Olanzapine discontinuation for schizophrenia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To investigate the effects of discontinuing olanzapine in people with schizophrenia.
Background
Description of the condition
Schizophrenia, with a life‐time prevalence of about 1% (Jablensky 1992) and an annual incidence averaging about 15 people per 100,000 (Tandon 2008), is often a chronic psychiatric disorder. The typical manifestations are positive symptoms such as fixed, false beliefs (delusions) and perceptions without cause (hallucinations), negative symptoms such as apathy and lack of drive, disorganisation of behaviour and thought, and catatonic symptoms such as mannerisms and bizarre posturing (Carpenter 1994).
As a major cause of disability among adults, schizophrenia compromises people's social and occupational functions (Carpenter 2003). Recent European estimates of employment rates in this group range from 8% to 35% (Marvaha 2007). The mortality rate among people with schizophrenia is high and the incidence of suicide is about 10% (Meltzer 1995).
Description of the intervention
Olanzapine is an established antipsychotic drug for schizophrenia and related disorders (Bhana 2001). It remains one of the more expensive newer drugs, earning Eli Lilly $4.7Bn in 2008 (Eli Lilly 2009). Studies tend to concentrate on instigation of the drug rather than its discontinuation, yet stopping medication is an almost unavoidable part of treatment of schizophrenia. The latter may occur because of patient preference, cost, access to treatment, or clinical indications such as adverse effects or doubt about the need for treatment over a protracted period of time. There are several possibilities how cessation could occur. Medication could be withdrawn abruptly, by slow titration, or by switching to other treatments.
How the intervention might work
Olanzapine is similar to clozapine in structure (Figure 1; Figure 2), but has a higher affinity for 5‐HT2 serotonin receptors than D2 dopamine receptors. It also antagonises H1 histamine receptors, causing sedation; this may also be the reason for weight gain. It seems as effective as other antipsychotic drugs (Belgamwar 2005; Duggan 2005; Komossa 2010) and has adverse effects such as weight gain, somnolence, dizziness, anticholinergic effects (constipation and dry mouth) and transient asymptomatic liver enzyme elevations. Since there is some evidence that 5HT2 antagonists are useful for the treatment of negative symptoms of schizophrenia (Tamminga 1998) and dopamine D2 receptors have, for a long time, been the linchpin of treatment of the so called 'positive' symptoms of schizophrenia (Seeman 2010), the efficacy of olanzapine is thought to be mediated through combined antagonism of these two receptor sites.
Olanzapine structure
Olanzapine structure‐2
Why it is important to do this review
Among people who have started antipsychotic treatment, relapse of psychosis is highly associated with discontinuation of antipsychotic medication (Gilbert 1995). Even decreasing olanzapine dose was found to be a significant predicting factor of relapse in patients with schizophrenia (Lipkovich 2007; Rouillon 2008). However, the benefit of antipsychotic treatment in relapse prevention is offset by their risk of troubling, sometimes life‐shortening adverse effects (Muench 2010). Sixty‐four percent of those assigned to olanzapine show discontinuation owing to intolerable side effects or inefficacy (Lieberman 2005).
People instigated on any antipsychotic drug ‐ including olanzapine ‐ will, at some time or another, wish or need to stop the drug. This review will provide healthcare professionals with the best available evidence of the effects of olanzapine discontinuation in people with schizophrenia.
Objectives
To investigate the effects of discontinuing olanzapine in people with schizophrenia.
Methods
Criteria for considering studies for this review
Types of studies
We will include all relevant randomised controlled trials (RCTs). Where a trial is described as 'double‐blind' but it is implied that the study is randomised, we will include these trials in a sensitivity analysis. If there is no substantive difference within primary outcomes, we will add these 'implied randomisation' studies, then include these in the final analysis. If there is a substantive difference, we will only use clearly randomised trials and will describe the results of the sensitivity analysis in the text. We will exclude all quasi‐randomised studies, such as those allocating by using alternate days of the week or surname of the patient.
Types of participants
Participants will be people of any age or gender with schizophrenia diagnosed by any criteria. Trials may include participants with any length of illness who are being treated with olanzapine.
Types of interventions
1. Withdrawal of olanzapine
It is feasible that the withdrawal of olanzapine could be done by different techniques. We do propose to find the overall effects of withdrawal but also to present the data in such a way that each technique is considered separately and compared with other techniques.
a. Abrupt cessation
b. Tapering off
c. Switching to another medication
2. Continuation of olanzapine
Types of outcome measures
We will analyse outcomes for different lengths of follow‐up: up to three months, six months, or more than six months.
Primary outcomes
1. Global state
1.1 Time to relapse
1.2 Clinically important change in global state
1.3 Any change in global state
1.4 Average endpoint global state score
1.5 Average change in global state scores
2. Death ‐ suicide or natural causes
3. Leaving the study early
Secondary outcomes
1. Service use outcomes
1.1 Time to hospitalisation
1.2 Days in hospital
1.3 Change in hospital status
2. Mental state
2.1 Clinically important change in mental state
2.2 Any change in mental state
2.3 Average endpoint mental state score
2.4 Average change in mental state scores
2.5 Clinically important change in specific aspects of mental state
2.6 Any change in specific aspects of mental state
2.7 Average endpoint specific aspects of mental state
2.8 Average change in specific aspects of mental state
3. Adverse effects
3.1 General
3.1.1 Clinically important adverse effect ‐ as defined by individual studies
3.1.2 Any change
3.1.3 Average score
3.2 Specific
3.2.1 Death (suicide and non‐suicide)
3.2.2 Central nervous system
3.2.3 Somnolence
3.2.4 Extrapyramidal reactions
3.2.5 Insomnia
3.2.6 Dizziness
3.2.7 Gastrointestinal
3.2.8 Dyspepsia
3.2.9 Constipation
3.2.10 Weight gain
3.2.11 Musckuloskeletal
3.2.12 Weakness
3.2.13 Other various effects
4. Behaviour
4.1 Clinically important change in general behaviour
4.2 Any change in general behaviour
4.3 Average endpoint general behaviour score
4.4 Average change in general behaviour scores
4.5 Clinically important change in specific aspects of behaviour
4.6 Any change in specific aspects of behaviour
4.7 Average endpoint specific aspects of behaviour
4.8 Average change in specific aspects of behaviour
5. Social functioning
5.1 Clinically important change in general functioning
5.2 Any change in general functioning
5.3 Average endpoint general functioning score
5.4 Average change in general functioning scores
5.5 Clinically important change in specific aspects of functioning, such as social or life skills
5.6 Any change in specific aspects of functioning, such as social or life skills
5.7 Average endpoint specific aspects of functioning, such as social or life skills
5.8 Average change in specific aspects of functioning, such as social or life skills
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 quality of life score
6.4 Average change in quality of life scores
6.5 Clinically important change in specific aspects of quality of life
6.6 Any change in specific aspects of quality of life
6.7 Average endpoint specific aspects of quality of life
6.8 Average change in specific aspects of quality of life
7. Satisfaction with care for either recipients of care or carers
7.1 Recipient of care satisfied with treatment
7.2 Recipient of care average satisfaction score
7.3 Recipient of care average change in satisfaction scores
7.4 Carer satisfied with treatment
7.5 Carer average satisfaction score
7.6 Carer average change in satisfaction scores
8. Economic
8.1 Direct costs
8.2 Indirect costs
Search methods for identification of studies
We will apply no language restrictions within the limitations of the search.
Electronic searches
Cochrane Schizophrenia Group Trials Register
We will search the register using the phrase:
((cessation* or withdr?w* or discontinu* or halt* or stop* or drop?out* or dropout* or rehospitalis* or relaps* or maintain* or maintenance* or recur* in title, abstract, index terms of REFERENCE) or (withdrawal* in interventions of STUDY)) AND (*olanz* OR *zyprex* OR *LY?170053* OR *LY?170052* OR *lanzac* OR *olansek* OR *zydis* or *zypadhera* in interventions of STUDY)].
This register is compiled by systematic searches of major databases, hand searches and conference proceedings (see group module).
Searching other resources
1. Reference searching
We will inspect references of all included studies for more trials.
2. Personal contact
We will contact the first author of each included study for missing information and for the existence of further studies.
3. Drug companies
We will contact the original manufacturers of olanzapine and ask them for further relevant studies and for missing information on identified studies.
Data collection and analysis
We will perform the review and meta‐analyses following the recommendations of The Cochrane Collaboration (Higgins 2011). We will perform the analyses using Review Manager 5.1 (Review Manager).
Selection of studies
FA and GMB will independently inspect citations from the searches and identify relevant abstracts. OA and GA will independently re‐inspect a random 20% sample of these citations to ensure reliability. FA and GB will obtain and inspect full reports of the abstracts meeting the review criteria, plus the citations reviewers disagree on. Again, OA and GA will independently re‐inspect a random 20% of these full abstracts 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 author FA and GMB will extract data from all included studies. In addition, to ensure reliability, OA will independently extract data from a random sample of these studies, comprising 10% of the total. Again, we will discuss any disagreement, document decisions and, if necessary, contact authors of studies for clarification. With remaining problems, CEA will help clarify issues and we will document these final decisions. We will extract data presented only in graphs and figures whenever possible, but include only if two authors independently reach the same result. We will attempt to contact authors through an open‐ended request in order to obtain missing information.
If studies are multi‐centre, where possible, we will extract data relevant to each component centre separately.
2. Management
2.1 Forms
We will use a standardised template of data collection form to extract data on methods, participants, interventions, and outcomes as listed above.
2.2 Scale‐derived data
2.2.1 Valid measures
We will include continuous data from rating scales only if: a. the psychometric properties of the measuring instrument have been described in a peer‐reviewed journal (Marshall 2000); and b. the measuring instrument has not been written or modified by one of the trialists for that particular trial. The data should be some estimation of a total score rather than sub‐scores. Ideally, the measuring instrument should either be i. a self‐report or ii. completed by an independent rater or relative (not the therapist).
2.2.2 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 (MD) rather than standardised mean differences (SMD) throughout (Higgins 2011, Chapter 9.4.5.2).
2.3 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).
2.4 Skewed data
Continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non‐parametric data, we aim to apply the following standards to all data before inclusion: a) standard deviations and means are reported in the paper or obtainable from the authors; b) when a scale starts from the finite number zero, the standard deviation, when multiplied by two, is less than the mean (as otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution (Altman 1996); c) if a scale starts from a positive value (such as PANSS 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 2SD>(S‐S min), where S is the mean score and S min is the minimum score. Endpoint scores on scales often have a finite start and end point and these rules can be applied. When continuous data are presented on a scale which includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not.
We will enter skewed data from studies of fewer than 200 participants in additional tables rather than into an analysis. Skewed data pose less of a problem when looking at means if the sample size is large; we will enter data from such studies into syntheses.
2.5 Conversion of continuous to binary
Where possible, we will attempt to convert outcome measures to dichotomous data. This can be done by identifying cutoff 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 Positive and Negative Syndrome Scale (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.
2.6 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 continuing olanzapine. Where keeping to this makes it impossible to avoid outcome titles with clumsy double‐negatives (e.g. 'Not improved'), we will report data where the left of the line indicates an unfavourable outcome. We will note this in the relevant graphs.
2.7 Summary of findings table
We will use the GRADE approach to interpret findings (Schünemann 2008) and will use GRADE profiler (GRADEPRO) to import data from Review Manager (RevMan) 5.1 (RevMan 2011) 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 will rate as important to patient‐care and decision making. We will select the following main outcomes for inclusion in the summary of findings table:
1. Global state
1.1 Clinical relapse
2. Service use
2.1 Hospital admission
2.3 Days in hospital
3. Adverse effect
Any important adverse event
4. Quality of life improved to an important extent
Assessment of risk of bias in included studies
Working independently, OH and GA will assess risk of bias using the tool described in the Cochrane Handbook for Systematic 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 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 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 achieve resolution by discussion.
We will note the level of risk of bias in the text of the review, in the Summary of findings table, and in summary figures.
Measures of treatment effect
1. Binary data
For binary outcomes we will calculate a standard estimation of the random‐effects (Der‐Simonian 1986) risk ratio (RR) and its 95% confidence interval (CI). It has been shown that RR is more intuitive (Boissel 1999) than odds ratios and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). This misinterpretation then leads to an overestimate of the impression of the effect.
2. Continuous data
For continuous outcomes we will estimate a MD between groups. In the case of where scales are of such similarity to allow pooling, we will calculate the SMD and, whenever possible, 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 pose 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, confidence intervals unduly narrow, and statistical significance overestimated. This causes type I errors (Bland 1997; Gulliford 1999).
If results from trials did not adjust for clustering, we will attempt to adjust the results for clustering, by multiplying the standard errors of the effect estimates (RR or MD, ignoring clustering) by the square root of the design effect. The design effect is calculated as DEff = 1 + (M ‐ 1) ICC, where M is the average cluster size and ICC is the intra‐cluster coefficient (Higgins 2008). If an ICC is not available from the trial, other sources will be used to impute ICCs (Campbell 2000).
Where clustering is 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. If a cluster study is appropriately analysed, taking into account intra‐class correlation co‐efficient and relevant data documented in the report, synthesis with parallel group randomised trials is possible using the generic inverse variance technique, where the natural logarithm of the effect estimate (and standard errors) for all included trials for that outcome is calculated and entered into RevMan 5.1 (RevMan 2011), along with the log of the effect estimate (and standard errors) from the cluster randomised trial(s). We will use methods described in section 7.7.7.2 and 7.7.7.3 of the Cochrane Handbook (Higgins 2011) to obtain standard errors.
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 schizophrenia, randomised cross‐over studies are eligible, but only data up to the point of first cross‐over.
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 and combine these 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 (Higgins 2011). 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). The loss to follow‐up in randomised schizophrenia trials is often considerable, calling the validity of the results into question. Nevertheless, it is unclear which degree of attrition leads to a high degree of bias. We, however, will use the risk of bias tool described above to indicate potential bias when more than 25% of the participants left the studies prematurely, when the reasons for attrition differ between the intervention and the control group, and when no appropriate imputation strategies are applied.
2. Binary data
In the case where attrition for a binary outcome is between 0 and 25% and where these data are not clearly described, we will present data on a 'once‐randomised‐always‐analyse' basis (an intention‐to‐treat analysis). Those leaving the study early are all assumed to have the same rates of negative outcome as those who completed, with the exception of the outcome of death and adverse effects. For these outcomes we will use the rate of those who stayed in the study ‐ in that particular arm of the trial ‐ for those who did not. We will undertake a sensitivity analysis testing how prone the primary outcomes are to change when 'completer' data only are compared to the intention‐to‐treat analysis using the above assumptions.
3. Continuous data
3.1 General
In the case where attrition for a continuous outcome is between 0 and 25% and completer‐only data are reported, we will reproduce these.
3.2 Missing standard deviations
If standard deviations 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 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 (Higgins 2011): When only the standard error (SE) is reported, standard deviations (SDs) are calculated by the formula SD = SE * square root (n). Chapters 7.7.3 and 16.1.3 of the Cochrane Handbook (Higgins 2011) present detailed formula for estimating SDs from P, T, or F values, confidence intervals, 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 Last observation carried forward
We anticipate that in some studies the method of last observation carried forward (LOCF) will be employed within the study report. As with all methods of imputation to deal with missing data, LOCF introduces uncertainty about the reliability of the results (Leucht 2007). Therefore, where LOCF data have been used in the trial, if less than 50% of the data have been assumed, we will reproduce these data and indicate that they are the product of LOCF assumptions.
Assessment of heterogeneity
1. Clinical heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will inspect all studies for clearly outlying situations or people which we had not predicted and discuss them fully.
2. Methodological heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We will inspect all studies for clearly outlying methods which we had not predicted and discuss them if evident.
3. Statistical
3.1 Visual inspection
We will visually inspect graphs to identify trials with non‐overlapping confidence intervals within a forest plot to suggest the possibility of statistical heterogeneity.
3.2 Employing the I2statistic
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 confidence interval for I2).
We will interpret I2 estimates greater than or equal to 50% accompanied by a statistically significant Chi2 statistic as evidence of substantial levels of heterogeneity (Section 9.5.2 ‐ Higgins 2011) and explore reasons for heterogeneity. If the inconsistency is high and the clear reasons are found, we will present data separately.
Assessment of reporting biases
We will enter data from all identified and selected trials for each outcome into a funnel plot (trial effect versus trial size) in an attempt to investigate the likelihood of overt publication bias. We will test for funnel plot asymmetry only for outcomes where there are 10 or more studies and if the studies are not of similar sizes, as recommended in Section 10.4.3.1 of the Cochrane Handbook (Higgins 2011). The statistical test by Egger (Egger 1997) will be used to formally assess funnel‐plot asymmetry, and will be supplemented by visual inspection of the forest plot to differentiate small study effects from other reasons for funnel plot asymmetry.
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 random‐effects model for all analyses. The reader is, however, able to choose to inspect the data using the fixed‐effect model.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1 Participants
We will try and present data for people with schizophrenia in similar states and stages together so these data can be considered together. For primary outcomes, if data exist, we will report these as subgroup analyses.
1.2 Intervention
We anticipate subgroup analyses investigating the different interventions utilised to stop or reduce the dose of olanzapine. These subgroups will be where olanzapine treatment was abruptly discontinued, where olanzapine dose was gradually tapered off, and where olanzapine was replaced with another medication. Although we will synthesise data overall, we will, if possible, present them in subgroups.
2. Investigation of heterogeneity
If inconsistency is high, we will report this. First we will investigate whether data have been entered correctly. Second, if data are correct, we will visually inspect the graph and successively remove studies outside of the company of the rest to see if homogeneity is restored. Should this occur with no more than 10% of the data being excluded, we will present data. If not, we will not pool data and will discuss issues.
Should unanticipated clinical or methodological heterogeneity be 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
These analyses will only apply to the primary outcomes. We are conscious of the risk of finding significant results because of the play of chance secondary to multiple analyses.
1. Risk of bias
We will analyse the effects of excluding trials that were judged to be at high risk of bias across one or more of the domains of randomisation (implied as randomised with no further details available): allocation concealment, blinding, and outcome reporting for the meta‐analysis of the primary outcome. If the exclusion of trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then we will include data from these trials in the analysis.
2. Imputed values
We will also undertake a sensitivity analysis to assess the effects of including data from trials where we used imputed values. If we note substantial differences in the direction or precision of effect estimates, we will not pool data, but will present them separately.
3. Fixed and random effects
We will synthesise data for the primary outcome using a random‐effects model to evaluate whether the greater weights assigned to smaller trials altered the significance of the results, compared with the less evenly distributed weights in the fixed‐effect model.
4. Unpublished studies
We will analyse data from published studies (those with a report in peer reviewed journals) and compare these findings with outcomes from trials that have not yet appeared in full report in peer reviewed journals. We propose to comment on these findings, but not take action on them.
5. Industry funding
We will analyse the primary outcomes from trials funded or supported by industry and compare these data with those from more independent studies. Again, we propose to comment on these findings, but not exclude or include studies because of them.
Olanzapine structure
Olanzapine structure‐2
