Description of the condition
Schizophrenia is a complex neuropsychiatric disorder characterised by positive, negative and cognitive symptoms with a median lifetime prevalence of 4 per 1000 (McGrath 2008). This illness is characterised by a relapsing and remitting course with frequent residual deficits. The mainstay of treatment since the advent of chlorpromazine in the 1950s has been antipsychotic medication. Antipsychotic medications block dopamine release, reducing the psychotic symptoms of schizophrenia and reducing the risk of relapse (Crumlish 2009). A consequence of this blockade, however, is increased prolactin secretion, leading to to hyperprolactinaemia.
Prolactin is a hormone secreted largely by the anterior pituitary gland. Amongst other functions, it has an important role in regulating lactation and suppression of fertility (Grattan 2008). The secretion of prolactin by the pituitary is predominantly inhibited by dopamine release by the hypothalamus. Inadvertent dopamine blockade by antipsychotics in the nigrostriatal pathway is linked with extrapyramidal or parkinsonian side effects (Casey 2004) and similar blockade in the tuberoinfundibular region with hyperprolactinaemia (Molitch 2005). Normal prolactin levels are less than 25 µg/L for women, and 20 µg/L for men (Holt 2008).
High prolactin levels are reported in patients as early as one week after initiation of antipsychotic therapy (Turkington 1972; Marken 1992). Hyperprolactinaemia (a high prolactin level) is linked to sexual dysfunction; studies on sexual dysfunction in schizophrenia report the prevalence ranging from 25% to 60% in patients treated with antipsychotics (Demyttenaere 1998; Peuskens 1998). In women, hyperprolactinaemia can result in amenorrhoea, galactorrhoea, gynaecomastia and osteoporosis. Sexual effects of increased prolactin in women include sexual dysfunction with reduced libido, atrophic vaginitis, decreased vaginal lubrication, anorgasmia, hypogonadism and infertility (Smith 2003). In men, hyperprolactinaemia contributes to decreased libido and erectile, orgasmic and ejaculatory dysfunction (Knegtering 2004; Spollen 2004). Increased prolactin causes low levels of sex hormones, which in turn result in osteopaenia and osteoporosis (Meaney 2004). High circulating prolactin levels are implicated in increasing risk of breast cancers (Bernichtein 2010). Hyperprolactinaemia is a dose (Staller 2006) and medication dependent side effect (Wudarsky 1999; Markianos 2001), with some antipsychotics like quetiapine, clozapine and aripiprazole having prolactin sparing properties (Byerly 2009).
Description of the intervention
Aripiprazole is an atypical antipsychotic with a novel mechanism of action. Aripiprazole is licensed for the treatment of schizophrenia. This antipsychotic reduces prolactin levels compared to placebo (Belgamwar 2011). Though atypical antipsychotics are associated with fewer extrapyramidal side effects compared to the typical antipsychotics, they are associated with an adverse metabolic profile (Leucht 2009). Aripiprazole has a better metabolic profile with less weight gain and less glucose and cholesterol elevation compared to most atypical antipsychotics (Rummel-Kluge 2010).
How the intervention might work
Aripiprazole has a unique mechanism of action, being a partial dopamine agonist (Lawler 1999; Burstein 2005). It has a functionally selective action wherein a mixture of agonist, antagonist or partial agonist actions can occur (Shapiro 2003). It has dopamine antagonist activity in hyperdopaminergic states and an agonist action in hypodopaminergic states (Cada 2003). Most antipsychotics induce a hypodopaminergic state in the tuberoinfundibular system thereby inducing hyperprolactinaemia, and aripiprazole might potentially reverse this with its dopamine agonistic action thereby normalising prolactin levels.
Why it is important to do this review
Antipsychotic induced hyperprolactinaemia is a common adverse effect. Medication related adverse effects are one of the important reasons for antipsychotic noncompliance in schizophrenia (Perkins 2002). Monitoring for, and management of, adverse effects might lead to better adherence to medications (DiBonaventura 2012). The most common approaches for dealing with the high prolactin levels are reducing the antipsychotic dose, using dopamine agonists, and switching to a less prolactinaemic antipsychotic medication. All these interventions carry a risk of relapse of the psychosis, which some perceive to be worse than having hyperprolactinaemia itself (Shim 2007). We will review the potential intervention of adding aripiprazole to the existing antipsychotic regimen to treat antipsychotic induced hyperprolactinaemia, which potentially does not worsen psychosis. The augmentation of other antipsychotic medication with aripiprazole is associated with a reduction in prolactin (Shim 2007) and improvement in sexual side effects (Mir 2008). This approach has its own limitations including the risk of a worsening side-effect profile from antipsychotic polypharmacy. The pros and cons of this novel intervention need to be studied in a systematic review.
To assess the effectiveness of the addition of aripiprazole, an atypical antipsychotic, in the treatment of antipsychotic induced hyperprolactinaemia.
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 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 participants by alternate days of the week. Where people are given additional treatments within the addition of aripiprazole to the hyperprolactinaemic antipsychotic regimen, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the addition of aripiprazole that is randomised. Cross-over trials meeting the above inclusion criteria will be considered. However, data will be considered only from the first phase of the trial, the other phases will not be used to avoid any carry-over effect. As the review studies the use of aripiprazole as an adjunct to existing hyperprolactinaemic antipsychotic medication, those trials where the causal antipsychotic has been switched will be excluded.
Types of participants
Adults, however defined, with schizophrenia or related disorders, including schizophreniform disorder, schizoaffective disorder and delusional disorder, again, by any means of diagnosis. Adults should have additional evidence of hyperprolactinaemia and should be on an antipsychotic regimen.
We are interested in making sure that information is as relevant to the current care of people with schizophrenia as possible so propose to clearly highlight the current clinical state (acute, early post-acute, partial remission, remission) as well as the stage (prodromal, first episode, early illness, persistent) and as to whether the studies primarily focused on people with particular problems (for example, negative symptoms, treatment-resistant illnesses).
Types of interventions
1. Aripiprazole as an adjunct to antipsychotic medication, any route, any dose
2. Control: defined as standard care i.e. the care a person with neuroleptic induced hyperprolactinaemia would normally receive with no addition of aripiprazole
Types of outcome measures
All outcomes will be divided into short term (less than six months), medium term (seven to 12 months) and long term (over one year).
1. Clinical response
1.1 Relapse as defined clinically by each of the studies
1.2 Average endpoint or change score in global state
1.3 Clinically significant response on psychotic symptoms - as defined by each of the studies
1.4 Average endpoint or change score on psychotic symptom scale
2.1 Compliane with medication
2.2 Compliance with non-drug treatment
3. Adverse effects
3.1 Hyperprolactinaemia symptoms
3.2 Changes in prolactin levels
3.3 Changes in bone density
1. Death, suicide or natural causes
2. Leaving the study early
3. Adverse effects
3.1 Number of participants with at least one adverse effect
3.2 Clinically important specific adverse effects (extrapyramidal side effects, metabolic side effects like weight gain, hyperglycemia and hyperlipidemia, electrocardiogram (EKG) changes - QTc prolongation)
3.3 Average change and specific change in specific adverse effects
4. Quality of life or satisfaction with care for either recipients of care or carers
4.1. Significant change in quality of life or satisfaction - as defined by each of the studies
4.2 General impression of carer or other
4.3 Average score, change in quality of life, satisfaction
5. Cognitive functioning
5.1 No clinically important change in overall cognitive functioning
5.2 Average endpoint of overall cognitive functioning score
5.3 Average change of overall cognitive functioning score
6. Economic outcomes
7. Summary of findings table
We will use the GRADE approach to interpret findings (Schünemann 2008) and used GRADE profiler (GRADE Profiler) to import data from RevMan 5 (Review Manager (RevMan)) 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 anticipate including the following short or medium or long term outcomes in a summary of findings table.
1. Clinical response: relapse
2. Adverse effects: changes in prolactin levels
3. Adverse effects: changes of hyperprolactinaemia symptoms, amenorrhoea, galactorrhoea, gynaecomastia, fertility and sexual functioning
4. Adverse effects: changes in bone density
5. Leaving the study early
Search methods for identification of studies
No language restriction but studies will be limited to human participants.
Cochrane Schizophrenia Group Trials Register
We will search the register using the phrase:
[(*aripiprazole* or *abilitat* or *abilify* or *OPC?14597* in interventions of STUDY) AND (*hyperprolactinaemia* or *hyperprolactinemia* or *prolactin* in title, abstract or indexing terms of REFERENCE or outcomes of STUDY)]
This register is compiled by systematic searches of major databases, handsearches and of conference proceedings (see group module).
Searching other resources
1. Reference searching
We will inspect references of all identified 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
VK and SB will independently inspect citations from the searches and identify relevant abstracts. A random 25% sample will be independently re-inspected by PB 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 VK. Again, a random 25% of reports will be re-inspected by PB 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
SB will extract data from all included studies. In addition, to ensure reliability, VK will independently extract data from a random sample of these studies, comprising 25% of the total. Again, any disagreement will be discussed, decisions documented and, if necessary, authors of studies will be contacted for clarification. With remaining problems VM will help clarify issues and these final decisions will be documented. Data presented only in graphs and figures will be extracted whenever possible, but included only if two review authors independently have the same result. Attempts will be made to contact authors through an open-ended request in order to obtain missing information or for clarification whenever necessary. If studies are multi-centre, where possible, we will extract data relevant to each component centre separately.
Data will be extracted onto standard, simple forms.
2.2 Scale-derived data
We will include continuous data from rating scales only if:
a. the psychometric properties of the measuring instrument have been described in a peer-reviewed journal (Marshall 2000); and
b. 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, in 'Description of studies' we will note if this is the case or not.
2.3 Endpoint versus change data
There are advantages of both endpoint and change data. Change data can remove a component of between-person variability from the analysis. On the other hand calculation of change needs two assessments (baseline and endpoint), which can be difficult in unstable and difficult to measure conditions such as schizophrenia. We have decided to primarily use endpoint data, and only use change data if the former are not available. Endpoint and change data will be combined in the analysis as we will use weighted mean differences (MD) rather than standardised mean differences throughout (Higgins 2011, Chapter 126.96.36.199 ).
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 started from a positive value (such as Positive and Negative Syndrome Scale (PANSS), which can have values from 30 to 210) the calculation described above was modified 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 endpoint and these rules can be applied. Skewed data from studies of less than 200 participants will be entered as other data within the data and analyses section rather than into a statistical analysis. Skewed data pose less of a problem when looking at means if the sample size is large and will be entered into syntheses.
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 and will be entered into statistical 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 (for example 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 PANSS (Kay 1986), this could be considered as a clinically significant response (Leucht 2005; Leucht 2005a). For prolactin levels the improvement will be defined as final prolactin within the normal range (prolactin at 25 µg/L for women, and 20 µg/L for men). 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 aripirazole addition to antipsychotic medication. Where keeping to this makes it impossible to avoid outcome titles with clumsy double-negatives (for example '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 VK and SB will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) to assess trial quality. This set of criteria is based on evidence of associations between overestimation 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, authors of the studies will be contacted 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 to, again, resolution will be made 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 1.
Measures of treatment effect
1. Binary data
For binary outcomes we will calculate a standard estimation of the risk ratio (RR) and its 95% confidence interval (CI). It has been shown that RR is more intuitive (Boissel 1999) than odds ratios and that odds ratios tend to be interpreted as RRs by clinicians (Deeks 2000). The number needed to treat or to harm (NNT/H) statistic with its confidence interval is intuitively attractive to clinicians but is problematic both in its accurate calculation in meta-analyses and the interpretation (Hutton 2009). For binary data presented in the 'Summary of findings' tables, 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 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 intra-class correlation coefficient (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 intra-class correlation coefficients and relevant data documented in the report, synthesis with other studies would 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 (for example 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 the 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 188.8.131.52 (Combining groups) of the Cochrane Handbook for Systematic Reviews of Interventions. Where the additional treatment arms are not relevant, these data will not be reproduced.
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 by down-rating quality. Finally, we will also downgrade quality within the 'Summary of findings' table should loss be 25% to 50% in total.
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 testing how prone the primary outcomes are to change when data only from people who complete the study to that point are compared to the intention-to-treat analysis using the above assumptions.
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 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 confidence intervals available for group means, and either a P value or t value available for differences in means, we can calculate them according to the rules described in the Cochrane Handbook for Systemic reviews of Interventions (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 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 the 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 inspect all included studies initially, 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 inspect all included studies initially, 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 I
Heterogeneity between studies will be investigated by considering the I
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 of the Cochrane Handbook for Systematic 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.
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 will choose a 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
We anticipate subgroup analyses investigating 'aripiprazole addition to typical antipsychotic regimen' and 'aripiprazole addition to atypical antipsychotic regimen', as typical and atypical antipsychotics have different pharmacological profiles.
1.2 Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of aripiprazole augmentation for people with schizophrenia in general. 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, the graph will be visually inspected and studies outside of the company of the rest will be successively removed to see if homogeneity is restored. For this review we decided that this should occur with data contributing to the summary finding of no more than around 10% of the total weighting, where data will be presented. If not, data are not 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.
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 descriptions 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 assumption compared with completer data only. If there is a substantial difference, we will report results and discuss them but continue to employ our assumption.
Where assumptions have to be made regarding missing SDs data (see Dealing with missing data), we will compare the findings on primary outcomes when we use our assumption compared with complete data only. A sensitivity analysis will be undertaken testing how prone results are to change when 'completer' data only are compared to the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them but continue to employ our assumption.
3. Risk of bias
We will analyse the effects of excluding trials that are 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 the 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 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 the greater weights assigned to larger trials with greater event rates altered the significance of the results compared to the more evenly distributed weights in the random-effects model.
The Cochrane Schizophrenia Group Editorial Base in Nottingham produces and maintains standard text for use in the Methods section of their reviews. We have used this text as the basis of what appears here and adapted it as required.
Contributions of authors
Venkata B Kolli - helped write protocol
Prasad Bestha - helped write protocol
Vishal Madaan - helped write protocol
Seenaiah Byreddy - helped write protocol
Declarations of interest
Venkata B Kolli - I am participating as a rater/co-investigator for the following studies but did not receive any monetary or travel compensation: Otsuka Pharmaceuticals, once weekly aripiprazole for tic disorder, Roche Glycine reuptake inhibitor RG1678 for Schizophrenia. Sponsored by Veterans Affairs, United States, VA Augmentation and Switching Treatments for Improving Depression Outcomes (VAST-D). Southern California Institute for Research and Education: Vilazodone for the Treatment of Posttraumatic Stress Disorder
Vishal Madaan - There is no known conflict of interest regarding this current manuscript. Outside of this, I am employed by the University of Virginia Health System, Charlottesville, VA. Based on the clinical trials that have been contracted with the University of Virginia, I have served as or am serving as (or will serve as) Principal Investigator for some of the multicentric clinical trials conducted by Shire, Pfizer, Merck, Lilly, Otsuka and Forest. I am on the editorial board for the American Psychiatric Association's Focus Self Assessment Editorial Board and have served as a consultant for the NOW Coalition for Bipolar Disorder.
Seenaiah Byreddy - none known.
Prasad Bestha - none known.
Sources of support
- Creighton University, USA.
- No sources of support supplied