Amphetamines versus placebo for schizophrenia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
The purpose of this review is to summarise the available evidence on the efficacy and safety of amphetamines compared with placebo in the treatment of adults with schizophrenia.
Background
Description of the condition
Schizophrenia is a mental disorder characterised by a disruption of thought processes and by impaired emotional responses. Schizophrenia affects more than 21 million people worldwide (WHO 2014), and has a global lifetime prevalence of about 0.3–0.7% (APA 2013). Symptoms are unique to each patient (NICE 2014), and usually divided into three broad categories: positive symptoms (such as hallucinations, delusions, thought and movement disorders), negative symptoms (like flat affect, and lack of pleasure), and cognitive symptoms (including poor executive functioning, problems with focusing and memory) (NIMH 2014). Diagnosis is based on observed behaviour and the patient's reported experiences.
The pathogenesis of schizophrenia is thought to be due to an imbalance in the concentrations of dopaminergic and glutamatergic systems in the brain where people with schizophrenia have been shown to have an overactivity of dopamine in the central nervous system (Snyder 1973). This overactivity can disturb all aspects of motor, cognitive and emotional functioning and can result in an acute schizophrenic psychosis. Based on the above, antipsychotic drugs, which balance dopamine levels in the central nervous system, are used in the treatment of people with schizophrenia.
Description of the intervention
Amphetamines are psychostimulant drugs that are classified by the United States Drug Enforcement Agency and the World Health Organization (WHO) as a controlled substance (Pedra 2013). The name 'amphetamine' comes from the chemical name alpha‐ethylphenethylamine. Amphetamines release dopamine and other biogenic amines from storage sites in presynaptic nerve terminals and block their re‐uptake (Moore 1977; Scheel‐Kruger 1971). Psychostimulants use causes increased alertness with increased vigilance, a sense of well‐being, and euphoria. Many users experience insomnia, anorexia, and some may develop psychotic symptoms. Psychostimulants effect on peripheral cardiovascular activity includes increased blood pressure and heart rate. Recurrent use of amphetamines may induce psychosis in healthy people, and may cause relapse in people with schizophrenia even if they are compliant with their antipsychotic medication (Baker 2005). Additionally, it can produce a sense of well‐being, elation, vigour and talkativeness (Brown 1997; Smith 1977), as well as improving recovery of motor and language functions in stroke patients (Martinsson 2003). However, depression and sedation can occur too (Dommisse 1984), and recent studies on mice shows that amphetamine decreased social play, and social preference (Manduca 2013; Moy 2013). It has also an appetite‐suppressing effect regulated by hypothalamic neuropeptide Y and two genes, c‐fos and c‐jun (Hsieh 2013). The American Psychiatric Association describes the following 10 amphetamine‐related psychiatric disorders (Larson 2013).
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Amphetamine‐induced anxiety disorder.
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Amphetamine‐induced mood disorder.
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Amphetamine‐induced psychotic disorder with delusions.
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Amphetamine‐induced psychotic disorder with hallucinations.
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Amphetamine‐induced sexual dysfunction.
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Amphetamine‐induced sleep disorder.
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Amphetamine intoxication.
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Amphetamine intoxication delirium.
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Amphetamine withdrawal.
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Amphetamine‐related disorder not otherwise specified.
Additionally, the WHO International Statistical Classification of Diseases and Related Health Problems 10th Revision (ICD‐10) classifies the following mental and behavioural disorders due to psychoactive substance use.
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Acute intoxication.
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Harmful use.
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Dependence syndrome.
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Withdrawal state.
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Withdrawal state with delirium.
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Psychotic disorder.
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Amnesic syndrome.
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Residual and late‐onset psychotic disorder.
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Other unspecified mental and behavioural disorders.
How the intervention might work
Amphetamine works by increasing extracellular dopamine and prolonging dopamine receptor signalling in the striatum and it accomplishes that by three major mechanisms. First, it is a substrate for the dopamine transporter that competitively inhibits dopamine uptake; second, it facilitates dopamine’s release out of the vesicles and into the cytoplasm, and third it promotes DAT‐mediated reverse‐transport of dopamine into the synaptic cleft independently of action‐potential‐induced vesicular release (Calapari 2013). All the above mentioned mechanisms lead to an increased availability of dopamine which plays an essential role in executive function through influencing behavior, thoughts, working memory concentration and attention as well as influencing mood and causing sensations of well being, elation, and talkativeness.Thus, amphetamines should, in theory, be useful in treating the apathy and negative symptoms associated with chronic schizophrenia.
Why it is important to do this review
Substance abuse among individuals with psychiatric disorders is a widely recognised problem (Drake 1989; Reiger 1990).
About 40% to 50% of individuals with schizophrenia have a lifetime suffering from substance abuse disorder (Blanchard 2000). However, estimates range between 10% and 65% and this wide range may be attributed to the use of different methodologies in each study, such as differing populations, assessment techniques and demographic characteristics (Mueser 1992).
Compared to individuals with schizophrenia who do not abuse drugs, individuals with schizophrenia who do abuse drugs have higher rates of hospitalisation (Cleghorn 1991; Drake 1990; Lieberman 1989), suicide (Cohen 1990), homelessness (Drake 1990), and unemployment (Seibyl 1993). Accordingly, substance abuse appears to affect both the course and the treatment of schizophrenia (Blanchard 2000), since it leads to decreased compliance with treatment as well as the effects of the drugs being used, hence leading to a poor outcome (Drake 1991).
The high incidence of drug abuse in people with schizophrenia has been thought to be due to one of the following reasons (Blanchard 2000); First, illegal drugs are used as self‐medication in schizophrenia. Second, substance abuse disorders can cause a schizophrenia‐like psychosis, and the third points towards substance abuse disorders and schizophrenia sharing a common genetic origin.
Theoretically, amphetamines and amphetamine‐like drugs could have a role in the treatment of negative symptoms experienced by some patients with chronic schizophrenia. Additionally, 40% to 62% of people with schizophrenia are overweight or obese. Obesity increases these patients’ risk for cardiovascular morbidity and mortality (Üçok 2008). Hence, through their appetite suppressant effect, amphetamines could aid these patients in weight loss. On the other hand, clinicians actively discourage people with psychosis from experimenting with psychostimulants (Baker 2001). They are driven by a strong clinical impression that suggests that using stimulants, such as amphetamines, is detrimental to the mental state and functioning of a person with schizophrenia. Also, amphetamines lead to several physical side effects such as increased blood pressure and heart rate which could be unsafe particularly in those who are sedentary, overweight and/or have additional medical diagnoses. Furthermore, abuse potential and tolerance issues related to long‐term amphetamine use must be kept in mind if they are to be implicated in the treatment of schizophrenia, as well as and the need, in some countries, to have individual prescriptions written and picked up by patients monthly which can cause a transportation problem for many of those with schizophrenia.
Objective quantification of the effects of amphetamines on people with schizophrenia is rare; however, this review aims to assess the evidence for efficacy and safety of amphetamines and amphetamine‐like substances in comparison with placebo in the treatment of people with chronic schizophrenia. An existing Cochrane systematic review, Nolte 2004, is now somewhat out of date, so this work represents a substantial update of that review.
Objectives
The purpose of this review is to summarise the available evidence on the efficacy and safety of amphetamines compared with placebo in the treatment of adults with schizophrenia.
Methods
Criteria for considering studies for this review
Types of studies
All relevant randomised controlled trials (RCTs). 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, 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 within amphetamines or placebo, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the amphetamines and placebo that is randomised.
Types of participants
People with schizophrenia or related disorders, including schizophreniform disorder, schizoaffective disorder and delusional disorder, again, by any means of diagnosis.
We are interested in making sure that information is as relevant to the current care of people with schizophrenia as possible so propose to clearly highlight, if possible, 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. Intervention: amphetamine at any dose
2. Comparators: placebo (active or inactive), or no treatment
Types of outcome measures
We will, if possible, divide outcomes into short term (less than six months), medium term (7‐12 months) and long term (over one year).
Primary outcomes
1. Global state
1.1 Clinically significant response in global state, as defined by each study.
1.2 Relapse, as defined by each study.
1.3 Any improvement, as defined by each study.
1.4 Average score/change in global state.
2. Mental state
2.1 Clinically significant response, as defined by each study.
2.2 Any improvement, as defined by each study.
2.3 Average score/change in mental state.
2.4 Average score/change in negative symptoms.
2.5 Any clinically significant response in mental state, as defined by each study.
2.6 Any clinically significant response in negative symptoms, as defined by each study.
3. Adverse effects: psychological adverse events
3.1 Any clinically significant stimulant‐induced psychosis.
3.2 Any clinically significant psychosis, as defined by each study.
3.3 Average score/change in psychological side effects.
3.4 Incidence of use of antipsychotic drugs.
Secondary outcomes
1. Service utilisation outcomes
1.1 Hospital admission.
1.2 Days in hospital.
2. Behaviour
2.1 Any clinically significant response in behaviour, as defined by each study.
2.2 Average score/change in behaviour.
2.3 Aggression/violence.
3. Adverse effects
3.1 Death.
3.2 Cardiovascular effects.
3.3 Genitourinary effects.
3.4 Gastrointestinal effects.
3.5 Central nervous system effects.
3.6 Respiratory effects.
3.7 Weight change.
3.8 Any abnormal laboratory tests.
3.9 Any other specific adverse effects.
4. Social functioning
4.1 Clinically significant response in social functioning, as defined by each study.
4.2 Any improvement, as defined by each study.
4.3 Average score/change in social functioning.
5. Quality of life/satisfaction with care for either recipients of care or caregivers
5.1 Significant change in quality of life/satisfaction, as defined by each study.
5.2 Average score/change in quality of life/satisfaction.
5.3 Any change in employment status, as defined by each study.
6. Cognitive functioning
6.1 Any significant change in cognitive functioning, as defined by each study.
6.2 Degree of change in cognitive functioning, as defined by each study.
7. Economic outcomes
7.1 Costs due to treatment, as defined by each study.
7.2 Savings due to treatment, as defined by each study.
8. Leaving the study early
8.1 Owing to relapse.
8.2 Owing to adverse effects.
8.3 For any reason.
'Summary of findings' table
We will use the GRADE approach to interpret findings (Higgins 2011) and will use GRADE profiler (GRADEPRO) to import data from RevMan 5.3 (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 main outcomes for inclusion in the 'Summary of findings' table.
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Global state: relapse, as defined in each study (medium term).
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Mental state: any improvement, as defined by each study (medium term).
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Mental state: specific symptoms, first‐rank symptoms (medium term).
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Psychological adverse effects: Stimulant induced psychosis (short term).
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Psychological adverse effects: Stimulant induced psychosis (medium term).
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Quality of life: significant change in quality of life/satisfaction (medium term).
Search methods for identification of studies
Electronic searches
1. Cochrane Schizophrenia Group’s Trials Register
The Trials Search Co‐ordinator (TSC) of the Cochrane Schizophrenia Group will search the Group's Registry of Trials using the following search strategies:
("Adipex P" or AdipexP or *amphetamine* or *methylphenyl* or *fetamine* or Avipron or Centramina or Chlorphentermine or Curban or Deoxyephedrine or Desopimon or Desoxyephedrine or Desoxyn* or Dexedrine or DextroStat or Didrex or Duromine or Ecstasy or Fenamine or Hydroxyphenylisopropylamine or "Iodine 123 IMP" or Iofetamine or Ionamine or "LY 121860" or "LY 123362" or LY121860 or LY123362 or Madrine or MDMA or Mephentermine or Methyltyramine or Mydrial or Norpholedrin or Oxydess or Paredrine or Phenamine or Phenopromin or Phentermine or Pre‐Sate or Thyramine) in Title or Abstract Fields of REFERENCE or (*amphetamine or *methylphenyl*) in Intervention Field of STUDY.
The Cochrane Schizophrenia Group's Registry of Trials is compiled by systematic searches of major resources (including AMED, BIOSIS, CINAHL, EMBASE, MEDLINE, PsycINFO, PubMed, and registries of clinical trials) and their monthly updates, handsearches, grey literature, and conference proceedings (see Group Module). There is no language, date, document type, or publication status limitations for inclusion of records into the register.
Searching other resources
1. Reference searching
We will inspect references of all included studies for further relevant studies.
2. Personal contact
We will, if necessary, contact the first author of each included study for information regarding unpublished trials.
Data collection and analysis
Selection of studies
Two authors (JI and RB) will independently inspect citations from the searches and initially identify relevant abstracts. As we do not expect to find many citations, a third author (NE) will independently re‐inspect all citations to ensure reliability. Where disputes arise, we will obtain the full‐text reports for further assessment. We will retrieve full reports of the conference proceedings meeting the review criteria, Two authors (BY and AM) will inspect these and a third (NE) will re‐inspect these full reports in order to assure 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
Two authors (JI and RB) will extract data from all included studies. In addition, to assure reliability, two other authors (MY and AM) will independently extract data from these studies. We will discuss any disagreement, document our decisions and, if necessary, attmept to contact authors of studies for clarification. With remaining problems, a fifth author (NE) will help clarify issues and we will document our final decisions in the full review. We will extract data presented only in graphs and figures whenever possible, but include only if two 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. For multicentre studies, where possible, we will extract data relevant to each component centre separately.
2. Management
2.1 Forms
We will extract data using pre‐standardised data extraction forms.
2.2 Scale‐derived data
We will include continuous data from rating scales only if:
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the psychometric properties of the measuring instrument have been described in a peer‐reviewed journal (Marshall 2000); and
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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 a self‐reporting tool or one that was completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly and thus will note if this is the case or not in the 'Description of studies' section of the full review.
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 to primarily use endpoint data, and only use change data if the former are not available. We will combine endpoint and change data in the analysis as we will use mean differences (MDs) rather than standardised mean differences (SMDs) 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.
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For change data, We will enter change data, as 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 change data into statistical analyses.
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For endpoint data:
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when a scale starts from the number 0, we will subtract the lowest possible value from the mean, and divide this by the standard deviation (SD). If this value is lower than 1, it strongly suggests a skew, and we will exclude the study. If this ratio is higher than 1 but below 2, there is suggestion of skew. We will enter the study and test whether its inclusion or exclusion would change the results substantially. Finally, if the ratio is larger than 2, we will include the study, because skew is less likely (Altman 1996; Higgins 2011);
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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) (Kay 1986), we will modify the calculation described above to take into account the scale starting point. In such cases skew is present if 2 SD > (S ‐ S min), where S is the mean score and S min is the minimum score.
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Irrespective of the above rules, we will enter endpoint data from studies of at least 200 participants in the analysis because skewed data pose less of a problem in large studies.
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, we will make efforts 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) or the PANSS (Kay 1986; Overall 1962), this could be considered as a clinically significant response (Leucht 2005a; Leucht 2005b). 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 Amphetamines. Where keeping to this makes it impossible to avoid outcome titles with clumsy double‐negatives (e.g. 'Not un‐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
Review authors (JI, RB, BY, AM) will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). 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 authors disagree, we will make the final rating by consensus, with the involvement of NE. Where inadequate details of randomisation and other characteristics of trials are provided, we will attempt to contact authors of the studies in order to obtain further information. We will report non‐concurrence in quality assessment, but if disputes arise as to which category a trial is to be allocated, again, we will resolve by discussion.
We will note the level of risk of bias in the text of the review, 'Risk of bias' summary, 'Risk of bias' graph and in the 'Summary of findings' table.
Measures of treatment effect
1. Binary data
For binary outcomes we will calculate standard estimations of risk ratios (RRs) and their corresponding 95% confidence intervals (CIs). It has been shown that RRs are more intuitive than odds ratios (ORs) (Boissel 1999), and that ORs tend to be interpreted as RRs by clinicians (Deeks 2000). The number needed to treat/harm (NNT/H) statistics with their CIs are intuitively attractive to clinicians but can be problematic both in terms of accurate calculation in meta‐analyses and interpretation (Hutton 2009). For binary data presented in the 'Summary of findings' tables, where possible, we will calculate illustrative comparative risks.
2. Continuous data
For continuous outcomes will estimate MDs between groups. We prefer not to calculate effect size measures (SMDs). 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. We will seek to contact first authors of such studies to obtain intra‐class correlation coefficients 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 intraclass correlation coefficient (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, we will simply add them and combine within the two‐by‐two table. If data are continuous, we will combine data following the formula in 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.
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 (ITT) 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 to the ITT 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 data only from people who complete the study to that point are reported, we will reproduce these.
3.2 Standard deviations
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 CIs available for group means, and either the 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). The Cochrane Handbook for Systemic reviews of Interventions presents detailed formulae for estimating SDs from P values, t or F values, CIs, ranges or other statistics (Higgins 2011). 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 I2 statistic
We will investigate heterogeneity between studies by considering the I2 statistic alongside the P value of the Chi2 test. The I2 statistic 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 both the magnitude and direction of effects and the strength of evidence for heterogeneity (e.g. P value from the Chi2 test, or CIs for I2 statistic). We will consider an I2 statistic estimate of greater than or equal to around 50% accompanied by a statistically significant Chi2 test (P value < 0.01) as evidence of substantial levels of heterogeneity (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
1. Protocol versus full study
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Higgins 2011). We will attempt 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 plots
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997; 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 the fixed‐effect or the 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 fixed‐effect model for all analyses. The reader is, however, able to choose to inspect the data using the random‐effects model.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1 Primary outcomes
No subgroup analysis is anticipated.
1.2 Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of amphetamines versus placebo for people with schizophrenia in general. However, we will attempt to report data on subgroups of people in the same clinical state, stage and with similar problems.
2. Investigation of heterogeneity
We will report relevant findings if heterogeneity was found to be high. Firstly, we will investigate whether data has been entered correctly. Secondly, if data is correct, we will visually inspect the graph and remove studies outside of the company of the rest to see if homogeneity is restored. For this review we 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 these data. If not, we will not pool these data and will discuss 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 we will use all the data from these studies.
2. Assumptions for lost binary data
Where assumptions have to be made regarding people lost to follow‐up (Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumptions 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 (Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumptions and when we use data only from people who complete the study to that point. We will perform a sensitivity analysis to test how prone results are to change when completer‐only data only are compared to 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, 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
We will synthesise all data 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 results.
