Description of the condition
Since 1950 when the first antipsychotic medication was discovered, the symptoms of schizophrenia and other related psychotic disorders, especially hallucinations and delusions, have been treated effectively with neuroleptic medications; these, however can have distressing side-effects such as tardive dyskinesia.
Tardive dyskinesia is a late onset, movement disorder often resulting from long-term use of neuroleptic (antipsychotic) medications. It manifests as repetitive, involuntary movements affecting the face, jaw, tongue, extremities and the trunk. Abnormal movements in tardive dyskinesia may involve tongue darting, repetitive grimacing, chewing movements of the mouth, sucking movements or puckering of the lips and purposeless, irregular, jerking movements of the limbs. These symptoms are highly stigmatising and associated with poor quality of life in affected individuals (Browne 1996).
Risk factors for tardive dyskinesia in patients with schizophrenia include female gender (Yassa 1992), older age (Niehaus 2008; Smith 1980), cognitive impairment or neurological deficits (Waddington 1987), diagnosis of a mood disorder especially depression (Casey 1995; Sachdev 1989; Kane 1986), worsening of psychopathology (Tenback 2007) and diabetes mellitus (Casey 1995; Woerner 1993). Tardive dyskinesia is also higher among those taking first generation (conventional) antipsychotic drugs compared with those on second generation (atypical) antipsychotic medications (Corell 2008; Nasrallah 2006). However, neuroleptic medications are not the sole cause of tardive dyskinesia, as similar abnormal motor movements has been reported among patients with schizophrenia who were never exposed to neuroleptic medications (Fenton 2000; Owens 1982).
The exact pathogenesis of tardive dyskinesia is unknown and several theories about its aetiology has been proposed. Foremost is the dopamine receptor supersensitivity hypothesis which posits that long-term receptor antagonism by antipsychotic drugs results in dopamine receptor supersensitivity and the movement disorder in tardive dyskinesia (Sachdev 1989). The neurotoxicity hypothesis states that tardive dyskinesia results from the neurotoxic effects of free radicals that are released during dopamine metabolism. It is believed that these free radicals cause cellular degeneration of striatal GABA-ergic neurons, leading to the loss of their inhibitory activities and the hyperkinetic state of tardive dyskinesia (Sachdev 1989). The use of antioxidants such as vitamin B6 (pyridoxine) as possible treatment for tardive dyskinesia symptoms is based on the neurotoxicity hypothesis (Lerner 2007).
Description of the intervention
Pyridoxal 5 phosphate is the metabolically active form of vitamin B6 (pyridoxine). Vitamin B6 is a naturally occurring vitamin that can be obtained from both animal and plant sources. Following ingestion, pyridoxine is absorbed from the upper small intestine, where it is transported to the liver and oxidised to form pyridoxal. It is then phosphorylated by pyridoxal kinase to form pyridoxal 5 phosphate. Unlike pyridoxine, which causes peripheral neuropathy when high doses are given, pyridoxal 5 phosphate is not associated with any known adverse effects even at doses as high as 1200 mg/day (Miodownik 2008; Schaumburg 1983).
How the intervention might work
Pyridoxal 5 phosphate is a coenzyme in the decarboxylation of DOPA leading to the production of neurotransmitters such as serotonin, dopamine, gamma amino butyric acid (GABA). Although its actual mechanism of action is not clear, it is believed that the role of pyridoxal 5 phosphate in the synthesis of these neurotransmitters accounts for its ability to reduce the symptoms of tardive dyskinesia (Lerner 2001). Thus, by promoting neurotransmitter synthesis, pyridoxine may reduce the symptoms of tardive dyskinesia (Lerner 2001).
Why it is important to do this review
Tardive dyskinesia is very disabling and disfiguring and its occurrence is associated with poor treatment adherence (Barnes 1993) and low quality of life (Browne 1996). The reported prevalence of tardive dyskinesia ranged from 3% to 70% with a median of 24% among patients on long-term use of neuroleptic medications (Yassa 1992).The annual incidence is 5.2% in those with a first episode schizophrenia placed on neuroleptic medications, the rate increasing to about 20% at five years (Chakos 1996). Several drugs have been used in an attempt to treat tardive dyskinesia, but little evidence exists to support their efficacy. Such interventions include melatonin (Nelson 2003), cholinergic agonists (Caroff 2001), vitamin E (Adler 1998), calcium channel blockers (Fay-McCarthy 1997) and clozapine (Bassitt 1998). While the evidence for the effectiveness for some of these interventions has been evaluated (McGrath 2001; Soares-Weiser 2004; Tammenmaa 2002), no evaluation has taken place for pyridoxal 5 phosphate. Thus, it is uncertain if pyridoxal 5 phosphate is effective in the treatment of neuroleptic-induced tardive dyskinesia. This review may provide evidence for its efficacy in the treatment of tardive dyskinesia among patients with schizophrenia and other psychotic disorders.
To determine the effects of pyridoxal 5 phosphate (pyridoxine, pyridoxal phosphate, tardoxal) for treating neuroleptic-induced tardive dyskinesia in individuals of any age group with schizophrenia and other psychotic disorders.
Criteria for considering studies for this review
Types of studies
All relevant randomised controlled trials. If a trial is described as 'double blind' but implies randomisation, we will include such trials in a sensitivity analysis (see Sensitivity analysis). If their inclusion does not result in a substantive difference, they will remain in the analyses. If their inclusion does result in important clinically significant, but not necessarily statistically significant differences, we will not add the data from these lower quality studies to the results of the better trials, but will present such data within a subcategory. We will exclude quasi-randomised studies, such as those allocating by alternate days of the week. Where people are given additional treatments to pyridoxal 5 phosphate, we will only include the data if the adjunct treatment is evenly distributed between groups and it is only pyridoxal 5 phosphate that is randomised.
Types of participants
People with schizophrenia or other chronic mental illness, diagnosed by any criteria, irrespective of gender, age or nationality, who:
- require the use of antipsychotics for more than three months;
- develope tardive dyskinesia (diagnosed by any criteria at baseline and at least one other occasion) during antipsychotic treatment; and
- for whom the dose of antipsychotic medication has been stable for one month or more (the same applies for those free of antipsychotics).
We will only include trials where the majority of participants have a diagnosis of schizophrenia.
Types of interventions
- Pyridoxal 5 phosphate (pyridoxal phosphate, pyridoxine, vitamin B6): any dose or means of administration.
- Placebo or no intervention.
Types of outcome measures
We will group the outcomes by duration of treatment into short term (less than six weeks), medium term (between six weeks and six months) and long term (over six months).
1. Global state: Clinical efficacy will be defined as an improvement in the symptoms of tardive dyskinesia of more than 50%, on any peer-reviewed scale, after at least six weeks of intervention
1. Global Outcomes
1.1 Death due to suicide or other causes
1.2 Average endpoint dose of pyridoxal 5 phosphate or vitamin B6
1.3 Any adverse effects (other than deterioration of tardive dyskinesia symptoms or change in mental state)
1.4 Average time to discontinuation of pyridoxal 5 phosphate and reasons for discontinuation
2. Tardive dyskinesia
2.1 Deterioration in tardive dyskinesia symptoms
2.2 Average endpoint tardive dyskinesia score
3. General mental state changes
3.1 Any deterioration in psychiatric symptoms (such as delusions and hallucinations)
3.2 Average endpoint psychiatric symptoms score
4. Summary of findings table
We will use the GRADE approach to interpret findings (Schünemann 2008) and will use GRADE profiler (GRADEPRO) to import data from RevMan 5 (Review Manager) to create 'Summary of findings' tables. These tables provide outcome-specific information concerning the overall quality of evidence from each included study in the comparison, the magnitude of effect of the interventions examined, and the sum of available data on all outcomes we rate as important to patient-care and decision-making. We aim to select all of our listed outcomes for inclusion in the 'Summary of findings' table.
Search methods for identification of studies
No language restriction will be applied within the limitations of the search tools.
1. Cochrane Schizophrenia Group Trials Register
The Trials Search Co-ordinator will search the Cochrane Schizophrenia Group’s Trials Register using the phrase:
[*Pyridoxal* OR *Pyridoxine* OR *P5P* OR *PLP* OR *tardoxal* OR *Vitamin B6* O *Vitamin B 6* R in title, abstract or index terms of REFERENCE, or interventions of STUDY]
The Cochrane Schizophrenia Group’s Trials Register is compiled by systematic searches of major databases, handsearches of journals and conference proceedings (see Group Module). Incoming trials are assigned to relevant existing or new review titles.
Searching other resources
1. Reference searching
We will inspect references of all identified studies for more studies.
2. Personal communication
We will contact the first author of each included study for more information regarding unpublished trials.
3. Pharmaceutical companies
We will contact Medicure Pharmaceutical company for information on unpublished or ongoing studies.
Data collection and analysis
Selection of studies
Review authors AOA and OA will independently inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently re-inspected by TMO to ensure reliability. Where disputes arise, the full report will be acquired for more detailed scrutiny. Full reports of the abstracts meeting the review criteria will be obtained and inspected by AOA and OA. Again, a random 20% of reports will be re-inspected by TMO in order to ensure reliable selection. Where it is not possible to resolve disagreement by discussion, we will attempt to contact the authors of the study for clarification.
Data extraction and management
Review authors AOA and OA will extract data from all included studies. In addition, to ensure reliability, TMO will independently extract data from a random sample of these studies, comprising 10% of the total. Again, any disagreement will be discussed, decisions documented and, if necessary, we will contact the authors of studies for clarification. With remaining problems, TMO will help clarify issues and these final decisions will be documented. Data presented only in graphs and figures will be extracted whenever possible, but will only be included if two review authors independently have the same result. We will attempt to contact authors through an open-ended request in order to obtain missing information or for clarification whenever necessary. If studies are multicentre, where possible, we will extract data relevant to each component centre separately.
We will extract data onto standard, simple forms.
2.2 Scale-derived data
We will include continuous data from rating scales only if:
a) the psychometric properties of the measuring instrument have been described in a peer-reviewed journal (Marshall 2000); and
b) the measuring instrument has not been written or modified by one of the trialists for that particular trial.
Ideally the measuring instrument should either be i. a self-report or ii. completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly, in 'Description of studies' we will note if this is the case or not.
2.3 Endpoint versus change data
There are advantages of both endpoint and change data. Change data can remove a component of between-person variability from the analysis. On the other hand, calculation of change needs two assessments (baseline and endpoint) which can be difficult in unstable and difficult to measure conditions such as schizophrenia. We have decided primarily to use endpoint data, and only use change data if the former are not available. Endpoint and change data will be combined in the analysis as we will use mean differences (MD) rather than standardised mean differences (SMD) throughout (Higgins 2011 ).
2.4 Skewed data
Continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non-parametric data, we aimed to apply the following standards to all data before inclusion:
a) standard deviations (SDs) and means are reported in the paper or obtainable from the authors;
b) when a scale starts from the finite number zero, the SD, when multiplied by two, is less than the mean (as otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution, (Altman 1996);
c) if a scale started from a positive value (such as the Positive and Negative Syndrome Scale (PANSS), (Kay 1986)), which can have values from 30 to 210), the calculation described above will be modified to take the scale starting point into account. In these cases skew is present if 2 SD > (S-S min), where S is the mean score and 'S min' is the minimum score.
Endpoint scores on scales often have a finite start and end point and these rules can be applied. Skewed data pose less of a problem when looking at means if the sample size is large (> 200) and we will enter these into the syntheses. We will present skewed endpoint data from studies of less than 200 participants as other data within the data and analyses section rather than enter such data into statistical analyses.
When continuous data are presented on a scale that includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. We will present and enter all useable change data into analyses.
2.5 Common measure
To facilitate comparison between trials, we intend to convert variables that can be reported in different metrics, such as days in hospital (mean days per year, per week or per month) to a common metric (e.g. mean days per month).
2.6 Conversion of continuous to binary
Where possible, efforts will be made to convert outcome measures to dichotomous data. This can be done by identifying cut-off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that if there is a 50% reduction in a scale-derived score such as the Brief Psychiatric Rating Scale (BPRS, Overall 1962) or the PANSS(Kay 1986), this could be considered as a clinically significant response (Leucht 2005; Leucht 2005a). If data based on these thresholds are not available, we will use the primary cut-off presented by the original authors.
2.7 Direction of graphs
Where possible, we will enter data in such a way that the area to the left of the line of no effect indicates a favourable outcome for pyridoxal 5 phosphate. Where keeping to this makes it impossible to avoid outcome titles with clumsy double-negatives (e.g. 'Not improved') we will report data where the left of the line indicates an unfavourable outcome. This will be noted in the relevant graphs.
Assessment of risk of bias in included studies
Again review authors AOA and OA will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011) to assess trial quality. This set of criteria is based on evidence of associations between overestimate of effect and high risk of bias of the article such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting.
If the raters disagree, the final rating will be made by consensus, with the involvement of another member of the review group. Where inadequate details of randomisation and other characteristics of trials are provided, we will contact the authors of the studies in order to obtain further information. Non-concurrence in quality assessment will be reported, but if disputes arise as to which category a trial is to be allocated, again, we will resolve by discussion.
The level of risk of bias will be noted in both the text of the review and in the 'Summary of findings' table.
Measures of treatment effect
1. Binary data
For binary outcomes, we will calculate a standard estimation of the risk ratio (RR) and its 95% confidence interval (CI). It has been shown that RR is more intuitive (Boissel 1999) than odds ratios and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). The number needed to treat/harm (NNT/H) statistic with its confidence intervals is intuitively attractive to clinicians but is problematic both in its accurate calculation in meta-analyses and interpretation (Hutton 2009). For binary data presented in the 'Summary of findings' tables, where possible, we aim to calculate illustrative comparative risks.
2. Continuous data
For continuous outcomes, we will estimate the MD between groups. We would prefer not to calculate effect size measures (SMD). However, if scales of very considerable similarity were used, we will presume there is a small difference in measurement, and we will calculate effect size and transform the effect back to the units of one or more of the specific instruments.
Unit of analysis issues
1. Cluster trials
Studies increasingly employ 'cluster randomisation' (such as randomisation by clinician or practice) but analysis and pooling of clustered data poses problems. Firstly, authors often fail to account for intra-class correlation in clustered studies, leading to a 'unit of analysis' error (Divine 1992), whereby P values are spuriously low, confidence intervals unduly narrow and statistical significance overestimated. This causes type I errors (Bland 1997; Gulliford 1999).
Where clustering is not accounted for in primary studies, we will present data in a table, with a (*) symbol to indicate the presence of a probable unit of analysis error. In subsequent versions of this review, we will seek to contact the first authors of studies to obtain intra-class correlation coefficients (ICCs) for their clustered data and to adjust for this by using accepted methods (Gulliford 1999). Where clustering has been incorporated into the analysis of primary studies, we will present these data as if from a non-cluster randomised study, but adjust for the clustering effect.
We have sought statistical advice and have been advised that the binary data as presented in a report should be divided by a 'design effect'. This is calculated using the mean number of participants per cluster (m) and the ICC [Design effect = 1+(m-1)*ICC] (Donner 2002). If the ICC is not reported, it will be assumed to be 0.1 (Ukoumunne 1999).
If cluster studies have been appropriately analysed taking into account ICCs and relevant data documented in the report, synthesis with other studies will be possible using the generic inverse variance technique.
2. Cross-over trials
A major concern of cross-over trials is the carry-over effect. It occurs if an effect (e.g. pharmacological, physiological or psychological) of the treatment in the first phase is carried over to the second phase. As a consequence, on entry to the second phase the participants can differ systematically from their initial state despite a wash-out phase. For the same reason cross-over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both effects are very likely in severe mental illness, we will only use data of the first phase of cross-over studies.
3. Studies with multiple treatment groups
Where a study involves more than two treatment arms, if relevant, the additional treatment arms will be presented in comparisons. If data are binary, these will be simply added and combined within the two-by-two table. If data are continuous, we will combine data following the formula in section 188.8.131.52 (Combining groups) of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). Where the additional treatment arms are not relevant, we will not use these data.
Dealing with missing data
1. Overall loss of credibility
At some degree of loss of follow-up, data must lose credibility (Xia 2009). We choose that, for any particular outcome, should more than 50% of data be unaccounted for, we will not reproduce these data or use them within analyses. If, however, more than 50% of those in one arm of a study are lost, but the total loss is less than 50%, we will address this within the 'Summary of findings' tables by down-rating quality. Finally, we will also downgrade quality within the 'Summary of findings' tables should loss be 25% to 50% in total.
In the case where attrition for a binary outcome is between 0% and 50% and where these data are not clearly described, we will present data on a 'once-randomised-always-analyse' basis (an intention-to-treat analysis). Those leaving the study early are all assumed to have the same rates of negative outcome as those who completed, with the exception of the outcome of death and adverse effects. For these outcomes, the rate of those who stay in the study - in that particular arm of the trial - will be used for those who did not. We will undertake a sensitivity analysis to test how prone the primary outcomes are to change when data only from people who complete the study to that point are compared with the intention-to-treat analysis using the above assumptions.
In the case where attrition for a continuous outcome is between 0% and 50%, and data only from people who complete the study to that point are reported, we will reproduce these.
3.2 Standard deviations
If standard deviations (SDs) are not reported, we will first try to obtain the missing values from the authors. If not available, where there are missing measures of variance for continuous data, but an exact standard error (SE) and confidence intervals are available for group means, and either a 'P' value or 't' value available for differences in mean, we can calculate them according to the rules described in the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011): When only the SE is reported, SDs are calculated by the formula SD = SE * square root (n). Chapters 7.7.3 and 16.1.3 of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011) present detailed formulae for estimating SDs from P values, t or F values, confidence intervals, ranges or other statistics. If these formulae do not apply, we will calculate the SDs according to a validated imputation method which is based on the SDs of the other included studies (Furukawa 2006). Although some of these imputation strategies can introduce error, the alternative would be to exclude a given study’s outcome and thus to lose information. We nevertheless will examine the validity of the imputations in a sensitivity analysis excluding imputed values.
3.3 Last observation carried forward
We anticipate that in some studies the method of last observation carried forward (LOCF) will be employed within the study report. As with all methods of imputation to deal with missing data, LOCF introduces uncertainty about the reliability of the results (Leucht 2007). Therefore, where LOCF data have been used in the trial, if less than 50% of the data have been assumed, we will present and use these data and indicate that they are the product of LOCF assumptions.
Assessment of heterogeneity
1. Clinical heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will simply inspect all studies for clearly outlying people or situations which we had not predicted would arise. When such situations or participant groups arise, these will be fully discussed.
2. Methodological heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We will simply inspect all studies for clearly outlying methods which we had not predicted would arise. When such methodological outliers arise these will be fully discussed.
3. Statistical heterogeneity
3.1 Visual inspection
We will visually inspect graphs to investigate the possibility of statistical heterogeneity.
3.2 Employing the I
Heterogeneity between studies will be investigated by considering the I
Assessment of reporting biases
1. Protocol versus full study
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. These are described in section 10.1 of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). We will try to locate protocols of included randomised trials. If the protocol is available, outcomes in the protocol and in the published report will be compared. If the protocol is not available, outcomes listed in the methods section of the trial report will be compared with actually reported results.
2. Funnel plot
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are again described in Section 10 of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). We are aware that funnel plots may be useful in investigating reporting biases but are of limited power to detect small-study effects. We will not use funnel plots for outcomes where there are 10 or fewer studies, or where all studies are of similar sizes. In other cases, where funnel plots are possible, we will seek statistical advice in their interpretation.
We understand that there is no closed argument for preference for use of fixed-effect or random-effects models. The random-effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This often seems to be true to us and the random-effects model takes into account differences between studies even if there is no statistically significant heterogeneity. There is, however, a disadvantage to the random-effects model. It puts added weight onto small studies which often are the most biased ones. Depending on the direction of effect, these studies can either inflate or deflate the effect size. We choose the random-effects model for all analyses. The reader is, however, able to choose to inspect the data using fixed-effect model.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1 Primary outcomes
We do not anticipate any subgroup analyses.
1.2 Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of pyridoxal 5 phosphate for people with neuroleptic-induced tardive dyskinesia in general. In addition, however, we will try to report data on subgroups of people in the same clinical state, stage and with similar problems.
2. Investigation of heterogeneity
If inconsistency is high, this will be reported. First, we will investigate whether data has been entered correctly. Second, if data are correct, the graph will be visually inspected and outlying studies will be removed to see if homogeneity is restored. For this review, we have decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, data will be presented. If not, data will not be pooled and issues will be discussed. We know of no supporting research for this 10% cut-off but are investigating use of prediction intervals as an alternative to this unsatisfactory state.
When unanticipated clinical or methodological heterogeneity are obvious, we will simply state hypotheses regarding these for future reviews or versions of this review. We do not anticipate undertaking analyses relating to these.
1. Implication of randomisation
We aim to include trials in a sensitivity analysis if they are described in some way as to imply randomisation. For the primary outcomes, we will include these studies and if there is no substantive difference when the implied randomised studies are added to those with better description of randomisation, then all data will be employed from these studies.
2. Assumptions for lost binary data
Where assumptions have to be made regarding people lost to follow-up (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from people who complete the study to that point. If there is a substantial difference, we will report results and discuss them but will continue to employ our assumption.
Where assumptions have to be made regarding missing SDs data (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from people who complete the study to that point. A sensitivity analysis will be undertaken to test how prone results are to change when completer-only data only are compared with the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them but will continue to employ our assumption.
3. Risk of bias
We will analyse the effects of excluding trials that are judged to be at high risk of bias across one or more of the domains of randomisation (implied as randomised with no further details available) allocation concealment, blinding and outcome reporting for the meta-analysis of the primary outcome. If the exclusion of trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then data from these trials will be included in the analysis.
4. Imputed values
We will also undertake a sensitivity analysis to assess the effects of including data from trials where we used imputed values for ICC in calculating the design effect in cluster randomised trials.
If substantial differences are noted in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we will not pool data from the excluded trials with the other trials contributing to the outcome, but will present them separately.
5. Fixed and random effects
All data will be synthesised using a random-effects model, however, we will also synthesise data for the primary outcome using a fixed-effect model to evaluate whether this alters the significance of the results.
The Cochrane Schizophrenia Group Editorial Base in Nottingham produces and maintains standard text for use in the Methods sections of their reviews. This text has been used as the basis of this protocol, with modifications where necessary.
Adegoke Oloruntoba Adelufosi was awarded a Reviews for Africa (Nigeria) Programme Fellowship funded by a grant from the UK Department for International Development (DFID) through the Effective Healthcare Research Consortium at the Liverpool School of tropical Medicine. This protocol was developed in part during the Reviews for Africa Programme protocol development course organised by the Nigerian Branch of South African Cochrane Centre, July 2012.
The search term was developed by the Trials Search Co-ordinator of the Cochrane Schizophrenia Group, Samantha Roberts.
We acknowledge and thank Dr Ranganath D Rattehalli for peer-reviewing this protocol and his helpful comments, and would also like to thank Heather Maxwell from Cochrane Copy Edit Support team for copy editing this protocol.
Contributions of authors
Adegoke Oloruntoba Adelufosi - Developed the protocol.
Olukayode Abayomi - Assisted in writing the protocol.
Tunde Massey-Ferguson Ojo - Assisted in writing the protocol.
Declarations of interest
The authors received no financial consideration from any parties for the preparation of this review.
Sources of support
- Reviews for Africa (Nigeria) Programme Fellowship, Nigeria.
- UK Department for International Development (DFID) through the Effective Healthcare Research Consortium at the Liverpool School of tropical Medicine., UK.