Magnetic seizure therapy for people with schizophrenia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To estimate the effects of magnetic seizure therapy (MST) alone compared with sham MST or with standard care or any other comparators for schizophrenia.
Background
Description of the condition
Schizophrenia is one of the most common mental disorders; its general population prevalence is estimated to be 1% (Lehman 2004) with no gender difference (McGrath 2008). It has two peaks of onset, during ages 15 to 24 years and 55 to 64 years respectively (Chan 2017). Clinical presentation is diversified and principal features include positive symptoms (e.g. delusions, hallucinations, disorganised speech), negative symptoms (e.g. affective flattening, alogia, avolition) and cognitive impairment (Tandon 2013). Diagnosis is built on history and mental state examination (Owen 2016) using operational criteria from manuals such as the Diagnostic and Statistical Manual of Mental Disorders (DSM) (APA 2013) and the WHO International Classification of Diseases (ICD) (WHO 1992). This psychopathology causes deterioration of functioning over time and is described as a highly disabling condition, which makes it a heavy burden on individuals, families and society. Schizophrenia was ranked 11th among the top 25 causes of global years lived with disability (YLDs) in 2013 (Global Burden of Disease Study 2013 Collaborators).
The main treatment plan for schizophrenia is antipsychotic medications combined with psychosocial interventions and rehabilitation (Lehman 2004; Owen 2016). Antipsychotics remain the mainstay of the treatments for schizophrenia (Owen 2016). However, 20% of people with schizophrenia do not respond to antipsychotics (Marder 1993) and need to seek other treatment options. One such treatment is electroconvulsive therapy (ECT). People with schizophrenia receive ECT treatment because of unpleasant side effects and unsatisfactory efficacy of medications, anticipation of or need for rapid response, or personal preference (APA 1990; Tharyan 2005).
Major depression is the main indication for ECT in the United States, Australia, and European countries (Chanpattana 2007; Moksnes 2010; Mowla 2015) while schizophrenia is the most common indication in Asia (Chanpattana 2005; Chanpattana 2010). ECT has been widely used in China since its introduction in the 1950s for the treatment of schizophrenia (Tang 2012). The usage rate of ECT for schizophrenia increased over the past decade in China while remaining low and relatively stable in other Asian countries (Xiang 2015). The popularity of ECT in developed countries such as the United States and United Kindom has declined since concerns about cognitive side effects arose (Allan 2011).
Description of the intervention
Since the introduction of ECT as a therapeutic method for schizophrenia in 1934, it has played an important role in the treatment for schizophrenia for over 70 years (Eitan 2006). ECT is the only non‐pharmacological physical treatment option for schizophrenia approved by the U.S. Food and Drug Administration (FDA) (Weiner 2013). It is also widely used for other psychiatric conditions such as major depressive disorder (MDD), bipolar disorder (BPD), catatonia, and schizoaffective disorder (Owen 2016). Advances in anesthesiology have greatly improved the safety and tolerability of ECT, however post‐ictal confusion, attention deficiency, and transient memory disturbance are often problematic and affect treatment compliance (Holtzheimer 2006; Hoy 2011; Lisanby 2003a). Attempts to improve the efficacy and side‐effect profile of ECT can be made by using alternative electrode placements, variations in stimulus configuration and focal electrical stimulation. Novel developments such as magnetic seizure therapy (MST) are also used (Eitan 2006; Lisanby 2003b; Loo 2006)
MST is a promising alternative to ECT that, for now, is only used for research purposes. MST is a noninvasive, physical treatment, developed as an improvement over conventional convulsive therapiess (Lisanby 2001b). It combines the characteristics of both ECT and repetitive transcranial magnetic stimulation (rTMS). MST induces a seizure to alleviate symptoms (Rau 2007) and generates electromagnetic stimulation by rapidly alternating magnetic fields like rTMS but in a more intensive way (Lisanby 2001b; Lisanby 2002).
MST is conducted under general anaesthesia, requiring short‐acting anaesthetics and muscle relaxants (Lisanby 2001b; Tharyan 2005). A twin coil held at the vertex (or sometimes a figure eight coil on the right prefrontal cortex) generates magnetic fields and forms an indirect electric current in the brain, which induces a seizure when it exceeds the individual seizure threshold (Fitzgerald 2013; Hoy 2010; Kayser 2015: Lisanby 2001a; Lisanby 2001b; Noda 2014; Polster 2015).The magnetic seizure threshold is normally titrated at the first treatment session by ascending duration in train (Fitzgerald 2013; Hoy 2011). Electroencephalograms (EEGs) are monitored and rated to ensure the required seizure (Kayser 2015) and precautions should be taken to prevent side effects. Earplugs are required for patients and staff present to prevent tinnitus or potential hearing damage (Fitzgerald 2013) and a bite‐block should be used by patients to protect their teeth (Hoy 2011). Session arrangements are basically the same as in an ECT treatment plan, occurring twice a week for a period of 5 to 6 weeks (Hoy 2011; Polster 2015).
How the intervention might work
The efficacy of ECT is affected by impedance of the scalp and skull. Impedance can elevate electrical intensity and influence current distribution which leads to less control over regional stimulation of the brain. The MST device is immune to impedance as it generates electromagnetic signals by rapidly alternating magnetic fields, so is not shunted into the scalp and cerebrospinal fluid and only affects cells to a depth of 2 cm below the scalp (Eitan 2006; Lisanby 2001a). Spherical model tests have shown that MST generates more focal and superficial stimulations than ECT (Deng 2009; Deng 2011). Due to its superficial and confined stimulation field, MST is thought to have less impact on deeper brain structures (Dwork 2004; Dwork 2009). Physiological findings in rhesus monkeys show that MST, compared to electroconvulsive shock (ECS, equivalence to human ECT), triggered remarkably less marked sympathetic and parasympathetic response (Rowny 2009).
EEG data also show that seizure characteristics in neurophysiology are different between a MST‐induced seizure and an ECS‐induced one. MST and ESC had some crossover in seizure expression, but MST had less marked expression and post‐ictal suppression than ECS (Cycowicz 2008). Further experiments demonstrated a link between ictal expression and cognitive side effects (Cycowicz 2009). Animal studies and human trials have found a positive effect for MST on cognitive functions including less impaired spatial working memory (McClintock 2013), better completion of criteria tasks (Spellman 2008), less acute memory disruption (Polster 2015), and shorter post‐ictal recovery and reorientation times (Kayser 2013) compared to ECS/ECT.
Why it is important to do this review
MST was first used in a study for treating a person with major depression in 2001 (Lisanby 2001a). Since then, an increasing number of studies have examined the antidepressant effect of MST for depression, and the results are promising (Fitzgerald 2013; Hoy 2011; Kayser 2011; Lisanby 2003a) but remain unclear. However, for schizophrenia there is a paucity of evidence. It remains a question whether MST is more or less efficacious than ECT (Allan 2011) or nonconvulsive TMS (Holtzheimer 2006) for schizophrenia and whether MST carries additional effects for people with schizophrenia.
The safety of MST is still being assessed. Noda et al reported a successful MST treatment in an adolescent participant with bipolar depression (Noda 2014). Also, as it has less impact on cognition, MST may be valuable in senior populations (Luber 2013). Currently there is no evidence for the safety of MST specifically for people with schizophrenia.
To our knowledge, to date there has been no systematic review to address the safety and efficacy of MST for schizophrenia. It is important to have good quality evidence for its efficacy and safety that can guide further development of this novel treatment.
Objectives
To estimate the effects of magnetic seizure therapy (MST) alone compared with sham MST or with standard care or any other comparators for schizophrenia.
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 (see Sensitivity analysis). We will exclude quasi‐randomised studies, such as those allocating by alternate days of the week. Where people are given additional treatments within MST, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the MST that is randomised.
There are no restrictions on language or publication status.
Types of participants
Adults, however defined, 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 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).
We will exclude studies in which the psychotic symptoms were caused by definite physical conditions such as cerebral lesions, hyperthyroidism.
Types of interventions
1. Experimental intervention
Magnetic seizure therapy, however defined, performed under general anaesthesia, inducing a seizure by electromagnetic fields (See Background).
The experimental intervention may be:
1.1 Magnetic seizure therapy; or
1.2 Magnetic seizure therapy + standard care.
2. Comparator intervention
Comparators may be one or combination of:
2.1 Placebo (sham MST or wait‐list);
2.2 Antipsychotic medications;
2.3 Electroconvulsive therapy;
2.4 Other physical treatments (e.g. Tai Ji, acupuncture, etc); or
2.5 Psychosocial therapies (e.g. cognitive behavioral therapy, psychoanalysis, art therapy, etc).
Types of outcome measures
We aim to divide outcomes into short term (less than 6 months), medium term (7 to 12 months) and long term (over 1 year).
We will endeavour to report binary outcomes recording clear and clinically meaningful degrees of change (e.g. global impression of much improved, or more than 50% improvement on a rating scale ‐ as defined within the trials) before any others. Thereafter we will list other binary outcomes and then those that are continuous.
Primary outcomes
1. Global state
1.1. Clinically important change ‐ as defined by individual studies (e.g. rated by any validated assessment such as the Clinical Global Impression Scale (CGI) (Guy 1976), the Brief Psychiatric Rating Scale (BPRS) (Overall 1962), the Positive and Negative Syndrome Scale (PANSS) (Kay 1986), or the Hamilton Rating Scale for Depression (HAMD) (Hamilton 1960))
1.2 Relapse ‐ as defined by individual studies
2. Cognitive functioning
2.1 Clinically important change ‐ as defined by individual studies (e.g. rated by any validated assessment such as the NIMH Measurement and Treatment Research to Improve Cognition in Schizophrenia (MATRICS) (Nuechterlein 2008))
3. Adverse effects
3.1 Clinically important adverse effect
Secondary outcomes
1. Global state
1.1 Any change in global state ‐ as defined by individual studies
1.2 Average endpoint/change score global state scale
2. Cognitive functioning
2.1 Any change overall cognitive functioning, as defined by each study
2.2 Average endpoint/change score total mental state scale
3. Adverse effects
3.1 General adverse effects
3.1.1 At least one adverse effect
3.1.2 Clinically important adverse effects
3.1.3 Average endpoint/change scores adverse‐effect scales
3.2 Specific adverse effects
3.2.1 Anticholinergic
3.2.2 Cardiovascular
3.2.3 Central nervous system
3.2.4 Gastrointestinal
3.2.5 Endocrine (e.g. amenorrhoea, galactorrhoea, hyperlipidaemia, hyperglycaemia, hyperinsulinaemia)
3.2.6 Haematology (e.g. haemogram, leukopenia, agranulocytosis/neutropenia)
3.2.7 Hepatitic (e.g. abnormal transaminase, abnormal liver function)
3.2.8 Metabolic
3.2.9 Movement disorders
3.2.10 Various other
4. Mental state
4.1 Overall
4.1.1 Any change overall mental state, as defined by each study
4.1.2 Average endpoint/change score total mental state scale
4.2 Positive symptoms
4.2.1 Clinically important change in positive symptoms, as defined by each study
4.2.2 Any change in positive symptoms, as defined by each study
4.2.3 Average endpoint/change score on total positive mental state subscale
4.3 Negative symptoms
4.3.1 Clinically important change in negative symptoms, as defined by each study
4.3.2 Any change in negative symptoms, as defined by each study
4.3.3 Average endpoint/change score on total negative mental state subscale
4.4 Aggressive symptoms/agitation
4.4.1 Clinically important change in aggressive symptoms/agitation, as defined by each of the studies
4.4.2 Any change in aggressive symptoms/agitation, as defined by each study
4.4.3 Average endpoint/change score on aggressive symptoms/agitation scale
4.5 Depressive symptoms
4.5.1 Clinically important change in depressive symptoms, as defined by each of the studies
4.5.2 Any change in depressive symptoms, as defined by each study
4.5.3 Average endpoint/change score on depressive symptoms scale
4.6 Anxiety symptoms
4.6.1 Clinically important change in anxiety symptoms, as defined by each study
4.6.2 Any change in anxiety symptoms, as defined by each study
4.6.3 Average endpoint/change score on anxiety symptoms scale
5. Quality of life
5.1 Clinically important change quality of life, as defined by each study
5.2. Any change quality of life, as defined by each study
5.3 Average endpoint/change score quality of life scale
6. Satisfaction
6.1. Any change quality of life (patient or carers), as defined by each study
6.2 Average endpoint/change score quality of life scale (patient or carers)
7. Service use
7.1 Hospital admission
7.2 Duration of hospital stay
7.3 Readmission
7.4 Contact with psychiatric services (binary or continuous measures)
8. Social functioning
8.1 Clinically important change in social functioning, as defined by each study
8.2 Any change in social functioning, as defined by each study
8.3 Average endpoint/change score social functioning scale
8.4 Imprisonment (police contact and arrest)
8.5 Employment status (employed/unemployed)
8.6 Accommodation status
8.7 Alcohol use
8.8 Illicit drug use
8.9 Occurrence of violent incidents (to self, others or property)
9. Leaving the study early
9.1 Any reason
9.2 Due to adverse effect
9.3 Due to inefficacy
10. Economic
10.1 Direct costs
10.2 Indirect costs
10.3 Cost effectiveness
'Summary of findings' table
We will use the GRADE approach to interpret findings (Schünemann 2011) and will export data from our review using GRADEpro 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 rated 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: clinically important change, as defined by individual studies.
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Global state: relapse.
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Cognitive functioning: clinically important change, as defined by individual studies.
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Adverse effects: clinically important adverse effect.
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Quality of life: clinically important change, as defined by individual studies.
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Social functioning: clinically important change in social functioning, as defined by each study.
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Leaving the study early: for any reason.
If data are not available for these prespecified outcomes but are available for ones that are similar, we will present the closest outcome to the prespecified one in the table but take this into account when grading the finding.
Search methods for identification of studies
Electronic searches
Cochrane Schizophrenia Group’s study‐based register of trials
The information specialist will search the register using the following search strategy.
(*Magnetic Seizure Therapy*) in Intervention Field of STUDY
In such a study‐based register, searching the major concept retrieves all the synonyms and relevant studies because all the studies have already been organised based on their interventions and linked to the relevant topics.
This register 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’s Module). There are 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 contact the first author of each included study and manufacturers including Magstim in the UK and MagVenture A/S in Denmark for information regarding unpublished trials. We will note the outcome of this contact in the table of included studies or of studies awaiting assessment.
Data collection and analysis
Selection of studies
Two review authors HW and JJ will independently inspect citations from the searches and identify relevant abstracts. Review author CL will independently re‐inspect a random 20% sample of these abstracts to ensure reliability. Where disputes arise, we will acquire the full report for more detailed scrutiny. Review authors HW and JJ will then obtain and inspect full reports of the abstracts or reports meeting the review criteria. Review author CL, again, will re‐inspect a random 20% of these full reports 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 HW and JJ will extract data from all included studies. In addition, to ensure reliability, review author CL will independently extract data from a random sample of these studies, comprising 10% of the total. We will attempt to extract data presented only in graphs and figures whenever possible, but include only if two review authors independently have the same result. If studies are multi‐centre, where possible, we will extract data relevant to each. We will discuss any disagreement and document decisions. If necessary, we will attempt to contact authors through an open‐ended request in order to obtain missing information or for clarification whenever necessary. With remaining problems review author JW will help clarify issues and we will document these final decisions.
2. Management
2.1 Forms
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);
b) the measuring instrument has not been written or modified by one of the trialists for that particular trial; and
c) the instrument provides for a global assessment of an area of functioning and not sub‐scores which are not, in themselves, validated or shown to be reliable. However there are exceptions, we will include sub‐scores from mental state scales measuring positive and negative symptoms of schizophrenia.
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 to primarily use endpoint data, and only use change data if the former are not available. If necessary, we will combine endpoint and change data in the analysis as we prefer to use mean differences (MDs) rather than standardised mean differences (SMDs) throughout (Deeks 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 will apply the following standards to relevant continuous data before inclusion.
Please note, we will enter all relevant data from studies of > 200 participants in the analysis irrespective of the following rules, because skewed data pose less of a problem in large studies. We will also enter all relevant 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. If we find skewed data using the rules below we will not enter these data into analyses but enter as 'other data'.
For endpoint data from studies < 200 participants:
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When a scale starts from the finite number zero, we will subtract the lowest possible value from the mean, and divided this by the standard deviation (SD). If this value is lower than one, it strongly suggests a skew and we will exclude these data. If this ratio is higher than one but below two, there is suggestion of skew. We will enter these data and test whether their inclusion or exclusion would change the results substantially. Finally, if the ratio is larger than two we will include these data, because skew is less likely (Altman 1996; Higgins 2011a).
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If a scale starts from a positive value (such as the Positive and Negative Syndrome Scale (PANSS; Kay 1986) which can have values from 30 to 210), we will modify the calculation described above 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.
2.5 Common measure
To facilitate comparison between trials we intend, if necessary, 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, Overall 1962) or the PANSS (Kay 1986), 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 MST. 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 and note this in the relevant graphs.
Assessment of risk of bias in included studies
Again review authors HW and JJ will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b) to assess trial quality. This set of criteria is based on evidence of associations between overestimate of effect and high risk of bias in domains such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting.
If the raters disagree, we will make the final rating 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 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 both the text of the review, Figure 1, Figure 2, and the Summary of findings table 1.
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 RRs are more intuitive (Boissel 1999) than odds ratios and that odds ratios tend to be interpreted as RRs by clinicians (Deeks 2000). The number needed to treat for an additional beneficial/harmful outcome (NNTB/NNTH) statistic with its CIs 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 MD 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 intraclass 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 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.
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 studies to obtain intra‐class correlation coefficients (ICCs) for their clustered data and to adjust for this by using accepted methods (Gulliford 1999).
We 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 we will assume it 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. This 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, we will present the additional treatment arms in comparisons. If data are binary we will simply add these and combine 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 Systematic Reviews of Interventions (Higgins 2011a). Where the additional treatment arms are not relevant, we will not reproduce 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). If for any particular outcome, more than 50% of data are 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% 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. We will use the rate of those who stay in the study ‐ in that particular arm of the trial ‐ and apply this also to 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 ITT analysis using the above assumptions.
3. Continuous
3.1 Attrition
We will reproduce and use data 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.
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 CIs available for group means, and either P value or t value available for differences in mean, we can calculate them according to the rules described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a): 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 Systematic Reviews of Interventions (Higgins 2011a) present detailed formulae for estimating SDs from P values, t or F values, CIs, ranges or other statistics. If these formula 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 Assumptions about participants who left the trials early or were lost to follow‐up
Various methods are available to account for participants who left the trials early or were lost to follow‐up. Some trials just present the results of study completers, others use the method of last observation carried forward (LOCF), while more recently, methods such as multiple imputation or mixed effects models for repeated measurements (MMRM) have become more of a standard. While the latter methods seem somewhat better than LOCF (Leon 2006), we feel that the high percentage of participants leaving the studies early and differences in the reasons for leaving the studies early between groups is often the core problem in randomised schizophrenia trials. We will therefore not exclude studies based on the statistical approach used. However, we will preferably use the more sophisticated approaches, e.g. we will prefer MMRM or multiple imputation to LOCF and we will only present completer analyses if some kind of ITT data are not available at all. Moreover, we will address this issue in the item 'incomplete outcome data' of the 'Risk of bias' tool.
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 and discuss such situations or participant groups.
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 and discuss any such methodological outliers.
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 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). We will interpret an I2 estimate greater than or equal to around 50%, accompanied by a statistically significant Chi2 statistic, as evidence of substantial levels of heterogeneity (section 9.5.2 Cochrane Handbook for Systematic Reviews of Interventions) (Deeks 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 10.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Sterne 2011).
1. Protocol versus full study
We will try to locate protocols of included randomised trials. If the protocol is available, we will compare outcomes in the protocol and in the published report. If the protocol is not available, we will compare outcomes listed in the methods section of the trial report with actually reported results.
2. Funnel plot
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 ten or fewer studies, or where all studies are of similar size. 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 choose to use the fixed‐effect model for all analyses.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1 Primary outcomes
We hope to be able to perform subgroup analyses on dose or frequency of MST, type and shape of coils, and placement of coils if enough data are gathered.
2. Investigation of heterogeneity
We will report if inconsistency is high. First we will investigate whether data have been entered correctly. Second, if data are correct, we will visually inspect the graph and we will successively remove studies outside of the company of the rest 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 data. If not, we will not pool these data and will discuss any 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
If there are substantial differences in the direction or precision of effect estimates in any of the sensitivity analyses listed below, we will not add data from the lower‐quality studies to the results of the higher‐quality trials, but will present these data within a subcategory. If their inclusion does not result in a substantive difference, they will remain in the analyses.
1. Implication of randomisation
If trials are described in some way as to imply randomisation, for the primary outcomes, we will pool data from the implied trials with trials that are clearly randomised.
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 compared with completer data only. If there is a substantial difference, we will report results and discuss them but continue to employ our assumption.
Where assumptions have to be made regarding missing SDs (see Dealing with missing data), we will compare the findings on primary outcomes when we use our assumption compared with completer data only. We will undertake a sensitivity analysis testing how prone results are to change when 'completer' 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 continue to employ our assumption.
3. Risk of bias
We will analyse the effects of excluding trials that are at high risk of bias across one or more of the domains (see Assessment of risk of bias in included studies) for the meta‐analysis of the primary outcome.
4. Imputed values
We will also undertake a sensitivity analysis to assess the effects of including data from trials where we use imputed values for ICC in calculating the design effect in cluster randomised trials.
5. Fixed‐effect and random‐effects models
We will synthesise 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.
