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Epilepsy&
Epilepsy & Behavior 4 (2003) 457–463
Behavior
www.elsevier.com/locate/yebeh
Controversies in Epilepsy and Behavior
Translating monotherapy trials into clinical practice:a look into the abyss
Santiago Arroyoa,* and Emilio Peruccab
a Department of Neurology, Medical College of Wisconsin, Froedtert Hospital, 9200 West Wisconsin Avenue, Milwaukee, WI 53226, USAb Clinical Pharmacology Unit, Department of Internal Medicine and Therapeutics, University of Pavia, Pavia, Italy
Received 2 July 2003; accepted 14 July 2003
Abstract
To be approved for monotherapy by regulatory authorities, new antiepileptic drugs (AEDs) must first be tested in well-controlled
studies in refractory patients (conversion to monotherapy trials) or in patients with newly diagnosed epilepsy. However, the ap-
plicability of the information obtained in these trials to day-to-day clinical practice is limited. Clinical trials in newly diagnosed
patients, particularly those allowing dose flexibility, offer more useful information, but a close scrutiny of methodological details is
required to avoid misinterpretation of the findings. In many instances, the neurologist has a drug with a label, but lacks critical
information on optimal titration rates, optimal target and maintenance dosages, response rates in populations with different epilepsy
syndromes, different age ranges and comorbidities, and long-term safety data. Such information becomes available only through
general clinical experience, well-designed phase IV studies, and postmarketing surveillance.
� 2003 Elsevier Inc. All rights reserved.
Keywords: Monotherapy; Antiepileptic drugs; Anticonvulsants; Polytherapy; Clinical trials
1. Introduction
The ideal way to manage epilepsy is with a mono-
therapy regimen. In fact, the majority of patients with
new-onset seizure disorders can be treated successfully
with a single antiepileptic drug (AED) [1]. The use of a
single drug has advantages over polytherapy in terms ofbetter tolerability, avoidance of drug interactions, better
compliance, and lower costs [2].
Over the past 15 years a number of second-generation
AEDs (felbamate, gabapentin, lamotrigine, levetirace-
tam, oxcarbazepine, tiagabine, topiramate, vigabatrin,
and zonisamide) have been introduced into the thera-
peutic armamentarium of epilepsy. All of them, except
felbamate and oxcarbazepine, were approved initiallyfor add-on therapy, and only later were some of these
AEDs also granted an indication for monotherapy use
after completion of monotherapy trials [3]. Such trials
* Corresponding author. Fax: 1-414-259-0469.
E-mail address: [email protected] (S. Arroyo).
1525-5050/$ - see front matter � 2003 Elsevier Inc. All rights reserved.
doi:10.1016/j.yebeh.2003.07.011
are required by law to obtain this indication both in the
United States and in Europe.
Data obtained in regulatory trials are used to deter-
mine the mode of use of an AED in routine clinical
practice. However, the complexity of clinical trials and
the purpose for which these trials are designed make it
difficult for many neurologists to evaluate the practicalimplications of trial-generated data [4]. In this article we
discuss the limitations of data derived from monother-
apy trials with respect to their applicability to clinical
practice.
2. Why are AEDs not approved with a wide indication?
Up to the early 1980s, the Federal Drug Adminis-
tration (FDA) of the United States and other regulatory
agencies granted AEDs a nonrestrictive indication for
the treatment of partial or generalized seizures, without
differentiating whether the drugs were to be used ad-
junctively or as monotherapy. In this way, carbamaze-
pine, phenytoin, phenobarbital, and primidone received
458 Controversies in Epilepsy and Behavior / Epilepsy & Behavior 4 (2003) 457–463
blanket regulatory approvals for their use in epilepsy.However, for the last 20 years, the FDA and other
agencies started to require proof of efficacy and safety
separately for adjunctive use and for monotherapy [5–7].
The reason for this change in policy was based on the
principle that a drug indication should be approved only
for those dosages and those populations for which
evidence of efficacy and safety has been provided in
well-controlled clinical trials.New AEDs are evaluated initially in adjunctive
therapy trials because, given the serious nature of seizure
disorders, it is generally considered unethical to test a
new AED as monotherapy without any evidence that
the same drug is effective when added onto preexisting
medication. Therefore, regulatory agencies consider that
if a drug was found to be efficacious as add-on in pa-
tients refractory to conventional medications, the sci-entific evidence permits only adjunctive therapy use [2].
Although the neurological community has sometimes
criticized this ‘‘regulatory loop,’’ there is in fact evidence
that these requirements are fully justified. For example,
the efficacy of three new AEDs (remacemide, vigabatrin,
and tiagabine) in monotherapy was worse than that of
carbamazepine [8–11]. Adverse effect profiles may also
differ between mono- and polytherapy regimens: inparticular, while side effects are usually more common
during combination therapy, this is not always true. For
example, paresthesias are reported much more fre-
quently when topiramate is used as monotherapy [12].
One reason behind the differences in efficacy and toler-
ability between monotherapy and polytherapy trials lies
in the pharmacodynamic interactions during adjunctive
use [13]. Furthermore, it may be argued that the AEDdosage assessed in the severely refractory population in
add-on trials may not be applicable to newly diagnosed
epilepsy patients whose seizures often respond to lower
doses of medication.
3. How does a monotherapy indication influence the way
an AED is prescribed?
In the United States, the FDA does not regulate the
physician�s use of medications. Thus, off-label use is
neither unethical nor illegal, though physicians should
be able to justify their therapeutic choice to an informed
patient. Yet, some practitioners consider off-label use a
legal liability. In a recent survey conducted by the
Practice Committee of the American Epilepsy Society,534 neurologists were asked to provide information on
their prescribing habits: although 92% would prescribe
off-label at some point, 62% of the neurologists and 46%
of the epileptologists felt that the FDA labeling does
influence their practice patterns [7]. Furthermore, the
absence of a monotherapy indication prevents the
pharmaceutical industry from promoting their products
for that indication, which, in turn, is likely to have amajor impact on the way an AED is prescribed. The
situation in Europe is similar, though in some countries
physicians are further discouraged from prescribing
drugs off-label as this precludes reimbursement of the
drug�s cost by national insurance programs.
4. How do we prove that monotherapy works?
The latest Declaration of Helsinki (2000) states that
‘‘the benefits, risks, burdens and effectiveness of a new
method should be tested against those of the best cur-
rent prophylactic, diagnostic and therapeutic methods.
This does not exclude the use of placebo, or no treat-
ment, in studies where no proven prophylactic, diag-
nostic and therapeutic method exists’’ [14]. Thefollowing statement represents the latest version of the
Declaration of Helsinki following the world Medical
General Assembly (2002) that is relevant to clinical trials
in epilepsy:
The WMA hereby reaffirms its position that extreme care must
be taken in making use of a placebo-controlled trial and that in
general this methodology should only be used in the absence of
existing proven therapy. However, a placebo-controlled trial
may be ethically acceptable, even if proven therapy is available,
under the following circumstances:
— Where for compelling and scientifically sound methodologi-
cal reasons its use is necessary to determine the efficacy or safety
of a prophylactic, diagnostic or therapeutic method; or
— Where a prophylactic, diagnostic or therapeutic method is
being investigated for a minor condition and the patients who
receive placebo will not be subject to any additional risk of se-
rious or irreversible harm.
Thus, the use of placebo as the sole therapy is gen-
erally considered ethically unacceptable in epilepsy, and,
consequently, controlled studies need to include an ac-tive treatment arm as comparator. This, however, may
complicate the interpretation of the trial results. For
example, when an investigational AED is compared
with an established AED and both show similar out-
comes in terms of efficacy endpoints, the study may be
regarded by regulatory authorities as lacking assay
sensitivity (i.e., it can be argued that the two treatments
might have been equally ineffective in the specific patientpopulation recruited for the study) [15]. This argument
has been often criticized, as many practitioners feel that
if a new AED appears to be no different from a gold
standard such as carbamazepine, there would be no
doubt of its efficacy. However, this assumption may not
always be true. For example, a review of clinical trials
comparing carbamazepine with new AEDs shows a
seizure-free rate with carbamazepine ranging from 20 to42% [16]. A more disturbing fact can be appreciated in
intent-to-treat analyses of carbamazepine trials in newly
diagnosed epilepsy in which 95% confidence intervals for
Controversies in Epilepsy and Behavior / Epilepsy & Behavior 4 (2003) 457–463 459
efficacy outcomes overlap with confidence limits for theplacebo (or pseudo-placebo) arm in other trials [4,7].
Thus, a trial showing no difference between two treat-
ments cannot be regarded as providing unequivocal
evidence of efficacy, and a design allowing demonstra-
tion of superiority over an appropriate control would
have clear advantages in this context.
A number of such designs have been developed in
recent years [4,17–19]. Invariably, these involve ran-domization of patients to a high dosage of the investi-
gational agent and to a suboptimal dosage of either the
same agent or an established AED. The use of a sub-
optimal dose (sometimes referred to as pseudo-placebo),
however, is controversial as it conflicts with the principle
of equipoise, which, according to the Declaration of
Helsinki, should govern all clinical trials.
The requirements to obtain a monotherapy indica-tion differ somewhat in Europe and in the United States.
The European Agency (EMEA) considers noninferiority
monotherapy trials using an established comparator at
optimized dosages as the best study design, although to
overcome assay sensitivity concerns supportive evidence
from some kind of superiority trial (conversion to
monotherapy or low-dose vs high-dose active control) is
also recommended [6]. The FDA, on the other hand,does not accept noninferiority trials and requires clear
demonstration of superiority versus a comparator, ei-
ther in refractory patients (conversion to monotherapy
design) or in newly diagnosed patients [5].
The trial designs used to address these regulations
differ according to the characteristics of the patient
populations. In refractory patients, two types of designs
are employed: the outpatient conversion to monother-apy and the inpatient presurgical withdrawal to mono-
therapy [19]. Both involve a short-term assessment
aimed at demonstrating superiority over a suboptimal
comparator or placebo. In newly diagnosed epilepsy,
two types of designs have also been applied: the supe-
riority design, which is usually a medium-term com-
parison versus a suboptimal comparator or placebo, and
the noninferiority design, which typically involves alonger-duration assessment [3]. Each of these ap-
proaches is briefly discussed in the sections below.
5. Outpatient conversion to monotherapy trials in patients
with refractory epilepsy
In this design, patients whose seizures are uncon-trolled with preexisting AED treatment are randomized
under double-blind conditions to a high dosage of the
investigational drug or a low dose of either the same
drug or an established AED (low-dose or pseudo-pla-
cebo arm) [19]. Baseline AED medication is then pro-
gressively reduced and eventually discontinued, leading
to a 12- to 16-week monotherapy period; those who are
unable to convert are considered treatment failures(noncompleters) and are included in the time-to-exit
analyses. Basically, the trial measures time to exit due to
fulfillment of one of the exit criteria, the aim being to
demonstrate that exit due to seizure deterioration occurs
more commonly in the low-dose than in the high-dose
group. Typical exit criteria include: a twofold increase in
partial seizure frequency in any 28-day period relative to
baseline; a twofold increase in the highest consecutive 2-day partial seizure frequency relative to baseline; oc-
currence of a single generalized seizure if none occurred
during the 6 months prior to randomization; or pro-
longation or worsening of generalized seizures requiring
intervention.
In trials conducted so far according to this design,
more than 70% of patients met exit criteria in the low-
dose (pseudo-placebo) arm. Patients randomized to ahigh dose of an effective investigational AED continued
in the trial for significantly longer periods; however,
more than 40% of these patients eventually met exit
criteria before completing the monotherapy phase [19].
Exposing patients to suboptimal therapy in these trials
has been criticized on ethical grounds [20]. To overcome
this concern it has been suggested that response to high-
dosage therapy could simply be compared with re-sponses observed in historical controls randomized to
suboptimal treatment in previous trials [4,7,21,22].
5.1. An example
Gilliam et al. [22] reported on a randomized double-
blind trial in which 156 patients on carbamazepine or
phenytoin monotherapy were randomly assigned to re-ceive increasing doses of lamotrigine (target dose, 300–
500mg/day) or a relatively low dose of valproic acid
(target dose, 1000mg/day). During an 8-week transition
period, carbamazepine or phenytoin was withdrawn and
the patients entered a 12-week monotherapy period. The
study drug was discontinued in patients who met pre-
determined escape criteria for seizure worsening. Sig-
nificantly more patients on lamotrigine completed thetrial (56% vs 20%), and the time to meet the escape
criteria was significantly longer in lamotrigine-treated
patients than in the valproic acid-treated patients (168
days vs 57 days).
5.2. What can we learn from this type of trial?
This trial design was driven by purely regulatoryconcerns, and it did not provide information that may
be of much use for routine clinical practice. Basically,
the findings of this study suggest that the investigational
drug, at high dosages, protects against seizure deterio-
ration after discontinuation of baseline AED therapy
[19]. These findings could be of some value when dis-
continuing concomitant medication in a patient who
460 Controversies in Epilepsy and Behavior / Epilepsy & Behavior 4 (2003) 457–463
had responded well to adjunctive therapy. However, thistype of study is fraught with the following limitations:
1. These studies do not necessarily assess the outcome
of conversion to monotherapy in a group of patients
who had responded satisfactorily to an optimized dos-
age of the investigational drug.
2. The dosages of the investigational drug and rates
of downtitration of preexisting medication are unlikely
to provide an estimate of the optimal dosages (and op-timal downtitration rates) to be used in day-to-day
practice.
3. The endpoints for exiting the trial may not neces-
sarily be applicable to decision making outside a trial
protocol.
4. The characteristics of the study population may
differ from those of a typical population in which con-
version to therapy is likely to be attempted in clinicalpractice.
5. The trial provides no information on clinical ben-
efit, because endpoints are based on seizure deteriora-
tion rather than improvement.
6. Most importantly, this type of study does not
provide any information on the efficacy, tolerability,
optimal titration rates, and maintenance dosage re-
quirements in patients with newly diagnosed epilepsywho are started on initial treatment.
6. Inpatient presurgical conversion to monotherapy trials
in patients with refractory partial epilepsy
These trials are conducted in hospitalized patients
undergoing video-EEG recording for presurgical as-sessment [19]. Given that in these patients baseline
AEDs are discontinued for diagnostic purposes, this
situation is exploited to test how the patients� seizuresrespond to the investigational drug compared with a
low-dose active control or even placebo. The use of
placebo, though criticized, has been justified by some
investigators in view of the intensive monitoring situa-
tion, which reduces the patient�s risks, and the addedusefulness of recording more seizures for the presurgical
evaluation. In these trials, study drugs are ‘‘loaded’’ and
the double-blind evaluation lasts 7 to 14 days. The main
objective is to compare time to exit due to fulfillment of
one of the exit criteria. The expectation is that patients
randomized to the high dosage of the investigational
agent are less likely to experience seizures than those
receiving a low-dose/placebo treatment.
6.1. An example
Arroyo et al. [23] reported on a multicenter, double-
blind, randomized, placebo-controlled, parallel-group
trial where patients were randomized to receive either
intravenous MHD (the active monohydroxy derivative
of oxcarbazepine) (2400mg/day) or placebo. The studyconsisted of a 48-hour baseline and a 7-day double-
blind treatment phase. Patients had to have 2 to 10
partial seizures during baseline and the trial was
completed either after 7 days of treatment or after
meeting one of the exit criteria (three partial seizures,
one new-onset secondarily generalized seizure, serial/
prolonged seizures, or status epilepticus). The per-
centage of patients meeting an exit criterion was theprimary efficacy variable. Of 107 randomized patients,
79.4% completed the trial and 20.6% were prematurely
discontinued; significantly more patients completed the
7-day assessment period in the MHD arm than in the
placebo arm (47.1% vs 9.8%). The main reason for
premature discontinuation was the occurrence of ad-
verse events (25% in the MHD group vs 7.3% in the
placebo group).
6.2. What can we learn from this type of trial?
The presurgical design is even less informative for
clinical practice than the outpatient conversion to
monotherapy trial. Because patients are withdrawn
from baseline medications very rapidly, this trial may
test primarily efficacy against drug withdrawal seizuresrather than spontaneously occurring seizures, a con-
sideration that reduces substantially the value of this
design even from the regulatory viewpoint. Other
shortcomings include (1) the very short time of as-
sessment, which is of no relevance to the routine use of
a drug in clinical practice; (2) the use of dosages and
rates of drug titration that are far from optimal; (3) the
possible confounding effect of pharmacodynamicinteractions resulting from carryover effects of the
discontinued medications; and (4) inclusion of a trial
population that is poorly representative of the type
of patients most commonly encountered in routine
practice.
7. Superiority monotherapy trial in newly diagnosedepilepsy
Superiority trials in patients with untreated, usually
new-onset, epilepsy use a multicenter, randomized,
double-blind, parallel-group, dose-controlled design,
i.e., a comparison of a low dosage with a high dosage.
Target dosages may be reached after an appropriate ti-
tration, and patients experiencing adverse effects duringtitration may be allowed to step back by one dose level.
Similar to the conversion to monotherapy designs, these
trials require patients to exit the study after meeting
specific criteria (e.g., occurrence of one or two seizures
after reaching the target dosage). Evidence of efficacy is
provided by the demonstration that patients randomized
to the high-dosage group remain in the trial for a longer
Controversies in Epilepsy and Behavior / Epilepsy & Behavior 4 (2003) 457–463 461
period than those randomized to the low dosage. Forpatients not meeting exit criteria, follow-up periods can
be extended for up to 1 year or longer. The typical total
sample size required to achieve adequate statistical
power in these studies may be on the order of 300 to 500
patients.
7.1. An example
Arroyo et al. [24] reported on a multicenter double-
blind trial in 470 patients with newly diagnosed (6 3
months) epilepsy or epilepsy relapse. Patients were
required to have had one or two partial-onset or gen-
eralized tonic–clonic seizures in a 3-month retrospective
baseline. They were randomized to topiramate at target
dosages of 50mg/day (low-dose group) or 400mg/day
(high-dose group). The primary efficacy parameter (timeto first seizure) significantly favored the high dose. A
secondary efficacy outcome measure included the
seizure-free rate at 6 months, which was 83% in the high-
dose group versus 71% in the low-dose group, a statis-
tically significant difference. Seizure-free rates at 1 year
(76 and 59%, respectively) also differed significantly
between groups. In terms of seizure-free rates, the dif-
ference between groups became statistically significantas early as Day 14, when patients were receiving only 25
and 100mg/day, respectively.
7.2. What can we learn from this type of trial?
This type of trial demonstrates that a high dose of an
AED is more efficacious than a low dose. Moreover,
long-term double-blind follow-up allows identificationof efficacy and tolerability profiles in relation to the
dosages used. Although the population involved in these
trials may be representative of patients who require
initial monotherapy in routine clinical practice, this is
not necessarily true. In the above study, for example, the
patient population was highly preselected in that seizure
frequency at baseline had to remain within a narrow
range.The main problem with this design is that dosages are
selected to maximize the probability of identifying a
difference and, therefore, may overestimate (high-dose
group) or underestimate (low-dose group) the optimal
dose range. Since dosages in these trials are not adjusted
according to clinical response, the optimal dose range
may not be identified, leading to labeling specifications
that may not reflect the optimal mode of use of the drug.The trial described above, for example, identified
400mg/day topiramate as an efficacious daily dosage for
initial monotherapy. Such a dose is likely to be consid-
ered by many clinicians as unnecessarily high based on
safety concerns, however (19% of patients withdrew
from the high-dose arm). This dose was derived from a
noninferiority study suggesting good responses at lower
doses [25]. Although in the superiority trial a dose of100mg during the titration phase was significantly more
effective than 25mg (and may therefore represent a more
appropriate initial target dosage), a comparison of the
100- and 25-mg doses was not the primary aim of the
study and, therefore, it may not be necessarily taken into
consideration by regulatory authorities in determining
the approved dose range.
8. Noninferiority monotherapy trials
Noninferiority monotherapy trials are multicenter,
double-blind, randomized, parallel-group studies where
the investigational drug is compared with an established
treatment at dosages likely to produce similar efficacy
outcomes. In these trials, patients with new-onset epi-lepsy are randomized to receive two or more study
treatments, and duration of follow-up is generally on the
order of 1 year. According to EMEA guidelines, the trial
should allow comparison of the investigational agent
and the reference treatment at flexibly adjusted, opti-
mized dosages. In many of the trials conducted to date,
however, the degree of flexibility has been limited. Pri-
mary endpoints in these studies typically include a pureefficacy measure (e.g., 6-month seizure-free rates) and a
combined measure of efficacy and tolerability (e.g., re-
tention of patients on the allocated treatment).
In noninferiority trials, sample size should be suffi-
cient to demonstrate, based on confidence limit analysis,
that response rates on the investigational drug are not
clinically significantly lower than those observed for the
reference (established) treatment. However, most trialsconducted to date with second-generation AEDs have
been statistically underpowered [27].
8.1. An example
Brodie et al. [26] reported on a double-blind, ran-
domized, parallel-group comparison of lamotrigine and
carbamazepine in 260 patients with newly diagnosedepilepsy who experienced partial or primarily general-
ized tonic–clonic seizures. Although this comparison
was nominally designed as a superiority trial, predicted
differences in responder rates used for calculation of
sample size were unrealistically high, and the authors
claimed to have demonstrated a similar efficacy of the
two treatments. The trial had a 48-week duration: after a
4-week fixed-dose escalation, doses were adjusted ac-cording to efficacy, adverse events, and plasma concen-
trations. The primary outcome measure was the
proportion of patients maintained seizure-free during
the last 24 weeks of treatment and was no different be-
tween the two groups (39% lamotrigine, 38% carbam-
azepine). Lamotrigine, however, appeared to provide a
better safety profile as fewer patients withdrew because
462 Controversies in Epilepsy and Behavior / Epilepsy & Behavior 4 (2003) 457–463
of adverse events (15% vs 27% on carbamazepine).Significantly more patients on lamotrigine than on car-
bamazepine (65% vs 51%) completed the study.
8.2. What can we learn from this type of trial?
The greatest appeal of these trials is that they are, or
appear to be, close to routine clinical practice. Dose
flexibility should allow optimal treatment in both studyarms, theoretically allowing a realistic estimate of the
relative efficacy and tolerability of the AEDs being
compared. For these reasons, these trials may provide
useful information that is relevant in the day-to-day
practice, and not surprisingly, they have considerable
influence on prescribing patterns. The specific trial de-
signs, however, need to be scrutinized very closely, be-
cause methodological problems and potential bias mayhave a profound effect on clinical outcome and invali-
date some of the claims made on the basis of the findings
presented.
One general problem with these studies is their lack of
assay sensitivity, defined as the ability to detect a
meaningful difference between treatments if such a dif-
ference existed. The issue of assay sensitivity has differ-
ent facets. First, as discussed above, experience hastaught us that variation in responder rates to established
and suboptimal treatments (including placebo) in dif-
ferent trials has been so wide that a finding of no dif-
ference does not really exclude the possibility that the
two treatments were equally ineffective under the con-
ditions in which they were tested [7,15]. Second, it must
be ascertained whether the study had sufficient power to
exclude a clinically significant difference. In the trialdiscussed above, for example, confidence limits for
outcome measures were so large that major differences
in efficacy, though not seen, could not be excluded [26].
Third, the maximal difference that is assumed to be
clinically irrelevant should be scrutinized. For example,
in a recent noninferiority trial comparing lamotrigine
and gabapentin in newly diagnosed epilepsy [28], it was
assumed that a difference in retention rate 6 20% be-tween the two treatments (e.g., a 45% retention rate on
the investigational drug vs a predicted 65% retention
rate on the reference drug) would be clinically irrelevant,
which is surely debatable. Fourth, it is important to
confirm that the selected outcome measures were not
suboptimal in terms of assay sensitivity. In the lamo-
trigine-versus-gabapentin comparison [28], for example,
the primary efficacy endpoint (time to exit due to inef-ficacy at the highest tolerated dose) was probably an
insensitive measure for the following reasons: the pro-
tocol required stepwise dose increments after any sei-
zure; the trial duration was only 30 weeks; and the
seizure frequency at baseline could be as low as one
seizure during the previous 12 months. (Not surpris-
ingly, of 299 patients included in the trial, only 5 exited
due to inefficacy!) Finally, it must be realized that assaysensitivity and statistical power can be weakened
through inclusion of heterogeneous patient populations.
In both trials discussed above [26,28], patients had both
partial and generalized epilepsies, which may respond
differentially to the administered drugs. Although simi-
lar efficacies were claimed for both types of epilepsy, the
subgroups were too small to allow meaningful conclu-
sions. For example, only 58 of 299 patients included inthe gabapentin-versus-lamotrigine trial [28] were diag-
nosed as having generalized epilepsy.
Another important shortcoming of some noninferi-
ority trials relates to the possibility of flaws in study
design which, at times, introduce bias in favor of the
sponsor�s product [18]. Many noninferiority trials com-
pleted to date have concluded that the sponsor�s productis similarly effective but better tolerated than an estab-lished older-generation AED. However, this conclusion
often was not supported by confidence limit analysis,
and in any case, it would be valid only for the dosing
regimens that were selected for those studies. The lam-
otrigine-versus-carbamazepine comparative trial de-
scribed above [26], for example, may have been biased
by the fact that both drugs were administered twice
daily, which is appropriate for lamotrigine but poten-tially suboptimal for the immediate-release carbamaze-
pine formulation used in that trial [29]. Likewise, an
excessively fast titration schedule may have contributed
to an unusually high withdrawal rate (27%) due to ad-
verse effects in the carbamazepine group.
In another trial comparing vigabatrin with carbam-
azepine, the dosage of vigabatrin could not exceed a
predefined limit (3000mg/day), whereas carbamazepinedosage had to be increased until seizures were controlled
or toxic effects had appeared [10]. This may explain why
in that study vigabatrin was not only better tolerated, but
also apparently less efficacious. In many trials in which a
new agent was reported to be better tolerated than an
established AED, it is not possible to exclude that such a
tolerability difference would have vanished, without
necessarily loss of efficacy, if the established agent hadbeen used at lower dosages [4]. Another shortcoming of
many trials conducted to date is that duration of follow-
up was relatively short, usually 1 year or less, which may
be insufficient for adequate optimization of dosage and
assessment of long-term efficacy and tolerability.
9. Conclusions
New AEDs should undergo monotherapy testing to
have an appraisal of their efficacy and tolerability profile
in this situation. However, the applicability of the in-
formation obtained in these trials to day-to-day clinical
practice may be minimal, especially with conversion to
monotherapy designs. Clinical trials in newly diagnosed
Controversies in Epilepsy and Behavior / Epilepsy & Behavior 4 (2003) 457–463 463
patients, particularly those allowing dose flexibility, of-
fer more useful information, but a close scrutiny of
several methodological issues is required to avoid mis-
interpretation of the findings. In many instances, the
neurologist has a drug with a label, but critical infor-mation on optimal titration rates, optimal target and
maintenance dosages, response rates in populations with
different epilepsy syndromes, different age ranges and
comorbidities, and long-term safety data will eventually
become available only through general clinical experi-
ence, well-designed phase IV studies, and postmarketing
surveillance.
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