Interventions for antipsychotic‐induced amenorrhoea
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the clinical effectiveness and safety of various treatments for antipsychotic‐induced amenorrhoea.
Background
Schizophrenia is a severe mental illness characterised by positive symptoms such as hallucinations and delusions, and negative symptoms such as social withdrawal and lack of affect. Its prevalence in adults is reported to be between 0.5% and 1.5% (Messias 2007). The management of schizophrenia and related disorders was revolutionised in the 1950s with the introduction of antipsychotic medications (Turner 2007). These medications are effective in the control of florid positive symptoms of psychoses (Adams 2014). In addition to their therapeutic action in acute psychotic episodes, maintenance therapy with antipsychotic drugs is associated with reduced risk of relapse (Leucht 2013)
However, antipsychotic medications have been associated with a range of adverse effects in both the short as well as in the long term. Short‐term adverse effects include extrapyramidal symptoms like tremors, rigidity and excessive salivation, and some antipsychotics also carry a long‐term risk of probable non‐reversible effects such as tardive dyskinesia (Divac 2014). Newer antipsychotics also have a particular risk of metabolic syndrome (Rummel‐Kluge 2010). Other adverse effects can affect women of reproductive age, who have an increased risk of experiencing endocrinological, metabolic and neurological adverse effects from antipsychotic medication (Seeman 2009).
Description of the condition
Menstrual dysfunction such as amenorrhoea (absence of menstruation) and oligomenorrhoea (infrequent or light menstruation) has multiple causes which can include developmental problems with reproductive organs, thyroid disease, stress, excessive weight loss and hyperprolactinaemia (high levels of prolactin production).
Hyperprolactinaemia is a significant endocrine effect that can be caused by antipsychotic medication. Conventional antipsychotics can cause dose‐dependent blockade of D2 receptors on lactotroph cells, removing the main inhibitory influence on prolactin level and causing hyperprolactinaemia. This is defined as a level above the upper limit of normal (> 24.20 ng/ml for females and > 18.77 ng/ml for males). Elevation of prolactin levels occurs within a few hours of treatment initiation and persists with long‐term treatment (Smith 2002). Women have significantly greater prolactin elevations than men during chronic antipsychotic treatment with equivalent doses (Bushe 2007; Madhusoodanan 2010; Pueskens 2014) .
Antipsychotic‐induced menstrual dysfunction has prevalence rates of approximately 45% for oligomenorrhoea/amenorrhoea and 19% for galactorrhoea (Kinon 2003; Wieck 2003). An illness‐related under‐function of the hypothalamic‐pituitary‐gonadal axis in women with schizophrenia may also contribute to menstrual irregularities. This review will focus on amenorrhoea. In an extensive study conducted in India, the prevalence of amenorrhoea in women on risperidone was 60% (Paul 2013).
Description of the intervention
There are several different interventions currently practiced by clinicians across different cultures to help reduce the symptoms of antipsychotic‐induced amenorrhoea.
1. Reduction of dose (antipsychotic drug)
Evidence shows that hyperprolactinaemia and resultant clinical amenorrhoea is often dose dependent (La Torre 2007) and that reducing the dose of prolactin‐raising antipsychotics whenever possible is often one of the first management strategies clinicians employ for antipsychotic‐induced oligomenorrhoea/amenorrhoea and galactorrhoea (Haddad 2004).
When oral antipsychotic therapy is discontinued, baseline prolactin levels may take up to three weeks to return to the normal range depending on the half‐life of the drug and its metabolites as well as storage in fatty tissues (Turkington 1972). In the case of depot medication, normalisation may take as long as four to six months (Wistedt 1981).
2. Switching antipsychotic drug (changing to a non‐prolactin raising antipsychotic)
Quetiapine (Keller 2002),olanzapine,aripiprazole and ziprasidone (Bargiota 2013) have higher 5‐HT2A:D2 binding ratios and differential effects on dopamine neurotransmission, with less interference in the tuberoinfundibular pathway resulting in no or insignificant change in prolactin level. Doses of the above antipsychotic drugs can be chosen to replace the drug that has caused the problems.
3. Adjunct use of dopamine agonists (e.g. bromocriptine)
Bromocriptine is a potent post‐synaptor dopamine agonist and is known to significantly reduce prolactin levels in patients with physiologically‐elevated prolactin levels and in patients with hyperprolactinaemia due to any cause. Bromocriptine has found its place in treatment of antipsychotic‐related hyperprolactinaemia and consequent clinical amenorrhoea/galactorrhoea (Lee 2010) however the benefits need to be balanced with the risk of a psychotic relapse for those on antipsychotics.
4. Alternative medicines ‐ (e.g. Chinese herbal medicines, jasmine flower extract)
Peony‐Glycyrrhiza decoction (PGD), a traditional chinese herbal preparation prepared by mixing sliced and broiled Paenoia and Glycyrrhiza radices through a standardised water extraction process is thought to help people with schizophrenia who have high prolactin levels due to antipsychotic drugs, without exacerbation of psychosis or change in any other hormones (Yuan 2008).
In South India the flower of the jasmine (Jasminum Sambac) is traditionally used to suppress puerperal lactation. Intranasally‐administered extract of jasmine flowers is known to reduced antipsychotic drug‐related hyperprolactinaemia and can probably be a more cost‐effective option as compared to dopamine agonists (Finny 2005).
How the intervention might work
Dopamine inhibits prolactin release and so dopamine antagonists (antipsychotic drugs) can be expected to increase prolactin plasma levels. The degree of prolactin elevation is probably dose‐related (Staller 2006). Hence, the reduction in dose of antipsychotic drug is expected to reduce prolactin level and thereby reverse menstrual dysfunction. Some antipsychotic drugs such as clozapine, olanzapine, quetiapine, aripiprazole and ziprasidone do not increase prolactin above the normal range at standard doses (Haddad 2004). When there are issues related to prolactin, a rational option would be to change to a non‐prolactin raising atypical antipsychotic drug (Keller 2002; Shim 2007). For women who need to remain on prolactin‐elevating antipsychotic drugs, adjunctive use dopamine agonists (bromocriptine (Duncan 1995), amantadine (Hammer 1998) and cabergoline (Cavallaro 2004)) may be an option. We are unclear how PGD and jasmine flower may be effective (Finny 2005; Yuan 2008)
Why it is important to do this review
Antipsychotic‐induced menstrual dysfunction, if not addressed, not only affects compliance with treatment in women suffering from schizophrenia or similar illnesses, but also is a major cause of distress. Amenorrhoea can have physical (for example, bone mineral density changes) and psychological consequences that affect well‐being (Haddad 2004). Although several interventions are used by clinicians, there has been no consensus regarding interventional strategies for antipsychotic‐induced amenorrhoea, nor a systematic review of the evidence of the effects of these strategies.
Objectives
To assess the clinical effectiveness and safety of various treatments for antipsychotic‐induced amenorrhoea.
Methods
Criteria for considering studies for this review
Types of studies
We will include 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). We will exclude quasi‐randomised studies, such as those allocating by alternate days of the week. Where people are given treatments additional to the chosen amenorrhoea intervention, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the chosen amenorrhoea intervention that is randomised.
Types of participants
Women of reproductive age who have schizophrenia or related disorders (including schizophreniform disorder, schizoaffective disorder and delusional disorder) and have antipsychotic‐induced amenorrhoea, by any means of diagnosis.
We define amenorrhoea as a temporary or permanent loss of menstrual periods, lasting longer than 3 consecutive cycles in a previously regular menses or previously irregular menses for 6 months. This is in context of a normal menstrual cycle defined as occurring every 21 to 35 days (David 2013).
We will only include trials where the majority (> 50%) of participants have a severe mental illness which was likely to be schizophrenia.We will not include trials where the sole diagnosis is bipolar or affective disorder.
We are interested in making sure that information is relevant to the current care of people with schizophrenia. We propose to highlight the participants' current clinical state (acute, early post‐acute, partial remission, remission) as well as the stage (prodromal, first episode, early illness, persistent) and whether the studies primarily focused on people with particular problems (for example, negative symptoms, treatment‐resistant illnesses).
Types of interventions
-
Antipsychotic drug ‐ reduction of dose
-
Antipsychotic drug ‐ changing to another antipsychotic drug
-
Use of other drugs ‐ e.g. metformin
-
Traditional remedies
-
Placebo or standard treatment
Types of outcome measures
We aim to divide all outcomes into short term (less than six months), medium term (seven to twelve months) and long term (over one year).
Primary outcomes
1. Amenorrhoea
1.1 Clinically‐important changes in amenorrhoea symptoms ‐ as defined by individual studies
2. Adverse events
2.1 Clinically‐important specific adverse effects (such as bone density loss, cardiovascular effects)
Secondary outcomes
1. Menstrual effects
1.1 Any change in menstrual cycle (cessation, change in pattern)
1.2 Significant changes in serum prolactin levels ‐ as defined by individual studies
1.3 Average endpoint/change score on menstrual measure
2. Satisfaction with treatment
2.1 Patient satisfaction with treatment
2.2 Carer satisfaction with treatment
2.3 Average endpoint/change score on satisfaction scale
3. Global state
3.1 Relapse ‐ as defined by individual studies
3.2 Clinically‐important change in global state ‐ as defined by individual studies
3.3 Any change in global state ‐ as defined by individual studies
3.4 Average endpoint/change score on global state scale
4. Mental state
4.1 Clinically‐important change in mental state ‐ as defined by individual studies
4.2 Any change in mental state ‐ as defined by individual studies
4.3 Average endpoint/change score on mental state scale
5. Compliance
5.1 Compliance with medication
5.2 Compliance with non‐drug treatment
6. Adverse event/effects
6.1 Anticholinergic.
6.2 Cardiovascular
6.3 Central nervous system
6.4 Gastrointestinal
6.5 Endocrine (e.g. amenorrhoea, galactorrhoea, hyperlipidaemia, hyperglycaemia, hyperinsulinaemia)
6.6 Haematology (e.g. haemogram, leukopenia, agranulocytosis/neutropenia)
6.7 Hepatitic (e.g. abnormal transaminase, abnormal liver function)
6.8 Metabolic
6.9 Movement disorders
6.10 Various other specific events/effects
6.11. Average endpoint/change score adverse event/effect scale
7. Leaving the study early
7.1 Any reason
7.2 Due to adverse effect
8. Quality of life
8.1 Clinically‐important change in quality of life ‐ as defined by individual studies
8.2 Any change in quality of life ‐ as defined by individual studies
8.3 Average endpoint/change score on quality of life scales
9. Economic outcomes
9.1 Direct and indirect cost of treatment
'Summary of findings' table
We will use the GRADE approach to interpret findings (Schünemann 2011) and use GRADEpro to import data from 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 rate as important to patient care and decision making. We aim to select the following main outcomes for inclusion in the 'Summary of findings' table:
-
Amenorrhoea: clinically‐important changes in menstrual cycle symptoms ‐ as defined by individual studies
-
Adverse effect: clinically‐important specific adverse effects ‐ as defined by individual studies
-
Menstrual effects: important reduction in serum prolactin level ‐ as defined by individual studies
-
Satisfaction ‐ participant satisfied with treatment
-
Global state: relapse
-
Leaving the study early
-
Quality of life: clinically‐important change in quality of life ‐ as defined by individual studies
Search methods for identification of studies
Electronic searches
1. Cochrane Schizophrenia Group’s Trials Register
The Information Specialist will search the Cochrane Schizophrenia Group’s Study‐Based Register of Trials using the following search strategy:
(*menstru* OR *menorrh* OR *prolactin*) in Healthcare Condition Field of STUDY
The Cochrane Schizophrenia Group’s Register of Trials is compiled by systematic searches of major resources (including AMED, BIOSIS, CINAHL, Embase, MEDLINE, PsycINFO, PubMed, and registries of clinical trials) and their monthly updates, handsearches, grey literature, and conference proceedings (see Group Module). There are no language, date, document type, or publication status limitations for inclusion of records into the register.
Searching other resources
1. Reference searching
We will inspect references of all 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
JPR and SD will independently inspect citations from the searches and identify relevant abstracts. Prathap Tharyan (PT) will independently re‐inspect a random 20% sample to ensure reliability. JPR and SD will obtain and inspect full reports of the abstracts that meet the review criteria and references/abstracts on which the authors disagree. Again, PT will re‐inspect a random 20% of these full reports 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
JPR and SD will extract data from all included studies. In addition, to ensure reliability, JPR and SD will independently extract data from a random sample of these studies, comprising 10% of the total. We will discuss any disagreement and document our decisions. If necessary, we will contact authors of studies for clarification. With remaining problems PT will help clarify issues and we will document these final decisions. We will attempt to extract data presented only in graphs and figures whenever possible, but will include these data only if both review authors independently reach 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‐based, wherever 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:
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.
c. the instrument should be a global assessment of an area of functioning and not sub‐scores which are not, in themselves, validated or shown to be reliable. However there are exceptions, we will include sub‐scores from mental state scales measuring positive and negative symptoms of schizophrenia.
Ideally the measuring instrument should either be i. a self‐reported one or ii. completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly. In the Description of studies section 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. We aim to combine endpoint and change data in the analysis as we prefer to use mean differences (MDs) rather than standardised mean differences (SMDs) throughout (Higgins 2011a).
2.4 Skewed data
Continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non‐parametric data, we will apply the following standards to relevant data before inclusion.
Please note, we will enter data from studies of at least 200 participants into the analysis irrespective of the following rules because skewed data pose less of a problem in large studies. We will also enter change data, as when continuous data are presented on a scale that includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. We will present and enter change data into statistical analyses.
For endpoint data N < 200
(a) When a scale starts from the finite number zero, we will subtract the lowest possible value from the mean, and divide this by the standard deviation (SD). If this value is lower than one, it strongly suggests a skew and we will exclude these data. If this ratio is higher than one but below two, there is suggestion of skew. We will enter these data and test whether their inclusion or exclusion changes the results substantially. Finally, if the ratio is larger than two we will include these data, because skew is less likely (Altman 1996; Higgins 2011a).
b) If a scale starts from a positive value (such as the Positive and Negative Syndrome Scale (PANSS);Kay 1986) 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 2 SD > (S‐S min), where S is the mean score and 'S min' is the minimum score.
2.5 Common measures
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, we will make efforts to convert outcome measures to dichotomous data. This can be done by identifying cut‐off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that if there is a 50% reduction in a scale‐derived score such as the Brief Psychiatric Rating Scale (BPRS, Overall 1962) or the PANSS, this could be considered as a clinically‐significant response (Leucht 2005a; Leucht 2005b). 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 either reduction in antipsychotic, use of bromocriptine or any other medication, use of Chinese herb extracts or jasmine or switch to any other antipsychotic. Where keeping to this makes it impossible to avoid outcome titles with clumsy double‐negatives (e.g. 'Not un‐improved') we will report data where the left of the line indicates an unfavourable outcome, and make notes in the relevant graphs.
Assessment of risk of bias in included studies
JPR and SD will work independently to assess risk of bias using criteria described in the Cochrane Handbook (Higgins 2011b) 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 in domains 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. 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. We will report non‐concurrence in quality assessment, but if disputes arise as to which classification a trial is to be given, again, we will find a resolution through discussion.
We will note the level of risk of bias 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).
2. Continuous data
For continuous outcomes we aim to estimate MD between groups. We prefer not to calculate effect size measures (SMD). However, if scales of very considerable similarity are used, we will presume there was 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, CIs unduly narrow and statistical significance is 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 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 received statistical advice 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 from the first phase of cross‐over studies.
3. Studies with multiple treatment groups
Where a study involves more than two treatment arms, if relevant, the additional treatment arms will be presented in comparisons. If data are binary we will simply add and combine within the two‐by‐two table. If data are continuous we will combine data following the formulae in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 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). If, for any particular outcome, more than 50% of data are unaccounted for, we will not reproduce these data or use them within analyses, except for the outcome of leaving the study early. If, however, more than 50% of those in one arm of a study are lost, but the total loss was less than 50%, we will mark such data with (*) to indicate that such a result may well be prone to bias.
2. Binary data
In the case where attrition for a binary outcome is between 0% and 50% and where these data are not clearly described, data will be presented 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 sensitivity analysis (see 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 Attrition
We will use data where attrition for a continuous outcome is between 0% and 50%, and data only from people who complete the study to that point are reported.
3.2 Standard deviations
If standard deviations (SDs) are not reported, we will try to obtain the missing values from the authors. If these are not available, where there are missing measures of variance for continuous data, but an exact standard error (SE) and CIs available for group means, and either P value or t value available for differences in mean, we can calculate SDs according to the rules described in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011). When only the SE is reported, SDs are calculated by the formula SD = SE * √(n). Chapters 7.7.3 and 16.1.3 of the Cochrane Handbook for Systematic Reviews of Interventions present detailed formulae for estimating SDs from P, t or F values, CIs, ranges or other statistics (Deeks 2011). If these formulae do not apply, we will calculate the SDs according to a validated imputation method which is based on the SDs of the other included studies (Furukawa 2006). Although some of these imputation strategies can introduce error, the alternative would be to exclude a given study’s outcome and thus to lose information. Nevertheless, we will examine the validity of the imputations in a sensitivity analysis that excludes imputed values.
3.3 Assumptions about participants who left the trials early or were lost to follow‐up
Various methods are available to account for participants who left the trials early or were lost to follow‐up. Some trials just present the results of study completers; others use the method of last observation carried forward (LOCF); while more recently, methods such as multiple imputation or mixed‐effects models for repeated measurements (MMRM) have become more of a standard. While the latter methods seem to be somewhat better than LOCF (Leon 2006), we feel that the high percentage of participants leaving the studies early and differences between groups in their reasons for doing so is often the core problem in randomised schizophrenia trials. We will therefore not exclude studies based on the statistical approach used. However, by preference we will use the more sophisticated approaches, i.e. we will prefer to use MMRM or multiple imputation to LOCF, and we will only present completer analyses if some kind of ITT data are not available at all. Moreover, we will address this issue in the item 'Incomplete outcome data' of the 'Risk of bias' tool.
Assessment of heterogeneity
1. Clinical heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will simply inspect all studies for clearly outlying people or situations which we had not predicted would arise. When such situations or participant groups arise, we will discuss these in full.
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, we will discuss these in full.
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
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 CI for I2). We will interpret an I2 estimate greater than or equal to around 50% accompanied by a statistically‐significant Chi2 statistic, as evidence of substantial levels of heterogeneity (Deeks 2011). When substantial levels of heterogeneity are found in the primary outcome, we will explore reasons for heterogeneity (see Subgroup analysis and investigation of heterogeneity).
Assessment of reporting biases
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are described in Chapter 10 of the Cochrane Handbook for Systematic Reviews of Interventions (Sterne 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 ten or fewer studies, or where all studies are of similar size. In other cases, where funnel plots are possible, we will seek statistical advice in their interpretation.
Data synthesis
We understand that there is no closed argument for preference for use of fixed‐effect or random‐effects models. The random‐effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This often seems to be true to us and the random‐effects model takes into account differences between studies even if there is no statistically‐significant heterogeneity. There is, however, a disadvantage to the random‐effects model. It puts added weight onto small studies which often are the most biased ones. Depending on the direction of effect these studies can either inflate or deflate the effect size. We choose to apply a random‐effects model for all analyses.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses ‐ only primary outcomes
We propose to provide an overview of the effects of reduction in dose, changing the antipsychotic, addition of bromocriptine, use of Chinese extracts and Indian jasmine for people with schizophrenia who have developed antipsychotic‐induced amenorrhoea. 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
We will report if inconsistency is high. 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 heterogeneity is restored. For this review we have decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, we will present such data. If not, we will not pool data and will discuss relevant issues. We know of no supporting research for this 10% cut off but are investigating the 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. Implied 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 enter data from these trials and if their inclusion does not result in a substantive difference, they will remain in the analysis. 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.
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 (see Dealing with missing data), we will compare the findings on primary outcomes when we use our assumption compared with complete data only. We will undertake a sensitivity analysis 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
For the primary outcomes 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). 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 relevant data from these trials in the analysis
4. Imputed values
For the primary outcomes, 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 models
We will synthesise all data 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 alter the significance of the results compared to the more evenly distributed weights in the random‐effects model.
