Pharmacological interventions for prevention of weight gain in people with schizophrenia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To determine the effects of pharmacological interventions for preventing weight gain in people with schizophrenia.
Background
Description of the condition
Schizophrenia and weight gain
Schizophrenia is a complex and severe neuropsychiatric disorder characterised by delusions, hallucinations, disorganised behaviour and progressive cognitive deficits (Keshavan 2008; van Os 2009). It is also a heterogeneous disorder with psychopathology varying across patients and over the course of the illness (Seaton 2001). The onset is typically in the late adolescence or early adulthood and is marked by episodes of psychosis and severe functional disability (Liversedge 2011). The complexity, phenotypic heterogeneity, and the polygenic nature of the genetic risk for schizophrenia make it a challenge to treat and investigate, and the etiopathogenesis (the cause and development of a disease or abnormal condition) of schizophrenia is yet to be understood fully (Keshavan 2011). The severity of the disability and lack of knowledge into its aetiology makes it the most disabling among all psychiatric disorders requiring a disproportionate share of mental health services (Mueser 2004); it is the costliest among severe mental disorders in terms of human suffering and expenditure incurred by the society (van Os 2009). The disability and cost to the society are compounded by the common presence of comorbid obesity in this population, a problem that has been exacerbated more recently with the increased use of second‐generation antipsychotics, many of which are associated with the risk of weight gain and metabolic disturbances such as diabetes and the metabolic syndrome (Allison 1999; Casey 2004; De Hert 2011; Homel 2002; Rajkumar 2017).
The World Health Organization (WHO) defines overweight and obesity as an 'abnormal or excessive fat accumulation that may impair health'. A person who has a body mass index (BMI) of over 25 is overweight and those with a BMI of over 30 are obese (WHO 2013). The prevalence of obesity in people with schizophrenia has been reported to be anywhere from 1.5 times to 4 times higher than the general population (ADA/APA 2004; Coodin 2001; Gurpegui 2012; Silverstone 1988); the risk may be even higher for long‐term inpatients (Ringen 2018). For people with schizophrenia, there is a marked increase in standardised mortality ratios for both natural and unnatural causes of death and much of this increment may be attributed to the increased prevalence of coronary heart disease risk (Cohn 2004; Goff 2005; Henderson 2005; Mackin 2005; Saari 2005; Westman 2017), and related obesity in this population (Annamalai 2017; Coodin 2001; Daumit 2003; Susce 2005). Obesity doubles the risk of all‐cause mortality, coronary heart disease, stroke and type 2 diabetes, increases the risk of some cancers, musculoskeletal problems and loss of function, and carries negative psychological consequences (DoH 2004). Being an obese or overweight adult is associated with increases in early mortality and large decreases in life expectancy, and these decreases are similar to those seen with smoking (Peeters 2003). The significance and recognition of this prevalence and its impact on premature mortality and morbidity has led to the development of consensus statements (ADA/APA 2004; De Nayer 2005) and guidelines (Cooper 2016) on its management. Despite this, evidence from a systematic review suggests that the all‐cause standardised mortality ratio between persons with schizophrenia and general population has risen steadily since the 1970s (Saha 2007). In stark contrast to the well‐recognised risk of metabolic comorbidity in schizophrenia, studies have repeatedly shown extremely low rates of intervention for these risk factors (De Hert 2011; Lappin 2018). Extremely low of intervention for what would be considered 'modifiable" cardiovascular risk factors is also apparent in young, first‐episode populations (Correll 2014). In turn, a concurrent body of literature suggests that metabolic risk is accrued early on in illness (De Hert 2006; Ward 2015), later shaving off 15 to 20 years of life (due to cardiovascular disease) (Hoang 2011;Newcomer 2007).
Beyond effects on cardiovascular morbidity and mortality, growing evidence in non‐psychiatric populations also suggests that obesity can be associated with structural brain changes, brain perfusion changes and cognitive deficits (Jagust 2007; Sellbom 2012), with observations supporting some similarities to those noted in schizophrenia (Reichenberg 2007). The clinical implications of being overweight or obese on cognitive function in addition to the deficits observed in schizophrenia, remains a relatively unexplored area of research. Emerging evidence has linked cognitive impairment in schizophrenia to metabolic dysfunction (Bora 2017; Friedman 2010; Lindenmayer 2012), which might in turn might suggest that interventions to reduce obesity and cardio‐metabolic risk could have dual salutary benefits on cardiovascular outcomes and illness‐related functional disability. Quality of life is further reduced for people with schizophrenia with a high BMI (Bueno‐Antequera 2018; Faulkner 2007a; Kurzthaler 2001; Strassnig 2003) and those gaining weight (Allison 2003). Furthermore, Weiden and colleagues (Weiden 2004) reported a significant, positive association between obesity, subjective distress from weight gain and medication non‐compliance in a sample of people with schizophrenia. People with schizophrenia face the combined challenges of living with the illness, and for many, additional obesity and related illnesses. This combination is a major public health problem (Bueno‐Antequera 2018; Wirshing 2004) and carries considerable human cost. Recognition of this has led to growing concern with how best to intervene (Birt 2003; Bueno‐Antequera 2018; Catapana 2004; Cooper 2016; Green 2000; Le Fevre 2001; Osborn 2001).
Mechanisms of weight gain in schizophrenia
To date, there is no consensus on what pharmacological factors may be involved in this weight gain particularly regarding the newer antipsychotics. As reviewed elsewhere (Ananth 2004; Jin 2008; Reynolds 2010; Reynolds 2017), a range of potential weight‐inducing mechanisms such as dopaminergic blockage; increased appetite due to the interaction of antipsychotic medication with dopamine, serotonin, and histamine neuronal receptors; increased leptin; and increases in systemic levels of various cytokines and soluble cytokine receptors could be implicated. Whether gender influences antipsychotic‐related weight gain susceptibility remains a topic of debate; while there are clinical data suggesting that women may be more susceptible to atypical antipsychotic‐associated weight gain (Aichhorn 2007; Gebhardt 2009), others have failed to demonstrate this (Basson 2001; Ratzoni 2002). The weight gain story may be further complicated through genetic and/or epigenetic mechanisms, which may modulate risk. In this regard, among others, dopamine, serotonin, and leptin gene polymorphisms have emerged as genetic candidates for antipsychotic‐related cardio‐metabolic side effects (Correll 2011). In addition, it is important to note that obesity was commonly reported before antipsychotics were widely introduced (Baptista 2002). Compared to the general population, people with schizophrenia also have a poor diet (Dipasquale 2013; McCreadie 1998; Strassnig 2003) and a physically inactive lifestyle (Brown 1999; Cohn 2004; Daumit 2005; Vancampfort 2017) and these lifestyle factors will contribute to weight gain. However, pharmacological intervention strategies may still treat or minimise weight gain associated with poor lifestyle.
Description of the intervention
Pharmacological agents that have been approved for weight loss in the general population, and other medications that may suppress appetite, increase satiety, or increase thermogenesis have been studied to prevent weight gain in people with schizophrenia. These include metformin, topiramate, H2 antagonists such as famotidine and nizatidine, and antidepressants such as fluoxetine and reboxetine. Most clinical trials have been between six and 12 weeks long. Very few have been for 24 weeks or longer. However, clear evidence regarding the optimal duration of such interventions is lacking (Cooper 2016).
Metformin is a biguanide and is a first‐line anti‐diabetic agent. It is usually administered in a dose ranging from 500 mg to 2500 mg and is usually administered in divided doses twice a day. Topiramate is an anticonvulsant that has recently approved by the Food and Drug Administration (FDA) in combination with phentermine for weight loss. The dose ranges from 100 mg to 200 mg given in divided doses twice a day. Famotidine (20 mg to 40 mg once a day) and nizatidine (150 mg to 300 mg once a day) are both commonly used in the treatment of peptic ulcer disease and gastroesophageal reflux disease as they block the histamine H2 receptor. Fluoxetine (20 mg once a day) and reboxetine (4 mg once a day) are antidepressants that have also been investigated for their weight loss promoting properties. Reboxetine is a norepinephrine reuptake inhibitor approved as an antidepressant in parts of Europe. Loss of appetite is a side effect of this medication prompting investigation as a weight loss agent. More recently, samidorphan, an opioid modulator that preferentially antagonises the μ‐opioid receptor is being investigated for preventing antipsychotic‐induced weight gain (Silverman 2018). It is taken orally, the usual dose is 5 mg/day. Common side effects include nausea, sedation and dizziness.
How the intervention might work
Pharmacological interventions may operate on a range of potential mechanisms such as suppressing appetite, increasing satiety, or increasing thermogenesis by modifying central nervous system neurotransmission of norepinephrine, dopamine and serotonin.
Metformin lowers liver glucose production and improves whole‐body insulin sensitivity. It has variably been associated with weight loss in non‐psychiatrically ill populations, and may prevent continual weight gain while improving insulin resistance (Hundal 2003). Hence,it is commonly understood as an peripheral insulin sensitiser. Suppression of appetite is seen commonly with topiramate and may occur by GABA‐mediated mechanisms in the central nervous system (Velazquez 2018). With respect to H2 receptor antagonists, it is unclear whether the weight loss action is a direct result of gastric histamine receptor antagonism or if other factors play a role. Histamine is known to mediate leptin action and is involved in energy and feeding regulation (Lett 2012). H2 receptor antagonists can therefore plausibly interact with these medicators to effect weight loss. Fluoxetine and nizatidine modify central nervous system neurotransmission of norepinephrine and serotonin impacting weight. Early studies had shown serotonin blockade to be an effective anorectic strategy (Goldstein 1994) that stimulated interest in studying these agents as weight loss medications.
At the organism level, preventing weight gain avoids all the negative outcomes associated with weight gain and may help engender a healthy lifestyle. Furthermore, sustained changes in health behaviours as a result of such interventions may reduce risk of mortality and morbidity independent of any weight loss (Wei 1999). Indeed, prevention of weight gain has been an area of active enquiry and both older interventions such as metformin (de Silva 2016) and newer molecules such as samidorphan may be useful in achieving this goal (Silverman 2018).
Why it is important to do this review
In the seminal meta‐analysis highlighting atypical‐antipsychotic related weight gain, every antipsychotic medication except ziprasidone and molindone were associated with some degree of weight increase after just 10 weeks of treatment (Allison 1999). The effects were greatest with olanzapine and clozapine which increased body weight by approximately 4 kg to 4.5 kg, followed by risperidone (mean weight gain 2 kg). Notably, these data were assembled from chronic populations characterised by many years of exposure to medications and illness‐related effects. What has become clearer is that factors related to illness chronicity likely result in an underestimation of the impact of antipsychotics on weight gain, and an overestimation of differences between agents. Collectively, data involving both short‐term and long‐term evidence comparing olanzapine or risperidone in chronic patients to those experiencing a first episode, demonstrate a three to four times larger magnitude of weight gain in those early on in the illness (Alvarez‐Jimenez 2008). Furthermore, no antipsychotic medication appears to be devoid of weight gain risk in patients with little prior antipsychotic exposure. For example, one 12‐week cohort study enrolling antipsychotic‐naive youth assigned to aripiprazole, quetiapine or olanzapine, demonstrated substantial weight gain not only with olanzapine (average 8.5 kg), but also with risperidone, quetiapine as well as aripiprazole (average 4.4 kg; Correll 2009). These findings have since been replicated, including in a recent meta‐analysis (Bak 2014). Interestingly, data in previously medication‐unexposed individuals also suggests that agents classified as being metabolically neutral may exhibit a more delayed onset of weight gain, with treatments differing by pattern, and not always the final amount of weight increase (Findling 2010; Perez‐Iglesias 2008; Zipursky 2005). Morover, results from a nation‐wide register‐based analysis suggest that all antipsychotics contribute to the risk of diabetes, independently of class (Rajkumar 2017). Obesity is also one of the most important risk factor for the development of dyslipidaemia, diabetes, cardiovascular diseases, leading to premature death (Alberti 2009). Taken together, these emerging data highlight the susceptibility, particularly of first‐episode patients, to antipsychotic‐related weight gain.This highlights the case for implementing early effective strategies to prevent or decrease metabolic risk accrual which may occur early in the treatment of the illness (Ward 2015).
We believe there is a sufficient volume of material to split the previous Cochrane Review (Faulkner 2007) into separate reviews focusing on behavioural and pharmacological interventions independently. Furthermore, given the vast number of pharmacological interventions tried for prevention and treatment of weight gain, we have chosen to split the review on pharmacological interventions to focus on prevention and treatment of weight gain in separate reviews. The current review focuses on pharmacological interventions for the prevention of weight gain. While previous studies have systematically analysed the role of metformin in preventing weight gain (de Silva 2016), no systematic review examining all available pharmacological interventions in a preventive role has been published. This is important as what we consider effective treatments for adult obesity produce modest weight loss (approximately 2 kg to 5 kg) compared to no treatment or usual care. While this degree of weight loss may have a meaningful impact, it is not sufficient to reverse the weight increases associated with antipsychotic treatment (e.g. average 8.5 kg increase in antipsychotic naive patients starting olanzapine Correll 2009). In this regard, prevention strategies may represent the most useful strategy. We are interested in identifying and including all randomised controlled trials (RCTs) of pharmacological agents to prevent weight gain, regardless of aetiology, in all people with schizophrenia or schizophrenia‐like illnesses.
Objectives
To determine the effects of pharmacological interventions for preventing weight gain in people with schizophrenia.
Methods
Criteria for considering studies for this review
Types of studies
We will consider all relevant randomised controlled trials (RCTs). We will include RCTs meeting our inclusion criteria and reporting useable data. We will consider trials that are described as 'double‐blind' ‐ in which randomisation is implied ‐ and include or exclude once we have carried out a sensitivity analysis (see Sensitivity analysis). We will exclude quasi‐randomised studies, such as those that allocate intervention by alternate days of the week. Where people are given additional treatments as well as pharmacological strategies for preventing weight gain, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the pharmacological strategy for preventing weight gain that is randomised.
Types of participants
People diagnosed with schizophrenia or schizophrenia‐like illnesses (such as schizoaffective disorder, schizophreniform disorder, and delusional disorder) using any diagnostic criteria irrespective of age, nationality or sex of participants. We will include trials regardless of the length of the participant's illness, stage of illness, treatment setting, current clinical state, or symptom cluster.
We are interested in making sure that information is as relevant as possible to the current care of people with schizophrenia, so aim to highlight the current clinical state clearly (acute, early post‐acute, partial remission, remission), as well as the stage (prodromal, first episode, early illness, persistent), and whether the studies primarily focused on people with particular problems (for example, negative symptoms, treatment‐resistant illnesses).
Types of interventions
1. Pharmacological intervention for preventing weight gain
Pharmacological interventions for preventing weight gain. For people with schizophrenia these 'weight prevention' interventions are typically 'adjunctive' (add‐on) interventions to other ongoing routinely prescribed medications such as antipsychotics.
We will consider all types of pharmacological interventions for preventing weight gain, these can include those currently licensed for weight loss, an off‐label therapy, withdrawn from the market, or an isolated nutritive supplement.
2. Standard care
We define this as care that the participants receive in the placebo arm of the research trial. This would include regular visits with the psychiatrist, continuing antipsychotic medications, and lifestyle and/or diet advice as mentioned in individual studies.
3. Other behavioural interventions
We will consider an intervention where an additional pharmacological intervention is combined with a behavioural intervention (i.e. diet and/or exercise). We will only consider interventions that compare such a combined intervention strategy with a behavioural intervention alone in order to assess the additive effect of using a pharmacological adjunct.
Types of outcome measures
If possible, we aim to divide all outcomes into short term (less than six months), medium term (seven to 12 months) and long term (over 12 months).
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.
* For types of scales we will extract data from please see (Data extraction and management)
For outcomes such as ‘clinically important change’, ‘any change’, ‘relapse’ we will use the definition used by each of the trials.
Primary outcomes
1. Weight (or another indicator of body mass e.g. body mass index (BMI), waist measurement, waist‐to‐hip ratio)
1.1 Clinically important change in weight
1.2 Clinically important change in BMI
2. Leaving the study early
2.1 For any reason
3. Compliance with treatment ‐ as defined by individual studies
4. Adverse effect/events
4.1 Specific
4.1.1 Gastrointestinal effects: nausea
Secondary outcomes
1. Weight (or another indicator of body mass e.g. body mass index (BMI), waist measurement, waist‐to‐hip ratio)
1.1 Any change in body weight
1.2 Any change in BMI
1.3 Clinically important change in waist circumference (as defined by individual studies)
1.4 Any change in waist circumference
1.5 Clinically important change in waist‐to‐hip circumference ratio (as defined by individual studies)
1.6 Any change in waist‐to‐hip circumference ratio
1.7 Clinically important change in percentage body fat
1.8 Any change in percentage body fat
2. Leaving the study early
2.1 For specific reason
3. Global state
3.1 Clinically important change in global state (as defined by individual studies)
3.2 Any change in global state
3.3 Average endpoint/change score on global state scale
4. Mental state
4.1. Clinically important change in general mental state
4.2. Any change in general mental state
4.3. Average endpoint/change score on mental state scale
5. Well‐being
5.1 Clinically important change in well‐being
5.2 Any change in well‐being
5.3 Average endpoint/change score on well‐being scale
6. Quality of life
6.1 Clinically important change in quality of life
6.2 Any change in quality of life
6.3 Average endpoint/change score on quality of life scale
7. Adverse effects/event ‐ general or specific
7.1 General
7.1.1 At least one adverse effect/event
7.1.2 Average endpoint/change score on general adverse effect scale
7.2 Specific
7.2.1 Clinically important specific adverse effects (e.g. cardiovascular, gastrointestinal)
7.2.2 Death ‐ suicide and natural causes
8. Physiological
8.1 Cardiovascular measures
8.2 Laboratory measures
9. Economic
9.1 Direct costs
9.2 Indirect costs
'Summary of findings' table
We will use the GRADE approach to interpret findings (Schünemann 2011); and will use GRADEpro GDT to export data from our review to create a 'Summary of findings' table . These tables provide outcome‐specific information concerning the overall certainty 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.
-
Weight: clinically important change in weight
-
Weight: clinically important change in BMI
-
Weight: waist circumference: clinically important change in waist circumference
-
Quality of life: clinically important change in quality of life
-
Adverse effect: nausea
-
Leaving the study early: for any reason
-
Compliance with treatment
If data are not available for these pre‐specified outdoes but are available for ones that are similar, we will present the closest outcome to the pre‐specified 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.
(*{Pharm}* in Intervention) AND (*Weight Gain* in Health Care Condition) of STUDY
In such 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 (Shokraneh 2017; Shokraneh 2018).
This register is compiled by systematic searches of major resources (CENTRAL, CINAHL, ClinicalTrials.Gov, Embase, MEDLINE, PsycINFO, PubMed, WHO ICTRP) and their monthly updates, ProQuest Dissertations and Theses A&I and its quarterly update, Chinese databases (CBM, CNKI, and Wanfang) and their annual updates, handsearches, grey literature, and conference proceedings (see Group's website). 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 contact the first author of each included study for information regarding unpublished trials. We will note the outcome of this contact in the 'Included studies' or 'Studies awaiting classification' tables.
Data collection and analysis
Selection of studies
Review authors SMA and ZA will independently inspect citations from the searches and identify relevant abstracts; MH will independently re‐inspect a random 20% sample of these abstracts to ensure reliability of selection. Where disputes arise, we will acquire the full report for more detailed scrutiny. ZA will then obtain and inspect full reports of the abstracts or reports meeting the review criteria. SMA will re‐inspect a random 20% of these full reports in order to ensure reliability of selection. Where it is not possible to resolve disagreement by discussion, we will attempt to contact the authors of the study concerned for clarification.
Data extraction and management
1. Extraction
Review authors MD, ZA, and JL will extract data from all included studies. In addition, to ensure reliability, SMA 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 will include only if two review authors independently obtain the same result. If studies are multi‐centre, then where possible we will extract data relevant to each. We will discuss any disagreement and document our decisions. If necessary, we will attempt to contact study authors through an open‐ended request in order to obtain missing information or for clarification. MH will help clarify issues regarding any remaining problems and we will document these final decisions.
2. Management
2.1 Forms
We will extract data onto standard, pre‐designed, 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 should be 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; however, calculation of change needs two assessments (baseline and endpoint) that can be difficult to obtain 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. 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.
For endpoint data from studies including fewer than 200 participants:
a) when a scale starts from the finite number zero, we will subtract the lowest possible value from the mean, and divide this by the standard deviation (SD). If this value is lower than one, it strongly suggests that the data are skewed and we will exclude these data. If this ratio is higher than one but less than two, there is suggestion that the data are skewed: we will enter these data and test whether their inclusion or exclusion would change the results substantially. If such data change results we will enter these as 'other data'. Finally, if the ratio is larger than two we will include these data, because it is less likely that they are skewed (Altman 1996; Higgins 2011a).
b) 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 the scale starting point into account. In these cases skewed data are present if 2 SD > (S − S min), where S is the mean score and 'S min' is the minimum score.
Please note: we will enter all relevant data from studies of more than 200 participants in the analysis irrespective of the above 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 or not data are skewed.
2.5 Common measurement
To facilitate comparison between trials we aim, where relevant, 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 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 pharmacological intervention for prevention of weight gain. 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
Review authors SMA and ZA will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systematic Reviews of Interventions to assess trial quality (Higgins 2011b). This set of criteria is based on evidence of associations between potential overestimation of effect and the level of risk of bias of the article that may be due to aspects of sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting, or the way in which these 'domains' are reported.
If the raters disagree, we will make the final rating by consensus. 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 regarding the category to which a trial is to be allocated, we will resolve this 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/s.
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), as it has been shown that RR is more intuitive than odds ratios (Boissel 1999); and that odds ratios tend to be interpreted as RRs by clinicians (Deeks 2000). Although the number needed to treat for an additional beneficial outcome (NNTB) and the number needed to treat for an additional harmful outcome (NNTH), with their CIs, are intuitively attractive to clinicians, they are problematic to calculate and interpret in meta‐analyses (Hutton 2009). For binary data presented in the 'Summary of findings' table/s we will, where possible, 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. Authors often fail to account for intra‐class correlation in clustered studies, leading to a unit‐of‐analysis error whereby P values are spuriously low, CIs unduly narrow and statistical significance overestimated (Divine 1992). 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 sought statistical advice and have been advised that the binary data from cluster trials 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) thus 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 and taken ICCs and relevant data documented in the report into account, 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, participants can differ significantly from their initial state at entry to the second phase, 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 carry‐over and unstable conditions are very likely in severe mental illness, we will only use data from 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 the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). Where 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). 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 the 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 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
We will 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
If standard deviations (SDs) are not reported, we will try to obtain the missing values from the authors. If these are 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 SDs 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 * √(n). The Cochrane Handbook for Systematic Reviews of Interventions presents detailed formulae for estimating SDs from P, t or F values, CIs, ranges or other statistics (Higgins 2011a). 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. Nevertheless, we will examine the validity of the imputations in a sensitivity analysis that excludes 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 to be somewhat better than LOCF (Leon 2006), we feel that the high percentage of participants leaving the studies early and differences between groups in their reasons for doing so is often the core problem in randomised schizophrenia trials. We will therefore not exclude studies based on the statistical approach used. However, by preference we will use the more sophisticated approaches, i.e. we will prefer to use 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 participants who are clearly outliers or situations that we had not predicted would arise and, where found, 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 inspect graphs visually 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 Chi² P value. 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 the magnitude and direction of effects as well as the strength of evidence for heterogeneity (e.g. P value from Chi² test, or a confidence interval for I²). We will interpret an I² estimate greater than or equal to 50% and accompanied by a statistically significant Chi² statistic as evidence of substantial heterogeneity (Chapter 9. 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 Systemic 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 10 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 a random‐effects model for all analyses.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1 Primary outcomes
No subgroup analysis of primary outcomes is anticipated.
2. Investigation of heterogeneity
We will report if inconsistency is high. Firstly, we will investigate whether data have been entered correctly. Secondly, if data are correct, we will inspect the graph visually and remove outlying studies successively 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 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 is 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
We will carry out sensitivity analyses for primary outcomes only. 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, we will compare data from the implied trials with trials that are 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 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.
3. Assumptions for lost continuous data
Where assumptions have to be made regarding missing SDs (see Dealing with missing data), we will compare the findings when we use our assumption compared with data that are not imputed. If there is a substantial difference, we will report results and discuss them but continue to employ our assumption.
4. 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).
5. 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.
6. Fixed‐ and random‐effects
We will synthesise data using a random‐effects model; however, we will also synthesise data for the primary outcome using fixed‐effect model to evaluate whether this alters the significance of the results.
