Case control

See discussions, stats, and author profiles for this publication at: https://www.researchgate.net/publication/12780993
Use of the Case-Control Approach in Vaccine Evaluation: Efﬁcacy and Adverse
Effects
Article  in  Epidemiologic Reviews · February 1999
DOI: 10.1093/oxfordjournals.epirev.a017988 · Source: PubMed
CITATIONS
67
READS
710
2 authors:
Some of the authors of this publication are also working on these related projects:
Bolsa Familia View project
MRC Tropical Epidemiology Group Programme Grant View project
Laura C Rodrigues
London School of Hygiene and Tropical Medicine
525 PUBLICATIONS   19,892 CITATIONS
SEE PROFILE
Peter g Smith
London School of Hygiene and Tropical Medicine
279 PUBLICATIONS   30,091 CITATIONS
SEE PROFILE
All content following this page was uploaded by Laura C Rodrigues on 31 May 2014.
The user has requested enhancement of the downloaded file.

Epidemiological Reviews
Copyright © 1999 by The Johns Hopkins University School of Hygiene and Public Health
All rights reserved
Vol. 21, No. 1
Printed in US A.
Use of the Case-Control Approach in Vaccine Evaluation: Efficacy and
Adverse Effects
L. C. Rodrigues and P. G. Smith
INTRODUCTION
The least ambiguous method with which to estimate
the protective effect of a vaccine and to assess possible
adverse effects associated with its use is a double-blind
randomized controlled trial (RCT). Double-blindness,
ensuring that neither trial participants nor those assess-
ing vaccine effects know who has received the vaccine
under evaluation and who has received the comparison
product, should eliminate bias. Randomization should
ensure, if the study is sufficiently large, that the vacci-
nated and unvaccinated groups are similar with respect
to risk factors, other than vaccination, for the disease
and adverse reactions under study. That is, randomiza-
tion controls for both known and unknown factors that
might otherwise confound the measurement of vaccine
effects. If the vaccine is designed to protect from a dis-
ease for which there is currently no effective vaccine,
the comparison product may be a placebo or, if a
placebo injection is considered unacceptable, another
vaccine which is not expected to have an impact on the
endpoints the trial is designed to assess. If, however, a
partially effective vaccine already exists, ethical con-
siderations may dictate that this be used as the com-
parison product. In such circumstances, the assess-
ments of efficacy and adverse effects are made relative
to the existing product, and absolute estimation of
effects is precluded.
Once an RCT of a vaccine has been conducted and
the vaccine has been shown to be efficacious, further
such trials may be considered unethical, especially
after the vaccine has been introduced into public health
use. However, it is often of interest to know not only
whether a vaccine is effective in the context of a trial
but also what its efficacy is under routine conditions,
Received for publication November 24, 1998, and accepted for
publication March 9, 1999.
Abbreviations: BCG, Bacillus Calmette-Guerin; DPT, diphtheria-
pertussis-tetanus; NCES, National Childhood Encephalopathy
Study; RCT, randomized controlled trial.
From the Department of Infectious and Tropical Diseases, London
School of Hygiene and Tropical Medicine, Keppel Street, London
WC1E 7HT, United Kingdom.
which are often less favorable than those in a trial.
Estimates may also be required of efficacy in sub-
groups of the population and of the frequency of any
adverse effects too rare to have been detected in con-
trolled trials. In addition, sometimes vaccines are
reformulated; and although the changes might be con-
sidered unlikely to diminish efficacy (e.g., as judged
by induced immunologic markers of protection), reas-
surance is required that this is the case, and assess-
ments using approaches that are quicker and less costly
than RCTs are required.
The use of observational approaches to evaluate the
impact of interventions was initially discouraged by
epidemiologists (1) as being too great a departure from
the "gold standard" of RCTs. While this was reasonable
at a time when RCTs were not widely used (in circum-
stances where they should have been used), it also had
the effect of discouraging alternative approaches, even
in situations where RCTs were not applicable. For
example, the case-control approach has been widely
used to assess disease risks associated with "noninter-
ventional" exposures, but with rare early exceptions
(2), only relatively recently have case-control studies
been applied in the context of vaccine evaluation.
One factor that prompted increased use of the case-
control approach for vaccine evaluation was contro-
versy regarding the efficacy of Bacillus Calmette-
Guerin (BCG) vaccine against tuberculosis. By the
early 1980s, BCG vaccine was recommended for rou-
tine use as a protective measure against tuberculosis in
many countries, but large, well-designed RCTs had
found efficacies ranging from nil to >80 percent. It
became clear that undertaking another large RCT
would not resolve the conundrum created by these
conflicting results. Indeed, the very large trial that was
set up in southern India in an attempt to answer many
of the outstanding questions regarding the efficacy of
BCG vaccine against tuberculosis raised more ques-
tions than it answered (3). Following the release
of the early results of that trial, the World Health
Organization recommended that further studies be
conducted to evaluate the efficacy of BCG vaccine
using the case-control approach in settings where BCG
56
by
guest
on
July
13,
2011
epirev.oxfordjournals.org
Downloaded
from

Case-Control Approach in Vaccine Evaluation 57
was given routinely (4). In 1982, Smith (5) promoted
the use of case-control studies for estimating the effi-
cacy of BCG vaccine against tuberculosis and dis-
cussed key methodological issues. Clemens and
Shapiro (6) also suggested that case-control and other
observational designs could be used to help resolve
controversies about the efficacy of pneumococcal vac-
cines. Since then, over 100 papers have been published
using or discussing case-control studies in the context
of the evaluation of vaccines.
In a case-control study, a measure of the influence of
the exposure of interest on the disease of interest is
obtained by comparing the proportions of exposed
cases and controls. In studies of vaccine efficacy, cases
have the disease the vaccine is designed to prevent,
and controls are chosen to be representative of the pop-
ulation from which the cases were derived. Histories
of vaccination are established for cases and controls,
ensuring that the collection of information is done in
the same way for both groups. In RCTs, randomization
ensures that the intervention and comparison groups
are similar, but in case-control studies the investigators
have no influence over who receives the vaccine under
study (since the evaluation is retrospective), and
attempts must be made to control for differences
between cases and controls that might influence the
estimate of vaccine efficacy. Control for confounding
variables, such as age or socioeconomic status, may be
taken into account in both the design of a study and the
analysis.
The odds ratio for vaccinated persons versus non-
vaccinated persons among cases and controls gives a
measure of the association between vaccination and
the disease. This may be based on the McNemar for-
mula (7), if matched controls are selected for each
case, or it may be derived following conditional or
unconditional logistic regression analysis if other vari-
ables need to be controlled for. For "rare" diseases, the
odds ratio approximates closely the risk ratio and the
rate ratio. With appropriate selection of controls, the
rate ratio or the risk ratio may be estimated using case-
control methods even if the disease is common (8, 9).
An example of the use of the case-control approach
for vaccine evaluation is a Brazilian study of
serogroup B meningococcal vaccine (10). This vaccine
was licensed, but doubts were raised about its efficacy
following its apparent failure to control an epidemic of
meningitis. For the case-control investigation, the
study population was defined as children aged 3-84
months who lived in the city of Sao Paulo, Brazil, dur-
ing the mass vaccination campaigns with serogroup B
meningococcal vaccine. Cases in the study were hos-
pitalized cases of meningococcal disease identified
from a hospital-based surveillance system. For each
case, four neighborhood controls were selected,
matched by age (for cases under age 24 months, con-
trols were matched within 6 months of age; for cases
aged >24 months, controls were matched within 1
year). The researchers identified controls by visiting
houses, following a systematic procedure starting from
the case child's place of residence. They interviewed
parents or guardians to obtain data on potentially con-
founding variables and inspected vaccination cards to
determine vaccination status. A child was deemed to
have been vaccinated if his or her vaccination card
showed a meningococcal vaccine stamp for each of
two doses, with an interval between the doses of 40
days-12 weeks, and more than 21 days had elapsed
between the last dose and the onset of disease (in the
matched case for controls). Children were considered
unvaccinated if they had a card with no record of
meningococcal B vaccination and the parent or
guardian reported no vaccination. Children without
cards, children with cards that showed an incomplete
vaccination history, and children for whom there was
conflicting information between the card and the infor-
mation given by the person interviewed were excluded
from the analysis. Conditional logistic regression
methods were used to adjust for confounding variables
and to estimate the vaccine efficacy and confidence
intervals.
The case-control design has also been used, though
much less widely, to study adverse effects of vaccina-
tion. The size of an RCT of a vaccine is usually deter-
mined on the basis of the statistical power needed to
detect a protective effect of a given size. An important
aspect of such trials is their ability to enable an unbiased
assessment to be made of adverse effects that may be
associated with vaccination. However, such trials may
not have sufficient power to identify rare but important
adverse effects of vaccination that may become appar-
ent, or be suspected, only when the vaccine is applied on
a widespread basis. When a potential adverse effect has
been thus identified, usually initially by case reports, the
association between the effect and vaccination can be
studied using case-control methodology.
An early case-control investigation of possible
adverse effects following vaccination in the United
Kingdom was the National Childhood Encephalopathy
Study (NCES), a study of neurologic illnesses in early
childhood and their relation to immunization with per-
tussis vaccine (11). The initial hypothesis with respect
to the forms of neurologic illness pertussis vaccination
might induce was not well defined, and thus a study
encompassing a range of such illnesses had to be set
up. National surveillance for the defined conditions
was instituted through contacts with consultant pedia-
tricians, infectious disease specialists, and neurosur-
Epidemiol Rev Vol. 21, No. 1, 1999
by
guest
on
July
13,
2011
Downloaded
from

58 Rodrigues and Smith
geons, who were asked to notify the investigators of all
children aged 2-24 months who were admitted to hos-
pital with these conditions during a 3-year period.
Over 1,000 such cases were reported. Children with a
neurologic abnormality upon discharge were examined
at home by a study physician. Two controls were
selected for each case, matched for age, sex, and area
of residence, using either birth registers or lists of chil-
dren eligible for immunization. Vaccination histories
of cases and controls were obtained from general prac-
titioner and community physician records. Controls
were also visited at home for collection of information
on risk factors that might have predisposed them to
neurologic illnesses.
Analysis focused on the comparison between cases
and controls of the proportion vaccinated and the time
interval between vaccination and the estimated date of
clinical onset of the neurologic illness (using a "pseudo-"
date of onset for controls corresponding to that of
the matched case). The investigators reported a sig-
nificantly increased risk within 7 days of diphtheria-
pertussis-tetanus (DPT) vaccination (3.5 percent of
cases and 1.7 percent of controls) but not for diphtheria-
tetanus vaccination. The risk associated with DPT was
greatest during the 72 hours following vaccination.
When analyses were confined to children who had been
"normal" prior to vaccination (e.g., excluding children
with a history of fits, which was a contraindication for
DPT vaccination), the relative risks were larger. The
authors concluded that serious neurologic reactions may
occur very rarely after DPT vaccination but most of the
cases studied did not appear to be associated with vac-
cination (11). On the assumption that the surveillance
system set up had identified all of the potential cases,
the NCES estimated the attributable risk of serious neu-
rologic disorders' occurring within 7 days of vaccina-
tion in previously normal children to be 1 in 110,000 (95
percent confidence interval: 1 in 360,000, 1 in 44,000).
The conclusions of the NCES have been the subject
of considerable controversy. The parents of a child
with permanent neurologic injury sued for damages,
and this led to a detailed legal review of the findings
from the NCES (12, 13). The court report judged that
"the evidence supports the conclusion that DPT some-
times causes febrile convulsions; it does not provide
evidence that such convulsions following DPT cause
brain damage... the results of the NCES do not sup-
port... that DPT can cause permanent neurological
damage" (13, p. 76). The judge highlighted a number
of issues in making his ruling, including the study
team's declared bias of trying to maximize the risk
rather than minimize it and the suspicion that vacci-
nated cases were more likely to be reported to the
study team than unvaccinated cases. In addition, the
results of a review of the relevant cases and their con-
trols indicated that although many case children were
recruited into the study, very few cases were of perma-
nent neurologic damage in previously normal children,
and a careful case-by-case review reclassified about
half of these. Debate on the findings of the NCES
has continued (14, 15). The American Academy of
Pediatrics concluded that pertussis vaccine has not
been proven to be a cause of brain damage (16).
The controversy caused by the NCES raised many
of the methodological issues related to the use of the
case-control approach in the study of adverse reac-
tions. These included the possibility that the presence
of contraindications may result in lower vaccination
rates among those likely to suffer the event presumed
to be caused by the vaccine (confounding), a greater
likelihood of diagnosis or ascertainment of presumed
adverse reactions among vaccinated cases than among
unvaccinated cases (diagnosis bias), and faulty recall
of the date of onset of symptoms or the date of vacci-
nation (recall bias). These issues are discussed below.
The controversy and methodological difficulties sur-
rounding the NCES may be at least part of the reason
why the case-control approach has been used much
less widely for the study of adverse reactions than for
the study of vaccine efficacy.
As was noted above, case-control studies have been
used to assess vaccines mainly with respect to two
issues: vaccine efficacy and adverse effects. These
issues are discussed separately below. We give formu-
lae for the measure of interest, contrast advantages and
disadvantages of the case-control approach in relation
to other available designs, and discuss relevant
methodological issues. We refer to case-control studies
in the literature to illustrate particular points.
VACCINE EFFICACY
Usually, a vaccine is not licensed for general use
without undergoing evaluation in at least one RCT
(Phase HI trial) (17). However, for any of several rea-
sons, it may be necessary to measure the performance
of a vaccine after it has been introduced into routine use
(18). Firstly, the results of RCTs may not have been
consistent; this was the case for BCG vaccine and
tuberculosis (19, 20). Secondly, the efficacy measured
in the Phase III trials may be greater than that applica-
ble when the vaccine is in public health use. Phase in
trials are generally designed to evaluate the efficacy of
a vaccine under carefully controlled conditions, and
may exclude persons who would not be excluded from
a routine vaccination program (e.g., those with concur-
rent illnesses). In addition, the conditions of storage of
the vaccine, the interval between doses, and the popula-
tion selected for vaccination can be controlled more
by
guest
on
July
13,
2011
Downloaded
from

carefully in a trial than in a routine vaccination pro-
gram. Case-control studies can be used after the imple-
mentation of routine vaccination to estimate the protec-
tion given by the vaccine under "normal" conditions
(17,20,21). Thirdly, case-control investigations may be
used to determine whether an outbreak of a vaccine-
preventable disease was due to poor vaccine efficacy
(22, 23) and to identify causes for this (24, 25).
Fourthly, there may be reasons to study the protection
conferred by a vaccine in populations or against disease
types that were not included in Phase HI investigations.
There may be interest in the efficacy of a vaccine in a
subgroup of the population (e.g., pneumococcal vaccine
in the elderly (26) or BCG vaccine in children of
Indian-subcontinent ethnic origin living in England
(27)), in a specific setting (e.g., influenza vaccine
among institutionalized persons (28)), against a specific
form of disease (e.g., BCG vaccine against miliary or
meningeal tuberculosis (20)) or level of severity (e.g.,
influenza vaccine against influenza mortality (29)), or
against a different disease (e.g., BCG vaccine against
leprosy (30)). Case-control studies have also been used
to assess the protection of a vaccine not against a spe-
cific disease but against a group of conditions presumed
to consist in part of the disease of interest (e.g., studies
of the efficacy of measles vaccine against all-cause
mortality (31, 32) and of pneumococcal vaccine against
hospitalization for pneumonia in the elderly (33)) and to
study effects not originally measured (e.g., the protec-
tive effect in infants of cholera vaccine given to women
who breastfeed (34)). It is also possible to measure the
efficacy of a vaccine against a long term complication
of a disease (e.g., the efficacy of measles vaccine
against subacute panencephalitis (35)).
Methodological issues associated with the use of
case-control and other observational approaches to the
evaluation of vaccine efficacy have been discussed in a
number of papers. Comstock (21, 36) provided two
overviews; Joseph and Joseph (37) discussed possible
biases; Smith et al. (8) and others (9, 38, 39) reviewed
the methodological implications of the presumed bio-
logic mechanism underlying vaccine protection;
Wunsch et al. (40) discussed different sources of con-
trols; and Clarkson and Fine (41) and Noah (42)
reviewed public health applications. A number of papers
discussing the field evaluation of vaccine efficacy (17,
43, 44) or reviewing efficacy studies for specific dis-
eases (e.g., pertussis (45, 46) and tuberculosis (47, 48))
contain relevant sections on case-control studies.
Measurement of vaccine efficacy
Vaccine efficacy is defined as the percentage reduc-
tion in the disease rate among vaccinated subjects that
is attributed to vaccination. In a situation where there
are no differences between vaccinated and unvacci-
nated individuals with respect to confounding vari-
ables, as in an RCT, vaccine efficacy (VE) is defined
as
VE = 100 (/„ - /„)//„ = 100 (1 - RRV/U),
where /„ = disease incidence in the unvaccinated
group, /„ = disease incidence in the vaccinated group,
and RRV/U = /„//„ (the relative risk of disease in vacci-
nated persons compared with unvaccinated persons).
Relative risk may be estimated in case-control (or
cohort) studies, and thus the formula may also be used
in such studies to estimate vaccine efficacy (usually
after the relative risk estimate has been adjusted for
potentially confounding variables).
In some circumstances—for example, in a disease
surveillance program—the information most readily
available may be the proportion of cases who have
been vaccinated (P ) and the proportion of the target
population who have been vaccinated (P ). A rapid
estimate of vaccine efficacy (though possibly biased,
since there is no adjustment for confounding variables)
is given by
{1 - [Pc( ~ PP)]/[PP(1 ~ Pc)]} X 100.
Application of this formula illustrates that in vaccina-
tion programs with high vaccine coverage and high
vaccine efficacy, it is to be expected that a high pro-
portion of persons with disease will have a history of
vaccination. For example, in a vaccine program which
achieves 95 percent coverage with a vaccine that has
90 percent efficacy, approximately two thirds of all
cases of disease will be in vaccinated individuals.
Mode of vaccine protection
Protection to the individual. Vaccine efficacy is a
measure which summarizes the impact that a vaccine
has on disease incidence among those vaccinated. The
level of protection given to different members of the
vaccinated population may vary, and different models
of vaccine action have been discussed. Under one
model, the vaccine is assumed to provide full protec-
tion to some individuals and leave the others as sus-
ceptible as they were before vaccination. In another
model, the vaccine is assumed to confer the same level
of partial immunity to all persons vaccinated (8). In
the former "all-or-nothing" model, a vaccine efficacy
of 80 percent corresponds to a situation in which 80
percent of those vaccinated are completely immune to
disease subsequent to vaccination and the other 20
percent remain as susceptible as they were prior to
by
guest
on
July
13,
2011
Downloaded
from

vaccination. That is, the number of subjects at risk of
disease is reduced by 80 percent and the incidence of
disease remains the same in the 20 percent who are
vaccinated but not protected. In the "partial immunity"
model, all persons vaccinated remain at risk of devel-
oping disease but each of their risks of disease is
reduced by 80 percent. Both of these models are ideal-
ized, and for most vaccines the true mode of action
probably fits neither of them, but for a specific vaccine
the mode of action may be closer to one model than to
the other.
The "all-or-nothing" model may be most relevant
for vaccines for which protection depends upon induc-
ing a sufficiently high immunologic response, where
persons beyond some critical level of a specific anti-
body after vaccination are immune from disease and
persons under this level have a rate of disease similar
to that of those who were not vaccinated. Often, how-
ever, those with lower induced antibody levels may
have some protection, and the degree of protection
may be correlated with antibody level. The implica-
tions of this, as well as variations in other assumptions
under these models (including homogeneity of protec-
tion among persons not made fully immune by vacci-
nation, homogeneity of exposure to infection, and
duration of immunity), have been discussed elsewhere
(49-55) and are also addressed in another paper in this
issue (119).
If the disease against which the vaccine is directed is
common, the underlying model of vaccine action is rel-
evant to the design and interpretation of studies of vac-
cine efficacy. If the immunity of vaccinated subjects
does not wane with time (which is perhaps unlikely),
under the "all-or-nothing" model, the proportion of
fully immune individuals among those who have not
yet suffered from disease will increase with time since
vaccination (because an increasing proportion of the
nonprotected vaccinated subjects will develop disease).
Under the "partial immunity" model, the risk of disease
among those who have not yet developed disease will
remain constant. The implications of the model of vac-
cine action for the design of case-control studies have
been discussed in detail elsewhere (8). hi brief, under
the "all-or-nothing" model, controls should be selected
from the population initially at risk after vaccination.
That is, individuals should be eligible for inclusion as
controls even if they develop the disease under study. If
such individuals are excluded from the control group,
the efficacy of the vaccine may be overestimated. For
example, in a mumps outbreak at a school, the esti-
mated efficacy of mumps vaccine was 71 percent, but
it increased to 78 percent when subjects with a prior
history of mumps were excluded (56). Under the "par-
tial immunity" assumption, controls should be selected
to represent the person-years at risk in the population
that produced the cases during the period covered by
the study. That is, potential controls should be excluded
if they develop disease before the date of disease onset
in the case to whom they are matched, but not if they
develop it afterwards (9). The underlying model is of
little consequence, however, unless the disease under
study is common (e.g., the attack rate in those vacci-
nated from the time of vaccination to the end of the
study period is -20 percent or more).
Direct and indirect protection. The protection
against disease conferred by a vaccine consists of both
a direct effect and an indirect effect. The direct effect
results from the immunity conferred by the vaccine to
vaccinated individuals; the indirect effect results from
the fall in the number of sources of infection caused by
the direct effect, leading to a reduction in the risk of
infection in the community (57, 58). A number of RCT
designs have been suggested for measurement of direct
and indirect effects, based on group randomization
(59). The relevance for observational studies is small.
In most situations, vaccinated and unvaccinated people
mix, and the impact of the indirect effect is the same in
both groups and will not be measurable in either cohort
or case-control studies.
Advantages and disadvantages of using the case-
control approach to assess efficacy. The advantages
and disadvantages of the case-control approach derive
from its features: being observational, having subjects
selected on the basis of disease status, and using con-
trols to represent the population from which the cases
were derived.
Case-control studies compared with randomized
controlled trials. In general, a double-blind RCT is the
best way to evaluate a vaccine, because through this
approach issues of confounding and bias have minimal
influence on the estimation of vaccine efficacy. In an
RCT, participants are allocated at random to a vaccine
group or a placebo group (if there is no existing effi-
cacious vaccine), with both trial participants and
researchers blinded as to which group received
placebo and which received vaccine. Both trial groups
are followed prospectively, and the incidence of dis-
ease is compared. In some circumstances, groups
rather than individuals may be randomized (60). In
contrast, case-control studies, in common with cohort
and case-population studies, are observational. The
individuals studied may or may not have been vacci-
nated, but the allocation to either of these groups has
not been random. Thus, the investigators must attempt
to control for differences between the groups that may
confound estimation of the vaccine effect.
The advantages of the case-control approach in com-
parison with RCTs are several. Firstly, case-control
by
guest
on
July
13,
2011
Downloaded
from

studies avoid ethical issues in situations where there is
already evidence that the vaccine being evaluated is
better than the comparison product, be that another vac-
cine or no vaccine. Secondly, because of their retro-
spective nature, case-control studies can generally be
conducted much more rapidly than RCTs. Thirdly,
case-control studies require smaller numbers of sub-
jects, and thus they are substantially cheaper to conduct
than RCTs.
Case-control studies compared with cohort studies.
Cohort studies are also observational studies in which
subjects have already been "self-allocated" to vacci-
nated or unvaccinated groups. Thus, they share with
case-control studies the potential for bias and con-
founding in the estimation of vaccine effects. Except
for this important aspect, the logic of a cohort study
follows that of an RCT. Persons in the population at
risk (those with no previous history of disease) are
classified as vaccinated or unvaccinated according to
their status at the beginning of the study period, and
disease incidence rates between the two groups are
compared. Cohort studies may be conducted in the
context of a routine vaccination program, in which
there is surveillance for new cases of disease and
records are kept centrally on both the population eligi-
ble for vaccination and the persons who have actually
been vaccinated (e.g., Sutherland et al.'s (61) studies
of BCG vaccine efficacy in the United Kingdom). Two
settings are particularly efficient for application of the
cohort approach: outbreaks and studies of contacts.
Methodological issues relevant to the design and con-
duct of cohort studies have been discussed elsewhere
(43, 44).
RCTs are prospective. Disease events are ascertained
following randomization of participants to vaccinated
and unvaccinated groups. The groups must be followed
until a sufficient number of disease events have
occurred to enable a good estimate of vaccine efficacy
to be made. Cohort studies may be prospective or ret-
rospective, but in both situations, as in RCTs, disease
events may occur over a considerable time period. This
may make it difficult to ensure uniform standards of
diagnosis, particularly for retrospective studies. In con-
trast, in case-control studies, cases are typically
recruited over a relatively short time period, and, par-
ticularly if this is done prospectively, it is easier to
ensure that strict diagnostic criteria are adhered to.
In case-control studies, information is collected on a
small representative sample of persons without the dis-
ease (the control group), whereas in cohort studies (and
RCTs) it is necessary to collect information on and fol-
low up all persons in the population from which the
cases were derived. This gives case-control studies a
very important advantage in terms of speed, cost, and
logistics—an advantage that increases with the rarity of
the disease. Because information needs to be collected
only for a small number of subjects, it is possible to col-
lect information on a much larger number of variables
than in cohort studies, enabling better control of con-
founding. A major disadvantage of the case-control
approach is the possibility of selection bias due to
selection of a group of controls who are not representa-
tive of the population whence the cases came.
Case-control studies compared with case-population
studies. The case-population approach is similar to the
case-control approach, but instead of data on a control
group, data on the whole population are used for con-
trast with vaccine coverage in the cases. The approach
has also been called rapid screening (for vaccine effi-
cacy) or case coverage (43, 44, 62, 63). Vaccine effi-
cacy is estimated by comparing vaccine coverage
among cases with the vaccine coverage in the popula-
tion. The only advantage the method has over the case-
control approach is that it is cheaper. It is a crude
method by which to assess vaccine efficacy, but it has
some uses. For example, the method may be used to
obtain a preliminary and rapid estimate of vaccine effi-
cacy, or to obtain reassurance that the proportion of
cases who have a history of vaccination is compatible
with vaccine coverage in the population and presumed
vaccine efficacy. The main limitation of this method is
that it allows for no control of confounding; therefore,
it is particularly important to make sure that the
"cases" and the "population" relate to the same age
group and geographic area.
Methodological issues
Study population. The study population will often
be selected on the basis of logistic considerations, but
the choice is likely to be influenced by two issues: the
generalizability of results and the proportion of the
population that may have been infected prior to vacci-
nation.
Generalizability. Vaccine efficacy may vary in dif-
ferent subpopulations and settings. The study must be
designed to estimate efficacy in the settings or sub-
populations of interest. Thus, if the main public health
target for a vaccine is the elderly, the study population
and thus the cases and controls must be drawn from
elderly persons. Examples of the use of case-control
studies to estimate vaccine efficacy in particular sub-
groups of the population include studies of pneumo-
coccal vaccine in 1) the immunocompromised elderly
(26), 2) the immunocompetent elderly (64), and 3) per-
sons with human immunodeficiency virus infection
(65).
Infection or disease prior to vaccination. Efficacy
studies of vaccines are difficult to interpret when they
by
guest
on
July
13,
2011
Downloaded
from

are undertaken in settings where a substantial number
of persons may have been infected (with the disease
agent under study) prior to vaccination. For most vac-
cines, vaccination would not be expected to influence
disease incidence among those who have been infected
prior to vaccination. For diseases with short incubation
periods, cases can be excluded from the study or can
be considered unvaccinated if the interval between the
last dose of vaccine and the onset of symptoms is
shorter than the incubation period (66, 67). In matched
case-control studies, controls should be considered
unvaccinated if they received vaccine after the pre-
sumed date of infection of the matched case. This is an
argument for matching, since each control can be
given a "pseudo-" date of disease onset which is the
same as that of the matched case.
For some diseases, the time between infection and
onset of disease may be both long and variable. With
tuberculosis, for example, clinical disease may
develop years after the initial infection, either because
of reinfection or because of reactivation of the original
infection. In most of the RCTs of BCG vaccine, previ-
ously infected subjects were excluded on the basis of a
tuberculin skin test. In many of the BCG mass vacci-
nation campaigns, however, an attempt was made to
administer BCG vaccine to all children under a certain
age, without prior tuberculin testing. Many of these
children, especially the older ones, will have been
infected with the tubercle bacillus prior to vaccination.
In a case-control study it would be impossible to
exclude those who were infected before vaccination,
and the efficacy measured would be expected to be
lower than that measured in RCTs restricted to persons
with no evidence of prior tuberculosis infection. Smith
(5) presented tables to illustrate the magnitude of the
impact of this on the measure of vaccine effect in a
case-control study, taking account of the efficacy of
the vaccine in persons who were not infected at the
time of vaccination, the proportion infected at the time
of vaccination, and the incidence of tuberculosis in
those infected and not infected in the absence of vac-
cination (table 1). The estimated vaccine efficacy may
be the measure of public health interest, of course, in
populations where BCG vaccine is given without a
previous skin test. The issues would be similar for a
disease such as malaria, where neither previous
episodes of disease nor current vaccines confer good
protection (68, 69).
Exposure. Validity of information on vaccination.
Reliable information on vaccination history is essen-
tial for estimating vaccine efficacy in case-control
studies, but it is often difficult to obtain, particularly
TABLE 1. Overall efficacy of Bacillus Calmette-Guerin (BCG) vaccine against tuberculosis in
populations in which some members are tuberculin-positive*,t
80% protection in the
tuberculin-negative
tuberculin-negative
tuberculin-negative
Proportion of
pupuidiiun
tuberculin-positive
0.0
0.1
0.2
0.3
0.4
0.5
0.0
0.1
0.2
0.3
0.4
0.5
0.0
0.1
0.2
0.3
0.4
0.5
Incidence in the tuberculin-positive/incidence in the tuberculin
0.5
80
76
71
66
60
53
50
47
44
41
38
33
20
19
18
16
15
13
1.0
80
72
64
56
48
40
50
45
40
35
30
25
20
18
16
14
12
10
1.5
80
69
58
49
40
32
50
43
36
30
25
20
20
17
15
12
10
8
2.0
80
65
53
43
34
27
50
41
33
27
21
17
20
16
13
11
g
7
4.0
80
55
40
29
22
16
50
35
25
18
14
10
20
14
10
7
5
4
-negative
10.0
80
38
23
15
10
7
50
24
14
g
7
5
20
9
6
4
3
2
* Reproduced with permission from Smith (5).
t The table shows the overall protective effect (%) that would be estimated in various circumstances according
to 1) the protective effect of BCG in those who were tuberculin-negative at vaccination; 2) the relative incidence of
tuberculosis in those who were tuberculin-positive compared with the incidence in those who were tuberculin-
positive and not vaccinated; 3) the proportion of the population who were tuberculin-positive before vaccination.
by
guest
on
July
13,
2011
Downloaded
from

when there is interest in the protective effect several
years after vaccination. The ideal vaccination history
consists of a record written at the time of vaccination.
Such records may be available in some situations, par-
ticularly in developed countries with good central
recording of vaccines administered. In many circum-
stances, however, vaccination records will not be
available or will be incomplete, and cases and controls
(or their parents or guardians) must be asked to recall
the vaccination history. Such recall may be imperfect.
The consequences of misclassification of vaccine
status vary. If the information about vaccination status
is subject to error but to a similar extent in cases and
controls (nondifferential misclassification), the esti-
mate of vaccine efficacy will be biased toward zero.
Some case-control studies of the efficacy of childhood
vaccines have presented results based on information
extracted from vaccination cards and also based on
maternal recall. In general, estimates of efficacy based
on recall have tended to be lower than those based on
vaccination cards (70, 71). Sometimes the sources of
vaccine history may vary between individuals, and a
decision must be made as to whether to restrict the
analysis to subjects with information based on written
records or to include those with information based on
parental recall only. In such circumstances, it is proba-
bly desirable to present both sets of results to indicate
the robustness (or lack thereof) of the estimate.
BCG and smallpox vaccine are among the few vac-
cines to leave a long-lasting physical mark after vacci-
nation. BCG scars have been used as an indication of
vaccination in case-control studies of the efficacy of
BCG vaccine. The sensitivity and specificity of this
measure of vaccination are less than 100 percent. In
one trial in Malawi, the validity of scar reading, esti-
mated where vaccine history was known, was low
(72), but further studies are necessary to establish
whether this would be true in other settings. Smith (5)
gives a formula and a table (table 2) and Fine et al. (72)
give tables showing the effect on the estimated vaccine
efficacy caused by misclassification of BCG vaccina-
tion history based on the sensitivity and specificity of
scar reading.
When the validity of vaccine history is different in
cases and controls (differential misclassification), the
efficacy may be biased towards or away from zero.
This is more likely to occur if information on vaccina-
tion is based solely on recall (recall bias), since cases
may be likely to recall their vaccination history with
different reliability than controls.
Vaccination of controls after disease onset in the
matched case. For most diseases, cases are unlikely to
be vaccinated after they have developed the disease
under study, and any such vaccination would be
TABLE 2. Bias in the estimate of the efficacy of Bacillus
Calmette-Guerin vaccinations which leave no scar*
%of
population
vaccinated
90
70
50
% of vaccinations which do not leave a scar
0
40|
40
40
5
31
37
39
10
26
35
38
20
19
31
36
* Reproduced with permission from Smith (5).
t Estimated overall protective effect based on a case-control
study (assuming that the protective effect in the tuberculin-negative
is 80%, the incidence of tuberculosis in the tuberculin-positive/the
incidence of tuberculosis in the tuberculin-negative is 4/1, and 20%
of the population are tuberculin-positive before vaccination).
ignored in a case-control evaluation. Care must be
taken that comparable vaccinations in controls are
treated in the same way in the analysis of the results.
This is straightforward in matched case-control stud-
ies, where the vaccination history of controls is con-
sidered only up to the age at which the matched case
developed disease. This strategy cannot be adopted
when frequency matching is done, or when matching
is not used at all. This is an additional reason for using
a matched design in such studies.
Variation in efficacy. Features associated with low
efficacy. It is possible to examine how the efficacy of
a vaccine varies according to factors such as age at
vaccination, vaccination schedule, place of vaccina-
tion, and time since vaccination. Two methods of
examining such variations have been employed, both
using the case-control approach. In the first approach,
there are no restrictions on inclusion in the study on
the basis of vaccination. Studies using this approach
have examined vaccine efficacy according to number
of doses, interval between doses, and schedule
(73-79). The effect of age at vaccination on the effi-
cacy of measles vaccine was established in early case-
control studies using this approach (80-83). Other
studies have examined other specific features sus-
pected of lowering vaccine efficacy (84).
In the second approach, the analysis is restricted to
cases and controls who give a history of vaccination.
The exposures studied are features of the vaccine that
are suspected of being associated with low efficacy—
for example, age at vaccination or number of doses. In
the simplest case, the analyses compare the propor-
tions of vaccinated cases and vaccinated controls with
and without the feature of interest, and the estimated
odds ratio provides a measure of how much vaccine
efficacy varies according to the presence or absence of
the feature (23, 71,85).
Time since vaccination. It is surprising how rarely
the case-control approach has been used to examine
changes in vaccine efficacy with time since vaccina-
by
guest
on
July
13,
2011
Downloaded
from

tion, especially given our ignorance of the long term
protective effect of many vaccines. For example, the
duration of protection given by BCG vaccine against
tuberculosis is unclear, despite the long history of use
of this vaccine (86). Estimation of efficacy according
to time since vaccination is straightforward in case-
control studies, if information on date of vaccination
and date of disease is collected (table 3).
One of the few examples of estimating change in
vaccine efficacy with time since vaccination using a
case-control approach is that of Reingold et al. (87).
These authors conducted successive case-control stud-
ies in the years following a mass vaccination campaign
with meningococcal polysaccharide A vaccine, and
they presented vaccine efficacy according to the
amount of time elapsed between the campaign and the
case-control studies.
Fine and Clarkson (46) have reviewed studies of the
efficacy of pertussis vaccine according to age at dis-
ease onset. In this instance, age at disease onset is
closely correlated with time since vaccination, as the
vaccine is given in early infancy.
Definition and selection of cases. Defining the
outcome of interest. The efficacy of a vaccine may be
different for different forms of a disease. For example,
efficacy may vary in persons with any clinical disease,
persons with severe disease (e.g., severe influenza
(88), mortality associated with influenza (29)), or
persons with specific forms of clinical disease (e.g.,
miliary and meningeal tuberculosis (20), invasive
Haemophilus influenzae type b (89), pertussis carriage
(46)).
A strength of the case-control approach is that it can
be employed to study the efficacy of a vaccine against
endpoints which cannot be studied in RCTs. Under the
special circumstances of an RCT, there is an ethical
obligation to treat cases of disease when they occur in
the study population. The surveillance systems set up
for the trial may have the effect of ensuring that most
cases of disease are treated early in their natural his-
tory, often preempting the occurrence of more severe
disease. Thus, it may be difficult or impossible to mea-
sure the impact of vaccination on severe disease,
TABLE 3. Estimation of vaccine efficacy (VE) in case-control
studies, by time since vaccination
Status Cases Controls O d d s
™
ratio 100
Unvaccinated a
Time since vaccination
(years)
<5 c
5-10 e
>1O g
d cb/ad 1 - (cb/ad)
f eb/af 1 - (eb/af)
h gb/ah 1 - (gb/ah)
which is likely to be the measure of most public health
importance. Because of their retrospective nature,
case-control studies do not suffer from this restriction.
Examples in which case-control studies have been
used to assess the efficacy of vaccines against serious
disease endpoints include assessments of the efficacy
of measles vaccine against all-cause mortality (31, 32)
and against hospitalization for dehydration (90).
Case definition. In case-control studies, as in RCTs,
it is important that the case definition be as specific as
possible, since the inclusion of "false positive" cases
will decrease the estimated vaccine efficacy. It is not
necessary to have a highly sensitive case definition, as
long as the case definition is applied without bias (as
to vaccine status) and it is possible to recruit enough
cases for the study to obtain the desired statistical
power. Cases can also be classified according to diag-
nostic certainty, and efficacy estimated for each level
of certainty (91).
There should be a clear definition of the target pop-
ulation from which cases are to be ascertained, and an
effort must be made to ascertain all cases, or a repre-
sentative sample of all cases, occurring in that popula-
tion over the study period. Controls should then be
selected to represent that population. Clarity regarding
the definition of the study population whence the cases
were derived is essential in order to avoid selection
bias when choosing controls. It is generally inefficient
to include cases and controls who are under the mini-
mum age recommended for vaccination, since they
will probably be unvaccinated and will not contribute
information to the study analysis.
Selection bias will also be introduced in a case-
control study if the chance of a case's or control's
being recruited into the study is influenced by his or
her vaccination history. Disease diagnosis or designa-
tion by the study as a case must be as independent as
possible from markers of vaccination. Thus, criteria
for case definition should not be based on immuno-
logic/serologic tests that are affected by vaccination.
For example, tuberculin sensitivity is induced by
infection with Mycobacterium tuberculosis and by
vaccination with BCG. If tuberculin testing were
included in the criteria for a diagnosis of tuberculo-
sis, more BCG-vaccinated children than unvacci-
nated children would be diagnosed as cases (because
of their past history of vaccination). This would lead
to a reduction in the estimated vaccine efficacy.
Definition and selection of controls. Controls
should be representative of the population that pro-
duced the cases. Selection bias is liable to be intro-
duced when they are not.
Selection bias. The easiest situation in which to rule
out selection bias is the one where the case-control
by
guest
on
July
13,
2011
Downloaded
from

study is nested within a cohort study (or in a well
defined population). In such circumstances, all cases
arising in that cohort or population can be included in
the study, and controls can be selected at random from
the cohort or population (possibly matched with the
cases according to characteristics such as age and sex).
In other situations, there should be a clear definition of
the population from which the cases were derived, and
the controls should be ascertained from, and be repre-
sentative of, that population. A good general rule for
deciding whether or not an individual should be eligi-
ble for being a control is whether, if that person devel-
oped the disease of interest, he or she would become a
case in the study.
Sources of controls. The selection of an appropriate
group of controls will be influenced largely by the
method of case selection, taking account of the need to
avoid selection bias and of logistic considerations.
Control selection is easiest in the context of a case-
control study set within a cohort study, as discussed
above, where the cases are derived from a closed pop-
ulation and the controls can be selected from the same
population. Such circumstances arise in a variety of
situations: For example, the study population may con-
sist of children in particular schools (80, 92), patients
registered with a general physician (93), persons visit-
ing an outpatient clinic (65), children listed in the child
health computer database in England (46), persons
enrolled in medical care programs in the United States
(33, 94), or infants on a list of births compiled by local
midwives (95).
Other potential sources of controls include hospitals
(if cases are ascertained through hospital admissions),
the neighbors of cases, friends of cases, and random
digit telephone dialing. When controls are selected
from hospitalized subjects, it is advisable to avoid
including controls with diseases that can be influenced
by the disease of interest (e.g., pneumonia if the dis-
ease of interest is measles) or by the vaccine (e.g., lep-
rosy if the study is designed to assess the protective-
ness of BCG vaccine against tuberculosis). Children
who have received one vaccine are more likely to have
received others, so often children with other vaccine-
preventable diseases will also be excluded from the
control group. When controls are selected through ran-
dom digit telephone dialing, cases should be excluded
from the study if they live in a home without a tele-
phone (96).
In studies conducted in developing countries, selec-
tion of controls from neighbors is often a reasonable
and efficient method. Controls are selected using a sys-
tematic approach starting at the house of the case.
Neighborhood controls are matched (by neighbor-
hood), and thus matched analysis must be used.
It is possible to use more than one control group
from different sources (97, 98). This is a good strategy
if there is no strong reason for preferring one type of
control group to another. If, in the analysis of the data,
similar results are obtained using either control group,
this gives some reassurance that the results are not
biased (or that they are consistently biased!). If, how-
ever, the analysis gives results which differ according
to the control group utilized, then bias is likely to be
present (with respect to at least one of the control
groups). If it is clear at the outset of the study that one
type of control is better than another on theoretical
grounds, it will only potentially complicate and con-
fuse the interpretation of the results to include both
control groups.
Confounding. Case-control studies are observa-
tional, and therefore there must be appropriate control
of confounding variables to ensure that the estimate of
vaccine efficacy is not biased by differences between
the characteristics of cases and controls. Confounding
variables are those which are independently associated
with the outcome and the exposure of interest. Thus, in
an assessment of a vaccine, a potentially confounding
variable will be one that influences the risk of the dis-
ease under study and is also associated with the likeli-
hood of vaccination. Factors such as age, sex, social
class, and, for some diseases, birth order may be asso-
ciated with rate of disease and with risk of vaccination,
and therefore are potentially confounding factors.
An issue that is sometimes discussed in the context
of using case-control studies to evaluate vaccine effi-
cacy is the extent to which the controls must have been
exposed to the same risk of infection as the cases (37).
With infections for which exposure is highly likely to
result in disease in the absence of vaccination, all of
the cases must clearly have been exposed, and the
unvaccinated controls are unlikely to have been
exposed (or else they would have been cases!). Thus,
ensuring equal chances of exposure to infection among
cases and controls cannot be necessary. The issue is
relevant only if the likelihood of vaccination is influ-
enced by the chance of exposure to the infection under
study. For example, if a vaccination program is tar-
geted at the poorer segment of a population, who may
be more exposed to infection, controls should be
matched to the cases with respect to socioeconomic
status (or area, if there is marked geographic variation
in vaccine coverage, due, for example, to variable
access to health services). If, however, poor and rich
are equally likely to be vaccinated, socioeconomic sta-
tus will not be a confounding factor, even if it is related
to the risk of infection or to disease, given infection.
Some vaccines are not universally recommended but
have defined target groups (e.g., pneumococcal vac-
by
guest
on
July
13,
2011
Downloaded
from

cine), and membership in one of the target groups
(e.g., being elderly, having another chronic illness) is
likely to be associated both with disease and with vac-
cination and should be controlled for (26, 88). The
same is true when vaccination is used as part of out-
break control measures, where vaccine is given to all
potential contacts of cases.
Matching. To control for confounding, controls may
be matched to cases on the basis of one or more poten-
tially confounding variables. It is often convenient to
pair-match, but sometimes this significantly adds to
the cost of a study, and stratum-matching may be more
appropriate. There is little difference in statistical effi-
ciency. The advantages of pair-matching have been
discussed above. This strategy allows a "pseudo-" date
of disease onset to be assigned to each control, based
on the date of onset in the matched case.
ADVERSE EFFECTS
When high population coverage is achieved with an
efficacious vaccine, the occurrence of cases of the dis-
ease that the vaccine prevents may be rare. In these cir-
cumstances, morbidity associated with the vaccine itself
or presumed to be associated with vaccination may
cause more public concern than the prevented disease.
Adverse effects which are relatively common and
which appear shortly after vaccination should usually
have been detected in Phase III studies of a vaccine, or
earlier. However, such effects may be missed, for any
of several reasons. For example, Phase III studies may
not have been conducted (e.g., if the change to a dif-
ferent vaccine formulation was based on serologic
studies only). The incidence of the adverse effect may
be too low to be detected with reasonable reliability in
Phase III studies, and the effects may only become
apparent when the vaccine is introduced into general
use. In addition, the adverse effect may occur after
longer periods postvaccination than were studied in
Phase in trials. Finally, in general use, vaccines may
be administered to a population which is less homoge-
nous than that vaccinated in a Phase III trial, and there
may be subgroups at higher risk of an adverse effect.
After Phase III trials have been completed and a vac-
cine is being given routinely, possible adverse effects
of vaccination may first be recognized through sur-
veillance systems set up for this purpose (e.g., the
"yellow card" surveillance system in the United
Kingdom (99) or the Vaccine Adverse Event Reporting
System (VAERS) in the United States (100)), through
a detected rise in the incidence of the putative adverse
effect in other surveillance systems, or simply because
doctors or other health care workers notice an apparent
increase and voice their concerns. More recently, the
first recognition has resulted from scanning large data
sets and Linking individual records of vaccination data
and morbidity data (e.g., the Vaccine Safety Datalink
Project in the United States (101) and linked hospital
discharge data and child health and general practice
records in the United Kingdom (102, 103)).
Many vaccines are given to very young children at
an age when developmental abnormalities first tend to
be noted and, in particular, the incidence of serious
neurologic illnesses is relatively high. Thus, the tem-
poral coincidence of vaccination and the recognition of
such developmental abnormalities is often thought to
indicate a causal connection (probably falsely more
often than not). Such alarms can have dramatic effects
on vaccination coverage rates and, indeed, may pre-
cipitate an epidemic of the disease that vaccination
would prevent. For example, following extensive
media coverage of a possible association between per-
tussis immunization and neurologic illness in the
United Kingdom, the national coverage of pertussis
vaccination dropped from 80 percent in 1974 to 31
percent in 1978 and coincided with the largest pertus-
sis epidemic in 20 years (11). More recently, media
coverage of a postulated association between measles-
mumps-rubella vaccine and autism in the United
Kingdom (104) was followed by a steep decline in
measles vaccination. It is important, therefore, that
appropriate epidemiologic studies be implemented
rapidly to investigate whether or not unexpected
adverse effects of vaccination are occurring and with
what frequency.
Because adverse reactions are often first detected or
suspected after a vaccine has been introduced into gen-
eral use, observational designs are usually employed to
try to link suspected adverse events to vaccination. The
approaches adopted may include cohort studies, case-
series analyses, and case-control studies. The advan-
tages and disadvantages of each approach and the
methodological issues relevant to case-control studies
are discussed below.
Key papers discussing the use of the case-control
approach in the study of adverse reactions to vaccines
include those by Comstock (21) on the use of case-
control studies in vaccine evaluation, Fine and Chen
(105) on confounding in studies of adverse reactions,
Fine (106) on methodological issues in the evaluation
of vaccine safety, Farrington et al. (107) on different
designs used in the study of adverse reactions, and
much of the literature addressing the controversy over
adverse effects associated with pertussis vaccines (11,
12, 14-16,87, 108-112).
Measurement
The case-control approach may be used to produce
estimates of the ratio of the risk of a specific adverse
by
guest
on
July
13,
2011
Downloaded
from

effect among vaccinated persons to the risk among
unvaccinated persons, based on a comparison of the
proportion vaccinated among cases with the suspected
adverse reaction and the proportion vaccinated among
controls.
The main measurement of interest when assessing
adverse reactions, however, is the frequency of
adverse effects attributable to vaccination among those
vaccinated. This is usually expressed as the number of
adverse reactions induced in a given number of per-
sons vaccinated (subtracting the baseline rate in the
population). This is theoretically straightforward in
cohort studies, since the rates of adverse reactions in
vaccinated and unvaccinated individuals are measured
directly. The rate of induced adverse reactions can be
estimated in a nested case-control study (113), in a
case-control study (102), and in a case series (107) if
the proportion of the population that is vaccinated and
the frequency of the suspected adverse reaction in the
population are known or can be estimated. Thus,
attributable risk = /•(/?- l)/(Rp - p + 1),
where p is the proportion of the population vaccinated,
r is the rate of the putative adverse event in the total
population, and R is the relative risk of the adverse
event in vaccinated individuals compared with unvac-
cinated individuals.
Advantages and disadvantages of the case-control
approach compared with other approaches
The "best" situation in which to investigate whether
or not a suspected adverse reaction is linked to vacci-
nation, using cohort, case-series, or case-control stud-
ies, is one where there is a clearly defined population
with a record of all vaccinations, all instances of the
disease event of interest (potential adverse effect), and
the possibility of linking these back to individuals.
Studies carried out within such a linked data set are
less prone to biases, particularly if the data set contains
information on dates of vaccination and dates of symp-
tom onset and this information was collected before
the link between the vaccine and the putative adverse
event was suspected. Case-control and cohort studies
require that vaccine coverage is not approaching 100
percent. Case series are based on examining vaccina-
tion history in a series of cases only, and this can be
done even if all cases are vaccinated, as long as the
occurrence of the adverse event shows a close tempo-
ral association with vaccination. Farrington et al. (107)
compared the case-series method with the other two
approaches.
The advantage of conducting investigations in pop-
ulations in which vaccination coverage is incomplete
is that it is possible, in theory at least, to study adverse
effects which may occur at any time after vaccination
and which may not show a close temporal relation with
vaccination. The change in risk with time since vacci-
nation may also be studied, but this is not critical in
establishing vaccination as a risk factor for the condi-
tion (whereas it is in the case-series approach). If vac-
cination coverage is very high, there is not a contem-
porary unvaccinated group of sufficient size with
which to compare the frequency of specific conditions,
using either cohort or case-control study designs. It is
in such situations that, with efficacious vaccines, there
may be the most population concern about possible
adverse effects (of vaccination against a disease that
does not occur—because vaccine coverage is so
high!). If the adverse effect does not follow vaccina-
tion after some characteristic time interval but may
occur at any time following vaccination, it may be
very difficult in situations of high vaccine coverage to
establish an association through analytic epidemio-
logic investigations. Ecologic studies or before-versus-
after studies, with all of their potential defects, may be
the only approaches applicable.
Fortunately, many adverse effects which are attribut-
able to vaccination tend to occur during a specific
period after vaccination, and thus the critical epidemio-
logic measure to study is the interval between vaccina-
tion and the onset of the condition under study. If the
interval between vaccination and the presumed adverse
effect is very short (for example, anaphylaxis within a
few minutes of vaccination), the association with vac-
cination may be obvious, but if the adverse effect
occurs days or weeks after vaccination and is not of a
nature which is clearly vaccine-associated, careful epi-
demiologic studies are required to elucidate whether or
not a causal association is a likely explanation.
Cohort and case-control approaches in linked data
sets. Developments in information technology have
facilitated the setting up of both retrospective and
prospective cohort studies for examining the incidence
of specific outcomes in vaccinated and unvaccinated
individuals, through linkage of vaccination records to
databases that record episodes of morbidity (such as
general practitioner and/or hospital records). The pos-
sibility of such record linkage studies exists in various
forms in the United Kingdom (102, 103), in the United
States (100, 113, 114), in some Scandinavian and other
European countries, and among persons in some pri-
vate medical insurance systems. Alternatively, or in
addition, case-control investigations may be conducted
in such settings in the form of "case-control within a
cohort" studies. This kind of circumstance is among
the best in which to conduct epidemiologic studies, be
they cohort or case-control investigations, because the
by
guest
on
July
13,
2011
Downloaded
from

study population is well defined and the medical
records for the population are such that all occurrences
of the disease of interest may be recorded (particularly
if the possible adverse effect is "severe"). The popula-
tion from which to select controls for a case-control
investigation is well defined, and this simplifies the
conduct and interpretation of the research, since many
of the common problems in control selection in case-
control studies are avoided by being able to sample
within the defined cohort (from which the cases are
also derived). If the hypothesis being investigated is
recent, it is better to restrict the study to cases diag-
nosed before the suspicion arose, to minimize the
chance of diagnosis bias (in which cases are more
likely to be diagnosed with the suspected "adverse
reaction" if they were vaccinated). It is still necessary
to control for confounding. If data for the control of
confounding are not available in the data set and must
be collected through interviews or examinations, case-
control studies are cheaper and faster to carry out than
cohort studies, because of the smaller sample size.
In circumstances where vaccination records are not
kept in such a form that they may be directly linked to
subsequent episodes of morbidity, it may still be pos-
sible to conduct case-control studies to detect associa-
tions between possible adverse effects and vaccination
histories. What is necessary in these circumstances is
that it be possible to detect the occurrence of all cases
of the condition putatively associated with vaccination
(or a "representative sample" of such cases) and that
the previous vaccination records of those cases can be
extracted, together with those of suitably chosen con-
trols.
Case-series analysis. Ascertainment of adverse
reactions based on case-series analyses among vacci-
nated persons was proposed by Farrington et al. (107,
115). The method is based on analysis of data on cases
only (with known dates of birth, known histories of
vaccination, and known dates of onset of symptoms)
and examines temporal clustering of events around the
date of vaccination. The approach depends upon hav-
ing accurate information on dates of vaccination and
the dates of onset of the putative adverse effect.
Potential biases arise if a physician's likelihood of
diagnosing the disease under study is influenced by
knowledge of recent vaccination history. The approach
is also potentially vulnerable to biased recall of dates
of vaccination and dates of onset. For example,
patients may tend to report dates of first onset of symp-
toms close to the date of vaccination if they believe
that vaccination caused their disease (or that of their
child). Confounding caused by a factor's being associ-
ated with vaccination and the disease event is avoided,
since the method uses data on vaccinated individuals
only, but factors related to timing of vaccination may
still introduce bias (107). The main limitation of the
case-series method is that it can only identify adverse
reactions that occur after a short and defined period
postvaccination. Farrington et al. present the method
with an example that examines febrile reactions as an
adverse effect of measles-mumps-rubella vaccine in
the United Kingdom (107).
Methodological issues
To associate a specific adverse effect with vaccina-
tion using the case-control approach, it is usually nec-
essary that three conditions hold. Firstly, whether or
not an individual is vaccinated must be independent of
the existence of conditions that may be associated with
the adverse event. Secondly, diagnosis of the event
must be independent of previous vaccination. Thirdly,
for adverse events that are presumed to occur soon
after vaccination, the date of vaccination and the date
of onset of symptoms must be recalled accurately. If
the first condition is not true, confounding can be
introduced. If the others are not true, diagnostic and
recall bias are introduced. These are discussed below.
Confounding and selection of controls. The con-
founding factors that must be taken into account when
assessing adverse effects of vaccination may be differ-
ent from those considered in assessing vaccine effi-
cacy (105). Many social and medical factors are asso-
ciated with avoidance of vaccination or with delaying
vaccination: existing chronic diseases, acute illness,
and high birth order, for example (105). Conditions
which contraindicate vaccination, such as a history of
fits or convulsions, may also be conditions associated
with some potential adverse effects of vaccination.
Unless this is taken into account, an association
between vaccination and the adverse event might be
obscured. Fine and Chen (105) concluded that this is
why the (artifactual) significantly reduced risk of sud-
den infant death after pertussis vaccination has been
found in so many studies, and why the estimated risk
of neurologic disease after pertussis vaccination is
increased when children with previous neurologic
disease are excluded from the analysis. Because the
contraindications for vaccination are similar for many
vaccines, some investigators have examined the
association between the supposed adverse effect of a
vaccine and other vaccines (not thought to be associ-
ated with the adverse effect). The finding of an associ-
ation which is specific for the vaccine under study
strengthens the likelihood that it is a true adverse effect
of the vaccine.
The choice of suitable controls is not always
straightforward, but the principles are the same as
those underlying the selection of controls for assess-
by
guest
on
July
13,
2011
Downloaded
from

ment of the efficacy of a vaccine, taking into account
factors which might confound any association.
Matching is also useful when a reference date for the
disease is needed for controls.
Diagnostic bias. After the hypothesis that a spe-
cific vaccine is associated with a specific adverse
effect has been publicized, there is a chance that cases
of the disease which occur close to the date of vacci-
nation may be preferentially ascertained. To avoid
such diagnosis bias, it is best to try to use cases that
were diagnosed in an already established information
system before the suspicion of a link with vaccination
was raised. If the study must be concurrent, or if the
hypothesis is old, cases should be sought within an
established data set, so that even if diagnosis bias is not
avoided, ascertainment bias is minimized.
Information or recall bias. In some situations, his-
torical information on vaccination might be difficult to
obtain, particularly for the study of adverse events not
closely associated in time with vaccination. For exam-
ple, in two case-control studies examining the associa-
tion of irritable bowel disease and Crohn's disease
with measles vaccination (116, 117), it proved impos-
sible to obtain sufficient information on vaccination
histories, and this component of the studies had to be
abandoned. The association was finally examined in a
third case-control study that was restricted to cases
with a more recent date of birth, for whom it was pos-
sible to collect information on vaccinations from exist-
ing electronic records (118).
Recall bias is introduced when disease status (being
a case or not) influences the likelihood of informa-
tion's being collected correctly. Such bias is usually
eliminated when information on exposure is based on
records collected prior to diagnosis, but it may be a
substantial problem when vaccination history has to be
ascertained directly from the cases and controls or
from their relatives. Biased recall of the date of onset
of the adverse event and the date of vaccination is also
a potential problem when the adverse effect is closely
related in time to vaccination.
CONCLUSION
In summary, the case-control approach is widely
used to complement RCTs in evaluating aspects of the
efficacy of vaccines in routine use, and more rarely to
identify adverse effects of vaccines. In addition to tak-
ing the usual precautions to prevent confounding and
biases in case-control studies, when using this design
to estimate efficacy one should consider the implica-
tions of the timing of infection and of vaccination, and
the mechanism of vaccine protection. In the study of
adverse reactions, efforts should be made to prevent a
previous history of vaccination's biasing the diagnosis
of the event of interest, as well as biased recall of the
date of vaccination or the date of onset of symptoms.
Case-control studies of the efficacy of and adverse
reactions to vaccines are best done in the context of
linked data sets.
ACKNOWLEDGMENTS
The authors thank Professor Paul E. M. Fine for helpful
discussions, especially with respect to the section on adverse
reactions.
REFERENCES
1. Sartwell PE. Retrospective studies: a review for the clinician.
Ann Intern Med 1974;81:381-6.
2. Weiss ES, Kendrick PL. The effectiveness of pertussis vac-
cine: an application of Sargent and Merrell's method of mea-
surement. Am J Hyg 1943;38:306-9.
3. Tuberculosis Prevention Trial. Trial of BCG vaccines in
south India for tuberculosis prevention: first report. Bull
World Health Organ 1979;57:819-27.
4. World Health Organization. BCG vaccination policies.
Geneva, Switzerland: World Health Organization, 1980.
5. Smith PG. Retrospective assessment of the effectiveness of
BCG vaccination against tuberculosis using the case-control
method. Tubercle 1982;63:23-35.
6. Clemens JD, Shapiro ED. Resolving the pneumococcal vac-
cine controversy: are there alternatives to randomized clini-
cal trials? Rev Infect Dis 1984;6:589-600.
7. Fleiss JL. Statistical methods for rates and proportions. New
York, NY: John Wiley and Sons, Inc, 1973.
8. Smith PG, Rodrigues LC, Fine PE. Assessment of the pro-
tective efficacy of vaccines against common diseases using
case-control and cohort studies. Int J Epidemiol 1984; 13:
87-93.
9. Rodrigues L, Kirkwood BR. Case-control design in the study
of common diseases: updates on the demise of the rare dis-
ease assumption and the choice of sampling scheme for con-
trols. Int J Epidemiol 1990; 19:205-13.
10. de Moraes JC, Perkins BA, Camargo MC, et al. Protective
efficacy of a serogroup B meningococcal vaccine in Sao
Paulo, Brazil. Lancet 1992;340:1074-8.
11. Miller DL, Ross EM, Alderslade R, et al. Pertussis immuni-
sation and serious acute neurological illness in children. Br
Med J (Clin Res Ed) 1981;282:1595-9.
12. Bowie C. Lessons from the pertussis vaccine court trial.
Lancet 1990;335:397-9.
13. Judgement no. 1982 L 1812. Susan Loveday suing Dr. G. H.
Renton and The Wellcome Foundation Limited. Before the
Right Honourable Lord Justice Stuart-Smith. London,
England: The High Court of Justice, Queen's Bench
Division, 1988:76.
14. Wentz KR, Marcuse EK. Diphtheria-tetanus-pertussis vac-
cine and serious neurologic illness: an updated review of the
epidemiologic evidence. Pediatrics 1991;87:287-97.
15. Marcuse EK, Wentz KR. The NCES reconsidered: summary
of a 1989 workshop. National Childhood Encephalopathy
Study. Vaccine 1990;8:531-5.
16. American Academy of Pediatrics, Committee on Infectious
Diseases. The relationship between pertussis vaccine and
brain damage: reassessment. Pediatrics 1991;88:397-400.
by
guest
on
July
13,
2011
Downloaded
from

17. Begg N, Miller E. Role of epidemiology in vaccine policy.
Vaccine 1990;8:180-9.
18. Clemens J, Brenner R, Rao M, et al. Evaluating new vaccines
for developing countries: efficacy or effectiveness? JAMA
1996;275:390-7.
19. Fine PE. BCG vaccination against tuberculosis and leprosy.
Br Med Bull 1988;44:691-703.
20. Rodrigues LC, Diwan VK, Wheeler JG. Protective effect of
BCG against tuberculous meningitis and miliary tuberculo-
sis: a meta-analysis. Int J Epidemiol 1993;22:1154—8.
21. Comstock GW. Vaccine evaluation by case-control or
prospective studies. Am J Epidemiol 1990;131:205-7.
22. Strassburg MA, Greenland S, Stephenson TG, et al. Clinical
effectiveness of rubella vaccine in a college population.
Vaccine 1985;3:109-12.
23. Davis RM, Whitman ED, Orenstein WA, et al. A persistent
outbreak of measles despite appropriate prevention and con-
trol measures. Am J Epidemiol 1987;126:438^9.
24. Wassilak SG, Orenstein WA, Strickland PL, et al. Continuing
measles transmission in students despite school-based out-
break control program. Am J Epidemiol 1985; 122:208-17.
25. Harrison LH, Tajkowski C, Croll J, et al. Postlicensure effec-
tiveness of the Haemophilus influenzae type b polysaccha-
ride-Neisseria meningitidis outer-membrane protein complex
conjugate vaccine among Navajo children. J Pediatr
1994; 125:571-6.
26. Shapiro ED, Clemens JD. A controlled evaluation of the pro-
tective efficacy of pneumococcal vaccine for patients at high
risk of serious pneumococcal infections. Ann Intern Med
1984;101:325-30.
27. Rodrigues LC, Noel Gill O, Smith PG. BCG vaccination in
the first year of life protects children of Indian subcontinent
ethnic origin against tuberculosis in England. J Epidemiol
Community Health 1991;45:78-80.
28. Patriarca PA, Weber JA, Parker RA, et al. Risk factors for
outbreaks of influenza in nursing homes: a case-control
study. Am J Epidemiol 1986;124:114-19.
29. Ahmed AE, Nicholson KG, Nguyen-Van-Tam JS. Reduction
in mortality associated with influenza vaccine during
1989-90 epidemic. Lancet 1995;346:591-5.
30. Muliyil J, Nelson KE, Diamond EL. Effect of BCG on the
risk of leprosy in an endemic area: a case control study. Int J
Lepr Other Mycobact Dis 1991;59:229-36.
31. Clemens JD, Stanton BF, Chakraborty J, et al. Measles vac-
cination and childhood mortality in rural Bangladesh. Am J
Epidemiol 1988;128:133O-9.
32. Aaby P, Samb B, Simondon F, et al. Non-specific beneficial
effect of measles immunisation: analysis of mortality studies
from developing countries. BMJ 1995;311:481-5.
33. Foster DA, Talsma A, Furumoto-Dawson A, et al. Influenza
vaccine effectiveness in preventing hospitalization for pneu-
monia in the elderly. Am J Epidemiol 1992; 136:296-307.
34. Clemens JD, Sack DA, Harris JR, et al. Breast feeding and
the risk of severe cholera in rural Bangladeshi children. Am
J Epidemiol 1990; 131:400-11.
35. Halsey NA, Modlin JF, Jabbour JT, et al. Risk factors in sub-
acute sclerosing panencephalitis: a case-control study. Am J
Epidemiol 1980; 111:415-24.
36. Comstock GW. Evaluating vaccination effectiveness and
vaccine efficacy by means of case-control studies. Epidemiol
Rev 1994;16:77-89.
37. Joseph KS, Joseph A. A potential bias in the estimation of
vaccine efficacy through observational study designs.
(Letter). Int J Epidemiol 1989;18:729-31.
38. Greenland S, Frerichs RR. On measures and models for the
effectiveness of vaccines and vaccination programmes. Int J
Epidemiol 1988;17:456-63.
39. Haber M, Orenstein WA, Halloran ME, et al. The effect of
disease prior to an outbreak on estimates of vaccine efficacy
following the outbreak. Am J Epidemiol 1995;141:980-90.
40. Wunsch-Filho V, Moncau JE, Nakao N. Methodological con-
siderations in case-control studies to evaluate BCG vaccine
effectiveness. Int J Epidemiol 1993;22:149-55.
41. Clarkson JA, Fine PE. An assessment of methods for routine
local monitoring of vaccine efficacy, with particular refer-
ence to measles and pertussis. Epidemiol Infect 1987;99:
485-99.
42. Noah N. Transmissible agents. In: Holland WW, Detels R,
Knox G, eds. Oxford textbook of public health. 2nd ed.
Oxford, England: Oxford University Press, 1991.
43. Orenstein WA, Bernier RH, Dondero TJ, et al. Field evalua-
tion of vaccine efficacy. Bull World Health Organ 1985;63:
1055-68.
44. Orenstein WA, Bernier RH, Hinman AR. Assessing vaccine
efficacy in the field: further observations. Epidemiol Rev
988
45. Fine PE. Implications of different study designs for the eval-
uation of acellular pertussis vaccines. Dev Biol Stand
1997;89:123-33.
46. Fine PE, Clarkson JA. Reflections on the efficacy of pertus-
sis vaccines. Rev Infect Dis 1987;9:866-83.
47. Comstock G. Prevention of tuberculosis. Bull Int Union
Tuberc Lung Dis 1990;91:9-ll.
48. Miceli I, de Kantor IN, Colaiacovo D, et al. Evaluation of the
effectiveness of BCG vaccination using the case-control
method in Buenos Aires, Argentina. Int J Epidemiol
1988; 17:629-34.
49. Haber M, Longini IM Jr, Halloran ME. Estimation of vaccine
efficacy in outbreaks of acute infectious diseases. Stat Med
1991; 10:1573-84.
50. Longini IM Jr, Halloran ME, Haber M. Estimation of vaccine
efficacy from epidemics of acute infectious agents under
vaccine-related heterogeneity. Math Biosci 1993;117:
271-81.
51. Farrington CP. The measurement and interpretation of age-
specific vaccine efficacy. Int J Epidemiol 1992;21:1014-20.
52. Halloran ME, Longini IM Jr, Struchiner CJ. Estimability and
interpretation of vaccine efficacy using frailty mixing mod-
els. Am J Epidemiol 1996; 144:83-97.
53. Halloran ME, Haber M, Longini IM Jr. Interpretation and
estimation of vaccine efficacy under heterogeneity. Am J
Epidemiol 1992,136:328-43.
54. Halloran ME, Watelet L, Struchiner CJ. Epidemiologic
effects of vaccines with complex direct effects in an age-
structured population. Math Biosci 1994,121:193-225.
55. Brunet RC, Struchiner CJ, Halloran ME. On the distribution
of vaccine protection under heterogeneous response. Math
Biosci 1993; 116:111-25.
56. Wharton M, Cochi SL, Hutcheson RH, et al. A large outbreak
of mumps in the postvaccine era. J Infect Dis 1988;158:
1253-60.
57. Longini IM Jr, Halloran ME, Haber M, et al. Measuring vac-
cine efficacy from epidemics of acute infectious agents. Stat
Med 1993; 12:249-63.
58. Haber M, Watelet L, Halloran ME. On individual and popu-
lation effectiveness of vaccination. Int J Epidemiol
1995 ;24:1249-60.
59. Haber M, Longini IM Jr, Halloran M. Measures of the effects
of vaccination in a randomly mixing population. Int J
Epidemiol 1991;2O:3OO-1O.
60. Bjune G, Hoiby EA, Gronnesby JK, et al. Effect of outer
membrane vesicle vaccine against group B meningococcal
disease in Norway. Lancet 1991;338:1093-6.
61. Sutherland I, Springett VH. Effectiveness of BCG vaccina-
tion in England and Wales in 1983. Tubercle 1987;68:81-92.
62. Farrington CP. Estimation of vaccine effectiveness using the
screening method. Int J Epidemiol 1993;22:742-6.
63. Moulton LH, Wolff MC, Brenneman G, et al. Case-cohort
analysis of case-coverage studies of vaccine effectiveness.
Am J Epidemiol 1995;142:1000-6.
64. Sims RV, Steinmann WC, McConville JH, et al. The clinical
effectiveness of pneumococcal vaccine in the elderly. Ann
Intern Med 1988; 108:653-7.
65. Gebo KA, Moore RD, Keruly JC, et al. Risk factors for pneu-
by
guest
on
July
13,
2011
Downloaded
from

mococcal disease in human immunodeficiency virus-infected
patients. J Infect Dis 1996;173:857-62.
66. Malfait P, Jataou IM, Jollet MC, et al. Measles epidemic in
the urban community of Niamey: transmission patterns, vac-
cine efficacy and immunization strategies, Niger, 1990 to
1991. Pediatr Infect Dis J 1994;13:38-45.
67. Pinner RW, Onyango F, Perkins BA, et al. Epidemic
meningococcal disease in Nairobi, Kenya, 1989. The
Kenya/Centers for Disease Control (CDC) Meningitis Study
Group. J Infect Dis 1992; 166:359-64.
68. Struchiner CJ, Halloran ME, Robins JM, et al. The behaviour
of common measures of association used to assess a vacci-
nation programme under complex disease transmission pat-
terns—a computer simulation study of malaria vaccines. Int
J Epidemiol 1990;19:187-96.
69. Struchiner CJ, Halloran ME, Spielman A. Modeling malaria
vaccines. I. New uses for old ideas. Math Biosci 1989;
94:87-113.
70. Killewo J, Makwaya C, Munubhi E, et al. The protective
effect of measles vaccine under routine vaccination condi-
tions in Dar es Salaam, Tanzania: a case-control study. Int J
Epidemiol 1991;20:508-14.
71. McDonnell LF, Jorm LR, Patel MS. Measles outbreak in
western Sydney: vaccine failure or failure to vaccinate? Med
JAustl995;162:471-5.
72. Fine PE, Ponnighaus JM, Maine N. The distribution and
implications of BCG scars in northern Malawi. Bull World
Health Organ 1989;67:35^2.
73. Deivanayagam N, Nedunchelian K, Ahamed SS, et al.
Clinical efficacy of trivalent oral poliomyelitis vaccine: a
case-control study. Bull World Health Organ 1993;71:307-9.
74. Balraj V, John TJ, Thomas M, et al. Efficacy of oral
poliovirus vaccine in rural communities of North Arcot
District, India. Int J Epidemiol 1990;19:711-14.
75. Robertson SE, Traverso HP, Drucker JA, et al. Clinical effi-
cacy of a new, enhanced-potency, inactivated poliovirus vac-
cine. Lancet 1988; 1:897-9.
76. Hennessy S, Liu Z, Tsai TF, et al. Effectiveness of live-
attenuated Japanese encephalitis vaccine (SA14-14-2): a
case-control study. Lancet 1996;347:1583-6.
77. Deming MS, Linkins RW, Jaiteh KO, et al. The clinical effi-
cacy of trivalent oral polio vaccine in The Gambia by season
of vaccine administration. J Infect Dis 1997;175(suppl
l):S254-7.
78. Bentsi Enchill AD, Halperin SA, Scott J, et al. Estimates of
the effectiveness of a whole-cell pertussis vaccine from an
outbreak in an immunized population. Vaccine 1997;15:
301-6.
79. Kotb MM, Shouman AE, Mortagy A. Epidemiological eval-
uation of oral polio vaccine efficacy in Cairo. J Egypt Public
Health Assoc 1993;68:617-25.
80. De Serres G, Boulianne N, Meyer F, et al. Measles vaccine
efficacy during an outbreak in a highly vaccinated popula-
tion: incremental increase in protection with age at vaccina-
tion up to 18 months. Epidemiol Infect 1995;115:315-23.
81. Rivest P, Bedard L, Arruda H, et al. Risk factors for measles
and vaccine efficacy during an epidemic in Montreal. Can J
Public Health 1995;86:86-90.
82. Simba DO, Msamanga GI. Measles vaccine effectiveness
under field conditions: a case control study in Tabora region,
Tanzania. Trop Geogr Med 1995;47:197-9.
83. Hull HF, Montes JM, Hays PC. Risk factors for measles vac-
cine failure among immunized students. Pediatrics
1985;76:518-23.
84. Vadheim CM, Greenberg DP, Bordenave N, et al. Risk fac-
tors for invasive Haemophilus influenzae type b in Los
Angeles County children 18-60 months of age. Am J
Epidemiol 1992;136:221-35.
85. Yuan L. Measles outbreak in 31 schools: risk factors for vac-
cine failure and evaluation of a selective revaccination strat-
egy. CMAJ [Can Med Assoc J] 1994;150:1093-8.
86. Sterne JA, Rodrigues LC, Guedes IN. Does the efficacy of
BCG decline with time since vaccination? Int J Tuberc Lung
Dis 1998;2:200-7.
87. Reingold AL, Broome CV, Hightower AW, et al. Age-
specific differences in duration of clinical protection after
vaccination with meningococcal polysaccharide A vaccine.
Lancet 1985;2:114-18.
88. Ahmed AH, Nicholson KG, Nguyen-van Tarn JS, et al.
Effectiveness of influenza vaccine in reducing hospital
admissions during the 1989-90 epidemic. Epidemiol Infect
1997;118:27-33.
89. Greenberg DP, Vadheim CM, Bordenave N, et al. Protective
efficacy of Haemophilus influenzae type b polysaccharide
and conjugate vaccines in children 18 months of age and
older. JAMA 1991;265:987-92.
90. Victora CG, Fuchs SC, Kirkwood BR, et al. Breast-feeding,
nutritional status, and other prognostic factors for dehydra-
tion among young children with diarrhoea in Brazil. Bull
91. Orege PA, Fine PE, Lucas SB, et al. Case-control study of
BCG vaccination as a risk factor for leprosy and tuberculosis
in western Kenya. Int J Lepr Other Mycobact Dis 1993;61:
542-9.
92. Lyons RA, Jones HI, Salmon RL. Successful control of a
school based measles outbreak by immunization. Epidemiol
Infect 1994;113:367-75.
93. Connolly AM, Salmon RL, Lervy B, et al. What are the com-
plications of influenza and can they be prevented?
Experience from the 1989 epidemic of H3N2 influenza A in
general practice. BMJ 1993;306:1452^1.
94. Black SB, Shinefield HR, Hiatt RA, et al. Efficacy of
Haemophilus influenzae type b capsular polysaccharide vac-
cine. Pediatr Infect Dis J 1988,7:149-56.
95. Rajapaksa L. A case control study to assess the efficacy of
measles vaccine. Ceylon Med J 1993;38:178-80.
96. Vadheim CM, Greenberg DP, Eriksen E, et al. Protection pro-
vided by Haemophilus influenzae type b conjugate vaccines
in Los Angeles County: a case-control study. Pediatr Infect
Dis J 1994;13:274-80.
97. Wunsch Filho V, de Castilho EA, Rodrigues LC, et al.
Effectiveness of BCG vaccination against tuberculous
meningitis: a case-control study in Sao Paulo, Brazil. Bull
98. Ramasamy DJ. Field evaluation of trivalent oral polio vac-
cine efficacy in Madras city—a case control study. J
Commun Dis 1994,26:151-5.
99. Salisbury DM, Begg NT. Immunization against infectious
disease. London, England: HMSO, 1996.
100. Chen RT. The complicated task of monitoring vaccine safety.
Public Health Rep 1997; 112:10-20.
101. Beeler J, Varricchio F, Wise R. Thrombocytopenia after
immunization with measles vaccines: review of the Vaccine
Adverse Events Reporting System (1990 to 1994). Pediatr
Infect Dis J 1996;15:88-90.
102. Farrington P, Pugh S, Colville A, et al. A new method for
active surveillance of adverse events froni diphtheria/
tetanus/pertussis and measles/mumps/rubella vaccines.
Lancet 1995;345:567-9.
103. Nash JQ, Chandrakumar M, Farrington CP, et al. Feasibility
study for identifying adverse events attributable to vaccina-
tion by record linkage. Epidemiol Infect 1995; 114:475-80.
104. Wakefield AJ, Murch SH, Anthony A, et al. Ueal-lymphoid-
nodular hyperplasia, non-specific colitis, and pervasive
developmental disorder in children. Lancet 1998;351:
637^1.
105. Fine PE, Chen RT. Confounding in studies of adverse reac-
tions to vaccines. Am J Epidemiol 1992; 136:121-35.
106. Fine PE. Methodological issues in the evaluation and moni-
toring of vaccine safety. Ann N Y Acad Sci 1995;754:30O-8.
107. Farrington CP, Nash J, Miller E. Case series analysis of
adverse reactions to vaccines: a comparative evaluation. Am
J Epidemiol 1996;143:1165-73.
108. Miller D, Madge N, Diamond J, et al. Pertussis immunisation
by
guest
on
July
13,
2011
Downloaded
from

and serious acute neurological illnesses in children. BMJ
1993;307:1171-6.
109. Cherry JD. The epidemiology of pertussis and pertussis
immunization in the United Kingdom and the United States:
a comparative study. Curr Probl Pediatr 1984; 14:1-78.
110. Griffith AH. Permanent brain damage and pertussis vaccina-
tion: is the end of the saga in sight? Vaccine 1989;7:199-210.
111. Sepkowitz S. Perverse reactions to pertussis vaccine by gov-
ernment medical agencies. J Okla State Med Assoc 1996;89:
135-8.
112. Cowan LD, Griffin MR, Howson CP, et al. Acute
encephalopathy and chronic neurological damage after per-
tussis vaccine. Vaccine 1993;11:1371—9.
113. Black S, Shinefield H, Ray P, et al. Risk of hospitalization
because of aseptic meningitis after measles-mumps-rubella
vaccination in one- to two-year-old children: an analysis of
the Vaccine Safety Datalink (VSD) Project. Pediatr Infect
DisJ 1997;16:500-3.
114. Chen RT, Glasser JW, Rhodes PH, et al. Vaccine Safety
Datalink project: a new tool for improving vaccine safety
monitoring in the United States. The Vaccine Safety Datalink
Team. Pediatrics 1997;99:765-73.
115. Farrington CP. Relative incidence estimation from case
series for vaccine safety evaluation. Biometrics 1995;51:
228-35.
116. Thompson NP, Fleming DM, Pounder RE, et al. Crohn's dis-
ease, measles, and measles vaccination: a case-control fail-
ure. (Letter). Lancet 1996;347:263.
117. Thompson NP, Pounder RE, Wakefield AJ. Perinatal and
childhood risk factors for inflammatory bowel disease: a
case-control study. Eur J Gastroenterol Hepatol 1995;7:
385-90.
118. Feeney M, Ciegg A, Winwood P, et al. A case-control study of
measles vaccination and inflammatory bowel disease. The
East Dorset Gastroenterology Group. Lancet 1997;350:764-6.
119. Halloran ME, Longini IM Jr, Struchiner CJ. Design and
interpretation of vaccine field studies. Epidemiol Rev
1999;21:73-88.
by
guest
on
July
13,
2011
Downloaded
from
View publication stats
View publication stats

Case control

Recommandé

Recommandé

Contenu connexe

Tendances

Tendances (19)

Similaire à Case control

Similaire à Case control (20)

Dernier

Dernier (20)

Case control