Anticholinergics versus placebo for neuroleptic‐induced parkinsonism
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effects of anticholinergic drugs compared with placebo for antipsychotic‐induced parkinsonism in people with schizophrenia and related disorders including schizophreniform disorder, delusional disorder, psychosis and schizoaffective disorder.
Background
Description of the condition
Extrapyramidal side effects (EPSE) can be divided into acute and chronic. Acute EPSE include the dystonias, parkinsonism and akathisia, and those classified as chronic are tardive dyskinesia and tardive dystonia (APA 2006).
Parkinsonism is a group of symptoms which resemble idiopathic Parkinson’s disease; the commonly observed symptoms include tremor, bradykinesia (slow movement), rigidity (limb stiffness), mask‐like face and postural instability. The less frequently observed symptoms include festinant (an involuntary tendency to take short accelerating steps when walking), hurrying gait, 3‐5Hz resting tremor, micrographia (reduction in size of handwriting) and rhythmic disturbance of handwriting (Gervin 2000). These effects, cause distress by affecting physical and social functioning. They usually emerge within a few days or weeks after starting antipsychotic treatment or a dose increase.
There are a number of scales for measuring EPSE generally, which include items for parkinsonism. These scales include the Extrapyramidal Symptom Rating Scale (Chouinard 1980), the Targeting Abnormal Kinetic Effects Scale (Wojcik 1980), the Extrapyramidal Symptoms Scale and the Simpson‐Angus Scale (Simpson 1970). The Simpson‐Angus Scale is the most widely used and was devised to measure drug‐induced parkinsonism.
Although parkinsonism is frequently seen in clinical life, the incidence from well‐conducted surveys is less clear and varies up to 40% (Gervin 2000) dependent on the type and dose of antipsychotic medication. Recent research has shown that there is no difference in the incidence of EPSE between people treated with atypical and typical antipsychotics (Miller 2008). Risk factors for developing parkinsonism are female gender, older age, non‐smoker, dose duration and type of treatment, cognitive impairment, acquired immunodeficiency syndrome (AIDS), tardive dyskinesia and pre‐existing movement disorder (Thanvi 2009).
Parkinsonism is associated with potent D2 receptor antagonists; more than 80% dopamine D2 receptor occupancy is consistent with drug‐induced parkinsonism (Hirose 2006). Newer generation antipsychotics are also associated with drug‐induced parkinsonism (Peluso 2012).
Description of the intervention
Guidelines recommend reducing or switching antipsychotic or adding short‐term anticholinergic medications as treatment for those presenting with antipsychotic‐induced parkinsonism (Taylor 2012). When a person presents with neuroleptic‐induced parkinsonian effects but with good response to neuroleptic medication, the main treatment option considered is anticholinergic medication. There are, however, risks associated with anticholinergic medication, such as an increase in ‘positive’ psychotic symptoms (Johnstone 1983), cognitive decline (Bottiggi 2006), and worsening of tardive dyskinesia (Yassa 1988). Anticholinergic medications can be abused for their stimulating and euphoriant effects (Pullen 1984) with one study showing that 33% of people prescribed anticholinergic medication abused them within the previous month (Buhrich 2000).
From a literature review regarding treatments for neuroleptic‐induced parkinsonism, several types of anticholinergic medication were found. The anticholinergic medications that are available in the United Kingdom are orphenadrine, procyclidine and trihexyphenidyl (BNF 2013). Biperiden is the anticholingeric drug on the World Health Organization's Essential Drug List (WHO 2013). There are other anticholinergic medications that are available elsewhere; these being benztropine, dexetemide, etybenzatropine and profenamine (also known as ethopropazine).
How the intervention might work
Dopamine normally suppresses acetylcholine activity; therefore, removal of dopamine inhibition causes an increase in release of acetylcholine and therefore anticholinergic activity (Stahl 2008). Anticholinergic drugs block the acetylcholine receptors, thereby overcoming the excessive cholinergic activity.
Why it is important to do this review
Parkinsonism is a common adverse effect of antipsychotic treatment (Dickenson 2013). It results in social and functional handicap (Gervin 2000) and the suffering and stigmatisation associated with drug‐induced parkinsonism is likely to remain with patients for a long time to come.
People living in low‐ and middle‐income countries have a limited choice of medication, which necessitates the use of higher potency antipsychotic drugs that are more likely to cause parkinsonism. Haloperidol, chlorpromazine hydrochloride, fluphenazine decanoate or enantate, risperidone and clozapine are the antipsychotic medications included in the WHO Essential Drug List (WHO 2013).
| Treatment | Prevalence of parkinsonism (%, 95% CI) |
| Chlorpromazine | 16 (14‐19) |
| Clozapine | 18 (13‐23) |
| Fluphenazine decanoate | 7 (4‐13) |
| Fluphenazine enantate | 31 (17‐50) |
| Haloperidol | 31 (29‐34) |
| Risperidone | 12 (8‐18) |
| from Dickenson 2013 | |
Objectives
To assess the effects of anticholinergic drugs compared with placebo for antipsychotic‐induced parkinsonism in people with schizophrenia and related disorders including schizophreniform disorder, delusional disorder, psychosis and schizoaffective disorder.
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). If their inclusion does not result in a substantive difference, they will remain in the analyses. If their inclusion does result in important clinically significant, but not necessarily statistically significant differences, we will not add the data from these lower quality studies to the results of the better trials, but will present such data within a subcategory. We will exclude quasi‐randomised studies, such as those allocating by alternate days of the week. Where people are given additional treatments within anticholinergic drugs and antipsychotic drugs, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the anticholinergic drug that is randomised.
Types of participants
People receiving any type of antipsychotic medication for schizophrenia or a related disorder and experiencing neuroleptic‐induced parkinsonism.
Types of interventions
1. Anticholinergic drug
Any anticholinergic drug, any dose, any frequency, any route of administration, taken with any type/dose/route/frequency of antipsychotic.
2. Placebo
Any dose, frequency or route of administration taken with any type/dose/route/frequency of antipsychotic.
Types of outcome measures
All outcomes will be divided into short term (less than 24 hours), medium term (one day to one week) and long term (over one week).
Primary outcomes
1. Specific symptoms
1.1 Clinically important change in symptoms of parkinsonism
2. General functioning
2.1 Clinically important change in general functioning
3. Quality of life
3.1 Clinically important change in quality of life
Secondary outcomes
1. Specific symptoms
1.1 Average endpoint parkinsonism score
1.2.Average change in parkinsonism score
2 General functioning
2.1 Average endpoint general functioning score
2.2 Average change in general functioning score
3. Quality of life
3.1 Average endpoint general quality of life score
3.2 Average change in general quality of life score
4. Mental state
4.1 Clinically important change in general mental state score
4.2 Average endpoint general mental state score
4.3 Average change in general mental state score
4.4 Clinically important change in specific symptoms
4.5 Average endpoint specific symptom score
4.6 Average change in specific symptom score
5. Adverse effects
5.1 Number of participants with at least one adverse effect
5.2 Clinically important specific adverse effects (cardiac effects, movement disorders, worsening of psychosis, sedation, seizures, weight gain, effects on white blood cell count, anticholinergic misuse)
5.3 Average endpoint in specific adverse effects
5.4 Average change in specific adverse effects
6. Hospitalisation and death
6.1 Number of participants requiring hospitalisation
6.2 Number of participants who died
7. Leaving the study early
7.1 Any reason
7.2 Adverse events
7.3 Inefficacy of treatment
8. '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 RevMan 5 (Review Manager) to create 'Summary of findings' tables. These tables provide outcome‐specific information concerning the overall quality of evidence from each included study in the comparison, the magnitude of effect of the interventions examined, and the sum of available data on all outcomes we 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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Specific symptoms: Parkinsonism ‐ clinically important change in the medium term
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General functioning ‐ clinically important change in the long term
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Quality of life ‐ improved to an important extent in the long term
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Mental state ‐ changes in mental state in the long term
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Adverse effects ‐ clinically important adverse effects, any further treatment required in the long term
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Leaving the study early ‐ due to adverse events or inefficacy of treatment in the short/medium/long term
Search methods for identification of studies
Electronic searches
The Trials Search Co‐ordinator will search the Cochrane Schizophrenia Group’s Trials Register applying the following search strategy:
((Benzhexol or trihexyphenidyl or triphenidyl or Biperiden* or (muscarin* NEXT antagonist*) or Dexetemide or Dexetimide or Dexbenzemide or "Dex benzemide" or Procyclidine or Orphenadrine or Benztropine or benzatropine or Methixene or Metixene or Ethybenztropine or Etybenzatropine or "n‐ethyl‐nortropine‐benzhydryl‐ether‐hydrobromide" or UK738 or ethopropazine or Elantrine or "dicyclohexyl‐sulfamate" or Bornaprine or Diethazine or Profenamine or Tropatepine) and placebo*)) in Title or Abstract and (parkinson*) in Title or Abstract or Keyword of REFERENCE or ((Benzhexol or trihexyphenidyl or triphenidyl or Biperiden* or (muscarin* NEXT antagonist*) or Dexetemide or Dexetimide or Dexbenzemide or "Dex benzemide" or Procyclidine or Orphenadrine or Benztropine or benzatropine or Methixene or Metixene or Ethybenztropine or Etybenzatropine or "n‐ethyl‐nortropine‐benzhydryl‐ether‐hydrobromide" or UK738 or ethopropazine or Elantrine or "dicyclohexyl‐sulfamate" or Bornaprine or Diethazine or Profenamine or Tropatepine) and placebo*)) in Intervention and (parkinson*) in Health Care Condition of STUDY
The Cochrane Schizophrenia Group’s Trials Register is compiled by systematic searches of major databases and their monthly updates, handsearches and conference proceedings (see Group Module).
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.
Data collection and analysis
Selection of studies
Review authors RD and SM will independently inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently re‐inspected by LD to ensure reliability. Where disputes arise, the full report will be acquired for more detailed scrutiny. Full reports of the abstracts meeting the review criteria will be obtained and inspected by RD and SM. Again, a random 20% of reports will be re‐inspected by LD 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 RD and SM will extract data from all included studies. In addition, to ensure reliability, LD will independently extract data from a random sample of these studies, comprising 10% of the total. Any disagreement will be discussed, decisions documented and, if necessary, we will contact the authors of studies for clarification. With any remaining problems, LD will help clarify issues and these final decisions will be documented. If we find data presented only in graphs and figures we will extract the data whenever possible, but only include if two review authors independently have the same result. We will attempt to contact authors through an open‐ended request in order to obtain missing information or for clarification whenever necessary. If studies are multicentre, where possible, we will extract data relevant to each component centre separately.
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:
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the psychometric properties of the measuring instrument have been described in a peer‐reviewed journal (Marshall 2000); and
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the measuring instrument has not been written or modified by one of the trialists for that particular trial.
Ideally, the measuring instrument should either be 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, therefore, in 'Description of studies' we will note if this is the case or not.
2.3 Endpoint versus change data
There are advantages of both endpoint and change data. Change data can remove a component of between‐person variability from the analysis. On the other hand, calculation of change needs two assessments (baseline and endpoint), which can be difficult in unstable and difficult to measure conditions such as schizophrenia. We have decided primarily to use endpoint data, and only use change data if the former are not available. Endpoint and change data will be combined in the analysis as we will use mean differences (MD) rather than standardised mean differences (SMD) throughout (Higgins 2011).
2.4 Skewed data
Continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non‐parametric data, we aim to apply the following standards to all data before inclusion:
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standard deviations (SDs) and means are reported in the paper or obtainable from the authors;
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when a scale starts from the finite number zero, the SD, when multiplied by two, is less than the mean (as otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution, (Altman 1996);
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if a scale started from a positive value (such as the Positive and Negative Syndrome Scale (PANSS), (Kay 1986)) ,which can have values from 30 to 210), the calculation described above will be modified to take the scale starting point into account. In these cases skew is present if 2 SD > (S‐S min), where S is the mean score and 'S min' is the minimum score.
Endpoint scores on scales often have a finite start and end point and these rules can be applied. Skewed data pose less of a problem when looking at means if the sample size is large (> 200) and we will enter these into the syntheses. We will present skewed endpoint data from studies of less than 200 participants as other data within the data and analysis section rather than enter such data into statistical analyses.
When continuous data are presented on a scale that includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. We will present and enter change data into analyses.
2.5 Common measure
To facilitate comparison between trials, we intend to convert variables that can be reported in different metrics, such as days in hospital (mean days per year, per week or per month) to a common metric (e.g. mean days per month).
2.6 Conversion of continuous to binary
Where possible, efforts will be made to convert outcome measures to dichotomous data. This can be done by identifying cut‐off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that if there is a 50% reduction in a scale‐derived score such as the Brief Psychiatric Rating Scale (BPRS, Overall 1962) or the 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.
2.7 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 the anticholinergic drug. Where keeping to this makes it impossible to avoid outcome titles with clumsy double‐negatives (e.g. 'Not improved'), we will report data where the left of the line indicates an unfavourable outcome. This will be noted in the relevant graphs.
Assessment of risk of bias in included studies
Again, review authors RD and SM will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011) to assess trial quality. This set of criteria is based on evidence of associations between overestimate of effect and high risk of bias of the article such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting.
If the raters disagree, the final rating will be made by consensus, with the involvement of another member of the review group. Where inadequate details of randomisation and other characteristics of trials are provided, we will contact the authors of the studies in order to obtain further information. Non‐concurrence in quality assessment will be reported, but if disputes arise as to which category a trial is to be allocated, again, we will resolve by discussion.
The level of risk of bias will be noted in both the text of the review and in the 'Summary of findings' table.
Measures of treatment effect
1. Binary data
For binary outcomes, we will calculate a standard estimation of the risk ratio (RR) and its 95% confidence interval (CI). It has been shown that RR is more intuitive (Boissel 1999) than odds ratios and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). The Number Needed to Treat/Harm (NNT/H) statistic with its confidence intervals 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 mean difference (MD) between groups. We prefer not to calculate effect size measures (standardised mean difference (SMD)). However, if scales of very considerable similarity are used, we will presume there is a small difference in measurement, and we will calculate effect size and transform the effect back to the units of one or more of the specific instruments.
Unit of analysis issues
1. Cluster trials
Studies increasingly employ 'cluster randomisation' (such as randomisation by clinician or practice) but analysis and pooling of clustered data poses problems. Firstly, authors often fail to account for intra‐class correlation in clustered studies, leading to a 'unit of analysis' error (Divine 1992) whereby P values are spuriously low, confidence intervals unduly narrow and statistical significance overestimated. This causes type I errors (Bland 1997; Gulliford 1999).
Where clustering is not accounted for in primary studies, we will present data in a table, with a (*) symbol to indicate the presence of a probable unit of analysis error. In subsequent versions of this review, we will seek to contact the first authors of such studies to obtain intra‐class correlation coefficients (ICCs) for their clustered data and to adjust for this by using accepted methods (Gulliford 1999).
Where clustering has been incorporated into the analysis of primary studies, we will present these data as if from a non‐cluster randomised study, but adjust for the clustering effect.
We have sought statistical advice and have been advised that the binary data as presented in a report should be divided by a 'design effect'. This is calculated using the mean number of participants per cluster (m) and the ICC [Design effect = 1+(m‐1)*ICC] (Donner 2002). If the ICC is not reported, it will be assumed to be 0.1 (Ukoumunne 1999).
If cluster studies have been appropriately analysed, taking into account ICCs and relevant data documented in the report, synthesis with other studies will be possible using the generic inverse variance technique.
2. Cross‐over trials
A major concern of cross‐over trials is the carry‐over effect. It occurs if an effect (e.g. pharmacological, physiological or psychological) of the treatment in the first phase is carried over to the second phase. As a consequence, on entry to the second phase the participants can differ systematically from their initial state despite a wash‐out phase. For the same reason, cross‐over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both effects are very likely in severe mental illness, we will only use data of the first phase of cross‐over studies.
3. Studies with multiple treatment groups
Where a study involves more than two treatment arms, if relevant, the additional treatment arms will be presented in comparisons. If data are binary, these will be simply added and combined within the two‐by‐two table. If data are continuous, we will combine data following the formula in section 7.7.3.8 (Combining groups) of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). Where the additional treatment arms are not relevant, we will not use these data.
Dealing with missing data
1. Overall loss of credibility
At some degree of loss of follow‐up, data must lose credibility (Xia 2009). We choose that, for any particular outcome, should more than 50% of data be unaccounted for, we will not reproduce these data or use them within analyses. If, however, more than 50% of those in one arm of a study are lost, but the total loss is less than 50%, we will address this within the 'Summary of findings' 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 analysis). Those leaving the study early are all assumed to have the same rates of negative outcome as those who completed, with the exception of the outcome of death and adverse effects. For these outcomes, the rate of those who stay in the study ‐ in that particular arm of the trial ‐ will be used for those who did not. We will undertake a sensitivity analysis to test how prone the primary outcomes are to change when data only from people who complete the study to that point are compared to the intention‐to treat analysis using the above assumptions.
3. Continuous
3.1 Attrition
In the case where attrition for a continuous outcome is between 0% and 50%, and data only from people who complete the study to that point are reported, we will reproduce these.
3.2 Standard deviations
If standard deviations (SDs) are not reported, we will first try to obtain the missing values from the authors. If not available, where there are missing measures of variance for continuous data, but an exact standard error (SE) and confidence intervals available for group means, and either a 'P' value or 't' value available for differences in mean, we can calculate them according to the rules described in the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011): When only the SE is reported, SDs are calculated by the formula SD = SE * square root (n). Chapters 7.7.3 and 16.1.3 of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011) present detailed formulae for estimating SDs from P values, t or F values, confidence intervals, ranges or other statistics. If these formulae do not apply, we will calculate the SDs according to a validated imputation method which is based on the SDs of the other included studies (Furukawa 2006). Although some of these imputation strategies can introduce error, the alternative would be to exclude a given study’s outcome and thus to lose information. We nevertheless will examine the validity of the imputations in a sensitivity analysis excluding imputed values.
3.3 Last observation carried forward
We anticipate that in some studies the method of last observation carried forward (LOCF) will be employed within the study report. As with all methods of imputation to deal with missing data, LOCF introduces uncertainty about the reliability of the results (Leucht 2007). Therefore, where LOCF data have been used in the trial, if less than 50% of the data have been assumed, we will present and use these data and indicate that they are the product of LOCF assumptions.
Assessment of heterogeneity
1. Clinical heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will simply inspect all studies for clearly outlying people or situations which we had not predicted would arise. When such situations or participant groups arise, these will be fully discussed.
2. Methodological heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We will simply inspect all studies for clearly outlying methods which we had not predicted would arise. When such methodological outliers arise these will be fully discussed.
3. Statistical heterogeneity
3.1 Visual inspection
We will visually inspect graphs to investigate the possibility of statistical heterogeneity.
3.2 Employing the I2 statistic
Heterogeneity between studies will be investigated by considering the I2 method alongside the Chi2 'P' value. The I2 provides an estimate of the percentage of inconsistency thought to be due to chance (Higgins 2003). The importance of the observed value of I2 depends on i. magnitude and direction of effects and ii. strength of evidence for heterogeneity (e.g. 'P' value from Chi2 test, or a confidence interval for I2). An I2 estimate greater than or equal to around 50% accompanied by a statistically significant Chi2 statistic, will be interpreted as evidence of substantial levels of heterogeneity (Section 9.5.2 ‐ Higgins 2011). When substantial levels of heterogeneity are found in the primary outcome, we will explore reasons for the heterogeneity (Subgroup analysis and investigation of heterogeneity).
Assessment of reporting biases
1. Protocol versus full study
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. These are described in section 10.1 of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). We will try to locate protocols of included randomised trials. If the protocol is available, outcomes in the protocol and in the published report will be compared. If the protocol is not available, outcomes listed in the methods section of the trial report will be compared with actually reported results.
2. Funnel plot
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are again described in Section 10 of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). We are aware that funnel plots may be useful in investigating reporting biases but are of limited power to detect small‐study effects. We will not use funnel plots for outcomes where there are 10 or fewer studies, or where all studies are of similar sizes. In other cases, where funnel plots are possible, we will seek statistical advice in their interpretation.
Data synthesis
We understand that there is no closed argument for preference for use of fixed‐effect or random‐effects models. The random‐effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This often seems to be true to us and the random‐effects model takes into account differences between studies even if there is no statistically significant heterogeneity. There is, however, a disadvantage to the random‐effects model. It puts added weight onto small studies, which often are the most biased ones. Depending on the direction of effect, these studies can either inflate or deflate the effect size. We choose to use the 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 Primary outcomes
No subgroup analyses are anticipated.
1.2 Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of anticholinergic drugs for people with neuroleptic‐induced parkinsonism. In addition, however, we will try to report data on subgroups of people in the same clinical state, stage and with similar problems.
2. Investigation of heterogeneity
If inconsistency is high, this will be reported. First, we will investigate whether data have been entered correctly. Second, if data are correct, we will visually inspect the graph and outlying studies will be successively removed to see if homogeneity is restored. For this review we decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, data will be presented. If not, data will not be pooled and issues will be discussed. We know of no supporting research for this 10% cut‐off but are investigating use of prediction intervals as an alternative to this unsatisfactory state.
When unanticipated clinical or methodological heterogeneity are obvious, we will simply state hypotheses regarding these for future reviews or versions of this review. We do not anticipate undertaking analyses relating to these.
Sensitivity analysis
1. Implication of randomisation
We aim to include trials in a sensitivity analysis if they are described in some way as to imply randomisation. For the primary outcomes, we will include these studies and if there is no substantive difference when the implied randomised studies are added to those with better description of randomisation, then all data will be employed from these studies.
2. Assumptions for lost binary data
Where assumptions have to be made regarding people lost to follow‐up (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumptions and when we use data only from people who complete the study to that point. If there is a substantial difference, we will report results and discuss them, but will continue to employ our assumption.
Where assumptions have to be made regarding missing SDs data (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from people who complete the study to that point. We will undertake a sensitivity analysis to test how prone results are to change when completer‐only data only are compared to the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them, but will continue to employ our assumption.
3. Risk of bias
We will analyse the effects of excluding trials that are judged to be at high risk of bias across one or more of the domains of randomisation (implied as randomised with no further details available) allocation concealment, blinding and outcome reporting for the meta‐analysis of the primary outcome. If the exclusion of trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then data from these trials will be included in the analysis.
4. Imputed values
We will also undertake a sensitivity analysis to assess the effects of including data from trials where we used imputed values for ICC in calculating the design effect in cluster randomised trials.
If substantial differences are noted in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we will not pool data from the excluded trials with the other trials contributing to the outcome, but will present them separately.
5. Fixed‐effect and random‐effects
All data will be synthesised using a random‐effects model, however, we will also synthesise data for the primary outcome using a fixed‐effect model to evaluate whether this alters the significance of the results.
