BIAS & CONFOUNDING
M.Tevfik DORAK
Bias and Confounding Lecture (PPT)
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 less likely to occur in a prospective cohort study. Selection bias cannot be
completely excluded in a case-control study because nonparticipation between case
patients and control subjects may have differed. The major types of bias in 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, multivariable 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 considerations and meticulous conduct of a study. Each analytic study design
has particular types of bias to which it is most vulnerable. In case-control studies,
selection bias (knowledge of exposure status influences the identification of diseased
and non-diseased 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
- may cause over or underestimation of the effect size
Increasing the sample size will not eliminate any bias. A study that suffers from bias
lacks internal validity.
Most simplistically, there are three types of bias: (1) selection bias, (2) information /
misclassification bias, (3) confounding bias. This basic classification derived from the
studies by Miettinen in the 1970s (see for example Miettinen & Cook, 1981). 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) (Wickström, 2000)
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:
(Note that many biases can be grouped in different classes which may be confusing.
They may also have different names in different contexts.)
Ascertainment Bias: Systematic error arising from the kind of individuals or patients that
the individual observer is seeing. Also systematic error arising from the diagnostic
process.
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: This is a special example of selection bias. Where
cases/controls are recruited from among hospital patients, the characteristics of these
groups will be influenced by hospital admission rates. This occurs when the combination
of exposure and disease under study increases the risk of hospital admission, thus
leading to a higher exposure rate among the hospital cases than the hospital controls
(Berkson J. Limitations of the application of fourfold table analysis to hospital data.
Biometrics Bulletin 1946;2:47-53). Examples include oral contraceptive usage and deep
vein thrombosis suspicion leading to higher referral rate to hospitals; usage of nonsteroid anti-inflammatory drugs and peptic ulcer (lower co-occurrence in hospital controls
with peptic ulcer) or orthopaedic disorders (higher co-occurrence in hospital controls
from orthopaedic ward). For details, see Feinstein, 1986; Flanders, 1989; Schwartzbaum,
2003; Hernan, 2004.
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.
Design bias: The difference between a true unknown value and that actually observed,
occurring as result of faulty design of a study.
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).
Information bias: A flaw in measuring outcome or exposure that results in differential
accuracy of information between compared groups. Many different biases (recall,
reporting, measurement, withdrawal etc) are collectively grouped in this class.
Measurement bias: Systematic error arising from inaccurate measurement (or
classification) of subjects on the study variables.
Misclassification bias: This is systematic distortion of estimates resulting from inaccuracy
in measurement of classification of study variables. The probability of misclassification
may be the same in all study groups (nondifferential misclassification) or may vary
between groups (differential misclassification). 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 a spurious one. This type of misclassification is rare when
exposures are recorded before the outcome is known (as in cohort design). 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
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 smaller than those for other types
of study. Another example is the mothers of leukaemic children who would remember
even trivial exposures. This situation in the case group results in differential accuracy.
Reporting bias: Selective suppression or revealing of information such as past history of
sexually transmitted disease. There is no point in doing an HIV-positivity prevalence
study on people volunteering to be tested (selective suppression would result in no HIVpositives).
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. Also called response bias
(systematic error due to difference in characteristics between those who choose to
participate in a study and those who do not).
Sampling bias: Unless the sampling method ensures that all members of the 'universe'
or reference population have the same probability of inclusion in the sample, bias is
possible.
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. In genetic association studies, missing data may
be distributed differentially between cases and controls and may generate spurious
associations (Clayton, 2005).
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 or life modification effects. If
the initial very high level was partly because of a large positive random component (and
of course, some were truly very high), next time some of those high values will be found
closer to normal range. 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 that is associated to the exposure but not to the disease, this is called
overmatching. Overmatching can underestimate an association. For a numerical
example, see slides 41-49 in the Case-Control Studies presentation by Chen. See also
Bland & Altman, 1994 and Sorensen & Gillman, 1995. Matching should only be
considered for confounding variables but such known confounding can be controlled at
the analysis phase in an unmatched design.
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). Likewise, in parental drug users, AIDS and liver
failure are competing causes of death (Delgado-Rodriguez & Llorca, 2004).
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. One consequence of publication bias is that
the first report of a given association may suffer from an inflated effect size (Ioannidis,
2001). See Publication Bias in Cochrane Collaboration.
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 multivariable
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 case-control 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),
- 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.
In summary, for a variable to be a confounder it has to meet the following conditions:
1. Relationship with the exposure
2. Relationship with the outcome even in the absence of the exposure
3. Not on the causal pathway
4. Uneven distribution in comparison groups
5. Similar odds ratio (OR) or relative risks (RR) in stratified groups and this (adjusted)
OR/RR is at least 15% different from the crude OR/RR (see Confounding Lecture by S
Dorjee at ACVCS)
Thus, smoking confounds an association of alcohol drinking with lung cancer but alcohol
drinking does not confound association of smoking with lung cancer. Likewise, maternal
age is a confounder for birth order association in Down syndrome but the opposite is not
true (see examples in Bias and Confounding Lecture).
Effect modification is not bias or confounding and when found it actually provides
information for the nature of an association. Effect modification is not something that
violates internal validity of the study and has nothing to do with sample size. It is
explored by adding an interaction term to the statistical model and if statistically
significant, requires stratified analysis for different levels of the interacting factor (like sex
or age group). (See examples in Bias and Confounding Lecture and MHC & Leukaemia
Associations in Humans).
Glossary of Bias: Delgado-Rodriguez & Llorca, 2004
Glossary of Clinical Epidemiology: Clinical Epidemiology Glossary (University of
Alberta, EBM Toolkit)
ACVCS: Lectures on Bias, Confounding and Interaction
References
- Armitage P & Colton T. Encyclopedia of Biostatistics. Volumes 1-8. John Wiley & Sons,
2005 (Bias in Observational Studies section by HA Hill & DG Kleinbaum)
- Bandolier Bias Guide
- 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;22:189-212 (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 (PDF)
Papers on Flaws in Epidemiologic Research:
Taubes G: Epidemiology Faces Its Limits. Science 1995 (PDF); Scandal of Poor
Epidemiological Research, BMJ 2004; Unhealthy Science, NY Times, 2007.
Epidemiology Links
Extensive Epidemiology and Biostatistics Links
Epidemiology & BioStatistics Super Lectures
Epidemiolog.Net
Online Epidemiology Textbook
Basic Statistics and Trial Design for Clinicians
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 13 June 2008
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