This document provides an overview of case control studies in epidemiology. It defines a case control study as a retrospective study that compares cases (people with a disease or condition) to controls (people without the disease or condition) to determine risk factors for the disease. The key steps outlined are: selection of cases and controls from the same study base; matching cases and controls on important characteristics; measuring exposure to suspected risk factors in the same way for both groups; and analyzing the data to compare exposure rates between cases and controls and estimate disease risk associated with exposure. Advantages are that case control studies are efficient for rare diseases, but limitations include potential for selection and recall bias.

2. CASE CONTROL STUDY
Presented by : Dr. Radhika Maniyar
Post Graduate student Public Health Dentistry
M. R. Ambedkar Dental College

3. Contents :
• Introduction
• Aims of epidemiology
• Epidemiologic methods
• Definition of case control study
• Framework of the study
• Basic steps of the study
• The three principles
• Selection of cases & controls
• Control sampling strategies
• Matching
• Measurement of exposure
• Analysis
• Variants of case control study
• Bias in case control study
• Advantages & disadvantages

4. INTRODUCTION
• Epidemiology is the basic science of preventive &
social medicine.
• It has evolved rapidly during the past few decades.
• Its ramifications cover not only study of disease
distribution & causation (thereby prevention), but
also health and health- related events occuring in
human population.

5. • Epidemiology is derived from the word epidemic, epi
= among; demos = people; logos = study.
• The study of distribution and determinants of the
health related events in specified population and
application of this study to control of health problems
(by John M. Last)
• A science concerned with the study of factors
influencing the occurrence and distribution of disease
defect disability or death in a group of individuals. (by
Clarke EG)

6. AIMS OF EPIDEMIOLOGY
• To describe the distribution and magnitude of health
and disease problems in human population
• To identify the etiological factors In the pathogenesis.
• To provide data essential to the planning,
implementation and evaluation of services for
prevention, control and treatment of diseases, and to
the setting up of priorities among those services

7. EPIDEMIOLOGIC METHODS

8. DESCRIPTIVE EPIDEMIOLOGY
• Usually the first phase of an epidemiologic
investigation.
• Concerned with observing the distribution of disease
or health- related characteristics in human
populations & identifying the characteristics with
which the disease in question seems to be associated.
• Describing the disease by time, place & person.

9. ANALYTICAL EPIDEMIOLOGY
• Second major type of epidemiological studies.
• The object is to test the hypothesis.
• One can determine : whether or not a statistical
association exists between a disease & a suspected
factor and if exists, the strength of association.
 Case control study
 Cohort study

11. CASE CONTROL STUDY

12. • Also called as “retrospective study”.
• It is a common first approach to test causal
hypothesis.
• It possesses three distinct features:
1. Both exposure and outcome (disease) have occurred
before the start of the study.
2. The study proceeds backwards from effect to cause.
3. It uses a control or comparison group to support or
refute an inference.

13. DEFINITION
• The observational epidemiologic study of persons with
the disease of interest and a suitable control group of
persons without the disease. The relationship of an
attribute to the disease is examined by comparing the
diseased and non-diseased with regard to how
frequently the attribute is present.
• John M. Last, Dictionary of Epidemiology

16. • It involves two populations- cases and controls.
• Unit is the individual rather than the group.
• The focus is on the disease or some other health
problem that has already developed.
• They are commonly referred to as “comparison
studies.”

17. FRAMEWORK OF THE STUDY
Suspected or risk
factors
Case
(disease present)
Control
(disease absent)
present a b
absent c d
a + c b + d

18. BASIC STEPS IN THE STUDY
SELECTION OF
CASES &
CONTROLS
MATCHING
MEASUREME
NT OF
EXPOSURE
ANALYSIS &
INTERPRETA
TION

19. THREE PRINCIPLES :
• The three principles in case control designs:
1. The study base principle
2. The deconfounding principle
3. The comparable accuracy principle

20. The concept of the “study base”
• Definitions of the “study base” concept (first introduced by Olli
Miettinen)
• The aggregate of total population-time in which cases occur
• The members of the underlying cohort or source population**
(from which the cases are drawn) during the time period when
cases are identified
• **The source population may be defined directly, as a matter of
defining its membership criteria; or the definition may be
indirect, as the catchment population of a defined way of
identifying cases of the illness. [Source: Miettinen OS, 2007]

21. The study base principle
• The study base principle goal is to sample controls
from the study base in which the cases arose
• Controls serve as the proxy for the complete study
base
• Controls should be representative of the person-time
distribution of exposure (exposure prevalence) in the
study base (i.e. be representative of the study base)
• Controls should be selected independent of the
exposure.

22. Types of study base: primary
Primary study base :
• The base is defined by the population experience
that the investigator wishes to target
• The cases are subjects within the base who develop
disease
• Generally implies that all cases are identifiable
(although not all are necessarily used)

23. Types of study base: secondary
• Secondary study base :
• Cases are defined before the study base is identified
• The study base then is defined as the source of the
cases; controls are people who would have been
recognized as cases if they had developed disease

24. The deconfounding principle
• The study base principle guides the selection of who can be
entered into the study
• The deconfounding principle deals with the problems
created when the exposure of interest is associated with
other possible risk factors. These other risk factors are
unmeasured since measured confounders could be handled
in the analysis.
• Confounders in one study base may not necessarily be
confounders in another study base
• Confounding by a factor is (theoretically) eliminated by
eliminating variability in that factor.
• For example, if gender is a possible confounder, selecting
only men or only women completely eliminates the
variability of gender.

25. The comparable accuracy
principle
• Comparable accuracy principle : The accuracy of the
measurement of the exposure of interest in the cases
should be the same as that in the controls
• Example: in a study of the effect of smoking on lung
cancer it would not be appropriate to measure smoking
with urine nicotine levels in the cases and with
questionnaires in the controls
• Example: in a study of a fatal disease, it is suspect to
measure an exposure by questioning the relatives of
diseased cases but questioning the actual controls
• Bias caused by differential errors in the measurement of
cases and controls should be eliminated (e.g. use the same
measurement tools in the same way for cases and controls).

26. • Summary
• If the principles of study base comparability,
deconfounding, and comparable accuracy are followed,
then any effect detected in a study should (hopefully!)
not be due to:
• Differences in the ways cases and controls are selected
from the base (selection bias)
• Distortion of the true effect by unmeasured confounders
(confounding bias)
• Differences in the accuracy of the information from
cases and controls (information bias)

27. SELECTION OF CASES & CONTROLS
1. Selection of cases: it involves defining the case and
determining the source of cases.
• DIAGNOSTIC CRITERIA : As the cause and effect
has already occurred, the proper diagnosis of the
disease under investigation is necessary in the
selection of a case. Once the diagnostic criteria is
established, it should not be changed or altered till the
end of the investigation.

28. • ELIGIBILITY CRITERIA-
Also, the eligibility of the case precludes that the
diagnosed disease should be fresh (new) within a
specified period of time.
• Old or advanced stages of the disease should not be
used (prevalent cases).
• Incident cases are preferable to prevalent cases for
reducing (a) recall bias and (b) over-representation of
cases of long duration

29. Source of the cases
Comes from two sites: hospitals and general population.
• Hospitals provide a convenient way to categorize the
population and the sample can be drawn.
• In general population, all the cases of the study
disease have to be necessarily within the same
geographic area. The entire population or a sample
can be drawn from it.

30. 2. Selection of controls:
• Controls should be selected from the same population
-the source population (i.e. study base) -that gives rise
to the study cases. If this rule cannot be followed,
there needs to be solid evidence that the population
supplying controls has an exposure distribution
identical to that of the population that is the source of
cases, which is a very stringent demand that is rarely
demonstrable.
• Controls should be selected independently of their
exposure status, in that the sampling rate for controls
should not vary with exposure.

31. Control sampling strategies
• Cumulative sampling (i.e. traditional case-control design):
from those who do not develop the outcome until the end of
the study period (i.e. from the “survivors” or prevalent
cases)
• Case-cohort design(case-base; case-referent) sampling:
from the entire cohort at baseline (start of the follow-up
period; when cohort is established)
• Incidence density case control design (risk-set sampling):
throughout the course of the study, from individuals at risk
(“risk-set”) at the time each case is diagnosed

32. Cumulative sampling case
control study

33. Case-cohort study

34. • Selection of cases :
• Because of the cohort nature of this design, it should
be possible to include all the cases (or an appropriate
random sample of them)
• Selection of controls :
• All or random sample from among those in the
baseline cohort.
• Same set of controls can be used for several case-
control studies (for various outcomes)
• This does include some who later become cases

35. Density case control studies

36. INCIDENCE DENSITY CASE CONTROL
STUDY• Select one or more controls from disease-free (at risk)
members of the source cohort at the ‘instantaneous’
time at which each case occurs.
• The probability of control selection is proportional to
the total person-time at risk.
• Establish the source cohort and identify cases
• Determine the date on which the first case occurred
• Identify all cohort members (including cases) who
were disease free (at risk) at that date (risk set)
• Randomly select one (or more) controls from the risk
set.
• Repeat steps 1-3 for 2nd, 3rd, .... last case.

37. • Source of controls :
• Population controls
• Hospital or disease registry controls
• Controls from a medical
practice
• Friend controls
• Relative controls

38. • Population control :
• When a population roster (sampling frame) is
available, the selection of population controls is
simplest.
• Census lists
• Birth certificates
• Electoral rolls
• Some possible approaches when
no roster is available:
• Random digit dialing
• Neighborhood controls

39. • Advantages and disadvantages of population controls

40. • Neighborhood and Friend Controls.
• For the former method, a census is taken of all households in
the immediate geographic area of the case and these are
approached in a random order until a suitable control is
found.
• Care must be taken to ensure that the control was resident at
the same time the case was diagnosed. Even with these
precautions, neighborhood sampling may yield biased controls
for hospital based studies since it will not be guaranteed that
the control would have been ascertained as a case if ill, thus
violating the study-base principle (Wacholder et al. 1992b).
• Neighborhood controls are also susceptible to overmatching
due to their similarity to the cases on factors associated with
exposure that are not risk factors for disease.
• These same difficulties confront the use of friend controls,
whereby a random selection is taken from among a census of
friends provided by each case.
• The primary advantage of friend controls would be a low level
of nonresponse.

43. Relative controls

44. If cases are dead, what
about controls?
• Main argument for choosing dead controls is to enhance
comparability
• Dead people are not in the study base for cases, since death
will preclude the occurrence of any further disease
• Choosing dead controls may misrepresent the exposure
distribution in the study base if the exposure causes or
prevents death in a substantial number of people
• If live controls are used for dead cases, then proxy
respondents can be used for live controls as well

45. How Many Controls per Case?
How Many Control Groups?
• For a fixed number of study subjects, statistical power
for testing the null hypothesis is optimized by having
equal numbers of cases and controls.
• With a fixed number of cases, the proportion of the
maximum precision (unlimited controls) that is
reached is approximately: r/(r+1), where r is the ratio
of controls to cases
• If r = 4 (4:1 matching) precision is 4/(4+1) = 0.80
• > 4 controls per case of little additional statistical
value

46. • multiple control groups were recommended by Dorn
(1959) to improve the case control study so that it
would “provide a more valid basis for generalization”.
• As explained by Hill (1971) “If a whole series of
control groups, e.g., of patients with different diseases,
gives much the same answer and only the one affected
group differs, the evidence is clearly much stronger
than if the affected group differs from merely one
other group.”
• Similar informal arguments have been put forward in
favor of multiple control groups as a means of
addressing the possible biases that may be associated
with the use of any one of them (Ibrahim and Spitzer
1979).

47. MATCHING
• An important consideration is to ensure comparability
within the cases and controls. This involves the
process of “matching”.
• Matching is defined as the process by which we select
controls in such a way that they are similar to cases
with regard to certain pertinent selected variables
which are known to influence the outcome of disease
and which if not adequately matched for
comparability, could distort or confound the results.

48. • The term “confounding factor” is defined as one
which is associated with both exposure and disease,
and is distributed unequally in study and control
groups.
• More specifically, a confounding factor is one that
although associated with exposure under investigation
is itself, independently of any such association, a risk
factor for the disease.

49. • Let us suppose that we are interested in examining the
relationship between current use of oral
contraceptives and ovarian cancer.
• In this example, it is appropriate to match on age,
since age is associated with the exposure of interest
(current oral contraceptive use) and is an independent
risk factor for ovarian cancer. In other words, age is a
confounding factor.
• Failure to match, or otherwise control, for age would
result in a biased assessment of the effect of oral
contraceptive use.

50. Problems with Matching
Practical problems with
Matching :
• If matching done for too
many characteristics,
difficult or impossible to
find an appropriate
control.
Conceptual problem :
• Once matched controls to
cases according to a
given characteristic, we
cannot study that
characteristic.
• We do not match on any
variable that we may
wish to explore in our
study.

51. • Overmatching
• Overmatching refers to matching on a factor that is not a
confounder of the disease exposure association.
• The most serious type of overmatching occurs when one
matches on a factor that is both affected by exposure and a
cause of disease.
• E.g. If the effect of anti-hypertensive medication on the
risk of myocardial infarction was being investigated, for
example, yet cases and controls were matched on blood
pressure measurements taken after treatment commenced,
the data would be completely useless for estimation of
treatment effect
• Ignoring the matching in the analysis would only
compound the error by driving the odds ratio even closer
towards unity.

52. MATCHING PROCEDURES
• Matching may be of two types :
• Group matching : consists of selecting the controls in
such a manner that the proportion of controls with a
certain characteristic is identical to the proportion of
cases with the same characteristic.
• Individual matching : in this approach, for each case
selected, a control is selected who is similar to the case
in terms of the specific variables of concern.

53. MEASUREMENT OF EXPOSURE
• Information about the exposure should be obtained
from both the cases and controls in the same manner.
• This may be achieved by:
1. Interviews
2. Questionnaires
3. Studying past records like hospital or employment
records etc.

54. ANALYSIS
• This is the final step in a case control study, and it
provides:
1. Exposure rates among cases and controls to the
suspected factor and
2. Estimation of disease risk associated with exposure.

55. EXPOSURE RATES
• A case control study provides a direct estimation of
the exposure rates to a suspected factor in disease and
non disease groups.
• The significance of measuring the exposure rates lies
in estimating the probability of associating the disease
and the factor under study

56. Exposure Rates:
Cases = a/(a+c) =33/35 =94.2%
Controls =b/(b+d) =55/82= 67.0%
P<0.001 ( highly significant)
Cases
Lung Cancer
Present
Controls
Lung Cancer
Absent
Smoking
(less than 5
Cigarettes a day)
33
(a)
55
(b)
Non Smokers 2
(c)
27
(d)
35
(a+c)
82
(b+d)

57. ESTIMATION OF RISK
• The second analytical step is estimation of disease risk
associated with exposure.
• It should be noted that if the exposure rate was 94.2%
in study group, it does not mean that 94.2% of those
smoked would develop lung cancer

58. • Estimation of risk: it is obtained by an index termed
as “relative risk” or “risk ratio”, which is defined as
the probability of an event(developing a disease)
occurring in exposed people compared to the
probability of the event in non-exposed people, or the
as the ratio of the two probabilities.
• Relative risk = risk in exposed / risk in non-exposed.

59. • As obviously, the case control study does not provides
actual incidence from which relative risk can be
calculated directly, because there is no appropriate
denominator or population at risk, to calculate these
rates.
• In general, the relative risk can be exactly determined
only from a cohort study.

60. ODDS RATIO
• It is a measure of the strength of the association
between risk factor and its outcome. It is closely
related to relative risk.
• The determination of odds ratio is based on 3
assumptions:
1. The disease to be investigated must be relatively
rare or a chronic disease.
2. The cases must be representative of those with the
disease and
3. The controls must be representative of those without
the disease

61. CONCEPT OF ODDS
• Probability of winning (p) = 60%
• Probability of losing (1-p) = 40%
• Odds of winning = probability of winning / probability of
losing
= 60 / 40 = 1.5:1
Odds of an event can be defined as the ratio of the number
of ways the event can occur to the number of ways the
event cannot occur.

62. • Odds Ratio (OR)
• Compares the odds of exposure among those with
disease to the odds of exposure among those without
the disease.
• Does not compare the incidence of disease between
groups.

63. Cases (with disease) Controls (without
disease)
Exposed a b
Not exposed c d
Total a + c b + d
Proportions exposed a/a + c b/ b + d
Odds of a case being exposed = a:c or a/c
Odds of a control being exposed = b:d or b/d
Odds ratio = odds that cases were exposed
odds that controls were exposed
= ad/bc

64. • Interpretation of the Odds Ratio
• OR = 1: no association between outcome and exposure
(same odds of exposure in cases and controls = same
odds of disease in exposed vs. unexposed)
• OR >1: exposure is associated with increased risk for
outcome (greater odds of exposure in cases than controls
= greater odds of disease in exposed vs. unexposed)
Harmful Effect
• OR <1: exposure is associated with reduced risk for
outcome (lower odds of exposure in cases than controls =
lower odds of disease in exposed vs. unexposed)
Protective Effect
• Always consider the confidence interval!

66. VARIANTS OF CASE CONTROL STUDY
• Nested case control studies
• Case cohort studies
• Density case control studies
• Cumulative (“epidemic”) case control studies
• Case-only, case-specular, & case-crossover studies
• Two- stage sampling
• Case control studies with prevalent cases.

67. Nested case control
study
• It is a hybrid design in which a case control study is
nested in a cohort study.
• In this type of study, a population is identified and
followed over time.
• At the time population is identified, baseline data are
obtained from interviews, blood tests and other ways.
• The population is then followed for a period of years.
• For most of the diseases that are studied, a small
percentage of study participants manifest the disease,
whereas most do not.

68. • A case control study is then carried out using persons
in whom the disease developed(cases) and a sample of
those in whom the disease did not develop(controls).
• Advantages :
• Recall bias is eliminated.
• We know that risk factor has preceded the disease.
• economical

69. Case only study
• There are a number of situations in which cases are the
only subjects used to estimate or test hypotheses about
effects.
• E.g. it is sometimes possible to employ theoretical
considerations to construct a prior distribution of
exposure in source population & use this distribution in
place of an observed control series.
• Such situations arise naturally in genetic studies, in
which basic laws of inheritance may be combined with
certain assumptions to derive a population or parental
specific distribution of genotypes.

70. Case specular study
• A type of case only study that obtains the actual
distribution of exposure among the dwellings of the
cases & a reflected or ‘specular’ exposure distribution
which is what the exposure distribution would have
been if the dwellings had been placed on the opposite
side of the street.
• From these two distributions (i.e. the actual &
specular distribution) & including the rare disease
assumption, a relative risk estimate for the effect of
exposure can be calculated.

71. Case crossover study
• This design is useful when the risk factor/exposure is
transient.
• Each case serves as its own control, i.e the study is self
matched. For each person, there is a 'case window',
the period of time during which the person was a case,
and a 'control window', a period time associated with
not being a case.
• Risk exposure during the case window is compared to
risk exposure during the control window.

72. • Advantages of Case crossover
• Efficient – self matching
• Efficient – select only cases
• Can use multiple control windows for one case window
• Disadvantages of Case crossover
• Information bias – inaccurate recall of exposure during
control window (can be overcome by choosing control
window to occur after case window)
• Requires careful selection of time period during which the
control window occurs (circumstance associated with the
control window should be similar to circumstances
associated with case window; e.g., traffic volume)
• Requires careful selection of the length and timing of the
windows

73. BIAS IN CASE CONTROL STUDY
• The concept of bias is the lack of internal validity or
incorrect assessment of the association between an
exposure and an effect in the target population.
• Confounding bias
• Selection bias
• Information bias

74. Confounding bias
• Confounding bias: non matching of cases and controls
create this bias. It can be eliminated by careful
matching of both the groups.

75. Selection bias
• The error introduced when the study population does
not represent the target population.
• It can be introduced at any stage of a research study
design :
1. Inappropriate definition of the eligible population,
2. lack of accuracy of sampling frame,
3. Uneven diagnostic procedures in the target population
4. implementation.

76. Inappropriate definition of the
eligible population
• Ascertainment bias :
• It is produced when the kind of patients gathered does not
represent the cases originated in the population.
• Healthcare access bias:
• when the patients admitted to an institution do not represent the
cases originated in the community. This may be due: to the own
institution if admission is determined by the interest of health
personnel on certain kind of cases (popularity bias), to the
patients if they are attracted by the prestige of certain clinicians
(centripetal bias), to the healthcare organisation if it is organised
in increasing levels of complexity (primary, secondary, and
tertiary care) and ‘‘difficult’’ cases are referred to tertiary care
(referral filter bias), to a web of causes if patients by cultural,
geographical, or economic reasons show a differential degree of
access to an institution (diagnostic/treatment access bias)

77. • Neyman bias: (synonyms: incidence-prevalence bias,
selective survival bias) when a series of survivors is
selected, if the exposure is related to prognostic factors, or
the exposure itself is a prognostic determinant, the sample
of cases offers a distorted frequency of the exposure.
• Lets suppose that a case-control study is carried out to
study the relation between tobacco smoking and acute
myocardial infarction (AMI), being cases interviewed one
week after the coronary attack. If smoker patients with
AMI die more frequently, the leaving cases will show lower
frequency of smoking, undervaluing the association
between smoking and AMI.
• It has been shown that the bias occurs only if the risk
factor influences mortality from the disease being studied

78. • Inclusion bias: produced in hospital based case-
control studies when one or more conditions of
controls are related with the exposure. The frequency
of exposure is higher than expected in the reference
group, producing a toward the null bias.
• Exclusion bias: when controls with conditions related
to the exposure are excluded, whereas cases with these
diseases as comorbidities are kept in the study. This
was the explanation given for the association between
reserpine and breast cancer: controls with
cardiovascular disease (a common comorbidity and
related to the use of reserpine) were excluded but this
criterion was not applied to cases, thus yielding a
spurious association between reserpine and breast
cancer.

79. • Berkesonian bias: termed after Dr. Joseph Berkson who
recognized this problem. It arises due to the different rates
of admission to hospitals for peoples with different
diseases, leading to bias in cases and control selection.
• Detection bias :if exposure influences the diagnosis of the
disease, detection bias occurs. Particular types of this bias
are:
• exposure can be taken as another diagnostic criterion
(diagnostic suspicion bias).
• Exposure can trigger the search for the disease; for
instance, benign anal lesions increases the diagnosis of anal
cancer.
• Exposure may produce a symptom/ sign that favours
diagnosis (unmasking-detection signal-bias) or a benign
condition close clinically to the disease (mimicry bias)

80. Information bias
• Information bias occurs during data collection.
• Misclassification bias : It is originated when sensitivity
and/or specificity of the procedure to detect exposure
and/or effect is not perfect, that is, exposed/diseased
subjects can be classified as nonexposed/ non-diseased and
vice versa. Given that perfect tools to gather data are very
uncommon most studies must assume a certain degree of
misclassification. Random error also can produce it. This
implies that random errors in data entry/capture, missing
data, end digit preference (rounding to 5 or 0), frequently
unavoidable, also introduce misclassification.

81. • There are two major types of misclassification bias:
• Differential misclassification bias: when
misclassification is different in the groups to be
compared; for example, in a case-control study the
recalled exposure is not the same for cases and
controls.
• Non-differential misclassification bias: when the
misclassification is the same across the groups to be
compared, for example, exposure is equally
misclassified in cases and controls.

82. • The most common biases producing misclassification
are:
• Observer/interviewer bias: the knowledge of the
hypothesis, the disease status, or the exposure status
(including the intervention received) can influence
data recording (observer expectation bias). The means
by which interviewers can introduce error into a
questionnaire include administering the interview or
helping the respondents in different ways (even with
gestures), putting emphases in different questions, and
so on. A particular situation is when the measure of an
exposure influences its value (for example, blood
pressure) (apprehension bias).

83. • Recall bias: if the presence of disease influences the
perception of its causes (rumination bias) or the
search for exposure to the putative cause (exposure
suspicion bias), or in a trial if the patient knows what
they receive may influence their answers (participant
expectation bias). This bias is more common in case-
control studies, in which participants know their
diseases.

84. Advantages
1. Relatively easy to carry out.
2. Rapid and inexpensive.
3. Require comparatively few subjects.
4. Particularly suitable to investigate rare diseases.
5. No risk to subjects.
6. Allows study of different etiological factors.
7. Risk factors can be identified.
8. No attrition problems, because case control do not
require follow up of individuals into future.
9. Ethical problems are minimal.

85. Disadvantages
1. Problems of bias relies on memory or past records, the
accuracy of which may be uncertain; validation of
information obtained is difficult or sometimes
impossible.
2. Selection of an appropriate control group may be
difficult.
3. We cannot measure incidence, and can only estimate the
relative risk.
4. Do not distinguish between causes and associated factors.
5. Not suited to the evaluation of therapy or prophylaxis of
disease.
6. Another major concern is the representativeness of
cases and controls.

86. • Be aware that the term case-control study is
frequently misused. All studies which contain cases
and controls are not case-control studies. One may
start with a group of people with a known exposure
and a comparison group (control group) without the
exposure and follow them through time to see what
outcomes result, but this doe not constitute a case
control study.

87. • Case-control studies are sometimes less valued for
being retrospective. However, they can be a very
efficient way of identifying an association between an
exposure and an outcome.
• Sometimes they are the only ethical way to investigate
an association. If care is taken with definitions,
selection of controls, and reducing the potential for
bias, case-control studies can generate valuable
information.

88. References
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