Cognitive side-effects of chronic antiepileptic drug treatment: A review of 25 years of research

EPILEPSY IIESF_A H ELSEVIER

Epilepsy Research 22 (1995) 65-95

Review

Cognitive side-effects of chronic antiepileptic drug treatment: A review of 25 years of research Jan Vermeulen, Albert P. Aldenkamp * Dept. of Neuropsychology, 'Meer & Bosch' Epilepsy Centre, Heemstede, The Netherlands Received 30 April 1995; accepted 22 July 1995

Keywords: Neuropsychology; Cognitive function; Antiepileptic drug; Cognitive side-effect

1. Introduction Antiepileptic drug (AED) treatment may last a lifetime in many patients. During such treatment a variety of side-effects may occur. Some may appear immediately, possibly showing some habituation, such as nystagmus or drowsiness. Others may be of insidious onset, emerging only after extended periods of treatment. A multitude of such chronic side-effects have been documented [1], including effects on, e.g., metabolism, bone and connective tissue, the endocrine system and the peripheral and central nervous system. The present paper reviews the cognitive aspects of chronic AED effects on CNS function. Such effects may critically influence a person's daily life functioning, e.g., learning in children, and should thus be carefully assessed. Cognitive side-effects are of considerable concern to the clinician and represent a major issue in current trials of new AEDs. A considerable body of research evaluating the cognitive side-effects of AEDs has accumulated during the past 25 years. According to Dodrill [2], previously published reviews of the literature have

* Corresponding author. 'Meer & Bosch' Epilepsy Centre, Achterweg 5, P.O. Box 21, 2100 AA Heemstede, The Netherlands. Tel.: (0)23-339060; fax: (0)23-294324 or (0)23-289412.

tended to be uncritical summaries of the conclusions presented in the various research reports, disregarding the often serious methodological limitations that might have invalidated the findings of these studies [3]. Making sense out of the voluminous literature is no mean task vis-a-vis such possible conclusion validity problems. The validity of the conclusions drawn in cognitive AED studies is a major theme that runs throughout most of the present article. The focus on methodological issues seems warranted given the multitude of potential validity threats that hinder the straightforward interpretation of the findings from much research in this complex field. For example, various complications arise from the lack of opportunity to conduct definitive randomized controlled trials, the acknowledged gold standard for deciding whether a particular treatment does any good or (cognitive) harm. In reality, clinical considerations often determine treatment allocation; interpretation of data from studies with non-randomly assigned treatment groups must always be done with great caution, of course, as the subjects cannot be assumed to be similar upon entry into the study, and the differences may be relevant to cognitive performance after AED treatments. Non-random treatment assignment is a rich source of artifacts that can masquerade as cognitive AED effects, or obscure them.

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Another issue especially relevant to this research area concerns conclusions drawn from 'negative findings'. Non-significant results tend to be regarded as disappointing, but research on side-effects is a case where one may actually want nonsignificance, for then the results might be interpreted as demonstrating the absence of harmful cognitive effects. Conclusions that state or imply this occur with some frequency in the literature. In fact, such conclusions, if valid, are good news, suggesting that one does not have to reckon with a possible trade-off between seizure control and adverse cognitive effects if medication is given or altered. An important point to consider in drawing conclusions from no-effect resuits is the statistical power of the study. That is, such conclusions only make sense if the study has a reasonable a priori chance (say, 80% or better [4]) of detecting a treatment effect, when in fact one is there. This probability, i.e., the statistical power, is heavily dependent on sample size; with large samples power is not an issue, but in cognitive AED research sample sizes tend to be small (e.g., less than 20 subjects per group), and power may be inadequate to support a meaningful no-effect conclusion. However, researchers in this field appear not to have been very sensitive to statistical power and the possibility of false-negative findings. The purposes of the present paper include the following: (1) to generate an up-to-date list of studies pertinent to cognitive side-effects of long-term AED treatment; (2) to assess the methodological quality of the studies included--we comment on various factors that can lead to false conclusions as to what effect, if any, AEDs have on cognition, and that are relevant to the proper interpretation of any study in this field; (3) to attempt to synthesize the findings from high-quality studies, giving less weight to results from studies with obvious methodological shortcomings; (4) to propose some criteria to be considered in further research in this area.

2. Method 2.1. Identification of relevant studies

Potentially relevant studies were identified through computerized and manual searches of the English-

language literature published from January 1970 through December 1994. A computerized search of the DIMDI database was conducted through the keywords AEDs and antiepileptic drugs; in addition, the bibliographies of several reviews on the same topic were examined [2,3,5-18]. This search yielded 1284 titles. These papers were judged for their relevance to cognitive side-effects of AEDs. The resulting literature base comprised 413 potentially relevant papers. Then the following inclusion criteria were applied to the full reports: 1. Type of article: report of original research in peer reviewed journals or proceedings. This represents an initial control on the quality of methods and results; abstracts, for example, usually do not provide sufficient detail to allow the readers to judge the validity of the results, and reports unacceptable to reviewers of international journals may lack reliability [19]. The constraint on publication date was set fairly arbitrarily at approximately 25 years ago. Studies after that date were all done in a time when most of the current AEDs had become available and modern cognitive tests had come in widespread use. 2. Subjects: epilepsy or healthy volunteers. The target group is the 'regular' outpatient epilepsy population, receiving long-term AED treatment. AED treatment in special groups without epilepsy may be ungeneralizable to the majority of epilepsy patients. Examples include psychiatric patients, delinquents, children with behavioral or mood disorders. Studies with subjects receiving AEDs for prophylaxis instead of treatment, e.g., to prevent the development of posttraumatic seizures [20] or the recurrence of febrile seizures in children [21-23], were also excluded for similar reasons. An exception was made for studies in healthy volunteers, as such studies offer several potential advantages and might suggest hypotheses worth further exploration in epilepsy. 3. Treatments: current AEDs. Studies on experimental drugs that have failed to prove efficacy and will not be introduced in clinical practice, such as flunarizine or loreclezole were excluded. 4. Outcome measures: psychometrically assessed cognitive functions. After application of these criteria, a database of 94 articles remained, representing 89 nonoverlapping

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studies. Two articles [24,25] concerned a reanalysis of data reported earlier [26,27], two articles [28,29] represent extensions of previous studies [30,31], one paper [32] reports the same data as an earlier one [33]. Some of these articles report multiple experiments.

2.2. Presentation minima In a number of articles meeting our inclusion criteria, the description of methods and results arguably fell below currently accepted standards of scientific communication (e.g., some did not even report the number of subjects studied). One is thus forced into the unfortunate position of either accepting the results uncritically, or specifying certain minima with respect to the methodological and statistical information provided that must be met before evaluation is possible. The criteria employed here were: (1) the design should be transparent; the term 'design' as used here refers to the scheduling of treatments (i.e., AEDs, placebo, no treatment) and outcome measurement sessions, and to the way subjects were assigned to treatment groups (i.e., on a random basis or not), (2) the total number of subjects and the numbers assigned to each treatment condition should be given, (3) the number and type of cognitiue variables employed should be clear, (4) descriptive statistics should at least include measures of central tendency (e.g., means or mean difference scores); these should be available for all cognitive variables on all assessment points, (5) inferential statistics should be reported, providing information about the type of statistical tests used (e.g., t-test, F-test) and the significance level. Studies that fail to meet any of these presentation minima will be listed in tables in the next sections, but their findings will generally not be given weight as they do not provide sufficient information to enable the reader to evaluate the methods and results adequately.

2.3. Notes on tables In the following, data tables will be presented as a guide to each study's main characteristics, showing: 1. Treatments. This section shows the treatment conditions associated with assessment points. Some-

67

times testing did take place under a particular treatment condition, e.g., for familiarization purposes or to eliminate practice effects, but data were not used for analysis. In such cases, the treatments involved are not given. The nomenclature and abbreviations for individual AEDs comply with the recommendations in Epilepsia, 34 (1993) 1151. In addition: P = Polytherapy; SAD = Single additional dose; Mono = monotherapy; Plac = placebo. None = no AEDs. Subscripts: AEDcr = controlled release f o r m u l a t i o n ; AEDDhi/Dme/DIo =high, medium, low dosage; AEDshi/Sl o --high vs low serum (or saliva) levels; Pred, mod = P reduction, c.q. other modification; PAEO+/-= P with vs without a particular AED; Ptox+/_ = P with toxic vs nontoxic serum levels. Slashes ( / ) indicate contrasts under study in a parallel group or posttest-only design (see below). Crosses ( X ) indicate crossover elements. Arrows ( ~ ) indicate change of one treatment to another. Plus signs ( + ) indicate that medication is added to an existing regimen. . Number of subjects. The numbers are shown separately for each treatment condition and untreated controls; they indicate the number of subjects who completed the trial and for whom test data were available. The subscripts n E and nNE denote epileptic and non-epileptic controls, respectively. A range is given for n when not all subjects completed all tests. Occasionally, we were unable to determine these numbers for the separate treatments (e.g., when only an overall n was provided), or for one or more outcome measures. This is indicated by a question mark. . Drop-out rate. This gives a rough indication as to whether a selection artifact might have developed during the trial. An overall rate is given separately for subjects on AEDs and untreated controis. About half the studies reviewed mention drop-out losses and present sufficient data to compute a drop-out rate for each outcome measure. A range may be given here as well due to incompletion in various degrees. A few studies explicitly state that no drop-out losses occurred (nil). In others, drop-out losses are mentioned but insufficient data is provided to compute a loss rate (?). Often, drop-out losses or their absence are not mentioned (n.m.), which may or may not

J. Vermeulen, A.P. Aldenkamp / Epilepsy Research 22 (1995) 65-95

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Table 1 Design nomenclature and classification Abbreviated designation

Design name

Definition

Posttest

Posttest-only

Single Parallel

Single-group pretest-posttest Parallel groups

X-over

Crossover

One or more groups of subjects are tested after (but not before) receiving treatment. A single group is tested both before and after the treatment period. Two or more groups are assigned to different treatment conditions and tested both before and after the treatment period. The same subjects are tested under different treatment conditions, counterbalancing the order of treatments.

Randomized treatment allocation, or treatment sequencing in a crossover design, is indicated by the suffix R.

mean that no such losses occurred. Sometimes a minimum rate is quoted ( > ) , more subjects may have been lost, but the data are unclear or ambiguous in this regard. 4. Design. Table 1 gives an overview of the general design types encountered. Occasionally, we were unable to discover a consistent principle underlying the scheduling of treatments and assessment points, or different schedules were employed for different subjects. In such cases the design was classified as unclear (?). 5. Number of cognitive variables. This gives an indication of the possible scope of the study with respect to cognitive functioning; also, this is a statistically relevant characteristic (see Results). Uncertainty as to the number of variables actually employed (?) in analyzing the data may occur even if the tests used are mentioned; often multi-

ple outcome variables may be derived from a single test (e.g., response speed, accuracy, subscales in intelligence tests). . Time on AED. This characteristic is important in judging the relevance of the results to chronic AED use. Its meaning depends on the particular design employed. In a posttest-only design (Table 1) the figures quoted relate to the duration of treatment prior to the assessment point. In repeated measurement designs with one or more groups (i.e., Single and Parallel) this refers to the duration of the experimentally changed AED treatment or the continuous medication interval studied. With multiple assessment points during the trial, the maximum interval studied is given. In a crossover design where multiple AEDs or dosages are given, this refers to the time on each AED c.q., dosage. An exception to this rule was

Table 2 Acute dose volunteer studies (1970-1994) Study

Treatments

Subjects (n)

Cognitive variables (n)

Time on dose

Idestr6m et al., 1972 [34]

PHT × plac PHT × plac PHTDh i × PHToj o × plac PHT × PB × plac VPA X PB × (VPA + PB) × plac LTG × PHT × DZP × plac CBZ × plac VGB × LZP X plac CBZ × CBZct × plac CBZ~ × plac none ~ (CBZ × OCBZ)

15 20 6 6 8 12 12 10 6 10 6

5 11 1 1 ? 14 5 13 3 7 2

2 hours 1 day 7 hours 7 hours 1 hour 1 day 34 h 1 day 1 day 14 h 10 h

Houghton et al., 1973 [35] Boxer et al., 1975 [36] Cohen et al., 1985 [37] MacPhee et al., 1986 [38] Saletu et al., 1986 [39] Tedeschi et al., 1989 [40] Van der Meyden et al., 1992 [41] Zaccara et al., 1992 [42]

All studies employ cross-over designs with randomized assignment to AEDs or placebo. Untreated controls are not employed.

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made for studies where the 'treatments' consist of assessing subjects at the expected peak and trough times in diurnal serum level fluctuations. The duration of the treatment prior to assessment was considered relevant here. A time range indicates that the interval between the relevant assessment points was variable between subjects. Time off AEDs is given in withdrawal studies, measured from the beginning of withdrawal to end of the trial.

3. Results

In order to structure our evaluation, articles were first classified according to the type of subjects involved, i.e., healthy volunteers vs people with epilepsy. Epilepsy studies were further subdivided according to treatment and design features discussed later. In line with the major conclusion validity theme in this paper, methodological/statistical issues pertinent to each study category will be emphasized. 3.1. Healthy volunteer studies Tables 2 and 3 list the reports of volunteer studies [28,30,34-48] we found in literature. From these tables it is evident that phenytoin (PHT) has received most attention, followed by carbamazepine (CBZ).

69

Other AEDs are represented by one or two smallscale trials only.

3.1.1. Methodological considerations Volunteer studies have the considerable advantage that factors such as seizure frequency and severity, or differences between AEDs in seizure control efficacy, do not confound the interpretation of the results. Volunteers offer the best opportunity to study the absolute cognitive effects of AEDs, as opposed to no treatment, which is rarely feasible in epilepsy. Also, AED administration is not constrained by clinical considerations; thus, all studies were able to implement relatively powerful cross-over designs with randomized assignment to AED(s) or placebo. However, these studies also suffer from at least three conclusion validity problems. 3.1.1.1. Generalizability across subjects. Arguably, volunteers are not representative of the population to which generalizations are to be made: the cerebral substrate in epilepsy patients and volunteers is different, hence, the drug response may be different. More specifically, one might hypothesize that an AED has less cognitive impact when imposed on a normally functioning brain than on an epileptic brain. 3.1.1.2. Generalizability across treatment durations. Owing to practical and ethical considerations, drug exposure periods in volunteer studies are typically

Table 3 Short-term exposure volunteer studies (1970-1994) Study

Treatments

Subjects (n)

Drop-out rate

Cognitive variables (n)

Time on AED

Stephens et al., 1974 [43] Smith and Lowrey, 1975 [44] Thompson et al., 1980 [45]

none ~ (PHTDhi X PHTol o) none ~ (PHT X plac) PHT X plac CBZ X plac none --->(PHT x plac) none --* (VPA × plac) none --* (PHT X CBZ) ~ none none ---, (PHT x CBZ) --+ none OCBZDh i X OCBZD] o x plac

107 10 8 8 8 10 21 15 12

3% n.m. n.m. n.m. n.m. n.m. 30% n.m. nil

9 12 6 6 16 17 12 1 > 12

2 weeks 3 weeks 2 weeks 2 weeks 2 weeks 2 weeks 1 month 1 month 14 days

Thompson et al., 1981 [46] Thompson and Trimble, 1981 [47] Meador et al., 1991 [30] Meador et al., 1993 [28] Curran and Java, 1993 [48]

All studies employ cross-over designs with randomized assignment to AEDs or placebo. Untreated controls (n = 8) are employed only by Thompson et al. [45], but test data are not provided.

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relatively brief. Tables 2 and 3 show that there is a natural dichotomy, studies involving either acute (a day or less) or short-term exposure (two weeks to a month). Exposure durations not representative of those in epilepsy patients on chronic treatment represent a major validity issue.

3.1.1.3. Statistical conclusion validity. A review of Tables 2 and 3 also reveals that small sample sizes and multiple outcome measures (usually in combination) are characteristic of these studies. Disregarding the Stephens et al. study [43], an obvious outlier with n = 107, the 'average' study uses about as many variables as subjects. This situation is somewhat typical of cognitive AED research in general, which is the reason for alerting the reader here to the statistical problems associated with it. (i) Statistical power. With small samples, 'no difference' or 'no effect' claims must be regarded with caution, as they might simply reflect inadequate statistical power. Unfortunately, none of these studies mention the power available. In fact, the issue of statistical power is considered in only one volunteer study [30] in connection with a 'no difference' claim, i.e., that the cognitive effects of PHT and CBZ are very similar. All these studies, with the exception of Stephens et al. [43], must have power problems, though. Some might have sufficient power to detect medium-sized effects, but most are at best sensitive only to large effects. To the statistically inclined reader familiar with, e.g., Cohen's power handbook [4], the sample size given in the tables will convey at least a sense of the power achieved in these studies. (ii) Multiple comparisons. One approach to the statistical analysis of data obtained on multiple outcome measures is to run separate tests on them, each at the conventional 5% significance level (this is done very often). However, the probability of falsely concluding that one or more significant effects exist (Type I error), increases as a function of the number of statistical tests performed and quickly runs out of control. For example, with 10 comparisons there is a 40% chance of obtaining one or more significant effects [49], which is unacceptably high. Separating the chance results from the real effects then becomes very difficult. There are good reasons for employing multiple outcome measures of course, but the uncritical use of

a large number of them in combination with small samples may result in a quagmire of false-positive and false-negative findings.

3.1.2. Reported cognitive effects The nine acute exposure studies (Table 2) are mainly concerned with toxic phenomena or neurological side-effects (e.g. disturbed eye movements, unsteadiness, sedation). Acute cognitive effects may be due to a lack of tolerance to the drug when given in single doses, and may disappear after a period of adjustment to the drug [2,46,50]. They will be excluded from consideration here. Two short-term studies (Stephens et al. [43] and Curran and Java [48]; Table 3) fall below our methodological/statistical presentation minima because descriptive statistics are presented only for the variable(s) yielding a significant effect. Thus, six studies remain. Smith and Lowrey [44], using three alternate forms of the Wechsler intelligence scale (WAIS) with elderly subjects, reported beneficial effects of three weeks of PHT (200 mg/day) on various WAIS subtests (Information, Comprehension and Digit Symbol) and on the Full Scale IQ (a difference of more than four IQ points), attributing these improvements to the underlying factor of improved concentration. Arguably, however, this outcome might reflect differences in practice effects for PHT and the baseline condition, the latter consisting of the averaged pretrial and placebo scores. Given the testing sequence employed, this results in a confounding of PHT performance with more testing experience, which presumably invalidates the reported beneficial effects. Also, the problem of spurious significance due to multiple measures was not considered. Thompson et al. [45], in two experiments, administered PHT or CBZ (300 and 600 m g / d a y respectively) to eight subjects for two weeks. For PHT, adverse effects relative to placebo were found on five of the six memory measures aimed at the ability to remember new information. By contrast, none of the CBZ/placebo comparisons was significant. In both experiments, separate analyses were run on each outcome measure without protection against false positives. In another study, Thompson et al. [46] found adverse effects relative to placebo using a dosage of

J. Vermeulen, A.P. Aldenkamp / Epilepsy Research 22 (1995) 65-95

300 m g / d a y PHT given for two weeks (n = 8), on 6 (out of 16) measures covering memory, concentration, mental and motor speed. On five of the measures strong correlations (in the 0.70 to 0.90 range) with PHT serum levels were obtained, such that performance decreased at higher serum levels. However, only two measures showed both significant differences with placebo and correlations with serum PHT concentrations, suggesting that these two approaches may yield different results. Again, however, outcome measures were analyzed separately and no protection against spurious significance due to multiple comparisons was used. Thompson and Trimble [47] examined the effects of two weeks of 1 g / d a y sodium valproate (VPA) in 10 subjects with a battery of cognitive tests nearly identical to that in the Thompson et al. [46] PHT study mentioned above. Overall, there was little evidence for differences between VPA and placebo. Only two significant differences were found with 17 cognitive outcome measures, analyzed with separate t-tests, without protection against false positives; no significant correlations (R not given) with serum concentrations were observed. Meador et al. [30] directly compared one-month exposure to PHT and CBZ (n = 21) using AED dosage adjustments to obtain serum concentrations in the therapeutic range. In recognition of the problems associated with multiple comparisons (separate Ftests were used), the only two comparisons between PHT and CBZ that reached significance were considered spurious. Their overall conclusion was that the cognitive effects of PHT and CBZ are very similar; subtle differences in cognitive side-effects may exist but such differences appear not to be clinically significant. Statistical vs clinical significance is a very important question that should be addressed in any cognitive AED study, though it may not have an easy answer (cf. Conclusion). As regards the absolute effects of the drugs relative to nondrug conditions (averaged data from preand post-trial testing), both produced impairment on Choice Reaction Time, CBZ impaired performance on a conflict interference task, and PHT impaired a measure of motor speed and coordination. In an extension of the 1991 study (mainly concerned with EEG effects) on a subset of the original subject sample (n = 15), Meador et al. [28] found

71

that CBZ but not PHT impaired memory performance (Story recall) as compared with nondrug baselines. The two drugs did not differ reliably in their effects, though. 3.1.3. Discussion The Thompson et al. [45,46] and Thompson and Trimble [47] studies illustrate the interpretation problems due to low power and multiple comparisons. All three studies are obviously low powered (with n = 8, 8 and 10 respectively). 'No difference' findings, as in the CBZ experiment [45] or the VPA study [47], thus carry little weight. On the other hand, where significant effects are reported there is the problem that no protection against spurious significance due to multiple comparisons was used in these studies. Faced with this problem, one might adopt a more conservative significance level for each comparison to achieve an acceptable overall o~. One option is to employ the Bonferroni correction, setting the individual significance levels to o~ divided by the number of statistical tests performed. Thus, in the first Thompson et al. [45] PHT study, one-tailed t-tests were used, only one of them reaching the more strict 1% significance level that would be required after the Bonferroni correction; similar loss of significance would occur in the other Thompson et al. PHT study [46]. However, the price to pay for such protection is reduced power and only strong effects will be declared significant. If multivariate analysis is employed, rather than fragmented individual comparisons, the power also generally declines as more dependent variables are used. The magnitude of effects 'worth detecting' is a point examined more fully in the Conclusion section. In summary, it seems difficult to identify any reliable specific effects of PHT, CBZ or VPA on cognition against this background of possible false positives and false negatives in these three studies. The Meador et al. studies [28,30] compare favourably to the other volunteer studies in terms of exposure duration (a month) and sample size (n = 21 and n = 15 respectively). Still, the 'no d~fference' conclusion as regards the cognitive profiles of CBZ and PHT must be regarded with caution in the absence of a formal power analysis showing what

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J. Vermeulen, A.P. Aldenkamp / Epilepsy Research 22 (1995) 65-95

effect sizes could have been detected. Compared to nondrug conditions, 3 out of 12 cognitive measures showed significant effects; if a Bonferroni correction were applied here (setting c~ at 0.004), only the impairment on the Stroop test would remain significant. A last point to be made is that even the short-term studies discussed here may cover a period when 'positive tolerance' for cognitive side-effects is still developing. To what degree and at what rate such tolerance to initial adverse cognitive effects is acquired with prolonged treatment is largely unknown. On the other hand, a number of authors have recognized the possibility that chronic AED use may result in insidious cognitive losses that emerge only after extended periods of treatment [51]. Extrapolation of the results obtained in volunteer studies to patients on chronic AED therapy thus seems hazardous: acute but possibly transient effects are emphasized, and 'slow' long-term effects are outside the scope of volunteer studies. What we are left with after these considerations is the conclusion that volunteer studies offer very limited data to go on; neither do they suggest reasonable hypotheses to test in studies with epilepsy patients.

3.2. Studies in epilepsy Studies of patients with epilepsy were further subdivided into the categories polytherapy vs monotherapy. Polytherapy studies form the mainstay of cognitive AED research, presumably because they involve a category of patients who might benefit from treatment manipulations aimed at, e.g., improving seizure control.

3.3. Polytherapy studies Studies were classified into the polytherapy category if subjects were treated with more than one drug at a time and no comparisons between individual drugs, or single drug vs no AED, were possible. Studies involving polytherapy [32,33,51-76] are listed in Table 4.

3.3.1. Methodological considerations 3.3.1.1. Treatment reproducibility. Polytherapy is by nature a heterogeneous treatment category; thus, one

finds treatment descriptions such as 'various combinations of the three major AEDs'[52] or 'PHT and one or more other AEDs' c.q. 'drug regimens exclusive of PHT' [51], or even 'no attempt was made to standardize drug therapy as part of the study' [75]. Obviously, widely different drug regimes would fit such descriptions, and results established with one regimen may not apply to another. Also, the polytherapy manipulations used in many studies actually are quite complex, making replication problematical. For example, all polytherapy reduction studies are done as part of individualized programs of therapy rationalisation. That is, patients did not have their medications changed for research purposes, and different types of medication change were not subjected to randomization. Rather, changes were typically made 'according to the individual needs of each patient' [65]. The clinical considerations underlying the medication changes are a major ingredient of the treatment package, albeit one that may not be easily reproduced.

3.3.1.2. Drug interactions. Combinations of AEDs may alter metabolism to produce changes in the level of active a n d / o r toxic metabolites. Examples include the decrease in CBZ levels due to the increased elimination of the drug when given together with PHT a n d / o r phenobarbital (PB), and the interactions of felbamate with most current AEDs. Such interactions can alter seizure control efficacy and may be relevant to cognitive functioning. With multiple drugs, identifying the components of a treatment most responsible for any observed effects presents a difficult problem. 3.3.1.3. Serum concentration-effect relationships. Cognitive AED effects may be examined through an analysis of the relationship between test scores of subjects and their individual serum drug levels, and this approach seems to offer a way out of the problem mentioned above. In fact, a number of studies report such relationships suggesting that, generally, higher serum levels are associated with lower cognitive scores. However, in patients with epilepsy, higher serum concentrations may be the reflection of higher AED doses prescribed for more severe epilepsy [77], perhaps with seizures not fully controlled [78]. Also, AEDs may interact on receptor sites, which would

8-20 10/20/15 43 28 312 12 9 13 8 25/20-21/ 14--15/22

P + (VPA × plac) P/(P --" (P~ea/Prea + CBZ)) PHT + (CLZ × PB) Pshi × Pslo P P --~ Mono P ~ (Pred + ZNS) P ~ Pmod P ~ VPA P / ( P ~ (PPrtT-/PcBz- / PVPA- )) P ~ Prnod P --~ Pmod PHT/Ppwr +/PI'HT P / ( P + VGB) CBZ -~ (CBZ + VPA) PPHT+ /(PPHT+ ~' PPHT ) (PcBz ~ Pcazcr)/n°ne P + (VGB × plac) P + (LTG × plac) P ~ (P + (VGB/plac)) P/(PczP+ --~ PczP- ) P -~ Pmod Pmod CBZ + (OCBZ × plac)/VPA + (OCBZ × plac)/PHT + (OCBZ × plac)/OCBZ

35/28

P~ox+/Ptox-

Van Rijckevorsel et al., 1990 [64] Durwen et al., 1992 [65] Dodrili and Wilensky, 1992 [51] McGuire et al., 1992 [66] McKee et al., 1992 [67] May et al., 1992 [68] Pieters et al., 1992 [69] Gillham et al., 1993 [70] Smith etlal. , 1993 [71] Dodrill et al., 1993 [72] Chataway et al., 1993 [73] Durwen and Elger., 1993 [74] Mitchell et al., 1993 [75] McKee et al., 1994 [76]

57 8-12

P (PDhi ~ Pome ~ Polo)/n°ne

26 13 11 / 11 / 11 15/15 16 12/17 15 24 40-44 83/85 11/11 27 ? 9/9/10/7

on AEDs

Reynolds and Travers, 1974 [52] Dekaban and Lehman, 1975 [53] Matthews and Harley, 1975 [54] Sommerbeck et al, 1977 [55] Thompson and Trimble, 1980, 1982 [33,32] Wilensky et al., 1981156] Thompson and Trimble, 1983 [57] Corbett et al., 1985 [58] Ludgate et al., 1985 [59] Berent et al., 1987 [60] Durwen et al., 1989 [61] Prevey et al., 1989 [62] Duncan et al., 1990 [63]

Subjects (n)

Treatments

Study

Table 4 Polytherapy studies (1970-1994)

33% 18% n.m. n.m. 16-17%

?

n.m.

19%

-

-

-

-

-

15NE -

X-over(R)

n.m. 83% n.m. 33% n.m. 6% 13% 46-51% 8% 52% n.m. -

Single Parallel Parallel Single Parallel Parallel X-over(R) X-over(R) Parallel(R) Parallel Single

28%

-

?

?

Single Single Single Single Parallel

n.m.

8

?

18 20 7 7 15 22 10 9 19 4 19

5

17 16 18 17 8

1

3 6 33 30 6 ? 20

Posttest Parallel Posttest X-over(R) Parallel X-over(R) X-over

n.m. n.m. n.m. 33-73% n.m. 22% n.m.

Cognitive variables

(n)

-

-

-

-

-

-

-

6 NE

-

untreated contols

Design

Dropout rate

3 weeks

3 months 5days 5 years 4 weeks 5 days 10 weeks 4 weeks 12 weeks 18 weeks 12 weeks 2 weeks 5 days ?

5 months 4 weeks

1 year 24 weeks ?

12 weeks 6 months 4 months 3 months ?

14-20 days ?

?

Time on AED

I

Q~

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not necessarily be reflected in serum concentrations. Such factors greatly reduce the interpretability of relationships between serum concentrations and cognitive performance. 3.3.1.4. Seizure confound. Polytherapy is typically given to patients with refractory epilepsy, and separating seizure effects from AED effects may thus be very difficult, particularly in add-on studies, where the cognitive evaluation is usually made in connection with an efficacy trial. That is, adverse cognitive AED effects may be masked by beneficial effects of better seizure control. Also, patients with refractory seizures may not be representative of the general population with epilepsy. Concerns regarding statistical conclusion validity due to small samples in combination with multiple outcome measures apply to many of these studies as well. Also, designs are sometimes employed (i.e., Posttest and Single) that may be regarded as generally uninterpretable (see the section on monotherapy studies). Due to the validity threats described above, acting singly or simultaneously, drawing conclusions about the cognitive effects of individual agents from polytherapy studies was not considered meaningful. We will therefore refrain from discussing the individual studies listed in Table 4.

3.4. Monotherapy studies Cognitive effects of an individual AED are best assessed in monotherapy [9], but such studies may be subject to interpretation problems as well. We first comment on those studies in which conclusion validity threats are so severe that inferences about cognitive side-effects of AEDs are generally impossible. One category of such studies employs a design (the non-randomized posttest-only design) that is too weak to permit reasonably valid conclusions. A second category comprises studies that are problematical because the methodological/statistical presentation provides insufficient information for evaluation. 3.5. Studies with a non-randomized posttest-only design The natural design to use in cognitive A E D research, where the concern is with performance trends over time, is some form of repeated measurement design in which the same patients are pretested and posttested with one or more (as in crossover designs) intervening treatments. In fact, most monotherapy studies employ one variant or another of this general class of designs. The practical difficulties associated with repeated testing and long-range follow-ups may explain why a

Table 5 Monotherapy studies with a non-randomized posttest-only design (1970-1994) Study

Treatments

Subjects (n)

on AEDs

untreated controls

Cognitive variables (n)

Dodrill, 1975 [26]; Dodrill and Temkin, 1989 [26]

PHTshi/PHTsl o

36/34

-

19

Butlin et al., 1984 [78] Andrewes et a1.,1984 [79] Andrewes et a1.,1986 [80] Brodie et al., 1987 [81] Gillham et al., 1988 [82] Gillham et al., 1990 [83] Gilham et al., 1991 [84] Bigarella et al., 1991 [85] Bittencourt et al., 1992 [86] Verma et al., 1993 [87] Aldenkamp et al., 1994 [88]

PHT/CBZ/VPA CBZ/PHT CBZ/PHT/none PHT/CBZ/VPA/none

57/34/25 16/16 21/21 15/30/9 40/19 19/35/30 48/28 20 7/16/8 19/19 25/25

21 E 14E/llNE 26 E 26E/24NE 26E/24NE 35NE 35NE -

15 30 9 12 12 11 6 5 7 14

CBZ/P/none PHT/CBZ/VPA/none VPA/P/none PB/none PHT/CBZ/VPA/none CBZ/PHT PHT/CBZ

Drop-out rates are impossible to determine in these studies.

?

Time on AED

?

3.2/4.8 yr 3.6/5.8 yr > 3 months ? > 3 months > 12 months ? > 1 year ? > 1 year

J. Vermeulen,A.P. Aldenkamp/ Epilepsy Research 22 (1995) 65-95

number of studies [24,26,78-88] have resorted to a cross-sectional approach, in which one or more treatment groups are tested only after (but not before) receiving AED treatment. However, with non-randomly formed treatment groups this design has so many inherent weaknesses that it is better avoided. This prompted us to treat the interpretative difficulties of monotherapy studies employing this design (Table 5) separately. Also, the repeated measurement studies discussed later sometimes incorporate a nonrandomized posttest-only comparison as well, and the same validity concerns apply there.

3.5.1. Methodological considerations An obvious flaw in this design is the absence of a pretest, so that there is no way of knowing whether the treatment was related to any kind of cognitive change [89]. Due to the lack of pretest data, differences among the patient groups in cognitive performance after AED treatment cannot be unequivocally be attributed to a treatment effect: they might simply reflect differences that already existed before treatment. Also, the absence of differences at the posttest does not rule out medication-related changes, which may well have the effect of reducing the magnitude of any differences that existed prior to treatment. Note that it is a different matter in experiments where random treatment assignment insures that all factors conceivably relevant to the outcome of the study are distributed equally over the treatment groups. Here, pretests can be dispensed with, though this is not advisable in view of the considerable drop-out rates in AED studies (see tables). However, none of the studies discussed in this review employs a randomized posttest-only design. 3.5.1.1. Selection. AED regimens in these studies were established for clinical purposes, i.e., treatment assignment was not the result of some randomization procedure. Obviously, AEDs are not randomly prescribed by physicians; the seizure type is an important factor determining the type of antiepileptic medication, but it is not the only one. Dodrill [90] has argued convincingly that differences in intelligence, financial status, or ability to comply with complex AED regimens may result in different prescriptions. For example, there is evidence that, at least in some countries, PHT may be given to other types of

75

patients than CBZ because it is cheaper and can be given once a day [88]. Systematic differences in such characteristics between subjects assigned to different treatment conditions may result in pseudo effects that have nothing to do with any cognitive AED effects. In some studies, relevant background characteristics are measured, such as age, education, IQ, duration of epilepsy, age at onset, seizure frequency, as a check on the comparability of the treatment groups. By showing that the groups to be compared did not differ in such characteristics, or arguing that the differences would not have an important influence on cognitive performance, some studies [81,83] attempt to take care of the selection threat. However, once the safeguard of randomization has been removed, one can never be certain that some variable that has been overlooked will not bias the evaluation of an experiment [91]. As Dodrill and Troupin [25] have pointed out, selection biases are not necessarily eliminated by matching for age, education, seizure type and so on, as is done in some studies. For example, Andrewes et al. [80] conclude that PHT shows an overall trend towards poorer performance on several cognitive tasks when compared to CBZ. This study is frequently cited as evidence for the cognitive side-effects of PHT. As Table 5 shows, however, the period of drug exposure is different in the two groups (on average 3.6 years for CBZ and 5.8 years for PHT), and it is conceivable that longer drug exposure in itself, regardless of the type of drug, leads to performance differences. Remarkably, other posttest-only studies do not consider such differences in drug exposure, and it is worth noting that in some studies treatment duration is not even mentioned.

3.5.1.2. Differential drop out. Even with randomly formed treatment groups, there is no guarantee that the initial comparability between groups will be maintained over time [89]. Attrition from a longitudinal study is not necessarily random, i.e., may be systematically related to treatments. Different kinds of subjects might drop out of different treatment conditions, resulting in a selection artifact developing during a trial, i.e., treatment groups may no longer be comparable at the posttest. Checking whether attrition from an experiment has been ran-

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dom or systematically related to the treatments should be an important component of all research on cognitive AED research. However, in a posttest-only design with only the enduring subjects to go on, there is no way to evaluate whether differential drop-out has produced pseudo effects. The deficiencies of the non-randomized posttestonly design are well recognized in methodological circles [92]; Cook and Campbell [89] consider this an example of a generally uninterpretable design. With one exception, though, these studies do not attempt to make explicit and rule out the validity threats inherent in this design. Gillham et al. [83], however, do consider (but dismiss) the possibility that observed differences between groups might have been due to the operation of selective factors. Most of these studies mention correlations between serum drug levels and cognitive performance. The interpretation difficulties associated with such data are the same as discussed in connection with polytherapy studies. In our opinion, the plausibility of selection differences with AED regimens established for clinical purposes renders this design uninterpretable. It should not be attempted in further cognitive AED research.

In a number of cases the reasons are obvious from the question marks in Table 6, e.g., uncertainties regarding the number of outcome variables (Butlin et al. [95]), or the number of subjects in each group who took a particular test at a particular assessment point (Butlin et al. [95]; Smith et al. [99]; Mitchell and Chavez [98]). Of special note is the large Veterans Administration Cooperative Study [99], where a behavioral toxicity battery was obtained before and at 1, 3, 6 and 12 months after the initiation of monotherapy with PB, CBZ, PHT or primidone (PRM) in patients who were previously untreated or undertreated. At the initiation of the study, 618 received the full battery, but it is unclear what number of patients were evaluated at subsequent test sessions, and information regarding performance levels in the drug groups prior to treatment was not presented. It is also unclear how many statistical tests were performed, but it may have been hundreds, and there appears to have been no adjustment of the significance level. These and other concerns with this study have been discussed extensively by Meador and Loring [3] and Massagli [20]. Other reasons for listing studies in this category include incomplete descriptive statistics as regards cognitive performance on all variables at all assessment points (Browne et al. [93]; Gannaway and Mawer [94]; Smith et al. [99]), uncertainties regarding the statistical test used (Butlin et al. [95]; Wilenski et al. [96]), or presenting conclusions unsup-

3.6. Studies providing insufficient information The monotherapy studies employing a design other than the non-randomized posttest-only design did not all meet our presentation minima [93-99] (Table 6). Table 6 Monotherapy studies providing insufficient information (1970-1994) Study

Treatments

Subjects (n) on AEDs

Browne et al., 1975 [93] Gannaway and Mawer, 1981 [94] Butlin et al., 1984 [95]

Wilensky et al., 1985 [96] Aldenkamp et al., 1987 [97] Mitchell and Chavez, 1987 [98] Smith et al., 1987 [99]

(plac -~ E S M ) / n o n e PHT/none

37 13

none -~ ( P H T / C B Z / V P A ) / n o n e (PHT ~ C B Z ) / P H T (CBZ ~ V P A ) / C B Z ZNS × CBZ CBZ ~ (CBZ × C B Z c R ) / n o n e CBZ/PB

?/?/? ?/? 7/7 4 11 ?/?

PB/PRM/PHT/CBZ/none

7/?/717

Dropout rate

Design

36 6 NE

5% 28%

Parallel ?

?r~E llNE -

n.m. n.m. n.m. 50% n.m. ?

Parallel Parallel Parallel X-over X-over(R) Parallel

? ? ? 4 14 2

3 months 3 months 3 months 12 weeks 3 months 12 months

?

Parallel(R)

18?

12 months

untreated controls

75

Cognitive variables (n) ? 4

Time on AED

8 weeks ?

J. Vermeulen,A.P. Aldenkamp/Epilepsy Research 22 (1995) 65-95

77

Table 7 Continued treatment monotherapy studies (1970-1994) Study

Treatments

Subjects (n) on AEDs

untreated controls

Dropout rate

Design

Cognitive variables

Time on AED/dose

(n)

Single drug studies MacLeod et al., 1978 [100] MacPhee et al., 1986 [101] Amman et al., 1987 [102] O'Dougherty et al., 1987 [103]

(PBD1o ~ PBDhi)/none CBZ + (SAD × plac) VPAsh i × VPAsl o none ~ (CBZsh i × CBZsIo) / none

19 8 46 6-11

20NE llNE

n.m. n.m. 6% 18--45%

Parallel X-over(R) X-over(R) Parallel

2 7 26 8

7 - 8 days 18h ? 2 w k - 1 yr

Amman et al., 1990 [104] Reinvang et al., 1991 [105] Brouwer et al., 1992 [106] Larkin et al., 1992 [107] Rtinnberg et al., 1992 [108] McKee et al., 1993 [109] Amman et al., 1994 [110]

CBZsh i × CBZsl o CBZsh i × CBZsl o (VPA --->V P A c R ) / n o n e none ~ CBZ (none -~ C B Z ) / n o n e CBZo. d × CBZb. d PHTsh i X PHTsl o

50 22 10-12 7 14 14 42-50

12NE 14NE -

n.m. n.m. n.m. 46% nil 26% n.m.

X-over(R) X-over(R) Parallel Single Parallel X-over(R) X-over(R)

22 14 27 10 13 11 26

most > lyr > 1 month 4 weeks 12 weeks 6 weeks 8 weeks ?

Dodrill and Troupin, 1977, 1991 [27,25]

CBZ × PHT

4O

2%

X-over(R)

24

4 months

Vining et al., 1987 [111] Calandre et al., 1990 [112]

PB X VPA PB/VPA/none

21 23/26

40NE

25% 23%(E)/ 33%(NE)

X-over(R) Parallel

35 3

6 months 9 - 1 2 months

Meador et al., 1990 [113] Forsythe et al., 1991 [114]

PB × PHT × CBZ none --->( C B Z / P H T / V P A ) / none

15 14/14/14

31NE

29% 34%(E)

X-over(R) Parallel(R)

9 8

Aikiae et al., 1992 [115] none ~ (OCBZ/PHT) Bittencourt et al., 1993 [116] PB ~ CBZ PB ~ PHT Helmstaedter et al., none ~ ( C B Z / V P A ) / n o n e 1993 [117]

14/15 20 22 11/5

19NE

22% 16% n.m.

Parallel(R) Single Single Parallel

7 6 6 20

Craig and Tallis, 1994 [118] Pulliainen and Jokelainen, 1994 [119]

12/16 23/20

21NE

40% 27%

Parallel (R) 18 Parallel (R) 24

Multiple drug comparisons

none ~ ( V P A / P H T ) none --, ( C B Z / P H T ) / n o n e

-

3 months 1 year 12 months 6 months 6 months 6 - 8 weeks 1 year 6 months

Table 8 Monotherapy withdrawal studies (1970-1994) Study

Gallassi et al., 1986 [120] Gallassi et al., 1987 [121] Gallassi et al., 1988 [122] Gallassi et al., 1990 [123] Gallassi et al., 1992 [124] Aldenkamp et al., 1993 [31] Tonnby et al., 1994 [29]

Discontinued treatments

PB/CBZ PHT/none PHT/CBZ/none VPA/none PB/PHT/CBZ/VPA/none PHT/CBZ/VPA/none PHT/CBZ/VPA/none

Subjects (n)

Drop-

Cognitive

on AEDs

untreated controls

out rate

variables (n)

6/5 10 12/13 20 27/16/18/29 10/56/17 10/56/17

10NE 26 NE 20 NE 28N~ 83NE 83NE

> 31% 33% ? 31% 33% 17% 17%

10 13 13 13 10 12 4

Time off AED

21 months 21 months 21 months 21 months 21 months 6 - 7 months 6 - 7 months

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ported by inferential statistics (Aldenkamp et al. [97]). It should be noted that certain studies listed earlier in the polytherapy and non-randomized posttest-only tables would belong in this category as well.

3.7. Remaining studies with a repeated measures design The remaining monotherapy studies fall naturally into two broad categories: they are either concerned with the effects of continued AED therapy [25,27,100-119] (Table 7) or with the effects of treatment discontinuation [29,31,120-124] (Table 8). The latter approach faces specific problems that deserve separate discussion. A distinction will be made here into studies involving a single AED, and those concerned with comparisons of several forms of monotherapy.

3.8. Continued treatment: single-drug studies Most single-drug studies have employed some form of treatment partitioning, that is, different dosages or serum levels of the drug were contrasted. Larkin et al. [107] and R/Snberg et al. [108] are exceptions in that unchanged maintenance medication is studied.

3.8.1. Methodological considerations Exposing subjects to relatively higher and lower levels of their medications, and noting relative performance across these levels, seems a sensible approach. However, a general problem is that such differences in medication levels, if large enough, may have a confounding effect on the primary seizure activity regulation action of the drug; also, one or both levels may fall outside the therapeutic range, thus limiting the clinical relevance of the results. With small differences, by contrast, the treatments may be too similar to reveal much about the cognitive effects of the drug. Basically, three ways have been devised to manipulate serum levels in an ethically acceptable manner: (1) altering doses in subjects with inadequate seizure control, (2) using different formulations of the same drug, e.g., conventional versus controlled

release, with different pharmacokinetic profiles, and (3) taking advantage of normal time-of-day variations in serum concentrations, either by varying testing time (Reinvang et al. [105]) or by altering the time of medication relative to testing, as in the three studies by Amman and coworkers [102,104,110]. Also, a non-experimental approach is to dichotomize subjects post-hoc into low versus high dosage or concentration groups. Four of the eleven single-drug studies employ a no-treatment control group, and may thus also allow for the examination of 'absolute' cognitive effects; problems associated with this will be discussed in the context of multiple drug studies.

3.8.2. Reported cognitive effects 3.8.2.1. Dosage contrasts. MacLeod et al. [100] tested 19 epileptic patients first under low (8-15 /xg/ml) and then, a week later, under high (20-32 /zg/ml) therapeutic levels of PB. The low dosage, i.e., the level of medication they had been receiving when admitted to the hospital, consistently preceded the high dosage because of the long half-life of PB. All patients had tonic-clonic seizures. Information processing paradigms from experimental psychology, i.e., the Sternberg scanning task and Posners letter-matching task, were used for investigating speed of access to respectively short-term and long-term memory information. Relative to response times of 20 controls without medication, response times of patients in the short-term memory scanning task were strikingly slowed under high PB levels. However, increased PB did not slow responses in the task requiring access to information in long-term memory. These results suggest that PB selectively impairs short-term (but not long-term) memory functioning. The main problem with this otherwise interesting study is that patients are retested one week after an increase of the PB dose. As PB has a half-life of several days, one would expect that this period is too short to produce a meaningful contrast between treatment conditions, and it is somewhat surprising to find any cognitive effects at all. Thus, the relevance of evidence from this study is to chronic PB effects is unclear. Also, with only two measures, description of cognitive function was limited.

J. Vermeulen,A.P. Aldenkamp/ Epilepsy Research 22 (1995) 65-95

The small-scale (n = 8) MacPhee et al. [101] study concerns a one-day evaluation of the effects of a single additional 400 mg dose of CBZ, administered if ongoing seizure activity in patients on chronic CBZ monotherapy suggested that a trial of higher CBZ dosage might be merited on clinical grounds. Obviously, this exposure period is too short to evaluate chronic medication effects. Also, the CBZ serum levels in most patients are greater than 12 mg/1, i.e., concentrations were achieved that have generally been associated with toxic signs. The generally large effects reported are clearly not representative of chronic effects of CBZ in regular therapeutic doses. O'Dougherty et al. [103] assessed cognitive functions before and during CBZ monotherapy in children with newly diagnosed complex partial epilepsy. Following the baseline evaluation at the time of diagnosis (before starting CBZ), the children were assessed on low and moderate CBZ levels. Six- to 12-week intervals typically followed each testing session. Drug dosage changes were dictated by the clinical needs of the child. To obtain variation in the drug level when no dosage change was clinically indicated, predose or postdose drug level testing sessions were scheduled, based on the child's initial drug level. They thus employed a mix of methods to achieve high and low serum concentrations, which does not contribute to the interpretability of the study. There were no changes in performance from the baseline to low drug level assessment. Moderate CBZ levels had a mild beneficial effect on speeded eye-hand coordination (compared to baseline and low levels), but efficiency in leaming paired associates was reduced. There are several problems with this study. The no-treatment baseline is contaminated as three of the children had been previously treated: two with CBZ, one was a crossover from PB. The tests are considered insensitive to practice effects on the basis of the finding that control subjects (n = 11) did not show significant performance changes with repeated testing; changes in the epilepsy group were then analyzed without regard to the (nonsignificant) changes in the controls. Of course, with n = 11 only huge retesting effects would have reached significance. There is a confounding of testing experience with drug level, as for four children the high serum level testing preceded the low level, for two the reverse

79

was the case. The testing intervals are variable, and there are systematic differences in the intervals between the three conditions. Not all subjects are tested under all three conditions. For example, the comparison between low and moderate CBZ levels involved only six subjects (the others never had both low and moderate levels). 'No difference' findings based on 11 subjects or less obviously carry no weight. This study clearly has too many interpretation problems. 3.8.2.2. Time-of-day variations in serum levels. All

three studies by Amman et al. [102,104,110] employ an identical method of manipulating serum levels of VPA, CBZ and PHT in children with epilepsy. Drug concentrations within subjects were modified by giving the daily morning dose before or after the testing procedure, i.e., the children were tested when drug concentrations were expected to be low or at peak level, in a randomized crossover design. In the VPA study [102] the time of testing, i.e., drug levels, had virtually no effect on performance, suggesting that VPA has no harmful cognitive effects. Given the large sample size (n = 46) and the intrinsic power of a repeated measures design, this 'no effect' conclusion might carry some weight. Subjects in this study are described as having well-controlled seizures, that is, most subjects (93%) were seizure free for at least two months prior to the study. Variable seizure control was therefore considered unlikely to have been a confounding factor. However, it is arguably premature to conclude that a child no longer has an active epilepsy after such a relatively short seizure-free interval. Occasional unobserved seizures may have occurred at night, and it is worth noting that half the generalized epilepsy group (n = 34) had absence seizures, that might easily be missed as well. VPA and CBZ are short half-life drugs, and on a once-a-day regimen, serum levels may fluctuate widely [125]. Withholding morning medication to achieve the low concentration condition may have resulted in very low serum levels prior to testing, and regulation of ictal a n d / o r interictal epileptiform activity may have been less effective than at peak level after morning medication. On this account, drug concentrations may have been confounded with the severity of epileptiform activity, with the possible effect of spuriously decreased performance in the low concentration condi-

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tion, which might have obscured any real adverse drug effects. In the CBZ study [104], children performed significantly better at CBZ peak salivary levels on measures of seat activity (i.e., less fidgeting), attention span and motor steadiness, whereas response times appeared to be influenced in a task-specific manner. The authors concluded that 'CBZ in normal therapeutic doses does not impair psychomotor functioning and may actually produce improvement'. In line with the scenario developed above it could be argued that CBZ does not in itself produce improvement; rather, withholding medication induces relative impairment. Also, after a Bonferroni adjustment for 22 separate comparisons only a single effect would remain significant (reduced seat activity on one of the tasks). In the PHT study [110], a comparison of performance at peak and trough times revealed few if any effects of salivary concentration levels. However, as the authors point out, PHT concentrations in this study were quite low, i.e., below the therapeutic range in the trough condition, and at the low end of the range in the peak condition, and may thus have been too low to cause adverse cognitive effects. All three studies also report an analysis in which subjects were divided into high- and low-dose groups. For VPA this revealed a relative disadvantage of the high-dose group, but with CBZ and PHT no differences were found. In recognition of some of the difficulties associated with this non-randomized posttest-only approach, the authors emphasize that dosage may have been confounded with severity of seizure disorder, and that it is impossible to determine if higher doses of VPA or greater severity of epilepsy (leading to higher doses) were the factor underlying impaired performance. In the CBZ study (but not in the PHT study) it is noted that uncontrolled subgroup differences may have offset any effects due to CBZ dosage. Reinvang et al. [105] employed an approach similar to that in the studies of Amman and coworkers. Serum levels were monitored from 8 a.m. to 8 p.m., and subjects (n = 22, mostly adults) were tested twice at times close to the expected maximum (noon) and minimum (8 a.m and p.m.) serum CBZ concentration. Mean noon levels were higher than at 8 a.m. or 8 p.m. (32.9, 26.2, and 24.3/xmol/l respectively).

No consistent differences between performance at peak and trough times were found. Note the confounding of serum levels with time of testing.

3.8.2.3. Different formulations of the same drug. Brouwer et al. [106] monitored serum levels of conventional VPA and a controlled release formulation (VPAcr), as well as performance on attention and vigilance tasks in children. The switch from VPA to VPAc~ had no effects on cognitive performance. However, mean diurnal trough and peak serum levels were quite similar for the two formulations. Comparison of performance of the epilepsy group during VPA and WPAcr with that of matched controls showed no differences. This is a posttest-only comparison, however. Also, the sample size (10-12) is clearly inadequate to support a no-difference conclusion. McKee et al. [109] undertook a comparison of once- against twice-daily dosing of modified-release CBZ in 14 subjects. There were no significant differences in cognitive function between once and twice daily dosing 1 and 4 hours after ingestion of the morning tablet. The treatments under comparison had very similar pharmacokinetic and pharmacodynamic effects: lower trough levels were observed on the once-a-day schedule, but otherwise no important differences were noted between the two dosing conditions. Unsurprisingly, the similar CBZ treatments did not differ in their cognitive effects. 3.8.2.4. Maintenance medication. The Larkin et al. [107] study is another example of a generally uninterpretable design [89], the Single-Group PretestPosttest design, in which a single group of subjects is tested before and after a treatment period. Apart from repeated testing, this design faces other conclusion validity threats, e.g., maturation, or statistical regression effects. These are beyond the scope of the present paper, however (but see Cook and Campbell [89]). Most other studies that have employed this design fall in the polytherapy category (Table 4). R/Snnberg et al. [108], evaluated the memory effects of CBZ. They tested 14 newly diagnosed patients before the start of CBZ treatment and retested them 6 weeks later, comparing their performance to matched controls. Patients were seizure free during the treatment phase. No effects of CBZ treatment on

J. Vermeulen,A.P. Aldenkamp/Epilepsy Research 22 (1995) 65-95 memory functioning were found. However, this was a relatively low dose treatment: CBZ serum levels varied from 13 to 38 /xmol/l, and six patients had a level below the recommended lower therapeutic range of 20 /xmol/1. High CBZ levels were associated with lower performance on two of the tests, but such findings are difficult to interpret due to possible confounding factors such as the severity of the epilepsy. 3.8.3. Discussion The two studies that employ systematic dose manipulation (MacLeod et al. [100] and MacPhee et al. [101]) lack generalizability if only because they have the problem of very short exposure durations. Studies concerned with fairly normal time-of-day variations in therapeutic CBZ and VPA levels provide no convincing evidence that swings from peak to trough concentrations affect cognitive performance one way or the other. The same conclusion applies to low-level PHT variations. While not without interest, such findings reveal nothing about possible cognitive effects of these AEDs per se. Studies with different formulations of the same drug have the problem that the treatments may not have been different enough in terms of their effects on serum levels to make a difference. Studies employing these two types of treatment manipulation thus provide no information about the absolute cognitive effects of the drug under study. The RSnberg et al. study [108] suggests that six weeks of low dosage therapy with CBZ has no dramatic absolute effect on memory. 3.9. Continued treatment: multiple-drug studies These are all studies where multiple AED treatments are contrasted, which allows for examination of the cognitive impact of one drug relative to another. Four of the ten studies (Table 7) employ a no-treatment control group, and may thus be relevant to the issue of 'absolute' effects as well. 3.9.1. Methodological considerations Differential treatment effects are less elusive to examination than absolute effects, but they are also less informative. Without a no-treatment reference there is generally no way to tell whether a difference

81

between AEDs is the reflection of the negative effects of one drug or the positive effects of another, or a combination of both. Though the concern seems to have been mainly with adverse AED effects, it is at least logically possible that an AED has positive cognitive effects. Claims to that effect may actually be found in the literature [44,104]. Also, as Aikiae et al. [115] have observed, lack of evidence for differential cognitive effects does not prove that the AEDs under study do not affect cognitive function. Some interesting problems arise in assessing absolute cognitive effects in epilepsy. Deliberately withholding AED treatment from epilepsy patients to form a control group is unethical; also, with untreated patients a seizure confound would be likely. All untreated control groups in these studies thus consist of non-epileptic individuals. This rules out random allocation to AED vs control conditions. One complication with non-randomly formed groups is that the interpretability of the results may depend on the particular outcome pattern. For example, an outcome pattern where 'the able become more able' may be very difficult to interpret unequivocally. This particular pattern will not necessarily have anything to do with the effects of a treatment, but it may seem if it does. One would expect this pattern of data if the treatment and control groups differed because the latter were, say, brighter on the average and were using their aptitude to gain more from the testing experience than a treatment group. Other patterns might have a fairly straightforward interpretation, but this issue is beyond the scope of the present paper (it is examined in detail by Cook and Campbell [89], though). Even a welldesigned study with random allocation to AED groups might thus yield ambiguous results as regards absolute cognitive effects. 3.9.2. Reported cognitive effects Dodrill and Troupin [27] compared CBZ with PHT in a randomized cross-over design in adults (n = 40). No significant differences appeared on the WAIS and an the Halstead battery, but on supplemental neuropsychological measures, 4 out of 11 comparisons all favoured CBZ. Fourteen years later, however, a reanalysis [25] of the four cognitive variables that had yielded a significant difference, showed that when patients with high ( > 40 /xg/ml

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or > 30 /zg/ml) initial PHT levels were excluded, the statistical significance of the neuropsychological differences between the drugs disappeared. It was argued that the loss of statistical significance was not due to a smaller number of subjects (n = 29 and n = 15, respectively) in the successive analyses since the differences in mean cognitive scores became smaller. Trimble [126] has pointed out that the patients in the remaining small sample may have become highly selected, as nearly 70% of the original sample was excluded (non-randomly). Also, only variables that had shown a statistically significant difference in the original paper were reanalysed. It would have been of interest to know what happened to the nonsignificant differences on the other 20 cognitive variables in the first analysis; 9 of these favoured PHT, 11 favoured CBZ. Some of these differences might have reached significance, favouring one drug or the other. The 'no difference' conclusion thus at best applies only to the four variables that were reanalysed and for which data are provided, in a selected subject group. In the original study, 26 persons were on PHT and 20 on CBZ during the first crossover period. As it is important to counterbalance the order of treatments in a crossover design, six PHT first individuals were randomly eliminated, leaving 40 cases with a balanced drug sequence. However, subjects in the reanalysis were eliminated from the pool of 46 subjects, i.e., a sample where the drug sequence was n o t exactly counterbalanced. With the successive elimination of subjects the unbalance may have become better or worse; in theory, with only 15 subjects remaining, the drug sequence may have been completely unbalanced. The relevant data are not provided, however. It is also worth noting that none of the original t-tests would be significant after a Bonferroni correction, setting the a level for the 24 individual comparisons at 0.002 to achieve an overall 0.05 a level. That is, the original significant results may have been spurious to begin with. The study by Vining et al. [111] is a randomized cross-over study comparing PB with VPA in 21 childrem:The study reports a favourable profile of VPA compared to PB. Block Design, performance and full-scale IQ (PIQ and FSIQ respectively) of the

Wechsler Intelligence Scale for Children (WISC) and the Berkeley Paired Association Learning Task showed superior performance on VPA ( P < 0.01). Four other differences approached significance ( P < 0.05). There were no differences between VPA and PB in controlling seizures. This study employed a conservative significance criterion (0.01; 0.05 was considered a trend) due to the very large number of variables (n = 35). However, this may not have been conservative enough, as the probability of obtaining one or more spuriously significant outcomes is still high (about 30% c.q. 83% for the trends). With the Bonferroni correction the significance criterion for individual comparisons should be set at 0.0014 to obtain an overall a of 0.05. Unfortunately it is impossible to determine if any of the comparisons were significant according to this criterion, as t-values are not given. In the Calandre et al. study [112], the WISC was given to 64 epileptic children and 60 healthy controis. Verbal IQ (VIQ), PIQ and FSIQ were employed as outcome measures. Patients were on chronic (i.e., at least 6 months) VPA (n = 32) or PB (n = 32). The test was repeated after a 9-12-month interval; 23 PB-treated children and 26 VPA treated children and 40 controls performed the second evaluation. Treatment allocation was not randomized. At baseline, FSIQ, VIQ and PIQ in PB children were lower than in controls. Comparing the first and second tests, a significant increase in IQ scores was detected among controls and VPA, but not among PB children. Controls and VPA increased more than PB. On the basis of these results it was concluded that long-term PB therapy induces a significant impairment in learning ability, whereas long-term VPA therapy does not. Hence, VPA should be preferred to PB whenever possible. There are some conclusion validity problems here, though. The interpretation of the baseline differences as a consequence of the treatment is problematical because it is based on posttest-only data. This study has an impressive drop-out rate, but drop-out artifacts are not considered: no less than one in three controls are lost to the study. In the PB group drop out is evidently not random, judging from the fact that FSIQ in the subjects completing the study is on average 5 points higher than in those entering the study (an increase from 87, with n = 32, to 92, with

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n = 23). In order to produce this increase, the mean FSIQ of the drop outs would have to be far below (around 74) that of the initial group. Also, the controis described as 'age matched' (upon entering the study) are in fact about one year older (m = 9.98, S.D. = 2.1) than VPA (m = 8.91, S.D. = 2.1) and PB (m = 8.90, S.D. = 2.5). In school age children this difference may be relevant. Age of the subjects completing the trial is not given, however. The outcome pattern in this study is of the difficult to interpret type in which 'the able become more able'. In the groups completing the study, for example, controls outperform PB children by 5 FSIQ points at the pretest, and at the posttest the difference has become larger (9 points). That is, they may have been using their aptitude to gain more from the testing experience. There may have been relevant age differences as well (older children gaining more). There are ways to assess the plausibility of such differential growth rates, but this alternative interpretation was not considered. The study by Meador et al. [113] used a randomized triple cross-over design, comparing CBZ, PHT and PB, each treatment lasting 3 months, in 15 patients. Cognitive assessment included five tests and two P3 evoked potential measures of cognitive processing speed. Drug serum levels and seizure frequency were used as covariates. The only significant effect was for Digit Symbol, where performance on PB was worse than on the other two AEDs. The other measures showed comparable performance for the three AEDs. To a large extent this is a 'no difference' finding, and as the authors point out, the small sample size may have limited statistical power, though this is at least partially compensated for by the inherently powerful repeated measures design. A formal power analysis was not reported, though. Forsythe et al. [114] randomly assigned new cases of childhood epilepsy (aged 5-14 years) to either CBZ (n = 23), PHT (n = 20) or VPA (n = 21), and assessed them before medication, at one month, six months and a year after starting treatment, with four cognitive measures covering memory, vigilance, speed of information processing and concentration. Tests of intelligence and reading were also administered, but premedication assessments were not available, making it difficult to evaluate the results of these tests. At the end of the year 14 subjects in each

83

drug group still participated in the study (i.e., overall, 34% were lost); however, due to missing data on some of the tests, the actual n after a year for the four principal outcome measures varied between 10 and 14 for CBZ and 12 and 14 for PHT and VPA. The drug groups were compared by analysis of covariance (ANCOVA) with age and pretreatment scores (to adjust for initial differences) as covariates. After six months as well as a year of treatment, memory scores of the children on VPA were better than for those on CBZ. At one month, speed of information processing was better in the VPA group than in CBZ and PHT, but these differences were no longer apparent at either six months or a year. Tests of concentration and vigilance revealed no differences between the drugs, a finding that carries little weight given the sample sizes. The authors concluded 'CBZ in moderate dosage adversely affected memory, but VPA and PHT did not'. However, this is a claim about absolute effects, whereas the data at best allow conclusions about relative effects (e.g., CBZ was worse compared to both other drugs). To be sure, the authors claim that the epilepsy groups were compared to controls, but data and the results of this comparison were not presented. Though the children are described as seizure free throughout the study period, it should be noted that PHT and CBZ, contrary to VPA, are generally less effective against absence seizures, i.e., seizures that might easily be missed in young children. This kind of masked seizure confound may have biassed the results against CBZ and PHT. This study also suffers from problems associated with multiple statistical testing: 4 major outcome variables × 4 assessment times gives a minimum of 16 comparisons. Data presentation is insufficient to evaluate the effects of a Bonferroni correction for 16 separate comparisons, however. Additional pairwise comparisons must have been carried out at some (or all) time frames, to identify which drugs differed significantly at a particular assessment time. Follow-up analysis procedures are not described, however, and it is impossible to determine if they may have contributed to spuriously significant findings. Aikiae et al. [115] report a one year follow-up in newly diagnosed patients with epilepsy who were randomly allocated to treatment with either oxcarbazepine (OCBZ; n = 14) or PHT (n = 15). Efficacy

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was analogous with both drugs. No significant interaction effect of group and time was found for any of the seven neuropsychological measures, i.e., no evidence was found favouring either AED over the other as regards cognitive side-effects. Power analysis was not reported and low statistical power not considered as a possible explanation for this 'no difference' outcome. Bittencourt et al. [116] studied a group of 51 patients with seizures refractory to therapy with PB, who underwent randomized change to PHT or CBZ. Of the 42 patients who finished the study, 22 were on PHT, 20 on CBZ. Results were analyzed separately for the groups changed to PHT and CBZ, i.e., no direct comparisons between the two groups were made. This effectively turns the study into one with two basically uninterpretable single-group pretestposttest elements in which cognitive effects of the drug change cannot be differentiated from, e.g., retesting effects. Of particular note is the spectacular seizure confound due to the success of the medication switch: upon entry into the study only 9% of the PHT group and none in the CBZ group were seizure free, whereas at the end of the trial these figures had improved to 65% and 61%, respectively. This study allows no valid conclusions regarding cognitive AED effects. Helmstaedter et al. [117] tested previously untreated epilepsy patients prior to medication and after 6-8 weeks of therapy with CBZ (n = 11) and VPA (n = 5). Pretest-posttest changes were compared to those in healthy controls (n = 19). No significant drug treatment effects could be detected on any of the 20 cognitive variables. There are a number of possible confounding factors in this study. The drug groups differed in seizure type: all patients on CBZ, but only one VPA, had complex partial seizures (the others on VPA had primarily generalized seizures). Duration of epilepsy was 8.8 years in the CBZ group and 2.2 years in the VPA group (remarkable figures in untreated patients). This difference is claimed to be nonsignificant without statistical justification; significant or not, this is a large difference by any standards. Also, 45% of the CBZ patients became seizure free, as opposed to 80% of the patients on VPA, though this difference was not significant (but note the n = 5 for VPA). The study was also concerned with the impact of

drugs as a function of whether or not there were pre-existing cerebral lesions, irrespective of the AED used. The problems with this aspect of the study have been discussed by Thompson [127]. Craig and Tallis [118] assessed attention, concentration, psychomotor speed and memory before randomized treatment with VPA (n = 18) or PHT (n = 20), at 6 weeks, 3 months, 6 months and 1 year in subjects with elderly-onset seizures. Of the 47 patients randomized, 38 were available at the 6-week assessment point, 18 on VPA and 20 on PHT, after a year 12 and 16, respectively, remained (giving an overall drop-out rate of about 40%). In most patients complete seizure control was achieved. Performance changes from baseline to the four other assessment points were compared for the two drugs, but no differences were noted between PHT and VPA with regard to impact on cognitive function. Finally, Pulliainen and Jokelainen [119] examined the cognitive effects of randomly assigned PHT or CBZ in newly diagnosed young adult patients, who were tested before and after half a year's treatment. Of the 59 subjects who entered, 43 completed the study, 20 on PHT and 23 on CBZ. Untreated controis were employed as well (n = 21); however, only the drug group data were subjected to a repeated measures ANOVA to evaluate possible differences in changes over time between CBZ and PHT, but no direct comparison to the changes in the controls was made. Thus, no conclusions regarding absolute drug effects can be drawn from this study, despite the control group. Patients on PHT showed less improvement in visual memory compared to those on CBZ; also, they tended to become somewhat slower (but this effect just missed significance). This study has a particularly severe multiple testing problem. In the drug groups alone there are three effects being tested for significance: the two main effects of group and time (reflecting e.g., retesting effects), and the group × time interaction which might reveal differential effects of the two AEDs and is thus of special interest. Separate analyses were done for each of the 24 outcome measures, i.e., 72 statistical tests were performed. Also, follow-up analyses must have been performed to interpret significant findings, but details are not provided. Only two of the interactions were significant (at P < 0.03), i.e., they may represent chance fluctuations.

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Interestingly, the authors observed that the controls appeared to show more pronounced practice effects than the drug groups, which may be one of the first signs of adverse cognitive AED effects. However, the controls were more educated than the drug groups and performed better on some of the baseline tests. Including them in the overall analysis would thus have yielded a difficult to interpret outcome pattern in which 'the able become more able'.

of medication. For example, Berg and Shinnar [128] in their meta-analysis estimate that the risk of relapse in relatively unselected seizure-free patients is on the order of 25% at 1 year and 29% at 2 years. Studies concerned with the cognitive effects of medication withdrawal are listed in Table 8. These studies all employ parallel groups designs in which subjects are tested while still on medication and after withdrawal.

3.9.3. Discussion Only two of the studies discussed above are relevant to absolute cognitive AED effects (Calandre et al. [112] and Helmstaedter et al. [117]), and both face too many interpretation problems to draw any valid conclusions regarding such effects. The other studies discussed above are relevant to differential cognitive AED effects only. Four have failed to find differences between, respectively, CBZ/PHT (Dodrill and T r o u p i n [25]), C B Z / P H T / P B (Meador et al. [113]), O C B Z / P H T (Aikiae-Et al[l15]) and P H T / V P A (Craig and Tallis [118]). The sample sizes involved are not impressive, though. Retrospective power analysis to support a meaningful 'no difference' conclusion would have been advisable in all these studies. Tentatively then, it appears that if differences between these AEDs do in fact exist, such differences are probably not very large. Again, this does not tell us whether the individual AEDs do any cognitive harm. Three studies report differences between drugs: Vining et al. [111] report a favourable profile of VPA compared to PB. Forsythe et al. [114] report results favouring PHT and VPA over CBZ. Pulliainen and Jokelainen [119] report a favourable profile of CBZ compared to PHT. However, these results should be interpreted with caution: they are probably best characterized as scattered significant findings, that were not predicted in advance, that may well represent chance fluctuations rather than genuine differences between drugs, as protection against type I errors was insufficient. Data presentation generally does not allow the reader to examine the results against a more strict significance criterion.

3.10.1. Methodological considerations Withdrawal studies with seizure-free subjects have the advantage that the effect of seizure activity on cognition is not an issue. However, drawing inferences about cognitive effects of an AED from changes that occur after removing it, is not without complications. The approach taken by Aldenkamp et al. [31] and Tonnby et al. [29], is to examine the changes in cognitive performance from AED treatment to complete drug withdrawal, and compare them to those observed in controls given the same testing schedule. Larger gains in the epilepsy group relative to the controls are considered evidence for a reversible impairment, attributable to AED use; the assumption is that such gains are due to the usual retesting a n d / o r maturation effects (also found in controls) plus dissipating adverse treatment effects that allow the former AED users to catch up with or even outperform the controls. The approach in Galassi et al. studies [120-124] is different and will be discussed separately below. Changes in the biochemistry or structure of the central nervous system (e.g., loss of neurons) induced by long-term AED exposure may well be slowly reversible or even irreversible [129], though. Obviously, the above type of analysis is blind to any effects that persist after drug withdrawal. The concern with possible prolonged effects led us to consider the time off AEDs a relevant characteristic of these studies. Another difficulty is that substantial relapse rates may occur in long-range studies. This may introduce a selection factor relevant to cognitive performance, namely that patients with a particularly difficult epilepsy will tend to be lost to the study. Selective loss of underperformers, for example, would result in higher mean scores in the remaining subject sample.

3.10. Discontinued treatment studies Many subjects who have been seizure free for years on AEDs will remain so after discontinuation

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3.10.2. Reported cognitive effects Aldenkamp et al. [31], in the so called 'Holmfrid' study, examined the effects of drug withdrawal in children who had been seizure free for more than a year. Subjects were tested before withdrawal at full medication, and six months later when they had been medication free for three to four months. The majority had been treated with CBZ (n = 56), the others had received VPA (n = 17) or PHT (n = 10). In the combined epilepsy group they found significant improvement attributable to drug withdrawal on only one of their 12 measures (i.e., tapping with the dominant hand). However, as the authors pointed out, this may well represent a chance finding; also, the virtual absence of withdrawal effects for the group as a whole does not eliminate the possibility that different AEDs have specific effects. Due to a possible confound with seizure type, the three drug groups were not compared to each other. However, a comparison of a subgroup of children with the same epilepsy type (Rolandic epilepsy) on PHT (n = 9) vs CBZ (n = 18) revealed no significant difference in the changes observed after withdrawal. Note the small n, however. No comparison to the controls was made for these two drug groups, that is, absolute withdrawal effects were not examined. Tonnby et al. [29], in an extension of the Aldenkamp et al. study [31], ran separate analyses on the CBZ (n = 56), PHT (n = 10) and VPA (n = 17) groups, comparing the changes over time in each drug group to those in matched controls on a subset of 4 from the original 12 cognitive variables, including motor speed, speed of visual information processing and two short-term memory tasks. Subjects were tested on medication around the time of expected peak drug concentrations (i.e., noon), and six months later after withdrawal. Mean peak serum concentrations fell in the middle of the recommended range for CBZ (33.7 /zmol/l), below the range for PHT (32 /xmol/l), and were high for VPA (625 /xmol/l). None of the changes on the four outcome measures differed from those observed in the controls. The CBZ group was also subdivided into three serum concentration groups which were compared to each other and the controls, but this is strictly non-randomized posttest only. The five Galassi et al. [120-124] studies all are

very similar in their design and analysis. The epilepsy groups are tested before, during and after withdrawal (four times altogether). All studies (except [120]) use a control group that is tested only once. The main conclusion drawn in these studies is that all AEDs studied, i.e., CBZ, PB, PHT and VPA, tend to have negative effects on cognitive performance that disappear after complete withdrawal. These studies suffer from a number of common design and analysis problems that merit separate discussion. All controlled studies in this series cite the following evidence for adverse drug effects. Test scores of the epilepsy groups, while still on AEDs, are compared to those of the control group, separate analyses being run for each AED and each test. In general, the epilepsy groups tend to do worse (on some tests), which is interpreted as a consequence of AED use. Note, however, that this is another example of a generally uninterpretable non-randomized posttestonly approach. Thus, epilepsy subjects in these studies are described as comparable to the controls in age and social and educational levels, but it would be methodologically naive to assume that this ensures that AED intake is indeed the sole relevant difference between epilepsy subjects and controls [124] at the beginning of the withdrawal trial. In all studies, this cross-sectional analysis is repeated for each of the three other testing moments. The general outcome is that any differences between AED and controls tend to disappear over time. This is taken as evidence that the differences obtained at first testing were reversible. One difficulty here concerns the statistical conclusion validity: if a difference is significant at one time but not at another, it is not legitimate to infer that a reliable change took place, nor that initial differences became smaller. Also, due to fact that the controls were tested only once it is impossible to determine whether the disappearance of differences between the epilepsy groups and the controls was due to the removal of adverse treatment effects or to differences in the frequency of measurement. Another argument for the reversibility of adverse AED effects is that cognitive functioning appears to improve in the epilepsy groups during withdrawal. Longitudinal analyses are performed in some of these studies [120,121,124], revealing higher test scores over time. Again, uncontrolled retesting effects are

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an obvious alternative interpretation. This conclusion validity issue is recognized in all Galassi et al. studies. To take care of this problem it is argued that parallel forms were employed, except for tests that did not seem sensitive to practice effects. However, parallel forms of the same test may show different mean performance levels, and insensitivity to practice effects is better demonstrated than argued. In these studies, the group comparisons at the four testing moments may either have involved all subjects still in the study at that time, or only those completing the trial; the statistical presentation is insufficient to establish this with certainty (e.g., degrees of freedom are not provided). In the former case there would be a cognitively relevant selective drop-out artifact to reckon with, relapse being a major drop-out reason in these studies. If the pre-

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withdrawal comparison did not include those subjects later lost, this represents another factor further confounding the interpretation of such posttest-only data. Due to these and other concerns (cf. Meador and Loring [3]), little faith can be placed in the conclusions reached in these studies.

3.10.3. Discussion The Holmfrid study [31] found no cognitive effects in a large (n = 83) sample of children for a mixture of AEDs comprising mainly of CBZ, 'contaminated' with some PHT and VPA. In small selected samples of PHT and CBZ users no differential effects of withdrawal of these drugs were found. Tonnby et al. [29] found no evidence for absolute reversible cognitive changes attributable to CBZ,

Table 9 Monotherapy studies in epilepsy relevant to absolute cognitive AED effects (1970-1994) Study

AED

n

Controls (n)

Epilepsy subjects

Interpretation problems

MacLeod et al., 1978 [100]

PB

19

20

Adults with uncontrolled tonic clonic seizures.

Short-term adverse effect of 60100% increase in dosage. Limited sampling of cognitive function (two measures).

Calandre et al., 1990 [112]

PB VPA

23 26

60

School-age children on chronic treatment.

PB, but not VPA, induces cognitive impairment. Outcome pattern of the type in which 'the able become more able'. Obvious non-random drop out in PB group.

R6nberg et al., 1992 [108]

CBZ

14

14

Adults, newly diagnosed.

Fairly short (6 weeks) low-dose treatment. 'No effect' outcome with small sample

Helmstaedter et al., 1993 [117]

CBZ VPA

11 5

19

Previously untreated patients with fairly long-standing epilepsy.

Possible confound of medication with seizure type, duration of epilepsy and seizure control. 'No effect' finding with very small sampies.

Tonnby et al., 1994 [29]

CBZ PHT VPA

56 10 17

83

School-age children who had become seizure free

Withdrawal, insensitive to permanent or slowly reversible effects. 'No effect' finding with small VPA and (also low serum) PHT samples, and limited coverage of cognitive function (4 measures).

Not included are studies that report no direct repeated measures comparison with controls [103,106,114,119], perform an inappropriate analysis [120-124], employ a generally uninterpretable design [107], or do not compare individual AEDs to controls [31].

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P H T and V P A ; particularly for the large C B Z group ( n = 56) this s e e m s a robust finding, but w i t h only four m e a s u r e s the scope o f the study w i t h respect to c o g n i t i v e f u n c t i o n i n g was limited. T h e other withdrawal studies h a v e too m a n y interpretive difficulties to a l l o w reasonably valid conclusions. It should be e m p h a s i z e d that these ' n o - e f f e c t ' findings pertain to effects that are reversible within

the study period, i.e., within half a year or so. The plausibility o f effects that persist after this period, or are irreversible, is difficult to j u d g e , but they represent m o r e than a theoretical concern. For e x a m p l e , F a r w e l l et al. [23], w h o e x a m i n e d the cognitive effects o f prophylactic P B in children w i t h febrile seizures, assessing t h e m prior to treatment, during treatment and after withdrawal, present e v i d e n c e that

Table 10 Monotherapy studies in epilepsy relevant to differential cognitive AED effects (1970-1974) Study

AED

n

Epilepsy subjects

Interpretation problems

Dodrill and Troupin, 1977; 1991 CBZ [27,25] PHT

40 40

Adults with long standing epilepsy.

Scattered significant findings favouring CBZ in original study, but no protection against type I error. 'No difference' conclusion in reanalysis at best applies only to the four variables that were reanalysed, in a selected subject group. Possibly unbalanced drug sequence in reanalysis.

Vining et al., 1987 [111]

PB VPA

21 21

School-age dren.

chil-

Scattered significant findings favouring VPA possibly due to insufficient protection against type I error

Calandre et al., 1990 [112]

PB VPA

23 26

School-age children on chronic treatment.

Outcome pattern of the type in which 'the able become more able', favouring VPA. Obvious non-random drop out in PB group.

Meador et al., 1990 [113]

CBZ PB PHT

15 15 15

Adults with long standing epilepsy.

'No difference' finding with all samples.

Forsythe et al., 1991 [114]

CBZ PHT VPA

14 14 14

Newly diagnosed school-age children.

Scattered significant findings possibly due to insufficient protection against type I error, favouring PHT and VPA over CBZ. Possible bias against CBZ and PHT which are not effective against absence seizures.

Aikiae et al., 1992 [115]

OCBZ PHT

14 15

Newly diagnosed adults.

'No difference' finding with small samples.

Aldenkamp et al., 1993 [31]

CBZ PHT

18 9

School-age children who had become seizure free.

Withdrawal, insensitive to permanent or slowly reversible effects. 'No difference' finding with small samples.

Helmstaedter et al., 1993 [117]

CBZ VPA

11 5

Previously untreated patients with fairly long standing epilepsy.

Possible confound of medication with seizure type, duration of epilepsy and seizure control. 'No difference' finding with very small samples.

Craig and Tallis et al., 1994 [118]

PHT VPA

16-20 12-18

Patients (aged > 60) with newly diagnosed elderly onset seizures.

'No difference' finding with small samples.

23 20

Newly diagnosed young adults.

Scattered significant findings possibly due to insufficient protection against type I error, favouring CBZ.

Pulliainen and Jokelainen, 1994: CBZ [119] PHT

Not included are studies that employ a generally uninterpretable design [116], perform an inappropriate analysis [120-124], or report no comparison between drug groups [29].

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PB depresses cognitive performance in such children, and that this effect may outlast discontinuation of the drug by at least several months.

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Table 11 Number of studies in epilepsy examining differential cognitive effects of specified AEDs (1970-1994) CBZ

PB

PHT

PB

PHT

VPA

PHT

VPA

OCBZ

VPA

4. Summary and conclusions

1

5

2

1

2

1

2

Over 90 investigations have been conducted over the past 25 years to determine what effect AEDs have on cognition. No satisfactory answer to this problem can be given, however, chiefly because there is a paucity of studies that pass fairly basic standards of methodology, design and analysis that apply to the evaluation of any clinical research. This severely limits the precision of statements regarding cognitive AED effects. More particularly, there is little reason to recommend any of the first-line AEDs as the AED of choice from the standpoint of cognitive side-effects. On the basis of the present review we are not in a position to provide a straightforward answer to the most pertinent question, i.e., whether AEDs in therapeutic doses have any cognitive effects at all, good or bad. If we reduce the available database to monotherapy studies in epilepsy that use control group data for comparison, employ an appropriate form of repeated measures analysis, and provide sufficient information, very few studies remain that are directly relevant to this issue. This in itself precludes definitive conclusions. As can be seen from Table 9, absolute effects of CBZ and VPA have been examined in epilepsy patients three times each (in four studies), PB has been examined two times, PHT only once. In addition to the paucity of relevant data, there are miscellaneous validity concerns in all of these studies, one recurring theme being that of inconclusive 'no effect' findings with small samples. Without firm knowledge about absolute effects, relative effects, and particularly their absence, are difficult to interpret. Employing the above criteria (except that concerning controls), ten epilepsy studies that address this issue remain (Table 10). It is instructive to look at the number of times particular AEDs have been compared against each other (Table 11). CBZ has been compared to PHT five times, other comparisons occur only once or twice. Again, this is hardly a basis for definitive statements, particularly because validity concerns oc-

cur here as well. Recurring concerns here are scattered significant findings that tend to disappear if adjustment of the significance level for multiple comparisons is done, and inconclusive 'no difference' findings with small samples. Even if there were no conclusion validity concerns in individual studies, comparison between studies would be complicated by considerable variation in the subjects studied. Five of the studies summarized in Tables 8 and 9 use children as subject, nine use adults; results obtained in one group may not be generalizable to the other. Also, subjects may be newly diagnosed cases, or patients already on chronic treatment. The latter choice of subjects may be a factor working against detecting cognitive side-effects, as the damage (if any) may already have been done before the beginning of the trial. In addition, a wide variety of assessment tools have been used to search for cognitive effects of AEDs, ranging from measurements of reaction time and motor speed to intelligence tests. Some of these may be more sensitive to drug induced changes in cognition than others. Still, the tentative overall picture emerging from the creme de la creme of research on cognitive AED effects is that differences in cognitive profiles may not be very large. An important point here, of course, is the magnitude of the difference one considers worth detecting. Very few studies have attempted to answer this question. In the majority of studies we examined, a large treatment effect was anticipated implicitly, judging from the generally limited sample sizes. The choice of a study design based on a large treatment effect size may not always be appropriate, though. Of course, one could argue that it is only large effects that may be of practical or clinical significance anyways [30] and that effects of lesser magnitude are of no consequence. However, there

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are many examples where even a small benefit of one treatment over another may arguably be of interest [130]. Given the fact that AEDs are typically given as chronic treatment, and the concern about the possible daily life impact of cognitive changes in subjects who receive drugs for years or decades, small effects could well be worth detecting. Unfortunately, there is no generally accepted method for assessing the clinical significance of cognitive changes, so there is no easy way to settle this issue. Presumably the most expedient way of getting at effects worth detecting is through conventional definitions [4] of small, medium and large effect sizes, employing effect sizes such as were encountered in previous relevant research as a reference. An interest in large effects only may not be realistic, as small and moderate effect sizes are prevalent in behavioral research [4]. There are no reasons to expect otherwise in this area of research. After all, the role of AED therapy must be appraised against a background of many factors, recognized and unrecognized, that may impact on cognitive functioning, including the underlying epilepsy, associated brain pathology, and psychosocial problems. If relatively small differences between AEDs are felt to be important clinically, samples required to draw definitive conclusions may become so large (i.e., hundreds of subjects) as to be unachievable in this field. We suggest that future research anticipate medium-sized effects, using this as the value for the treatment effect size factor in sample size calculations.

variability among subjects due to individual differences is eliminated. Careful randomization (4) is a prerequisite for high quality research. However, as drop-out losses in AED studies tend to be considerable, the initial comparability between groups may be difficult to maintain over the course of the trial. No-treatment controls are indispensable in examining absolute effects (5), but will generally mean the introduction of a non-randomly assigned element in the design. Interpretation of designs with non-random treatment allocation is always treacherous (6), and the reader is alerted the problem that some outcome patterns may be more interpretable than others [89]. The magnitude of the treatment effect considered worth detecting (7) is a crucial element in any trial, if only because this is an important factor in sample size calculations; we present arguments for medium effect sizes, but other options are conceivable and the rationale for their choice should be provided. The number of subjects is a major determinant of statistical power (8); studies with low power are inconclusive when they fail to reject the null hypothesis. Multiple outcome measures (9) may give a more complete and detailed description of cognitive AED effects. However, one argument against the use of a large number of outcome variables is that the power of multivariate methods generally declines as the number of dependent variables increases; univariate analyses with adjustment of the significance level face the same problem. Besides adding robustness, a smaller number of variables is apt to facilitate interpretation [49]. Finally (10), to

5. Recommendations

Table 12 Recommendations for cognitive AED research

Although previous studies may not have yielded much definitive knowledge of cognitive AED effects, they at least have provided suggestions for improvements in the methodology of such studies. Table 12 gives some recommendations for further research. The effects of individual agents can only be assessed satisfactorily in monotherapy (1), in subjects with well-controlled seizures (2). The use of a repeated measures design (3) is both appropriate and practical here; such designs are comparatively powerful, i.e. they require relatively few subjects, as

1. 2. 3.

Examine monotherapy only Employ seizure-free subjects Employ a repeated measures design (parallel groups or crossover) 4. Use random treatment allocation when comparing AEDs 5. Employ a no-treatment control group to assess absolute effects 6. Interpret designs with a non-randomly assigned element (e.g., controls) with caution 7. Discuss the rationale for the choice of anticipated treatment effects 8. Use a sample size that results in adequate power (say, 0.80) 9. Economy in the number of outcome measures 10. Follow commonly accepted guidelines for reporting data

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enable the reader to evaluate the statistical conclusion validity of the results, currently accepted criteria and standards for reporting data should be adopted; many papers we reviewed were insufficient in this regard.

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