1. Parenting interventions

We included all parenting programmes whose primary aim was to improve the parenting skills or parent–child interaction (or both) of parents with schizophrenia or a related serious mental illness. Programmes may have been any length, delivered in any type of setting, in any form, including by a trained professional, through peer‐support or in the form of self‐help, and may have been underpinned by any theoretical approach.

We excluded mother and baby units as these are considered crisis programmes for mothers experiencing acute psychotic symptoms after the birth of their child, where the focus is primarily to treat the mother's symptoms while not separating the mother and baby.

2. Control

We considered any control intervention whether active or inactive.

Primary outcomes

1. Parenting outcomes

   1. Parenting behaviours, skills, attitudes, or knowledge

      1. Clinically important change in parenting behaviours, skills, attitudes, or knowledge

      2. Any change in parenting behaviours, skills, attitudes, or knowledge

2. Adverse events involving child or parent

   1. General adverse events (i.e. parenting stress, deterioration of parent's mental state)

      1. At least one adverse event

Secondary outcomes

1. Parenting outcomes

   1. Parenting behaviours, skills, attitudes, or knowledge

      1. Average endpoint or change score on a parenting behaviours, skills, attitudes, or knowledge scale

   2. Quality of relationship with child (i.e. attachment, parental reflectivity, parental sensitivity)

      1. Clinically important change in quality of relationship with child

      2. Any change in quality of relationship with child

      3. Average endpoint or change score on a quality of relationship with child scale

2. Adverse events involving child or parent

   1. General adverse events (i.e. parenting stress, deterioration of parent's mental state)

      1. Clinically important adverse event

      2. Average endpoint or change score on an adverse‐event/effect scale

   2. Death

      1. Any cause except suicide, homicide, and filicide (death of child caused by parent)

      2. Suicide

      3. Homicide

      4. Filicide

3. Behaviour of child

   1. General

      1. Clinically important change in general behaviour

      2. Any change in general behaviour

      3. Average endpoint or change score on a general behaviour scale

   2. Specific

      1. Clinically important change in specific aspects of behaviour (e.g. aggression, socioemotional adjustment)

      2. Any change in specific aspects of behaviour (e.g. aggression, socioemotional adjustment)

      3. Average endpoint or change on specific aspects of behaviour scale

4. Social services involvement

   1. At least one child protection issue reported

   2. Child referred to social services for an assessment/investigation

   3. Child taken into care

5. General functioning of parent or child

   1. Overall

      1. Clinically important change in general functioning, including working ability

      2. Any change in general functioning, including working ability

      3. Average endpoint or change score on a general functioning scale

   2. Specific

      1. Clinically important change in specific aspects of functioning, such as life skills

      2. Any change in specific aspects of functioning, such as life skills

      3. Any change in educational status

      4. Any change in employment status

      5. Average endpoint or change score on specific aspects of functioning scale

6. Social functioning of parent or child

   1. Clinically important change in social functioning

   2. Any change in social functioning

   3. Average endpoint or change score on a social functioning scale

7. Global state of parent

   1. Clinically important change in global state (e.g. global impression of much improved, or more than 50% improvement on a rating scale)

   2. Relapse

   3. Any change in global state

   4. Average endpoint or change score on a global state scale

   5. Use of other medications

8. Mental state of parent

   1. General

      1. Clinically important change in general mental state

      2. Any change in general mental state

      3. Average endpoint or change score on a general mental state scale

   2. Specific

      1. Clinically important change in specific symptoms (e.g. positive, negative, affective, cognitive symptoms of schizophrenia)

      2. Any change in specific symptoms (e.g. positive, negative, affective, cognitive symptoms of schizophrenia)

      3. Average endpoint or change score on a specific symptom scale

9. Quality of life of parent or child

   1. Overall

      1. Clinically important change in quality of life

      2. Any change in quality of life

      3. Average endpoint or change score on a quality‐of‐life scale

   2. Specific

      1. Clinically important change in specific aspects of quality of life

      2. Any change in specific aspects of quality of life

      3. Average endpoint or change score on specific aspects of quality‐of‐life scale

10. Service use of parent

    1. Clinically important engagement with services

    2. Any engagement with services

    3. Average endpoint or change score on engagement scale

    4. Compliance with medication or other treatment, or both

    5. Number of hospitalisations

    6. Number of days in hospital

    7. Inability to be discharged from hospital

11. Leaving the study early

    1. 11.1. For any reason

    2. Due to inefficacy

    3. Due to adverse effect

12. Economic costs

    1. Costs due to treatment, as defined by each study

    2. Savings due to treatment, as defined by each study

Cochrane Schizophrenia Group's Study‐Based Register of Trials

On 30 March 2020 and 10 February 2021, the Information Specialist searched the register using the following search strategy:

*Parenting* in Intervention Field of STUDY

In such a study‐based register, searching the major concept retrieves all the synonyms and relevant studies because all the studies have already been organised based on their interventions and linked to the relevant topics (Shokraneh 2017; Shokraneh 2021; Roberts 2021). This allows rapid and accurate searches that reduce waste in the next steps of systematic reviewing (Shokraneh 2019).

Following the methods from Cochrane (Lefebvre 2019), this register is compiled by systematic searches of major resources (Cochrane Central Register of Controlled Trials (CENTRAL), Cumulative Index to Nursing and Allied Health Literature (CINAHL), ClinicalTrials.Gov, Embase, International Standard Randomised Controlled Trial Number (ISRCTN), MEDLINE, PsycINFO, PubMed, the World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) and their monthly updates, ProQuest Dissertations and Theses A&I and its quarterly update, handsearches, grey literature, and conference proceedings (Shokraneh 2020; see Group's website). There are no language, date, document type, or publication status limitations for inclusion of records into the register.

1. Reference searching

We inspected references of the included studies for further relevant studies.

2. Personal contact

We contacted the first author of the included study for information regarding unpublished trials. We noted the outcome of this contact in the Characteristics of included studies table.

1. Extraction

Two review authors (JR and CG) extracted data from the included study and presented in the Characteristics of included studies table. We attempted to extract data presented only in graphs and figures whenever possible, but only included the data if two review authors independently obtained the same result. If studies were multicentre, we extracted data relevant to each where possible. We discussed any disagreements and documented our decisions. If necessary, we attempted to contact authors through an open‐ended request to obtain missing information or for clarification. One review author (JB) helped clarify issues regarding any remaining problems and we documented these final decisions.

2. Management

1. Binary data

For binary outcomes, we would have calculated a standard estimation of the risk ratio (RR) and its 95% confidence interval (CI), as it has been shown that RR is more intuitive than odds ratios (Boissel 1999); and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). Although the number needed to treat for an additional beneficial outcome (NNTB) and the number needed to treat for an additional harmful outcome (NNTH), with their 95% CIs, are intuitively attractive to clinicians, they are problematic to calculate and interpret in meta‐analyses (Hutton 2009). For binary data presented in summary of findings Table 1, we had planned to calculate illustrative comparative risks.

2. Continuous data

For continuous outcomes, we would have estimated MD between groups. We would have preferred not to calculate effect size measures (SMD). However, if scales of very considerable similarity had been used, we would have presumed there was a small difference in measurement, calculated the effect size and transformed the effect back into the units of one or more of the specific instruments.

1. Cluster‐randomised trials

Studies increasingly employ 'cluster randomisation' (such as randomisation by clinician or practice), but analysis and pooling of clustered data poses problems. Authors often fail to account for intraclass correlation in cluster‐randomised studies, leading to a unit‐of‐analysis error whereby P values are spuriously low, CIs unduly narrow, and statistical significance overestimated (Divine 1992). This causes type I errors (Bland 1997; Gulliford 1999).

Where clustering had been incorporated into the analysis of primary studies, we had planned to present these data as if from a non‐cluster‐randomised study, but adjusted for the clustering effect.

Where clustering had not been accounted for in primary studies, we had planned to present data in a table, with a (*) symbol to indicate the presence of a probable unit‐of‐analysis error. We would have sought to contact first authors of studies to obtain intraclass correlation coefficients (ICC) for their clustered data and to adjust for this by using accepted methods (Gulliford 1999).

We sought statistical advice and were advised that the binary data from cluster‐randomised trials 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: thus design effect = 1 + (m − 1) × ICC (Donner 2002). If the ICC is not reported, it is assumed to be 0.1 (Ukoumunne 1999).

If cluster studies had been appropriately analysed and taken ICCs and relevant data documented in the report into account, synthesis with other studies would have been possible using the generic inverse variance technique.

2. Cross‐over trials

A major concern of cross‐over trials is the carry‐over effect. This 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, participants can differ significantly from their initial state at entry to the second phase, despite a washout phase. For the same reason, cross‐over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both carry‐over and unstable conditions are very likely in severe mental illness, we planned to use only data from the first phase of cross‐over studies.

3. Studies with multiple treatment groups

Where a study involved more than two treatment arms, if relevant, we planned to present the additional treatment arms in comparisons. If data were binary, we would simply have added these and combined them within the two‐by‐two table. If data were continuous, we planned to combine data following the formula in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). Where additional treatment arms were not relevant, we would not have reproduced these data and would have listed them in the Characteristics of included studies table.

1. Overall loss of credibility

At some degree of loss to follow‐up, data must lose credibility (Xia 2009). We chose that, for any particular outcome, should more than 50% of data have been unaccounted for, we would not have reproduced these data or used them within analyses. 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 addressed this within summary of findings Table 1 by downgrading certainty. Finally, we also planned to downgrade certainty within summary of findings Table 1 should the loss have been 25% to 50% in total.

2. Binary

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 (ITT) analysis). We would have assumed that those leaving the study early had the same rates of negative outcome as those who completed. We planned to use the rate of those who stayed in the study – in that particular arm of the trial – and apply this also to those who did not. We planned to undertake a sensitivity analysis testing how prone the primary outcomes were to change when we only used data from people who completed the study to that point, compared to the ITT analysis using the above assumptions.

3. Continuous

1. Clinical heterogeneity

We had planned to consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We would simply have inspected all studies for participants who were clearly outliers or situations that we had not predicted would arise and, where found, would have discussed such situations or participant groups.

2. Methodological heterogeneity

We had planned to judge methodological heterogeneity by considering all included studies before seeing comparison data. We would have reviewed all studies for clearly outlying methods that we had not predicted would arise, and would have discussed any such methodological outliers.

3. Statistical heterogeneity

1. Protocol versus full study

We tried to locate protocols of included randomised trials. If the protocol was available, we planned to compare outcomes in the protocol with those in the published report. If the protocol was not available, we planned to compare outcomes listed in the methods section of the trial report with the results actually reported.

2. Funnel plot

We are aware that funnel plots may be useful in investigating reporting biases but are of limited power to detect small‐study effects. We did not use funnel plots for outcomes where there were 10 or fewer studies, or where all studies were of similar size. In other cases, where funnel plots were possible, we would have sought statistical advice in their interpretation.

1. Subgroup analyses

We did not expect there to be sufficient power to report subgroup analyses. However, if data were available, we would have looked at the effects of gender of the parent, ethnicity of the parent, marital status of the parent, sexual orientation of the parent, and the type of parenting intervention being investigated (e.g. Mental Health Positive Parenting Program (Phelan 2006) versus Falkov's Family Model (Falkov 2012)).

2. Investigation of heterogeneity

We would have reported if inconsistency was high. First, we would have investigated whether data had been entered correctly. Second, if data were correct, we would have inspected the graph visually and removed outlying studies successively to see if homogeneity was restored. For this review, we decided that should this occur with data contributing to the summary finding of no more than 10% of the total weighting, we would have presented data. If not, we would not have pooled these data and instead would have discussed any issues. 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 was obvious, 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 planned to include trials in a sensitivity analysis if they were described in some way as to imply randomisation. For the primary outcomes, if there was no substantive difference when the implied randomised studies were added to those studies with better description of randomisation, we would have included these studies.

2. Assumptions for lost binary data

Where 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 compared with completer data only. If there had been a substantial difference, we planned to report results and discuss them, but would have continued to employ our assumption.

Where assumptions had to be made regarding missing SDs (see Dealing with missing data), we planned to compare the findings on primary outcomes when we used our assumption compared with completer data only. We would have undertaken a sensitivity analysis testing how prone results were to change when completer 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 would have continued to employ our assumption.

3. Risk of bias

We planned to analyse the effects of excluding trials that were at high risk of bias across one or more of the domains for the meta‐analysis of the primary outcome (see Assessment of risk of bias in included studies).

4. Imputed values

We planned to undertake a sensitivity analysis to assess the effects of including data from trials with imputed values for ICC in calculating the design effect in cluster‐randomised trials.

5. Fixed‐effect and random‐effects

We planned to synthesise data using a random‐effects model; however, we would also have synthesised data for the primary outcome using a fixed‐effect model to evaluate whether this altered the significance of the results.

We aimed to carry out these sensitivity analyses for primary outcomes only. If there had been substantial differences in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we would not have added data from the lower‐quality studies to the results of the higher‐quality trials, but instead presented these data within a subcategory. If their inclusion had not resulted in a substantive difference, they would have remained in the analyses.