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RF_RES_3_SUDHA
chapter
4
i
FREQUENCY
In Chapter 1. we outlined the central questions facing clinicians as they
care for patients. In this chapter, we will build a foundation tor the evidence
that clinicians use to gunle their diagnostic and therapeutic decisions. Let
us introduce the subject with a patient.
A 22-year-old man presents with sore throat, lever, and malaise of 2 days
duration. Further history indicates no exposure to sick persons and no prior history
of significant illness. Phvsical examination reveals a temperature of 38°C. an
erythematous pharynx with whitish exudate and tonsillar enlargement, tender
anterior cervical lymph nodes, and no other positive findings.
In planning further diagnosis and treatment, the clinician must deal
with several questions:
1. How likely is the patient to have streptococcal pharyngitis?
2. If the patient has streptococcal infection, how likely is he to develop
a serious complication, such as acute rheumatic fever or acute glo
merulonephritis?
3. How likely is penicillin treatment to prevent rheumatic fever or
glomerulonephritis?
4. If the patient is treated with penicillin, how likely is an important
allergic reaction?
Depending on the answers to these questions, the physician may treat with
penicillin right away, obtain a throat culture and await the result, or ofter
only symptomatic treatment.
Each of these questions concerns the likelihood or commonness of a
clinical event under certain circumstances. The questions could all be
recast so as to ask—I low frequently do streptococcal pharyngitis or rheu
matic fever or penicillin allergic reactions occur under particular circum
stances?
The evidence required to manage this patient rationally—the likelihood
or frequency of disease or outcomes—is. in general, the kind of evidence
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77
needed to answer most clinical questions. Decisions are guided by the
commonness of things. Usually, they depend on the relative commonness
of things under alternative circumstances: in the presence of a positive test
versus a negative test or after treatment A versus treatment B. Because the
commonness of disease, improvement, deterioration, cure, or death forms
the basis for answering most clinical questions, this chapter will examine
measures of clinical frequency.
assigning^numbers to probability statementsJ
Physicians often communicate probabilities as words—“usually.”
“sometimes.” “rarely.” etc.—rather than as numbers. Substituting words
for numbers is convenient and avoids making a precise statement when
one is uncertain about a probability. However, it has been shown that
there is little agreement about the meanings of commonly used words for
frequency.
Example—Physicians were asked to estimate the likelihood of disease for each
of 30 expressions of probability found by reviewing radiology and laboratory
reports. There was great difference of opinion for each expression. Probabilities for
“consistent with" ranged from .18 to .98: for “unlikely,” the range was .01 to .93.
These data support the authors' assertion that “difference of opinion among
physicians regarding the management of a problem may reflect differences in the
meaning ascribed to words used to define probability" (1).
Patients also assign widely varying values for expressions of probability. In
another study, highly skilled and professional workers thought “usually” referred
to probabilities of .35 to 1.0 (± 2 standard deviations from the mean): “rarely”
meant to them a probability ofO to .15 (2).
Thus, substituting words for numbers diminishes the information con
veyed. We advocate using numbers whenever possible.
PREVALENCE AND INCIDENCE"]
In general, clinically relevant measures of the frequency of events arc
fractions in which the numerator is the number of patients experiencing
the outcome (cases) and the denominator is the number of people in whom
the outcome could have occurred. Such fractions are of course proportions,
but by common usage, are often referred to as “rates.” As ex-students of
physics, we recognize the incorrectness of this use of rate, but there seems
to be little chance that it will disappear.
Clinicians encounter two measures of commonness—prevalence and
incidence.
. .
A prevalence is the fraction (proportion) of a group possessing a clinical
condition at a given point in time." Prevalence is measured by surveying a
" There are two kinds of prevalence. Point prevalence is measured at a single point in time for
each person, although not necessarily for all the people in the defined population. Period
prevalence is a count of the proportion of cases that were present at any time during a period
of time.
m
In
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FREQUENCY
CLINICAL EPIDEMIOLOGY—THE ESSENTIALS
1981
1982
1983
o—
o-----o----o---------
0-----------o
oo—
o------o--------o---------
Oo-
Figure 4.1.
oo—
o-----
o Onset
----- Duration
Occurrence of disease in 100 people at risk from 1981-1983.
defined population containing people with and without the condition of
interest, at a single point in time.
An incidence is the fraction or proportion of a group initially f ree of the
condition that develops it over a given period of time. As described later
in this chapter and in greater detail in C hapter 5. incidence is measured
by identifying a susceptible group of people (i.e.. people free of the disease
or the outcome) and examining them periodically over an interval of time
so as to discover and count new cases that develop during the interval.
To illustrate the differences between prevalence and incidence. Figure
4.1 shows the occurrence of disease in a group of 100 people over the
course of 3 years (1981. 1982, 1983). As time passes, individuals in the
group develop the disease. They remain in this state until they either
recover or die. In the 3 years, 16 people suffer the onset of disease and 4
already had it. Eighty do not develop disease and do not appear on the
figure.
At the beginning of 1981 there are four cases, so the prevalence at that
point in time is 4/100. If all 100 individuals, including prior cases, are
examined at the beginning of each year, one can compute the prevalence
at those points in time. At the beginning of 1982. the prevalence is 5/100
because two of the pre-1981 cases lingered on into 1982 and two of the
new cases developing in 1981 terminated (hopefully in a cure) before the
examination at the start of 1982. Prevalences can be computed for each of
the other two annual examinations, and assuming that none of the original
100 people died, moved away, or refused examination, these prevalences
are 7/100 at the beginning of 1983 and 5/100 at the beginning of 1984.
To calculate the incidence of new cases developing in the population,
we consider only the 96 individuals free of the disease at the beginning of
1981 and what happens to them over the next 3 years. Five new cases
79
developed in 1981; six new cases developed in 1982, and five additional
new cases developed in 1983. The 3-year incidence of the disease is all new
cases developing in the 3 years (16) divided by the number of susceptible
individuals at the beginning of the follow-up period (96). or 16/96 in 3
years. What would be the annual incidences for 1981. 1982. and 1983,
respectively? Remembering to remove the previous cases from the denom
inator, the annual incidences would be 5/96 for 1981. 6/91 for 1982, and
5/85 for 1983.
Every measure of disease frequency of necessity contains some indica
tion of time. With measures of prevalence, time is assumed to be instan
taneous. as in a single frame from a motion picture. Prevalence depicts the
situation at that point in time for each patient even though it may, in
reality, have taken several weeks or months to collect observations on the
various people in the group studied. For incidence, time is the essence
because it defines the interval during which susceptible subjects were
monitored for the emergence of the event of interest. Two distinct ap
proaches to the assessment of incidence are encountered in the medical
literature and are described below.
Table 4.1 summarizes the characteristics of incidence and prevalence.
Although the distinctions between the two seem clear, the literature is
replete with misuses of the terms, particularly incidence (3).
Why is it important to know the difference between prevalence and
incidence? Because they are answers to two different questions: (1) What
proportion of a group of people have a condition? and (2) at what rate do
new cases arise in a group of people as time passes? The answer to one
question cannot be obtained directly from the answer to the other.
--------------- ----—---------------p
/ measuring prevalence and INCIDENCE ■
Prevalence Studies
The prevalence of disease is measured by surveying a group of people,
some of whom are diseased at that point in time while others are healthy.
Table 4.1
Characteristics of Incidence and Preualence
Incidence
Prevalance
Numerator
New cases occurring during a
period of time among a group
initially free of disease
All cases counted on a single
survey or examination of a
group
Denominator
All susceptible people present at
the beginning of the period
All people examined, including
cases and noncases
Time
Duration of the period
Single point
How measured
Cohort study (see Chapter 5)
Prevalence (cross-sectional) study
SO. Cl IN1CAL LP1DI MIOI ()(i\
I HI
ESSEN HALS
The fraction or proportion of the group who arc diseased (i.e., cases)
constitutes the prevalence of the disease.
Such one-shot examinations or surveys of a population of individuals
including cases and noncases are calledjJ/xiuz/czzcc.sLudies. Another term
is cross-sectiona/ studies because people are studied at a point (cross
section) in time, fhey are among the more common types of research
designs reported in the medical literature, constituting approximately onethird of original articles in major medical journals.
The following is an example of a typical prevalence study.
Example—What is the prevalence of rheumatoid arthritis in the general popu
lation? To answer this question. O’Sullivan and Cathcart surveyed all 4552 of the
people over age 15 living in a small town in Massachusetts. Each participant
completed a questionnaire and underwent an examination that included a medical
history, physical examination, and blood tests. I he presence of rheumatoid arthritis
was defined by explicit criteria in general use: the New York and the American
Rheumatology Association (ARA) criteria.
Of the 77% of the defined population who participated, the prevalence of
rheumatoid arthritis was about 4 cases per I()()() by the New York criteria and 26
per 1000 by the ARA criteria (4).
I REQI JENCY
81
denominator. An incidence of this type is expressed as the number of new
cases per total number of person-years at risk and is sometimes called an
incidence density.
The person-years approach is also useful for estimating the incidence of
disease in large populations of known size when an accurate count of new
cases and an estimate of the population at risk are available—for example,
a population-based cancer registry.
A disadvantage of the incidence density approach is that it lumps
together different lengths of follow-up. A small number of patients followed
for a long time can contribute as much to the denominator as a large
number of patients followed for a short time. If these long-term follow-up
patients are systematically different from short-term follow-up patients,
the resulting incidence measures may be biased.
INTERPRETING MEASURES OF CLINICAL FREQUENCY
In order to make sense of prevalence and incidence, the first step is a
careful evaluation of the numerator and denominator. Two questions serve
to guide this evaluation: What is a case, and what is the population?
What is a “Case”?—Defining the Numerator
Incidence Studies
In contrast to prevalence, incidence is measured by first identifying a
population free of the event of interest and then following them through
time with periodic examinations to determine occurrences of the event.
This process, also called a cohort study, will be discussed in detail in
Chapter 5.
Up until now, we have defined incidence as the rate of new events in a
group of people of fixed size, all of whom are observed over a period of
lime. This is called ciunidative incidence because new cases arc accumu
lated over time.
Example—The death rate after acute respiratory failure complicating chronic
respiratory disease was studied by observing the survival of 145 patients. After 1
year, 90 patients had died, for a death rate (incidence of death) of 90/145/year.
After 5 years, the death rate was 122/145/5 years (5).
A second approach to incidence is to measure the number of new cases
emerging in an ever-changing population, where people are under study
and susceptible for varying lengths of time. Typical examples are clinical
trials of chronic treatment in which eligible patients are enrolled over
several years so that early enrollees arc treated and followed longer than
late enrollees. In an effort to keep the contribution of individual subjects
commensurate with their follow-up interval, the denominator of the inci
dence measure in these studies is not persons at risk for a specific time
period but person-time at risk of the event. An individual followed for 10
years without becoming a case contributes 10 person-years, whereas an
individual followed for 1 year contributes only one person-year to the
Up to this point, the general term “case" has been used to indicate a
disease or outcome the frequency of which is of interest. Classically,
prevalence and incidence refer to the frequency of a disease among groups
of people. E
ver, clinical decisions often depend on information about
the frequency of disease manifestations, such as symptoms, signs, or
laboratory abnormalities, or the frequency of disease effects, such as death,
disability, symptomatic improvement, etc.
To interpret rates, it is necessary to know the basis upon which a case is
defined, because the criteria used to define a case can strongly affect rates.
Example—One simple way to identify a case is to ask people whether they have
a certain condition. How does this method compare to more rigorous methods? In
the Commission on Chronic Illness study, the prevalences of various conditions,
as determined by personal interviews in the home, were compared to the prevalences
as determined by physician examination of the same individuals. Figure 4.2
illustrates the interview prevalences and the clinical examination prevalences for
various conditions.
The data illustrate that these two methods of defining a case can generate very
different estimates of prevalence and in different directions, depending on the
condition (6).
For some conditions, broadly accepted, explicit diagnostic criteria are
available. The American Rheumatism Association criteria for rheumatoid
arthritis (Table 4.2) are an example (7). These criteria demonstrate the
extraordinary specificity required to define reliably so common a disease
as rheumatoid arthritis. They also illustrate a trade-off between rigorous
82
FREQUENCY
CLINICAL EPIDEMIOLOGY—THE ESSENTIALS
Table 4.2
Rheumatoid Arthritis Diagnostic Criteria (American Rheumatism Association 1958
Revision)"
METHOD OF DEFINING CASE
Clinical Examination
Questionnaire
HERNIA
HEART DISEASE
PEPTIC ULCER
DIABETES
HYPERTENSION
ARTHRITIS
CHRONIC BRONCHITIS
ASTHMA/HAYFEVER
CHRONIC SINUSITIS
10
i
I
iiii
8
6
4
i
i
4
2
2
0
PREVALENCE (%)
83
6
Figure 4.2. Prevalence depends on the definition of a case. The prevalence of
diseases in the general population based on people's opinions (survey) and clinical
evaluation. (Data from Sanders BS: Have morbidity surveys been oversold? Am J
Public Health 52:1648-1659, 1962.
1. Morning stiffness.
2. Pain on motion or tenderness in at least one joint.'b
3. Swelling (soft tissue thickening or fluid, not bony overgrowth alone) in at least one
joint?
4. Swelling of at least one other joint?
5. Symmetrical joint swelling with simultaneous involvement of the same joint on both
sides of the body? Terminal phalangeal joint involvement will not satisfy the criterion.
6. Subcutaneous nodules over bony prominences, on extensor surfaces, or in juxtaarticular regions?
7. Roentgenographic changes typical of rheumatoid arthritis (which must include at least
bony decalcification localized to or greatest around the involved joints and not just
degenerative changes).
8. Positive agglutination (anti-gammaglobulin) test.
9. Poor mucin precipitate from synovial fluid (with shreds and cloudy solution).
10. Characteristic histologic changes in synovial membrane.
11. Characteristic histologic changes in nodules.
CATEGORIES
NUMBER OF
CRITERIA
REQUIRED
MINIMUM DURATION OF
CONTINUOUS
SYMPTOMS
Classic
Definite
Probable
7 of 11
5 of 11
3 of 11
6 weeks (Nos. 1-5)
6 weeks (Nos. 1-5)
6 weeks (1 of Nos. 1-5)
definition and clinical reality. If only “classic” cases were included in a
rate, most patients who would ordinarily be considered to have the disease
would not be included. On the other hand, including “probable” cases
could overestimate the true rate of disease.
a Adapted from Ropes MW, Bennett CA, Cobb S, Jacox R, Jessar RA: 1958 revision of
diagnostic criteria for rheumatoid arthritis. Bull Rheum Dis 9:175-176, 1958.
0 Observed by physician.
What is the Population?—Defining the Denominator
In order to make sense out of the number of cases, we must have a clear
picture of the size and characteristics of the group of individuals in which
the cases arose. A rate is useful only to the extent that the individual
practitioner can decide to which kinds of patients the rate applies.
Customarily, the group indicated in the denominator of a rate is referred
to as the population or, more particularly, the population at risk, where
“at risk” means susceptible to the disease or outcome counted in the
numerator. For example, it is not meaningful to describe the incidence or
prevalence of cervical cancer in a population that includes women who
have had hysterectomies or includes men.
Ideally, the denominator of a rate would include all people who could
have the condition or a representative sample of them. But what is relevant
depends on one’s perspective. For example, if we wanted to know the true
prevalence of rheumatoid arthritis in Americans, we would prefer to
include in the denominator all people in the United States, rather than
patients in office practice. But if one wanted to know the prevalence of
rheumatoid arthritis in office practice—perhaps in order to plan services—
the relevant denominator would be patients seen in office practice, not
people in the population at large. In one survey, only 25% of adults found
to have arthritic and rheumatic complaints (not necessarily rheumatoid
arthritis) during a community survey had received services for such com
plaints from any health professional or institution (8).
It is customary for epidemiologists to think of a population as consisting
of all individuals residing in a geographic area. And so it should be for
studies of cause-and-effect in the general population. But in studies of
clinical questions, the relevant populations generally consist of patients
suffering from certain diseases or exhibiting certain clinical findings, and
who are found in clinical settings that are similar to those in which the
information will be used. Commonly, such patients are assembled at a
limited number of clinical facilities where academic physicians see patients.
In these instances, the population includes all patients with the appropriate
84% CLINICAL LP1DLMIOI ()(h
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FREQUi:N(’Y 85
I SSI N 1 I Al S
findings from the hospitals or clinics involved. I hey may be a small and
peculiar subset of all patients with the findings in some geographic area,
and even unusual for office practice in general.
What difference might the choice of a population make? What is at issue
is the generalizability of observed rales. As discussed in Chapter I. the
incidence of further seizures in children who have had one febrile seizure
varied from about 5C in the general population to as high as 75% in some
clinics. Knowing which incidence is appropriate to one's patients is critical
because it will inlluence the decision whether to begin chronic anticonvul
sant treatment. The appropriate incidence depends upon the location and
nature of the reader's practice. If the reader is an academic pediatric
neurologist, referral center experience is more relevant. If the reader is a
family physician or pediatrician providing community-based primary care,
referral center experience may be irrelevant. Some of the authors reporting
high incidences of subsequent seizures in children seen in referral centers
argued that their high rate indicated that all such children should receive
long-term anticonvulsant treatment. Such a conclusion may not be justified
for the clinician in primary care practice, where the incidence of subsequent
seizures is less than 5%.
^Sampling
It is rarely possible to study all the people who have or might develop
the condition of interest. Usually one takes a sample, so that the number
studied is of manageable size. This raises a question: Is the sample repre
sentative of the population?
In general, there are two ways to sample. In a random sample, every
individual in the population has an equal probability of being selected.
The more general term probability sample is used if every person has a
known (not necessarily equal) probability of being selected. On the average,
the characteristics of people in probability samples are similar to those of
the population from which they were selected, particularly if a large number
are chosen.
Other methods of selecting samples may well be biased and so do not
necessarily represent the parent population. Most groups of patients de
scribed in the medical literature, and found in most clinicians' experience,
are based on biased samples. Typically, patients are included in studies
because they are under care in an academic institution, available, willing
to be studied, and perhaps also particularly interesting and/or severely
affected. There is nothing wrong with this practice—as long as it is
understood to whom the results do (or do not) apply.
RELATIONSHIP AMONG INCIDENCE, PREVALENCE, ANDl
DURATION OF DISEASE
1
As described previously anything that increases the duration of the
clinical findings in a patient will increase the chance that that patient will
be identified in a prevalence study. The relationship among incidence and
Table 4.3
The Relationships Among Incidence, Prevalence and Duration8 of Disease: Asthma in
the United States*
AGE
ANNUAL INCIDENCE
PREVALENCE
0-5
6-16
17-44
45-64
65+
6/1000
3/1000
2/1000
1/1000
0
3/1000
29/1000
32/1000
26/1000
33/1000
36/1000
30/1000
a Duration
PREVALENCE
DURATION =----------------------------ANNUAL INCIDENCE
4.8 years
10.7 years
13.0 years
33.0 years
33.0 years
10.0 years
Prevalence
Annual Incidence
* Approximated from several sources.
prevalence and duration of disease in a steady state—that is. where none
of the variables is changing much over time—is approximated by the
expression:
Prevalence ~ Incidence x Average Duration of the Disease
Example—Tabic 4.3 shows approximate annual incidence and prevalence rates
for asthma. Incidence falls with increasing age. illustrating the fact that the disease
arises primarily in childhood. But prevalence stays fairly stable over the entire age
span, indicating that asthma tends to be chronic and is especially chronic among
older individuals. Also, because the pool of prevalent cases does not increase in
size, about the same number of patients arc recovering from their asthma as new
patients are acquiring it.
If we use the formula (Prevalence + Incidence = Average Duration), we can
determine that asthma has an average duration of 10 years. When the duration of
asthma is determined for each age category by dividing the prevalences by the
incidences, it is apparent that the duration of asthma increases with increasing age.
This reflects the clinical observation that childhood asthma often clears with time,
whereas adult asthma tends to be more chronic.
BIAS IN PREVALENCE STUDIES]
Prevalence studies can be used to investigate potentially causal relation
ships between risk factors and a disease. For this purpose, they are quick
but inferior alternatives to incidence studies. Two biases are particularly
troublesome: temporal sequence and old versus new cases.
Interpreting Temporal Sequences
In prevalence studies, disease and the possible factors responsible for the
disease are measured simultaneously, and so it is often unclear which came
before the other. The time dimension is lost, and if it is included in the
interpretation it must be inferred. In contrast, studies of incidence do have
i
FREQUENCY 87
86 QLINICAL EPIDEMIOLOGY—THE ESSENHALS
u_nter Population
DISEASE OR Ou i COME
• POSSIBLE CAUSES
INCIDENCE STUDY
/ Population^
free-of disease
but exposed/
non-exposed
v to possible .
\ causes /
Measure development
of new cases of
disease over time
INCIDENT
CASES
All New Cases
Arising in a
Defined
Population
TIME
PREVALENT
CASES
Present
at a Point
\ in Time /
PREVALENCE STUDY
Measure past or
present exposure
to possible causes
—i
___ i
Early
Deaths
Population
of existing
cases and
non-cases
Figure 4.4.
Figure 4.3.
Cures
Leave PopulationSevere disease
Mild disease
Prefer other care
Etc.
The difference in cases for incidence and prevalence studies.
Temporal relationship between possible causal factors and disease
for incidence and prevalence studies.
a built-in sequence of events because possible causes of disease are mea
sured initially, before disease has occurred. These relationships are illus
trated in Figure 4.3.
Old Versus New Cases
The difference between cases found in the numerator of incidences and
of prevalences is illustrated in Figure 4.4. In a cohort study most new
cases can be ascertained if a susceptible population is to lowed carefully
through time. On the other hand, prevalence surveys include old as well
as new cases, and they include only those cases that are available at the
time of a single examination—that is. they identity only cases that happen
to be both active (i.e., diagnosable) and alive at the time ot the survey.
Obviously, prevalences will be dominated by those patients who are able
to survive their disease without losing its manifestations.
In many situations, the kinds of cases included in the numerator of an
incidence are quite different from the kinds of cases included in the
numerator of a prevalence. The differences may influence how the rates
arep1retvakrKe^is affected by the average duration of disease. Rapidly fatal
episodes of the disease would be included in an incidence but most would
be missed by a prevalence survey. For example, 25-40 /o of all deaths from
coronary heart disease occur within 24 hours of the onset of symptoms in
individuals with no prior evidence of disease. A prevalence survey would,
therefore, underestimate cases of coronary heart disease. On the other
hand, diseases of long duration are well represented in prevalence surveys,
even if their incidence is low. For example, although the incidence of
Crohn's disease is only about 2-7/100.000/year. its prevalence is over 100/
100.000. reflecting the chronic nature of the disease (9).
Prevalence surveys can also selectively include more severe cases of
disease, ones that are particularly sustained and obtrusive. For example,
patients with rheumatoid arthritis who are not currently active would not
be included in a survey based on current symptoms and physical findings.
Similarly, patients with recurrent but controllable illnesses, such as conges
tive heart failure or depression, may be well at a given point in time and
therefore might not be discovered on a single examination. Unremitting
disease, on the other hand, is less likely to be overlooked and, therefore,
would contribute disproportionately to the pool of cases assembled by a
prevalence survey.
pJSES OF INCIDENCE AND PREVALENCE)
What purposes do incidence and prevalence serve? Clinicians use them
in three different ways: predicting the future, describing things as they are,
and making comparisons.
Predicting the Future
Incidence is a description of the rate at which a disease has arisen over
CLINICAL LPII)LMI()l.O(i>
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Uli I SS1NHALS
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described previously, they become much more powerful tools in support
of clinical decisions when used to make comparisons. It is the comparison
between the frequencies of disease among individuals exposed to a factor
and individuals not exposed to the factor that provides the best evidence
suggesting causality, not just the commonness of the disease among those
exposed. For example, the risk (incidence) of lung cancer among males
who smoke heavily is of the order of 0.17% per year, hardly a common
event. Only when this incidence is contrasted with the incidence in
nonsmokers (approximately 0.007% per year) does the devastating effect
of smoking emerge. Clinicians use measures of frequency as the ingredients
in comparative measures of the association between a factor and the disease
or disease outcome. Ways of comparing rates will be described in more
detail in Chapter 5.
time in a group of people assembled in the past. It can also be used to
predict the probability that similar people will develop the condition in
the future. For incidence, the sequence of events is clear because the
population is known to be free of the outcome at the outset and all cases
are assessed.
On the other hand, as pointed out above, prevalence describes the
situation among a group of individuals at a given point in time; it offers
no sound basis for predicting the future. If 30% of patients with stroke are
depressed, this does not mean that 30% of stroke patients will become
depressed in the future. It may be that depression predisposes to stroke or
that nondepressed stroke patients are more likely to recover quickly.
Because of the way in which they are measured, prevalences often reveal
little about the sequence of events and only include a fraction of all possible
cases. Thus, they are treacherous grounds for predicting the future.
SUMMARY
The Probability that a Patient Has the Condition
This study represents a rational approach to the use of prevalences as
indicators of individual probabilities of disease in guiding clinical decision
making.
Most clinical questions are answered by reference to the commonness
of events under varying circumstances. The commonness of clinical events
is indicated by proportions or fractions, the numerators of which include
the number of cases and the denominators of which include the number
of people from whom the cases arose.
There are two measures of commonness—prevalence and incidence.
Prevalence is the proportion of a group who have the disease at a single
point in time. Incidence is the proportion of a susceptible group who
develop new cases of the disease over an interval of time.
Prevalence is measured by a single survey of a group containing cases
and noncases, whereas measurement of incidence requires examinations
of a previously disease-free group over time. Thus, prevalence studies
identify only those cases who are alive and diagnosable at the time of the
survey, whereas cohort (incidence) studies ascertain all new cases. Prevalent
cases, therefore, may be a biased subset of all cases because they do not
include those who have already succumbed or been cured. Additionally,
prevalence studies frequently do not permit a clear understanding of the
temporal relationship between a causal factor and a disease.
To make sense of incidence and prevalence, the clinician must under
stand the basis upon which the disease is diagnosed and the characteristics
of the population represented in the denominator. The latter is of particular
importance in trying to decide if a given measure of incidence or prevalence
pertains to patients in one’s own practice.
Incidence is the most appropriate measure of commonness with which
to predict the future. Prevalence serves to quantitate the likelihood that a
patient with certain characteristics has the disease at a single point in time
and is used for decisions about diagnosis and screening. The most powerful
use of incidence and prevalence, however, is to compare different clinical
alternatives.
Making Comparisons
POSTSCRIPT
Although isolated incidencesand prevalences serve useful functions, as
Counting clinical events as described in this chapter may seem to be the
Prevalence is particularly useful in guiding decisions about whether or
not to use a diagnostic test, as pointed out in Chapter 3 because prevalence
is a determinant of predictive value. Knowing that a patient with a
combination of demographic and clinical characteristics has a given prob
ability of having the disease not only inlluences the interpretation of a
diagnostic test result but also may affect powerfully the selection among
various treatment options.
The patient with pharyngitis, presented at the beginning of this chapter,
illustrates how variations in prevalence can influence the approach to a
clinical problem.
Example—Three approaches to the treatment of pharyngitis were compared.
Their value was judged by weighing the potential benefits of preventing rheumatic
fever against the costs of penicillin allergy. T he three options were to obtain a
throat culture and treat only those patients with throat cultures positive for fihemolytic Group A streptococci, treat all patients without obtaining a culture, and
neither culture nor treat any patient.
The analysis revealed that the optimal strategy depended upon the likelihood
that a patient would have a positive culture, which can be estimated from the
prevalence of streptococcal infection in the community at the time and the presence
or absence of such clinical findings as fever. It was concluded that, if the probability
of a positive culture for an individual patient exceeds 20%. the patient should be
treated: if it is less than 5%. the patient should not be cultured or treated: and if
the probability lies between 5% and 20%, the patient should be cultured first and
treated based on the result (10).
■
:•
.90 CLINICAL EPIDEMIOLOGY—THE ESSENTIALS
most mundane of tasks. It seems so obvious that examining counts of
clinical events under various circumstances is the foundation of clinical
science. It may be worth reminding the reader that Pierre Louis introduced
the “numerical method” of evaluating therapy less than 200 years ago. Dr.
Louis had the audacity to count deaths and recoveries from febrile illness
in the presence and absence ol blood-letting. He was excoriated for allowing
lifeless numbers to cast doubt on the healing powers of the leech, powers
that had been amply confirmed by decades of astute qualitative clinical
observation.
REFERENCES
s
chapter w
RISK
' ?n?a4niiGK)8n0rman GR: ExPressionsofProbabilit^ wordsand numbers. N Engl J Med
J V—. H I 1. 1 7 O v.
2. Toogood JH: What do we mean by “usually”? l.ancel 1:1094, 1980.
1
usa8e and abusa^- "prera'ence" and ■■incidence." Ann Intern
Med 84:502-503. 1976.
4. O Sullivan JB Cathcart ES: The prevalence of rheumatoid arthritis. Follow-up evaluation
^97^ e"ect °'cr*ter’u on rales *n Sudbury, Massachusetts. Atm Intern Med 76:573-577,
5. Asmundsson T. Kilburn KH: Survival after acute respiratory failure. Ann Intern Med
80:54-57, 1974.
6. Sanders BS: Have morbidity surveys been oversold? J/h J Puhi Health 52:1648-1659
1962.
7. Ropes MW. Bennett GA, Cobb S. Jacox R. Jessar RA: 1958 revision of diagnostic criteria
tor rheumatoid arthritis. JJ Bunim (Ed). Hull Rheum Dis ^AlS-Xlb. 1958.
8. Spitzer WO, Harth M, Goldsmith CH, Norman GR. Dickie GL. Bass MJ, Newell JP:
Ipoa™ n A<;COmp,aint in primary care: Prevalence’ related disability, and costs. J Rheum
3:88—99, 1976.
9. Sedlack RE, Whisnant J. Elveback LR. Kurland LT: Incidence of Crohn's disease in
Olmsted County, Minnesota. 1935-1975. Am J Epidemiol 112:759-763, 1980.
10. Tompkins RK, Burnes DC, Cable WE: An analysis of the cost-eflectiveness of pharyngitis
management and acute rheumatic fever prevention. Ann Intern Med 86:481-492, 1977.
Risk generally refers to the probability of some untoward event. In this
chapter, the term “risk” is used in a more restricted sense to describe the
likelihood that people who are without a disease, but are exposed to certain
factors (“risk factors”), will acquire the disease.
Many people in our society have a strong interest in their risk of disease.
Their concern has spawned many popular books about risk reduction and
is reflected in newspaper headlines about the risk of cancer from exposure
to toxic chemicals or nuclear accidents, of cardiovascular disease after use
of birth control pills and of AIDS from sexual behavior or transfusion.
In this chapter, we will consider how estimates of risk are obtained by
observing the relationship between exposure to possible risk factors and
the subsequent incidence of disease. Then we will describe several ways of
comparing risks, both as they affect individuals and populations.
SUGGESTED READINGS
Ellenberg JH. Nelson KB: Sample selection and the natural history of disease: Studies of
lebnie seizures. J.JA/.-l 243:1337-1340. 1980.
Fr£d™a->n
.^dical USage and abllsagc' “prevalence" and "incidence.” Ann Intern Med
0*4:502—503, 19/6.
Morgenstern H, Kleinbaum DG, Kupper LL: Measures of disease incidence used in epide
miologic research. Int J Epidemiol 9:97-104, 1980.
APPENDIX 4.1. MAIN QUESTIONS FOR DETERMINING THE
VALIDITY OF STUDIES OF PREVALENCE3
1. What are the criteria for being a case?
2. What is the defined population?
3. Are cases and-----------noncases—
from
,..i an unbiased sample of the population ?
a These questions are not meant to be all-inclusive nor to replace independent, critical
thinking. They are a rough guideline, including only the most basic elements of a
sound study.
RISK FACTORS
Factors that are associated with an increased risk of becoming diseased
are called risk factors. There are several kinds of risk factors. Some, such
as toxins, infectious agents, and drugs, are found in the physical environ
ment. Others are part of the social environment. For example, disruption
of family (e.g., loss of a spouse), daily routines, and culture has been shown
to increase rates of disease—not only emotional but physical illness as
well. Other risk factors are behavioral: among them are smoking, inactivity,
and driving without seat belts. Risk factors are also inherited. For example^
having the haplotype HLA B27 greatly increases the risk of acquiring the
spondylarthropathies.
Exposure to a risk factor means that a person has, before becoming ill,
come in contact with or has manifested the factor in question. Exposure
can take place at a single point in time, as when a community is exposed
to radiation during a nuclear accident. More often, however, exposure to
risk factors for chronic disease takes place over a period of time. Cigarette
91
92* CLINICAL. EPIDEMIOLOCh
Uli ESSENHALS
smoking, hypertension, sexual promiscuity, and sun exposure are exam
ples. There are many different ways of characterizing the dose of chronic
exposure: ever exposed, current dose, largest dose taken, total cumulative
dose, years of exposure, years since first exposure, etc. (I). Although the
various measures of dose tend to be related to each other, some may show
an exposure-disease relationship, whereas others do not. For example,
cumulative dose of sun exposure is a risk factor for nonmelanoma skin
cancer, whereas episodes of severe sunburn is a better predictor of mela
noma. Choice of an appropriate measure of exposure is usually based on
all that is known about the biologic effects of the exposure and the
pathophysiology of the disease.
INFORMATION ABOUT RISK .
l arge and dramatic risks are easy for anyone to appreciate. Thus, it is
not difficult to recognize the relationship between exposure and disease for
such conditions as chickenpox, sunburn, or aspirin overdose because they
follow exposure in a relatively rapid, certain, and obvious way. But much
of the morbidity and mortality in our society is caused by chronic diseases.
For these, the relationships between exposure and disease are far less
obvious. It becomes virtually impossible lor individual clinicians, however
astute, to develop estimates of risk based on their own experiences with
patients. This is true for several reasons, which are discussed below and
summarized in Table 5.1.
• Long latency
Many chronic diseases have long latency periods between exposure to
risk factors and the first manifestations of disease. Patients exposed during
one time in a clinician’s professional life may experience the consequences
in another, years later, when the original exposure is all but forgotten. The
link between exposure and disease is thereby obscured.
• Frequent exposure to risk factors
Many risk factors—such as cigarette smoking or driving when intoxi
cated—occur so frequently in our society that they scarcely seem danger
ous. Only by comparing patterns of disease in other populations, or
Table 5.1
Situations in which Personal Experience is Insufficient to Establish a Relationship
Between Exposure and Disease
Long latency period between exposure and disease
Frequent exposure to risk factor
Low incidence of disease
Small risk from exposure
Common disease
Multiple causes of disease
RISK 93
investigating special subgroups within our own (e.g.. Mormons who neither
smoke nor drink), can we recognize risks that are in fact rather large.
• Low incidence of disease
Most diseases, even ones thought to be “common.” are actually quite
rare. Thus, although lung cancer is the most common kind of cancer in
Americans, the yearly incidence of lung cancer even in heavy smokers is
less than 2/1,000. In the average physician's practice, years may pass
between new cases of lung cancer. It is difficult to draw conclusions about
such infrequent events.
• Small risk
If a factor confers only a small risk, a large number of “cases” are
required to observe a difference in disease rates between exposed and
unexposed people. This is so even if both the risk factor and the disease
occur relatively frequently. It is still uncertain whether coffee and diabetes
are risk factors for carcinoma of the pancreas, because estimates of risk are
all small and. therefore, easily discounted as resulting from bias or chance.
In contrast, it is not controversial that hepatitis B infection is a risk factor
for hepatoma, because people with evidence of hepatitis B infection are
hundreds of times more likely to get liver cancer than those without it.
• Common disease
If the disease is one of those ordinarily occurring in our society—heart
disease, cancer, or stroke—and some of the risk factors for it are already
known, it becomes difficult to distinguish a new risk factor from the others.
Also, there is less incentive to look for a new risk factor. For example, the
syndrome of sudden, unexpected death in adults is a common way to die.
Many cases seem related to coronary heart disease. However, it is entirely
conceivable that there are other important causes, as yet unrecognized
because an adequate explanation for most cases is available.
On the other hand, rare diseases invite efforts to find a cause. Phocomelia
is such an unusual congenital malformation that the appearance of just a
few cases raised suspicion that some new agent (as it turned out. the drug,
thalidomide) might be responsible. Similarly, physicians were quick to
notice when several cases of carcinoma of the vagina, a very rare condition,
began appearing. A careful search for an explanation was undertaken, and
maternal exposure to diethylstilbestrol was found.
• Multiple causes and effects
There is usually not a close, one-to-one, relationship between a risk
factor and one particular disease. Some people with hypertension develop
congestive heart failure and many do not. Many people who do not have
hypertension develop congestive heart failure as well. The relationship
between hypertension and congestive heart failure is obscured by the fact
that there are several other causes of the disease, and hypertension causes
several diseases. Thus, although people with hypertension are about three
times more likely to develop congestive heart failure and hypertension is
RISK 95
94 .CLINICAL EPIDEMIOLOGY—THE ESSENTIALS
* the leading cause of that condition, physicians were not particularly attuned
to this relationship until recently, when adequate data became available.
For these reasons, individual clinicians are rarely in a position to confirm
associations between exposure and disease, though they may suspect them.
For accurate information, they must turn to the medical literature, partic
ularly studies that are carefully constructed and involve a large number of
patients.
USES OF RISK
Information about risk serves several purposes.
Prediction
Risk factors are used, first and foremost, to predict the occurrence of
disease. The quality of predictions depends on the similarity of the people
on whom the estimate is based to the people for whom the prediction is
made.
Although risk factors may signify an individual's increased risk of
disease, relative to an unexposed person, their presence does not mean
that an individual is very likely to get the disease. Most people, even those
with many strong risk factors, are unlikely to get a disease—at least over
several years’ time. Thus, a heavy cigarette smoker, who has a twenty-fold
increase in the risk of lung cancer compared to nonsmokers, nevertheless
has only a one in a hundred chance of getting lung cancer in the next 10
years.
In individual patients, risk factors usually are not as strong predictors of
disease as are clinical findings of early disease. As Rose put it:
Often the best predictor of future major diseases is the presence of existing minor
disease. A low ventilatory function today is the best predictor of its future rate of
decline. A high blood pressure today is the best predictor of its future rate of rise.
Early coronary heart disease is better than all of the conventional risk factors as a
predictor of future fatal disease (2).
Cause
It is often assumed that any excess incidence of disease in exposed versus
nonexposed persons is because of exposure to a risk factor. However, risk
factors need not be causes. A risk factor may mark a disease outcome
indirectly, by virtue of an association with some other determinant(s) of
disease—that is, it may be confounded with a causal factor. For example,
lack of maternal education is a risk factor for low birth weight infants. Yet,
other factors related to education, such as poor nutrition, less prenatal
care, cigarette smoking, etc., are more directly the causes of low birth
weight.
A risk factor that is not a cause of disease is called a marker, because it
“marks” the increased probability of disease. Not being a cause does not
diminish the value of a rib.v factor as a way of predicting the probability of
disease. But it does imply that removing such a risk factor might not
remove the excess risk associated with it.
Diagnosis
The presence of a risk factor increases the probability that a disease is
present. Knowledge of risk, therefore, can be used in the diagnostic process,
inasmuch as increasing the prevalence of disease among patients tested is
one way of improving the performance (positive predictive value) of a
diagnostic test.
However, the presence of a risk factor usually increases the probability
of disease very little for any one individual at one point in time, compared
to other aspects of the clinical situation. For example, age and sex are
relatively strong risk factors for coronary artery disease, yet the prevalence
of disease in the most at-risk age and sex group, old men, is only 12.3%
compared to 0.4% for the least at-risk group, young women. When specifics
of the clinical situation, such as type of chest pain and results of an
electrocardiographic stress test, are considered as well, the prevalence of
coronary disease can be raired to 99.8% for old men and 93.1 % for young
women (3).
More often, it is helpful to use the absence of a risk factor to help rule
out disease, particularly when one factor is strong and predominant. Thus,
it would be reasonable to consider mesothelioma in the differential diag
nosis of a pleural mass if the patient were an asbestos worker; but meso
thelioma would be considerably less likely if the patient had never worked
with asbestos. Knowledge of risk factors is also used to improve the
efficiency of screening programs by selecting subgroups of patients at
increased risk.
Prevention
If a risk factor is also a cause of disease, its removal can be used to
prevent disease whether or not the mechanism by which the disease takes
place is known. Some of the classic events in the history' of epidemiology
are illustrations. For example, before bacteria were identified Snow found
an increased rate of cholera among people drinking water supplied by a
particular company and controlled an epidemic by cutting off that supply.
The concept of cause and its relationship to prevention will be discussed
in Chapter 11.
PROBABILITY AND THE INDIVIDUAL
The best available information for predicting disease in an individual is
past experience with a large number of similar people. For example, an
observed incidence of 2/1000/year for the occurrence of lung cancer in
heavy smokers becomes an estimate of the probability. 0.002. that an
individual heavy smoker will get lung cancer in a year. In practical terms.
9(> C LINICAL I P1D1 Mi()L()(i\
RISK
Illi I SSI N I I M S
incidence is used lo estimate the probability that an individual will expe
rience the event of interest. If our knowledge of human disease were more
complete, we would not need to resort to probability. But we do not have
that luxury.
However, there is a basic incompatibility between the incidence of a
disease in groups of people and chances that an individual will contract
that disease. Quite naturally, both patients and clinicians would like to
answer questions about the future occurrence of disease as precisely as
possible. They arc uncomfortable about assigning a probability, such as
the chances that a person will gel lung cancer or stroke in the next 5 years.
Moreover, any one person will, al the end ol 5 years, either have the disease
or not. So in a sense, the average is always wrong for the individual,
because it is expressed in different terms.
Nevertheless, probabilities can guide clinical decision making. Even il a
prediction does not come true in an individual patient, il will usually be
borne out in many such cases. After all. weather forecasts are not always
accurate either, but they do help us decide whether lo carry an umbrella.
---------------- ------- - —v
STUDIES OF RISK
There are several scientific strategies for determining risk. In general,
there is a trade-ofTbetween scientific rigor and feasibility.
Observational Studies
The most satisfactory way of determining whether exposure to a poten
tial risk factor results in an increased risk ol disease would be to conduct
an experiment. People currently without disease would be divided into
groups of equal susceptibility lo the disease in question. One group would
be exposed to the purported risk factor and the other would not. but the
groups would otherwise be treated the same. Later, any difference in
observed rates of disease in the groups could be attributed to the risk factor.
Unfortunately, the effects of most risk factors cannot be studied in this
way. Consider some of the questions ol risk that concern us today. Arc
inactive people at increased risk for cardiovascular disease, everything else
being equal? Does heterosexual exposure lead lo AIDS? Do seat belts
decrease the risk of dying from an auto accident? For such questions as
these, it is usually not possible lo conduct an experiment. People become
exposed or not to risk factors for reasons that have nothing to do with the
scientific value of the information their exposure may provide. As a result,
il is usually necessary to study risk in less obtrusive ways.
Clinical studies in which the researcher gathers data by simply observing
events as they happen, without playing an active part in what takes place,
are called observational studies. On the other hand, in experimental studies.
the researcher determines w ho is exposed. Although experimental studies
are more scientifically rigorous, observational studies are the only feasible
way of studying most questions of risk.
97
Observational studies are subject lo a great many more potential biases
than are experiments. When people become exposed or not exposed to a
certain risk factor in the natural course of events, they are also likely to
difter in a great many other ways. If these ways are also related lo disease
they could account for any association observed between risk factors and
disease.
This leads to the main challenge of observational studies: to deal with
extraneous ditTerences between exposure groups in order to mimic as
closely as possible an experiment. The differences are considered “extra
neous" from the point of view of someone trying to determine cause-effect
relationships. The following example illustrates one approach to handling
such differences.
Example—Although the presence of sickle-cell trait (HbAS) is generally regarded
as a benign condition, several studies have suggested that it is associated with
defects in physical growth and cognitive development. A study was undertaken,
therefore, to see if children born with HbAS experienced problems in growth and
development more frequently than children with normal hemoglobin (HbAA).
everything else being equal. It was recognized that a great many other factors are
related both to growth and development and also to having HbAS. Among these
are race. sex. birth dale, birth weight, gestational age. 5-minute Apgar score, and
socioeconomic status. If these were not taken into account, it would not be possible
to distinguish the effects of HbAS. in and of itself, from the effects of the other
factors. The authors chose to deal with these other factors by matching. For each
child with HbAS. they selected a child with HbAA who was similar with respect to
the seven other factors. Fifty newborns with HbAS and 50 with HbAA were
followed from birth to 3-5 years old. No differences in growth and development
were found (4).
Other ways of dealing with differences between groups will be described
in the next chapter (Chapter 6).
Cohorts
The term cohort is used to describe a group of people who have
something in common when they are first assembled, and who are then
observed for a period of time to see what happens to them. Table 5.2 lists
some of the ways in which cohorts are used in clinical research.
Whatever members of a cohort have in common, observations of them
should fulfill two criteria if they are to provide sound information.
First, cohorts should be observed over a meaningful period of time in
the natural history of the disease in question. This is so there will be
sufficient time for the risk to be expressed. If we wish lo learn whether
neck irradiation during childhood results in thyroid neoplasms, a 5-year
follow-up would not be a fair test of the risk associated with irradiation,
because the usual time period between exposure and the onset of this
disease is considerably longer.
Second, all members of the cohort should be observed over the full
98 CLINICAL EPIDEMIOLOGY—THE ESSENTIALS
Table 5.2
Cohorts and their Purposes
RISK 99
AT RISK
CHARACTERISTIC IN
COMMON
TO ASSESS
Age
Age
EFFECT OF
Date of birth
Calendar time
Exposure
Risk factor
Disease
Prognosis
Preventive interven
tion
Prevention
Therapeutic inter
vention
Treatment
EXAMPLE
Life expectancy for people
age 70 (regardless of
when born)
Tuberculosis rates for peo
ple born in 1910
Lung cancer in people who
smoke
Survival rate for patients
with breast cancer
Reduction in incidence of
pneumonia after pneu
mococcal vaccination
Improvement in survival for
patients with Hodgkin's
disease given combina
tion chemotherapy
period of follow-up. To the extent that people drop out of the cohort and
their reasons for dropping out are related in some way to the outcome, the
information provided by an incomplete cohort can be a distortion of the
true state of affairs.
Cohort Studies
In a cohort study, a group of people (a cohort) is assembled, none of
whom has experienced the outcome of interest. On entry to the study,
people in the cohort are classified according to those characteristics that
might be related to outcome. These people are then observed over time to
see which of them experience the outcome. It is then possible to see how
initial characteristics relate to subsequent outcome events. A cohort study
is diagrammed in Figure 5.1. Other names for such studies are longitudinal
(emphasizing that patients are followed over time), prospective (implying
the forward direction in which the patients are pursued), and incidence
(calling attention to the basic measure of new' disease events over time).
The following is a description of a classical cohort study, which has
made an extremely important contribution to our understanding of car
diovascular disease.
Example—The Framingham Study was begun in 1949 to identify factors asso
ciated with an increased risk of coronary heart disease (CHD). A representative
sample of 5209 men and women, aged 30-59, was selected from approximately
10,000 persons of that age living in Framingham, a small town near Boston. Of
these. 5127 were free of CHD when first examined and. therefore, were at risk of
EXPOSURE TO
RISK FACTOR
DISEASE
EXPOSED
YES
NO
PEOPLE
AT
RISK
------ TIME
NOT EXPOSED
/ YES
NO
Figure 5.1.
Design of a cohort study of risk.
developing CHD subsequently. There people have been re-examined biennially for
evidence of coronary disease. The study has run for 30 years and has demonstrated
that risk of developing CHD is associated with blood pressure, serum cholesterol,
cigarette smoking, glucose intolerance, and left ventricular hypertrophy. There is a
large difference in risk between those with none and those with all of these risk
factors (5).
Historical Cohort Studies
Cohort studies can be conducted in two ways (Fig. 5.2). The cohort can
be assembled in the present and followed into the future (a concurrent
cohort study): or it can be identified from past records and followed forward
from that time up to the present (a historical cohort study).
Most of the advantages and disadvantages of cohort studies, as a strategy,
apply whether they are concurrent or historical. However, the potential for
difficulties with the quality of data is different for the two. In concurrent
studies, data can be collected specifically for the purposes of the study and
with full anticipation of what is needed. It is thereby possible to avoid
biases that might undermine th: accuracy of the data. On the other hand,
data for historical cohorts are often gathered for other purposes—usually
as part of medical records for patient care. These data may not be of
sufficient quality for rigorous research.
Disadvantages of Cohort Studies
Cohort studies of risk are the best available substitute for a true experi
ment, when experimentation is not possible. However, they present a
considerable number of practical difficulties of their own. Some of the
advantages and disadvantages of cohort studies, for the purpose of describ
ing risk factors, are summarized in Table 5.3.
The principal disadvantage is that, if the outcome is infrequent, and
most are, a large number of people must be entered in a study and remain
under observation for a long time before results are available. For example.
100
CLINICAL I PIDI-MIOLOG^
PAST
I ill LSSLN 11 Al S
PRESENT
FUTURE
101
questions. This has led to efforts to find more efficient, yet dependable
ways of assessing risk. One of these ways, case control studies, will be
discussed in Chapter 10.
COMPARING RISKS
Historical
Cohort
Cases
---------- ►Follow-Up
Assembled
Concurrent
Cohort
Cases
----------- ► Follow-Up
Assembled
Figure 5.2.
RISK
Historical and concurrent cohort studies.
The basic expression of risk is incidence, defined in Chapter 4 as the
number of new cases of disease arising in a defined population during a
given period of time. But usually we want to compare the incidence of
disease in two or more cohorts, which have different exposures to some
possible risk factor. To compare risks, several measures of the association
between exposure and disease, called measures of effect, arc commonly
used. 1 hey represent different concepts of risk and arc used for different
purposes. Four measures of effect are discussed below, summarized in
Table 5.4, and illustrated by an example in Table 5.5.
Attributable Risk
Table 5.3
Advantages and Disadvantages of Cohort Studies
ADVANTAGES
DISADVANTAGES
The only way of establishing incidence (i.e .
absolute risk) directly
Follow the same logic as the clinical
question: if persons exposed, then do
they get the disease?
Exposure can be elicited without the bias
that might occur if outcome were already
known
Can assess the relationship between
exposure and many diseases
Inefficient, because many more subjects
must be enrolled than experience the
event of interest; therefore, cannot be
used for rare diseases
Expensive because of resources necessary
to study many people over time
Results not available for a long time
Can only assess the relationship between
disease and of exposure to relatively few
factors (i.e., those recorded at the outset
of the study)
First, one might ask. “What is the additional risk (incidence) of disease
following exposure, over and above that experienced by people who are
not exposed?” The answer is expressed as attributable risk, the incidence
of disease in exposed persons minus the incidence in nonexposed persons.
Attributable risk is the additional incidence of disease related to exposure,
taking into account the background incidence of disease, presumably from
other causes. Note that this way of comparing rates implies that the risk
factor is a cause and not just a marker. Because of the way it is calculated,
attributable risk is also called risk difference.
Table 5.4
Measures of Effect
EXPRESSION
the Framingham Study of coronary heart disease was the largest of its kind
and studied one of the most frequent of the chronic diseases in America.
Nevertheless, over 5000 people had to be followed for several years before
the first, preliminary conclusions could be published. Only 5% of the
people had experienced a coronary event during the first 8 years!
A related problem with cohort studies results from the fact that the
people being studied are usually “free living” and not under the control of
researchers. A great deal of effort and money must be expended to keep
track of them. Cohort studies, therefore, are expensive, sometimes costing
millions of dollars.
Because of the time and money required for cohort studies, this approach
cannot be used for all clinical questions about risk. For practical reasons,
the cohort approach has been reserved for only the most important
Attributable risk (risk
difference)
Relative risk (risk ratio)
Population attributable risk
Population attributable
fraction
QUESTION
What is the incidence of disease
attributable to exposure?
How many times more likely are
exposed persons to become
diseased, relative to nonexposed?
What is the incidence of disease in a
population, associated with the
occurrence of a risk factor?
What fraction of disease in a
population is attributable to
exposure to a risk factor?
a Where:
If = incidence in exposed persons
Ie = incidence in nonexposed persons
P = prevalence of exposure to a risk factor
It = total incidence of disease in a population
DEFINITION®
AR
Ie ~ Ie
rr = -
Ie
ARP = AR x P
AFP
ARp
It
102
4
CLINICAL 1 PIDLMlOLOG'i
Illi I SSI N HALS
RISK
Table 5.5
Calculating Measures of Effect: Cigarette Smoking and Death from Lung Cancer3
150 - A
O
Simple Risks
Death rate from lung cancer in cigarette smokers
Death rate from lung cancer in nonsmokers
Prevalence of cigarette smoking
Total death rate from lung cancer
0.96/1000/year
0.07/1 OOO/year
56%
0.56/1 OOO/year
Compared Risks
Attributable risk = 0.96/1 OOO/year - 0.07/1 OOO/year
= 0.89/1 OOO/year
Relative risk
100
I O
< tr
Ld Ld
Q CL
O
15
°<
10
—I
Prevalence of
Elevated BP at
Various Levels
5
O
0.50/1 OOO/year
Population attributable fraction
50
0
Ll
Population attributable risk = 0.89/1 OOO/year x 0.56
= 0.50/1 OOO/year
Excess Death Rate
Attributable to
BP > 90 mmHg
^Tld
0.96/1 OOO/year
“0.07/1 OOO/year
= 13.7
a_
“ 0.56/1 OOO/year
I-
0
= 0.89
a Estimated data from Doll R. Hill AB: Br Med J 1 1399-1410. 1964.
Relative Risk
On the other hand, one might ask. “How many times more likely are
exposed persons to get the disease relative to nonexposed persons? To
answer this question, we speak of relative risk or risk ratio, the ratio of
incidence in exposed persons to incidence in nonexposed persons. Relative
risk tells us nothing about the magnitude of absolute risk (incidence). Even
for large relative risks, the absolute risk might be quite small if the disease
is uncommon. Il does tell us the strength of the association between
exposure and disease and so is a useful measure of effect for studies of
disease etiology.
Interpreting Estimates of Individual Risk
The clinical meaning attached to relative and attributable risk is often
quite different, because the two expressions of risk stand for entirely
different concepts. The appropriate expression of risk depends upon the
question being asked.
Example—The Royal College of General Practitioners has been conducting a
study of the health effects of oral contraceptives. During 1968 and 1969, over
23,000 women taking oral contraceptives and an equal number of women who had
never taken the pill were entered into the study by 1400 physicians. These physicians
subsequently reported oral contraceptive use, morbidity, and mortality twice a
year. The use of oral contraceptives was updated regularly. After 10 years of follow-
103
58 4
C
co
cn co
Id I
O H
X <
LxJ Ld
60 r
40
24 i
20
oH
50
i
60
70
80
90
100
% Excess Deaths
Attributable to
Various Levels
of Hypertension
I
175
“I
no
120
i
130
DIASTOLIC BLOOD PRESSURE (mmHg)
Figure 5.3. Relationships among attributable risk, prevalence of risk factor, and
population risk for hypertension. (Adapted from The Hypertension Detection and
Follow-up Cooperative Group. Ann NY Acad Sci. 304:254-266, 1978.)
up. it was reported that oral contraceptive users had a risk of dying from circulatory'
diseases that was 4.2 times greater than for nonusers. But the risk of dying was
increased by only 22.7/100.000 women-years. An individual woman, weighing the
risks of oral contraceptives, must deal with the two concepts of risk very differently.
On the one hand, a four-fold greater risk of dying might loom large. On the other,
two chances in 10.000 is a very remote possibility (6).
In general, because attributable risk represents the actual, additional prob
ability of disease in those exposed, it is a more meaningful expression of
risk in most clinical situations.
Population Risk
Another way of looking at risk is to ask, “How much does a risk factor
contribute to the overall rates of disease in groups of people, rather than
RISK
104 CL1NICA1 1 PIDl MIDI (KiV
105
till FSSI-.N 11 M.S
disease, its presence allows one to predict the probability that disease will
individuals?” This information is useful for deciding which risk factors are
particularly important and winch are trivial to the overall health of a
community, and so it can inform those in policy positions how to choose
priorities for the deployment of health care resources.
To estimate population risk, it is necessary to lake into account ie
frequenev with which members of a community are exposed to a iisK
factor. A relatively weak risk factor (in terms ol relative risk) that is quite
prevalent could account for more of the overall incidence of disease in a
community than a stronger risk factor that is rarely pi esent.
Population alinbuiahlc risk is a measure of the excess incidence of
disease in a community that is associated with the occurrence of a risk
factor. It is the product of the attributable risk and the prevalence of the
risk factor in a population.
One can also describe the traction ol disease occurrence in a population
that is associated with a particular risk factor, the populalion aliribulable
fraclion. It is obtained by dividing the population attributable risk by the
total incidence of disease in the population.
Figure 5.3 illustrates how the prevalence ol a risk factor determines the
relationship between individual and population risk. .1 shows the attrib
utable risk of death according to diastolic blood pressure. Risk increases
with increasing blood pressure. However, lew people have extremely, ugi
blood pressure (/?). When hypertension is taken to be a diastolic blood
pressure > 90 mm Hg. most hypertensive people are just oyer ) ) and very
few are in the highest category. 115 mm Hg. As a result (C ). the greatest
percentage of excess deaths in the population (>K.4 < ). is attributable to
relatively low-grade hypertension. 90-105 mm Hg. Paradoxically, then,
physicians could save more lives by efTective treatment ol mild hyperten
sion than severe hypertension.
.
frequently encountered in the
Measures of populalion risk arc less frequently
clinical literature than arc measures of individual risk. e.g.. attributable
and relative risk. But a particular practice is as much a population for its
health care providers as is a community for health policy makers. Also,
the concept of how the prevalence of exposure afTects risk in groups can
be important in the care of individual patients. For instance, when patients
cannot give a history or when exposure is difficult for them to recognize,
we depend on the usual prevalence of exposure to estimate the likelihood
of various diseases. When considering treatable causes ol cirrhosis in a
North American patient, for example, it would be more profitable to
consider alcohol than schistosomes, inasmuch as few North Americans are
exposed to Schistosoma mansoni. Of course, one might take a very dinerent
stance in the Nile Delta, where people rarely drink alcohol and schisto
somes are prevalent.
SUMMARY
Risk factors are characteristics that are associated with an increased risk
of becoming diseased. Whether or not a particular risk factor is a cause or
°L Most suspected risk factors cannot be manipulated for the purposes of
an experiment, so it is usually necessary to study risk by simply observing
people’s experience with risk factors and disease. One way ol doing so is
to select a cohort of people who are and are not exposed to a risk factor
and observe their subsequent incidence of disease.
When disease rates are compared, the results can be expressed in several
wavs. Attributable risk is the excess incidence of disease related to exposure.
Relative risk is the number of times more likely exposed people are to
become diseased, relative to nonexposed. The impact of a risk factor on
groups of people takes into account not only the risk related to exposure
but the prevalence of exposure as well.
Although it is scientifically preferable to study risk by means of cohort
studies, this approach is not always feasible because of the time, effort, and
expense they entail.
REFERENCES
1 Weiss NS LifT JM: Accounting for the multicausal nature of disease in the design and
’ analvsis of epidemiologic studies., tm J Epidemiol
2. Rose G: Sick individuals and sick populations. Int J Epidemiol 14.3.-38. 1985.
T. Diamond GA. Forrester JS: Analysis of probability as an aid in the clinical diagnosis of
coronary-artery disease. N En^l J Med 300:1350-1358. 1979.
4 Kramer'MS Rooks Y. Pearson HA: Growth and development in children with sickle
cell trait. N Enid J Med 299:686-689. 1978.
5. Dawber TR: The Framingham Study. The Epidemiology of Atherosclerotic Disease.
Cambridge. Harvard University Press. 1980.
.
6. Royal College of General Practitioners' Oral Contraception Study: Further analysis of
mortality in oral contraceptive users. Lancet 1:541-546. 1981.
SUGGESTED READINGS
Dawber TR: The Framingham Study. The Epidemiology of Atherosclerotic Titease. Cambridge Harvard University Press. 1980.
.
Morganstern H. Kleinbaum DG. Kupper LL: Measures of disease incidence used in epide
miologic research. Int J Epidemiol 9:97-104. 1980.
Relative or attributable risk? Editorial. Lancet 2:1211-121_. 1981.
Rose G: Sick individuals and sick populations. Int J Epidemiol 14:32-38. 1985.
5.
I
Source:
Cohort Studies
10
Ch. 10: Observational studies:
------ I.
----Cohort
------------- studies.
------------- Ch.11: Observational studies: II. Case-control studies.
New York: Oxford University Press.
OBSERVATIONAL STUDIES:
I. COHORT STUDIES
Table 10-1. The Distinction between Cohort and Case-Control Studies
CASE-CONTROL STUDY
In the experimental method, an investigator studies the effect of a change in the
genetic composition or environment of a cell, an organ, or an organism and makes
a comparison with a similar cell, organ, or organism that has not been subjected
to that change. This ideal is the basis of both experimental and observational
epidemiologic studies. In an experimental epidemiologic study, the investigator
assigns the treatment; however, in the observational study, the investigator can
only observe the outcomes associated with the individual exposures experienced
by participants in the study. The investigator does not control the assignment of
that exposure experience.
The data collected in an observational study can be tabulated in the form of
a fourfold table, as shown in Table 10-1. If two similar groups can be identified
that differ only by being exposed to a given environmental factor, e.g., oral con
traceptives, or by possessing a particular characteristic, e.g., a specific blood
group, the epidemiologist can follow these two groups and observe the incidence
of disease in each. This type of investigation is known as a “cohort” study and
is the subject of this chapter. In many situations, however, it is impractical for
the epidemiologist to identify groups of individuals based upon their exposure
histories or characteristics. One can more readily identify those individuals who
have (“cases”) or do not have (“controls”) the disease of interest; the individ
uals’ histories of past exposure to the factor or characteristic of interest can then
be obtained and compared. This type of investigation is known as a “case-con
trol” study, and will be discussed in Chapter 11.
The general concept of a cohort study is relatively simple, although such
studies can be conducted in several ways. A sample of the population is selected
and information is obtained to determine which persons either have a particular
X ____________
ETIOLOGICAL
CHARACTERISTIC OR
EXPOSURE
a >
8
198
199
Lilienfeld DE, Stolley RD. (1994). Foundations of epidemiology
DISEASED GROUP
(CASES)
NONDISEASED GROUP
(CONTROLS)
Present (exposed)
Absent (not exposed)
characteristic (such as a behavior or physiological trait) that is suspected of being
related to the development of the disease being investigated, or have been exposed
to a possible etiological agent. These individuals are then followed for a period
of time to observe who develops and/or dies from that disease or physiological
condition (such as decline in a pulmonary function test). The necessary data for
assessing the development of the disease can be obtained either directly (by peri
odic examinations of everyone in the sample) or indirectly (by reviewing physi
cian and hospital records, disease registration forms, and death certificates). Inci
dence or death rates for the disease are then calculated, and the rates are compared
for those with the characteristic of interest and those without it. If the rates are
difierent (either absolutely or relatively), an association can be said to exist
between the characteristic and the disease. It is important to obtain information
on other general characteristics of the study groups, such as age, gender, ethnicity,
and occupation, in addition to the specific characteristic of interest, in order to
account for the influence of any factors that are known to be related to the disease.
Statistical methods are available for such analyses (Breslow and Day, 1987; Kel
sey et al., 1986; Kahn and Sempos, 1989; Fleiss, 1981).
This type of study has been described by a variety of terms: “prospective,”
“incidence,” “longitudinal,” “forward-looking,” and “follow-up,” but
“cohort study” will be used in this book. A distinction should be noted between
cohort studies, described in this chapter, and cohort analyses, discussed in Chapter
5. In cohort studies individuals are followed or traced, whereas in cohort analyses
there is no actual follow-up of persons; the follow-up is artificially constructed
by the analysis of mortality (or morbidity) in successive age groups over a series
of time periods (see p. 94).
MEASURING ASSOCIATION IN COHORT STUDIES
The data collected in a cohort study consist of information about the exposure
status of the individual and whether, after that exposure occurred, the individual
developed a given disease. These data may be tabulated into a 2 X 2 table (Table
JO
•• )
Epidemiologic Studies
Framework of a Cohort Study
Table 10-2.
ETIOLOGICAL CHARACTERISTIC
OR EXPOSURE
DEVELOPED DISEASE
DID NOT
DEVELOP DISEASE
TOTAL
a
c
b
d
a+b
c+d
Present (exposed)
Absent (not exposed)
10-2). The incidence rate among those persons exposed to the factor being inves
tigated is a/(a + b), while the rate for those not so exposed is c/(c + d). The
epidemiologist is interested, then, in determining whether the incidence rate for
those exposed is greater than the rate for individuals not exposed, i.e., is
a/(a 4- b) greater than c/(c + d)? If it is, then an association is said to exist
between the factor and the subsequent development of disease. The question then
asked by the epidemiologist is: How strong is the association?
Relative Risk
The relative risk (“RR”) is used to measure the strength of an association in an
observational study (Cornfield, 1951):
Relative Risk (RR)
Incidence rate of disease in exposed group
Incidence rate of disease in unexposed group
The variance, confidence limits, and statistical tests for the relative risk may be
found in the Appendix (p. 317). In a cohort study, if the incidence of myocardial
infarction among cigarette smokers was 3 per 1,000 and that for nonsmokers was
1 per 1,000, then the relative risk of myocardial infarction for smokers compared
to nonsmokers would be:
RR
(3/1,000)
(1/1,000)
3.0
This value of the relative risk means that a cigarette smoker is three limes as
likely to develop a myocardial infarction as is a nonsmoker.
The magnitude of the relative risk reflects the strength of the association;
i.e., the greater the relative risk, the stronger the association. A relative risk of
3.0 or more indicates a strong association; for cigarette smoking and lung cancer,
for instance, it is greater than 10.0, signifying a very strong relation (United Stales
Surgeon General, 1982). In contrast, the relative risk for a family history of breast
Cohort Studies
201
cancer (sister or mother) and female breast cancer is about 2.0, indicating a mod
erate association (Kelsey, 1979). A relative risk between 1.0 and 1.5 indicates a
weak association.
Relative risks may also be less than 1.0 in value, suggesting a protective
effect from exposure to a factor. For example, in a cohort study in Mali of menin
gococcal vaccine efficacy conducted during an epidemic of meningococcal men
ingitis, Binken and Bond (1982) found that the incidence rate of the disease
among those vaccinated was 0.7 per 10,000 persons and among those not vac
cinated 4.7 per 10,000 persons over the 5-week period following the vaccination
campaign. Hence, the relative risk of meningitis for those vaccinated compared
to those not vaccinated was 0.15, meaning that the risk of developing meningitis
for someone who was vaccinated is only 15 percent of that for someone who was
not vaccinated. This relative risk suggests a strong association between vacci
nation and protection from developing the disease.
Inferences about the association between a disease and exposure to a factor
are considerably strengthened if information is available to support a gradient in
the relationship between the degree of exposure (or “dose”) to the factor and the
disease. Relative risks can be calculated for each dose of the factor. The general
approach is to treat the data as a series of 2 X 2 tables, comparing those exposed
at various levels of the factor with those not exposed at all. An example of this
type of analysis is the study by Vessey and his colleagues (1989) of the relation
ship between oral contraceptive use and ovarian cancer.
In the early 1970s, the possibility of a relation between oral contraceptive
use and gynecologic cancer occurrence was suggested. During the period 19681974, 17.032 white married women, aged 25 to 39 years, were recruited at the
Oxford Family Planning Association clinics in England and Scotland (Vessey el
al., 1976). Of those enrolled, 6,838 were parous women who used oral contra
ceptives and 3,154 were parous women who used an intrauterine device (IUD).
Some of these women were followed for up to 20 years (from 1968) and deaths
were recorded by specific cause. The risk of mortality from ovarian cancer for
different duration levels of oral contraceptive use are shown in Table 10-3 com
pared with those who had no exposure, i.e., women who used an IUD. The relative
risks of death from ovarian cancer for oral contraceptive users relative to nonusers
were:
RR (less than 48 months of oral contraceptive use)
RR (48-95 months of oral contraceptive use)
12.1/9.2 = 1.32
= 1.8/9.2
0.20
RR (more than 96 months of oral contraceptive use) = 1.5/9.2
= 0.16
Epidemiologic Studies
Cohort Studies
Table 10-3. Mortality Rates per 100,000 Women-Years and Relative
Risk of Ovarian Cancer by Duration of Use of Oral Contraceptives
TOTAL DURATION
OF USE
Never*
< 47 months
48-95 months
96+ months
OVARIAN CANCER
MORTALITY RATE
RELATIVE RISK’ OF
9.2
12.1
1.8
1.5
1.00
1.32
0.20
0.16
OVARIAN CANCER
"Compared to "Never” users
bIntra-uterine device users
Source: Vessey et al. (1989).
This pattern of declining relative risk of ovarian cancer with increased duration
of oral contraceptive use suggests that these pharmaceuticals might protect against
this disease. A statistical significance test to determine whether such relative risks
are different from 1.0 was developed by Cochran (1954), and a method for cal
culating an overall (pooled) relative risk for all categories was developed by
Mantel and Haenszel (1959) (see Appendix, p. 320). If several studies of the same
epidemiologic problem have been carried out at different times and in different
places, it may be useful to scrutinize the estimates and then determine whether
they are similar (Breslow and Day, 1987; Greenland, 1987; Kahn and Sempos,
1989).
Attributable Fraction
A measure of association that is influenced by the frequency of a characteristic
in a population is the attributable fraction (also known as the “attributable
risk”). Levin (1953) originally defined it in terms of lung cancer and smoking as
the “maximum proportion of lung cancer attributable to cigarette smoking."
Attributable fraction can also be defined as the maximum proportion of a disease
in a population that can be attributed to a characteristic or etiologic factor. Another
way of using this concept is to think of it as the proportional decrease in the
incidence of a disease if the entire population were no longer exposed to the
suspected etiological agent. Although we are discussing attributable fraction in
the context of cohort studies, this measure of association is also useful in the
interpretation of case-control investigations (see Chapter 11).
As an example of the calculation of the attributable fraction, suppose that
the incidence of lung cancer in the overall population is 120 cases per 100,000
persons; among nonsmokers in that population, it is 30 cases per 100,000 persons;
203
and among smokers, it is 330 cases per 100,000 persons. The relative risk of lung
cancer among smokers compared to nonsmokers would then be 11.0 (330 per
100,000 / 30 per 100,000). Also assume that 30 percent of the population smokes.
If the 30 percent of the population that smokes were to stop, then the incidence
of lung cancer in that group would be reduced from 330 cases per 100,000 persons
to 30 cases per 100,000 persons. The attributable fraction of lung cancer for
cigarette smoking would then be:
Attributable Fraction (AF)
= 0.3 (330 per 100,000 - 30 per 100,000)
120 per 100,000
= 0.3 (300 per 100,000)
120 per I(X).(X)()
_ 90 per lOO.OOO
’ 120 per 100.000
= 75%
An alternative way to calculate the attributable fraction is:
Attributable Fraction (AF) =
P (RR - 1)
X HXK/f
P (RR - 1) + 1
where RR = the relative risk and P = proportion of the total population that has
the characteristic; the derivation of this formula can be found in the Appendix
(p. 319). In the lung cancer example, P is 30 percent and RR is 11.0. The attrib
utable fraction would therefore be:
AF
0.3 (11.0 - 1)
3.0
0.3 (11.0 - 1) + I
3.0 + 1
3.0
— = 75%
4.0
Standard error and confidence limits have been derived for the attributable frac
tion by Walter (1975, 1976) (see Appendix).
The effect of various values of the relative risk (RR) and various proportions
of those with a characteristic in the population (P) on the values of the attributable
fraction is shown in Table 10^4. When the frequency of a characteristic in a
population is low (e.g., 10 percent) and the relative risk for that characteristic in
a given disease is also low (e.g., 2), only a small proportion (9 percent) of the
cases of disease can be attributed to that characteristic (Adams et al., 1989).
However, with a high relative risk (e.g., 10) and a high proportion of the popu
lation having the characteristic (e.g., 90 percent), a much larger percentage (89
204'
Cohort Studies
Epidemiologic Studies
Table 10-4.
Attributable Fractions* as a Proportion for Selected Values of Relative
Risk and Population Proportion with the Characteristic
RR = RELATIVE RISK
P = PROPORTION OF POPULATION
WITH CHARACTERISTIC (%)
2
10
.09
.23
.33
.41
30
50
70
90
95
♦Attributable fraction =
.47
.49
4
io-
12
.23
.47
.73
.82
.86
.89
.90
.52
.77
.84
.89
.91
.92
.47
.60
.67
.73
.74
P (RR - 1)
P (RR - 1) + 1
percent) of cases can be attributed to it. In these calculations, it is assumed that
other etiological factors are equally distributed among those with and without the
characteristic.
The measurement of attributable fraction is particularly useful in planning
disease control programs (Walter, 1975, 1976; Stellman and Garfinkel, 1989). It
enables health administrators to estimate the extent to which a particular disease
is due to a specific factor anJ to predict the effectiveness of a control program in
reducing the disease by eliminating exposure to the factor. For example, epide
miologic studies have suggested that throughout the world, the hepatitis B virus
is the etiologic agent for 75 percent to 90 percent of primary hepatocellular cancer
(Beasley, 1988). A global hepatitis B vaccination campaign could therefore
greatly reduce the occurrence of this cancer.
Computations of attributable fraction are also helpful in developing strate
gies for epidemiologic research, particularly if there are multiple factors. In the
United States, for example, it is estimated that in certain age groups, 80 to 85
percent of lung cancer can be attributed to cigarette smoking. Other etiological
factors apparently play a relatively minor role, and the investigator interested in
ascertaining these factors may decide to limit further studies to nonsmoking lung
cancer patients. In general, if close to 100 percent of a disease is attributable to
one or more factors, a search for additional etiological factors may not be prof
itable unless one is interested in studying other characteristics that influence those
already exposed to a high-risk factor.
Exposure Assessment
A crucial aspect of the design of cohort studies concei
he categorization of
subjects into “exposed” and “unexposed” groups that can be compared with
205
respect to disease incidence. If subjects cannot be correctly categorized, a cohort
study is not feasible. An example of this inability to correctly classify exposure
arose when epidemiologists at the Centers for Disease Control attempted to plan
a cohort study of Vietnam veterans in regard to their exposure to Agent Orange,
a defoliant that contained the toxic contaminant dioxin (Lilienfeld and Gallo,
1989; Centers for Disease Control Veterans Health Study, 1988). It was hoped
that by learning about troop locations each day and comparing them to areas
where the defoliant was sprayed the same day, an exposure score could be com
puted for each subject. However, when this score was compared with serum
dioxin levels in a sample of such persons, it was clear that the exposure score
would not be valid. Thus, the correct classification of exposure was problematic.
The cancellation of the cohort study led to great protest by veterans’ organizations
who felt that their possible health risks were being ignored. However, conducting
a cohort study with this high potential for misclassification might have led to
results that underestimated the health risks of exposure to Agent Orange, if such
risks actually exist.
Exposure assessment is important in all cohort studies, not only in those of
occupational exposures. For example, the possible role of cardiovascular risk
factors, such as hypertension and hypercholesterolemia, in pediatric atheroscle
rosis and adult cardiovascular disease is currently being studied in a cohort study
of several thousand children in Bogalusa, Louisiana (Berenson and McMahon,
1980; Berenson, 1986). The exposure to these factors during childhood can be
assessed directly, rather than trying to do so later in life.
TYPES OF COHORT STUDIES
Cohort studies can be classified as follows:
1. Concurrent studies
(a) General population sample
(b) Select groups of the population
(i) Special groups—professional, veteran, etc.
(ii) Exposed groups—occupational, etc.
2. Nonconcurrent studies
(a) Population census taken in the past—usually special and unofficial
(b) Select groups of the population
(i) Special groups—professional, veteran, etc.
(ii) Exposed groups—occupational, etc.
Concurrent and
concurrent cohort studies are contrasted in Figure 10-1.
In a concurrent study, those with and without the characteristic or exposure are
Epidemiologic Studies
2v
f
Concurrent Study
Non-Concurrent Study
,◄----------I
I
l
l
I Exposed in
I
1962
l
I
I
I
I
I
I
I
I
In 1992 Select
Exposed and NonExposed Groups
' Exposedin
1992
Trace
The groups
by various
means,
from 1962
to 1992
1962
I
I
I
I
I
I
I
I
1992
Follow
The groups
from 1992 for
the desired
time period
(e g . until 2022)
i
I
I
i
i
I
i
i
i
i
i
i
i
i
i
2022
Figure 10-1. Diagrammatic representation of concurrent and nonconcurrent cohort
studies.
selected at the start of the study (1992 in Figure 10-1) and followed over a number
of years by a variety of methods. In a nonconcurrent study, the investigator
goes back in time (to 1962 in Figure 10-1), selects his or her study groups, and
traces them over time, usually to the present, by a variety of methods. These two
types of cohort studies must be distinguished because they involve different meth
odological problems.
A simple example of a nonconcurrent cohort study would be an investigation
of the safety of silicone breast implants. The epidemiologist might locate a group
of plastic surgeons, each of whom used only one brand of silicone breast implant.
The patient records of these surgeons would be reviewed for patients who had an
implant placed two or three decades ago. Alternatively, if the epidemiologist
identified a group of community hospitals in which silicone breast implant pro
cedures were conducted, the medical records of the hospitals could be reviewed
to provide information on the patients and the brand of implant used for each
procedure. Regardless of the means by which the patients were identified, they
would be followed up to the present time by contacting either the patient or the
patient's family. For each brand of implant, the morbidity and mortality experi
ence of the patient group would then be compared with that of the general pop
ulation.
Concurrent Studies
In concurrent studies, the investigator begins with a group of individuals and
follows them for a number of years. This was the approach used in the American
Cancer Society’s Cancer Prevention Study I (CPS 1) of the health effects of
cigarette smoking (Hammond, 1966; Garfinkel, 1985). The design of this study
was similar to that of an earlier, smaller study (Hammond and Horn, 1958). For
Cohort Studies
207
this investigation, 68,116 volunteers were recruited between October 1, 1959 and
February 15, 1960. Each volunteer was asked to enroll families in which at least
one person was 45 years of age or older. All persons in each household were
asked to complete forms detailing their smoking histories, family history, medical
history, occupational history, and various health habits. Follow-up was conducted
every year (through the volunteers), and every two years subjects were asked to
complete a follow-up questionnaire. Death certificates were obtained for each
reported death. About 1,045,000 completed forms were received from persons
residing in 1,121 counties in 25 states. Through September 30, 1962, 97.4 percent
of the participants were successfully traced; 971,362 were reported to be alive,
46,212 had died, and 27,513 could not be traced. Age- and cause-specific and
age-standardized mortality rates by history of tobacco use were computed from
the collected data. Since tobacco use differed so markedly between men and
women, the data were analyzed separately by gender. Figures 10-2 and 10-3
illustrate some of the findings for men in this classic study.
Figure 10-2 shows an increasing risk of mortality from bronchogenic (or
lung) cancer with increasing number of cigarettes smoked and lower mortality
rates among ex-smokers than among current smokers. Figure 10-3 shows that
the mortality rates among ex-smokers decrease as the period of time since (hey
had stopped increases, except for (hose who had stopped smoking within a year
of entry into the study. This exception may reflect the fact that some of the men
gave up smoking because they had already been diagnosed as having lung cancer.
Such findings (the outcomes associated with cessation of exposure) are important
o
8
8
cs
250
Q] NON-SMOKERS
200
(3 I ’ CIG / DAY
10-19 CIG / DAY
< |
150
^1 40+ CIG /DAY
So
or
LU LU
[g] 20 39 CIG / DAY
O CL
100
o
50 -
I
z
<
o
z
F
ZD
■
. .... I
o
J
SMOKING HABITS
Figure 10-2. Age-adjusted death rates from malignant neoplasm of lung for men by
amount of cigarette smoking at beginning of cohort study in 1959-1960. Source: Ham
mond (1966).
Epidemiologic Studies
■R
Cohort Studies
500
si
5z
ao
P- CD
LU CY
2.5
■ CURRENTLY SMOKES
cn
Qi
CY
BS
NON-SMOKING
SPOUSf
LU
400 _
o
z
<
o
0
z
Z)
[J STOPPED < 1 YEAR
^STOPPED 1-4 YEARS
300 "
STOPPED 5-9 YEARS
0 STOPPED 10+ YEARS
5§
■
200
100
LU
CL
K- n
|l
0
1-19CIG./DAY
20+ CIG./DAY
Figure 10-3. Age-adjusted death rates from malignant neoplasm of lung among men
who had never smoked, who had stopped smoking, and who were still smoking at
beginning of cohort study in 1959-60. Source: Hammond (1966).
in deriving etiological inferences from cohort studies (a subject that will be dis
cussed in detail in Chapter 12). The groups in the CPS I study were not probability
samples of the general population, which would have been preferable, but a prob
ability sample of the required size would have been impossible to obtain. A
similar study, known as the Cancer Prevention Study II, was started by the Amer
ican Cancer Society in the late 1970s in order to examine more recent exposures
of persons who may have been too young to participate in the CPS I study. Data
collected in this ongoing investigation are now being analyzed.
A similar approach was used by Hirayama (1981a, b) in his pioneering study
of passive smoking and lung cancer. He had collected infonnation on the smoking
habits of spouses of 91,540 nonsmoking wives and 20,289 nonsmoking husbands
in six prefectures in Japan in 1965. The mortality of these men and women was
assessed from death certificates during the 14 years of follow-up. Nonsmoking
spouses of smokers had an elevated risk of lung cancer compared with that for
nonsmoking couples (Figure 10^1). For nonsmoking men whose wives smoked
20 or more cigarettes daily, the risk was more than twice that of nonsmoking men
married to nonsmoking women.
In some situations a cohort study can be conducted in a population selected
from a well-defined geographical, political, or administrative area. This is partic
ularly feasible when the disease or cause of death is fairly frequent in the popu
lation and does not require recruitment of a large number of persons for the study.
The Framingham Heart Study is a good example of this type of cohort study
(Dawber, 1980). It was initiated in 1948 by the United States Public Health Ser
vice to study the relationship of a variety of factors to the subsequent development
2 -
-W
f—1 SPOUSE SMOKES
LJ 1 I4CIG /DAY
li
RTj SPOUSE SMOKES
LJ ISI9OG /DAY
1.5 -
209
F7<| SPOUSE SMOKES
LZJ >> c>G / Dav
::::::::::
O
22
Q:
1
>
I—
<
Ed
or
t
«•
LU
0.5 -
0
••>•:
1
NON-SMOKING WIVES
--------- -- fG..- J
M
(0)
NON-SMOKING HUSBANDS
Figure 10-4. Age-adjusted relative risk of lung cancer among nonsmoking husbands
and wives, by the smoking habits of their spouses. Source: Adapted from Hirayama
(1981a).
of heart disease. The town of Framingham, Massachusetts, was chosen for its
population stability, cooperation with previous community studies, presence of a
local community hospital, and proximity to a large medical center. The initial
population sample was a group of persons 30 to 62 years old that, when followed
over a period of twenty years, would result in enough new cases or deaths from
cardiovascular disease to ensure statistically reliable findings. The town’s popu
lation in this age group was approximately 10,000. A sample of 6,507 men and
women was selected. About 98 percent of the 4,469 respondents were free of
coronary heart disease at the initial examination (Feinleib, 1985). Another 740
volunteers were also included in the cohort as part of a community outreach effort
to ensure the continued participation in the study by each cohort member. After
the first examination, each person was reexamined at two-year intervals for a
thirty-year period. Information was obtained on several factors that could be
related to heart disease, such as serum cholesterol level, blood pressure weight
and history of cigarette smoking. Table 10-5 presents the incidence rates of cor
onary heart disease (CHD) among men and women during the first thirty years
of follow-up by initial systolic blood pressure, gender, and age (Stokes et al.,
1989). There is an increasing risk of CHD with increasing initial systolic blood
pressure m the 35- to 64-year-old age group, a gradient of CHD disease which
is slightly sleeper in the older male age group and slightly less steep for the
women.
The Framingham ’ ’1 Study also illustrates a strength of the cohort study.
1
210
Epidemiologic Studies
!
Table 10-5. Average Annual Incidence per 1,000 Persons of Coronary Heart Diseae
in Framingham, Massachusetts. 30-Year Follow-Up, by Systolic Blood Pressure
and Gender
SYSTOLIC BLOOD
PRESSURE (mmHg)
MEN
WOMEN
MEN
WOMEN
<120
120-139
140-159
160-179
>180
7
11
16
23
22
3
4
7
9
15
11
19
27
34
49
10
13
16
35
31
AGE 35-64
AGE 65-94
Source: Stokes et al. (1989).
investigating a variety of outcomes associated with a given exposure. For exam
ple, tn addition to investigating the association between systolic blood pressure
and CHD, for example, the Framingham investigators explored the relation
between systolic blood pressure and stroke; a strong relationship between
increased systolic blood pressure and elevated stroke risk was found.
The Framingham Heart Study became a prototype for similar studies in
Tecumseh, Michigan, and other areas (Keys, 1970; McGee and Gordon, 1976;
Napier et al.. 1970). However, the difficulties in selecting general population
samples for such studies tend to make investigators utilize a special group that
for one reason or another can be followed more easily; cenain professional
groups, people enrolled in medical care programs, veterans, and others. In Doll
and Hill’s (1964) classic cohort study of cigarette smoking and lung cancer for
instance, a questionnaire was sent to all physicians on the British Medical Register
who were living in the United Kingdom (see Chap. 1, p. 9). Follow-up was
simplified because the subjects were physicians and therefore maintained contact
with several professional organizations. Information from death certificates that
listed '-physician” as occupation was obtained from the Registrar General’s
Office. Lists were also obtained from the General Medical Council or the British
Medical Association for deaths that had occutred abroad or in the military
service.
J
A more recent example of the use of a unique population is the Oral Con
traception Study of the Royal College of General Practitioners (1974) in England
(Kay, 1984). Between May 1968 and July 1969, 23,000 oral contraceptive users
and an equal number of nonusers, matched only for age and marital status were
recruited by physicians from among their patients. The oral contraceptive users
selected were the first two women in each calendar month for whom the physi
cians wrote a prescription for an oral contraceptive. A nonuser was selected by
the following procedure; starting with the user’s record, returned to its correct
place m the doctor's file, each subsequent record was examined in alphabetical
I
I
Cohort Studies
21k_>'
order until the next record was found for a woman whose year of birth was within
three years either side of that of the user and who had never used an oral contra
ceptive. Both the user and the nonuser had to be either married or known to be
living as married.” These 46,000 women were followed with regard to their
morbidity and mortality experience. In 1974, 1977, 1978, 1981, and 1988, prog
ress reports were issued, showing associations between oral contraceptive use and
(1) deep venous thrombosis. (2) acute myocardial infarction, and (3) subarachnoid
hemorrhage (Table 10-6).
A similar approach was used by Hennekens and his colleagues (1979) in the
Nurses’ Health Study. These investigators sent questionnaires on possible risk
factors (e.g., oral contraceptive use. smoking habits) to 121,700 nurses in 1976.
Follow-up questionnaires were sent every two years thereafter to update risk
factor information and to ascertain newly diagnosed conditions. Such data allow
the epidemiologist to determine the effect of changes in risk factors on subsequent
health events.
Concurrent cohort studies are not limited to noninfectious diseases. An
example of the application of this method to infectious diseases is the study by
Beasley el al. (1981. 1988) implicating the hepatitis B virus in the etiology of
primary hepatocellular cancer. These investigators recruited 21,227 male Tai
wanese government civil servants between November 1975 and June 1978. and
1,480 from a cohort study of risk factors for cardiovascular disease. Of these
22,707 men. 3.454 were hepatitis B surface antigen (HBsAg) positive, indicating
past infection with the hepatitis B virus. By the end of 1986, 161 participants had
developed primary hepatocellular cancer. The HBsAg positive group had a sig
nificantly higher rale of the disease than did the HbsAg negative group (Table
10-7). The relative risk of death from primary hepatocellular carcinoma among
those who were HBsAg positive compared with that for those who were negative
Table 10-6.
Age-Adjusted Relative Risks of Oral Contraceptive Users Compared
to Nonusers
RELATIVE RISK (ORAL
CONTRACEPTIVE USER
disease (icd-9 c ati-gory)
TO NONUSER)
Nonrheumatic heart disease and hypertension (400-429)
Ischemic heart disease (410-414)
Subarachnoid hemorrhage (430)
Cerebrovascular accident (431-433)
Deep thrombosis of the leg, pulmonary embolism (450-453)
5.6
3.9
4.0
2.1
(*)
Source: Adapted from Layde cl al. (1981).
*Raic for nonusers was 0.0; no relative risk could be calculated.
Epidemiologic Studies
Cohort Studies
Table 10-7. Relation between HBsAg Antibody Status on Entrance to Study and
Subsequent Development of Primary Hepatocellular Carcinoma through
December 31, 1986
AVERAGE ANNUAL1
INCIDENCE RATE OF PRIMARY
CASES OF PRIMARY
HEPATOCELLULAR
HEPATOCELLULAR
CARCINOMA PER 100.000
HBSAg STATUS
NUMBER
CARCINOMA
POPULATION
Positive
Negative
3,454
19,253
152
9
4945
53
Relative risk of death from primary hepatocellular carcinoma among those who are HBsAg
positive compared with those who arc negative is (494.5/1 (X),000)/(5.3/100.(X)0) = 98.4.
'For 8.9 years of follow-up.
Source: Beasley (1988).
was 98.4, indicating a very strong association between HBsAg status and primary
hepatocellular carcinoma.
The concurrent cohort study is particularly useful when the investigator does
not know what the specific agent is when the study begins. In early 1984, for
example, before the human immunodeficiency virus (HIV-1) had been identified
as the etiologic agent for the acquired immunodeficiency syndrome (AIDS), the
Multicenter AIDS Cohort Study (MACS) was begun to investigate the etiology
and natural history of the disease (Kaslow et al., 1987). In Baltimore, Chicago,
Los Angeles, and Pittsburgh, 4,955 homosexual men were recruited between
April, 1984 and March, 1985. Each recruit provided blood, urine, feces, saliva,
and semen specimens, which were stored for future analyses. The study popula
tion is reexamined every six months to determine if the participants have anti
bodies to the HIV-1 virus and, if so, what AIDS manifestations, if any, have
developed. As hypotheses concerning the various manifestations of AIDS are
developed, these specimen banks will be used to test those hypotheses.
In the concurrent cohort studies discussed so far, the study population was
divided into those with and those without one or more possible etiological factors.
The groups were sometimes classified according to different degrees of exposure
or to levels of a characteristic such as the presence of the hepatitis B surface
antigen. The incidence and mortality rates of these subgroups were then com
pared. The study groups were selected because they offered particular advantages
for follow-up and information about a specific factor was obtainable from them.
In a different type of concurrent study, a specific group that has been exposed to
a possible etiological factor is selected and followed to determine the effects of
this exposure as compared with the experience of a popon not exposed to
213
that substance. This method has been especially useful in studies of the effects
of exposure to substances in occupational environments. The elucidation of the
relation between occupational exposure to asbestos and lung cancer provides an
example of this strategy.
In 1955, Doll reported that the relative risk of lung cancer in a group of
asbestos factory workers compared to the general population was 10. In 1963,
Selikoff and his co-workers began a cohort study of 370 members of the Inter
national Association of Health and Frost Insulators and Asbestos Workers (IAHFIAW) (Selikoff et al., 1968). Follow-up of this cohort continued until 1967,
when the investigation ended. The study findings suggested that there was an
interaction between asbestos exposure and cigarette smoking in the development
of respiratory cancer. These investigators initiated a study in 1967 of all U.S. and
Canadian members of the 1AHF1AW (Selikoff, 1979). The union provided the
investigators with a membership list for 1966. Each member was mailed a ques
tionnaire in which he was questioned about his smoking habits and the use of a
mask while working. Some 17,800 men were followed from January 1, 1967 until
December 31,1976; 2,271 men died during the nine-year period. A control group,
which had not been exposed to asbestos, was selected from the roster of 1,045,000
persons enrolled by the American Cancer Society in 1959 for the CPS I study
described earlier. The control group, selected to be similar to the exposed group
except for the exposure to asbestos, consisted of “men, not a farmer, no more
than a high school education, a history of occupational exposure to dust, fumes,
vapors, gases, chemicals, or radiation, and alive as of January 1, 1967.’’ This
group numbered 73,763 such persons. Follow-up of the nonexposed individuals
was conducted in September, 1972. Official mortality statistics were used to
extrapolate the observed mortality through 1976.
One of the major findings of this study is the positive interaction between
both cigarette smoking and asbestos in markedly elevating the risk of lung cancer
(Table 10-8). This type of relation is indicated by the fact that the death rate for
Table 10-8. Age-Adjusted Lung Cancer Death Rates per 100,000 Man-Years, by
Cigarette Smoking Status and Occupational Exposure to Asbestos Dust
NONSMOKERS
CIGARETTE SMOKERS
Not exposed to asbestos dust
11.3
(1.0)*
122.6
Exposed to asbestos dust
58.4
(5.2)
(10.9)
601.6
(53.2)
♦Figure in parentheses is relative risk of lung cancer mortality compared with that for nonsmoking
persons not exposed to asbestos dust.
Source: Hammond el al. (19
J
2
Epidemiologic Studies
the combination of cigarette smoking and asbestos exposure was five times that
of arette smokers without asbestos exposure and ten times that of nonsmoking
persons with asbestos exposure. One might expect the relative risk for smoking
workers to be about 15 if no positive interaction were present; however, it was
53, indicating such an interaction.
J
I
215
20
d NO RADfATION
TREATED WITH X-RAY
<
15
TREATED WITH P32
=> o
TREATED WITH X-RAY AND P32
10
Nonconcurrent Studies
In nonconcurrent cohort studies, the period of observation starts from some date
in the past, as illustrated in Figure 10-1; aside from the observation period, how
ever, all other aspects of a nonconcurrent cohort study are the same as for a
concurrent cohort investigation. These studies cannot be conducted with samples
of the general population unless the investigator has access to a census of a
community, usually unofficial, which was conducted in the past. Samples of the
population covered by the census can then be selected and traced from the time
of the census (Comstock, Abbey, and Lundin, 1970).
Nonconcurrent studies usually involve specially exposed groups or industrial
populations because past census information is often unavailable and employ
ment, medical, or other types of records usually are available. This is illustrated
by the study of the relation between polycythemia vera (PV) and leukemia, which
had been clinically observed since 1905 (Modan and Lilienfeld, 1965). The
increased medical use of radiation treatment for PV and the observations of the
leukemogenic effect of ionizing radiation in various studies raised the question
as to whether the development of leukemia in patients with PV was pan of the
disease’s natural history or a result of treatment with X-ray and/or P52, a radio
active isotope. A study was undertaken to estimate the risk of developing leu
kemia among patients with PV and to determine whether it was increased as a
result of P32 and/or X-ray treatment. Medical records of patients with PV who
had been seen during 1947-1955 in seven medical centers were obtained at the
same time as those of two comparison groups: (a) patients with polycythemia
secondary to lung disease and (b) patients with questionable polycythemia. These
groups were then classified by method of treatment into four categories: (1) no
radiation treatment, (2) X-ray alone, (3) P32 only, and (4) a combination of X-ray
and P32. The patients were traced through December 31, 1961. Leukemia occurred
predominantly in patients who had received some form of radiation, either X-ray,
P32, or a combination of the two (Figure 10-5). This finding has since been
confirmed in a randomized clinical trial (Berk et al., 1981).
Nonconcurrent cohort studies of industrial exposures to possible etiological
agents of disease can only be carried out by using company records of past and
present employees that include information on the date that they begin their
employment, age at hiring, the date of departure, and whether they are living or
Cohort Studies
8z
5 -
0
_ mO
POLYCYTHEMIA
VERA
I
QUESTIONABLE
POLYCYTHEMIA
VERA
____(Q)
(0) (0)
SECONDARY
POLYCYTHEMIA
Figure 10-5. Incidence of leukemia among persons with polycythemia vera, ques
tionable polycythemia vera, and secondary polycythemia vera. Source: Modan and Lil
ienfeld (1965).
dead. The mortality experience can be determined and compared with that of
another industry, or with the mortality rate of the state where the industry is
located, or of the country as a whole. This approach was used by Rinsky and his
colleagues (1987) in a study of the relationship between exposure to benzene and
leukemia mortality.
The study population consisted of all 1,165 nonsalaried white men employed
in a rubber hydrochloride department of any of three plants in Ohio engaged in
the manufacture of this natural rubber film for at least one day between January
1, 1940 and December 31. 1965. The cohort was assembled by using company
personnel records. The cohort was traced through December 31, 1981, using vital
status data from the Social Security Administration, the Ohio Bureau of Motor
Vehicles, and a commercial tracing service. Death certificates were obtained for
all deceased members. At the same time, an industrial hygienist used company
records of benzene exposure to estimate the cumulative occupational exposure to
benzene of each person in the cohort. At the time these exposure estimates were
developed, the industrial hygienist did not know which of the cohort members
had died from leukemia or from other causes.
The observed mortality from leukemia (nine deaths) was then compared with
that expected if the cohort had had the same mortality experience as the United
States population during the same time period. The results, shown in Figure 106, indicated a striking relationship between cumulative occupational exposure to
benzene and leukemia mortality.
'J
Epidemiologic Studies
Cohort Studies
70
60
50
<
40
ZD
UJ
30
DC.
20
10
0
20
120
300
500
EXPOSURE TO BENZENE ( PPM-YRS )
Figure 10-6. Standardized mortality ratio for 1,165 white men with at least one day
of exposure to benzene from January 1,1940 through December 31,1965, according
to cumulative exposure (parts of benzene per million particles x years of exposure).
Source: Adapted from Rinsky et al. (1987).
STUDY PROCEDURES
A major source of difficulty in carrying out cohort studies is maintaining follow
up of the selected groups of persons. This is least troublesome in concurrent
cohort studies for obvious reasons. At the very start of such studies, methods can
be adopted for keeping in contact with the population on an annual basis, includ
ing periodic home visits, telephone calls, and mailed questionnaires, or even all
three. The names and addresses of several friends and relatives can be obtained
at the beginning of a study so that they may be contacted if the person moves out
of the community. (Geographic mobility of people, particularly in the United
States, can pose a problem.) To minimize the difficulties posed by tracing a
cohort, cohort studies are often conducted in a health maintenance organization,
in which the study population can be relatively easily followed. Another approach
is to use a health or disability (for morbidity) or life (for mortality) insurer’s
clientele, as there is an economic incentive for the study population to inform the
insurance company of the outcomes of interest. For deaths in the United States
that have occurred since 1979, the National Death Index (administered by the
National Center for Health Statistics) will inform investigators of the year and
place of death for a given person (User’s Manual, Nation
iath Index, 1981).
217
In many countries, national or regional registries for cancer and other diseases
can be used to follow up subjects in a cohort study.
Despite the best efforts, a certain number of individuals will likely be lost
to follow-up. Even for this group, information on mortality status can often be
obtained from state vital statistics bureaus. Their mortality experience can then
be compared with that of the individuals not “lost to follow-up’’ to determine if
there are any differences between the two groups. In addition, (he successfully
traced group can be compared to the “lost” group with respect to several known
characteristics. To the extent that they show similar frequencies of a variety of
characteristics of interest in the study, one’s confidence is increased that no bias
has been introduced into the findings by the lost group.
In a nonconcurrent cohort study, when one goes back perhaps twenty or
thirty years to select a study group, the problem of tracing becomes more difficult.
Every available source of information about subjects in the study should be used.
Table 10-9 presents the various means used by Modan (1966) in determining the
survivorship status of patients in his study of polycythemia vera and leukemia.
In all cohort studies, it is desirable to trace as high a percentage of the study
group as possible. Questions are frequently raised about the possibility of bias in
the results if the degree of follow-up is less than 95 percent. This issue has been
considered in several studies. Modan and Lilienfeld (1965) found that a very
good estimate of the total mortality rate was obtained from the first 77 percent of
the patients traced, although the group that was reached first had a somewhat
higher leukemia mortality rate than those traced later. In a study of the outcome
of neurosis, on the other hand, Sims (1973) found considerable differences
Table 10-9. Distribution of Sources of Information on Patiem’s
Survivorship Status in the Study of Polycythemia Vera and Leukemia
SOURCE OE INFORMATION
Patient
Local physician
Relative
Hospital
Neighbors
Postmaster
Town-County clerk
Health department
Other
Untraced
Total
Source: Modan (1966
NUMBER OF PATIENTS
PERCENT
158
201
103
540
49
18
20
89
24
20
12.9
1,222
16.4
8.4
44.2
4.0
1.5
1.6
7.3
2.0
1.6
100.0
Epidemiologic Studies
between the patients who were easily contacted and those who were traced with
more effort. Only three deaths had occurred among the first 110 patients traced
(59 percent of the study group), but eighteen additional deaths were discovered
in the sixty-six patients (36 percent of the study group) who were found by more
intensive tracing. Rimm and his colleagues (1990) have noted that even the type
of mail service used during follow-up can affect response rates. Thus, it appears
that the pattern varies in different studies and, perhaps, with different diseases,
so that a general rule cannot be established about the degree of follow-up nec
essary to ensure unbiased conclusions. The safest course is to attempt to achieve
as complete a follow-up as possible.
Cohort Studies
PERSON-YEARS
OF
OBSERVATION
1--------1------- 1------- 1“>1 ALIVE
Ar
i
C
O
H
O
R
T
M
E
M
B
E
P
S
l
I
I
I
l
l
B t
4---------4.1--------- 1------- 1—>1 DEATH I
I
I
I
lI
I
I
I
I
I
I
Cf—r
I
I
I
I
I
I
I
I
I
I
D i-------- 1I
4------ I---- DEATH I
I
Illi
I
I
I
I
I
I
I
I
r I
I
I
I
t
► | DEATH |
|
I
I
I
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Illi
I
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]—h>lDEArHl
F |___ ___ |___
ANALYSIS OF RESULTS
219
~r
I
I
I
I
I
I
I
I
I
I
I
LOST TO FOLLOW-UP
8 \
6
4
29
4
1
6
YEARO
YEAR 6
YEAR A
YEAR 8
YEAR 2
START OF STUDY
END OF STUDY
YEAR?
YEAR!
YEARS
YEAR 3
TIME
General Strategy
It has already been made clear that the results of cohort studies are preferably
analyzed in terms of relative risks, which provide a relatively simple expression
of the relation between mortality rates from different diseases in the groups being
compared. This is particularly true if the follow-up observations are made in the
same period for all the study groups.
Many cohort studies, however, whether concurrent or nonconcurrent,
involve lengthy and varying periods of observations. Persons are lost to follow
up or die at different times during the course of the study, and consequently they
are under observation for different time periods. In some studies, persons are
enlisted or enter the study at different times and, if the follow-up is terminated at
a specific time, they will have been observed for different lengths of time. Two
related methods are available for analyzing the results of such studies:
1. The calculation of person-years or months of observation as the denom
inator for the computation of incidence or mortality rate.
2. Actuarial, life table, or survivorship analysis (also known as cumulative
incidence or mortality analysis).
Person-years of observation are often used as denominators in the computation
of rates in cohort studies, as in the Royal College of General Practitioner’s Oral
Contraceptives Study. They are particularly useful when several factors, such as
age, sex, and varying periods of observation (which result from persons entering
and leaving the study at different ages and times), make the computation of an
actuarial life table difficult or impossible. This analytic approach takes into con
sideration both the number of persons who were followed and the duration of
Figure 10-7. Diagrammatic illustration of contribution of person-years observed in a
hypothetical eight-year cohort study of six persons (A,B,C,D,E, and F).
observation. In Figure 10-7, six persons are followed during an eight-year con
current cohort study. Four of these persons (B, C, D, and E) die during the course
of the follow-up. One person (A) is alive at the end of the study, and one person
(F) is lost to follow-up after six years. The total number of person-years of obser
vation (during which the cohort members were at risk of dying) is 29 years. The
death rate in this study is therefore 4 deaths/29 person-years of observation (13.8
per 100 person-years of observation).
The use of person-years of observation makes it possible to express in one
figure the time period when a varying number of persons is exposed to the risk
of an event such as death or the development of disease. In addition, the age
distribution of the groups under observation changes as a study progresses, as do
the mortality and morbidity rates over time (Matanoski et al., 1975). The use of
person-years is limited by the assumption that the risk of occurrence of an event
per unit time is constant during the period of observation for the individual and
that that risk is the same among similar persons in the cohort (Sheps, 1966;
Breslow and Day, 1987). The overall effect of these limitations is modest and
usually acceptable in most cohort studies.
Many regard using life tables (also known as survivorship methods) as the
preferred method of analyzing data from cohort studies (see Appendix) (Chiang,
1961; Kahn and Sempos, 1989; Breslow and Day, .1987). They provide direct
estimates of the probability of developing or dying from a disease for a given
time period, and relative risks can be computed as the ratio of these probabilities.
Life table methods can be used when the assumptions for person-years cannot be
satisfied.
1
?o
Epidemiologic Studies
Latency
Regardless of the technique used to estimate the relative risk of developing a
disease, one must also examine the possible effect of different latency or incu
bation periods. For instance, if a malignancy does not develop for at least a decade
after the exposure to the suspected carcinogen began, then persons in the cohort
would not be at risk for developing the disease until at least a decade had passed
since their first exposure. Only after that decade had passed would those persons
begin to accrue person-years of observation or be included in a life table (in the
first interval); likewise, only if the disease developed after that first decade would
that event be included in the analysis.
Adjustment for Age and Other Factors
The relative risks that are calculated by using either person-years or life table
methods are unadjusted for age or other possible confounding factors. A con
founding factor is one that is related both to the disease of interest and to another
factor that is itself associated with the disease. For example, suppose that an
epidemiologist conducted a cohort study of cigarette smoking and lung cancer.
Many factors related to cigarette smoking (e.g., age, gender, and race) are inde
pendently associated with lung cancer. Hence, to measure the true relative risk
between lung cancer and cigarette smoking, the epidemiologist would need to
adjust the observed relative risk for these and other possible confounding factors.
If adjustment for these factors does not change the relative risk, then little or no
confounding is said to be present.
The epidemiologist may use two different approaches to adjust (or “con
trol”) for possible confounding factors:
1. Stratify the data by the possible confounding factors into multiple 2X2
tables to calculate the stratum-specific relative risk. An adjusted relative
risk may then be calculated with Mantel-Haenszel techniques.
2. Use statistical techniques to mathematically model the risk of developing
the disease, adjusted for the effects of the possible confounding factors.
Examples include the logistic, the log-linear, and the proportional hazards
models.
Where the entire study groups was exposed, however, it is necessary to use
an external comparison or control group. If none is available, the mortality (or,
if such data are available, the morbidity) experience of the exposed group is
usually compared with that of the entire population living in the same geograph
ical area as the exposed group, with statistical adjuj
nts for age, sex, and
Cohort Studies
221
calendar time of exposure and follow-up. For mortality, the number of deaths in
the exposed group is compared with the expected number, based on the appro
priate death rates for that geographical area. This comparison is then expressed
as a Standardized Mortality Ratio (SMR) (see Chapter 4). This approach is fre
quently used in epidemiologic studies of occupational exposures (Monson, 1990).
The previously described benzene-leukemia study by Rinsky et al. (1987) pro
vides an example of this type of data analysis (see p. 215).
SUMMARY
In a cohort study, the investigator assembles a group of persons exposed to a
possible etiologic factor and another, comparable group not exposed to that factor.
These two groups are followed for the development of diseases. The investigator
then calculates the incidence rate for a given condition in the exposed and unex
posed groups, and a relative risk of developing the disease is calculated from
those incidence rates. The stronger the association, the larger the relative risk;
relative risks of 3.0 to 4.0 or more are usually indicative of strong associations
between the factor and the disease. The proportion of disease in a population that
is associated with that factor (assuming an etiologic relation) is the attributable
fraction. The larger the attributable fraction of a disease for a given factor, the
more difficult it becomes to study other possible agents of that disease.
There are two types of cohort studies: concurrent and nonconcurrent. In a
concurrent study, the investigator assembles the exposed and nonexposed groups
at the same time that the study is being conducted; these groups are then followed
concurrently with the conduct of the study. In a nonconcurrent study the inves
tigator reconstructs the groups in their entirety at some time in the past. This may
be done with any set of records that provides information on all members of the
population regarding their exposure at the same time in the past. Both groups are
then followed to the present for the development of disease.
The process of following up the cohort of persons exposed and not exposed
poses the greatest challenge to the epidemiologist in this study design. Inadequate
follow-up can result in biased data and either spurious associations or missed
relationships. It is also possible that the follow-up conducted in the early phases
of a study may provide information on a portion of the cohort that is not reflective
of the entire group. Analysis of the data at such a stage might result in different
inferences than if one waited until both groups had been followed up completely.
Two methods are available for the analysis of cohort studies: (1) the calcu
lation of incidence rates among those exposed and those not exposed using per
son-years of observari ~' and (2) the calculation of life-tables to provide interval
specific incidence rat of disease among those exposed and those not exposed.
Epidemiologic Studies
The use of person-years assumes that the risk of developing the disease is the
same in each time period of follow-up and also that the risk of developing disease
for each member of the cohort is the same. The incidence rates for those exposed
and those not exposed are then compared by calculating the relative risk of dis
ease, a measure of the strength of the association between the exposure and the
disease. The magnitude of the relative risk may be affected by the presence of
confounding factors, which may be related to the exposure, to the disease, or
both. The effects of confounding may be adjusted for by stratification (calculating
stratum-specific relative risks) or by constructing a statistical model of the data.
If the entire cohort was exposed to the factor (e.g., an occupational study), an
SMR-based analysis may be used to control for possible confounding factors,
such as age and gender.
STUDY PROBLEMS
1. It has often been stated that the Standardized Mortality Ratio (SMR) and
the relative risk are equivalent. Are they? Why might such a statement
be made?
2. How useful is the attributable fraction to the epidemiologist?
3. A certain virus V is suspected of being the cause of infectious disease D.
Design a cohort study to elucidate the relationship between V and D.
How does the design change if V is a ‘‘slow virus” or if D is currently
viewed as a noninfectious disease?
4. Internationally, several medical billing data bases are being developed by
health maintenance organizations (HMOs) and national health care sys
tems. How can these systems be used to conduct both concurrent and
nonconcurrent cohort studies?
5. A few surgeons seek your advice (as the local epidemiologist) concerning
a study they would like to conduct to determine the effect of tonsillectomy
on subsequent mortality. What might you recommend?
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}
*
Case-Control Studies
11
227.,
T
)
*
Table 11-1. Framework of a Case-Control Study
NUMBER OF INDIVIDUALS
OBSERVATIONAL STUDIES:
II. CASE-CONTROL STUDIES
In case-control studies, comparisons are made between a group of persons that
have the disease under investigation and a group that do not. Usually those with
the disease are called “cases” and those without the disease are called “con
trols.” Indeed, case-control studies may be viewed as an extension of the case
series that a health professional might assemble from his or her practice but with
an important addition—the control group allows for a comparison to be made
with regard to exposure history. Since the exposure history is assessed for some
period in the past, case-control studies are also called “retrospective studies.”
Whether the characteristic or factor of interest is (or was) present in the two
groups is usually determined by interview, review of records, or biological assay.
The proportion of cases exposed to the agent or possessing the characteristic (or
factor) of etiological interest is compared to the corresponding proportion in the
control group. If a higher frequency of individuals with the characteristic is found
among the cases than among the controls, an association between the disease and
the characteristic may be inferred.
When interested in determining whether prior exposure to an environmental
factor is etiologically important, the epidemiologist will attempt to obtain a history
of such exposure by interviewing the cases and controls. In practice, information
on both current and past characteristics is usually obtained. One must constantly
be aware that the derivation of inferences depends upon the temporal sequence
between the characteristic and the disease.
The data for a case-control study are generally tabulated in the form of a
four-fold table, as shown in Table 11-1. Such a table allows for the comparison
226
WITH DISEASE
WITHOUT DISEASE
CHARACTERISTIC
(CASES)
(CONTROLS)
TOTAL
With
Without
Total
a
c
a+c
b
d
b+d
a+b
c+d
a+b+c+d=N
of the prevalence of exposure among the cases, a/(a + c), with that for the
controls, bl(b + d).
In a case-control study the odds ratio is an estimate of relative risk calculated
as the cross-product of the entries in Table 11-1, ad/bc (see Appendix). Two
assumptions are necessary in making this estimate: (a) the frequency of the disease
. in the population must be small, and (b) the study cases should be representative
of the cases in the population and the controls representative of the noncases in
the population. This cross-product estimate can be made with either actual num
bers or percentages (Cornfield, 1951). The relative risk (or odds ratio) stays the
same whatever the frequency of the exposure in a population. For example,
whether smoking is highly prevalent or not, for a mother who smokes, the odds
ratio describes her increased risk of delivering a low-birth-weight baby.
A study by Hurwitz and his colleagues (1987) of the relationship between
the use of various medications and Rcye’s syndrome shows how the case-control
approach can be used to investigate an etiological hypothesis and how the data
can be analyzed with a four-fold table. Reye’s syndrome is a rare, acute, and
often fatal encephalopathy marked by brain swelling, low blood sugar, and fatty
infiltration of the liver. Observations from case-series studies, case reports, and
smaller case-control studies had implicated aspirin (salicylate) ingestion during
viral illness as a possible cause of this disease of children. Cases deemed eligible
for the Hurwitz study had to have received a diagnosis of Reye’s syndrome from
a physician, reported an antecedent respiratory or gastrointestinal illness or
chicken pox within the three weeks before hospitalization, and experienced stage
Il or deeper encephalopathy. The control group consisted of children who did not
have Reye’s syndrome but did have chicken pox or a respiratory or gastrointes
tinal illness within a period of a few weeks before selection for the study. In this
study there were four types of controls: emergency room patients (ER controls),
inpatients (hospital controls), school children at the same school as the patient
(school controls), and children located by the use of random-digit telephone dial
ing (community controls). The controls were matched to the cases on three patient
characteristics: age, race, and the presence of an antecedent illness. The key data
from the study are shown in Table 11-2. The percentage of salicylate users among
I
In
28
Epidemiologic Studies
Case-Control Studies
Table 11-2. Number of Hospitalized Reye’s Patients and Number of Pooled Controls
with a History of Salicylate Use in Three-Week Period
CASES OF REYE’S SYNDROME
CONTROLS (POOLED)
26
I
53
87
27
140
Used salicylates
Did not use salicylates
Total
Source: Hurwitz et al., 1987.
the cases was 96.3% (26/27) as compared to 37.9% (53/140) among the controls,
and the odds ratio (the estimate of relative risk) was calculated as follows:
ad
26 X 87
be
53 X 1
2262
------ = 42.7
53
The variance, standard error, confidence limits, and significance test for the odds
ratio can be computed by the procedures presented in the Appendix.
Children with viral illnesses (chicken pox, upper respiratory, or gastrointes
tinal) who used salicylates during the illness were 42.7 times more likely to
develop Reye’s syndrome than were children with the same viral illness who did
not use salicylates. Thus, aspirin use during viral illness appeared to be strongly
associated with the development of Reye’s syndrome, increasing the risk over
forty-fold.
While these data provide an estimate of risk, they do not allow one to esti
mate the incidence of Reye’s syndrome in the population of children at risk. To
estimate the incidence one would need to know the number of all cases of Reye’s
syndrome among children (for the numerator) and the number of children who
experienced respiratory or gastrointestinal illnesses or chicken pox (the denomi
nator). Most case-control studies do not allow one to estimate incidence because
denominator data are not available and numerator data may be incomplete.
22*)
among studies using different types of control groups increases the validity of
inferences that may be derived from the findings.
How many controls should be obtained for each case? Appropriate controls
are often scarce or limited. In comparing workers at a factory who were or were
not exposed to a substance, for instance, one would be limited to the finite set of
workers who worked at the factory. In other situations, appropriate controls are
readily available, as when studying normal birth outcomes compared to undesii
able birth outcomes. Even when controls are abundant, it may be costly and time
consuming to enroll and interview controls; one would want to include only as
many as are needed. In studies of rare diseases the number of cases may be so
small that the study has insufficient power to detect meaningful differences in
exposure. An increased number of controls—up to four per case—may give the
study more power (Gail et al., 1976). When the number of cases is large and the
power is greater than 0.9 with only one control per case, additional controls cannoi
add very much to the power.
In selecting cases one may often use all cases occurring in a defined time
Table 11-3. Some Sources of Cases and Controls in Case-Control Studies*
CASES
CONTROLS
All cases diagnosed in the community (in
hospitals, other medical facilities
including physicians' offices)
Probability sample of general population in
a community obtained by various
methods including random-digit dialing
All cases diagnosed in a sample of the
general population
Noncascs in a sample of the general
population or subgroup of a sample of
general population (e.g., random-digit
dialing)
All cases diagnosed in all hospitals in the
community
Sample of patients in all hospitals in the
community who do not have the
diseases being studied
All cases diagnosed in a single hospital
Sample of patients in same hospital where
cases were selected
THE SELECTION OF CASES AND CONTROLS
All cases diagnosed in one or more
hospitals
Sample of individuals who are residents in
same block or neighborhood of cases
Various methods have been used to select cases and controls for case-control
studies (Table 11-3) Sometimes investigators select cases from one source and
controls from a variety of sources, permitting comparisons with different control
groups as in the Reye’s syndrome study (see Table 11-4). Consistency of results
Cases selected by any of the above
methods
Spouses, siblings, or associates
(schoolmates or workmates) of cases
Accident victims
‘Various combinations of sources are possible.
. 230
Case-Control Studies
Epidemiologic Studies
Table 11-4. Comparison of Salicylate Exposure among Reye’s Patients and Four
Types of Controls
CONTROLS
Exposed to
aspirin (%)
Total N
Odds ratios
CASES
EMERGENCY ROOM
INPATIENT
SCHOOL
COMMUNITY
96
40
27
44
34
27
30
39
22
66
45
33
43
44
23
under study is already known or has been observed in available mortality statis
tics, morbidity surveys, or other sources. In addition, when cases and controls are
matched on any selected characteristic, the influence of that characteristic on the
disease can no longer be studied. Hence, caution should be exercised in deter
mining the number of variables selected for matching, even when feasible. If the
effect of a characteristic is in doubt, the preferable strategy is not to match but to
adjust for these characteristics in the statistical analysis.
Source: Hurwitz et al.. 1987.
POTENTIAL SOURCES OF BIAS
period or geographic area. The researcher then has an idea about the age. race,
and gender of the cases, as well as other characteristics. To ensure comparability
of cases and controls one may restrict the controls to the same age range, race,
and gender (or other characteristic) as the cases, or one may group match (also
known as frequency match). For example, the cases can be stratified into dif
ferent ten-year age groups. The control group can then be similarly stratilied.
Comparisons can then be made at each factor level between cases and controls
with the usual statistical significance tests (Cochran, 1954; Mantel and Hacnszel,
1959).
As an alternative to group matching, individual cases and controls can be
pair-matched for various characteristics so that each case has a pairmale. Ideally,
these pairmates should be chosen to be alike on all characteristics except for the
particular one under investigation. In practice, if many characteristics are chosen
for matching, or if many levels are chosen for each characteristic, it becomes
difficult to find matching controls for each of the cases. In epidemiologic studies,
there are usually a small number of cases and a large number of potential controls
to select (or sample) from. Each case is then classified by characteristics that are
not of primary interest, and a search is made for a control with the same set of
characteristics. If the factors are not too numerous and there is a large reservoir
of persons from which the controls can be chosen, case-control pair matching
may be readily carried out. However, if several characteristics or levels are con
sidered and there are not many more potential controls than cases, matching can
be difficult. It is quite likely that for some cases, no control will be found; indeed,
it may be necessary to either eliminate some of the characteristics from consid
eration or reduce the number of levels for some of them. With age matching, for
example, it is often unlikely that pairs can be formed using one-year age intervals,
but five- or ten-year age groups may make matching feasible.
The number of characteristics or levels for which matching is desirable and
practical is actually rather small. It is usually sensible to match cases and controls
only for characteristics such as age and gender whose association with the disease
Selection Bias
A method commonly used in conducting case-control studies is to select the cases
of the disease under study from one or more hospitals. The control groups usually
consist of patients admitted to the same hospital, with diseases other than the one
under study. This is a popular method for the initial studies that explore a sus
pected relation because the data can generally be obtained quickly, easily, and
inexpensively. But several assumptions and sources of bias must be considered
in analyzing the findings from such studies.
Selection bias is one of the major methodological problems encountered
when hospital patients are used in case-control studies. W. A. Guy (see Chapter
2) was the first to suggest that a spurious association between diseases or between
a characteristic and a disease could arise because of the different probabilities of
admission to a hospital for those with the disease, without the disease, and with
the characteristic of interest (Guy. 1856). This possibility was then demonstrated
mathematically by Berkson (1946).
The influence of these differences on the study group in the hospital can be
illustrated with a hypothetical example.
Let X = Etiological factor or characteristic
A = Disease group designated as cases
B
Disease group designated as controls
Assume that there is no real association between disease A and X in the group
population, as indicated in Table 11-5; that is, the percentage of those with A
who have X and the percentage of those with B who have X is equal. Assume
also that there are different rates or probabilities of admission to the hospital for
persons with X, A. and B, each of which acts independently, as follows: X = 50
i
x_'232
Epidemiologic Studies
Case-Control Studies
Table 11-5. Frequency of Characteristic X in Disease
Groups A and B in the General Population
Table 11-6. A Hypothetical Hospital Population
Based on Differential Rates of Hospital Admission
NUMBER OF INDIVIDUALS
IN DISEASE GROUPS
A
B
(CASES)
(CONTROLS)
WithX
Without X
200
800
200
800
Total
Percent of total with X
1.000
20
1.000
20
CHARACTERISTIC
NUMBER OF INDIVIDUALS
IN DISEASE GROUPS
Total admitted
(b) For those with 4 and without X:
10 percent of the 800 in this category are admitted because
they have A
(c) For those with B and X:
70 percent of the 200 in this category are admitted because
they have B
50 percent of the remaining 60 in this category with B are
admitted because they have X
Total admitted
(d) For those with B and without X:
IO percent of the 800 in this category are admitted because
they have B
A
B
(CASES)
(CONTROLS)
With X
Without X
110
80
170
560
Total
Percent of total with X
190
58
730
23
CHARACTERISTIC
percent; A = 10 percent; B = 70 percent. Now consider the actual numbers of
people in these groups who are admitted to the hospital:
(a) For those with A and X:
10 percent of the 200 in this category are admitted because
they have A
50 percent of the remaining 180 in this category are admitted
because they have X
233x->*
20
90
110
= 80
140
30
170
= 560
These numbers are then inserted into the four cells of Table 11-5, allowing
a comparison of disease A (cases) and disease B (controls) with respect to those
who do and do not have the characteristic in our hypothetically constructed hos
pital population, as shown in Table 11-6. The result is that 58 percent of those
with disease A have X as compared to 23 percent o
>se with disease B. This
indicates that an association exists between A and X, even though this association
is not present in the general population (the source of the hospital population).
This spurious association results from the different rates of admission to the hos
pital for people with the different diseases and X. However, spurious associations
such as this will not arise if either (Kraus, 1954):
1. X does not affect hospitalization, that is, no person is hospitalized simply
because of X; or
2. the rate of admission to the hospital for those persons with A is equal to
those with B.
One can never be absolutely ce;tain that the first condition is met in any
given study. For example, if X represents eye color, it might be assumed that this
would not influence the probability of hospitalization. It is possible, however, that
persons with a particular eye color belong to an ethnic group whose members are
mainly of a specific social class, which, in turn, may influence the probability of
their hospitalization. The likelihood of a spurious association is greater if the
factor under investigation (i.e., X) is another disease rather than a characteristic
or an attribute. The second condition is, of course, the exception rather than the
rule since persons with different diseases usually have different probabilities of
hospitalization. In any event, one cannot assume that these differences do not
exist unless it is demonstrated that there are no differences in the hospitalization
rates for individuals regardless of the disease.
In hospital studies, the same factors that may produce a spurious association,
also termed “Berksonian” or “selection” bias, can have the reverse effect. The
differences in hospital admission rates may conceal an association in a study and
fail to detect one that actually exists in the population.
Selection bias is not limited to the analysis of hospital patients. It may be
present in any situation or type of population where persons with different dis
eases or charactei
:s enter a study group at different rates or probabilities. For
example, in studying an autopsy series from a specified hospital population where
^34
Epidemiologic Studies
Case-Control Studies
the autopsy rates differ for the diseases and characteristics being studied in the
manner described above, the inferred associations will be biased and may result
in a spurious association or mask a real association (McMahan, 1962; Mainland,
1953; Waifeet al., 1952).
Selection biases, however, do not necessarily invalidate study findings. This
issue should be resolved on its own merits for any particular investigation, and
the following means are available to increase the likelihood that an observed
association is real:
1. The strength of the association can be evaluated to see if it could result
from the type of selection bias described above. A strong association is less likely
to result from selection bias than a weak one.
2. Depending on the disease and the personal characteristic (such as serum
cholesterol level) or the possible etiological factor (such as cigarette smoking), it
may be possible to classify the characteristic or factor into a gradient from low
to high levels. If the degree of association between the disease and the charac
teristic or factor consistently increases or decreases with increasing levels of the
characteristic or factor, this “dose-response relationship’’ reduces the likelihood
that the association is a result of selection bias. For selection bias to occur, it
would be necessary to hypothesize the very unlikely occurrence of a similar
gradient of rates of entry into the study group or of hospitalization in a study of
hospitalized patients for the characteristic and the disease. This can be illustrated
with some data from a recent study of oral contraceptive use and breast cancer
among women 45 years old and younger in England (McPherson, et al., 1987).
Information was obtained on past oral contraceptive use by women with breast
cancer in six London hospitals and two Oxford hospitals during 1980-1984. The
same information was obtained from a similarly aged control group (female
patients in these hospitals admitted for conditions not related to contraceptive
use) during this time period. Table 11-7 presents the results of a comparison of
breast cancer patients and controls according to the duration of oral contraceptive
use before the first pregnancy. Not only is there a higher proportion of oral con
traceptive users among the breast cancer patients than the controls, but the breast
cancer patients tended to use oral contraceptives for a longer time period than the
control patients. A gradient showing an increase in oral contraceptive use among
the cases compared with the controls is evident. Another illustration is provided
by Antunes and his colleagues (1979), who examined the possible relationship
between estrogen use and endometrial cancer with a case-control research design.
Their findings are shown in Figure 11-1. A gradient of duration of postmeno
pausal estrogen use and endometrial cancer is evident.
3. As a precaution against the influence of selection biases, one may draw
controls from a variety of sources. Should the frequency of the study characteristic
be similar in each control group and differ from the case group, selection bias
would not be a likely explanation for the observed association. The study of
Reye’s syndrome used controls from an emergency room, in patients, school
children, and the community and found consistent results for each group (Table
11-4). In their classic study of lung cancer and smoking Doll and Hill (1952)
demonstrated the importance of multiple control groups. They obtained infor-
15Y
14z
13-z
£
CD 12-z
cr
LU
5
9-
8Z
O
H
<
cr
6Z
CD
Q
Q
5-z
O
DURATION OF ORAL
11-z
> 10LU
Table 11-7. Duration of Oral Contraceptive Use before
First Term Pregnancy among Female Breast Cancer
Patients and Hospital Controls 45 Years Old and Younger
4-z
CONTRACEPTIVE USE
CASES(%)
CONTROLS (%)
3Z
No Use
1 Year
1-4 Years
> 4 Years
235 (67%)
Z1 (8%)
43(12%)
46(13%)
273 (78%)
26 (7%)
29 (8%)
23 (7%)
2-z
Total
351 (100%)
351 (7%)
Source: McPherson et al., 1987.
235
i4^
None
<1 year
1-5 years
>5 years
YEARS OF ESTROGEN USE
Figure 11-1. Odds ratios for endometrial cancer cases and controls according to
duration of use of postmenopausal estrogen. Source: Adapted from Antunes, et al.
(1979).
)
^236
V }
Epidemiologic Studies
mation on the smoking habits of a sample of the general population from a social
survey that was conducted in Great Britain during 1951. The smoking habits
of patients in their control group were compared with those of persons in the
social survey who were residents of Greater London, after adjusting for the
age differences between the two groups. Table 11-8 shows the distribu
tion of smoking habits among males in these two groups. The smaller propor
tion of nonsmokers and the higher proportion of heavy smokers among the
controls than in the general population may result from the fact that patients in
the control group had diseases that were also related to smoking habits. Thus,
the degree of relationship between smoking and lung cancer shown in
Table 11-8 was actually underestimated by the use of hospital controls in that
investigation.
Representativeness
When cases are drawn from death certificate data bases or centralized registries,
it is possible to select a representative sample of cases. This applies to case-control
studies of various causes of death or of cancer or other registered illnesses. When
cases are drawn from a limited, well-defined population it is also fairly easy to
identify all cases. Thus, a case-control study of diarrhea in a day-care center can
be designed to interview the parents of every child in the day-care center, or even
to examine every child.
Many times it is not easy to identify all the cases of a disease. Even if one
canvasses physicians, laboratories, and hospitals to find cases of an illness, there
may be people with the illness who are not being treated or who are unaware of
their condition. An example might be early miscarriage; a proportion of miscar
riages may occur in women who are not aware that they are pregnant (and thus
not aware that they miscarried), or women who have not yet been to a physician
Table 11-8. Comparison between Smoking Habits of Male Patients without Cancer of
the Lung (Control Group) and of Those Interviewed in the Social Survey: London. 1951
PERCENT SMOKING DAILY
PERCENTAGE OI-
AVERAGE OF CIGARETTES
NUMBER
SUBJECT
NONSMOKERS
1-4
5-14
15-24
25 +
INTERV1I-WED
Patient with diseases
other than lung
cancer
General population
sample (Social
Survey)
7.0
4.2
43.3
32.1
13.4
1.390
12.1
7.0
44.2
28.1
8.5
199
Source: Doll and Hill (1952).
Case-Control Studies
23’O
to begin prenatal care. There is probably no easy way to ensure obtaining a
representative sample of women having early miscarriages. Cases of miscarriage
drawn from a population of female physicians, for example, would probably select
higher educated, higher social class women who are more likely to seek prenatal
care earlier in pregnancy. In a study of life style and miscarriages this might
introduce a bias, especially if the controls were selected from the general popu
lation.
Bias in Obtaining Information
Another bias that may distort the findings from case-control studies develops from
the interviewer’s awareness of the identity of cases and controls. This knowledge
may influence the structure of the questions and the interviewer's manner, which
in turn may influence the response. Whenever possible, interviews should be
conducted without prior knowledge of the identify of cases and controls, although
administrative constraints often prevent such “blind" interviews. In special cir
cumstances, hospital patients may be interviewed at the time of admission so that
information of epidemiologic interest is obtained before the patient is seen by a
physician and thus before a diagnosis is made establishing the identity of cases
and controls. This requires a comprehensive, general-purpose interview routinely
administered to all patients admitted. Several epidemiologic studies have utilized
a unique set of data from the Roswell Park Memorial Institute, where such a
procedure is used (Bross, 1968; Bross and Tidings. 1973; Levin et al.. 1950;
Levin et al., 1955; Lilienfeld. 1956; Solomon et al.. 1968; Winkelstein et al..
1958). Comparing their results with those of studies that depend on more con
ventional sources of controls provides a means for evaluating possible interviewer
bias. A similar approach is used by the Slone Epidemiology Unit which routinely
obtains drug histories from patients entering hospitals in the Boston region and
other cities.
Patients interviewed as diagnosed cases in studies occasionally have had
their diagnoses changed later. If data obtained from the erroneously diagnosed
group resemble data from the control rather than the case series, interviewer bias
can be discounted (Table 11-9).
The association of a factor and a disease may often be restricted to a specific
histologic type or other component of the disease spectrum, as determined by
objective means. For example, the fact that oat cell pulmonary carcinoma is more
positively related to a history of exposure to bis-chloromethyl ether (BCME) than
adenocarcinoma of the lung more firmly established the relationship between the
two (Pasternak, et al., 1977). When such diagnostic details and their significance
are unknown to the interviewer, another check on possible interviewer bias is
provided.
The subjects
sponses to an interview can also be directly validated by
^..238
Epidemiologic Studies
Case-Control Studies
Table 11-9. The Smoking Habits of Patients in Different Disease Groups, 45-74
Years of Age, Standardized According to the Age Distribution of the Population of
England and Wales as of June 30, 1950
PERCENT SMOKING DAILY
DISEASE GROUP
AVERAGE OF CIGARETTES
NUMBER
INTERVIEWED
PERCENTAGE
OF NONSMOKERS
<5
5^44
15-24
25 +
0.3
5.3
4.6
9.9
55.9
35.5
35.0
37.8
24.3
11.4
1,224
102
1.9
9.9
38.3
38.7
11.2
301
4.6
5.6
9.4
9.0
47.2
44.8
26.0
26.9
12.8
13.7
473
875
40.6
66.9
13.7
16.4
22.0
12.7
9.5
4.2
14.2
0.0
90
45
66.5
22.4
0.0
11.1
0.0
25
68.4
55.9
14.3
22.1
11.0
5.0
3.6
1.2
0.9
294
157
Males
Cancer of lung
Patients incorrectly
thought to have
cancer of lung
Other respiratory
diseases
Other cancers
Other diseases
Females
Cancer of lung
Patients incorrectly
thought to have
cancer of lung
Other respiratory
diseases
Other cancers
Other diseases
17.5
Source: Doll and Hill (1952).
comparison with other records. This was shown in a study of the accuracy of
recall of the history of contraceptive use. Case-control studies of the relation
between oral contraceptive use and a variety of diseases assumed that women
recalled their use of oral contraceptives with reasonable accuracy (Collaborative
Group for the Study of Stroke in Young Women, 1973; Mann et al., 1975;
Thomas, 1972; Vessey and Doll, 1968). This assumption was tested by comparing
oral contraceptive histories of seventy-five women attending family planning clin
ics with information available in the clinic records. It was found that the type of
information obtained in the case-control studies was likely to be remembered
with reasonable accuracy (Glass et al., 1974). This finding has been confirmed
by Stolley et al. (1978).
Most investigators take great pains to prevent bias by rigorously training
study interviewers in proper interview methods. Moreover, it is possible to check
the interviewers’ technique by video-taping the interview or reinterviewing a
sample of the subjects to detect information bias at an early stage of a study when
corrective measures are possible.
239-
ANALYZING CASE-CONTROL STUDIES
We described the odds ratio in the beginning of this chapter. The comparison of
exposure among cases and controls and the calculation of the odds ratio are the
unique features in analyzing data from case-control studies. Odds ratios can be
calculated for different amounts of exposure, or for subgroups stratified by other
risk factors. Analysis of matched pairs is a special case when each pair is a
separate strata. Multivariate methods can be used to estimate the effect of several
variables on the odds ratio, and one can consider each variable while controlling
for the others.
Odds Ratio for Multiple Levels of Exposure
Inferences about the association between a disease and a factor are considerably
strengthened if information is available to support a gradient between the degree
of exposure (or “dose”) to a characteristic and the disease in question. Odds
ratios can be computed for each dose of the characteristic. The general approach
is to treat the data as a series of 2 X 2 tables, comparing controls and cases at
different levels of exposure, and then calculating the risk at each level. The data
from Table 11-7 are presented in Table 11-10, together with the computed odds
ratios. The users with different durations of oral contraceptive use are compared
with the nonusers, whose risk of breast cancer is set at 1.0. The odds ratios (OR)
for users relative to nonusers are:
OR (^1 year’s use) =
27 X 273
26 X 235
7,371
= 1.2
6,110
OR (1-4 years’ use) =
43 X 273
29 X 235
11,739
6,815
OR (>4 years’ use) =
46 X 273
23 X 235
12,558
1.7
5,405
It is possible to employ statistical tests of significance to determine whether or
not the obtained relative risks differ from “unity” or 1.0. These tests can be
applied to the summary relative risk (Cochran’s test) or to all the categories (the
Mantel-Haenzel test) (Cochran, 1954; Mantel and Haenszel, 1959) (see Appen
dix).
240
Epidemiologic Studies
Case-Control Studies
Table 11-10. Relative Risk of Breast Cancer for Smokers and Nonsmokers, by
Duration of Oral Contraceptive Use (Data from Table 11-7)
DURATION OF ORAL
CONTRACEPTIVE USE
BREAST
HOSPITAL
ODDS RATIO
CANCER CASES
CONTROLS
(ESTIMATED RELATIVE RISK)
235
27
273
1.0
26
29
23
1.2
1.7
2.3
No use
< 1 Year
1-4 Years
> 4 Years
43
46
241
Table 11-12. Matched Pair Analysis of a Case-Control Study of the Association
between Chlamydia trachomatis and Ectopic Pregnancy
___ ___________ CONTROLS
PAST EXPOSURE TO
NO EXPOSURE TO
C. TRACHOMATIS
C. TRACHOMATIS
Past exposure to C. trachomatis
72
109
No exposure to C. trachomatis
36
40
Cases
Source: McPherson el al., 1987.
Source: Chow, 1990, personal communication.
Matched Cases and Controls
her colleagues recruited the cases of ectopic pregnancies from admissions and
the controls from prenatal clinics. The case-control pairs were matched for age
(± 1 year), ethnicity, hospital, and restricted to women whose pregnancy was of
12 to 24 weeks duration. Cases with previous bilateral tubal ligation, ectopic
pregnancy, or an intrauterine device present at the time of conception were
excluded from the study. A total of 257 matched case-control pairs were assem
bled and each pair was categorized as to past exposure to Chlamydia trachomatis
(assessed by antibody titer of > 1:64). Based on Table 11-11, each pair could be
categorized in one of four ways:
When cases and controls are matched in pairs in order to make the two groups
comparable with regard to one or more factors, the fourfold (2 X 2) table takes
a form different from that shown in Table 11-1. The status of the cases with
regard to the presence or absence of the characteristic is compared with its pres
ence or absence in their respective controls (Table 11-11). The cell in the upper
left-hand comer of Table 11-11 contains r number of pairs in which both cases
and controls possess the characteristic of interest. The marginal totals (a, b, c, d)
represent the entries in the cells of Table 11-11 and the total for the entire table
is VzN pairs where N represents the total number of paired individuals. The cal
culation of the odds ratio for this table is simple (Kraus, 1958): OR = s/l (provided
t is not 0). Both a test of significance and a method of calculating the standard
error are presented in the Appendix.
An example of the method of analysis for matched pairs in a case-control
study comes from the work of Chow et al. (1990) on the relation between past
exposure to Chlamydia trachomatis and ectopic pregnancy. Prior Chlamydia tra
chomatis infection had been associated with both tubal infertility and pelvic
inflammatory disease, conditions associated with ectopic pregnancy. Chow and
Table 11-11. Symbolic Representation of Matched Cases and
Controls with and without the Exposure of Interest
_________ CONTROLS__________
Exposed
Unexposed
Total
EXPOSED
UNEXPOSED
TOTAL
r
t
b*
s
a*
c*
72 N
u
d*
*a. b. c. and d correspond to (he cells of Table 11-1.
r. Case exposed and control exposed (+ +) = 72
s. Case exposed and control not exposed (+-) = 109
t. Case not exposed and control exposed (— +) = 36
u. Case not exposed and control not exposed (—) = 40
Group 5 is the group where cases were exposed and controls were not (+-);
group t is the group where cases were not exposed, but controls were exposed
(- + ). As in the above formula, the odds ratio is estimated as s/t or 109/36 =
3.0 (see Table 11-12). The calculation considers only the discordant pairs, and
this can be explained intuitively: One can see that pairs where both were exposed
or where both were unexposed would give no information about the relationship
of exposure to disease. For example, one could not measure the effect of fluoride
on cavities in a group of pairs that had all received fluoride, or that had all been
unexposed to fluoride (Schlesselman, 1982).
Interrelationships between Risk Factors
Odds ratios can also be used to determine whether interrelationships exist between
various characteristic • risk factors. A case-control study of lung cancer, ciga
rette smoking, and asL^..tos exposure among workers in southern Norway exposed
242
J
Epidemiologic Studies
to multiple risk factors provides an example of this (Kjuus et al. 1986). In two
neighboring counties in the southern part of Norway, all cases of lung cancer in
males during 1979-1983 were ascertained. For each case, a similarly aged control
was selected from among the patients in the same geographical area as the case.
All men with conditions that would have precluded possible employment in heavy
industry were excluded from the study. The 176 cases and 176 controls were
interviewed about their history of exposure to asbestos and their smoking habits.
The histories were then coded into four categories according to the level of asbes
tos exposure the person had reported (no exposure, light or sporadic exposure,
moderate exposure between 1 and 10 years duration or heavy exposure less than
1 year in duration, and more than 10 years of moderate exposure or more than 1
year of heavy exposure). The relative risks for each category of asbestos exposure
and smoking habit are shown in Table 11-13. From these data, it appears that
the relative risk increases with an increase in either smoking or asbestos exposure.
When the factors are considered together, the odds ratio rises sharply. This
suggests that these factors modify and increase each other’s effect on the
disease.
Effect of Misclassification
Misclassification of both disease and exposure can occur in any type of study. In
a case-control study, misclassification of disease would lead to some of the selec
tion biases already discussed; it would alter a person’s probability of entering the
study. Assuming that selection bias has been dealt with, misclassification of expo
sure must be addressed in a case-control study. Exposure status usually cannot
be measured directly by the researcher in such a study. Instead, the researcher
relies on records (e.g., employment records describing work assignments and
possible occupational exposures), recall (e.g. employment, residential, smoking,
pharmaceutical histories), or even the recall of a close friend or relative, usually
a spouse (e.g. diet, smoking, alcohol consumption, exercise). There are two types
of misclassification that can occur: (1) differential—where the amount or direction
of misclassification is different in the cases and controls, and (2) nondifferential—
where the amount and direction of misclassification is the same in cases and
controls. Misclassification error can occur in one direction for cases and controls;
for example, everyone may underreport their own or their spouse’s habitual alco
hol consumption. Misclassification can occur in opposite directions; spouses of
cirrhosis patients might overreport alcohol consumption, while spouses of other
patients might continue to underreport alcohol use. People typically may misre
port their abortion histories, smoking histories, number of sexual partners, and
income, and this may be all in one direction or not. People may also misreport
information because they can’t remember their typical breakfast 10 years ago, the
number of cigarettes their husbands used to smoke, the length of their menstrual
Case-Control Studies
243
Table 11—13. Odds Ratio Estimates of the Relative Risks of Lung Cancer for
Combined Exposure to Asbestos and Smoking
CIGARETTES
SMOKED DAILY
0-4
5-9
10-19
20-29
>30
ASBESTOS EXPOSURE
NONE
LITTLE
MODERATE
HEAVY
1.0
1.2
1.2
1.9
19.8
108.4
2.7
7.8
24.6
44.6
243.8
4.1
11.9
2.9
9.1
16.5
90.3
37.3
67.7
370.2
Source: adapted from Kjuus et al. (1986).
cycle during each decade of life, or how many hours a day (hey were exposed to
silica dust during each year of employment.
Differential misclassification (because the exposure status of cases is more
or less likely to be miscategorized than that of the controls) can produce bias in
either direction, raising or lowering the estimate of risk (Schlesselman. 1982).
Nondifferential misclassification (randomly distributed among cases and controls)
generally shifts the odds ratio toward the null hypothesis (OR = 1.0). but excep
tions to this can occur (Dosemeci et al., 1990). The effect of misclassification
may also depend on how exposure is defined, as a continuous or categorical
variable, and if categorical, as a two-level or multilevel variable.
These effects of misclassification emphasize the need to verify the infor
mation obtained in a study by every feasible means. Information with respect to
previous exposures or characteristics of study individuals may be verified by
obtaining records from independent sources (such as hospitals, physicians,
schools, military services, and employment records) on either all or a sample of
individuals in the study. Disease diagnoses should be verified whenever possible
by independent review of medical records, histological slides, electrocardiograms,
etc. The degree of verification possible depends upon the factors or characteristics
and the diseases being studied. For example, verification of alcohol consumption
or of the content of an individual’s diet over a period of time poses serious
problems of verification. Alternatively, in a health maintenance organization, for
instance, records of prior illness or drug prescriptions may be available, elimi
nating the possibility of misclassification. Another approach is to use antibody
titers as an index of past exposure to an infectious agent. This method has been
used in case-control studies of hepatitis B infection and primary' liver cancer
(Szmuness, 1978). Recently, biological markers for some other exposures have
been developed. For example, the presence of cotinine. a metabolite of nicotine,
in the blood, urine, or saliva can serve as a biomarker of exposure to cigarette
smoking; a high level would indicate active smoking, and a low level, exposure
to environmental tobacco smoke.
244
Epidemiologic Studies
Case-Control Studies
Attributable Fraction
Another measure of association, influenced by the frequency of a characteristic
in the population, is the attributable fraction. As noted in Chapter 10, this is the
proportion of a disease that can be attributed to an etiological factor; alternatively,
it is considered the proportional decrease in the incidence of a disease if the entire
population were no longer exposed to the suspected etiological agent. As in cohort
studies, the attributable fraction may be estimated in case-control studies as fol
lows:
Attributable Fraction (AF) =
P(OR - 1)
X 100%,
P(OR - 1) + 1
where OR = the odds ratio and P = proportion of the total population classified
as having the characteristic. The derivation of this formula can be found in the
Appendix. Standard errors and confidence limits have been derived for the attrib
utable fraction by Walter (1975, 1978) (see Appendix).
Computations of attributable fraction are also helpful in developing strate
gies for epidemiologic research, particularly if there are multiple etiological fac
tors (Walter, 1975). In the study of past Chlamydia trachomatis infection and
ectopic pregnancy, forexample, the attributable fraction for past chlamydial infec
tion was 47 percent, while that for douching (an independent risk factor) was 45
percent (Chow et al., 1990). These data suggest the need for further investigation
of douching practices in relation to ectopic pregnancy occurrence, while under
scoring the need for control of chlamydial infections to prevent ectopic pregnan
cies.
Regression Models and Adjustment for Confounding Variables
In a case-control study, several variables may be studied as potential risk factors,
variables thought to influence the outcome (occurrence of disease). As will be
discussed in Chapter 12, it is always possible that these variables may be con
founded with one another. For example, in a case-control study of lung cancer,
exposures of interest may include cigarette smoking, exposure to asbestos, and
use of alcohol. Which of these exposures are associated with lung cancer and
which are not (but are associated with one another)? The epidemiologist can deal
with this problem by using multivariate analysis, a set of techniques for studying
the effects of several factors simultaneously (Kleinbaum et al., 1982). These tech
niques range from simple cross-classification and adjustment to more complex
methods of statistical regression analysis.
Various models have been used by epidemio)
ts, such as “multiple logis
tic.” “log-linear,” “multiple linear,” and “sim^ linear” regression. These
245 ,
techniques permit the investigator to determine which of the variables has an
independent association with the outcome, to determine which variables interact
among themselves, and to quantify the relative contribution of each variable or
combination of variables to the risk of the disease. Multivariate analysis does not
necessarily distinguish causal from noncausal associations, but it may give indi
cations about the relative strengths of the independent and joint effects of multiple
exposures.
ADVANTAGES AND DISADVANTAGES OF CASE-CONTROL
STUDIES
Advantages
The case-control study can be used to test hypotheses concerned with the long
term effects of an exposure on a disease, and the study can often be completed
quickly. For example, in one to two years data can be collected about 20 or 30
years of exposure to an environmental or occupational hazard.
The case-control study can also be used to test hypotheses about rare diseases
or diseases that have long latency periods. The first case-control study estimating
the association between diethylstilbestrol (DES) and adenocarcinoma of the
vagina in young women used only 8 cases and 32 controls (Herbst et al., 1971).
The disease was very rare (about 10 cases in 10 million young women) and 15
to 20 years elapsed between exposure and disease, but the case-control study
identified the risk factor and estimated the relative risk. In Table 11-14 one may
see how the rareness of disease influences the number of subjects needed in cohort
or case-control studies and the advantage of a case-control study for studying rare
conditions.
The case-control study is well suited to the study of adverse effects of a drug
or treatment, or of a new disease where efficient identification of a risk factor can
lead to prompt public health intervention.
The case-control study can be relatively inexpensive because it may use
fewer study subjects and take a shorter period of time than some other designs.
It also allows examination of several risk factors for a single disease.
Disadvantages
It is sometimes difficult to find an appropriate control group, for theoretical or
practical reasons. For example, what is the appropriate control group for auto
accident victims? What is the appropriate control group for tennis players with a
particular injury? V' ’’ there be enough subjects available for a control group?
It is sometime., difficult to decide if the exposure preceded the disease. In
r
Epidemiologic Studies
-- 246
Case-Control Studies
Table 11-14. Sample Size Requirements for Cohort and Case-Control Studies*
SAMPLE SIZE NEEDED IN
EACH GROUP
FREQUENCY
IN UNEXPOSED
OF ATTRIBUTE
DETECTABLE IN
GROUP
POPULATION (%)
DISEASE INCIDENCE
1/1,000
50
1/100
50
1/10
50
RELATIVE
RISK
COHORT
STUDY
CASE-CONTROL
STUDY
1.2
2.0
4.0
576,732
31.443
5,815
2,535
177
48
1.2
57 J 00
2.535
2.0
4.0
3,100
567
177
48
1.2
2.0
4.0
5,137
266
42
2.535
177
48
’Power = 90%; alpha = 5%.
Source: Kahn and Sempos (1989).
studying diarrhea among breast-fed or formula-fed babies, one would want to
know if diarrhea led to cessation of breast feeding, or if cessation of breast feeding
led to an episode of diarrhea. Similarly, in a study of heart disease among letter
carriers, one would like to know whether healthy people choose to become letter
carriers or whether letter carrying (and walking each day) leads to healthier car
diovascular systems.
Case-control studies are subject to a number of biases, especially survival
biases, selection biases, recall biases, and misclassification. Well-designed studies
can sometimes minimize the introduction of biases, but the potential for biases
must be considered for each study question. Case-control studies frequently rely
on information collected from living cases of the disease of interest. If the
deceased cases are different from the surviving cases, a bias may be introduced
into the study.
Case-control studies do not actually measure incidence of disease in the
population at risk, although estimates can sometimes be made (when all cases of
the disease are known, and the population at risk is known).
247
(controls). The proportion of those exposed among the cases is compared with
that among the controls. If these proportions are different, then an association
exists between the factor and the disease. Cases can be ascertained from hospitals,
clinics, disease registries, or during a prevalence or incidence survey in a popu
lation. Controls can likewise be sampled from hospitals, clinics, or a random
sample of the population. Care must be exercised in the case and control selection
methods, because selection biases can lead to spurious associations. An alternative
approach to control selection is to match each control to each case, based on
factors thought to be related to the exposure of interest and the disease. In the
process of matching, the investigator loses representativeness, i.e., the ability to
generalize the findings to the general population, but gains greater comparability
among the cases and controls. Unbiased collection of data from both cases and
controls is necessary. Biases can occur in recalling past exposures.
The measure of the strength of an association in a case-control study is the
odds ratio estimate of the relative risk of developing the disease for those who
have been exposed compared with that for those not exposed. Odds ratios can be
calculated for both matched and unmatched designs. Misclassification of either
the presence or absence of disease, or of exposure status, can affect the estimate
of the relative risk. Confounding factors can also affect the estimate of the relative
risk. Techniques such as the Mantel-Haenszel test and logistic regression can be
used to adjust for confounding factors in the data analysis. However, such statis
tical techniques cannot make up for errors in study design or data collection.
Another measure of association is the attributable fraction, which measures
the proportion of disease occurrence that is associated with the factor of
interest.
Case-control studies have many advantages and disadvantages compared
with cohort studies (Table 11-15). Among the advantages are their lower costs,
shorter time to completion, and the ability to examine the association of many
Table 11-15. Advantages and Disadvantages of Case-Control Studies
Advantages
1. Generally a short study period.
2. One may study rare diseases.
3. Inexpensive.
4. One may study several risk factors for a single disease.
5. Useful for studying adverse drug reactions or new diseases.
SUMMARY
Disadvantages
In a case-control study, the investigator compares the history of past exposure to
a factor or presence of a characteristic among those persons with a given disease
or condition (cases) and among those who do not have the disease or condition
1. Sometimes difficult to choose appropriate control.
2. Sometimes difficult to determine if exposure preceded the disease.
3. Prone to biases in selection and information.
4. One is usually unable to calculate incidence rates.
' 248
Case-Control Studies
Epidemiologic Studies
factors with a given disease. Among their disadvantages are the potential for bias
in case and control selection, the potential for recall bias during data collection,
and the possible bias associated with investigating survivors of a disease.
STUDY PROBLEMS
1. What would be an appropriate control group (or groups) for the following
conditions (mention possible exclusions):
(a) Babies bom at very low birth weight (<1500 grams).
(b) Infants with chronic ear infections.
(c) Transplant patients who reject a transplant.
(d) Russian roulette suicide victims.
2. Marzuk et al. (1992) conducted a case-control study of cocaine and alco
hol use as risk factors for suicide by Russian roulette. The controls were
handgun suicides. Toxicological analyses were performed and the data
below were obtained. The authors did not calculate an odds ratio, but you
can. Calculate the odds ratios and write one sentence for each odds ratio
explaining its meaning.
(a)
DRUGS OR
ALCOHOL
NO DRUGS
PRI-SENT
OR ALCOHOL
IN BLOOD
IN BLOOD
TOTAL
1I
Russian roulette suicide victims
Handgun suicide victims
33
3
21
14
54
Total
44
24
68
COCAINE
DETECTED
NO COCAINE
DETECTED
IN BLOOD
IN BLOOD
TOTAL
Russian roulette suicide victims
Handgun suicide victims
9
19
5
35
14
54
Total
28
40
68
(b)
3. Name an advantage and a disadvantage of using a case-control study
design to test the hypothesis that cocaine us^ ’"'creases the probability of
death from Russian roulette.
249'
4. The recent controversy over silicone breast implants began with the
observation of breast cancer among women with the implants.
(a) What is the advantage in using a case-control study to test the hypoth
esis that silicone breast implants are associated with breast cancer?
(b) Who should be the cases in such a study?
(c) What groups would make appropriate controls?
(d) What variables might one use to select the control group?
(e) What variables might be useful in group or pair matching?
(f) What would be the problem in choosing many variables for match
ing?
(g) How could one collect information about women’s silicone breast
implants?
(h) What problems arise in collecting the women’s medical histories?
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i.
THE LANCET
COMMENTARY
Third-generation oral contraceptives:
how risky?
-J
See pages 1569, 1575, 1582, 1589, 1593
The risk of venous thromboembolic disease in a woman
who is taking oral contraceptives (OCs) exceeds that of
other women.' In view of the results reported in this issue
by the World Health Organization (WHO), Jick et al, and
Bloemenkamp et al, can we now conclude that women
who are taking a “third generation” OC—ie, one that
contains, as its progestagen component, either desogestrel
or gestodene—are at particularly high risk? We must look
to such non-randomised epidemiological studies for an
answer because (a) differences among OCs in their
influence on coagulation variables are generally modest,
and may or may not be relevant clinically; and (6) it is not
feasible to conduct randomised trials of sufficient size to
examine the possibility of an adverse effect that may occur
in only a tiny fraction of OC users.
The latest results provide reasonably strong evidence
that users of third-generation OCs have a higher risk of
venous thromboembolic disease than do users of other
OCs, and further suggest that the newer OCs are in fact
responsible. Each study was large, and each came to the
same conclusion: that there was approximately a two-fold
difference in risk between current users of thirdgeneration OCs and other OCs. The increases in risk
were similar for desogestrel and gestodene. The
association persisted after adjustment for several risk
factors for venous thromboembolism that might have
influenced the choice of preparation—eg, age, weight,
smoking, parity, and varicose veins. The hypothesis of a
causal relation receives modest support from the
previously
documented
influence
of hormonal
composition of OCs on a woman’s risk of vascular
disease. Increases in both the oestrogenic and
progestagenic potency of OCs are associated with an
increased risk of arterial disease,2,5 and the risk of venous
thromboembolism probably rises with increasing
oestrogen dose.2-6 However, while the work on
thromboembolism in relation to progestagen potency of
earlier OCs has not been extensive, it does not point to an
association.16
Are there some users of third-generation OCs whose
risk of venous thromboembolic disease is unusually high,
relative to their risk if they were taking a different OC?
The WHO data suggest that the added risk to a woman
taking a third-generation OC is roughly the same
irrespective of body mass index. Bloemenkamp et al show
that the magnitude of the added risk is not influenced
by family history of venous thrombosis, but may be
especially large in women who have never been pregnant
or who are carriers of the factor V Leiden mutation.
Is the evidence of an increased risk of venous
thromboembolism in users of third-generation OCs
strong enough for health professionals to recommend that
women discontinue or not start taking such a preparation
and use another OC instead? A recommendation of this
sort must take into account the size of both risks and
benefits related to different types of OCs. The increased
risk of venous thromboembolic disease attributable to use
of a third-generation OC, beyond the risk associated with
use of an earlier OC, seems to be about 10-15 per
100 000 woman-years of use. If the typical case-fatality
1570
was about 1%, the increased rate of fatal venous
thromboembolism would be 1-1*5 per million womanyears. Unfortunately, we know very little about the risks
and benefits of any serious health outcome other than
venous thromboembolic disease. The data of Jick et al
provide some reassurance that mortality from vascular
disease as a whole among current users of thirdgeneration OCs, about half of which is due to arterial
disease, does not differ from that of users of other OCs.
However, only very substantial differences in risk would
have been detected in that study. Possible differences in
the incidence of myocardial infarction or diabetes
mellitus—differences that could well be present and
favour users of third-generation OCs, if metabolic
responses are any guide8—have not been examined.
In practical terms, what do women and their health
advisers need to know? Certainly women who have been
or who are considering using third-generation OCs need
to be aware of the probable increased risk of venous
thromboembolic disease. However (and putting aside
issues such as menstrual cycle control), the actual
decision comes down to weighing an increase in this risk,
one that would cause about one death in one million
users each year, against a possible decrease in the risk of
other serious conditions. Until (i) we know more about
the relation of incidence and mortality of other important
health outcomes between users of third-generation and
earlier OCs; or (ii) a subgroup of women can be identified
who are at very much higher risk of venous
thromboembolic disease with third-generation OCs than
with earlier OCs, women will not have a sound basis for
making a decision.
Noel Weiss
Department of Epidemiology, University of Washington.
Seattle. WA. USA
1
2
3
4
5
6
7
8
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Speroff L, DeChemey A, and the Advisory Board for the New
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Waiting for coronary artery bypass surgery:
abusive, appropriate, or acceptable?
See page 1605
Waiting for the doctor is as old as the profession itself. In
ancient days long waiting times were the signboard of a
wise and skilful doctor or signified the presence of
Vol 346 • December 16, 1995
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