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Table 9.1 (continued)
Measure Denition Example
Odds Used in a case–control study, this measure denes the
probability (p) of ahealth outcomeoccurring divided
by the probability of the health outcome not occurring
(1−p)*, in a group dened by a characteristic, e.g.
exposure
Odds=numerator (number of cases of the health
outcome)/denominator (number of subjects who did not
have the health outcome)
*when p is very small 1−p is close to p, so odds
approximates risk
Prevalence This measure denes the proportion of a health
outcome at a given period of time, irrespective of new
or pre-existing. It indicates how widespread the health
outcome is at a given time
Prevalence=numerator (number of all casesof the
health outcome)/denominator (total number of
individuals at risk at a particular point in time [termed
point prevalence] (or over a given time (study) period
[termed period prevalence]
The odds of rhabdomyolysis in patients
exposed to a statin for 1year would be
calculated as follows:
numerator (number of patients who had the
diagnosis)/denominator (number of patients
who did not have the diagnosis)
if the probability (p) of rhabdomyolysis is
0.75, then the odds of rhabdomyolysis in this
exposed population is
p/(1−p)=0.75/(1−0.75)=3
The point prevalence of heart disease as
recorded in a primary care database among
men aged 18–65years in England at the start
of 2020 would be calculated as follows:
numerator (number of men with a diagnosis
of heart disease (new or pre-existing)/
denominator (number of men in database at
the start of 2020).The point prevalence of 0.25
indicates that 25% of men within that age
group were affected by heart disease at the
start of 2020.
The period prevalence would be the
proportion of cases of heart disease during
2020
A period prevalence of 0.25 indicates that
25% of men within that age group were
affected by heart disease in that year.
D. Lay ton
When estimating these measures, there is
always uncertainty around that estimate because
the number is based on a sample of the population under study. The condence interval (CI) is
the range of values that one expects the estimate
to fall between a certain percentage of the time if
you repeat the study or re-sample the population
similarly. The 95% CI is often reported—it is
beyond the scope of this chapter to provide details
of the statistical foundation of measuring the
variability of estimates but sufce to say, based
on the normal distribution and that the central
value represents truth, it is assumed that one can
be condent that the estimate reported lies within
the range that spans the true estimate, should the
study be repeated many times.
Measures of association quantify the relationship between two variables—for example,
between a specic exposure and a health outcome (such as an adverse event or adverse drug
reaction), and enable comparisons to be made on
health outcomes between study populations, for
example, between those with a particular exposure and those without. Common measures of
association include the absolute difference or the
relative difference (as a ratio) between risks, rates
or odds (Table9.2).
3.1.2 P-value
The probability (p)-value is used in medical statistics to allow one to make a decision about whether
any differences in the observed effect estimates
may have occurred by chance. It indicates the
strength of evidence against the hypothesis of no
difference (reected by the relevant null values).
The basis of that decision is usually taken to be a
xed value of 0.05. When the p-value is large (and
above this threshold of 0.05), investigators often
report this as statistically non- signicant result and
proceed as if they have proved there is no effect—
but actually this can also demonstrate a failure to
detect a statistically signicant one. There is a relationship between p-value and the CI such that the
95% upper and lower bounds do not include the
9 Pharmacoepidemiologic Studies
Table 9.2 Common measures of association
These estimates should always be reported with 95% condence interval
Measure Denition Example
Risk (rate)
difference
Risk (rate)
ratio (RR)
Odds ratio
(OR)
This measure represents the absolute difference between
two groups and represents the excess risk (or rate)
attributable to the exposure of interest. The value may be
positive indicating higher risk or negative indicating a
protective effect. If the value is zero (referred to as ‘null’
value for a difference), then there is no absolute difference
in effect
Risk difference*=Risk
Rate Difference = Rate
* may also be referred to as Attributable Risk (AR)
**the unexposed group may also be called the reference
group if exposed to an alternative treatment
The relative difference is dened as a ratio of risk (or rate)
in the exposed group to the risk in the unexposed group.
The value may be higher than 1 indicating higher risk or
lower than indicating a protective effect. If the value is 1
(the null value for a ratio), then there is no difference in
effect
Risk ratio***=Risk
*** may also be referred to as Relative Risk(RR)
Rate ratio=Rate
This is a relative measure, that is, the ratio of the odds of an
event in the exposed group to the odds of the same event in
the nonexposed group. The OR can range from zero to
innity. OR>1 indicates exposure increases risk while
OR<1 indicates that exposure is protecting against risk. If
the value is 1 then there is no difference in effect
Odds ratio=Odds of event in exposed group/Odds of event
in unexposed group
exposed
exposed
/Rate
exposed
exposed
/Risk
−Risk
−Rate
unexposed
unexposed**
unexposed**
unexposed
The risk of serious gastrointestinal bleeds
in the rst year after starting treatment is
0.05% for a COX-2 selective inhibitor
(exposure of interest) and 0.1% for
another NSAID (reference group).
The risk difference (attributable risk)
is−0.05% with a 95% CI (−0.07, −0.02)
indicating that since the upper 95% CI
bound does not go above zero (i.e.
−0.02), the exposure of interest is
associated with a protective effect
The rate of deep vein thrombosis in rst
6months after starting treatment is 1.15
per 1000 person-years for a COX-2
selective inhibitor (exposure of interest)
and 0.69 per 1000 person-years for
another NSAID (reference group).
The crude RR is 1.66 and the 95% CI is
(1.16, 2.38), indicating that since the
95% CI does not go below 1, the
exposure of interest is associated with a
higher rate of this adverse event
For a trial comparing a new anticoagulant
to warfarin, the odds of all-cause
mortality for the new anticoagulant was
0.4 and for warfarin the odds was 0.8.
The crude OR is 0.5 and the 95% CI is
(0.4, 0.6), meaning that since the 95% CI
does not go above (1) the odds of death
in those exposed to the new anticoagulant
is 50% less than those exposed to
warfarin
215
null value; it is likely that the observation will be
signicant. The term 5% signicance is often used
in observational epidemiology. For example, consider the hypothetical statement ‘In a cohort study
comparing the risk of rhabdomyolysis between
statin users and non-statin users within the rst 3
months of use, a risk ratio of 4.96 (with a 95%CI of
2.8, 8.7) was reported’. The p-value was p<0.0001.
This would be considered a statistically signicant
result at the 5% level of signicance. However, a
5% signicance level indicates that once in every
20 times a test is undertaken on the same sample,
the result is likely to be signicant by chance alone.
Therefore, there is always the possibility of making
the wrong decision, and one should not rely on an
absolute p-value alone but evaluate this in combination with other information such as clinical signicance and the 95% CI.
3.1.3 Bias
As alluded to in the previous section, the variability of any estimate is an inherent part of the
data being measured and the measurement process. In statistics, the term ‘error’ is used to dene
the difference between a calculated value and the
‘true’ value. It does not imply a mistake. This
error can be divided into two components—random and systematic.
• Random errors: are chance uctuations in the
data through natural variation. It is random,
such that the next measurement cannot be
predicted from the previous value. Natural
variation means that on occasion, measures
may be imprecise (reected by a wide 95%
CI), but it still represents the population
value.
216
• Systematic errors: are introduced through
inaccuracy in the research methodology which
contains some constant ‘offset’ that can occur
reproducibly. Bias is a term used to describe
any systematic error in an epidemiological
study that results in an incorrect estimate of
the association between exposure and risk of
disease. Notably the 95% CI may appear to be
narrow (indicating a precise measure), but it
may still be biased.
Avoidance of random error is inuenced by
using good quality assurance systems to ensure
high internal validity. However, in contrast, the
presence of systematic error is hard to avoid and can
result in a distortion of the study estimate in any
direction. It can lead to an underestimation or overestimation of a measure and cannot be corrected for
at the analysis stage. Bias may occur at any stage of
a study. The presence of bias cannot be determined
internally, and one must look to some sort of external standard. There are many types of bias; however, we will focus on one of the most important for
epidemiological studies—selection bias.
Selection bias occurs when the association
between exposure and disease is different for
those who complete a study compared with those
who are in the target population (this phenomenon is call ‘depletion of susceptibles’); or where
the study members are systematically different
through a sampling method, compared to the
overall population for which the measure of
effect is intended to provide inference about (e.g.
Box 9.2).
Box 9.2 Loss to Follow-Up Bias in Medical
Research
Suppose in a hypothetical cohort study
below, investigators compared the incidence
of myocardial infarction (MI) in 10,000 men
taking an NSAID and 10,000 men not taking an NSAID for 1year. MI occurred in 20
subjects taking the NSAID and in 10 subjects not taking the NSAID, so the unbiased
risk ratio is (20/10,000)/(10/10,000) = 2.0,
D. Lay ton
with the rate ratio as (20/10,000 personyears (pyrs))/10/10,000pyrs)=2.0.
However, suppose there were substantial losses (attrition) to both groups over the
period after entering the study (follow-up)
for any reason, i.e. 6000 in the exposed
group and 4000 in the unexposed group
had less than 1year of follow-up.
This substantially reduces the number
of patients in not only the ‘denominator’
for risk but also the rate. In addition, suppose here was a greater tendency to lose
subjects taking the NSAID who subsequently developed MI.Assume there wasa
loss of 12 diseased subjects in the group
taking NSAIDs (leaving 8 subjects), but
only 2 subjects with MI in the unexposed
group (leaving 8 subjects). In other words,
there is a differential loss between the
groups and there is also a change in
the numerator of cases of MI. This would
result in a biased risk ratio of
(8/10,000)/8(10,000) = 1.0. Remember
the denominator is of persons at risk at the
start of the study which is the same as
before.
However, assuming those subjects that
left contributed an average of 6months of
follow-up time in the year, the denominator
would be less, i.e. in the exposed group,
4000 patients contribute 4000 pyrs but
6000 contribute 3000 pyrs giving a sum of
7000 pyrs, whilst in the unexposed
group 6000 patients contribute 6000 pyrs
and 4000 contribute 2000 pyrs giving a
sum of 8000 pyrs, such that the biased
rate ratio would be (8/7000 pyrs)/
(8/8000pyrs)=1.14.
So in this scenario, whilst there was substantial attrition in both groups, there was
greater loss of diseased patients in the
exposed group than the unexposed group.
For a more detailed understanding of selection
bias and other different types of bias, the reader is
referred to other texts [16, 17].
9 Pharmacoepidemiologic Studies
3.1.4 Confounding
Confounding is another type of systematic error.
It is an important concept because if present it
can also cause an under- or over-estimate of the
association between exposure and an outcome. It
occurs when other factors that are independently
related to both the disease and primary exposure
distort the observed association. The distortion
may be large or even change the direction of the
association effect. It must be understood that it is
rarely only the exposure that is associated with an
outcome and other factors may be associated
with that outcome independent of the exposure.
Therefore, these other factors (called ‘confounders’) need to be accounted for when evaluating
any association. Whilst confounding is a form of
bias which can occur in any epidemiological
study, it can, unlike most bias, be handled in the
analysis of a study. Each potential confounder
should be assessed according to (a) whether it is
a known risk factor for the outcome of interest
and (b) independently associated with the main
exposure of interest (and not caused by it). For
more details, the reader is referred to other texts
[16]. An example of confounding (in the form of
channelling) is given in Box 9.3.
Box 9.3 Channelling and Confounding
In RCTs, the process of randomisation
ensures that the allocation of treatment is
independent of patients’ health characteristics and also balances the prole of health
characteristics between the two groups.
However, pharmacoepidemiological observational studies do not employ randomisation and are thus used in real-world clinical
practice data to compare groups of patients
taking a drug compared to those who do
not. In this situation, it is the patient or their
doctors who choose whether or not to use
the medicine based on clinical need, so
allocation is not random. The indication for
treatment will be related to the choice of
treatment and could be related to any outcome the patient experiences. This phe-
217
nomenon therefore introduces a selection
bias through preferential prescribing of a
drug to subsets of patients who have a different underlying risk to those who are not
exposed to the drug. The validity of then
comparing safety outcomes between the
exposed and unexposed is determined by
the extent to which the observed difference
in the risk of an event between the comparison groups can be attributed to the drug
rather than other factors.
An example of where channelling may
have had a profound effect on the interpretation of safety is that of rofecoxib—this
being an NSAID associated with a lower
risk of gastrointestinal bleeding (through
its selective mechanism of action via inhibition of the cyclooxygenase (COX) 2
enzyme). Rofecoxib and similar NSAIDs
were commonly known as ‘coxibs’ and
were different to NSAIDs that had been
available for many years which did not
demonstrate this selective inhibition [18].
That rofecoxib was advocated as a pharmacologically ‘cleaner’ drug with a reduced
risk of gastrointestinal bleeding resulted in
the product being prescribed in real-world
clinical practice to patients who were considered at high risk of GI bleed [19]. Whilst
this advantage was indeed observed, it was
noted that coxibs were being prescribed
instead of traditional NSAIDs to high
comorbidity patients susceptible to other
types of adverse health outcomes including
those of cardiovascular origin.
Many observational studies were conducted to explore this safety issue, but due to
the type of data available, it was often not
possible to account for differences in baseline
cardiovascular risk between study populations, not only for the prevalence of cardiovascular disease but also for other risk factors
associated with cardiovascular disease. Thus,
missing or partial information on cardiovascular risk factors is likely to have confounded
(distorted) the study ndings [20].
218
Fa
t
Te mporality of association may be established
•
D. Lay ton
3.2 Observational Study Designs
3.2.1 Cross-Sectional Studies
These studies measure the prevalence of health
outcomes (e.g. adverse event or adverse drug
reaction) and/or a particular determinant of
health (e.g. exposure to a drug) at the same point
in time [12] (Fig.9.1). There is no evaluation of
what happens to a patient after that point in time
(or several xed points of time) or what happened to the patient before that point, so no temporal sequence between an exposure and health
outcome can be established. This in turn means
this type of study cannot infer any causal relationship. However, it can offer insights into drug
prescribing or disease burden. This type of
approach may also be used to examine associations between exposure and outcome at the population level for ecological studies. In terms of
applications, this design may be applied for
drug utilisation research—an essential part of
pharmacoepidemiology as it describes the
extent, nature and determinants of drug exposure at the patient level.
How the data are sampled and the response
rate to the survey (if applicable) will determine
the generalisability of results from a crosssectional study to the broader population. The
optimum situation would be the sampling frame
based on the whole population, but for representativeness of the population, responders should
also be representative. If performing an active
survey rather than using existing data, nonresponse is a problem which has been observed for
descriptive safety surveillance studies such as
Prescription-Event Monitoring which relies on
general practitioners to ll out questionnaires
[21].
Case Study 1 (Sect. 7.1) explores the applica-
tion of a cross-sectional design to address a regulatory issue. Concerns of the persistence and
severity of the adverse effects of uoroquinolones, mainly involving the nervous system, muscles and joints, resulted in the 2018 referral
procedure led by the European Medicines Agency
(EMA). They advised to stop prescribing uoroquinolones for infections of mild severity or of a
presumed self-limiting course and for prevention
Looking back into the past (retrospective)
Start with identifying subjects with the
•
exposure of interest at index date and
then identify subjects who do not have
that exposure at index date
•
All subject are examined for presence of
factors in the past; none should have the
outcome previously recorded
All subjects are followed from index date
•
into the future to determine if they develope an outcome
Risks, rates and ratios of risks and rates
•
are reported (+95%Cl)
Temporality of association can be
•
established
ctors present or absent
Fig. 9.1 Overview of cross-sectional, cohort and case–
control study designs
Adapted from: Dupépé, Esther & Kicielinski, Kimberly &
Gordon, Amber & Walters, Beverly. (2019). What is a
TIME (INDEX DATE)
CROSS SECTIONAL STUDY
COHORT STUDY
Exposed
Unexposed
CASE CONTROL STUDY
Following up into the future (prospective)
•
Individuals examined for presence of factors
and outcome at a single point (date) in time
(or an interval between two dates).
Risks (prevalence) and ratio of risks are
•
reported (+95%Cl)
Te mporality of association cannot be
•
established
Particular outcome(s) present or absent
Start with identifying all cases with the outcome
•
at index date and then identify controls without
Case
Control
Case-Control Study? Neurosurgery. 84. 819–826.
10.1093/neuros/nyy590
that outcome at index date sampled from the
same population
Cases and controls examined for presence of
•
factors at index date from information in the pas
Odds Ratios are reported (+95%Cl)
•
9 Pharmacoepidemiologic Studies
219
of infections, plus to restrict prescriptions in
cases of milder infections where other treatment
options are available and restrict in at-risk populations. The drug utilisation study utilised a
cross-sectional approach in the analysis by
estimating uoroquinolone prescribing trends for
each month between 2018 and 2019 [22].
3.2.2 Cohort Studies
Cohort studies can be used to estimate the incidence risk and rate of an event after exposure to a
medicine (see Sect. 3.1.1). They are particularly
suitable for assessing multiple health outcomes
following exposure, especially over a long-term
period. In particular, cohort studies have the
advantage that the temporal relationship between
an exposure (e.g. to a medicine) and an outcome
(e.g. adverse event or adverse drug reaction) can
be established since the selection of the population is based on a particular exposure before the
event has occurred, i.e. at the start of follow-up,
given that all subjects are free of the outcome
(Fig.9.1). Such a study may also be referred to as
a longitudinal study. However, there are several
disadvantages in that cohort studies often require
large sample sizes and possibly a long study
duration especially if the outcomes are rare.
A cohort study may be prospective, which
identies a cohort based on present day and follows a cohort into the future for an outcome,
whilst a retrospective study uses historical information tracing the cohort back in time for exposure information knowing the outcome may have
already occurred (Fig. 9.1). More often retrospective studies will use data that already exists
in data sources such as registries, health insurance claims or primary care clinical practice electronic medical records. In such circumstances,
these data are being re-used, and the term ‘secondary use of data’ is applied to indicate that the
data has not been specically generated for the
study.
In designing a cohort study, as with any study,
a protocol must be developed, and the following
general steps would be used:
• After dening the research aims and objec-
tives, the investigator should identify all of the
criteria that would be used to characterise the
population at risk, the exposure and the outcomes. This may be through code lists if using
secondary data sources.
• Once the general framework of the desired
characteristics is dened, the investigator
must identify the best source data that are t
for purpose to address the research question
(see Sect. 5.3). The source data should be generalisable to the region or country to which the
result would apply.
• From that data source, the study subjects at
risk of the outcome and who would be treated
with the medicine of interest will be identied. The investigator should construct relevant inclusion criteria and minimal inclusion
criteria to identify the eligible study population using the characteristics previously
dened. Since not all subjects within that data
source may be used, the selection of subjects
from the data source should ideally be representative of the data source and also the target
population to which the results would apply.
• If the study aims to contextualise the risk or
rate of the outcome(s) against, e.g. another
drug or subjectsunexposed to the medicine of
interest, two or more groups of subjects
(referred to as study cohorts) that differ according to their exposure may be identied. In this
scenario, the measure of effect (ratio of risks or
rates—see Sect. 3.1.1) can be calculated.
• The study investigator should dene the relevant calendar period to capture all data (this
dening study start and stop date). In addition,
the length of time that each study subject
should be observed from rst exposure to the
medicine (dened as index date) should be
dened, including the criteria that outline
what to do when a patient can no longer be
followed (called censoring). Each group
(exposed to a medicine or not) should be followed from index date with sufcient time to
observe the occurrence of the outcome(s) of
interest, should it occur. For example, if an
event only occurs after 6 months, then subjects should be observed for at least 7months
in order for information for that event to be
captured, should it occur.
• The study investigator should also dene how
far back records will be examined to dene
220
D. Lay ton
clinical characteristics at index date for each
cohort (termed ‘look back’); often a minimum
of 12months is needed.
• The statistical analysis plan should not only
include how the risk and rate (or risk or rate
ratio) will be calculated but also how to best
account for other characteristics that may be
associated with the outcome itself (risk factors) or characteristics that may be associated
with both exposure and the outcome (confounders). The study investigator should dene
appropriate statistical modelling approaches
for ‘adjusting’ for these variables. In this sense,
to adjust is to try and balance the groups in
terms of particular characteristics so that any
effect of a particular characteristic is effectively reduced. Various methods exist, and it is
beyond the scope of this chapter to review
these [23]. In addition, the study investigator
should consider how to test the robustness of
any results. This may be through examining
model diagnostics and/or conducting sensitivity analyses whereby, for example, denitions
of variables or follow-up time may be modied
to see if the results change in any way.
• Finally the study investigator should consider
all of the possible biases and sources of error
that may affect the study conduct and/or results.
By identifying as many in advance as possible,
steps can be put in place to reduce that risk.
However, sometimes risks that occur are beyond
the control of the study investigator.
Case Study 2 (Sect. 7.2) explores the application
of a cohort study design for contextualisation of
safety signals arising from spontaneous reporting
data. A particular concern arose regarding thrombotic events, with concurrent thrombocytopenia
reported among individuals vaccinated with adenovirus-based vaccines against SARS- CoV- 2. As of
May 26, 2021, 348 spontaneous reports of major
thromboembolic events with thrombocytopenia had
been documented following 24 million rst doses
and 13 million second doses of an adenovirus-based
COVID-19 vaccine in the UK.Although fewer concerns have been raised about safety signals for an
mRNA-based COVID-19 vaccine, instances of
immune thrombocytopenia had also been observed
among recipients of this vaccine. In this cohort
study, the authors estimated the incidence of thrombosis, thrombocytopenia and thrombosis with
thrombocytopenia over the 28days following a rst
dose of the an adenovirus-based COVID-19 vaccine
and an mRNA-based COVID-19 vaccine and compared these rates with historical, pre-pandemic rates
in the general population [24].
3.2.3 Case–Control Study
Case–control studies are particularly useful if
investigating whether there is an association
between a medicinal product (or several products)
and a rare outcome (e.g. a specic rare adverse
event), as well as to identify other multiple risk
factors for that rare outcome. Advantages of a
case–control study include a computational efciency far superior to the cohort design, the possibility to initiate a study based on a set of cases
already identied (e.g. in a hospital); they require
fewer subjects and are less expensive to conduct.
In contrast to a cohort study (whereby the investigator identies a subject based on exposure before
the event has occurred), in a case–control study,
the investigator identies subjects on the basis of
whether they had the event (cases) and looks
backwards to examine a range of factors including exposures to medicines that may have contributed to being a case (Fig.9.1). Thus, case–control
studies are usually retrospective. However, in
order to make any meaningful interpretation, the
distribution of these factors must also be examined for subjects who originate from the same
population as cases but do not have the event
called (controls). In contrast to cohort studies,
case–control studies do not measure incidence
because of the sampling method (see below), so
only the ‘relative’ size of a measure of disease frequency can be estimated, namely the odds of a
case being exposed to a particular factor (medication) can be compared to the odds of a control
being exposed to that same factor and the odds
ratio calculated (see Sect. 3.1.1).
In designing a case–control study, whilst some
common steps overall should be followed as outlined for the design of a cohort study (protocol,
data feasibility and possible bias/sources of error),
some different aspects should be considered:
9 Pharmacoepidemiologic Studies
221
• After dening the research aims and objectives, the investigator should identify all of the
criteria that would be used to dene the case
andany risk factors (including exposures) that
need to be investigated.
• From the chosen data source, the study subjects who are cases will be identied. The
investigator should construct relevant inclusion criteria and minimal inclusion criteria to
identify the eligible case population using the
characteristics previously dened.
• An important aspect that the investigator must
specify is how the ‘control’ subjects who are
not cases will be sampled from the same source
from which the cases originate. Controls
should be as comparable as possible (termed
‘counterfactual’) to the cases with the only
exception being that they are not a case. In
order to do this, a process of ‘matching’ is necessary. For each case, the investigator should
specify how many controls are desired per case
and the factors to match on. Through a random
allocation process, a pseudo-case date is created for each control. Generally matching factors are measured at this pseudo- index date
and are most often those for which the confounding effect is well known, e.g. age (often
±5 year age bands), sex and calendar time.
This creates a set of eligible controls for each
case; this group of cases and controls is called
a ‘risk set’.Although this matching may help
to control for some unmeasured confounders
making cases and controls more similar, it may
also introduce a distribution of that matching
factor in the study population that is different
to the overall source population which itself
can reduce generalisability to other populations. Once a risk set has been created, further
renement of the risk set may be specied, e.g.
matching on several other factors using methods such as propensity scores [23]. Up to 10
controls per case can be used.
• As for the cohort study, the study investigator
should dene the relevant calendar period to
capture all data (thus dening study start and
stop date). In addition, the length of time that
each study subject should be observed historically (the look back period) should be dened
up to the date of the matched event date. This
should be relevant to the outcome, for example, ifan important risk factor could be longterm exposure to a drug, the look back period
should be sufciently long enough to capture
such exposure, should it have occurred for
both cases and controls. The creation of these
risk sets also requires a specic analytical
approach called conditional logistic regression modelling which the study investigator
should specify, along with other risk factors
and confounders that should be adjusted for,
excluding the matching factors.
However, there are some important limitations. Because of the way that the study population is assembled, there is risk of differential
sampling ofcases and controls suchthat the distribution of exposure categories among controls
is nota valid representation of the distribution
of exposure in the source population.
Furthermore, being retrospective in nature, such
studies are subject to recall bias, where knowledge regarding exposure or other risk factors
may not be accurately recalled by participants
or care providers or recorded in the databases.
Another disadvantage is the difculty to study
very rare exposures, as a large sample of cases
and controls would be needed to identify
exposed groups large enough for the planned
statistical analysis.
In order to increase the efciency of exposure
assessment in case–control studies, an alternative
approach is a design in which the source population is a cohort. The nested case–control design
includes all cases occurring in the cohort and a
pre-specied number of controls randomly chosen
from the population at risk at each time a case (or
other relevant event) occurs [25]. Another study
design, a case–cohort study includes all cases and
a randomly selected sub-cohort from the population at risk [26]. Advantages of such designs are to
allow the conduct of a set of case–control studies
from a single cohort and use efciently electronic
healthcare records (EHRs) databases where data
on exposures and outcomes are already available.
Case Study 3 (Sect. 7.3) explores the application
of a case–control study that has been nested within
a cohort study for purposes of further exploring a
safety signal (termed signal strengthening).
222
D. Lay ton
Selective serotonin re-uptake inhibitors (SSRI) are
associated with an increased risk of bleeding, most
notably upper gastrointestinal bleeding [27]. Results
from the Women’s Health Initiative Study suggest a
doubling in the risk of haemorrhagic stroke amongst
post-menopausal SSRI recipients [28]. This nested
case–control study aimed to investigate whether
SSRI use was associated with an increased risk of
haemorrhagic stroke [29].
4 Real-World Data Sources
Two of the three case studies presented in Sect.
3.2 were conducted in more than one data source.
EHRs, population-based registries and health
insurance administrative databases are now being
used extensively via linkage to other data sources
or via a network across many countries for pharmacoepidemiological studies [30]. These systems
take advantage of record linkage to provide rapid
access to thousands of patients and thus reduce
the time and expense required to explore relationships between drug exposure and outcomes.
Collaborations for multi-database studies have
been embraced by regulators, marketing authorisations and researchers alike in providing realworld data for the generation of decision-grade
evidence for benet–risk assessment of licensed
medicines. For example, DARWIN EU is a federated network involving several databases that is
supported by the EMA and designed to engage in
rapid analytics of safety concerns identied by the
EMA that warrant urgent investigation [31].
The European Network of Centres for
Pharmacoepidemiology and Pharmacovigilance
(ENCePP) is an initiative that brings together
expertise and resources in pharmacoepidemiology
and pharmacovigilance across Europe. ENCePP is
coordinated by the EMA, and its aim is to
strengthen the monitoring of the benet:risk balance of medicinal products. This is achieved by
facilitating the conduct of high-quality, multicentre, independent PASS with a focus on observational research. ENCePP is composed of
research centres and networks referred to as
‘ENCePP partners’, and participation in ENCePP
is voluntary. ENCePP is globally acknowledged
for its expertise and outputs [32]. A meta-data cat-
alogue (the ENCePP Resources Database) was
developed as a publicly available electronic index
of available European research organisations, networks and data sources, in the elds of pharmacoepidemiology and pharmacovigilance [33]. It
included information on expertise and research
experience across the region and serves as a hub
for both researchers and study sponsors seeking to
identify organisations and datasets for conducting
specic pharmacoepidemiology and pharmacovigilance studies in Europe.This has beenreplaced
in 2024 by the new EMA-HMA Catalogues of
data sources and non- interventional studies.
According to the ENCePP methodological
guide [30], the advantages of using multidatabase designs over single databases include:
• An increase in the size of the study popula-
tions. This especially facilitates research on
rare events, drugs used in specialised settings
or when the interest is in subgroup effects.
• Exploitation of the heterogeneity of treatment
options across countries, which allows studying
the effect of different drugs used for the same
indication or specic patterns of utilisation.
• Exploitation of the differences in outcome/
event rates across countries/regions.
• Provision of additional knowledge on the gen-
eralisability of results and on the consistency
of association, for instance whether a safety
issue can be identied in several countries.
• Engagement of experts from various countries
addressing case denitions, terminologies,
coding in databases and research practices
provides opportunities to increase consistency
of results of observational studies.
• In the case of primary data collection, shorten-
ing the time needed for obtaining the desired
sample size and therefore accelerating investi-
gation of drug safety issues or other outcomes.
Disadvantages relate to data access due to data
protection rules as well as the need for standardisation and harmonisation of data architecture to support the pooling of data (or results). Over the last
decade, the number of common data models (CDM)
that facilitate such harmonisation has grown [34].
An example of a collaborative research network that
includes EU databases that uses a generalised CDM
9 Pharmacoepidemiologic Studies
223
is Observational Health Data Sciences and
Informatics (OHDSI) (www.ohdsi.org). Through
an open science community (European Health Data
& Evidence Network (EHDEN) www. www.ehden.
eu), many EU databases that participate within
OHDSI have been mapped according to the
Observational Medical Outcomes Partnership
(OMOP) CDM used by OHDSI independent of a
study, supported by rigorous quality assurance procedures [27]. When a study is required, a common
protocol is developed and a centrally created analysis programme is created that runs locally on each
database to extract and analyse the data. The output
of the common programmes shared may be an analytical dataset or study estimates, depending on the
governance of the network [34].
5 A Prospective Look at
Pharmacoepidemiology:
Quality, Transparency
andReproducibility
During one’s career as a healthcare professional,
for making decisions about appropriate use of
medicines for a patient, one must evaluate published evidence and guidelines and has to make
decisions on what constitutes reliable quality evidence on the safety of medicines. With the
increasing availability of EMR, there has been a
global expansion of observational research.
However, in parallel, there have been numerous
examples of failures due to poor quality research
that has cast a huge shadow on the acceptability
of evidence from observational studies [35, 36].
As we navigate the journey from real-world
data to real-world evidence, one needs to establish condence that the evidence is of sufcient
quality, so we must ask ourselves questions such
as the following: Given imperfect data, how do
we know if the data are of sufcient quality and
t for purpose? Are the generation, recording,
verication, analysis and reporting of results
accurate enough? Has quality been managed
through all stages of the study?
However, quality is not a singular concept that
can be directly observed, and researchers must
still make judgements about the reliability of
study ndings. Methods must be developed to
measure and manage quality. The ideal is to have
in place a quality management system that can
apply a risk-based approach—both at the system
level (e.g. the computerised system) and at the
study level (e.g. are the data to be used and is the
study design appropriate to answer the research
question). There is no singular denition for
quality; however, one can consider the attributes
(Box 9.4) that describe quality along the continuum of evidence creation [37].
Box 9.4 Desired Attributes of Reliable
Quality Evidence [37]
Repeatable For the same question, one gets
identical results when applying
the same analysis to the same
data by the same researcher
Reproducible For the same question, a different
researcher should get the same
results as another researcher
when applying the same analysis
to the same data
Replicable For the same question, the same
(or a different researcher) should
get similar results when applying
the same analysis to a different
dataset data
Generalisable For the same question conducted
across several databases, similar
results are observed when
applying the same analysis,
despite anticipated heterogeneity
Robust For the same question, results
are not overly sensitive to
subjective choices made within
an analysis
Calibrated The performance of any
evidence-generating system
should be veried
With many stakeholders having a vested interest in generating quality evidence from pharmacoepidemiological studies, the construction and
harmonisation of processes supporting the continuum are rmly underway. What follows are summary descriptions of only a few notable initiatives
in the EU; there are many others, and it is beyond
the scope of this chapter to present them all.
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