion bias (end-of-scale or central tendency bias): In questionnaire-based surveys, respondents
usually avoid ends of scales in their answers. They tend to try to be conservative and wish to be in the
middle.
Overmatching bias: When cases and controls are matched by a non-confounding variable (associated to
the exposure but not to the disease), this is called overmatching. Overmatching can underestimate an
association.
Competing death bias: As each person will only die once, if there are mutually exclusive causes of death,
they compete with each other in the same subject (Chiang, 1991). For example, in parenteral drug users,
liver failure and AIDS are competing causes of death and may influence any research on either subject.
Likewise, the apolipoprotein E genotype is associated with cardiovascular disease mortality and
Alzheimer's disease; AD and death are competing risks involving apolipoprotein E genotype frequency
changes with old age (Corder, 1995).
Publication bias: Editors and authors tend to publish articles containing positive findings as opposed to
negative result papers. This results in a belief that there is a consistent association while this may not be
the case. Plots of relative risks by study may be used to check publication bias in meta-analyses. If
publication bias is operating, one would expect that, of published studies, the larger ones report the
smaller effects, as small positive trials are more likely to be published than negative ones. This can be
examined using the funnel plot in which the effect size is plotted against sample size (Sterne & Egger,
2001). If this is done, the plot resembles an inverted funnel, with the results of the smaller studies being
more widely scattered than those of the larger studies, as would be expected if there is no publication
bias.
Confounding
Bias involves error in the measurement of a variable; confounding involves error in the interpretation of
what may be an accurate measurement. Confounding in epidemiology is mixing of the effect of the
exposure under study on the disease (outcome) with that of a third factor that is associated with the
exposure and an independent risk factor for the disease (even among individuals nonexposed to the
exposure factor under study). The consequence of confounding is that the estimated association is not
the same as true effect. In contrast to other forms of bias, in confounding bias the actual data collected
may be correct but the subsequent effect attributed to the exposure of interest is actually caused by
something else. Classic example of confounding is the initial association between alcohol consumption
and lung cancer (confounded by smoking, which is associated with alcohol use and an independent risk
factor for lung cancer). Likewise, an association between gambling and cancer is confounded by at least
smoking and alcohol. Confounding can cause overestimation or underestimation of the true association
and may even change the direction of the observed effect. An example is the confounding by age of an
inverse association between level of exercise and heart attacks (younger people having more rigorous
exercise) causing overestimation. The same association can also be confounded by sex (men having
more rigorous exercise) causing underestimation of the association. For a variable to confound an
association, it must be associated both with the exposure and outcome, and its relation to the outcome
should be independent of its association with the exposure (i.e., not through its association with the
exposure). Confounding factor should not be an intermediate link in the causal chain between the
exposure and disease under study. Age and sex are associated with virtually all diseases and are related
to the presence or level of many exposures. Even though they act as surrogates for etiologic factors most
of the time, age and sex should always be considered as potential confounders of an association.
Confounders can be positive or negative. Positive confounders cause overestimation of an association
(which may be an inverse association), and negative confounders cause underestimation of an
association. It is not easy to recognise confounders. A practical way to achieve this is to analyse the data
with and without controlling for the potential confounders. If the estimate of the association differs
remarkably when controlled for the variable, it is a confounder and should be controlled for (by
stratification or multivariate analysis). To be able to do this, investigators should make every effort to
obtain data on all available risk factors for the disease under study.
A factor can confound an association only if it differs between the study groups. Therefore, in a casecontrol study, for age and sex to be confounders, their representation should sufficiently differ between
cases and controls. This is the basis of methods to control confounding in the design. Randomisation
(ensures that potential confounding factors, known or unknown, are evenly distributed among the study
groups), restriction (restricts admission to the study to a certain category of a confounder) and
matching (equal representation of subjects with certain confounders among study groups) can overcome
a great deal of confounding. The protection against confounders obtained by randomisation will only be
maintained if all participants remain in the group to which they were allocated and no systematic loss to
follow-up occurs. To avoid this possibility, it is best to try to maximise follow up and carry out an intention
to treat analysis (Hollis & Campbell, 1999). In practice, restriction ensures comparisons to be performed
only between observations that have the same value of the confounder (for example only white men);
and matching ensures comparisons between groups that have the same distribution of the confounder
(frequency matching or one-to-one matching). In addition to the extra effort, time, money and loss of
potential study subjects, the more important disadvantage of restriction and matching is the inability to
evaluate the effect of the variable used for restriction or matching. One other problem with matching is
that in the analysis, the effective sample size is reduced because the analyses are based on only
discordant pairs. Despite the use of these methods, at the analysis stage of a study, it may still be
necessary to control for residual confounding. For example if a study of heart attacks restricted the entry
to 40-65 year-old subjects, there may still be an age effect (residual confounding) within this range.
Methods used to control for confounding at the analysis stage include stratified analysis (unable to
control simultaneously for even a moderate number of potential confounders) and multivariable
analysis (can control for a number of confounding factors simultaneously as long as there are at least
ten subjects for every variable investigated -in a logistic regression situation-). If matching was done,
then the most common analysis methods would be McNemar test or conditional logistic regression.
Glossary of Bias: Delgado-Rodriguez & Llorca, 2004
References
- Armitage P & Colton T. Encyclopedia of Biostatistics. Volumes 1-6. John Wiley & Sons, 1998 (Bias in
Observational Studies section by HA Hill & DG Kleinbaum)
- Bandolier Bias Guide
- Bias in Clinical Research (exercises)
- Bias & Effect Modification Presentation
- Boffetta P. Molecular epidemiology. J Intern Med 2000;248:447-54
- Bradford Hill A & Hill ID: Bradford Hill's Principles of Medical Statistics. London: Edward Arnold. 12th
Edition, 1991
- Davey Smith G & Ebrahim S. Data dredging, bias, or confounding. BMJ 2002;325: 1437–8
- Epidemiology for the Uninitiated
- Greenland S & Morgenstern H. Confounding in health research. Annu Rev Public Health 2001;22:189212 (PDF)
- Hennekens CH, Buring JE, Mayrent SL (Eds). Epidemiology in Medicine. Boston: Little, Brown and
Company. 1987 (Amazon)
- Kaptchuk TJ. Effect of interpretive bias on research evidence. BMJ 2003;326:1453-5
- Katz MH. Multivariable Analysis. Ann Intern Med 2003;138:644-50
- Potter JD. Epidemiology, cancer genetics and microarrays: making correct inferences, using
appropriate designs. Trends Genet 2003;19:690-4
- Sackett DL. Bias in analytic research. J Chronic Dis 1979;32:51-63
- Schoenbach VJ & Rosamond WD. Understanding the Fundamentals of Epidemiology
- Taioli E & Garte S. Covariates and confounding in epidemiologic studies using metabolic gene
polymorphisms. Int J Cancer 2002;100:97-100
- Vineis P & McMichael AJ. Bias and confounding in molecular epidemiological studies. Carcinogenesis
1998;19:2063-7
See also: Choi & Noseworthy, 1992; Grimez & Schulz, 2002
Epidemiology Links
Extensive Epidemiology and Biostatistics Links Online Dictionary of Epidemiology
Epidemiology & BioStatistics Super Lectures
Epidemiolog.Net
Online Epidemiology Textbook
Basic Statistics and Trial Design for Clinicians
Bias & Confounding in Clinical Trials
Radiology Statistical Concepts Series Article: Bias
A Catalog of Biases in Questionnaires (CDC)
Error, Bias & Confounding Presentation (WHO)
M.Tevfik Dorak, M.D., Ph.D.
Last updated on 18 April 2005
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