Memantine for schizophrenia

  • Protocol
  • Intervention

Authors


Abstract

This is the protocol for a review and there is no abstract. The objectives are as follows:

To assess the clinical effectiveness and safety of memantine in treating patients with schizophrenia or schizophrenia-like psychosis.

Background

Description of the condition

Schizophrenia is a serious mental illness. It accounts for 1.1 % of the total disability-adjusted life years worldwide and 2.8 % of the years lived with disability worldwide (Picchioni 2007). It affects about 1% of the world population, with similar rates across different countries, cultures and sexes. The age of onset tends to be between 16 to 30 years and the illness can be present throughout the person's adult life. The cause is unknown but it is believed that genetic factors, early environmental and social factors contribute (Mueser 2004). It is still a matter of debate whether schizophrenia is a neurodegenerative condition with progressive neurodegenerative changes manifesting in early adulthood or is a neurodevelopmental disorder starting in early life (Rund 2009). Different regions of the brain are believed to be implicated in patients with schizophrenia - enlarged ventricles, smaller cingulate gyri, reduction in the volume of Dorsolateral Prefrontal Cortex (DLPFC), smaller temporal lobes and hippocampi (Galderisi 2008).

A person diagnosed with schizophrenia often presents with a combination of positive (i.e. hallucinations, delusions, catatonic behaviour), negative (i.e. apathy, low motivation, social withdrawal) and cognitive (i.e. disorganised thinking, memory deficits, difficulty in integrating thoughts, behaviour and feelings) symptoms which lead to problems in social and occupational functioning and self-care (Mueser 2004). Schizophrenia not only affects people in terms of personal suffering but has a significant impact on the caregiver and society at large. It entails significant cost implications in terms of considerable direct and indirect costs which include frequent hospitalisations, the need for long-term psychosocial and monetary support and life-time lost productivity (Awad 2008).

Description of the intervention

Memantine (1-amino adamantane derivative) is an uncompetitive N-methyl-D-aspartate receptor (NMDAR) antagonist with moderate affinity (Sonkusare 2005). It is currently used in the treatment of moderate to severe Alzheimer's dementia either as a monotherapy or in combination with acetylcholinesterase inhibitors (Lo 2011 ). N-methyl-D-aspartate (NMDA) receptor is a subtype of glutamate receptors. The three well-studied subtypes of glutamate receptors include NMDA, α-amino-3-hydroxy-5-methyl-4 isoxazole propionic acid (AMPA) and kinate receptors. They are ligand-gated ion channels also known as ionotropic glutamate receptors. They are found throughout the mammalian brain and form the major excitatory transmitter system. Glutamate is the main excitatory neurotransmitter in the central nervous system acting on these receptors (Hollmann 1994).

NMDA receptors are believed to have a role in various basic functions in the central nervous system. They are involved in regulating neurodevelopment and synaptic plasticity, which in turn have an effect on cognitive processes namely learning and memory formation (Gonda 2012). Overactivation of the NMDA subtype of glutamate receptors can lead to excitotoxic neuronal cell death. However, for normal neuronal functioning, NMDA receptor activity is essential (Chen 2006 ). Memantine is also a NMDAR blocker but because of its low affinity and rapid on-and-off kinetics, it has a reduced potential to cause psychotomimetic-like effects (Monaghan 2009). It therefore allows normal physiological functioning and has been found to be relatively safe and effective in animal models, and in treating patients with Alzheimer's dementia (Dominguez 2011).

How the intervention might work

For decades the mainstay neurochemical hypothesis behind schizophrenia has been dopamine dysfunction. This suggests that excess dopaminergic neurotransmission, particularly in the striatal brain region and dopaminergic deficits in the pre-frontal brain region may be responsible for causing the positive and negative symptoms of schizophrenia (Javitt 2010). The role of the glutamatergic system in the pathophysiology of schizophrenia has been under study with new evidence emerging that the glutamatergic dysfunction may be responsible for dopamine excess. The NMDA receptor hypofunctioning is believed to play a role in the pathophysiology of schizophrenia (Schwartz 2012). There is more evidence to suggest dysregulation of NMDARs as an important factor in the pathophysiology of schizophrenia (Gonzalez-Burgos 2012).

There seems to be an association between NMDA receptors and dopamine. Although NMDA receptors are located throughout the brain, they may play a role in dopamine release via NMDA receptors. This possibly explains that dopaminergic deficits in schizophrenia could also be as a result of underlying glutamatergic dysfunction (Javitt 2010). Recent genetic studies have demonstrated that memantine, a N-methyl-D-aspartate receptor antagonist promotes cell proliferation and production of mature granule neurons in the hippocampus (Maekawa 2009). Memantine, because of its uncompetitive antagonist and rapid on-and-off kinetics, and neuroprotective properties, may be of use in restoring this dysfunction and providing the required neuroprotection in schizophrenia patients. We anticipate that because of its novel action, it would prove useful in patients with schizophrenia, especially un-remitted schizophrenia, notably by improving the negative symptoms and cognitive deficits.

Why it is important to do this review

Schizophrenia's traditional models of the causative pathology have focused mainly on the dopamine hypothesis (Olney 1995). It has been suggested that there could be a possible role for other neurotransmitters such as serotonin, acetylcholine and glutamate in treating schizophrenia. This is based on the fact that currently available antipsychotics, both conventional and second generation, leave many symptoms untreated and cause undue side effects (Stone 2007).

Lately, the focus has been on the role of the excitatory neurotransmitter glutamate acting via NMDARs (Bondi 2012). It is therefore imperative to undertake a systematic review of the current studies with a view to establish if memantine with an uncompetitive antagonist action at NMDA receptors could be added to the armoury of drugs for treating schizophrenia.

Objectives

To assess the clinical effectiveness and safety of memantine in treating patients with schizophrenia or schizophrenia-like psychosis.

Methods

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 (Sensitivity analysis). If their inclusion does not result in a substantive difference, we will retain them in the analyses. If their inclusion does result in 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 within the memantine group, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the memantine that is randomised. Randomised cross-over studies will be eligible but only data up to the point of first cross-over because of the instability of the problem behaviours and the likely carry-over effects (Elbourne 2002).

Types of participants

Adults (age 16 years or more), with schizophrenia or other types of schizophrenia-like psychoses including schizophreniform disorder, schizoaffective disorder and delusional disorder, regardless of the diagnostic criteria used, age, ethnicity and sex. There is no clear evidence that the schizophrenia-like psychoses are caused by fundamentally different disease processes or require different treatment (Carpenter 1994). We will exclude children, adults with dementing illnesses, depression and primary problems associated with substance misuse.

Where a study describes the participant group as suffering from 'serious mental illnesses' and does not give a particular diagnostic grouping, these trials will be included assuming that most people suffer from schizophrenia. The exception to this rule will be when the majority (over 50%) of those randomised clearly do not have a functional non-affective psychotic illness.

We will ensure that the information is as relevant to the current care of people with schizophrenia as possible. Hence, we will clearly highlight the current clinical state (acute, early post-acute, partial remission, remission) as well as the stage (prodromal, first episode, early illness, persistent) and as to whether the studies primarily focused on people with particular problems (for example, negative symptoms, treatment-resistant illnesses).

Types of interventions

1. Memantine

Given orally alone or in combination with other antipsychotics, any dose .

Compared with:

a. Conventional and atypical antipsychotics

Any dose via any route of administration.

b. Placebo or no intervention

Types of outcome measures

The outcomes will be grouped into the short term (up to 12 weeks), medium term (13 to 26 weeks) and long term (over 26 weeks) based on the study duration. We will be more interested in long-term outcomes, especially for primary outcomes, considering the chronic nature of the condition.

Primary outcomes
Clinical response

1.1 Clinically significant response - as defined by each of the studies or
1.2 Any clinical response - as defined by each of the studies

2. Adverse effects - any serious, specific adverse effects - long term

Secondary outcomes
1. Leaving the study early

1.1 For specific reasons
1.2 For general reasons

2. Global state

2.1 Clinically important change in global state (as defined by individual studies)
2.2 Relapse (as defined by the individual studies)

3. Mental state

3.1 Clinically important change in general mental state score
3.2 General mental state score (average and endpoint)
3.3 Clinically important change in specific symptoms (positive symptoms of schizophrenia, negative symptoms of schizophrenia)
3.4 Speicfic symptom score ( average and endpoint)

4. General functioning

4.1 Clinically important change in general functioning
4.2 General functioning score ( average and endpoint)

5. Cognitive functioning (as measured by psychometric tests)

5.1 Clinically important change in overall cognitive functioning
5.2 Overall cognitive functioning score (endpoint and average)
5.3 Clinically important change in specific cognitive functions (attention, concentration, memory, language, executive functioning)
5.4 Speicfic cognitive score (average and endpoint)

6. Quality of life

6.1 Clinically important change in quality of life
6.2 Any change in quality of life score (average and endpoint)

7. Adverse effect

7.1 Death
7.2 Any non-serious general adverse effects
7.3 Any serious, specific adverse effects - other time periods
7.4 Any change in general adverse effect score (average and endpoint)
7.5 Clinically important change in specific adverse effects
7.6 Any change in specific adverse effects score (average and endpoint)

8. Economic outcomes

8.1 Direct costs
8.2 Indirect costs

9. Behaviour

9.1 Clinically important change in general behaviour
9.2 Any important change in general behaviour (average and end point)
9.3 Clinically important change in specific aspects of behaviour
9.4 Any important change in specific aspects of behaviour score (average and end point)
9.5 Average change in specific aspects of behaviour

10. Service outcomes

10.1 Duration of hospital stay
10.2 Change in hospital stay score (average and endpoint)
10.2 Re-admission
10.3 Clinically important engagement with services
10.4 Engagement with services score (average and endpoint)

11. Satisfaction with treatment

11.1 Number of participants satisfied with treatment
11.2 Number of participants not satisfied with treatment.

12. 'Summary of findings' table

We will use the GRADE approach to interpret findings (Schünemann 2008) and 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 the following short- or medium-term outcomes for inclusion in the 'Summary of findings' table.

  1. Global state: clinically important change in global state

  2. Leaving the study early: any reason, adverse events, or inefficacy of treatment

  3. Mental state: clinically significant change in mental state - as defined by each of the studies

  4. General functioning: clinically important change in general functioning

  5. Cognitive functioning: clinically important change in overall cognitive functioning

Search methods for identification of studies

Electronic searches

Cochrane Schizophrenia Group Trials Register

We will search the register using the phrase:

 [(*Mematine* OR *Axura* OR *Akatin?* OR *Namenda* OR *Ebixa* OR *Abixa* OR *Memox* OR *Memary* in interventions of STUDY)]

 This register is compiled by systematic searches of major databases, handsearches and conference proceedings (see Group Module).

Searching other resources

1. Reference searching

We will inspect references of all included and excluded studies for further relevant studies.

2. Personal contact

We will contact the first author of each included study for information regarding unpublished trials.

3. Pharmaceutical companies

We will contact relevant pharmaceutical companies and request information about any relevant published and unpublished data.

Data collection and analysis

Selection of studies

Two review authors (KK and RK) will independently inspect citations from the searches and identify relevant abstracts. A third review author (JS) will independently re-inspect the majority 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 KK and RK. Again, the majority of reports will be re-inspected by JS 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

1. Extraction

Review authors KK and RK will extract data from all included studies. In addition, to ensure reliability, JS 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, authors of studies will be contacted for clarification. With remaining problems JS will help clarify issues and these final decisions will be documented. Data presented only in graphs and figures will be extracted whenever possible, but included only if two review authors independently have the same result. Attempts will be made to contact authors through an open-ended request in order to obtain missing information or for clarification whenever necessary. If studies are multi-centre, where possible, we will extract data relevant to each component centre separately.

2. Management
2.1 Forms

Data will be extracted 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 aim to 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 aim 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 starts from a positive value (such as the Positive and Negative Syndrome Scale (PANSS) 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 endpoint data from studies of less than 200 participants will be entered in other tables within the data analyses section rather than into a statistical analysis. Skewed data pose less of a problem when looking at means if the sample size is large and we will enter skewed endpoint data from larger trial (over 200 participants) into statistical syntheses.

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 enter skewed change data from both large and small trails into syntheses.

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 memantine. 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, JS and KK 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 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, resolution will be made 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 to Benefit/Harm (NNTB/H) statistic with its CI 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' table/s, where possible, we will calculate illustrative comparative risks.

2. Continuous data

For continuous outcomes, we will estimate theMD between groups. We prefer not to calculate effect size measures (SMD). However, if scales of very considerable similarity are 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, CIs 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 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 7.7.3.8  (Combining groups) of the Cochrane Handbook for Systemic reviews of Interventions. Where the additional treatment arms are not relevant, these data will not be reproduced.

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 table/s by down-rating quality. Finally, we will also downgrade quality within the Summary of Findings table/s should loss be 25-50% in total.

2. Binary

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 testing how prone the primary outcomes are to change when data only from people who complete the study to that point are compared to the intention to treat analysis using the above assumptions.

3. Continuous
3.1 Attrition

In the case where attrition for a continuous outcome is between 0% and 50% and completer-only data are reported, we will reproduce these.

3.2 Standard deviations (SDs)

If 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 (CIs) available for group means, and either a 'P' value or 't' value are 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 standard error (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, CIs, 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 reproduce 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 I2 statistic

Heterogeneity between studies will be investigated by considering the I2 method alongside the Chi2 'P' value. The I2 provides an estimate of the percentage of inconsistency thought to be due to chance (Higgins 2003). The importance of the observed value of I2 depends on i. magnitude and direction of effects and ii. strength of evidence for heterogeneity (e.g. 'P' value from Chi2  test, or a CI for I2). An I2 estimate greater than or equal to around 50% accompanied by a statistically significant Chi2 statistic, will be interpreted as evidence of substantial levels of heterogeneity (Section 9.5.2 - Cochrane Handbook for Systemic reviews of Interventions - Higgins 2011). When substantial levels of heterogeneity are found in the primary outcome, we will explore reasons for heterogeneity (Subgroup analysis and investigation of heterogeneity).

Assessment of reporting biases

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are 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.

Data synthesis

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 nevertheless favour using a random-effects model for all analyses but additionally we will investigate the use of a fixed-model approach in sensitivity analyses for the primary outcomes.

Subgroup analysis and investigation of heterogeneity

1. Subgroup analyses
1.1 Clinical state, stage or problem - primary outcomes only

We propose to undertake this review and provide an overview of the effects of memantine for people with schizophrenia 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 have been entered correctly. Second, if data are correct, we will visually inspect the graph and remove outlying studies 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, we will present the data. If not, we will not pool the data and discuss relevant issues. 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.

Sensitivity analysis

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 we 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 are compared to the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them, but we 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 we will include data from these trials 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 fixed-effect model however, we will also synthesise data for the primary outcome using a random-effects model to evaluate whether this alters the significance of the result.

Acknowledgements

We would like to thank Claire B Irving in the Cochrane Schizophrenia Group editorial base, Nottingham, UK for all her help and patience.

We would also like to acknowledge and thank Dr Samir Srivastava for peer reviewing this protocol.

The Cochrane Schizophrenia Group Editorial Base in Nottingham produces and maintains standard text for use in the Methods section of their reviews. We have used this text as the basis of what appears here and adapted it as required.

The search term has been developed by the Trial Search Co-ordinator of the Cochrane Schizophrenia Group, Samantha Roberts.

Contributions of authors

Kamalpreet Kour - development and writing of the protocol.

Rupinder Kour - helped write the protocol.

Jasvinder Singh - helped write the protocol and gave advice.

Declarations of interest

The review authors have no known conflicts of interest.

Sources of support

Internal sources

  • Cochrane Schizophrenia Group, Nottingham, UK.

External sources

  • None, Not specified.

    No sources of support provided

Ancillary