Types of studies

• Randomised controlled trials (RCTs) using either:

  • an adequate method of allocation concealment (e.g. sealed opaque envelopes); or

  • a 'quasi' method of randomisation (e.g. allocation by date of birth).

• Studies may be double‐blind, single‐blind or unblinded.

• Studies must include a comparison of sodium valproate monotherapy with phenytoin monotherapy in individuals with epilepsy.

Types of participants

• We included children or adults with focal onset seizures (simple focal, complex focal or secondarily generalised tonic‐clonic seizures) or generalised onset tonic‐clonic seizures, with or without other generalised seizure types (in other words, those who had only generalised tonic‐clonic seizures and those who had both generalised onset tonic‐clonic seizures and generalised seizures of other types (e.g. absence, myoclonic etc.)).

• We excluded individuals with other generalised seizure types alone without generalised tonic‐clonic seizures (e.g. those who had only absence seizures without any generalised clonic tonic‐seizures) due to differences in first‐line treatment guidelines for other generalised seizure types (NICE 2012).

• We included individuals with a new diagnosis of epilepsy, or who have had a relapse following withdrawal of antiepileptic monotherapy.

Types of interventions

Sodium valproate or phenytoin as monotherapy. For brevity, sodium valproate is referred to a 'valproate' herein.

Types of outcome measures

Below is a list of outcomes investigated in this review. Reporting of these outcomes in the original trial report was not an eligibility requirement for inclusion in this review.

Electronic searches

We searched the following databases. We did not impose any language restrictions.

• The Cochrane Epilepsy Group's Specialised Register (19 February 2018) using the search strategy outlined in Appendix 1.

• The Cochrane Central Register of Controlled Trials (CENTRAL; 2018, Issue 2) in the Cochrane Library (searched 19 February 2018) using the search strategy outlined in Appendix 2.

• MEDLINE (Ovid, 1946 to 19 February 2018) using the search strategy outlined in Appendix 3.

• SCOPUS (last search 19 February 2013) using the search strategy outlined in Appendix 4. We searched SCOPUS as an alternative to Embase, but this is no longer necessary, because randomised and quasi‐RCTs in Embase are now included in CENTRAL, so we will not be updating the SCOPUS search.

• ClinicalTrials.gov (19 February 2018) using the search terms 'phenytoin AND valproate | Epilepsy'.

• WHO International Clinical Trials Registry Platform ICTRP (19 February 2018) using the search terms 'valproate and phenytoin and epilepsy'.

Searching other resources

In addition, we handsearched relevant journals, reviewed the reference lists of retrieved studies to search for additional reports of relevant studies, contacted Sanofi (manufacturers of valproate in Europe), Abbott (manufacturers of valproate in the USA), Parke‐Davis (manufacturers of phenytoin), and experts in the field for information about any ongoing studies.

Selection of studies

Two review authors (SJN and AGM) independently assessed trials for inclusion, resolving any disagreements by mutual discussion.

Data extraction and management

We requested the following individual participant data (IPD) for all trials meeting our inclusion criteria.

• Trial methods

• • method of generation of random list

  • method of concealment of randomisation

  • stratification factors

  • blinding methods

• Participant covariates

• • gender

  • age

  • seizure types

  • time between first seizure and randomisation

  • number of seizures prior to randomisation (with dates)

  • presence of neurological signs

  • electroencephalographic (EEG) results

  • computerised tomography/magnetic resonance imaging (CT/MRI) results

• Follow‐up data

• • treatment allocation

  • date of randomisation

  • dates of follow‐up

  • dates of seizures post‐randomisation or seizure frequency data between follow‐up visits

  • dates of treatment withdrawal or treatment failure and reasons for treatment withdrawal or treatment failure

  • dose

  • dates of dose changes

For each trial for which IPD were not obtained, we carried out an assessment to see whether any relevant aggregate level data had been reported. If possible, SJN extracted any aggregate level data from publications and extracted data were verified by JW.

For three trials, seizure data were provided in terms of the number of seizures recorded between clinic visits rather than specific dates of seizures (Craig 1994; Ramsay 1992; Turnbull 1985). To enable time‐to‐event outcomes to be calculated, we applied linear interpolation to approximate the dates on which seizures occurred. For example, if four seizures were recorded between two visits which occurred on 1 March and 1 May (an interval of 61 days), then date of first seizure would be approximately 13 March. This allowed an estimate of the time to achieve six‐month and 12‐month remission and the time to first seizure to be computed.

We calculated time to achieve six‐month and 12‐month remission from the date of randomisation to the date (or estimated date) the individual had first been free of seizures for six or 12 months, respectively. If the person had one or more seizure(s) in the titration period, a six‐month or 12‐month seizure‐free period could also occur between the estimated date of the last seizure in the titration period and the estimated date of the first seizure in the maintenance period.

We calculated time to first seizure from the date of randomisation to the date that their first seizure was estimated to have occurred. If seizure data were missing for a particular visit, these outcomes were censored at the previous visit. These outcomes were also censored if the individual died or if follow‐up ceased prior to the occurrence of the event of interest. These methods had been used in the remaining two trials for which outcome data were provided directly (De Silva 1996; Heller 1995).

Treatment failure data were not available for one trial (Craig 1994). For two trials, we extracted dates and reason for treatment failure from trial case report forms for the original review (De Silva 1996; Heller 1995). Two review authors (SJN and AGM) independently extracted data from all case report forms, resolving disagreements by discussion and reconsidering the case report forms. For the remaining trials (Ramsay 1992; Turnbull 1985), data on length of time spent in trial and reason for withdrawal from treatment or treatment failure were provided directly.

Time to treatment failure was calculated as date of randomisation to date of treatment failure. For the analysis of time‐to‐event, we defined an 'event' as treatment failure because of reasons related to the treatment (i.e. lack of efficacy, adverse events, or both lack of efficacy and adverse events), non‐compliance with the treatment regimen, withdrawal of consent from the trial, etc.). We censored the outcome if treatment failure or withdrawal of treatment was for reasons not related to the trial treatment: i.e. loss to follow‐up, death (not treatment or epilepsy‐related), withdrawal of treatment due to remission, etc. We also censored individuals who were still on allocated treatment at the date of the end of follow‐up. We considered documented reasons for treatment failure or treatment withdrawal on a case‐by‐case basis in relation to treatment; two authors (SJN and AGM) independently classified reasons for treatment failure as 'events' or 'censored' and resolved any disagreements by discussion.

For the analysis of 'time to treatment failure due to adverse events,' only treatment failures which were documented to be due to adverse events (either as a sole reason or due to both a lack of efficacy and adverse events) were classed as an 'event' within time‐to‐event analyses and all other reasons for treatment failure were censored. Similarly, for the analysis of 'time to treatment failure due to lack of efficacy' only treatment failures which were documented to be due to lack of efficacy (i.e. continued seizures, either as a sole reason or due to both a lack of efficacy and adverse events) were classed as an 'event' within time‐to‐event analyses and all other reasons for treatment failure were censored.

Two trials presented times at which the allocated drug was withdrawn and the reason for treatment failure in the trial publication for each individual (Forsythe 1991; Shakir 1981). Hence, these two trials could be incorporated into the analysis of 'time to treatment failure'; one of the trials also presented information by seizure type (focal onset or generalised onset seizures) and therefore could also be included in the stratified analysis for 'time to treatment failure' (Shakir 1981).

Shakir 1981 presents 'time on trial drug' in months for each participant; therefore to calculate 'time to treatment failure', we assumed that if 'time spent on trial drug' was five months, the individual spent five full months (152 full days) on the trial drug before treatment failure. Forsythe 1991 presents 'withdrawal and time of occurrence by month' for each participant; therefore to calculate 'time to treatment failure', we assumed that if treatment failure occurred during the fifth month, that the treatment failure occurred halfway between the fifth and sixth month (i.e. participants spent 167 full days on treatment before treatment failure).

Assessment of risk of bias in included studies

Two review authors (SJN and JW) independently assessed the risk of bias for each trial using the Cochrane 'Risk of bias' tool, as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We rated each of the following six domains as low, unclear or high risk of bias: method of generating random sequence, allocation concealment, blinding methods, incomplete outcome data, selective outcome reporting and other sources of bias. Any discrepancies in risk of bias judgements of the two review authors were resolved by discussion. In the event of the presence of high risk of bias in included trials (due to inadequate allocation concealment or lack of blinding), we planned sensitivity analyses excluding these trials.

Measures of treatment effect

We measured all outcomes in this review as time‐to‐event outcomes with the hazard ratio (HR) and 95% confidence interval (CI) used as the measure of treatment effect. We calculated outcomes from IPD provided, where possible, or extracted from published trials if possible.

Unit of analysis issues

We did not have any unit of analysis issues. The unit of allocation and analysis was the individual for all included trials; and no trials included in meta‐analyses were of a repeated measures (longitudinal) nature or of a cross‐over design.

Dealing with missing data

For each trial that supplied IPD, we reproduced results from trial results where possible and performed the following consistency checks.

• We cross‐checked trial details against any published report of the trial and contacted original trial authors if we found missing data, errors or inconsistencies. If trial authors could not resolve inconsistencies between the IPD and the published data, depending on the extent of the inconsistencies, we planned to perform sensitivity analysis or excluded the data from the meta‐analysis.

• We reviewed the chronological randomisation sequence and checked the balance of prognostic factors, taking account of factors stratified for in the randomisation procedure.

Assessment of heterogeneity

We assessed heterogeneity statistically using the Q test (P < 0.10 for significance) and the I² statistic (greater than 50% indicating considerable heterogeneity; Higgins 2003), and visually by inspecting forest plots.

Assessment of reporting biases

Two review authors (SJN and JW) undertook all full quality and risk of bias assessments. In theory, a review using IPD should overcome issues of reporting biases, as unpublished data can be provided and unpublished outcomes calculated. Any selective reporting bias detected could be assessed with the ORBIT classification system (Kirkham 2010).

Data synthesis

We carried out our analysis on an intention‐to‐treat basis (that is, we analysed participants in the group to which they were randomised, irrespective of which treatment they actually received). Therefore, for the time‐to‐event outcomes, 'time to six‐month remission', 'time to 12‐month remission', 'time to 24 month remission' and 'time to first seizure post‐randomisation', we did not censor participants if treatment was withdrawn or if treatment failure occurred but follow‐up within the trial continued (e.g. if a participant continued to be followed up on a different treatment).

For all outcomes, we investigated the relationship between the time‐to‐event and treatment effect of the antiepileptic drugs. We used Cox proportional hazards regression models to obtain trial‐specific estimates of log (HR) or treatment effect and associated standard errors in Stata Statistical Software, version 14 (Stata 2015). The model assumes that the ratio of hazards (risks) between the two treatment groups is constant over time (i.e. hazards are proportional). We tested this proportional hazards assumption of the Cox regression model for each outcome of each trial by testing the statistical significance of a time varying covariate in the model. We evaluated overall pooled estimates of HRs (with 95% CIs) using the generic inverse variance method. We expressed results as a HR and a 95% CI.

By convention, a HR greater than 1 indicates that an event is more likely to occur earlier on valproate than on phenytoin. Hence, for time to treatment failure or time to first seizure, a HR less than 1 indicates a clinical advantage for valproate (e.g. HR = 0.8 would suggest a 20% reduction in hazard of treatment failure from valproate compared to phenytoin), and for time to achieve six‐month and 12‐month remission, a HR less than 1 indicates a clinical advantage for phenytoin.

Subgroup analysis and investigation of heterogeneity

Due to the strong clinical belief that valproate is more effective in generalised onset seizures, while phenytoin is more effective in focal onset seizures, we have stratified all analyses by seizure type (focal onset versus generalised onset), according to the classification of main seizure type at baseline. We classified focal seizures (simple or complex) and focal secondarily generalised seizures as 'focal epilepsy'. We classified primarily generalised seizures as 'generalised epilepsy'. We conducted a Chi² test of interaction between treatment and epilepsy type.

If we found significant statistical heterogeneity to be present, we performed meta‐analysis with a random‐effects model in addition to a fixed‐effect model, presenting the result of both models and performing sensitivity analyses to investigate differences in study characteristics.

Sensitivity analysis

One trial recruited only individuals with generalised onset tonic‐clonic seizures, some of whom were experiencing other generalised seizure types, such as absence or myoclonus (Ramsay 1992), and all generalised seizure types were recorded during follow‐up for this trial. The remaining four trials recruited individuals with focal onset seizures (simple/complex focal or secondarily generalised tonic‐clonic) and individuals with generalised onset tonic‐clonic seizures. For the individuals with generalised onset tonic‐clonic seizures recruited into these four trials, other generalised seizure types were not recorded during follow‐up. As a result, the majority of the data from the five trials does not address the treatment of generalised seizure types, such as absence or myoclonus, but applies only to generalised onset tonic‐clonic seizures. In our primary analysis, we use only the data for generalised onset tonic‐clonic seizures during follow‐up as this is the most consistent approach; we also report a sensitivity analysis which includes data on all generalised seizure types from Ramsay 1992 for the outcomes 'time to first seizure' and 'time to six‐month remission' (Ramsay 1992 was less than one year duration so does not contribute to 'time to‐12 month remission').

Misclassification of seizure type is a recognised problem in epilepsy, whereby some people with generalised seizures have been mistakenly classed as having focal onset seizures and vice versa. There is clinical evidence that individuals with generalised onset seizures are unlikely to have an 'age of onset' greater than 25 to 30 years (Malafosse 1994). Such misclassification impacted upon the results of three reviews in our series of pair‐wise reviews for monotherapy in epilepsy comparing carbamazepine to phenobarbitone, phenytoin and sodium valproate in which around 30% to 50% of participants analysed may have had their seizure type misclassified as generalised onset (Marson 2000; Nolan 2016c; Nevitt 2017b). Given the potential biases introduced into those reviews, we examined the distribution of age at onset for individuals with generalised seizures in the trials included in this review, to assess the potential impact of misclassification of seizure type on the outcomes:

• 84 out of 86 individuals classified as having generalised onset seizures (98%) in Craig 1994;

• 37 out of 71 individuals (52%) in Heller 1995;

• 30 out of 136 (22%) in Ramsay 1992;

• 2 out of 14 (14%) in Shakir 1981; and

• 35 out of 77 (45%) in Turnbull 1985.

Therefore, a total of up to 188 out of 384 individuals (49%) classified as having generalised onset seizures may have had their seizure type misclassified (De Silva 1996 was a paediatric trial so no individuals over the age of 30 were recruited). Such a misclassification could bias our results against finding an interaction between treatment and seizure types (focal onset versus generalised onset). We undertook the following two analyses to investigate misclassification.

• We reclassified all individuals with generalised seizures and age at onset greater than 30 into an 'uncertain seizure type' group.

• We reclassified individuals with generalised seizures and age at onset greater than 30 as having focal onset seizures.