Description of the condition
Severe myoclonic epilepsy in infants (SMEI), also known as Dravet syndrome (Dravet 2005), is one of the most refractory forms of epilepsy, for whose treatment stiripentol (STP) has been recently licensed for add-on use. It is a rare disease, with an estimated incidence ranging between 1 per 20,000 (Yakoub 1992) to 1 per 40,000 children (Hurst 1990). De novo mutations in the sodium channel SCN1A are a major cause of this syndrome (Fujiwara 2003) and have been found in 40% to 70% of patients with typical SMEI (Nabbout 2003).
According to the International League Against Epilepsy classification (ILAE 1989), SMEI is defined by "febrile and afebrile generalized and unilateral, clonic or tonic–clonic, seizures, that occur in the first year of life in an otherwise normal infant and are later associated with myoclonus, atypical absences, and partial seizures. All seizure types are resistant to antiepileptic drugs (AEDs). Developmental delay becomes apparent within the second year of life and is followed by definite cognitive impairment and personality disorders."
In this nosologically and aetiologically homogeneous syndrome, seizures are refractory to conventional AEDs. Newer drugs, such as stiripentol, have been proposed in order to achieve a better seizure control in SMEI.
In this review we will investigate the efficacy and tolerability of stiripentol and other antiepileptic drug treatments in people with SMEI.
Description of the intervention
Stiripentol is a new AED developed in France and recently approved by the European Medicines Agency (EMEA) for the treatment of Dravet syndrome, as an adjunct treatment with valproate (VPA) and clobazam (CLB), with a promising effect (Chiron 2007).
Some adverse events of STP have been related to a significant increase in the plasma concentration of VPA and CLB after the addition of STP (Perez 1999). They include drowsiness, ataxia, nausea, abdominal pain, and loss of appetite with weight loss. Asymptomatic neutropenia is also occasionally observed (Chiron 2007).
How the intervention might work
Stiripentol is structurally unrelated to any other marketed AED. A GABAergic effect of stiripentol has been demonstrated in vitro (Quilichini 2006), and is probably due to an allosteric modulation of the GABA-A receptor (Fisher 2009). Therefore the efficacy of STP could be secondary to a potentiation of GABAergic inhibitory neurotransmission (Quilichini 2006) and enhancement of the action of benzodiazepines (Fisher 2009). In humans, STP also inhibits the cytochrome P450 enzymes (CYP) in the liver, resulting in an increased plasma concentration of concomitant AEDs metabolized by CYP (Chiron 2005). In Dravet patients, such a pharmacokinetic interaction particularly applies to clobazam (Giraud 2006).
Why it is important to do this review
To date, studies evaluating stiripentol in SMEI have been uncontrolled and have included few participants, leading to potentially biased estimates of treatment effect.
Recently, a systematic review and meta-analysis of individual patient data has been conducted to evaluate the efficacy of available treatments for SMEI (Kassaï 2008). Twenty-three uncontrolled studies and two randomised controlled trials (RCTs) comparing stiripentol with placebo were found. Overall, 64 children aged between 3 and 20 years were included in the two RCTs. The odds ratio of responding to stiripentol relative to placebo was 32 (Confidence Interval (CI): 6.2 to 161) and stiripentol reduced seizure rate by 70% (93% to 47%). However, this review did not consider the tolerability of stiripentol. Moreover to date no study has systematically reviewed the literature on the role of other antiepileptic drugs in the treatment of SMEI.
In this systematic review, we will aim to assess and summarise the existing evidence regarding the efficacy and adverse effects of stiripentol and other antiepileptic drugs (and including ketogenic diet, although it is an antiepileptic treatment rather than a drug) for people with SMEI.
To evaluate the efficacy and tolerability of stiripentol and other antiepileptic drug treatments (including also ketogenic diet) as therapy for patients with severe myoclonic epilepsy in infancy (SMEI).
Criteria for considering studies for this review
Types of studies
We will include studies meeting all of the following criteria:
(1) randomised controlled trials (RCTs) or quasi-randomised controlled trials (e.g. sequence generated by date of birth or clinical record number);
(2) double, single or unblinded trials;
(3) parallel group studies.
We will exclude all other study designs, including cohort studies, case-control studies, outcomes research, case studies, case series and expert opinion.
We will not impose any language restrictions.
Types of participants
We will consider people with a defined diagnosis of severe myoclonic epilepsy in infancy (SMEI) made according to International League Against Epilepsy criteria (ILAE 1989), regardless of age, sex, ethnicity and prior therapy, including children with disabilities.
Types of interventions
- Any trial that compares at least one antiepileptic drug therapy against placebo.
- Any trial that compares at least one antiepileptic drug therapy against no therapy.
- Any trial that compares at least one antiepileptic drug therapy against another therapy or a different dose of the same therapy.
We will also include trials evaluating ketogenic diet.
The therapies may be given singly (monotherapy) or in combination (add-on therapy).
Types of outcome measures
- Fifty percent or greater reduction in seizure frequency: proportion of participants with at least 50% or greater reduction in seizure frequency at the end of the study compared to the pre-randomisation baseline period.
- Seizure freedom: proportion of participants achieving total cessation of seizures at the end of the trial. We will use the most current International League Against Epilepsy (ILAE) proposed definition of seizure freedom: no seizures of any type for either 12 months or 3 times the longest (pre-intervention) seizure-free interval, whichever is longest (Kwan 2010).
For each outcome, an intention-to-treat primary analysis will be made in order to include all patients in the treatment group to which they were allocated, irrespective of the treatment they actually received, hence also including drop-outs. The analysis will use intention-to-treat (ITT) data of all randomised patients recorded during the entire treatment period, including both titration and evaluation phases.
1. Adverse effects:
- Proportion of participants experiencing at least one adverse effect.
- Proportion of participants experiencing each separate adverse effect.
2. Proportion of drop outs/withdrawals due to side effects, lack of efficacy or other reasons. This is used as a measure of global effectiveness.
3. Improvement in quality of life as assessed by validated and reliable rating scales.
Search methods for identification of studies
We will search the following databases:
- the Cochrane Epilepsy Group Specialised Register;
- the Cochrane Central Register of Controlled Trials (CENTRAL, The Cochrane Library);
- Online trials registries.
We present the proposed search strategy for MEDLINE in Appendix 1. This strategy will be modified for use with the other databases.
We will not impose any language restrictions.
Searching other resources
We will contact experts in the field for information about any unpublished or ongoing studies. We will review the reference lists of articles retrieved by the electronic searches to check for other relevant reports. In order to find other relevant trials we will review conference proceedings not included in the Cochrane Epilepsy Group Specialised Register after checking with the Trials Search Coordinator to avoid duplication of effort.
Data collection and analysis
Selection of studies
Two review authors (FB and MS) will independently screen all the titles and abstracts of publications identified by the searches to assess their eligibility. We will exclude publications that do not meet the criteria at this stage. Following screening, we will assess the full-text of potentially-eligible citations for inclusion. The review authors will reach consensus on the selection of trials and the final list of studies. We will discuss any disagreements and resolve them where possible. If we cannot reach consensus, we will consult a third member of the team (ADF).
Data extraction and management
Two review authors (FB and MS) will independently extract the following characteristics of each included trial from the published reports where possible. We will use data extraction forms and resolve any disagreements by mutual agreement. We will record the rawest form of the data, when possible. In case of missing or incomplete data, we will contact the principal investigators of included trials and request additional information.
(c) Epileptic seizure types.
(d) Etiology of epilepsy.
(e) Duration of epilepsy.
(f) Family history of epilepsy.
(g) Number of seizures or seizure frequency prior to randomization.
(h) Presence of status epilepticus.
(i) Number and types of AEDs previously taken.
(j) Concomitant AEDs.
(k) Presence of neurological deficit/signs.
(l) Neuropsychological status.
(m) Electroencephalography (EEG) findings.
(n) Neuroradiologic findings (computed tomography (CT)/magnetic resonance imaging (MRI)).
(a) Criteria used to diagnose epilepsy.
(b) Inclusion and exclusion criteria.
(c) Method of randomisation.
(d) Method of allocation concealment.
(e) Method of blinding.
(f) Stratification factors.
(g) Number of participants allocated to each group.
(h) Length of baseline period, titration period, treatment period.
Intervention and control
(a) Intervention given to controls.
(b) Dosage of stiripentol.
(a) Duration of follow up.
(b) Reasons for incomplete outcome data.
(c) Drop-out or loss to follow-up rates.
(d) Methods of analysis (e.g. intention-to-treat, modified intention-to-treat, per protocol, worst-case or best-case scenario analysis).
Assessment of risk of bias in included studies
Two review authors (FB and MS) will assess the risk of bias of each trial according to the approaches described in The Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will assess the risk of bias as: low, high or unclear risk of bias.We will evaluate the following characteristics:
(a) Random sequence generation (selection bias).
(b) Allocation concealment (selection bias).
(c) Blinding of participants and personnel (performance bias).
(d) Blinding of outcome assessment (detection bias).
(e) Incomplete outcome data addressed.
(f) Selective reporting (reporting bias).
(g) Other bias, including outcome reporting bias (Kirkham 2010) assessed with an ORBIT table in the review.
Measures of treatment effect
We will use statistical methods in accordance with The Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) to measure treatment effect.
We will use mean differences (MD) with 95% confidence intervals (CI) for continuous data where we find data provided as means and standard deviations. Alternatively, if possible, we will calculate these data by using conventional statistical formulae.
We will analyse dichotomous data by calculating risk ratios (RR) for each trial with the uncertainty in each trial being expressed using 95% CI. For individual adverse effects we will use 99% CIs to make allowance for multiple testing. Both for dichotomous and continuous data, we will calculate a weighted treatment effect across trials.
Unit of analysis issues
The duration of trials may vary considerably. If the range seems too great to combine all trials into one meta-analysis, we will undertake a meta-regression to explore the effect of trial duration on treatment effect. If adverse effects occur more than once, we will adopt statistical methods for count data. For trials comparing more than two intervention groups, we will assess the relevant comparisons separately.
Dealing with missing data
For individual missing data such as drop-out or loss to follow up, we will use an intention-to-treat analysis whenever possible. We will contact the chief investigators to request missing data if possible. We will address the potential implications of missing data (e.g. loss to follow up and no outcome obtained, receiving the wrong treatment, lack of compliance, or ineligibility) in the "Discussion" section of the review.
Assessment of heterogeneity
Visual inspection of the forest plots will be used to investigate the possibility of statistical heterogeneity. We will evaluate homogeneity among trial results using a standard Chi
Assessment of statistical heterogeneity will be supplemented using the I
The interpretation of I
- 0% to 40%: may not be important;
- 30% to 60%: represents moderate heterogeneity;
- 50% to 90%: represents substantial heterogeneity;
- 75% to 100%: represents considerable heterogeneity.
We will combine trial outcomes to obtain a summary estimate of effect (and the corresponding confidence interval (CI)) using a fixed-effect model, unless there is a significant heterogeneity (that is, I
We will assess possible sources of heterogeneity (for example clinical heterogeneity, methodological heterogeneity or statistical heterogeneity) by using sensitivity analysis as described below.
Assessment of reporting biases
We may use a funnel plot to detect reporting biases if sufficient numbers of studies are available. Possible sources of funnel plot asymmetry can exist as publication bias, language bias, citation bias, poor methodological quality, true heterogeneity, etc., and we will analyse them according to the trials.
Provided we think it clinically appropriate, and no important clinical and methodological heterogeneity is found, we plan to synthesise the trial results in a meta-analysis. We will use the Mantel-Haenszel method for analysing dichotomous data and inverse variance for continuous data.
We will perform separate analyses on each intervention (AED or ketogenic diet) given singly (monotherapy) or in combination (add-on therapy). Different control groups will be also analysed separately.
We will synthesise data on all seizures and also according to seizure type. We do not plan further subgroup analyses for the current review but it should be considered in future revisions. We will use Review Manager to combine trial data.
In the case of residual unexplained heterogeneity, we will evaluate the robustness of the results of the meta-analysis by comparing fixed-effect and random-effects model estimates, removing trials with low methodological quality or excluding trials with large effect size. We will also use the worst-case and best-case scenarios for the efficacy outcomes whenever possible. If the conclusions we observe remain unchanged, then we will consider the evidence to be robust.
Participants randomised but excluded from analysis (e.g. for not completing follow-up or with inadequate seizure data) were assumed non-responders in the active treatment group and responders in the placebo/no treatment group.
Participants randomised but excluded from analysis (e.g. for not completing follow-up or with inadequate seizure data) were assumed responders in the active treatment group and non-responders in the placebo/no treatment group.
Appendix 1. MEDLINE search strategy
This search strategy is based on the Cochrane Highly Sensitive Search Strategy for identifying randomised trials (Lefebvre 2011).
1. randomized controlled trial.pt.
2. controlled clinical trial.pt.
5. clinical trials as topic.sh.
8. 1 or 2 or 3 or 4 or 5 or 6 or 7
9. exp animals/ not humans.sh.
10. 8 not 9
11. severe myoclonic epilepsy.tw.
13. Dravet* syndrome.tw.
14. 11 or 12 or 13
15. 10 and 14
Contributions of authors
Francesco Brigo and Monica Storti wrote the manuscript.
Declarations of interest