Summary of findings
Description of the condition
Postnatal psychosis is almost always a mood disorder accompanied by features such as loss of contact with reality, hallucinations, severe thought disturbance, and abnormal behaviour. It is a worldwide, life-threatening condition with abrupt onset within a month of childbirth. Symptoms rapidly reach a climax of severity in new mothers developing frank psychosis, cognitive impairment, and disorganised behaviours that affect functioning (Sit 2006).
Some women have typical manic symptoms, such as euphoria, overactivity, decreased sleep requirement, loquaciousness, flight of ideas, increased sociability, disinhibition, irritability and delusions, which are usually grandiose or religious in content. Others have severe depression with delusions, auditory hallucinations, mutism, stupor or transient swings into hypomania. Some switch from mania to depression (or vice versa) within the same episode. Atypical features include perplexity, confusion, emotional states including extreme fear and ecstasy, catatonia or rapid changes of mental state with transient delusional ideas .The most commonly recalled symptoms are feeling excited, elated or high, not needing to sleep or inability to sleep, feeling active or energetic and talking more or feeling very chatty (Heron 2008). Sadly, postnatal psychosis can lead to the mother neglecting, harming and even killing her baby, in addition to an increased risk of suicide.
Postnatal Psychosis affects approximately one to two in every 1000 new mothers within a few days of childbirth (Spinelli 2009), and it follows an episodic course. It can last many months without treatment, but usually resolves within a few weeks with modern therapy. Postnatal psychosis is more common in first time mothers, and it appears to have a specific heritable factor (Jones 2001) with probable linkage to chromosome 16 (Jones 2007). Factors that increase the risk of postnatal psychosis include primiparous mothers who are single, who are older (Nager 2005; Valdimarsdottir 2009), or with a past psychiatric history and family history of affective psychosis in first or second degree relatives (Benvenuti 1992; Garfield 2004; Marks 1992; McNeil 1986; Schopf 1994), prenatal depression (Ebeid 2010) and autoimmune thyroid dysfunction (Bergink 2011). Mothers who have experienced a previous postnatal psychosis are at significant risk of future episodes, some of which occur after other children are born, some during pregnancy or after an abortion, and some unrelated to childbearing (Benvenuti 1992; Pfuhlmann 1999; Robertson 1995; Robling 2000; Schopf 1994; Terp 1999; Videbech 1995). The risk of a future postnatal recurrence of a psychotic episode lies between 25% and 57% and the risk of non-postnatal relapse is even higher.
Description of the intervention
This review focuses on prevention of the postnatal psychosis. Its treatment, however, is a psychiatric emergency, with inpatient psychiatric treatment essential to ensure the safety of mother and baby. Treatment should be guided by the symptom profile (Sharma 2003). Acute treatment involves the issue of mood stabilisers, antipsychotics and benzodiazepines. Insomnia should be treated aggressively (Chaudron 2003; Sharma 2003). Electro-convulsive therapy is highly effective (Reed 1999) and should be considered for management of illness that is unresponsive to conventional therapy or when a quick resolution is required because of illness severity or safety concerns (Sharma 2003). The neuroendocrine role in the pathophysiology of postpartum disorders suggests that hormone replacement may be therapeutic in postpartum affective states (Ahokas 2000).
Preventive interventions for postnatal psychosis aim at identifying women with risk factors, early recognition of imminent psychosis through screening, and preventive drug therapy (Sharma 2003). Mood stabilisers, antipsychotic drugs (Chaudron 2003; Sit 2006) and hormone therapy (Ahokas 2000) may be beneficial in the prevention of postnatal psychotic episodes in women at high risk.
How the intervention might work
The causes of postnatal psychosis are still poorly understood. Hormonal fluctuations are associated with increased risk of affective dysregulation and mood episodes in women with bipolar disorder (Freeman 2002), and there may be a genetic basis for the trait of postpartum mood symptoms in women with bipolar disorder (Payne 2008). A review of available studies supports a link between postpartum psychosis and bipolar disorder, with implications for perinatal prophylactic treatment (Chaudron 2003). Preventive interventions for postnatal psychosis might work through early diagnosis and prophylactic treatment with mood stabilisers and antipsychotic drugs. Risk factors can be easily identified and are highly predictive (Oates 2000; RCOG 2001), and early detection may be followed by a variety of other interventions. Lithium is the mood stabiliser with the most evidence for prophylaxis of psychosis (Grof 2000). Given either in late pregnancy or immediately after delivery, lithium may prevent the development of postnatal psychosis in high-risk women (Cohen 1995; Stewart 1991; Viguera 2000). In addition, preventing sleep loss near delivery may avert an episode of postpartum psychosis (Sharma 2003a).
Why it is important to do this review
Given the high risk of relapse and recurrence in women with postpartum psychosis, prophylaxis is imperative (Sit 2006). In addition, postnatal psychosis has serious consequences for the mother and the newborn. Potential risks include suicide (Appleby 1998; Babu 2008), child neglect and abuse (Chandra 2002; Chandra 2006), or infanticide (Spinelli 2004). Prevention could, therefore, save the lives of both the mother and her baby, improve the mother-baby relationship, and save family relationships and economical status. This review is important because it summarises the best available evidence for the benefits and harms of preventive interventions for postnatal psychosis.
To investigate the best available evidence for interventions aimed at preventing postnatal psychosis.
Criteria for considering studies for this review
Types of studies
All relevant randomised controlled trials. If a trial was described as 'double blind' but implied randomisation, we planned to include such trials in a sensitivity analysis (see Sensitivity analysis). If their inclusion did not result in a substantive difference, they would have remained in the analyses. If their inclusion did result in important clinically significant, but not necessarily statistically significant differences, we would not have added the data from these lower quality studies to the results of the better trials, but would have presented such data within a subcategory. Quasi-randomised studies, such as those allocating by alternate days of the week were not eligible for inclusion.
Types of participants
Pregnant women at increased risk of postnatal psychosis, e.g., women with a personal history of postpartum psychosis and related disorders, or a family history of postpartum psychosis and related disorders.
Types of interventions
1. Interventions aimed at preventing the development of postnatal psychosis
For example, mood stabilisers, antipsychotic medications or oestrogen prophylaxis given prior to the presentation of psychotic symptoms either before birth or directly postpartum.
2. Placebo, no intervention, usual care or any other intervention
Types of outcome measures
Considering that postnatal psychosis usually resolves within a few weeks with modern therapy (see Background), we intended to divide all outcomes into short term (less than one month), medium term (one to three months) and long term (more than three months).
1. Clinical global state
1.1 Occurrence of postnatal psychosis
1.2 Clinically important change in global state
1.3 Average endpoint global state score
1.4 Average change in global state scores
2. Leaving the study early
5. Well-being and quality of life measure
5.1 Clinically important change in quality of life
5.2 Average endpoint quality of life score
5.3 Average change in quality of life scores
5.4 Clinically important change in specific aspects of quality of life
5.5 Average endpoint specific aspects of quality of life
5.6 Average change in specific aspects of quality of life
1. Death of natural causes
2. Mental state
2.1 Any change in general mental state
2.2 Average endpoint general mental state score
2.3 Average change in general mental state scores
2.4 Clinically important change in specific symptoms
2.5 Any change in specific symptoms
2.6 Average endpoint specific symptom score
2.7 Average change in specific symptom scores
3.1 Clinically important change in general behaviour
3.2 Any change in general behaviour
3.3 Average endpoint general behaviour score
3.4 Average change in general behaviour scores
3.5 Clinically important change in specific aspects of behaviour
3.6 Any change in specific aspects of behaviour
3.7 Average endpoint specific aspects of behaviour
3.8 Average change in specific aspects of behaviour
4. Satisfaction with treatment
4.1 Leaving the study early
4.2 Recipient of care satisfied with treatment
4.3 Recipient of care average satisfaction score
4.4 Recipient of care average change in satisfaction scores
4.5 Carer satisfied with treatment
4.6 Carer average satisfaction score
4.7 Carer average change in satisfaction scores
5. General functioning
5.1 Clinically important change in general functioning
5.2 Average endpoint general functioning score
5.3 Average change in general functioning scores
5.4 Clinically important change in specific aspects of functioning, such as mother-baby relationship
5.5 Average endpoint specific aspects of functioning, such as mother-baby relationship
5.6 Average change in specific aspects of functioning, such as mother-baby relationship
6. Service outcomes
6.1 Time to hospitalisation
6.2 Days in hospital
6.3 Change in hospital status
7. Adverse effects
7.1 Any general adverse effects
7.2 Average endpoint general adverse effect score
7.3 Average change in general adverse effect scores
7.4 Clinically important change in specific adverse effects
7.5 Any change in specific adverse effects
7.6 Average endpoint specific adverse effects
7.7 Average change in specific adverse effects
8. Adverse effects affecting the baby
(Any adverse effects reported by the researchers, e.g. poor hydration, sedation, poor feeding, weight gain, signs of hepatic and haematological impairment, as well as being placed in care)
8.1 Any general adverse effects
8.2 Average endpoint general adverse effect score
8.3 Average change in general adverse effect scores
8.4 Clinically important change in specific adverse effects
8.5 Any change in specific adverse effects
8.6 Average endpoint specific adverse effects
8.7 Average change in specific adverse effects
9.1 Direct costs
9.2 Indirect costs
10 'Summary of findings' table
We were to use the GRADE approach to interpret findings (Schünemann 2008) and use GRADE profiler (GRADE PRO) to import data from RevMan 5 (Review Manager) to create a 'Summary of findings' table. This table provides 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 aimed to select the following main outcomes for inclusion in the 'Summary of findings' table.
- Recurrence of postnatal psychosis
- Service utilisation outcomes
- Adverse effects
Search methods for identification of studies
No language restriction were applied, within the limitations of the search.
1. Cochrane Schizophrenia Group Trials Register (26 October 2012)
We searched the register using the phrase:
[*post?natal* OR *post?partum* OR *baby?blues* OR *Puerperal* OR (*post* AND * natal*) OR (* baby* AND *blues*) OR (*post* AND *partum*) in title, abstract, index terms of REFERENCE]
This register is compiled by systematic searches of major databases, handsearches and conference proceedings (see group module).
2. Cochrane Central Register of Controlled Trials (CENTRAL) (26 October 2012)
#1 post natal or post-natal or postnatal in Trials
#2 post partum or post-partum or postpartum in Trials
#3 baby blues or baby-blues in Trials
#4 puerperal in Trials
#5 (#1 OR #2 OR #3 OR #4)
#6 sr-depressn in Trials
#7 (#5 AND #6)
Searching other resources
1. Reference searching
We planned to inspect references of all identified studies for further relevant studies.
2. Personal contact
We intended to contact the first author of each included study for information regarding unpublished trials.
Data collection and analysis
We did not find any relevant studies that we could include in this review. As such, we were unable to carry out most of the prestated methodology. We describe the methods we planned to use if we had found relevant studies.
We planned to perform the review and meta-analyses following the recommendations of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). The analyses would have been performed using Review Manager (RevMan 5.1).
Selection of studies
Thee review authors (SA, AG and NE) independently inspected citations from the searches and identified relevant abstracts. A random 20% sample of these citations were independently re-inspected by AE to ensure reliability. Full reports of the abstracts meeting the review criteria, plus the citations review authors disagreed on, were obtained and inspected by SA, AG and NE. Again, a random 20% of these full abstracts were re-inspected by AE in order to ensure the reliability of the selection process. If it had not been possible to resolve disagreement by discussion, we would have attempted to contact the authors of the study for clarification.
Data extraction and management
Review authors SA, AG and NE planned to extract data from all included studies. In addition, to ensure reliability, AE would have independently extracted data from a random sample of these studies, comprising 10% of the total. Again, any disagreement would have been discussed, decisions documented and, if necessary, we would have contacted authors of studies for clarification. With remaining problems, AE would have helped clarify issues and these final decisions would have been documented. We planned to extract data presented only in graphs and figures whenever possible, but the data would only have been included if two review authors independently had the same result. Attempts would have been made to contact authors through an open-ended request in order to obtain missing information or for clarification whenever necessary. If studies were multi-centre, where possible, we would have extracted data relevant to each component centre separately.
We planned to extract data onto standard, simple forms.
2.2 Scale-derived data
We planned to include continuous data from rating scales only if:
a. the psychometric properties of the measuring instrument had been described in a peer-reviewed journal (Marshall 2000); and
b. the measuring instrument had not been written or modified by one of the trialists for that particular trial.
Ideally, the measuring instrument should either be i. a self-report or ii. completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly, therefore, in Description of studies, we would have noted if this was 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 intended primarily to use endpoint data, and only to use change data if the former were not available. Endpoint and change data would have been combined in the analysis as we planned to use mean differences (MD) rather than standardised mean differences (SMD) throughout (Higgins 2011).
2.4 Skewed data
Continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non-parametric data, we aimed to apply the following standards to all data before inclusion:
- standard deviations (SDs) and means are reported in the paper or obtainable from the authors;
- when a scale starts from the finite number zero, the SD, when multiplied by two, is less than the mean (as otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution, (Altman 1996);
- if a scale started from a positive value (such as the Positive and Negative Syndrome Scale (PANSS) (Kay 1986), which can have values from 30 to 210), the calculation described above would have been modified to take the scale starting point into account. In these cases skew is present if 2 SD >(S-S min), where S is the mean score and S min is the minimum score.
Endpoint scores on scales often have a finite start and end point and these rules can be applied. We would have entered skewed endpoint data from studies of less than 200 participants 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 skewed endpoint data from trials with over 200 participants would have been entered into the statistical 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. Change data from both small and large trials would have been entered into the syntheses.
2.5 Common measure
To facilitate comparison between trials, we intended 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 would have converted 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). If data based on these thresholds were not available, we intended to use the primary cut-off presented by the original authors.
2.7 Direction of graphs
Where possible, we intended to enter data in such a way that the area to the left of the line of no effect indicated a favourable outcome for preventive interventions. Where keeping to this would have made it impossible to avoid outcome titles with clumsy double-negatives (e.g. 'not improved'), we would have reported data where the left of the line indicated an unfavourable outcome. This would have been noted in the relevant graphs.
Assessment of risk of bias in included studies
Review authors SA, AG and NE would have independently assessed 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 overestimate of effect and high risk of bias of the article such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting.
If the raters had disagreed, the final rating would have been made by consensus, with the involvement of AE. If inadequate details of randomisation and other characteristics of trials had been provided, we would have contacted the authors of the studies in order to obtain further information. Non-concurrence in quality assessment would have been reported, but if disputes had arisen as to which category a trial was to be allocated, again, resolution would have been made by discussion.
The level of risk of bias would have been noted in both the text of the review and in the 'Summary of findings' table.
Measures of treatment effect
1. Binary data
For binary outcomes, we planned to 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). For statistically significant results, we intended to use 'Summary of findings' tables to calculate the number needed to treat to provide benefit /to induce harm statistic and its 95% CI.
2. Continuous data
For continuous outcomes, we planned to estimate mean difference (MD) between groups. We preferred not to calculate effect size measures (SMD). However, if scales of very considerable similarity had been used, we would have presumed that there was a small difference in measurement, and we would have calculated effect size and transformed 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).
If clustering had not been accounted for in primary studies, we planned to present the 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 contact the first authors of studies to obtain intra-class correlation coefficients (ICCs) for their clustered data and adjust for this by using accepted methods (Gulliford 1999). If clustering had been incorporated into the analysis of primary studies, we would have presented these data as if from a non-cluster randomised study, but adjusted for the clustering effect.
We have sought statistical advice and have been advised that the binary data as presented in a report should be divided by a 'design effect'. This is calculated using the mean number of participants per cluster (m) and the ICC [Design effect=1+(m-1)*ICC] (Donner 2002). If the ICC is not reported it will be assumed to be 0.1 (Ukoumunne 1999).
If cluster studies have been appropriately analysed taking into account ICCs and relevant data documented in the report, synthesis with other studies would have been carried out 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 planned only to use data of the first phase of cross-over studies.
3. Studies with multiple treatment groups
If a study had involved more than two treatment arms, if relevant, we intended to present the additional treatment arms in the comparisons. Binary data would have been simply added and combined within the two-by-two table. Continuous data would have been combined following the formula in section 18.104.22.168 (Combining groups) of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Irrelevant data from additional treatment arms would not have been used.
Dealing with missing data
1. Overall loss of credibility
At some degree of loss of follow-up, data must lose credibility (Xia 2009). We chose that, for any particular outcome, should more than 50% of data be unaccounted for, we would not to reproduce these data or use them within analyses, (except for the outcome 'leaving the study early'). If, however, more than 50% of those in one arm of a study were lost, but the total loss was less than 50%, we would have marked such data with (*) to indicate that such a result may well be prone to bias.
In the case where attrition for a binary outcome was between 0% and 50% and where these data were not clearly described, we would have presented data on a 'once-randomised-always-analyse' basis (an intention-to-treat analysis). Those leaving the study early would have all been 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 - would have been used for those who did not. We would have undertaken a sensitivity analysis to test how prone the primary outcomes were to change when data only from people who completed the study to that point were compared to the intention-to-treat analysis using the above assumptions.
In the case where attrition for a continuous outcome was between 0% and 50%, and data only from people who completed the study to that point were reported, we planned to present and use these data.
3.2 Standard deviations (SDs)
If SDs had not been reported, we would have tried to obtain the missing values from the authors. If not available, where there were missing measures of variance for continuous data, but an exact standard error (SE) and confidence intervals (CIs) available for group means, and either 'P' value or 't' value available for differences in mean, we would have calculated them according to the rules described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). If only the SE was reported, we would have calculated SDs by the formula SD=SE * square root (n). Chapters 7.7.3 and 16.1.3 (Higgins 2011) present detailed formulae for estimating SDs from P values, t or F values, CIs, ranges or other statistics. If these formulae did not apply, we would have calculated 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 would have examined the validity of the imputations in a sensitivity analysis excluding imputed values.
3.3 Last observation carried forward
We anticipated that in some studies the method of last observation carried forward (LOCF) would 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 had been used in the trial, if less than 50% of the data had been assumed, we would have reproduced these data and indicated that they were the product of LOCF assumptions.
Assessment of heterogeneity
1. Clinical heterogeneity
We planned to judge clinical heterogeneity by inspecting all included studies initially. We would have simply inspected all studies, without seeing comparison data, for clearly outlying people or situations which we had not predicted. If such situations or participant groups had arisen, these would have been fully discussed.
2. Methodological heterogeneity
We planned to judge methodological heterogeneity by considering all included studies initially. We would have simply inspected all studies, without seeing comparison data, for clearly outlying methods which we had not predicted. If such methodological outliers had arisen, these would have been fully discussed.
3. Statistical heterogeneity
3.1 Visual inspection
We intended to inspect graphs visually to investigate the possibility of statistical heterogeneity.
3.2 Employing the I
We planned to investigate heterogeneity between studies 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 theCochrane 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 would not have used funnel plots for outcomes where there were 10 or fewer studies, or where all studies were of similar sizes. In other cases, where funnel plots were possible, we would have sought 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. 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. There are no included studies, and therefore, no analyses. In future updates of this review, we will use the random-effects model for all analyses. The reader however, will be able to choose to inspect the data using the fixed-effect model.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses - only primary outcomes
We intended to present data for women with similar risk factors for postnatal psychosis so that these data could be considered together. For primary outcomes, if data for individual risk factors had been reported, these would have been included in subgroup analyses.
We anticipated subgroup analyses investigating the different interventions used for the prevention of postnatal psychosis. These data, although synthesised overall, would, if possible, have been presented in subgroups.
2. Investigation of heterogeneity
If inconsistency had been high, this would have been reported. First, we would have investigated whether data had been entered correctly. Second, if data were correct, we would have visually inspected the graph and removed outlying studies to see if homogeneity was restored. For this review, we had decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, we would have presented data. If not, we would not have pooled data and issues would have been discussed.
If there had been unanticipated clinical or methodological heterogeneity, we would have simply stated hypotheses regarding these for future reviews or versions of this review. We did not anticipate undertaking analyses relating to these.
1. Implication of randomisation
We aimed to include trials in a sensitivity analysis if they were described in some way as to imply randomisation. For the primary outcomes, we would have included these studies and if there was no substantive difference when the implied randomised studies were added to those with better description of randomisation, then we would have used all the data from these studies.
2. Assumptions for lost binary data
If assumptions had to be made regarding people lost to follow-up (see Dealing with missing data), we planned to compare the findings of the primary outcomes when we used our assumption and when we used data only from people who completed the study to that point. If this had resulted in a substantial difference, we would have reported results and discussed them, but we would have continued to employ our assumption.
If assumptions had to be made regarding missing SDs data (see Dealing with missing data), we would have compared the findings of the primary outcomes when we used our assumption and when we used data only from people who completed the study to that point. A sensitivity analysis would have been undertaken to test how prone results were to change when completer-only data only were compared to the imputed data using the above assumption. If there had been a substantial difference, we would have reported results and discussed them, but continued to employ our assumption.
3. Risk of bias
We aimed to analyse the effects of excluding trials that were judged to be at high risk of bias across one or more of the domains of randomisation (implied as randomised with no further details available), allocation concealment, blinding and outcome reporting for the meta-analysis of the primary outcome. If the exclusion of trials at high risk of bias did not substantially alter the direction of effect or the precision of the effect estimates, then we would have included data from these trials in the analysis.
4. Imputed values
We also aimed to 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 were noted in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we would not have pooled data from the excluded trials with the other trials contributing to the outcome, but would have presented them separately
5. Fixed-effect and random-effects
We planned to synthesise all data using a random-effects model, however, we also intended to synthesise data for the primary outcome using a fixed-effect model to evaluate whether this altered the significance of the result.
Description of studies
Results of the search
Our search of databases identified 54 records. After screening the records, we assessed three full-text articles; two planned trials that do not seem to have commenced (Nakigudde 2008 and Paykel 2000) and a published report (Destounis 1965), which we excluded because it was a case series report of eight cases of depression (see Study flow diagram, Figure 1).
|Figure 1. Study flow diagram.|
This review does not contain any included studies.
Risk of bias in included studies
No studies met the inclusion criteria.
Effects of interventions
No studies met the inclusion criteria.
Postnatal psychosis is a psychiatric emergency that affects about one to two in every 1000 new mothers. A variety of preventive interventions for postnatal psychosis have been attempted. Such interventions include identifying women with risk factors, early recognition of imminent psychosis through screening, and preventive drug therapy using mood stabilisers, antipsychotic drugs and hormone therapy in women at high risk. However, we were unable to locate a single prospective, randomised trial of preventive interventions for postnatal psychosis.
This is an "empty review" (Yaffe 2012), and 'empty reviews' may stimulate intervention research related to important problems. This particular review points out an urgent need for randomised trials in the area of postnatal psychosis prevention. In order to identify possible preventive interventions, we performed an extra search for non-randomised trial publications in PubMed. This search was not planned in our protocol, and yielded 1313 results. After screening titles and abstracts, the full text of 39 references were retrieved, and 10 reports were relevant to this review ( Table 1). A single case-report (Murray 1990), involved a woman with a history of postnatal psychosis in her first pregnancy. She was prescribed progesterone five days before delivery in her second pregnancy, and thioridazine in her third pregnancy. The woman had a postnatal psychosis relapse in her second pregnancy, but not in her third pregnancy, suggesting a lack of preventive effect of progesterone. Similar failure of transdermal oestrogen in preventing postnatal psychosis was reported in a series of 29 at-risk pregnant women (Kumar 2003). Another series of 11 at-risk women, however, suggested a benefit for high doses of oestrogen in preventing postnatal psychosis (Sichel 1995). Comparable conflicting results have been reported for the preventive value of mood stabilisers. In a small retrospective case-control study, none of the women taking a mood stabiliser developed postpartum psychosis (Cohen 1995), and in a small prospective controlled trial, none of the at-risk women who were taking a mood stabiliser relapsed during the study that lasted through the pregnancy and postnatal period (Bilszta 2010). As for specific mood stabilisers, divalproex sodium given immediately after birth compared with no treatment demonstrated no preventive effect of postpartum episodes in women with bipolar disorder in a small controlled trial (Wisner 2004). Lithium prophylaxis taken during pregnancy or immediately postpartum was effective in three series of women at risk of postpartum psychosis (Bergink 2012; Stewart 1988; Stewart 1991). The favourable effect of lithium prophylaxis in the prevention of postnatal psychosis was also suggested in a controlled trial of 17 women with bipolar disorder or puerperal affective psychosis (Austin 1992). Another small controlled trial suggested a value for olanzapine alone or in combination with other psychotropic drugs for postnatal psychosis prevention (Sharma 2006).
Summary of main results
This is not an 'empty review' - it is a review full of unanswered questions ( Summary of findings for the main comparison). The non-randomised controlled trials and the two designs seen in the studies awaiting assessment, suggest that randomised studies of preventive interventions for postnatal psychosis are possible. Nakigudde 2008 and Paykel 2000 both seemed studies that were possible to undertake; although it seems that neither ever got off the ground. The evidence that we found was based on observational data, rather than data from randomised controlled clinical trials and we cannot be confident of any of their findings.
Overall completeness and applicability of evidence
There is currently no randomised trial-based evidence.
Quality of the evidence
There is currently no randomised trial-based evidence.
Potential biases in the review process
We have tried to minimise potential biases in our review process.
Agreements and disagreements with other studies or reviews
There is currently no randomised trial-based evidence that could be compared with other studies.
Implications for practice
1. Women at risk of postnatal psychosis and their relatives
Women and their carers are justified to be disappointed in the medical/research fraternity. Those interested may wish to lobby for studies in this area.
Despite growing interest in women's mental health, the literature in the area of postnatal psychosis is still very limited. It seems that clinicians have no choice but to continue with their current practices using clinical judgement because of the lack of randomised evidence to help guide their choice of intervention. Clinicians have a responsibility to lobby and help good research in this area.
3. Policy makers
Policy makers have no randomised evidence upon which to base guidelines for the prevention of postnatal psychosis. They are likely to continue to rely on opinion and habit when making their recommendations.
Implications for research
Preventive interventions for postnatal psychosis can not be justified without well-designed, well-conducted, and well-reported randomised studies. At present, there is no convincing evidence to support the use of preventive interventions for postnatal psychosis. Clinically meaningful randomised studies are needed to help guide clinicians in their management of women at risk of postnatal psychosis. Available publications suggest that such studies are possible.
Funders of studies may wish to make this important subgroup of people a priority for future research.
We are well aware that design of such a study needs care and considerable attention to detail. We suggest a design here of very low-key set of interventions rather than the use of specific drugs during the pregnancy and after delivery ( Table 2).
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.
The search terms have been developed by the Trial Search Co-ordinator of the Cochrane Schizophrenia Group, Samantha Roberts.
We would like to thank Lorna Duggan for peer reviewing this review and her helpful comments.
Data and analyses
This review has no analyses.
Last assessed as up-to-date: 13 November 2012.
Contributions of authors
Review authors AE and SA prepared the protocol and wrote review.
Review authors AG and NE wrote review.
Declarations of interest
Sources of support
- Association for Evidence-Based Medicine, Syrian Arab Republic.
- No sources of support supplied
Differences between protocol and review
We have updated some sections of the methods to the latest template of the Cochrane Schizophrenia Group, and modified some of the Background in response to peer review comments.
Medical Subject Headings (MeSH)
MeSH check words