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The risk of infection associated with tumor necrosis factor ╨Ю┬▒ antagonistsMaking sense of epidemiologic evidence.

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Vol. 58, No. 4, April 2008, pp 919–928
DOI 10.1002/art.23396
© 2008, American College of Rheumatology
The Risk of Infection Associated With
Tumor Necrosis Factor ␣ Antagonists
Making Sense of Epidemiologic Evidence
Daniel H. Solomon,1 Mark Lunt,2 and Sebastian Schneeweiss1
full spectrum of benefits and risks of a drug in routine
There have been several epidemiologic studies
regarding the association of TNF␣ antagonists with
infections, as summarized in Table 1 (3–9). On first
glance, the studies seem similar in their population
composition and in the choice of comparator drugs, but
the results vary meaningfully. Three studies found no
increase in the risk of bacterial infection associated with
use of TNF␣ antagonists as compared with methotrexate, whereas 3 studies showed a statistically significant
increase in infection risk. Does this seemingly inconsistent data from the literature suggest an inherent weakness in the methodologies used? Or, as we would
suggest, are the studies different in subtle, but important, methodologic aspects, so that they are actually
addressing different study questions? This review examines key methodologic issues in pharmacoepidemiologic
studies of TNF␣ antagonists and the related risk of
infections, and weighs the strengths and weaknesses of
each study to provide a more coherent framework for
understanding these issues.
The data suggesting that tumor necrosis factor ␣
(TNF␣) antagonists are associated with certain opportunistic infections seem quite strong; however, the association of these agents with typical bacterial infections is
less clear. Since bacterial infections are much more
common than opportunistic infections, defining this
potential risk is clinically important. Although one metaanalysis found an increased risk of infection with the use
of these agents as compared with methotrexate, the
limitations of that systematic review have been well
described (1). Randomized controlled trials are the gold
standard for defining the efficacy of a drug or for
determining how beneficial a drug can be in ideal
circumstances. However, trials often are conducted in
highly selected populations for short durations and in
very controlled settings. Not only can the benefits of a
particular drug be much different in a routine care
setting than in a randomized controlled trial, but also the
full range of adverse events related to a drug is rarely
observed in a randomized controlled trial during the
premarketing stage (2). Thus, epidemiologic studies may
offer important complementary information about the
Exposure risk window
Daniel H. Solomon, MD, MPH, Sebastian Schneeweiss, MD,
ScD: Brigham and Women’s Hospital, and Harvard Medical School,
Boston, Massachusetts; 2Mark Lunt, PhD: University of Manchester,
Manchester, UK.
Dr. Solomon has served in the last year as an unpaid member
of the advisory boards of Abbott and Amgen; he has received research
grants in the last 2 years from Pfizer and Savient. Dr. Schneeweiss has
received consulting fees, speaking fees, and/or honoraria (less than
$10,000) from HealthCore and (more than $10,000) from i3 Drug
Address correspondence and reprint requests to Daniel H.
Solomon, MD, MPH, Brigham and Women’s Hospital, Division of
Rheumatology, Immunology and Allergy, 75 Francis Street, Boston,
MA 02115. E-mail:
Submitted for publication October 22, 2007; accepted in
revised form December 20, 2007.
The exposure risk window refers to the period
during which a given drug may be causing the (toxicityrelated) outcome of interest, either because the drug is
physically still present in the body (pharmacokinetic
presence) or because the drug is acting through more
indirect physiologic pathways (pharmacodynamics). In
our example, the characterization of the exposure risk
window should be based on the presumed underlying
biologic link between TNF␣ antagonist exposure and
infection. This relationship is poorly understood, and
assumptions need to be made about when to begin and
when to end the exposure risk window.
National Data Bank for
Rheumatic Diseases
British Society of
Rheumatology Biologics
Commercial insurance
Medicare beneficiaries 65
years and older
British Society of
Rheumatology Biologics
Commercial insurance
Wolfe, 2006 (4)
No. of
Hospitalized with infection,
death, or requiring IV
Hospitalized with infection
or requiring IV antibiotics
Hospitalized with infection,
death, or requiring IV
Hospitalized with infection
or requiring IV antibiotics
Hospitalized with infection
Hospitalized with pneumonia
Hospitalized with infection
End point
Absence of drug
of interest†
Drug-specific adjusted relative risk
(95% confidence interval)
etan. 1.55 (0.73–3.34); inflix. 2.41 (1.23–4.70)§
TNF␣ 1.30 (0.93–1.78); TNF␣ 4.6 (1.8–11.9)‡
TNF␣ 1.0 (0.60–1.67)
TNF␣ 1.94 (1.32–2.83)
ada. 1.1 (0.6–1.9); etan. 0.8 (0.6–1.1); inflix. 1.1
ada. 1.07 (0.67–1.72); etan. 0.97 (0.63–1.50);
inflix. 1.04 (0.68–1.61)
etan. 2.16 (0.9–5.4); inflix. 2.13 (0.8–5.5)
* DMARD ⫽ disease-modifying antirheumatic drug; etan. ⫽ etanercept; inflix. ⫽ infliximab; ada. ⫽ adalimumab; IV ⫽ intravenous.
† For example, adalimumab was compared with no adalimumab.
‡ The first TNF␣ study included a 90-day extension period, while the second assessed only the initial 90 days of exposure.
§ Assessed only the initial 180 days of exposure.
Curtis, 2007 (9)
Dixon, 2007 (8)
Schneeweiss, 2007 (6)
Curtis, 2007 (7)
Dixon, 2006 (5)
German Biologics Registry
Study population
Listing, 2005 (3)
First author, year
Table 1. Summary of major epidemiologic cohort studies of the risk of infection associated with tumor necrosis factor ␣ (TNF␣) antagonists among patients with rheumatoid
Figure 1. Exposure risk windows. The exposure risk window refers to
the period during which a subject would be considered exposed and at
risk for the outcome of interest. The start and end of the exposure risk
window can be defined in many different ways, based on the biologic
features of the potential drug–outcome association. A–D illustrate
several options associated with the use of tumor necrosis factor ␣
(TNF␣) antagonists. A, An exposure risk window with no lag period
would begin immediately with the first use of the medication. This may
be a reasonable assumption for an outcome such as infection, but may
not be reasonable for a malignancy with a longer induction time. B, An
exposure risk window with a lag period would begin after a defined
period of delay. This may be more appropriate if the relationship
between drug and outcome is assumed to be of slower onset. C, An
exposure “washout” risk window would have a brief period of extension after a drug has been discontinued, to account for the period when
a drug is still biologically active in the body. D, An indefinite exposure
risk window would be assumed to continue indefinitely after the
cessation of the drug; this may be a useful assumption for an outcome
such as malignancy.
One might assume that the risk of infection
begins with the first dosage of a TNF␣ antagonist
(Figure 1A). This would seem to be a reasonable
assumption, based on prior case series regarding mycobacterial infections among patients taking TNF␣ antagonists (10). However, in other drug–toxicity relationships, there may be a lag period between drug initiation
and onset of risk (Figure 1B). In such instances, events
that occur prior to the onset of the exposure risk window
(i.e., before the end of the lag period) should not be
considered to be outcomes related to the study treatment. When taking into account lagged exposure risk
windows, it is presumed that one knows when a drug was
initiated. This is not the case when patients on long-term
treatment, without a known start date, are allowed in an
There is a similar set of questions regarding the
end of the exposure risk window after the last dosage of
drug. The risk might continue for some period after the
last dosage is fully washed out of the body, i.e., several
half-lives of a given drug (Figure 1C); this might be as
long as 4–6 months for a drug like infliximab. In fact,
with rituximab, this washout period might be much
longer. Conversely, the risk might be indefinite, especially if one is considering indolent outcomes, such as
osteomyelitis or cancers developing as a result of genetic
damage caused by a given drug (Figure 1D).
Defining an extended exposure risk window incorrectly results in falsely attributing nonexposed cases
to the study exposure, leading to overestimated risk
ratios. Conversely, if the time period of the window is
too short, valid cases might be missed, leading to underestimation of a causal effect. In practice there is no
algorithm to classify exposure 100% correctly. The
choice of strategy depends on whether one needs to be
more concerned about falsely classifying the person-time
period as exposed or as unexposed, and also depends on
the pharmacologic aspects of the hypothesized drug
Comparator drug
Most epidemiologic analyses of drug safety focus
on the relative risk associated with use of a given
medication compared with a comparator drug with the
same or similar indication. In the example of TNF␣
antagonists, most analyses use methotrexate or nonbiologic disease-modifying antirheumatic drugs (DMARDs)
as the comparator drugs. Ideal comparator drugs are
those that have the same indication as the study drug
and that might be used interchangeably, so that the
physician’s choice of drugs is almost random (11). If the
population receiving the drug of interest (i.e., TNF␣
antagonists) and the population with the comparator
exposure (i.e., nonbiologic DMARDs) differ in clinical
characteristics that could be predictive of the study
outcome, then confounding will bias the results. In such
circumstances, statistical adjustments are required.
If the reference group for patients taking TNF␣
antagonists is those who do not take TNF␣ antagonists
(i.e., “nonusers”), then the patient populations being
compared may not be similar. Such nonusers of TNF␣
antagonists may include patients who are taking only
nonsteroidal antiinflammatory drugs (NSAIDs), since
they would have very mild rheumatoid arthritis (RA).
Because disease severity may be related to the risk of
infection (12), and because this is difficult to measure
and completely adjust for in multivariable models, non-
user comparison groups may cause intractable confounding. The use of methotrexate as a comparator drug
may be more appropriate in cases in which, for example,
RA patients taking methotrexate have disease activity
that is similar to that in patients taking TNF␣ antagonists. Such a comparison group may still result in
noncomparable exposure groups. Requiring that the
comparators be between those who have switched from
one DMARD to methotrexate and those who have
switched from a DMARD to a TNF␣ antagonist might
further improve the balance in disease activity between
Drug initiator versus ongoing user cohorts
The relative risk of an unintended event often
varies during the course of therapy. Several of the
epidemiologic studies of TNF␣ antagonists and infection
suggest that the relative risk of infections is highest
shortly after treatment initiation and then drops over
time (8,9). Such a time-varying hazard function is typical
in settings in which adverse effects related to a drug are
recognized quickly, which leads to patients being removed from the cohort because of drug discontinuation,
resulting in a remaining cohort of “survivors” (13). This
has implications in choosing the study cohort, which
could include either patients who have recently started
the drug (“drug initiators”) or patients who have been
continuing to receive the treatment for some time
(“ongoing users”) (Figure 2).
Drug initiators are defined as patients for whom
there is no recent use of a given drug, i.e., within the
preceding 6–12 months, whereas ongoing users are those
who have been taking a given drug for some time
immediately prior to entering the study cohort. If infections tend to occur shortly after treatment initiation,
then a cohort of ongoing (long-term) users would cause
the risk of infection experienced by drug initiators to
become mixed with that experienced by long-term users,
diluting the effect of the early increased risk. Moreover,
if patients in the TNF␣ antagonist cohort are initiators,
while those in the comparison group are ongoing users,
this may lead to an overestimation of the risk with TNF␣
antagonists. Drug initiator cohorts have the additional
advantage of a clearly defined temporality of baseline
characteristics and treatment. In such a design, patient
characteristics are assessed before drug initiation, and
are therefore not the consequence of treatment but
predictors thereof.
Because pure placebo-controlled trials in RA
would be unethical, randomized controlled trials of
Figure 2. Comparison of drug initiator and ongoing user designs.
Because of the time-varying risk of most adverse events, the most valid
way of assessing whether a drug may “cause” a specific adverse event
is the drug initiator design. However, other designs for assessing the
risk associated with use of tumor necrosis factor ␣ (TNF␣) antagonists
are also available (A–D). A, Typical randomized controlled trial (RCT)
design. Patients taking methotrexate (MTX) are randomized (R) to
receive either placebo (Pbo) or a TNF␣ antagonist. This design is very
useful for assessing the efficacy of TNF␣ antagonists in comparison
with placebo. However, since initiators of a TNF␣ antagonist are
being compared with long-term users of MTX, the design may not
be as useful for examining the potential of a TNF␣ antagonist to
have adverse effects. B, Epidemiologic version of the RCT design.
Patients taking a disease-modifying antirheumatic drug at baseline
(DMARDold) either continue on the DMARDold monotherapy or add
or substitute a TNF␣ antagonist in the regimen. C, Drug initiator
design. Patients taking a DMARD at baseline then either switch to
monotherapy with a new DMARD (DMARDnew) or add or substitute
a TNF␣ antagonist. The design in B compares drug initiators with drug
initiators, whereas that in C compares drug initiators with new users
and is therefore less subject to bias. D, A version of the drug initiator
design. Patients with no prior use of a DMARD start treatment with a
TNF␣ antagonist and/or a DMARD or start treatment with a comparator drug (DMARDnew). While the scenario in D may be less
common, this possibility should be considered. C ⫽ cohort.
TNF␣ antagonists frequently add active treatment or
placebo to a background of methotrexate. Thus, initiators of a TNF␣ antagonist are compared with ongoing
users of methotrexate (Figure 2A). Although epidemiologic studies can mimic the randomized controlled trial
design (Figure 2B), recommendations for pharmacoepidemiologic studies suggest using cohorts of initiators of
both the study drug (i.e., TNF␣ antagonists) and the
comparator drug (Figures 2C and D), to minimize bias
Combination therapy
Combination therapy is the rule and not the
exception in RA therapy. In fact, TNF␣ antagonists were
approved for use in RA in combination with other
DMARDs. How should one estimate the independent
risk of infection from a TNF␣ antagonist when it is used
so commonly in combination with other therapies that
also might contribute to an infection risk? Moreover,
how can the relative risk from different combinations be
appropriately communicated to physicians and patients?
Several different analytic approaches have been
considered for patients taking a TNF␣ antagonist in
combination with other treatments. The most straightforward approach analytically may be the least clear to
interpret. This involves assigning each exposure,
whether mono- or combination therapy, into separate
exposure categories. Thus, for a patient taking a TNF␣
antagonist, methotrexate, and a glucocorticoid simultaneously, all 3 exposure categories would contribute to
the risk estimates in the multivariable model, allowing
one to estimate the independent effects of each exposure compared with all other exposures. This approach is
complicated to interpret for readers, since it creates a
“floating” reference group that changes with each relative risk estimate.
Another relatively straightforward approach is to
represent combination therapy explicitly as a specific
exposure group. Thus, during the time that patients are
simultaneously taking a TNF␣ antagonist, methotrexate,
and a glucocorticoid, they would be represented in an
exposure group for this specific combination. This allows
the combinations to be compared with a fixed and
well-defined comparator group. As many combinations
as necessary could be defined. This approach is most
useful if there are several dominant combinations of
treatments, thus allowing a reader to identify the relative
risk associated with a combination exposure group of
interest. This is the case with TNF␣ antagonists and
combination treatment with a nonbiologic DMARD
such as methotrexate. Group sizes can get small when
patients switch to different drugs often or when there are
no dominant combination regimens.
Another approach is to consider a hierarchy of
exposures, such that patients taking a TNF␣ antagonist,
methotrexate, and a glucocorticoid are only represented
in the TNF␣ antagonists category. This approach is
problematic, since patients in the TNF␣ antagonists
Figure 3. Potential confounders in the relationship between tumor
necrosis factor ␣ (TNF␣) antagonists and infection. A confounder is a
variable that is associated with both an exposure of interest, such as a
TNF␣ antagonist, and an outcome, such as infection. The confounder
is not an intermediate variable on the causal pathway between the
exposure and the outcome, but instead has an independent relationship with both. Important potential confounders in the TNF␣
antagonist–infection relationship include disease activity or severity,
such as in patients with rheumatoid arthritis, as well as comorbid
conditions, such as in patients with diabetes.
category are actually heterogeneous in their exposures,
with some of these patients taking TNF␣ antagonist
monotherapy and others taking a variety of combinations that include a TNF␣ antagonist. Nevertheless, this
approach might be useful if there are only a few cases in
the treatment group of interest and one wishes to
broaden the group.
Control for potential confounding
Confounding is the bane of pharmacoepidemiology. It refers to the potential for a third factor to be a
predictor of treatment choice and to be an independent
risk factor for the study outcome. If we consider the
example of TNF␣ antagonists and infection, one can
imagine several possible potential confounders, such as
age, disease severity, and comorbidities (Figure 3). For
example, patients with worse disease activity are more
likely to be prescribed a TNF␣ antagonist, and they also
appear more likely to develop infections independent of
treatment (12). Thus, the relationship between TNF␣
antagonists and infection may be explained by disease
severity, which could cause doctors to differentially
prescribe (“channel”) these agents to patients at higher
risk of infection.
Another type of potential confounder is comorbid conditions. If, for example, doctors are less likely to
treat patients with diabetes with a TNF␣ antagonist
because of infection concerns, and preferentially prescribe a nonbiologic DMARD, then nonbiologic
DMARDs could appear to be associated with infection,
if diabetes is strongly linked with infection.
One can attempt to control for these potential
confounding factors using several different methods.
First, if one has some information on the confounder, it
should be included in the multivariable model. Thus,
information on comorbid conditions, such as diabetes,
need to be adjusted for, when available. Second, the use
of active comparators, such as methotrexate, helps to
“match” patients according to disease severity. However, this may not completely control for this issue, since
there may be residual confounding.
Propensity scores are increasingly being used in
pharmacoepidemiologic studies to control for confounding (15). The propensity score is calculated as the
probability of receiving one treatment compared with
another, i.e., a TNF␣ antagonist versus a nonbiologic
DMARD. The probability of treatment is estimated in a
logistic regression model that includes a host of covariates that may be related to choice of treatment, mimicking a physician’s decision process. If more covariates can
be included in the propensity score model as compared
with the conventional outcomes regression model
(which is limited by the number of outcomes [16]), then
adjustments in the propensity score may provide better
adjustment for otherwise incompletely measured confounders. However, in practice, propensity score analyses have almost never produced results significantly
different from those produced by conventional outcomes models in pharmacoepidemiology (15).
Other than better control for confounding, there
are several other reasons to consider the use of a
propensity score model. By plotting the propensity score
distributions in patients taking the study treatment in
comparison with control patients, one can gain a better
appreciation of the distribution of covariates. At times,
there is little overlap at the low and/or high end of the
propensity score distributions, and trimming the tails of
the distribution may be appropriate to focus the analysis
on those patients with apparent treatment equipoise in
routine care. Finally, when the relative risks differ by
propensity score stratum, it can suggest an effect modification that would need further exploration.
Another promising analytic method for improving control of confounding is the instrumental variable
analysis that has been applied in safety studies of
NSAIDs (17). An instrumental variable refers to a
variable independently related to treatment choice (i.e.,
TNF␣ antagonists), but unrelated to confounders or the
outcome, other than through the actual treatment (18).
Once these assumptions are fulfilled, an instrumental
variable serves as an unconfounded substitute for the
actual treatment, which results in an unbiased treatment
effect estimate, even if confounders remain unmeasured. The statistical inefficiency of instrumental variable estimates may limit their application in the study of
TNF␣ antagonists and infrequent outcomes.
Definition of the end point
The definition of infection differs dramatically
across studies. Different definitions of infection can
arise because of variation in prediagnosis surveillance
and in the criteria applied for infection. Some studies
rely on patient-reported infections, with some attempt to
confirm the diagnosis based on physician notes. Other
studies use a physician report of infection, with only
minimal confirmation based on primary records. Still
others use a primary hospital diagnosis of infection, with
or without a review of the medical records. None of the
studies have optimal sensitivity and specificity for identifying infections. Even in an ideal study setting, infection can be difficult to define, since many types of
infections have no standard definition. Generally, in
epidemiologic studies with relative risk measures, it is
preferred to use outcome definitions that have high
specificity, since they result in less biased relative risk
estimates even if sensitivity is low (19).
The validity of a study’s results can be threatened
when there are different surveillance measures or diagnostic criteria applied to patients in various exposure
groups. One can imagine that differential surveillance
might be performed for patients taking a TNF␣ antagonist versus those taking a nonbiologic DMARD. If a
physician and/or patient believes that a TNF␣ antagonist
may be related to infection, he or she may be more likely
to follow up on symptoms that may or may not be related
to infection. This may result in the application of
dissimilar diagnostic algorithms being applied to patients taking a TNF␣ antagonist versus those taking a
nonbiologic DMARD, leading to an artificial difference
in the risk of infection. This potential for surveillance
bias is minimized by studying only serious infections that
may require hospitalization, a definition that is less
Time-varying confounding
Over time, patients are reevaluated regarding the
need for medications, and this can change with variation
in disease activity over time. It can be assumed that
before every new prescription, such an evaluation has
Table 2. Major cohort types used in studies of tumor necrosis factor ␣ antagonists and infection
Cohort type
Disease-based registry
Drug-based registry
Practice-based or populationbased registries
Health care utilization data
Diagnosis is usually very accurate; diseasespecific information is very rich; medical
records are often available
Diagnosis is usually very accurate; diseasespecific information is very rich; medical
records are often available
Medical records are often available; patients
represent those in routine care; often
allows for linkage to pharmacy data; often
allows for linkage to other registries
Patients represent those in routine care;
includes linkage to pharmacy data; often
very large cohorts can be assembled
taken place. Therefore, many potential confounders
(i.e., disease activity) can vary in terms of the amount of
bias that may be introduced over time. Since disease
activity may change over time in RA, either because of
treatment or because of the typical oscillations in disease, and disease activity may affect the risk of infection,
it may be desirable to control for such changes. However, if a TNF␣ antagonist reduces disease activity, then
controlling for the subsequent change in disease activity
may “control away” the benefit of the TNF␣ antagonist
that may be on the causal pathway to infection. While
there are techniques that consider time-varying confounding, there are only rare instances when such methods have been shown to produce substantially different
results than those produced with models that include
only baseline variables (20).
Different data sources
There are 4 dominant data sources used in studying the safety of medications: disease-based registries
(e.g., the National Data Bank for Rheumatic Diseases or
the Consortium of Rheumatology Researchers of North
America), drug-based registries (e.g., the British Society
of Rheumatology Biologics Register), practice- or
population-based registries (e.g., the UK General Practice Research Database or Scandinavian patient cohorts), and health care utilization (“claims”) databases
(e.g., Medicare). Each of these different data sources
has a set of strengths and weaknesses, many related
directly to the methodologic issues described above
(Table 2).
A disease-based RA registry includes patients
with RA whose disease is often diagnosed by specialists.
Thus, patients recruited into such databases represent a
cohort who may have more severe disease that requires
Patients may not represent “typical” cases
“Unexposed” patients may not be similar
Diagnosis may not be accurate; outcome
assessment may not be accurate; diseasespecific information may be lacking
Diagnosis may not be accurate; outcome
assessment may not be accurate; diseasespecific information may be lacking
consultation with a specialist. It is unclear how the
sample of referring specialists is recruited and, in turn,
how they select their patients. These factors do not
affect the validity of the findings from such cohorts, but
the generalizability may be more limited. Moreover, the
report of specific comorbid conditions and adverse
events occurring between scheduled visits may be imprecise, relying on a patient’s self-report. When investigators study such cohorts, they often will attempt to access
medical records to confirm important diagnoses, such as
an infection or cancer.
Drug-based registries are generally established in
conjunction with a governmental prescribing program,
such as a registry designed to assess the value of TNF␣
antagonist use. Alternatively, they may be established by
a drug manufacturer interested in postmarketing safety
studies. Although these registries may enroll a fairly
complete group of patients, as in registries comprising
RA patients taking TNF␣ antagonists, the selection of
comparator patients is less clear. In the case of the
British Society of Rheumatology Biologics Register,
patients who were candidates for a biologic DMARD
but opted for a nonbiologic DMARD were eligible for
recruitment. However, some of the patients taking nonbiologic DMARDs may have had very different levels of
disease activity or a relative contraindication to use of a
biologic DMARD, such as a prior malignancy. Confirmation of end points presents the same set of challenges
in a drug-based registry as it does in a disease-based
Practice- or population-based registries combine
the advantages of being large with providing representative populations and fairly detailed clinical data.
Sometimes, the full medical record, including complete
data on the disease of interest, can be accessed. Access
No lag,
duration not
No lag,
according to
No lag,
according to
supply plus
90 days
No lag,
according to
supply plus 3
half lives
No lag, varied
No lag,
according to
supply plus
90 days
Wolfe, 2006 (4)
Curtis (9)
Nonbiologic DMARD
Nonbiologic DMARD
No prednisone
Nonbiologic DMARD
Comparator drug
Propensity score with disease
severity measures,
prednisone use, no
HAQ scores, disease
duration, prednisone use,
HAQ score, DAS,
prednisone use,
HAQ score, DAS,
prednisone use,
Comorbidities, prednisone
use, health system factors
Propensity score,
comorbidities, prednisone
use, health system factors
Comorbidities, prednisone
use, health system factors
No DMARD, no
Control for confounding
Drug initiated
Median 17 months
Mean 15 months with
TNF␣, mean 7
months with nonbiologic DMARD
Hospitalized with infections,
death, or IV antibiotics
Median 15 months with
TNF␣, median 11
months with nonbiologic DMARD
Median 17 months
Hospitalized with infections
defined by diagnosis codes
with primary record
Hospitalized with infections,
death, or IV antibiotics
Hospitalized with infections
defined by validated primary
diagnosis code
Hospitalized with infections
defined by diagnosis codes
with primary record
Patient self-report, with some
Reported by study investigators
End point assessment
Median 30 months
12 months maximum,
74% completed the
full 12 months
Duration of followup
* DMARD ⫽ disease-modifying antirheumatic drug; HAQ ⫽ Health Assessment Questionnaire; DAS ⫽ Disease Activity Score; IV ⫽ intravenous; MTX ⫽ methotrexate.
Dixon, 2007 (8)
2007 (6)
Curtis, 2007 (7)
Dixon, 2006 (5)
No lag, fixed
duration of
365 days
Exposure risk
Listing, 2005 (3)
First author,
year (ref.)
Table 3. Summary of the methodology used in major epidemiologic cohort studies of the risk of infection associated with tumor necrosis factor ␣ (TNF␣) antagonists among
patients with rheumatoid arthritis*
to medical records allows for easier confirmation of end
points, more reliable information about comorbidities,
and often direct pharmacy data about medication-filling
histories. This type of cohort registry rarely contains
information about the severity of diseases such as RA,
unless it is collected routinely and recorded in the
medical record. However, laboratory information, such
as levels of inflammation markers, may be accessible.
Health care utilization databases have been
widely used for a variety of pharmacoepidemiologic
studies. These databases comprise insurance-billing
claims for outpatient medical, hospital, and pharmacy
services. Included with such claims are diagnosis and
procedure codes that allow one to construct a detailed
“virtual” medical record. Since these databases contain
routinely collected information, they are relatively easy
to construct and may contain many thousands of patients, such as large cohorts of patients with RA who are
taking TNF␣ antagonists. Their major drawback is in the
limited clinical information available, such as indices of
disease severity. Moreover, one must rely on diagnosis
and procedure codes provided by physicians and hospitals during routine encounters. Although coding algorithms for many conditions, including infections, have
been developed and assessed (21), some misclassification of outcomes is inevitable. Some investigators have
augmented the information from these databases by
obtaining medical records, to confirm or refute specific
infection diagnoses (22).
Health system and health care utilization database cohorts have the advantage of being collected in
routine practice. This may avoid certain biases that arise
through the use of disease- or drug-based registries,
when investigators are unblinded to their hypotheses
during the collection of data. Routine practice may also
include a broader mix of patients, representing both
mild cases of RA and cases involving more complex
comorbid conditions. Nevertheless, disease- and drugbased registries utilize a specified data collection tool,
and thus may have more subtle clinical information that
would be important when controlling for confounding.
comparator groups, the potential confounders, the exposure risk window, and the study end points.
No one study provides a complete picture of the
risk of infections associated with TNF␣ antagonists.
However, as a group, the epidemiologic studies do
provide some important insights. Compared with patients starting methotrexate, those starting a TNF␣
antagonist and continuing treatment for ⬃1 year did not
appear to have an associated increased risk of serious
infection requiring hospitalization (6). Other studies
have shown that during the first 6 months of treatment
with a TNF␣ antagonist, patients did appear to be at an
increased risk of severe infection requiring hospitalization when compared with patients who were receiving
ongoing treatment with methotrexate and who seemed
to tolerate this or other DMARDs (3,5,7,9). These
studies test both the causal effect of TNF␣ antagonists
and the effect of step-up therapy (i.e., adding a TNF␣
antagonist to a DMARD) on infection. Among patients
receiving long-term treatment with TNF␣ antagonists as
compared with patients receiving glucocorticoids and no
DMARD, there was no observed increase in the risk of
pneumonia requiring hospitalization (4).
Randomized controlled trials and meta-analyses
of trials give a limited view of a drug’s safety. Epidemiologic studies designed to assess the safety of a drug in
routine care can complement the information provided
by randomized controlled trials. The current observational studies of TNF␣ antagonists and infection have
important methodologic differences that may explain
their apparently discrepant results. As with all science,
the “devil is in the details” with epidemiologic studies of
the safety of TNF␣ antagonists.
Dr. Solomon had full access to all of the data in the study and
takes responsibility for the integrity of the data and the accuracy of the
data analysis.
Study design. Solomon, Lunt, Schneeweiss.
Acquisition of data. Solomon.
Analysis and interpretation of data. Solomon.
Manuscript preparation. Solomon, Lunt, Schneeweiss.
Statistical analysis. Solomon, Lunt, Schneeweiss.
Epidemiologic studies on the outcomes of drug
therapy are methodologically challenging. The apparent
discrepancies in findings across studies of TNF␣ antagonists and infections can be explained by important
differences in methodology (Table 3). In part, the various studies are addressing different questions by applying different definitions of the at risk population, the
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