Second‐generation antipsychotic drugs for anxiety disorders
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effects of second generation antipsychotics for people with primary anxiety disorder.
Background
Description of the condition
Anxiety disorders are common, with a life‐time prevalence of 17% in the general population (Somers 2006). Among the anxiety disorders, panic disorder (life time prevalence 5%, Grant 2006) is characterised by 'panic attacks', which are recidivating states of extreme anxiety, typically of a duration of ten minutes. Generalized anxiety disorder (GAD) (life time prevalence 5%, Munk‐Jorgensen 2006) is in contrast characterised by continuous excessive worrying about problems of life such as financial issues or physical health, and is frequently accompanied by physical symptoms such as fatigue, restlessness, sleep problems, etc. Specific phobias are inappropriate fears related to specific objects (e.g. snakes, spiders) or situations (e.g., heights). In particular, social phobia (life time prevalence 13%, Kessler 1994) is characterised by a marked and persistent fear of one or more social or performance situations in which the person is exposed to unfamiliar people or to possible scrutiny by others.
All subtypes of anxiety disorders usually lead to a high degree of suffering and disability amongst those affected.
Description of the intervention
Whilst antidepressant drugs and benzodiazepines can be efficacious treatments for anxiety disorders, the rates of treatment resistance are high. Bystritsky 2006 reported that approximately 40% of people with anxiety disorders do not sufficiently respond to treatment with antidepressants. Therefore, there is a need for other agents to alleviate the symptoms of these disorders.
Second generation ('atypical') antipsychotic drugs were introduced for the treatment of schizophrenia in the 1990s. They may include: amisulpride, aripiprazole, clozapine, olanzapine, quetiapine, paliperidone, risperidone, sertindole, ziprasidone or zotepine. Their main advantage compared to conventional antipsychotic drugs such as haloperidol is that they induce fewer extrapyramidal side effects, including the disabling, often irreversible and stigmatising tardive dyskinesia (Correll 2004). Superior tolerability and potential effects on depression, anxiety and negative symptoms make them candidates as sole or adjunctive agents for the treatment of disorders other than schizophrenia.
There is evidence that 70 % of all prescriptions of second generation antipsychotics are for indications other than schizophrenia (Sajatovic 2003). The manufacturers of these drugs also aggressively try to expand the indications of their compounds; however, atypical antipsychotic drugs are very costly. For example, the estimated costs of atypical antipsychotics totaled $11.7 billion in the United States in 2005 (Vital Signs 2007). Furthermore, some second generation antipsychotics are associated with severe adverse events such as weight gain (Allison 1999).
How the intervention might work
Second generation antipsychotic drugs block central dopamine receptors, most of them also block serotonin receptors and many other neuroreceptors (Arnt 1998), but, despite some promising data suggesting potential therapeutic benefits for the use of some second generation antipsychotic drugs in anxiety disorders, the exact mechanism is currently unknown (Gao 2006).
Why it is important to do this review
To the best of our knowledge there is currently only one systematic review on this topic (Gao 2006). Gao and colleagues included only two studies on the treatment of anxiety disorders with second‐generation antipsychotic drugs. A large number of studies about treatment of anxiety disorder with second‐generation antipsychotic drugs have been conducted and published since searches were conducted for this review. Furthermore, Gao 2006 addressed only efficacy, and efficacy of a treatment can only be seen in the context of its side effects.
Given the frequent off‐label use in practice, uncertain efficacy, potential side effects and the high costs of second generation antipsychotic drugs in anxiety disorders, an up to date systematic review is important.
Objectives
To assess the effects of second generation antipsychotics for people with primary anxiety disorder.
Methods
Criteria for considering studies for this review
Types of studies
We will include all randomized double‐blind trials, meaning that at least the participants, the raters and the treatment team will have to be blinded (double‐blind is a conventional definition of this situation in drug trials). Cluster randomized studies meeting certain criteria will also be included (see below). Randomised cross‐over studies will be eligible but only data up to the point of first cross‐over will be used because of the instability of the problem behaviours and the likely carryover effects of the treatments.
Types of participants
We will include participants with the primary anxiety disorders generalized anxiety disorder, panic disorder and specific phobias (including social phobia) according to DSM‐III/DSM‐IV (300.21, 300.01, 300.02 ) (APA 1980; APA 1987; APA 1994) or ICD‐10 (F 40 and F41) (WHO 1992). Obsessive compulsive disorder will be excluded, because we will address this disorder in a separate review and because ICD‐10 does not classify it among the anxiety disorders. Children and adolescents will be excluded, because these have been addressed in another review (Hawkridge 2005). Thus participants will have to be older than 18 years (no upper limit). There will be no limits in terms of setting. Studies in participants with a primary or secondary diagnosis of another axis 1 or axis 2 disorder will be excluded, if these make up for more than 20% of the participants. Anxiety disorder trials in participants with a serious concomitant medical illness will not be excluded.
Types of interventions
Second generation antipsychotics may be given as mono or adjunctive therapy compared to placebo, benzodiazepines or antidepressants.
1. Experimental treatments will be one of the following: second generation antipsychotic drugs: amisulpride, aripiprazole, clozapine, olanzapine, quetiapine, paliperidone, risperidone, sertindole, ziprasidone or zotepine (any dose, any oral mode of administration).
2. Comparator substances will be either placebo, a benzodiazepine or any of the following antidepressants, all at any dose and oral mode of administration: tricyclic/heterocyclic antidepressants, SSRIs (fluoxetine, paroxetine, sertraline, fluvoxamine, citalopram, escitalopram), SNRIs (venlafaxine, duloxetine, milnacipran), MAOIs or newer agents (mirtazapine, bupropion, reboxetine) or St John’s Wort. Treatment can be given either as monotherapy or as add‐on.
We will exclude treatment with first generation antipsychotics, which due to their overall higher risk of extrapyramidal side‐effects are rarely used in this indication. Head‐to‐head comparisons of second generation antipsychotic drugs will also be excluded. Psychological treatment will be allowed as long as it is provided to both the treatment and control group. We will exclude studies with only non pharmacological treatment as comparator.
There will be no limits in terms of duration of treatment. We will categorize all outcomes as short term (up to 12 weeks), medium term (3‐6 months) and long term (longer than 6 months).
Types of outcome measures
Primary outcomes
Our primary outcome will be clinically significant response to treatment. In studies on generalized anxiety disorder response to treatment will be defined as the number of participants with an at least 50% reduction of Hamilton Anxiety Scale (HAM‐A, Hamilton 1959) score from baseline. For panic disorder and social phobia we will apply the same cut‐off (at least 50% reduction from baseline) of the Panic Disorder Severity Scale (PDSS, Shear 1997) or the Sheehan Panic Anxiety Scale‐Patient (SPAS‐P, Raj 1987), and the Brief Social Phobia Scale (BSPS, Davidson 1997) or the Liebowitz Social Anxiety Scale (LSAS, Liebowitz 1987), respectively. Whenever results of these specific scales have been presented we will use their results. If no anxiety scale is provided, we will look for the Clinical Global Impression Scale (CGI, Guy 1976). We will consider a CGI‐S (severity) score of one, two or three; and a CGI‐I (improvement) score of one or two as significant response. If no scale or none of the cut‐offs specified above is provided, we will accept any definition of outcome from the authors.
Secondary outcomes
1. Anxiety symptoms will be addressed by HAM‐A (Hamilton 1959) or BSPS (Davidson 1997) or PDSS (Shear 1997) score or other anxiety rating scales at the end of the study.
2. Relapse ‐ number of participants relapsed (as defined by the authors).
3. Remission measured as the number of participants showing 17 or less on 14‐item HAM‐A (Hamilton 1959) (or any other similar cut‐off value on the anxiety scale, depending on the study authors' definition) or not ill or borderline mentally ill (score one or two) on CGI‐Severity (Guy 1976), or according to authors' definition of remitters at follow up.
4. Number of participants who received additional benzodiazepines.
5. Depressive symptoms will be addressed by the Montgomery Åsberg Depression Rating Scale (MADRS, Montgomery 1979) or the Hamilton Depression Rating Scale (HAM‐D, Hamilton 1960) score at endpoint.
6. Premature study discontinuation due to any reason, due to inefficacy of treatment, due to adverse events.
7. Adverse events (use of antiparkinson medication, tardive dyskinesia, weight gain, sedation, prolactin increase).
8. Service use ‐ numbers of participants rehospitalised for psychiatric reasons.
If the original authors present dichotomised results of rating scales using cut‐offs (e.g. the number of participants with an at least 50% reduction of the MADRS) we will present them in addition to the results based on mean scores.
Search methods for identification of studies
Electronic searches
With the assistance of the Cochrane Collaboration Depression, Anxiety and Neurosis Group's (CCDAN) Trials Search Coordinator (TSC) we will search the Group's Controlled Trials Registers (CCDANCTR‐References and CCDANCTR‐Studies). The CCDANCTR‐References Register contains more than 23,000 references to completed or ongoing trials in depression, anxiety and neurosis, of which 16,000 have been coded in the CCDANCTR‐Studies Register. The CCDANCTR References Register is updated weekly with the results of searches of MEDLINE (1966‐), EMBASE (1980‐) and PsycINFO (1974‐). CENTRAL is searched every 3 months (with each new release of this database on the Cochrane Library); PSYNDEX (1977‐), LILACS (1982‐), KoreaMed and IndMed are searched on an annual basis and AMED (1985‐) and CINAHL (1980‐) are searched on an individual review basis (or at least annually). In addition to this, references to trials identified from hand‐searches of major psychiatric, medical journals and conference proceedings are also included in the CCDAN Registers.
The search terms used will be: (anxiety or anxious or panic or phobi*) and (amisulprid* OR aripiprazol* OR clozapin* OR olanzapin* OR paliperidon* OR quetiapin* OR risperidon* OR sertindol* OR ziprasidon* OR zotepin*).
Searching other resources
AMD and KK will inspect the references of all identified studies and of previous reviews for more trials.
AMD, KK and SL will contact the first author of each included study for missing information and for the existence of further studies.
AMD, KK and SL will contact the manufacturers of atypical antipsychotic drugs and ask them about further relevant studies and for missing information on identified studies.
Data collection and analysis
Selection of studies
Authors AMD and KK will independently inspect citations identified from the search. All potentially relevant reports this identified will be ordered for reassessment. Where difficulties or disputes arise we will asked authors SL and WK for assistance / adjudication and if it is impossible to decide, full texts will be ordered for assessment. This process will be repeated for the assessment of the full texts. If it is impossible to resolve disagreements, authors of the papers will be contacted for clarification.
Data extraction and management
Authors AMD and KK will independently extract data from included studies. Again, any disagreement will be discussed, decisions documented and, if necessary, authors of studies will be contacted for clarification. With remaining problems SL and WK will help clarify issues and those final decisions were documented.
Data will be extracted onto standard, simple forms.
Assessment of risk of bias in included studies
Again, working independently, KK and AMD will assess risk of bias using the tool described in the Cochrane Collaboration Handbook (Higgins 2008). This tool encourages consideration of how the sequence was generated, how allocation was concealed, the integrity of blinding at outcome, the completeness of outcome data, selective reporting and other potential sources of bias. We will not include studies where sequence generation is assessed as being at a high risk of bias, where allocation is clearly not concealed, and where double‐blinding has not taken place.
If disputes arise as to which category a trial has to be allocated, again, resolution will be made by discussion, after working with a third reviewer (SL or WK).
Measures of treatment effect
1. Binary data
We will calculate the odds ratio (OR) and its 95% confidence interval (CI).
2. Continuous data
We will calculate the weighted (N) mean differences as it preserves the original units and is therefore easier to interpret.
2.2 Change versus endpoint data
We will use change data only when endpoint data is not available.
2.3 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 apply the following standards to all data before inclusion: (a) data from studies of e.g. at least 200 participants will be entered in the analysis irrespective of the following rules, because skewed data pose less of a problem in large studies. (b) Endpoint data: 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. If this value was lower than 1, it strongly suggests a skew and the study will be excluded. If this ratio is higher than one but below 2, there is suggestion of skew. We will enter the study and test whether its in or exclusion substantially would change the results. If the ratio was larger than 2 the study will be included, because skew is less likely (Altman 1996, Higgins 2008). (c) 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 is skewed or not. We will enter the study, because change data tends to be less skewed and because excluding studies would also lead to bias, because not all the available information was used.
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. We will seek to contact first authors of studies to obtain intra class correlation co‐efficient of their clustered data and to adjust for this by using accepted methods (Gulliford 1999). Where clustering is incorporated , we will present the data as if from a parallel‐group randomised study, but adjusted for the clustering effect. We will additionally exclude such studies in a sensitivity analysis.
If cluster studies are appropriately analysed taking into account intra‐class correlation co‐efficient and relevant data documented in the report, synthesis with other studies will be possible using the generic inverse variance technique.
2. Crossover trials
A major concern of cross‐over trials is the potential for carryover 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 anxiety disorder, randomised cross‐over studies will be eligible but only data up to the point of first cross‐over, data from the following (second) period of the cross‐over trial will not be considered for analysis. We will describe cross‐over studies to be at risk of bias and we will exclude cross‐over studies in a sensitivity analysis.
3. Studies with multiple treatment groups
1. Multiple dose groups
We expect that some studies will address the effects of different doses of the same compound compared to the competitor (e.g. quetiapine 50mg/day, quetiapine 150mg/day and placebo). In the case of dichotomous outcomes we will sum up the sample sizes and the number of people with events across both (quetiapine) groups. For continuous outcomes means and standard deviations will be combined using methods described in chapter 7 (section 7.7.3.8) of the Cochrane Handbook (Higgins 2008).
2. Multiple medications
We expect that some other studies will combine several interventions with one comparison group (e.g. a three arm study comparing amisulpride and olanzapine with placebo). In this case we will analyse the effects of the amisulpride and olanzapine group versus placebo separately, but will divide up the total number of participants in the placebo group. In the case of continuous outcomes the total number of participants in the placebo group will again be divided up, but the means and standard deviations will be left unchanged (see chapter 16, section 16.5.4 in Higgins 2008).
Dealing with missing data
1. Missing participants
Dichotomous data:
All data will be analysed on the basis of the ITT principle: dropouts will always be included in this analysis. Where participants have withdrawn from the trial before the endpoint, it will be assumed their condition would have remained unchanged if they had stayed in the trial. This is conservative for outcomes related to response to treatment (because these participants will be considered to have not responded to treatment). It is not conservative for adverse events, but we think that for the adverse events of interest in our review (see outcomes) a worst case scenario is clinically unlikely. When there are missing data and the method of “last observation carried forward” (LOCF) has been used to do an ITT analysis, then the LOCF data will be used, with due consideration of the potential bias and uncertainty introduced. We are not going to perform a “worst case” and “best case” ITT analysis.
Continuous data:
Concerning continuous data, the Cochrane Handbook recommends avoiding imputations of continuous data and suggests rather that the data must be used in the form they have been presented by the original authors. Whenever ITT data have been presented by the authors they will be preferred to ‘per protocol/completer’ datasets. Furthermore, we acknowledge that all methods of imputation to deal with missing data introduce uncertainty about the reliability of the results. This will depend on the degree of ‘missingness’, the pooled estimate of the treatment effect and the variability of the outcomes. We will consider variation in the degree of missing data as a potential source of heterogeneity.
2. Missing statistics
When only the SE or p values are reported, SDs are calculated according to Altman (Altman 1996). In the absence of supplemental data after requests to the authors, the SDs will be calculated according to a validated imputation method (Furukawa 2006). We will examine the validity of this imputations in the sensitivity analyses.
Assessment of heterogeneity
We will assess heterogeneity on the basis of the Cochrane Handbook's recommendations (I2 values of 0‐40%: might not be important ; 30% to 60%: may represent moderate heterogeneity; 50% to 90%: may represent substantial heterogeneity; 75% to 100%: considerable heterogeneity). In addition to the I 2 value (Higgins 2003) we will present the χ2 and its p‐value and consider the direction and magnitude of the treatment effects. As in meta‐analysis with few studies the χ2 test is underpowered to detect heterogeneity should it exist, a p‐value of 0.10 is used as a threshold of statistical significance.
Assessment of reporting biases
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 (Higgins 2008). 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 were ten or fewer studies, or where all studies were of similar sizes.
Data synthesis
We understand that there a debate around the use of fixed or random‐effects models. The random‐effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects (Der‐Simonian 1986). This does seem true to us as we are a priori expecting some clinical heterogeneity between the patients in the different trials. Therefore, we have chosen the random effects model for all analyses.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analysis
We plan a subgroup analysis based on whether response to treatment depended on whether or not participants with a history of treatment resistance were included. We will also analyse whether the response of inpatients (and day hospital patients) differs from that of outpatients.
2. Heterogeneity
When we find high inconsistency of effects by the measures explained above and clear reasons explaining the heterogeneity are present, we will present the data separately. If not, we will comment on the heterogeneity of the data.
Sensitivity analysis
We will conduct the following sensitivity analyses to investigate the degree to which the effect sizes depend on the assumptions made by the reviewers: we will exclude cluster trials, cross‐over trials, imputed statistics and risk of bias assessment.
