cochrane database systematic review 2016

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2016 impact factor for cochrane database of systematic reviews is 6.124.

The 2016 Journal Citation Report (JCR) has just been released by Clarivate Analytics (formerly Thomson ISI), and we are pleased to announce that Cochrane Database of Systematic Reviews (CDSR) Impact Factor is now 6.124 . This is a slight  increase on the 2015 impact factor, which was 6.103. The CDSR impact factor is calculated by taking the total number of citations in a given year to all Cochrane Reviews published in the past 2 years, and dividing that number by the total number of Reviews published in the past 2 years. It is a useful metric for measuring the strength of a journal by how often it its publications are cited in scholarly articles. Some highlights of the CDSR 2016 Impact Factor include:

• The CDSR is ranked 14 of the 154 journals in the Medicine, General & Internal category.
• The CDSR received 57,740 cites in the 2016 Impact Factor period, compared with 47,899 for the 2015 Impact Factor calculation.
• The total number of times the CDSR was cited increased from 47,899 in 2015 to 57,740 in 2015 meaning the CDSR received the 5th highest number of citations in its category.
• The 5-Year Impact Factor is 7.018.

The main Impact Factor report and the CRG reports will be delivered after the JCR is updated in September. This is because, as has happened in previous years, Clarivate was unable to accurately index Cochrane Reviews for this Impact Factor window; Wiley and Cochrane are following-up with Clarivate regarding the calculation of the 2016 impact factor.

We expect that the CDSR impact factor will be revised when the JCR is updated in September 2017. When this occurs, we will revise and re-circulate documentation accordingly. In the meantime, we encourage Cochrane contributors to use and share the CDSR impact factor noting that this June release will be revised in the September update from Clarivate.

More information is available here on how the CDSR Impact Factor is calculated.

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Chapter iv: updating a review.

Miranda Cumpston and Ella Flemyng

Key Points:

• As new studies are completed, the results of reviews may become out of date and thereby provide misleading information to decision makers.
• Cochrane Reviews should be assessed periodically to determine whether an update is needed. The decision to update should be based on the continuing importance of the review question to decision makers and the availability of new data or new methods that would have a meaningful impact on the review findings.
• A review update provides an opportunity for the scope, eligibility criteria and methods used in the review to be revised.
• An update should be conducted according to the standards required for any review, with some additional requirements to ensure that any changes are managed appropriately and reported clearly to readers.

This chapter should be cited as: Cumpston M, Flemyng E. Chapter IV: Updating a review. In: Higgins JPT, Thomas J, Chandler J, Cumpston M, Li T, Page MJ, Welch VA (editors). Cochrane Handbook for Systematic Reviews of Interventions version 6.4 (updated August 2023). Cochrane, 2023. Available from www.training.cochrane.org/handbook .

IV.1 Introduction

Since its inception, Cochrane has sought to maintain its reviews to ensure they are updated to include the most recent evidence. Reviews that are out of date and do not incorporate all the available evidence risk providing misleading information to decision makers and other stakeholders.

Garner and colleagues define an update as “a new edition of a published systematic review with changes that can include new data, new methods, or new analyses to the previous edition” (Garner et al 2016). Adding new studies and new data can substantively change the findings of the review. Even where the new studies observe results consistent with the existing data, increasing the number of studies can improve precision of effect estimates, demonstrate wider applicability of the effect, or enable additional comparisons or subgroup analyses to be performed. The introduction of new review methods, such as updated risk of bias assessment tools or improved statistical analysis methods, can also change both the results and the certainty of the review’s findings. Examples of the impact of incorporating new information and methods are illustrated in Box IV.1.a .

All Cochrane Reviews should be assessed periodically to determine whether an update is needed. Some areas of research evolve rapidly, whereas others are more stable, and some research questions stop being relevant to decision makers. A report assessing 100 systematic reviews published between 1995 and 2005 concluded the median time to require an update was 5.5 years, although 23% of reviews were out of date within two years, 15% within one year, and 7% were already out of date at the time of publication (Shojania et al 2007). Authors of Cochrane Reviews should therefore consider both whether an update is warranted, and when it will be most beneficial for each specific review (see Section IV.2 ).

In some areas, authors are establishing ‘living’ systematic reviews that adopt a continual updating process, such as monthly searching followed by rapid incorporation of new evidence into the published review. Living systematic reviews are most likely to be appropriate for questions that are of high importance to decision makers, and for which new evidence is likely to be frequently published and to have an important impact on the review’s findings (Elliott et al 2017). Considerable resources are required to support such an ongoing process. Further discussion of living systematic reviews is presented in Chapter 22, Section 22.2.3 .

Cochrane’s Methodological Expectations of Cochrane Intervention Reviews (MECIR) , which guide the conduct of Cochrane Reviews, include expectations for updating reviews. See the online MECIR Manual for the 11 expectations specifically relevant to updates, although updated reviews should also meet the expectations that apply to all reviews. This chapter elaborates on the recommendations for the planning, conduct and reporting of Cochrane Review updates.

Box IV.1.a Examples of what factors might change in an updated systematic review (Garner et al 2016). Reproduced from Garner P, Hopewell S, Chandler J, MacLehose H, Akl EA, Beyene J, et al. When and how to update systematic reviews: consensus and checklist. BMJ 2016; 354: i3507 licensed under CC BY 3.0 .

IV.2 Deciding whether and when to update

The decision to undertake an update of a review requires consideration of a number of different factors. Garner and colleagues conducted an international consensus process to establish good practice guidance for determining when a systematic review should be updated (Garner et al 2016). Their published framework and checklist can assist authors in thinking through these issues in a structured way (see Figure IV.2.a ).

Figure IV.2.a Decision framework to assess systematic reviews for updating, with standard terms to report such decisions (Garner et al 2016). Reproduced from Garner P, Hopewell S, Chandler J, MacLehose H, Akl EA, Beyene J, et al. When and how to update systematic reviews: consensus and checklist. BMJ 2016; 354: i3507 licensed under CC BY 3.0 .

When deciding whether to update a particular review, the first consideration should be to determine whether the review question remains relevant to decision makers, and is well-targeted to answer current questions in policy and practice. Knowledge of the particular field will be required to answer this question. Checking whether the existing review is frequently accessed or cited can also be useful to indicate whether there is a need to update. A second aspect to this question is whether the original review was conducted well and used appropriate methods (Garner et al 2016). If the review question remains fundamentally of interest, additions and improvements may be possible to enhance the review’s methods (see Section IV.3.4 ). Depending on the changes required, it may be more appropriate to conduct a new review from scratch meeting current standards. A comparison between currently recommended methods and the methods used in the review can identify any important changes required.

If the review remains important and is of a sufficient standard, then the next step is to consider whether there are any new studies, newly available information, or newly recommended methods that could be incorporated into the review. The existing version of the review may include details of ongoing studies identified at the time of its publication, for example through searches of trials registers, and these trials may now be complete. Some authors may choose to monitor the literature continually for new studies (e.g. through automated alerts), or may conduct a rapid scoping search for this purpose.

If either new information or new methodology is available, a critical next step is to evaluate whether incorporating these into the review would be likely to impact on its findings (Garner et al 2016). In some cases, this decision can be very straightforward, for example when the existing reviews findings are considered very uncertain (for example, using the GRADE approach to assessment, see Chapter 14 ). For some reviews, the findings are of very high certainty, and it is unlikely that new information will meaningfully impact the conclusions. In some cases, maintaining credibility through the incorporation of additional information and new methods is sufficient in itself to warrant updating (Garner et al 2016).

In some cases, although the main findings of the review may be unaffected, additional information may shed light on more nuanced effects of different variations on the intervention, different settings, additional outcomes, or population subgroups. In other cases, it may not be clear whether the extent of new information available will be enough to impact meaningfully on the results (Garner et al 2016).

To date there is no consensus on when to update a review (Tsertsvadze et al 2011), although several methods have been proposed (e.g. Sampson et al (2008), Shekelle et al (2011), Tovey et al (2011), Ahmadzai et al (2013), Takwoingi et al (2013)). These methods use signals to indicate the need for an update and the likely impact of new studies on existing conclusions. They include surveillance searches, contact with experts, and quantitative or qualitative assessments, or both. Chapter 22, Section 22.2 , outlines a range of methods for surveillance of the literature and the interpretation of signals for updating, including statistical methods based on sample size calculations or the application of prediction equations to assess the impact of new evidence. Garner and colleagues also summarize a series of available methods (Garner et al 2016). Ultimately, review authors should make a judgement based on an individual assessment and their knowledge of the field covered by the review.

IV.3 Planning an update

Before embarking on an updated review, it is important to take the time to plan the process. Any proposed modifications or additions to the existing review should be planned in detail, and on occasion may require drafting a new protocol for the review. In addition, there are several issues unique to updates that should be considered.

Many of the approaches using new technologies designed to facilitate the review process are intended to support easier and more frequent updates. Further information is available in Chapter 4 , Section 4.6.6 , and Chapter 22 , Section 22.2.4 .

See the online MECIR Manual for expectations relevant to planning an update.

IV.3.1 Reconsidering review questions and eligibility criteria

Even when the overall review question has been agreed to remain relevant, an update is an opportunity to consider changes to the question and its scope. Authors should reconsider all elements of the review question (PICO), the eligibility criteria, comparisons and outcomes of interest. For example, evolving understanding of the problem may lead to the inclusion of a new comparison, an additional category of patients (e.g. children in addition to adults) or an important new outcome (e.g. adverse effects) that may not have been adequately addressed in the original review. Review authors may also wish to include additional objectives, such as addressing the economic aspects of the intervention or its implementation. Additional engagement with stakeholders may reveal current issues around which there is uncertainty (see Chapter 2 ).

Irrespective of whether the review question(s) change, there may be reason to amend the eligibility criteria for the review (see Chapter 3 ). For example, new intervention options may have become available since the publication of the original review. As the number of available studies increases over time, this may also affect decisions about eligibility. For example, if the original review included both randomized trials and non-randomized studies, and the former provide sufficient evidence to answer the review questions, it may be reasonable to decide to exclude non-randomized studies from subsequent updates of the review. Conversely, it may be reasonable to add non-randomized studies to a review that was previously restricted to randomized trials, to widen the evidence base, making use of methodological developments in critical evaluation of the validity of non-randomized studies (see Chapter 24 ).

IV.3.2 Splitting and merging reviews

As the body of evidence accumulates over time, a review may become too large for authors to manage (some of the largest Cochrane Reviews include hundreds of studies across multiple comparisons). It is sometimes appropriate to consider splitting the review into two or more reviews with more narrowly defined questions. For example, an early Cochrane Review investigated all interventions for shoulder pain. As this review became large and unwieldy over time, it was split into multiple separate reviews, each looking at an intervention category. One of these reviews looked at physiotherapy interventions for shoulder pain (Green et al 2003). As time went on, this review also became too large to manage, and was split into a number of reviews examining different physiotherapy interventions and specific types of shoulder pain (e.g. Page et al (2014a), Page et al (2014b), Page et al (2016a), Page et al (2016b)).

Narrower reviews may allow deeper investigation of specific intervention types, and more focused information for stakeholders, and may distribute the updating burden between several review author teams. On the other hand, narrower reviews can sometimes prevent readers from considering findings across all the interventions relevant to a decision (see Chapter 2, Section 2.3 ). Overviews of Reviews are an alternative option, allowing authors to summarize several more narrowly defined reviews that may have been split from a larger review (see Chapter V ).

It is also possible for one or more narrower Cochrane Reviews to be merged into a larger review, where agreed by all authors that this would present a more useful synthesis for decision makers. For example, it might be concluded that a network meta-analysis to compare multiple intervention options for a particular condition would be more useful than an existing series of separate reviews of specific interventions (see Chapter 11 ).

IV.3.3 Planning the search strategy for an update

Once the scope and eligibility criteria for the update have been agreed, authors will prepare for an update by deciding on the appropriate search process and strategy.

A starting point for identifying new studies for inclusion may be those already identified as ongoing studies at the time of the existing version of the review. Following this, in some cases, the search strategy can be re-run as specified in the existing review, with the addition of date limits set to the period following the most recent search. However, an information specialist or healthcare librarian should be consulted to ensure the strategy remains appropriate. Changes to electronic databases, their access mechanisms and controlled vocabulary can require expert amendments to the search strategies. In addition, informed by the experience of the search for the original review, a decision may be made to modify the list of sources to be searched or search terms to be used (Garner et al 2016).

If important changes to the PICO for the review or the eligibility criteria have been made since the original search, or developments in the field have led to the emergence of new terms to be added to the search, it may be necessary to re-run parts of the search back to the earliest records, to ensure that any records relevant to new search terms were not missed in the original search.

IV.3.4 Planning the methods for an update

Methodological advances in systematic review conduct since publication of the original review may result in a need to revise or extend the methods of the review update (Shea et al 2006). Authors are encouraged to consult current guidance on review methods and compare these with the methods used in the existing review to identify important changes.

Examples of situations in which review methodology might be updated include:

• incorporating updated guidance on risk of bias assessment (see Chapter 7 and Chapter 8 );
• using a new synthesis strategy, such as an improved method to perform a random-effects meta-analysis (see Chapter 10 ), or alternative methods for synthesis where meta-analysis is not possible (see Chapter 12 ).
• incorporating GRADE assessments and ‘Summary of findings’ tables if not already included (see Chapter 14 ); and
• adopting new guidance on the structure and presentation of findings, such as structured tabulation of results or alternative methods for visual presentation of results in reviews where meta-analysis is not used (see Chapter 12 ).

Changes to the scope of the review, such as expansion to include different study designs or outcome data, will require planning for new methods appropriate to the data expected.

Where changes to the review methods are substantive, authors are encouraged to write a complete, updated protocol to guide the conduct of the review update . In some cases, it may be more appropriate to consider the work as a new review, rather than an update.

Specific methods developed for systematic reviews that conduct ongoing and prospective approaches to accumulating evidence to maintain review currency are outlined in Chapter 22 . Formal sequential statistical methods that aim to address errors associated with repeating meta-analyses over time have been developed. However, such approaches are explicitly discouraged for updated meta-analyses in Cochrane Reviews, except in the context of a prospectively planned series of primary research studies (see Chapter 22, Section 22.4 ).

IV.3.5 Incorporating feedback and comments

Updating a published review provides an opportunity to consider any feedback or comments submitted to Cochrane or directly to the authors. Review authors are expected to be responsive to comments on their reviews, in the spirit of the scientific process and publication ethics. Comments may represent valid concerns and can usefully identify additional studies that were overlooked by the review authors.

IV.4 Conducting an update

An update of a review should be conducted according to the protocol, as closely as possible to the methods of the existing review while incorporating any planned changes (see Section IV.3 ). All steps should be conducted in accordance with the guidance presented throughout this Handbook .

A systematic search should be conducted for new studies (see Chapter 4 ), and the date of the search should be within 12 months of publication of the update. If new, potentially relevant studies are found, they should be assessed for inclusion in the review according to the eligibility criteria. If the existing review included records of any ongoing studies that are now complete, or studies for which classification as included or excluded was pending, newly available information should be sought and, where possible, final inclusion decisions made.

If new studies are to be included in the updated review, data should be collected (see Chapter 5 ) and risk of bias assessments completed for all new studies (see Chapter 7 ). On a practical note, when changes have been made to the scope or PICO of the review, tools such as the original data collection forms may need to be altered or extended and piloted again to ensure they are fit for purpose. This may also be needed if new software tools are to be used for data collection, or if a new author team has taken on the review, although existing templates and forms may be available from the original review authors or repositories such as the Systematic Review Data Repository ( https://srdr.ahrq.gov/ ).

The findings of any new studies should be integrated into the synthesis of the review (see Chapter 10 , Chapter 11 , and Chapter 12 ), and GRADE assessments completed (or revised), taking full account of the new body of evidence (see Chapter 14 ).

If no new studies are found to be included in the review, authors should complete and publish the updated review (see Section IV.5 ). While not modifying the findings, including the details of an updated search will reassure readers and decision makers of the currency of the review.

See the online MECIR Manual for expectations relevant to conducting an update.

IV.4.1 Updating data from previously included studies

Since the time of publication, additional information may be available about one or more studies included in the existing review. For example, additional outcome data measured at later time points may now be available, or the study may have been corrected or retracted due to errors, fraud or a range of other reasons. It is important to search online journals or databases such as MEDLINE (if the study is indexed there) for any notifications, corrections or retractions.

Any additions or corrections should be incorporated into the information contained in the review, if relevant. The reasons for retraction of any included studies should be considered. In addition to the publication record, this information may be available in reports of investigations, such as by the authors’ institutions or funders. In those cases where data appear to be incorrect or possibly fabricated, they should be removed from the review analysis and this decision should be reported in the review. Other studies by the same author(s) which would also be eligible for inclusion should be checked for similar issues, and a decision made as to whether they should similarly be removed. Further guidance on identifying corrected or retracted studies is provided in Chapter 4, section 4.4.6 , and in the Cochrane policy for managing potentially problematic studies .

If a new comparison or a new outcome has been added to the review, it may be necessary to go back to the original included studies and check whether they included any information not previously collected that would be relevant to the update.

IV.5 Reporting an updated review

An updated review should meet the same standards of reporting as any review (see Chapter III ), while ensuring that all updated information and changes made to the scope and methods of the review are reported clearly. The details of any changes, including justifications for the decisions made, can be briefly documented at the beginning of the Methods section of the review and elaborated on additional supplementary material if they are significant. Authors should clearly alert readers that this is an update of an earlier version, including statements in the Abstract, Background and Protocol and registration sections of the review.

Appearing at the beginning of the review, the Background section is not directly impacted by an update, but authors may wish to review the content of the Background to ensure that it remains fit for purpose. Discussions of the prevalence or incidence of a condition, new insights into the mechanism of action or impact on populations, or descriptions of current practice or policy options may be updated. Up-to-date references should be supplied to support this information. Any references to time, such as words like ‘recently’ or ‘in the next five years’, should be amended or, if possible, removed.

Reporting the details of the updated search alongside the search information in the existing review can become quite complex, especially if there have been several updates to the review over time. Detailed information on search strategies will be reported in Cochrane Reviews as supplementary material, so does not need to be described at length in the text of the review. There are several approaches to reporting the results of an updated search:

1. An integrated approach describes all searches together, which may be most feasible if the same search was repeated.

2. An incremental approach adds information at each update to describe explicitly which searches were done for the update, retaining all information about previous searches.

3. A replacement approach describes only the searches done for the update, using the previous review as one source of studies.

If any of the sources originally searched were not searched for the update, this should be explained and justified.

The updated search should also be presented in a PRISMA-type flow diagram (see Chapter 4, Section 4.5 ). Again, there are options as to how to present the results of multiple searches coherently in the diagram. Authors can retain the results of previous searches in the review and supplement with information about studies identified in the update or, alternatively, present only information about searches in the current update, with the previous version of the review serving as one particular source of studies. If taking the latter approach, the flow diagram should show one box for the number of studies included in the original review or previous update and an additional box for the new studies retrieved for the current update. If multiple searches have been conducted for the current update, the results of all the searches should be added together. It may be helpful to consider the clarity of the diagram as a summary for readers when selecting an approach.

The methods and results described throughout the review and its summaries (including the ‘Summary of findings’ table, Abstract and Plain Language Summaries) should be checked to ensure they still reflect the methods used accurately. Where the review is considered a ‘living’ systematic review, and regular updates are planned, additional methods should be included to describe the timing and nature of this process (see Chapter 22, Section 22.2 ).

The extent of revision to the Results of the review will depend on the influence of the new data on the results of the review. Examples include:

• the addition of small studies bringing about no change in the results or conclusions of the review (and so requiring very little revision of the text);
• increased certainty of pre-existing results and conclusions (requiring some modification of the text); and
• a change in the conclusion of a review (requiring a major rewrite of the Results, Discussion, Conclusion, ‘Summary of findings’ table, Abstract and Plain Language Summary).

When reporting the results, it is more helpful to readers to present an integrated picture of the overall results, rather than sequential or separate results for the update (especially where there has been more than one update), although any particularly notable changes to the review’s conclusions may be of interest to discuss when interpreting the results.

Authors should check that nothing else in the review requires editing, such as references to other Cochrane Reviews that may have been updated, or additions to the Acknowledgements. The ‘Declarations of interest’ sections of the review should be updated.

Finally, to inform returning readers, authors should summarize key changes in the ‘What’s new’ section. This should include the number of new studies and participants in those studies, and the nature of any changes in findings, the certainty of the evidence (e.g. using GRADE) and in the implications for practice.

IV.5.1 Changes in authorship

If there is a change in the authorship of the review, such as new authors joining the team, or an entirely new team of authors updating the review, the by-line (list of authors) may need to be changed. The decision regarding who is named in the by-line of an updated review, and in what order, should be assessed in terms of contributions to content in the updated version of the review (which will include historical content), and responsibility for approving the final content of the manuscript. If an author is no longer actively contributing to or involved in the approval of an updated review, the author should not be listed in the by-line of the new version and should be named in the Acknowledgements section. In addition, the contributions of all authors to both the update and earlier versions of the review should be described in the ‘Contributions of authors’ section.

See Cochrane’s policy on authorship and contributorship for Cochrane Reviews for more information.

IV.6 Chapter information

Authors: Miranda Cumpston and Ella Flemyng

Acknowledgements : This chapter builds on earlier versions of the Handbook . Contributors to earlier versions include Jacqueline Chandler, Julian Higgins, Rachel Marshall, Ruth Foxlee and members of the former Updating Working Group (Mike Clarke, Mark Davies, Davina Ghersi, Sally Green, Sonja Henderson, Harriet MacLehose, Jessie McGowan, David Moher, Rob Scholten (convenor) and Phil Wiffen). David Tovey, Carol Lefebvre and Sally Hopewell provided comments on earlier versions. Rachel Marshall re-drafted version 5.1 on which this version was based with input from Harriet MacLehose. Mona Nasser contributed to section IV.2.1. Rachel Churchill contributed to the re-structuring of this version. The work of Garner and colleagues (Garner et al 2016), a key reference used throughout, was based on a consensus meeting of experts funded by Cochrane.

IV.7 References

Adams SP, Tsang M, Wright JM. Lipid lowering efficacy of atorvastatin. Cochrane Database of Systematic Reviews 2012; 12 : CD008226.

Ahmadzai N, Newberry SJ, Maglione MA, Tsertsvadze A, Ansari MT, Hempel S, Motala A, Tsouros S, Schneider Chafen JJ, Shanman R, Moher D, Shekelle PG. A surveillance system to assess the need for updating systematic reviews. Systematic Reviews 2013; 2 : 104.

Elliott JH, Synnot A, Turner T, Simmonds M, Akl EA, McDonald S, Salanti G, Meerpohl J, MacLehose H, Hilton J, Tovey D, Shemilt I, Thomas J, Living Systematic Review N. Living systematic review: 1. Introduction-the why, what, when, and how. Journal of Clinical Epidemiology 2017; 91 : 23-30.

Garner P, Hopewell S, Chandler J, MacLehose H, Schünemann HJ, Akl EA, Beyene J, Chang S, Churchill R, Dearness K, Guyatt G, Lefebvre C, Liles B, Marshall R, Martinez Garcia L, Mavergames C, Nasser M, Qaseem A, Sampson M, Soares-Weiser K, Takwoingi Y, Thabane L, Trivella M, Tugwell P, Welsh E, Wilson EC, Schünemann HJ, Panel for Updating Guidance for Systematic Reviews (PUGs). When and how to update systematic reviews: consensus and checklist. BMJ 2016; 354 : i3507.

Green S, Buchbinder R, Hetrick S. Physiotherapy interventions for shoulder pain. Cochrane Database of Systematic Reviews 2003; 2 : CD004258.

Higgins JPT. Convincing evidence from controlled and uncontrolled studies on the lipid-lowering effect of a statin. Cochrane Database of Systematic Reviews 2012: ED000049.

Page MJ, Green S, Kramer S, Johnston RV, McBain B, Buchbinder R. Electrotherapy modalities for adhesive capsulitis (frozen shoulder). Cochrane Database of Systematic Reviews 2014a; 10 : CD011324.

Page MJ, Green S, Kramer S, Johnston RV, McBain B, Chau M, Buchbinder R. Manual therapy and exercise for adhesive capsulitis (frozen shoulder). Cochrane Database of Systematic Reviews 2014b; 8 : CD011275.

Page MJ, Green S, McBain B, Surace SJ, Deitch J, Lyttle N, Mrocki MA, Buchbinder R. Manual therapy and exercise for rotator cuff disease. Cochrane Database of Systematic Reviews 2016a; 6 : CD012224.

Page MJ, Green S, Mrocki MA, Surace SJ, Deitch J, McBain B, Lyttle N, Buchbinder R. Electrotherapy modalities for rotator cuff disease. Cochrane Database of Systematic Reviews 2016b; 6 : CD012225.

Prasad K, Singh MB, Ryan H. Corticosteroids for managing tuberculous meningitis. Cochrane Database of Systematic Reviews 2016; 4 : CD002244.

Sampson M, Shojania KG, McGowan J, Daniel R, Rader T, Iansavichene AE, Ji J, Ansari MT, Moher D. Surveillance search techniques identified the need to update systematic reviews. Journal of Clinical Epidemiology 2008; 61 : 755-762.

Shea B, Boers M, Grimshaw JM, Hamel C, Bouter LM. Does updating improve the methodological and reporting quality of systematic reviews? BMC Medical Research Methodology 2006; 6 : 27.

Shekelle P, Newberry S, Wu H, Suttorp M, Motala A, Lim Y, et al. Identifying Signals for Updating Systematic Reviews: A Comparison of Two Methods (Prepared by: The RAND Corporation, Southern California Evidence-based Practice Center, Santa Monica, CA under Contract No 290-2007-10062I; Tufts Evidence-based Practice Center, Tufts Medical Center, Boston, MA under Contract No 290-2007-10055I; University of Ottawa Evidence-based Practice Center, Ottawa, Canada under Contract No 290-2007-10059I). Rockville (MD): Agency for Healthcare Research and Quality; 2011.

Shojania KG, Sampson M, Ansari MT, Ji J, Doucette S, Moher D. How quickly do systematic reviews go out of date? A survival analysis. Annals of Internal Medicine 2007; 147 : 224-233.

Takwoingi Y, Hopewell S, Tovey D, Sutton AJ. A multicomponent decision tool for prioritising the updating of systematic reviews. BMJ 2013; 347 : f7191.

Tovey D, Marshall R, Bazian Ltd, Hopewell S, Rader T. National Institute for Health Research Cochrane-National Health Service Engagement Award Scheme Fit for purpose: centralised updating support for high-priority Cochrane reviews 2011. http://www.editorial-unit.cochrane.org/fit-purpose-centralised-updating-support-high-priority-cochrane-reviews .

Tsertsvadze A, Maglione M, Chou R, Garritty C, Coleman C, Lux L, Bass E, Balshem H, Moher D. Updating comparative effectiveness reviews: Current efforts in AHRQ's Effective Health Care Program. Journal of Clinical Epidemiology 2011; 64 : 1208-1215.

Zani B, Gathu M, Donegan S, Olliaro PL, Sinclair D. Dihydroartemisinin-piperaquine for treating uncomplicated Plasmodium falciparum malaria. Cochrane Database of Systematic Reviews 2014; 1 : CD010927.

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Vitamin supplementation for preventing miscarriage

Miscarriage is a common complication of pregnancy that can be caused by a wide range of factors. Poor dietary intake of vitamins has been associated with an increased risk of miscarriage, therefore supplementing women with vitamins either prior to or in early pregnancy may help prevent miscarriage.

The objectives of this review were to determine the effectiveness and safety of any vitamin supplementation, on the risk of spontaneous miscarriage.

Search methods

We searched the Cochrane Pregnancy and Childbirth Group Trials Register (6 November 2015) and reference lists of retrieved studies.

Selection criteria

All randomised and quasi‐randomised trials comparing supplementation during pregnancy with one or more vitamins with either placebo, other vitamins, no vitamins or other interventions. We have included supplementation that started prior to conception, periconceptionally or in early pregnancy (less than 20 weeks' gestation).

Data collection and analysis

Three review authors independently assessed trials for inclusion, extracted data and assessed trial quality. We assessed the quality of the evidence using the GRADE approach. The quality of evidence is included for numerical results of outcomes included in the 'Summary of findings' tables.

Main results

We included a total of 40 trials (involving 276,820 women and 278,413 pregnancies) assessing supplementation with any vitamin(s) starting prior to 20 weeks' gestation and reporting at least one primary outcome that was eligible for the review. Eight trials were cluster‐randomised and contributed data for 217,726 women and 219,267 pregnancies in total.

Approximately half of the included trials were assessed to have a low risk of bias for both random sequence generation and adequate concealment of participants to treatment and control groups.

Vitamin C supplementation

There was no difference in the risk of total fetal loss (risk ratio (RR) 1.14, 95% confidence interval (CI) 0.92 to 1.40, seven trials, 18,949 women; high‐quality evidence ); early or late miscarriage (RR 0.90, 95% CI 0.65 to 1.26, four trials, 13,346 women; moderate‐quality evidence ); stillbirth (RR 1.31, 95% CI 0.97 to 1.76, seven trials, 21,442 women; moderate‐quality evidence ) or adverse effects of vitamin supplementation (RR 1.16, 95% CI 0.39 to 3.41, one trial, 739 women; moderate‐quality evidence ) between women receiving vitamin C with vitamin E compared with placebo or no vitamin C groups. No clear differences were seen in the risk of total fetal loss or miscarriage between women receiving any other combination of vitamin C compared with placebo or no vitamin C groups.

Vitamin A supplementation

No difference was found in the risk of total fetal loss (RR 1.01, 95% CI 0.61 to 1.66, three trials, 1640 women; low‐quality evidence ); early or late miscarriage (RR 0.86, 95% CI 0.46 to 1.62, two trials, 1397 women; low‐quality evidence ) or stillbirth (RR 1.29, 95% CI 0.57 to 2.91, three trials, 1640 women; low‐quality evidence ) between women receiving vitamin A plus iron and folate compared with placebo or no vitamin A groups. There was no evidence of differences in the risk of total fetal loss or miscarriage between women receiving any other combination of vitamin A compared with placebo or no vitamin A groups.

Multivitamin supplementation

There was evidence of a decrease in the risk for stillbirth among women receiving multivitamins plus iron and folic acid compared iron and folate only groups (RR 0.92, 95% CI 0.85 to 0.99, 10 trials, 79,851 women; high‐quality evidence ). Although total fetal loss was lower in women who were given multivitamins without folic acid (RR 0.49, 95% CI 0.34 to 0.70, one trial, 907 women); and multivitamins with or without vitamin A (RR 0.60, 95% CI 0.39 to 0.92, one trial, 1074 women), these findings included one trial each with small numbers of women involved. Also, they include studies where the comparison groups included women receiving either vitamin A or placebo, and thus require caution in interpretation.

We found no difference in the risk of total fetal loss (RR 0.96, 95% CI 0.93 to 1.00, 10 trials, 94,948 women; high‐quality evidence ) or early or late miscarriage (RR 0.98, 95% CI 0.94 to 1.03, 10 trials, 94,948 women; moderate‐quality evidence ) between women receiving multivitamins plus iron and folic acid compared with iron and folate only groups.

There was no evidence of differences in the risk of total fetal loss or miscarriage between women receiving any other combination of multivitamins compared with placebo, folic acid or vitamin A groups.

Folic acid supplementation

There was no evidence of any difference in the risk of total fetal loss, early or late miscarriage, stillbirth or congenital malformations between women supplemented with folic acid with or without multivitamins and/or iron compared with no folic acid groups.

Antioxidant vitamins supplementation

There was no evidence of differences in early or late miscarriage between women given antioxidant compared with the low antioxidant group (RR 1.12, 95% CI 0.24 to 5.29, one trial, 110 women).

Authors' conclusions

Taking any vitamin supplements prior to pregnancy or in early pregnancy does not prevent women experiencing miscarriage. However, evidence showed that women receiving multivitamins plus iron and folic acid had reduced risk for stillbirth. There is insufficient evidence to examine the effects of different combinations of vitamins on miscarriage and miscarriage‐related outcomes.

Plain language summary

What is the issue?

Miscarriage occurs frequently among pregnant women but it is often difficult to know the factors responsible. Poor diet, without enough vitamins, has been associated with an increased risk of women losing their baby in early pregnancy. Does vitamin supplementation taken by women before pregnancy and during pregnancy decrease the risk of spontaneous miscarriage? Does supplementation improve maternal, birth and infant outcomes, and are there any side effects?

Why is this important?

Vitamin supplementation is commonly recommended for pregnant women and women planning to conceive. Considering the widespread use of vitamin supplementation before and during pregnancy, it is important to study the relation between vitamin supplementation and early pregnancy outcomes, particularly since the causes of miscarriage are unknown and the nutritional status of a mother can affect her baby’s development.

What evidence did we find?

This review included 40 randomised controlled trials involving 276,820 women and 278,413 pregnancies. Supplementing women with any vitamins does not reduce the number of women who have miscarriages. However, the risk for stillbirth was reduced among women receiving multivitamins plus iron and folic acid compared with iron and folate only groups. Although total fetal loss was lower in women who were given multivitamins without folic acid and multivitamins with or without vitamin A, these findings included one trial each with small numbers of women involved. Also, they include studies where the comparison groups included women receiving either vitamin A or placebo, and thus require caution in interpretation.

What does this mean?

Taking vitamin supplements before pregnancy or in early pregnancy may be beneficial; but this review did not show sufficient evidence that taking vitamin supplements prevents miscarriage.

Summary of findings

Summary of findings for the main comparison.

1 Not effective but 95% CI is narrow and precise.

2 Non significant with wide 95% CI.

3 Small sample size.

Summary of findings 2

1 High and unclear risk of attrition bias.

2 Wide 95% CI.

Summary of findings 3

1 Publication bias detected by funnel plot.

2 Wide confidence interval crossing the line of no effect.

Description of the condition

Miscarriage can be caused by a wide range of factors, and determining the aetiology is often difficult given the variety of underlying mechanisms potentially responsible. Consideration of the timing of the miscarriage is also important, as diverse causes of miscarriage manifest at different periods of gestation. The most common causes include abnormal chromosomal rearrangements, endocrinological disorders and uterine abnormalities ( Garrido‐Gimenez 2015 ). Early miscarriages are mostly associated with chromosomal abnormalities, defective placental development and maternal disease conditions; while late miscarriages are more likely due to structural problems of the uterus and/or cervix such as cervical incompetence. Women experiencing recurrent miscarriage often have an underlying medical condition such as autoimmune disease, i.e. systemic lupus erythematosus and antiphospholipid syndrome, or other blood clotting disorders such as hyperhomocysteinaemia (high levels of homocysteine in the blood) or another thrombophilia ( Preston 1996 ). Other risk factors for miscarriage include higher maternal age at conception, multiple pregnancies and a history of previous miscarriage (Baba 2011; Garcıa‐Enguıdanos 2002 ; Hure 2012 ). Behavioural factors including alcohol consumption ( Maconochie 2007 ), smoking (Baba 2011; Hure 2012 ), use of illicit drugs ( Garcıa‐Enguıdanos 2002 ), and exposure to non‐steroidal anti‐inflammatory drugs (NSAIDs) around the time of conception are also suggested causes of miscarriage ( Li 2003 ; Nielsen 2001 ). While several factors may promote miscarriage, for a great proportion of women, no cause can be found.

In clinical practice, surgical and non‐surgical interventions are used in the management of miscarriage. Bed rest, commonly prescribed for preventing miscarriage, is lacking proven benefit (Aleman 2005). Similarly, there is currently insufficient evidence on the benefit provided from the use of uterine muscle relaxant drugs ( Lede 2005 ), Chinese herbal medicine ( Li 2012 ), hormones ( Devaseelan 2010 ; Haas 2013 ; Lim 1013 ; Morley 2013 ), and immunotherapy ( Wong 2014 ).

Description of the intervention

Vitamins are essential nutrients required in the body for numerous functions such as to ensure normal metabolism, physical growth and development as well as to prevent diseases. Based on evidence from observational studies, vitamin supplementation has been advocated for the prevention of miscarriage ( Hasan 2009 ; Maconochie 2007 ), most commonly folate and B vitamins. Due to consistent associations between pregnancy complications and decreased antioxidant defence and infections, it has been suggested that vitamin supplementation during pregnancy might provide protection against adverse pregnancy outcomes and may influence the risk of spontaneous miscarriage in women.

How the intervention might work

Vitamins are either water soluble – such as vitamin C and the B group vitamins (including folate) or fat soluble such as vitamins A, D, E and K. They may be obtained directly from the diet or in the form of dietary supplements of either individual vitamin or multivitamin preparations. Multivitamins contain a range of vitamins and minerals, usually in doses similar to the recommended dietary intakes.

The rationale for vitamin supplementation for the prevention of miscarriage is based on epidemiological studies linking healthy dietary patterns with reduced risk for miscarriage ( Hasan 2009 ; Maconochie 2007 ). Several studies have reported an association between certain vitamin deficiencies and adverse reproductive outcomes ( George 2002 ; Guerra‐Shinohara 2010 ; Hübner 2008 ; Reznikoff‐Etiévant 2002 ). Nutritional mechanisms underlying this association include homocysteine metabolism and oxidative stress.

Homocysteine is an amino acid that is involved in several key metabolic processes, vital to ongoing cellular activity of the living organism. The metabolism of homocysteine is facilitated by B vitamins and folate. The concentration of homocysteine in the blood is determined by various dietary factors, including folate, vitamin B6 and vitamin B12. Disturbance of maternal and fetal homocysteine metabolism has been associated with various obstetric conditions including miscarriage ( Hague 2003 ; Nelen 2000 ), and hyperhomocysteinaemia is considered a risk factor for recurrent early pregnancy loss. Therefore, supplementation with B vitamins and folate may influence the risk of spontaneous miscarriage in women with recurrent miscarriage. Moreover, low serum vitamin B12 concentrations have been reported in women with recurrent miscarriage ( Hübner 2008 ). Evidence on the effect of vitamin supplementation, particularly folic acid, on risk of miscarriage is still conflicting; however the few studies that have adjusted for confounding support a protective effect.

Oxidative stress is caused by an imbalance between pro‐oxidants and antioxidants. Pro‐oxidants act either by generating reactive oxygen species (ROS) or by inhibiting antioxidant systems. In living cells, ROS are formed continuously both from biochemical processes occurring in the body and in reaction to external factors. Excessive ROS production may however, overpower the body’s natural antioxidant defence system, creating an environment unsuitable for normal female reproductive processes ( Al‐Gubory 2010 ). A recent review of evidence from experimental and observational studies suggests that oxidative stress is an important cause in spontaneous and recurrent miscarriage ( Agarwal 2012b ; Al‐Gubory 2010 ; Gupta 2007 ). Adequate maternal antioxidant status before and during pregnancy could prevent and control oxidative stress. Therefore, intake of antioxidant vitamins such as vitamin C and vitamin E may be an important factor to reduce the risk of miscarriage. In a population‐based case‐control study, vitamin supplementation (including vitamin C), and eating fresh fruits and vegetables daily were associated with reduced risk of miscarriage ( Maconochie 2007 ). Another observational study demonstrated an association between the risk of spontaneous early miscarriage and dietary factors; poor intake of green vegetables, fruit and dairy products coupled with a high intake of fat was associated with a high risk of spontaneous miscarriage ( Di Cintio 2001 ). There is limited information available about the impact of vitamins on the risk of early versus late miscarriage. However, dietary factors could theoretically influence structural abnormalities such as cervical incompetence. There is a growing body of research investigating the relationship between nutrition and placental development, fetal growth, pregnancy outcomes and adult diseases ( McMillen 2008 ; Meher 2015 ; Wu 2004 ). Therefore, adequate maternal nutrition, particularly vitamin intake, may be an important factor in preventing spontaneous miscarriage. Currently, little information is available about the most appropriate vitamin type or combination. Similarly, many commercially available vitamin preparations contain a range of combinations of vitamins. Therefore, this review will cover all vitamin types.

Why it is important to do this review

Vitamin supplementation is frequently recommended for pregnant women and women planning to conceive. The documented benefits of supplementation relate mainly to the lowered risk of congenital anomalies such as neural tube defects ( Hovdenak 2012 ; MRC Vitamin Study Research Group 1991 ). Given the widespread vitamin supplementation before and during pregnancy, studying the relationship between this common exposure and early pregnancy outcomes is of great value, particularly since the causes of miscarriage are unknown and this exposure is known to affect specific developmental processes.

This is an update of a Cochrane review first published in 2005 and previously updated in 2011. The previously updated review included 28 trials involving 96,674 women (98,267 pregnancies ( Rumbold 2011 )). Based on available evidence, Rumbold 2011 concluded that taking any vitamin supplements prior to pregnancy or in early pregnancy does not prevent women from experiencing miscarriage or stillbirth. However, there is insufficient evidence to examine the effects of different combinations of vitamins on miscarriage. In the current review, we examined the effect of different vitamin combinations on the risk of miscarriage. The scope of the current update has been restricted to look at miscarriage and miscarriage‐related outcomes.

• To determine the effectiveness and safety of any vitamin supplementation taken by women prior to conception, periconceptionally and in early pregnancy on the risk of spontaneous miscarriage.
• If vitamins are effective, to determine which of these agents are best and to compare vitamins with other interventions.

Criteria for considering studies for this review

Types of studies.

All randomised trials (including individual‐ and cluster‐randomised) and quasi‐randomised trials comparing one or more vitamins with either placebo, other vitamins, no vitamins or other interventions, prior to conception, periconceptionally or in early to mid pregnancy. Cross‐over trials were not included.

Types of participants

Pregnant women (less than 20 weeks' gestation) or women in the reproductive age group planning on becoming pregnant in the near future, regardless of whether they are at low or high risk of having a miscarriage. No restrictions were placed on the age of participants or past obstetric history.

Types of interventions

Comparisons of specific vitamin(s), alone or in combination with other agents with either placebo, other vitamin(s), no vitamin(s) or other interventions for the prevention of miscarriage, either in areas where there is an inadequate dietary intake or where there is a presumed adequate intake of that vitamin(s).

The review authors deemed it important to include any supplementation trials, where supplementation began prior to 20 weeks' gestation, and where at least one miscarriage‐related outcome as specified in the review was reported, even if the intervention was not specifically for the prevention of miscarriage. We excluded trials where the onset of supplementation occurred definitely after 20 weeks' gestation or where it was reported that the majority of women commenced supplementation after 20 weeks' gestation. We included trials where the onset of supplementation occurred both prior to and after 20 weeks' gestation, and when it could not be established whether the majority of the women started supplementation prior to 20 weeks' gestation.

Types of outcome measures

The scope of the current update has been restricted to look at miscarriage and miscarriage‐related outcomes.

Primary outcomes

• Total fetal loss, defined as the combined numbers of early miscarriage (spontaneous pregnancy loss less than 12 weeks' gestation), late miscarriage (spontaneous pregnancy loss greater than or equal to 12 and less than 24 weeks), and stillbirth (pregnancy loss at greater than or equal to 24 weeks).
• Early or late miscarriage.

To overcome wide variation in the definitions of miscarriage and stillbirth between studies, we included the combined outcome 'total fetal loss' in the review.

Secondary outcomes

• Stillbirth.
• Congenital malformations.
• Adverse effects of vitamin supplementation sufficient to stop supplementation, such as manifestations of hypervitaminosis, headache, nausea, vomiting, diarrhoea

Search methods for identification of studies

The following methods section of this review is based on a standard template used by the Cochrane Pregnancy and Childbirth Group.

Electronic searches

We searched the Cochrane Pregnancy and Childbirth Group’s Trials Register by contacting the Trials Search Co‐ordinator (6 November 2015).

The Register is a database containing over 21,000 reports of controlled trials in the field of pregnancy and childbirth. For full search methods used to populate the Pregnancy and Childbirth Group's Trials Register including the detailed search strategies for CENTRAL, MEDLINE, Embase and CINAHL; the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service, please follow this link to the editorial information about the Cochrane Pregnancy and Childbirth Group in The Cochrane Library and select the ‘ Specialized Register ’ section from the options on the left side of the screen.

Briefly, the Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co‐ordinator and contains trials identified from:

• monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
• weekly searches of MEDLINE (Ovid);
• weekly searches of Embase (Ovid);
• monthly searches of CINAHL (EBSCO);
• handsearches of 30 journals and the proceedings of major conferences;
• weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.

Search results are screened by two people and the full text of all relevant trial reports identified through the searching activities described above is reviewed. Based on the intervention described, each trial report is assigned a number that corresponds to a specific Pregnancy and Childbirth Group review topic (or topics), and is then added to the Register. The Trials Search Co‐ordinator searches the Register for each review using this topic number rather than keywords. This results in a more specific search set which has been fully accounted for in the relevant review sections ( Included studies ; Excluded studies ; Studies awaiting classification ; Ongoing studies ).

[We carried out additional author searching in an earlier version of this review ( Rumbold 2005 ), see Appendix 1 for details]

Searching other resources

We searched the reference lists of retrieved studies.

We did not apply any language or date restrictions.

For methods used in the previous version of this review, see Rumbold 2011 .

For this update, the following methods were used for assessing the 90 reports that were identified as a result of the updated search.

Selection of studies

Two review authors independently assessed all the potential studies identified as a result of the search strategy for inclusion. Disagreements were resolved through discussion and, when required, we consulted a third person. We created a study flow diagram to map out the number of records identified, included and excluded.

Data extraction and management

We collected data from the selected studies using a pre‐designed data extraction form. For eligible studies, two review authors extracted the data using the agreed form. We resolved discrepancies through discussion. If discrepancies could not be resolved, we consulted a third review author. We entered data into Review Manager software ( RevMan 2014 ) and checked for accuracy. When information regarding any of the above was unclear, we attempted to contact authors of the original reports to provide further details.

Assessment of risk of bias in included studies

Two review authors independently assessed risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions ( Higgins 2011 ). We resolved any disagreement by discussion or by involving a third assessor.

(1) Random sequence generation (checking for possible selection bias)

We describe for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.

We assessed the method as:

• low risk of bias (any truly random process, e.g. random number table; computer random number generator);
• high risk of bias (any non‐random process, e.g. odd or even date of birth; hospital or clinic record number);
• unclear risk of bias.

(2) Allocation concealment (checking for possible selection bias)

We describe for each included study the method used to conceal allocation to interventions prior to assignment and assessed whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.

We assessed the methods as:

• low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
• high risk of bias (open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth);

(3.1) Blinding of participants and personnel (checking for possible performance bias)

We describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We considered that studies were at low risk of bias if they were blinded, or if we judged that the lack of blinding would be unlikely to affect results. We assessed blinding separately for different outcomes or classes of outcomes.

• low, high or unclear risk of bias for participants;
• low, high or unclear risk of bias for personnel.

(3.2) Blinding of outcome assessment (checking for possible detection bias)

We describe for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We assessed blinding separately for different outcomes or classes of outcomes.

We assessed methods used to blind outcome assessment as:

• low, high or unclear risk of bias.

(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)

We describe for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We state whether attrition and exclusions were reported and the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information was reported, or supplied by the trial authors, we re‐included missing data in the analyses which we undertook.

We assessed methods as:

• low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);
• high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomisation);

(5) Selective reporting (checking for reporting bias)

We describe for each included study how we investigated the possibility of selective outcome reporting bias and what we found.

• low risk of bias (where it is clear that all of the study’s pre‐specified outcomes and all expected outcomes of interest to the review have been reported);
• high risk of bias (where not all the study’s pre‐specified outcomes have been reported; one or more reported primary outcomes were not pre‐specified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);

(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)

We describe for each included study any important concerns we have about other possible sources of bias.

We assessed whether each study was free of other problems that could put it at risk of bias:

• low risk of other bias;
• high risk of other bias;
• unclear whether there is risk of other bias.

(7) Overall risk of bias

We made judgements about whether studies were at high risk of bias, according to the criteria given in the Handbook (Higgins 2011). With reference to (1) to (6) above, we assessed the likely magnitude and direction of the bias and whether we considered it was likely to impact on the findings. We explored the impact of the level of bias through undertaking sensitivity analyses ‐ see Sensitivity analysis .

Assessment of the quality of the evidence using the GRADE approach

For this update, we assessed the quality of the evidence using the GRADE approach as outlined in the GRADE handbook in order to assess the quality of the body of evidence relating to the following outcomes in the comparisons: 1) vitamin C and vitamin E versus placebo, 2) vitamin A plus iron plus folate versus iron plus folate and 3) multivitamin plus iron plus folate versus iron plus folate.

• Total fetal loss, defined as the combined numbers of early miscarriage (spontaneous pregnancy loss less than 12 weeks’ gestation), late miscarriage (spontaneous pregnancy loss greater than or equal to 12 and less than 24 weeks), and stillbirth (pregnancy loss at greater than or equal to 24 weeks).
• Adverse effects of vitamin supplementation sufficient to stop supplementation.

We used the GRADEpro Guideline Development Tool to import data from Review Manager 5.3 ( RevMan 2014 ) in order to create ’Summary of findings’ tables. A summary of the intervention effect and a measure of quality for each of the above outcomes was produced using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of the body of evidence for each outcome. The evidence was downgraded from 'high quality' by one level for serious (or by two levels for very serious) limitations, depending on assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates or potential publication bias.

Measures of treatment effect

Dichotomous data.

For dichotomous data, we present results as summary risk ratio (RR) with 95% confidence intervals (CI).

Continuous data

For continuous data, we planned to use the mean difference (MD) if outcomes were measured in the same way between trials and, if appropriate, the standardised mean difference (SMD) to combine trials that measured the same outcome, but used different methods.

Unit of analysis issues

Where trials recruited women prior to becoming pregnant, we reported the denominators for each trial as all women randomised; or where there was accurate information about the number of women in each trial who became pregnant, we reported the denominators as the number of women randomised with confirmed pregnancy.

We included all included trials in the initial analysis which we performed by any vitamin to include all vitamin combinations and then by individual vitamin type.

Cluster‐randomised trials

We included cluster‐randomised trials in the analyses along with individually‐randomised trials. We used the effect estimates and uncertainty range from the cluster trials to perform the meta‐analysis using the generic inverse variance approach for the meta‐analysis of dichotomous outcomes where trials using cluster‐randomisation techniques were included ( Alderson 2004 ).

Dealing with missing data

For included studies, we noted levels of attrition. We explored the impact of including studies with high levels of missing data in the overall assessment of treatment effect by using sensitivity analysis.

For all outcomes, we carried out analyses, as far as possible, on an intention‐to‐treat basis, i.e. we attempted to include all participants randomised to each group in the analyses, and all participants were analysed in the group to which they were allocated, regardless of whether or not they received the allocated intervention. The denominator for each outcome in each trial was the number randomised minus any participants whose outcomes were known to be missing.

Assessment of heterogeneity

We applied tests of heterogeneity between trials to assess the significance of any differences between trials in the analyses. We regarded heterogeneity as substantial if the I² was greater than 30% and either the Tau² was greater than zero, or there was a low P value (less than 0.10) in the Chi² test for heterogeneity.

Assessment of reporting biases

We investigated reporting biases (such as publication bias) using funnel plots. We assessed funnel plot asymmetry visually. If asymmetry was suggested by a visual assessment, we performed exploratory analyses to investigate it.

Data synthesis

We carried out statistical analysis using the Review Manager software ( RevMan 2014 ). We used fixed‐effect meta‐analysis for combining data where it was reasonable to assume that studies were estimating the same underlying treatment effect: i.e. where trials were examining the same intervention, and the trials’ populations and methods were judged sufficiently similar. If there was clinical heterogeneity sufficient to expect that the underlying treatment effects differed between trials, or if substantial statistical heterogeneity was detected, we used random‐effects meta‐analysis to produce an overall summary, if an average treatment effect across trials was considered clinically meaningful. We treated the random‐effects summary as the average of the range of possible treatment effects and we discuss the clinical implications of treatment effects differing between trials. If the average treatment effect was not clinically meaningful, we did not combine trials. Where we used random‐effects analyses, we have presented the results as the average treatment effect with 95% confidence intervals, and the estimates of Tau² and I².

Subgroup analysis and investigation of heterogeneity

Had we identified substantial heterogeneity, we planned to investigate it using subgroup analyses and sensitivity analyses and to consider whether an overall summary was meaningful, and if it was, to use random‐effects analysis to produce it.

In this update, we were not able to carry out the following subgroup analyses:

• the dose of vitamin(s) (below or above the recommended dietary intake); and the duration of vitamin usage, based on time of trial entry: before pregnancy, < 12 weeks’ gestation, between 12‐20 weeks’ gestation or ’mixed’, which included women enrolled before and after 20 weeks’ gestation;
• their risk of spontaneous miscarriage (high risk defined as the presence of medical conditions associated with miscarriage such as hyperhomocysteinaemia, thrombophilia, antiphospholipid syndrome, systemic lupus erythematosus; low risk defined as none of the above conditions); their risk of recurrent miscarriage (high risk defined as two or more previous consecutive spontaneous miscarriages, and/or the presence of medical conditions associated with miscarriage such as hyperhomocysteinaemia, thrombophilia, antiphospholipid syndrome, systemic lupus erythematosus; low risk defined as none of the above conditions);
• low or adequate dietary vitamin intake at trial entry (low intake defined as less than the recommended daily intake for each vitamin in that setting, as measured by dietary questionnaire).

We would have included all outcomes in the subgroup analysis.

We planned to assess subgroup differences by interaction tests available within RevMan (RevMan 2014) and to report the results of subgroup analyses quoting the Chi² statistic and P value, and the interaction test I² value.

Sensitivity analysis

We carried out sensitivity analysis to explore the effects of trial quality and type of randomisation on the primary outcomes related to fetal loss (total fetal loss and early or late miscarriage). We included only trials with 'adequate' rating on allocation concealment, We considered these trials to be of high quality. We also carried out sensitivity analysis by excluding cluster‐randomised trials and comparing the results of cluster‐randomised trials with the individually‐randomised trials.

Description of studies

See tables Characteristics of included studies and Characteristics of excluded studies for details of individual studies.

Included studies

For the 2016 update, we included a total of 40 trials (involving 276,820 women) assessing supplementation with specific vitamin(s) starting prior to 20 weeks' gestation. Many of the trials assessed interventions not specifically for the prevention of miscarriage, however, the authors included any supplementation trials, where supplementation began prior to 20 weeks' gestation, and where at least one miscarriage‐related outcome as specified in the review was reported.

Participants

The demographic and obstetric characteristics of the women varied widely between the trials (see table Characteristics of included studies ). The 40 included trials contributed data for analysis from 276,820 women. Eight of the 40 included studies were cluster‐randomised trials including 217,726 women ( Bhutta 2009 ; Katz 2000 ; Summit 2008 ; Sunawang 2009 ; West 2011 ; West 2014 ; Zagre 2007 ; Zeng 2008 ). Two of the trials from the previous version of this review (one cluster ( Katz 2000 ), and one small trial ( Roberfroid 2008 )) included women who were pregnant more than once in the study period; resulting in data contributing to 59,146 pregnancies for the individual trials and 219,267 pregnancies from the cluster trials. Five trials enrolled women prior to conception ( Czeizel 1994 ; Hemmi 2003 ; ICMR 2000 ; Kirke 1992 ; MRC 1991 ) and asked women to continue taking the supplements up until the second or third missed menstrual period. One trial ( Katz 2000 ) supplemented women from before conception, through pregnancy and postpartum for a total of 3.5 years postpartum. Another eight trials enrolled women in the first trimester ( Briscoe 1959 ; Hans 2010 ; Rumiris 2006 ; Tofail 2008 ; West 2011 ; West 2014 ; Wibowo 2012 ; Zagre 2007 ), and 24 trials in early to mid pregnancy ( Bhutta 2009 ; Chappell 1999 ; Fawzi 1998 ; Fawzi 2007 ; Fleming 1968 ; Fleming 1986 ; Kumwenda 2002 ; McCance 2010 ; Osrin 2005 ; People's League 1942 ; Poston 2006 ; Prawirohartono 2011 ; Roberfroid 2008 ; Roberts 2010 ; Rumbold 2006 ; Rush 1980 ; Schmidt 2001 ; Spinnato 2007 ; Steyn 2003 ; Sunawang 2009 ; Van den Broek 2006 ; Villar 2009 ; Xu 2010 ; Zeng 2008 ). Some of the trials enrolling women in early to mid pregnancy included women enrolled at or after 20 weeks' gestation ( Chappell 1999 ; Fawzi 1998 ; Fawzi 2007 ; Fleming 1968 ; Fleming 1986 ; Kumwenda 2002 ; McCance 2010 ; Osrin 2005 ; People's League 1942 ; Roberfroid 2008 ; Rumbold 2006 ; Rush 1980 ; Schmidt 2001 ; Spinnato 2007 ; Steyn 2003 ; Van den Broek 2006 ; Villar 2009 ; Zeng 2008 ). One trial ( Summit 2008 ), enrolled 41,839 women at 'any gestational age', although more than 70% of the women were enrolled in the first or second trimester.

Two trials ( Fawzi 1998 ; Kumwenda 2002 ) involved vitamin A supplementation in women seropositive for the Human Immunodeficiency Virus (HIV); one trial ( Poston 2006 ) involved only women with clinical risk factors for pre‐eclampsia, while one trial ( McCance 2010 ), limited the eligibility to women with type1 diabetes. Roberts 2010 involved only nulliparous women.

Baseline characteristics of women enrolled in the intervention group and control group were comparable in all the trials except two ( Xu 2010 ; Zagre 2007 ). In Xu 2010 , there was a slightly higher proportion of women with multiple pregnancies in the placebo group; while in Zagre 2007 , women in the control group tended to be poorer and less educated, while women in the intervention group had larger households and used more preventive measures against malaria.

The trials were conducted in both resource‐rich and resource‐poor countries including the United States ( Briscoe 1959 ; Roberts 2010 ; Rush 1980 ), Canada ( Xu 2010 ), the United Kingdom ( Chappell 1999 ; McCance 2010 ; People's League 1942 ; Poston 2006 ), Hungary ( Czeizel 1994 ), Tanzania ( Fawzi 1998 ; Fawzi 2007 ), Nigeria ( Fleming 1968 ; Fleming 1986 ), Burkino Faso ( Roberfroid 2008 ), Japan ( Hemmi 2003 ), India ( ICMR 2000 ), Nepal ( Katz 2000 ; Osrin 2005 ), the Republic of Ireland ( Kirke 1992 ), Uganda ( Hans 2010 ), Bangladesh ( West 2011 ; West 2014 , Tofail 2008 ), China ( Zeng 2008 ), Niger ( Zagre 2007 ), Pakistan ( Bhutta 2009 ), Australia ( Rumbold 2006 ), Brazil ( Spinnato 2007 ), Mexico ( Xu 2010 ), Malawi ( Kumwenda 2002 ; Van den Broek 2006 ), Indonesia ( Prawirohartono 2011 ; Rumiris 2006 ; Schmidt 2001 ; Sunawang 2009 ; Summit 2008 ; Wibowo 2012 ), and South Africa ( Steyn 2003 ). One trial involved 33 international centres ( MRC 1991 ) and another trial was a multi‐country study involving India, Peru, South Africa and Vietnam ( Villar 2009 ).

Interventions

The 40 trials assessed a range of vitamin supplements, alone or in combination with other supplements. The vitamins included vitamin A, alone or with iron, folic acid, multivitamins, or β‐carotene ( Fawzi 1998 ; Katz 2000 ; Kumwenda 2002 ; Prawirohartono 2011 ; Schmidt 2001 ; Van den Broek 2006 ; West 2011 ); vitamin C with or without multivitamins or vitamin E ( Briscoe 1959 ; Chappell 1999 ; Hans 2010 ; Hemmi 2003 ; McCance 2010 ; Poston 2006 ; Roberts 2010 ; Rumbold 2006 ; Spinnato 2007 ; Steyn 2003 ; Villar 2009 ; Xu 2010 ); folic acid with or without multivitamins and/or iron ( Czeizel 1994 ; Fleming 1968 ; Fleming 1986 ; ICMR 2000 ; Kirke 1992 ; MRC 1991 ); antioxidant vitamins ( Wibowo 2012 ); multivitamins with/without folic acid, vitamin A, vitamin E or iron and folic acid ( Bhutta 2009 ; Czeizel 1994 ; Fawzi 1998 ; Fawzi 2007 ; ICMR 2000 ; Kirke 1992 ; MRC 1991 ; Osrin 2005 ; Roberfroid 2008 ; Rumiris 2006 ; Rush 1980 ; Sunawang 2009 ; Summit 2008 ; Tofail 2008 ; West 2014 ; Zagre 2007 ; Zeng 2008 ); and multivitamins alone ( People's League 1942 ; Rush 1980 ). The doses of vitamins were similar for the vitamin C supplementation trials (range 400 mg to 1000 mg). However, they varied widely between trials for the folic acid (range 0.3 mg to 10 mg), multivitamins and vitamin A trials (range 5000 international units (IU) to 23,300 IU). The components of MMN supplementation were different among the trials but all of them contained iron and folate in the MMN supplements. All supplements were taken orally from the enrolment until delivery or up to 3.5 years postpartum.

Main outcomes

Thirty‐six trials reported pregnancy loss as miscarriage or stillbirth. The outcome 'total fetal loss' included both miscarriage or stillbirth, and overcame problems with different definitions of miscarriage and stillbirth. There was no consistency amongst trials with regards to the definition of miscarriage. For some trials, miscarriage was considered to occur up until 26 or 28 weeks' gestation, while other studies reported miscarriage as pregnancy loss prior to 20 weeks' gestation. Other studies did not specify their definition of miscarriage or stillbirth.

Other outcomes

There was no consistency amongst trials with regards to the definition of stillbirth. In some trials, stillbirth was considered as pregnancy loss greater than or equal to 20 weeks' gestation, while some trials considered stillbirth as pregnancy loss beyond 24 weeks' gestation. Thirty trials reported stillbirth as an outcome. Only one trial ( Spinnato 2007 ) reported on adverse effects of vitamin sufficient to stop supplementation, while congenital malformations was reported in nine trials ( Czeizel 1994 ; Kirke 1992 ; McCance 2010 ; MRC 1991 ; Osrin 2005 ; Poston 2006 ; Spinnato 2007 ; Villar 2009 ; Xu 2010 ).

Excluded studies

We excluded 48 trials, of which 16 trials reported no clinically relevant data, or data in a format suitable for inclusion ( Christian 2003 ; Chelchowska 2004 ; Correia 1982 ; Hibbard 1969 ; Laurence 1981 ; Lira 1989 ; Meirinho 1987 ; Mock 2002 ; Moldenhauer 2002 ; Semba 2001 ; Suharno 1993 ; Tanumihardjo 2002 ; Taylor 1982 ; Thauvin 1992 ; Villamor 2002 ; Vutyavanich 1995 ). Seven trials did not clearly report the gestational age when supplementation was started ( Biswas 1984 ; Fletcher 1971 ; Hampel 1974 ; Lumeng 1976 ; Schuster 1984 ; Trigg 1976 ; Young 2015 ), and for two trials, the majority of women were enrolled after 20 weeks and did not report outcomes separately for women starting supplementation prior to 20 weeks ( Ferguson 1955 ; Giles 1971 ). Thirteen trials ( Baumslag 1970 ; Blot 1981 ; Chanarin 1968 ; Colman 1974 ; Coutsoudis 1999 ; Dawson 1962 ; Edelstein 1968 ; Feyi‐Waboso 2005 ; Hankin 1966 ; Kaestel 2005 ; Marya 1981 ; Metz 1965 ; Owen 1966 ) reported supplementation after 20 weeks' gestation. One trial ( Ross 1985 ) did not specify the contents of the supplements; in five trials all women were given a vitamin supplement ( Hekmatdoost 2011 ; Hunt 1984 ; Huybregts 2009 ; Shu 2002 ; Wehby 2012 ); one trial was a food intervention ( Potdar 2014 ) and two were non‐randomised ( Smithells 1981 ; Ulrich 1999 ).

Three other trials ( Beazley 2005 ; Chaudhuri 1969 ; Rivas‐Echeverria 2000 ) supplemented women for the prevention of pre‐eclampsia, and did not report any outcomes related to pregnancy loss. These trials are covered in the Cochrane review ' Antioxidants for preventing pre‐eclampsia ' ( Rumbold 2008 ).

Risk of bias in included studies

Figure 1 and Figure 2 illustrate that the trials were of variable quality. Two trials ( Fleming 1968 ; People's League 1942 ) used quasi‐random allocation methods involving alternate allocation of participants. Similarly, eight trials ( Bhutta 2009 ; Katz 2000 ; Summit 2008 ; Sunawang 2009 ; West 2011 ; West 2014 ; Zagre 2007 ; Zeng 2008 ) used cluster randomisation.

'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies

'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study

Sequence generation: 25 trials adequately randomised the participants to the intervention and control groups and were judged to be of low risk of bias ( Bhutta 2009 ; Chappell 1999 ; Hans 2010 ; Kirke 1992 ; Kumwenda 2002 ; McCance 2010 ; MRC 1991 ; Osrin 2005 ; Poston 2006 ; Prawirohartono 2011 ; Roberfroid 2008 ; Roberts 2010 ; Rumbold 2006 ; Rumiris 2006 ; Spinnato 2007 ; Steyn 2003 ; Summit 2008 ; Tofail 2008 ; Van den Broek 2006 ; Villar 2009 ; West 2011 ; West 2014 ; Wibowo 2012 ; Xu 2010 ; Zeng 2008 ). The method used for random sequence generation was unclear in 13 trials ( Briscoe 1959 ; Czeizel 1994 ; Fawzi 1998 ; Fawzi 2007 ; Fleming 1986 ; Hemmi 2003 ; ICMR 2000 ; Jauniaux 2004 ; Katz 2000 ; Rush 1980 ; Schmidt 2001 ; Sunawang 2009 ; Zagre 2007 ), because methodological details were not reported or not clearly described. The remaining two trials Fleming 1968 and People's League 1942 used quasi‐randomised methods and were rated as high risk of bias for sequence generation.

Allocation concealment: 20 trials were assessed to have a low risk of bias for adequate concealment of participants to treatment and control groups ( Bhutta 2009 ; Chappell 1999 ; Fawzi 2007 ; Kirke 1992 ; Kumwenda 2002 ; McCance 2010 ; MRC 1991 ; Roberfroid 2008 ; Rumbold 2006 ; Rumiris 2006 ; Spinnato 2007 ; Steyn 2003 ; Summit 2008 ; Tofail 2008 ; Van den Broek 2006 ; Villar 2009 ; West 2011 ; West 2014 ; Zagre 2007 ; Zeng 2008 ). In 18 trials the method for allocation concealment was not described or not clearly described ( Briscoe 1959 ; Czeizel 1994 ; Fawzi 1998 ; Fleming 1986 ; Hans 2010 ; Hemmi 2003 ; ICMR 2000 ; Jauniaux 2004 ; Katz 2000 ; Osrin 2005 ; Poston 2006 ; Prawirohartono 2011 ; Roberts 2010 ; Rush 1980 ; Schmidt 2001 ; Sunawang 2009 ; Wibowo 2012 ; Xu 2010 ). In two trials, allocation was not concealed and therefore judged as high risk of bias ( Fleming 1968 ; People's League 1942 ).

Participants and personnel: 28 trials were assessed as having a low risk of performance bias and reported blinding of participants and personnel to the treatment allocation ( Bhutta 2009 ; Briscoe 1959 ; Chappell 1999 ; Fawzi 1998 ; Fawzi 2007 ; Fleming 1968 ; Fleming 1986 ; Katz 2000 ; Kirke 1992 ; McCance 2010 ; MRC 1991 ; Poston 2006 ; Prawirohartono 2011 ; Roberfroid 2008 ; Roberts 2010 ; Rumbold 2006 ; Rumiris 2006 ; Spinnato 2007 ; Summit 2008 ; Tofail 2008 ; Van den Broek 2006 ; Villar 2009 ; West 2011 ; West 2014 ; Wibowo 2012 ; Xu 2010 ; Zagre 2007 ; Zeng 2008 ). Another 11 trials were judged to have an unclear risk of bias because no or not enough information were provided ( Czeizel 1994 ; Hans 2010 ; Hemmi 2003 ; ICMR 2000 ; Jauniaux 2004 ; Kumwenda 2002 ; Osrin 2005 ; People's League 1942 ; Rush 1980 ; Schmidt 2001 ; Steyn 2003 ). Sunawang 2009 was rated as high risk of bias as personnel (but not participants) were aware of participants' allocation due to the different appearance of the supplements.

Outcome assessment: blinding of outcome assessors was clearly stated in 14 trials ( Bhutta 2009 ; Chappell 1999 ; Fawzi 2007 ; Fleming 1968 ; Fleming 1986 ; McCance 2010 ; Prawirohartono 2011 ; Roberts 2010 ; Summit 2008 ; Tofail 2008 ; Villar 2009 ; West 2011 ; West 2014 ; Xu 2010 ) and unclear in 23 trials ( Briscoe 1959 ; Czeizel 1994 ; Fawzi 1998 ; Hans 2010 ; Hemmi 2003 ; ICMR 2000 ; Jauniaux 2004 ; Katz 2000 ; Kumwenda 2002 ; MRC 1991 ; People's League 1942 ; Poston 2006 ; Roberfroid 2008 ; Rumbold 2006 ; Rumiris 2006 ; Rush 1980 ; Schmidt 2001 ; Spinnato 2007 ; Steyn 2003 ; Van den Broek 2006 ; Wibowo 2012 ; Zagre 2007 ; Zeng 2008 ). In Kirke 1992 ; Osrin 2005 and Sunawang 2009 outcome assessors were not blinded to the allocation code and the trials were rated as high risk of detection bias.

Incomplete outcome data

Loss to follow‐up ranged from no loss at all in Briscoe 1959 ; Rumbold 2006 ; Rumiris 2006 ; Steyn 2003 to over 20% in Fleming 1968 ; ICMR 2000 ; Summit 2008 and Van den Broek 2006 . Incomplete outcome data was judged low risk of bias in 21 trials and high in nine trials. Ten trials were rated as unclear risk of bias due to missing information about loss of follow‐up.

Selective reporting

Eighteen trials were considered to have a low risk of reporting bias. Another 20 trials were assessed as unclear risk of bias because of unavailability of trial registration or protocol ( Bhutta 2009 ; Rush 1980 ), variations between the protocol and the publication ( Poston 2006 ), due to insufficient details provided about methods or selective reporting ( Briscoe 1959 ; Fleming 1968 ; Hans 2010 ; Hemmi 2003 ; ICMR 2000 ; Kirke 1992 ; MRC 1991 ; People's League 1942 ; Roberfroid 2008 ; Steyn 2003 ; Villar 2009 ; Zagre 2007 ), variations of information between serial publications ( Czeizel 1994 ; Fawzi 1998 ; Katz 2000 ; Schmidt 2001 ), or the trial was stopped before completion ( Jauniaux 2004 ). The remaining two trials were at high risk of reporting bias; in Fleming 1986 , not all outcomes were reported for all treatment groups and in McCance 2010 , fewer outcomes were stated in the trial registration compared with the report.

Other potential sources of bias

In 18 trials, other sources of bias were not detected and these trials were rated as low risk of bias. Fourteen trials provided only limited methodological details to exclude other sources of bias and were judged as unclear ( Briscoe 1959 ; Czeizel 1994 ; Fawzi 1998 ; Fleming 1968 ; Fleming 1986 ; ICMR 2000 ; Jauniaux 2004 ; Kumwenda 2002 ; People's League 1942 ; Prawirohartono 2011 ; Rush 1980 ; Schmidt 2001 ) as well as Rumiris 2006 , were participants in the control and intervention group slightly differed in systolic blood pressure at baseline. Additionally, Zeng 2008 was rated as unclear due to an imbalanced number of excluded clusters across the intervention groups, which may have been due to important baseline differences. The remaining eight trials were at high risk of bias. In Bhutta 2009 , the distribution of study participants across the urban and rural areas is unclear from the text and no adjustments were made for cluster design. In Hemmi 2003 , no placebo was used in the control group. Two trials ( Katz 2000 ; Roberfroid 2008 ) used the total number of pregnancies during the study period as dominator and not the total number or randomised women. In Kirke 1992 and MRC 1991 , the trials were terminated at an earlier stage and in Steyn 2003 the outcomes resulted from an interim analysis. In Zagre 2007 , the participants in the control and interventions groups differed substantially in their baseline characteristics.

Effects of interventions

See: Table 1 ; Table 2 ; Table 3

See Table 1 ; Table 2 ; Table 3 for each of the main comparisons. The quality of evidence is included for numerical results of outcomes included in the 'Summary of findings' tables. We have included 40 trials, involving 276,820 women and 278,413 pregnancies. One trial ( Jauniaux 2004 ) contributed no outcome data because it was stopped early and withdrawn. Thus, 39 trials contributed data to our analyses.

The trials involving vitamin C supplementation included the following interventions: vitamin C plus multivitamins versus placebo plus multivitamins ( Briscoe 1959 ; Hans 2010 ), vitamin C and vitamin E supplementation versus placebo ( Chappell 1999 ; McCance 2010 ; Poston 2006 ; Roberts 2010 ; Rumbold 2006 ; Spinnato 2007 ; Xu 2010 ), and vitamin C alone versus no supplement or placebo ( Hemmi 2003 ; Steyn 2003 ).

There was no difference in the risk of total fetal loss between women receiving:

Comparison 1 Vitamin C plus vitamin E versus placebo, Outcome 1 Total fetal loss.

Comparison 2 Vitamin C versus no supplement/placebo, Outcome 1 Total fetal loss.

Comparison 3 Vitamin C plus multivitamins versus placebo plus multivitamins or multivitamins alone, Outcome 1 Total fetal loss.

compared with placebo or no vitamin C groups.

Similarly, we found no overall difference in the risk for early or late miscarriage between women receiving:

Comparison 1 Vitamin C plus vitamin E versus placebo, Outcome 2 Early or late miscarriage.

Comparison 2 Vitamin C versus no supplement/placebo, Outcome 2 Early or late miscarriage.

Comparison 3 Vitamin C plus multivitamins versus placebo plus multivitamins or multivitamins alone, Outcome 2 Early or late miscarriage.

There was no difference in the risk of stillbirth for women receiving:

Comparison 1 Vitamin C plus vitamin E versus placebo, Outcome 3 Stillbirth.

Comparison 2 Vitamin C versus no supplement/placebo, Outcome 3 Stillbirth.

compared with placebo or no vitamin C groups. We found no difference in the risk of congenital malformations ( Analysis 1.4 ) or adverse effects of vitamin supplementation (RR 1.16, 95% CI 0.39 to 3.41, one trial, 739 women; Analysis 1.5 ; moderate‐quality evidence ).

Comparison 1 Vitamin C plus vitamin E versus placebo, Outcome 4 Congenital malformations.

Comparison 1 Vitamin C plus vitamin E versus placebo, Outcome 5 Any adverse effects of vitamin supplementation sufficient to stop supplementation.

The trials involving vitamin A supplementation included the following interventions: vitamin A and/or beta‐carotene versus placebo ( Katz 2000 ; Prawirohartono 2011 ; West 2011 ), vitamin A with or without multivitamins versus multivitamins (excluding vitamin A) or placebo ( Fawzi 1998 ), and vitamin A plus iron and folic acid versus iron and folic acid ( Kumwenda 2002 ; Schmidt 2001 ; Van den Broek 2006 ).

We found no difference in the risk of total fetal loss between women receiving:

Comparison 4 Vitamin A plus iron and folate versus iron and folate, Outcome 1 Total fetal loss.

Comparison 5 Vitamin A versus placebo, Outcome 1 Total fetal loss.

Comparison 6 Beta‐carotene versus placebo, Outcome 1 Total fetal loss.

Comparison 7 Vitamin A or beta‐carotene versus placebo, Outcome 1 Total fetal loss.

Comparison 8 Vitamin A (with/without multivitamins) versus multivitamins or placebo, Outcome 1 Total fetal loss.

compared with placebo or no vitamin A groups.

The heterogeneity in Analysis 5.1 seemed to have been contributed by combining two cluster‐randomised trials and one individually‐randomised trial. Heterogeniety was no longer present when the individually‐randomised trial was excluded. However, this did not change the conclusion of no significant difference between vitamin A and no vitamin A groups.

There was no evidence of a difference in the risk for early or late miscarriage between women receiving:

Comparison 4 Vitamin A plus iron and folate versus iron and folate, Outcome 2 Early or late miscarriage.

Comparison 5 Vitamin A versus placebo, Outcome 2 Early of late miscarriage.

Comparison 6 Beta‐carotene versus placebo, Outcome 2 Early or late miscarriage.

Comparison 8 Vitamin A (with/without multivitamins) versus multivitamins or placebo, Outcome 2 Early or late miscarriage.

There was no difference in the risk for stillbirth for the following supplementation treatments:

Comparison 4 Vitamin A plus iron and folate versus iron and folate, Outcome 3 Stillbirth.

Comparison 5 Vitamin A versus placebo, Outcome 3 Stillbirth.

Comparison 6 Beta‐carotene versus placebo, Outcome 3 Stillbirth.

Comparison 8 Vitamin A (with/without multivitamins) versus multivitamins or placebo, Outcome 3 Stillbirth.

compared with placebo or no vitamin A groups. Congenital malformations and adverse effects of vitamin supplementation were not reported by trials included in these analyses.

The trials involving multivitamin supplementation included the following interventions: multivitamins with or without folic acid versus no multivitamins or folic acid ( Czeizel 1994 ; ICMR 2000 ; MRC 1991 ); multivitamins with or without folic acid versus folic acid ( Kirke 1992 ; MRC 1991 ; Zeng 2008 ); multivitamins with or without vitamin A versus vitamin A or placebo ( Fawzi 1998 ); multivitamins versus control ( People's League 1942 ); multivitamins with vitamin E versus multivitamins without vitamin E or control ( Rush 1980 ); multivitamins with iron and folic acid versus iron and folic acid ( Bhutta 2009 ; Fawzi 2007 ; Osrin 2005 ; Roberfroid 2008 ; Rumiris 2006 ; Sunawang 2009 ; Summit 2008 ; Tofail 2008 ; West 2014 ; Zagre 2007 ).

The risk for total fetal loss was reduced in women supplemented with:

Comparison 10 Multivitamin without folic acid versus no multivitamin/folic acid, Outcome 1 Total fetal loss.

Comparison 15 Multivitamin with/without vitamin A versus vitamin A or placebo, Outcome 1 Total fetal loss.

compared with placebo or no multivitamin groups.

There was no difference in the risk of total fetal loss for the following interventions:

Comparison 9 Multivitamin plus iron and folic acid versus iron and folic acid, Outcome 1 Total fetal loss.

Comparison 11 Multivitamin with/without folic acid versus no multivitamin/folic acid, Outcome 1 Total fetal loss.

Comparison 12 Multivitamin plus folic acid versus folic acid, Outcome 1 Total fetal loss.

Comparison 13 Multivitamin without folic acid versus folic acid, Outcome 1 Total fetal loss.

Comparison 14 Multivitamin with/without folic acid versus folic acid, Outcome 1 Total fetal loss.

Comparison 16 Multivitamin versus control, Outcome 1 Total fetal loss.

Comparison 17 Multivitamin plus vitamin E versus multivitamin without vitamin E or control, Outcome 1 Total fetal loss.

Comparison 18 Multivitamin plus folic acid versus no multivitamin/folic acid, Outcome 1 Total fetal loss.

Similarly, we found no difference in the risk for early or late miscarriage between women receiving the following interventions:

Comparison 9 Multivitamin plus iron and folic acid versus iron and folic acid, Outcome 2 Early or late miscarriage.

Comparison 10 Multivitamin without folic acid versus no multivitamin/folic acid, Outcome 2 Early or late miscarriage.

Comparison 11 Multivitamin with/without folic acid versus no multivitamin/folic acid, Outcome 2 Early or late miscarriage.

Comparison 12 Multivitamin plus folic acid versus folic acid, Outcome 2 Early or late miscarriage.

Comparison 13 Multivitamin without folic acid versus folic acid, Outcome 2 Early or late miscarriage.

Comparison 14 Multivitamin with/without folic acid versus folic acid, Outcome 2 Early of late miscarriage.

Comparison 17 Multivitamin plus vitamin E versus multivitamin without vitamin E or control, Outcome 2 Early or late miscarriage.

Comparison 18 Multivitamin plus folic acid versus no multivitamin/folic acid, Outcome 2 Early or late miscarriage.

The heterogeneity in Analysis 18.1 and Analysis 18.2 seemed to have been contributed by ICMR 2000 , which included women who had previously given birth to a child with an open neural tube defect. When this trial was excluded, the heterogeneity was no longer present.

There was evidence of a decrease in the risk for stillbirth among women receiving multivitamin plus iron and folic acid compared iron and folate only groups (RR 0.92, 95% CI 0.85 to 0.99, 10 trials, 79,851 women; Analysis 9.3 ; high‐quality evidence ).

Comparison 9 Multivitamin plus iron and folic acid versus iron and folic acid, Outcome 3 Stillbirth.

There was no difference in the risk of:

Comparison 10 Multivitamin without folic acid versus no multivitamin/folic acid, Outcome 3 Stillbirth.

Comparison 11 Multivitamin with/without folic acid versus no multivitamin/folic acid, Outcome 3 Stillbirth.

Comparison 12 Multivitamin plus folic acid versus folic acid, Outcome 3 Stillbirth.

Comparison 13 Multivitamin without folic acid versus folic acid, Outcome 3 Stillbirth.

Comparison 14 Multivitamin with/without folic acid versus folic acid, Outcome 3 Stillbirth.

Comparison 16 Multivitamin versus control, Outcome 2 Stillbirth.

Comparison 17 Multivitamin plus vitamin E versus multivitamin without vitamin E or control, Outcome 3 Stillbirth.

Comparison 18 Multivitamin plus folic acid versus no multivitamin/folic acid, Outcome 3 Stillbirth.

Comparison 10 Multivitamin without folic acid versus no multivitamin/folic acid, Outcome 4 Congenital malformations.

Comparison 11 Multivitamin with/without folic acid versus no multivitamin/folic acid, Outcome 4 Congenital malformations.

Comparison 12 Multivitamin plus folic acid versus folic acid, Outcome 4 Congenital malformations.

Comparison 13 Multivitamin without folic acid versus folic acid, Outcome 4 Congenital malformations.

Comparison 14 Multivitamin with/without folic acid versus folic acid, Outcome 4 Congenital malformations.

Comparison 18 Multivitamin plus folic acid versus no multivitamin/folic acid, Outcome 4 Congenital malformations.

There were no data available to conduct any analysis for adverse effects of vitamin supplementation .

The trials involving folic acid supplementation included the following interventions: folic acid with or without multivitamins compared with no folic acid or multivitamins ( Czeizel 1994 ; ICMR 2000 ; MRC 1991 ); folic acid with or without multivitamins compared with multivitamins ( Kirke 1992 ; MRC 1991 ); folic acid and iron compared with iron ( Fleming 1968 ); folic acid and iron compared with no iron or folic acid ( Fleming 1986 ).

We found no difference in the risk of:

Comparison 19 Folic acid plus multivitamin versus no folic acid/multivitamin, Outcome 1 Total fetal loss.

Comparison 20 Folic acid without multivitamin versus no folic acid/multivitamin, Outcome 1 Total fetal loss.

Comparison 21 Folic acid with/without multivitamin versus no folic acid/multivitamin, Outcome 1 Total fetal loss.

Comparison 22 Folic acis plus multivitamin versus multivitamin, Outcome 1 Total fetal loss.

Comparison 23 Folic acid without multivitamin versus multivitamin, Outcome 1 Total fetal loss.

Comparison 24 Folic acid with or without multivitamin versus multivitamin, Outcome 1 Total fetal loss.

Comparison 25 Folic acid plus iron versus iron, Outcome 1 Total fetal loss.

Comparison 26 Folic acid plus iron and antimalarials versus iron and antimalarials, Outcome 1 Total fetal loss.

Comparison 19 Folic acid plus multivitamin versus no folic acid/multivitamin, Outcome 2 Early or late miscarriage.

Comparison 20 Folic acid without multivitamin versus no folic acid/multivitamin, Outcome 2 Early or late miscarriage.

Comparison 21 Folic acid with/without multivitamin versus no folic acid/multivitamin, Outcome 2 Early or late miscarriage.

Comparison 22 Folic acis plus multivitamin versus multivitamin, Outcome 2 Early or late miscarriage.

Comparison 23 Folic acid without multivitamin versus multivitamin, Outcome 2 Early or late miscarriage.

Comparison 24 Folic acid with or without multivitamin versus multivitamin, Outcome 2 Early or late miscarriage.

Comparison 25 Folic acid plus iron versus iron, Outcome 2 Early or late miscarriage.

Comparison 26 Folic acid plus iron and antimalarials versus iron and antimalarials, Outcome 2 Early or late miscarriage.

between women supplemented with folic acid with or without multivitamins and/or iron compared with no folic acid groups. The heterogeneity found seemed to have been contributed by ICMR 2000 , which included women who had previously given birth to a child with an open neural tube defect. Excluding this trial removed the heterogeneity but did not change the conclusion of no difference between the treatment groups.

Comparison 19 Folic acid plus multivitamin versus no folic acid/multivitamin, Outcome 3 Stillbirth.

Comparison 20 Folic acid without multivitamin versus no folic acid/multivitamin, Outcome 3 Stillbirth.

Comparison 21 Folic acid with/without multivitamin versus no folic acid/multivitamin, Outcome 3 Stillbirth.

Comparison 22 Folic acis plus multivitamin versus multivitamin, Outcome 3 Stillbirth.

Comparison 23 Folic acid without multivitamin versus multivitamin, Outcome 3 Stillbirth.

Comparison 24 Folic acid with or without multivitamin versus multivitamin, Outcome 3 Stillbirth.

Comparison 25 Folic acid plus iron versus iron, Outcome 3 Stillbirth.

Comparison 19 Folic acid plus multivitamin versus no folic acid/multivitamin, Outcome 4 Congenital malformations.

Comparison 20 Folic acid without multivitamin versus no folic acid/multivitamin, Outcome 4 Congenital malformations.

Comparison 21 Folic acid with/without multivitamin versus no folic acid/multivitamin, Outcome 4 Congenital malformations.

Comparison 22 Folic acis plus multivitamin versus multivitamin, Outcome 4 Congenital malformations.

Comparison 23 Folic acid without multivitamin versus multivitamin, Outcome 4 Congenital malformations.

Comparison 24 Folic acid with or without multivitamin versus multivitamin, Outcome 4 Congenital malformations.

compared no folic acid groups. There were no data available to conduct any analysis for adverse effects of vitamin supplementation .

The trial involving antioxidant vitamins supplementation included the following interventions: antioxidant with multivitamins compared multivitamins with low antioxidant content ( Wibowo 2012 ).

In the one trial involving 110 women ( Wibowo 2012 ), there was no evidence of differences between women given antioxidant with multivitamins compared multivitamins with low antioxidant group on early or late miscarriage (RR 1.12, 95% CI 0.24 to 5.29, one trial, 110 women, Analysis 27.1 ). No other primary or secondary outcomes were reported by this trial.

Comparison 27 Antioxidant vitamin supplementation, Outcome 1 Early or late miscarriage.

Subgroup analyses by dose of vitamins and duration of vitamin usage

Subgroup analyses by dose of vitamin(s) (below or above the recommended dietary intake) were complicated by the limited number of studies in each vitamin group, and by the use of multivitamin supplements. For many of the vitamin types and for those reporting pregnancy loss outcomes, all of the trials supplemented women with amounts that were above the recommended dietary intake. Similarly, the duration of vitamin usage was complicated by the fact that many of the trials had wide recruitment periods, and one trial ( Katz 2000 ) supplemented women up until three years postpartum. We have not performed subgroup analyses based on vitamin dosage or time of trial entry.

Subgroup analyses by women's risk of spontaneous or recurrent miscarriage

Information enabling women to be classified at high or low risk of either spontaneous miscarriage or recurrent miscarriage was not clearly stated in any of the trials included in this update. Based on the inclusion criteria, one trial ( Rumbold 2006 ) included women at low risk of miscarriage. One trial ( Briscoe 1959 ) included women who had experienced recurrent miscarriage as well as women at high risk of miscarriage (more than two previous miscarriages and/or bleeding in the pregnancy) and low‐risk women (two or less previous miscarriages and no bleeding in the pregnancy). After classifying women into these groups, the number of women in the high‐risk group was too small to permit any meaningful comparisons and we have therefore not performed subgroup analyses.

Subgroup analyses by dietary intake of vitamins

Seven trials ( Bhutta 2009 ; Fleming 1968 ; Kumwenda 2002 ; People's League 1942 ; Schmidt 2001 ; Steyn 2003 ; West 2011 ) reported information about women's nutritional status or the percentage of women who were dietary deficient at trial entry for the vitamin of interest. Other trials reported that they were being undertaken in countries where the population was at high risk of multiple micronutrient deficiencies ( Osrin 2005 ; Prawirohartono 2011 ; Roberfroid 2008 ; Summit 2008 ; Villar 2009 ), or there was a high prevalence of anaemia ( Bhutta 2009 ; Fleming 1986 ; Sunawang 2009 ; Zagre 2007 ; Zeng 2008 ), but provided no specific information on nutritional status of participants. Two trials ( Rumiris 2006 ; Wibowo 2012 ) included women with 'low antioxidant status'. There were not enough trials within each vitamin group to assess the role of supplementation in women with dietary deficient intakes of the individual vitamins and results were not reported separately for women with a low dietary vitamin intake; therefore, we could not perform subgroup analyses.

Sensitivity analyses

We carried out sensitivity analysis to explore the effects of trial quality and type of randomisation on the primary outcomes related to fetal loss (total fetal loss and early or late miscarriage). We included only trials with 'adequate' rating on allocation concealment, but found that restricting to only trials with adequate allocation concealment made very little difference to the results for the primary outcomes. Effect of type of randomisation was explored by excluding cluster‐randomised trials and restricting the analyses to individually‐randomised trials. We found no difference between women supplemented with multivitamins compared with controls for total fetal loss or early or late miscarriage when the analyses were restricted to individually‐randomised trials only. These sensitivity analyses indicate that the analyses for the effects of multivitamins on outcomes related to fetal loss and early or late miscarriage are no different when only individually‐randomised trials are included.

Summary of main results

The purpose of this review was to determine the effectiveness and safety of any vitamin supplementation taken by women pre‐ or periconceptionally on the risk of miscarriage. In this updated version of the review, we included 40 studies involving 59,094 women from individually‐randomised trials plus a further 217,726 women from eight cluster‐randomised controlled trials. The results did not provide sufficient evidence to support the use of single vitamin supplementation for preventing total fetal loss or early or late miscarriage. However, stillbirth was significantly lower in women given multivitamin supplementation plus iron and folic acid compared to iron and folic acid alone. Although there was evidence of decreased risk for total fetal loss among women receiving multivitamins without folic acid compared with no multivitamin/folic acid and multivitamin supplementation with/without vitamin A compared with vitamin A or placebo; these findings occurred in analyses involving one trial each with small numbers of women involved. Also, they include studies where the comparison groups included women receiving either vitamin A or placebo, and thus require caution in interpretation.

Overall completeness and applicability of evidence

There was considerable consistency in reported total fetal loss (including miscarriages or combined miscarriages and stillbirths) among included studies with no difference in the rates of miscarriage and stillbirth across treatment groups. While this may suggest the true effect of vitamin supplementation on risk of miscarriage, most of the studies included in this review did not originally set out to examine the effect of vitamin supplementation on the risk of miscarriage.

Our review included trials that randomised women prior to conception; however, in some cases, not all women enrolled in these trials fell pregnant during the study period. Some of the trials reported outcomes only for women falling pregnant, whereas other trials did not distinguish between women who were never pregnant and women who may have been pregnant but were lost to follow‐up. The outcomes in this review relating to pregnancy outcomes are not relevant for the women who never became pregnant during the study period. In this review, where trials provided accurate information about the number of women who joined the study and became pregnant in the time period, we included this number in the totals, rather than the number of women who may have been randomised. Where it was not clear about the exact number of women with a confirmed pregnancy, we included all women who had been randomised. This may therefore mean that a certain proportion of women in the denominator were never pregnant during the study period. By including these women who were never pregnant in the totals, the review assumes that if these women had become pregnant, they would not have had a miscarriage, which is unlikely to be entirely correct. Including these women creates the potential to underestimate any treatment effects observed.

Similarly, for one large trial ( Katz 2000 ) and one smaller trial ( Roberfroid 2008 ), some women were pregnant more than once during the study period. In these trials, the denominators reported are the total number of pregnancies during the study period, not the total number of women randomised, which incorrectly assumes that each data point included is independent from the next. This has the potential to either underestimate or overestimate the results, depending on whether the women contributing data for more than one pregnancy may be more or less susceptible to experiencing miscarriage or stillbirth. One way to overcome this may be to summarise the data for each woman so that there is only one set of data points for each woman; however, we were unable to do this for these particular studies.

Quality of the evidence

Some of the trials included in the review were at high risk of bias, either due to poor or unclear allocation concealment or large losses to follow‐up. The data were also complicated by differing definitions of miscarriage. For some trials, miscarriage was considered to occur up until 26 or 28 weeks' gestation, while other studies reported miscarriage as pregnancy loss prior to 20 weeks' gestation, and stillbirth as pregnancy loss greater or equal to 20 weeks' gestation. Other studies did not specify their definition of miscarriage or stillbirth. In addition to the problems with differing definitions, the timing of the onset of vitamin supplementation for some of the included trials occurred in mid‐pregnancy, which may limit the impact of supplementation on the risk of miscarriage. The review attempted to overcome these issues by using the outcome 'total fetal loss', which included either miscarriage or stillbirth.

We assessed the quality of the evidence using GRADE and judged the evidence for vitamin C and vitamin E compared with control as high quality for total fetal loss, and moderate quality for early or late miscarriage, stillbirth, and adverse effects, which was downgraded due to wide 95% confidence intervals (CIs) ( Table 1 ). For vitamin A plus iron plus folate versus iron plus folate trials were judged to have low quality of evidence for total fetal loss, early or late miscarriage, and stillbirth due to design limitation and wide 95% CI ( Table 2 ). No studies reported any adverse effects for this comparison. For multivitamin plus iron plus folate versus iron plus folate trials were judged to be high quality for total fetal death and stillbirth, moderate quality for early or late miscarriage, downgraded due to publication bias suspected by funnel plot, or wide CI crossing the line of no effect ( Table 3 ). No studies reported any adverse effects for this comparison.

In order to determine the effect of publication bias, we undertook funnel plots for comparisons with 10 or more studies ( Figure 3 ; Figure 4 ; Figure 5 ) for the comparisons of multivitamins plus iron and folic acid versus iron and folic acid. Asymmetry was suggested by visual assessment of Figure 4 for early or late miscarriage.

Funnel plot of comparison: 9 Multivitamin plus iron and folic acid versus iron and folic acid, outcome: 9.1 Total fetal loss.

Funnel plot of comparison: 9 Multivitamin plus iron and folic acid versus iron and folic acid, outcome: 9.2 Early or late miscarriage.

Funnel plot of comparison: 9 Multivitamin plus iron and folic acid versus iron and folic acid, outcome: 9.3 Stillbirth.

Potential biases in the review process

We took steps to minimise the introduction of bias during the review process. All relevant trials were identified including published abstracts from conference proceedings, English and non‐English publications. A pro forma translation sheet was used to extract relevant information from non‐English articles. At least two review authors independently assessed each trial, performed data extraction, and assessment of risk of bias for each of the included trials. Our assessment of previously identified ongoing trials that remained unpublished were limited to trial published protocols or the records of the initial communication between our authors and the authors of the unpublished trials.

Agreements and disagreements with other studies or reviews

There are several Cochrane reviews evaluating the effect of single vitamin supplementation during pregnancy on maternal, fetal, neonatal and infant outcomes. Benefits or hazards of vitamin supplementation in pregnancy on total fetal loss and miscarriage have not been or insufficiently investigated. However, our results on secondary outcomes are consistent with finding in the particular publications.

In the analysis by vitamin type, vitamin C supplementation alone or in combination with vitamin E or multivitamins did not show any effect on total fetal loss, miscarriage, or the secondary outcomes stillbirth, congenital malformation and adverse effects. A review focusing on vitamin C supplementation alone or in combination with other separate supplements on pregnancy outcomes, did not observe effects on stillbirth or congenital malformations which is consistent with our results ( Rumbold 2015 ).

Supplementing women with vitamin A alone or in combination with iron and folic acid or multivitamins was not associated with changes in fetal loss or miscarriage as well as stillbirth. These findings are consistent with the Cochrane review ' Vitamin A supplementation during pregnancy for maternal and newborn outcomes ' ( McCauley 2015 ), which found no difference in the rate of stillbirth for women receiving vitamin A alone compared with placebo/no treatment or vitamin A with other micronutrients compared with micronutrient supplementation without vitamin A.

In the analysis comparing multivitamin alone or in combination with other vitamins, we found a positive effect of multivitamin supplementation without folic acid compared with no multivitamin/folic acid as well as multivitamin with/without vitamin A compared with vitamin A alone or placebo on total fetal loss. However, these findings resulted from only one study, respectively. Stillbirth was significantly reduced for women receiving multivitamin plus iron and folic acid. This result is consistent with findings in a review assessing the effect of multiple‐micronutrient supplementation during pregnancy on maternal, fetal and infant health outcomes ( Haider 2015 ). Here they also reported a significant reduction in the risk of stillbirth. Miscarriage (loss before 28 weeks) was not effected by this intervention.

Folic acid supplementation with or without multivitamin compared to no folic acid/multivitamin or multivitamin alone did not reduce the risk of total fetal loss, miscarriage, stillbirth or congenital malformations. This in accordance with a review evaluating the effectiveness of oral folic acid supplementation during pregnancy on maternal health and pregnancy outcomes ( Lassi 2013 ). The authors did not observe any effect of folic acid supplementation on stillbirth. Even though miscarriage was included as a secondary outcome, none of the included studies reported on miscarriage. In addition, another review assessed the effects and safety of periconceptional oral folate supplementation for preventing birth defects ( De‐Regil 2015 ). There was no effect of folate versus no intervention, placebo or other micronutrients without folate on miscarriage or stillbirth. They investigated the effect of folate supplementation on several congenital malformations and found a 69% reduction in the risk of neural tube defects.

Antioxidant vitamin supplementation had no effect on early or late miscarriage. The effectiveness and safety of any antioxidant supplementation during pregnancy on the risk of various pregnancy outcomes is explored in the Cochrane review ' Antioxidants for preventing pre‐eclampsia ' ( Rumbold 2008 ). Our results are in accordance with the results form this review where any antioxidant supplementation compared to control or placebo had no effect on miscarriage or stillbirth.

Implications for practice

There is no evidence to support the prophylactic use of single vitamins to prevent either early or late miscarriages. Supplementing women with multivitamin with or without iron and/or folic acid or vitamin A, may decrease the risk of total fetal loss and stillbirth, Even though there is a positive effect of multivitamin supplementation on pregnancy outcomes, there was insufficient evidence to examine the effect of different combinations of vitamins on miscarriage and miscarriage‐related outcomes. Our findings suggest, that no particular vitamin decreases the risk of miscarriage or stillbirth, but the combination of various vitamins may have the potential to positively influence pregnancy outcomes. This could be due to an overall improvement in maternal nutrition and health status, making women more resistant to infections during pregnancy. However, this needs to be investigated further before recommendations on routine multivitamin supplementation to prevent miscarriage can be given.

Implications for research

The impact of different combinations of vitamins (i.e. individual vitamins or multivitamin preparations with or without vitamin A and folic acid) on miscarriage and miscarriage‐related outcomes is unclear. Any future studies of vitamin supplementation should be high quality and focus on women at high risk of miscarriage. Considerations should include timing of the intervention and trials should assess the most appropriate vitamin type and dosage; to see whether it is beneficial without causing any harms to the mother or fetus and include assessments of any psychological effects and long‐term follow‐up of mothers and infants. Further, the data in the current review were complicated by differing definitions of miscarriage and so this may be an important issue to consider in any future trials.

Protocol first published: Issue 1, 2003 Review first published: Issue 2, 2005

Acknowledgements

For previous versions of the review, we thank Simon Gates for statistical advice regarding inclusion of cluster‐randomised trials, Lelia Duley for helpful comments on the format of the review and Sonja Henderson for assisting with review administration.

We also thank Ning Pan, Caroline Crowther and Philippa Middleton for their contribution as authors on previous versions of the review.

We thank the following for their translation help: Izabella Brzostowicz and Agnieszke Kimball for Chelchowska 2004 ; Rebecca Gainey and Kate Bartos for Lira 1989 ; and Lucia Bartos for Métneki 1996 .

As part of the pre‐publication editorial process, this review has been commented on by three peers (an editor and two referees who are external to the editorial team), a member of the Pregnancy and Childbirth Group's international panel of consumers and the Group's Statistical Adviser.

This project was supported by the National Institute for Health Research, via Cochrane Infrastructure funding to Cochrane Pregnancy and Childbirth. The views and opinions expressed therein are those of the authors and do not necessarily reflect those of the Systematic Reviews Programme, NIHR, NHS or the Department of Health.

Rintaro Mori's institution receives government funding from the Clinical Research Program for Child Health and Development, AMED, Japan to provide support for the PCG Satellite in Japan.

Appendix 1. Additional searching carried out for the initial version of the review

For the initial version of the review, authors carried out a separate search of CENTRAL (The Cochrane Library, 2003, Issue 2) for the following terms: miscarriage*, spontaneous abortion, recurrent abortion, spontaneous pregnancy loss, recurrent pregnancy loss, fetal death, vitamin*, folate, folic acid; and also MEDLINE (1966 to May 2003), Current Contents (1998 to May 2003) and EMBASE (1980 to May 2003) using the search strategy given below:

• miscarriage*
• spontaneous abortion
• recurrent abortion
• habitual abortion
• spontaneous pregnancy loss
• recurrent pregnancy loss
• early pregnancy loss
• early pregnancy bleeding
• fetal death
• #1 or #2 or #3 or #4 or #5 or #6 or #7 or #8 or #9
• carotenoid*
• niacin or nicotinamide or nicotinic acid
• pantothenic acid or pantothenate
• cyanocobalamin or cobalamin
• tocopherol* or alpha‐tocopherol
• phylloquinone
• menaquinone
• #13 or #14 or #15 or #16 or #17 or #18 or #19 or #20 or #21 or #22 or #23 or #24 or #25 or #26 or #11 or #12
• #10 and #27
• controlled‐clinical‐trial
• #28 and #31

New search for studies and content updated (no change to conclusions)

Data and analyses

Comparison 1, comparison 2, comparison 3, comparison 4, comparison 5, comparison 6, comparison 7, comparison 8, comparison 9.

Comparison 9 Multivitamin plus iron and folic acid versus iron and folic acid, Outcome 4 Congenital malformation.

Comparison 10

Comparison 11, comparison 12, comparison 13, comparison 14, comparison 15, comparison 16, comparison 17, comparison 18, comparison 19, comparison 20, comparison 21, comparison 22, comparison 23, comparison 24, comparison 25, comparison 26, comparison 27, characteristics of studies, characteristics of included studies [ordered by study id].

B‐HCG: Beta human chorionic gonadotropin BMI: body mass index F: folic acid Hb: haemoglobin HbCC: haemoglobin C disease HbSC:haemoglobin SC disease HbSS: haemoglobin sickle cell disease HELLP syndrome: haemolysis, elevated liver enzymes, low platelet count syndrome HIV‐1: Human Immunodeficiency Virus‐1 HOFPP: Hungarian Optimal Family Planning Programme IQR: interquartile range IFA: iron and folic acid IU: international units IVF‐ET: in vitro fertilization and embryo transfer mcg: micrograms mg/mL: milligrams per millilitre MF: multivitamins with folic acid mg: milligrams MMN: multiple micronutrient MRDR: modified relative dose‐response MV: multivitamins without folic acid MRC: Medical Research Council NTD: neural tube defect P: progesterone PAI‐1: plasminogen activator inhibitor‐1 PAI‐2: plasminogen activator inhibitor‐2 PCV: packed cell volume sTfR: Soluble transferrin receptor UK: United Kingdom UNIMMAP: United Nations International Multiple Micronutrient Preparation USA: United States of America WBC: white blood cell

Characteristics of excluded studies [ordered by study ID]

Characteristics of studies awaiting assessment [ordered by study id].

IFA: iron and folic acid IUGR: Intrauterine growth restriction MMN: multiple micronutrient

Characteristics of ongoing studies [ordered by study ID]

IU: internation unit(s)

Differences between protocol and review

2011 update

We now include trials where supplementation occurred in mid‐pregnancy. This was not specified in the original protocol for this review, but this was amended to be in line with other miscarriage reviews such as 'Progestogen for preventing miscarriage' ( Haas 2009 ). We included trials where the onset of supplementation occurred both prior to and after 20 weeks' gestation, and when it could not be established whether the majority of the women started supplementation prior to 20 weeks' gestation. To overcome differences in the definition of miscarriage and stillbirth, we have used a combined outcome of total fetal loss (early or late miscarriage or stillbirth). We have still reported early or late miscarriage and stillbirth separately in addition to this combined outcome. Similarly, we specified in the original protocol that we would exclude studies reporting greater than 20% losses to follow‐up. In this review we have included studies that reported more than 20% losses to follow‐up and undertaken further analyses based on trial quality.

2016 update The methods section was updated to current Cochrane Pregnancy and Childbirth standard text.

The scope of the current update has been restricted to look at miscarriage and miscarriage‐related outcomes. Comparison 1 (any vitamins) and comparison 2 (sensitivity analysis) have been deleted in this update. After discussion it was decided that it did not make sense to compare any vitamin supplementation with no supplementation from either a clinical or consumer perspective.

We deleted the following primary outcomes. For the woman

• Placental abruption.
• Pre‐eclampsia.
• Psychological effects (anxiety and depression) (previously included as maternal outcomes)

For the infant

• Preterm birth (defined as birth less than 37 weeks' gestation).
• Birthweight.
• Small‐for‐gestational age (birthweight less than the third centile or the most extreme centile reported) (previously included as infant outcomes)

and secondary outcomes:

• Multiple pregnancy (including only trials supplementing women prior to or around the time of conception).
• Very preterm birth (defined as less than 34 weeks' gestation).
• Apgar score less than seven at five minutes.
• Use of blood transfusion for the mother.
• Anaemia (maternal and infant).
• Placental weight.
• Methods of feeding: breastfeeding, formula or both.
• Subsequent fertility (subsequent pregnancy rate per couple or as defined by the authors).
• Poor growth at childhood follow‐up.
• Disability at childhood follow‐up.
• Maternal views of care.
• Gynaecological hospital admission.
• Admission to neonatal intensive care unit.
• Healthcare costs.

All subgroups have been deleted from any analysis.

Contributions of authors

Olukunmi Balogun: screened studies for inclusion/exclusion, data extraction, 'Risk of bias' assessment, data analysis, manuscript revision.

Kathrina da Silva Lopes: screened studies for inclusion/exclusion, data extraction, 'Risk of bias' assessment, manuscript revision.

Erika Ota: screened studies for inclusion/exclusion, statistical support, 'Summary of findings' tables, overall supervision.

Yo Takemoto: screened studies for inclusion/exclusion, data extraction, 'Risk of bias' assessment, manuscript revision.

Alice Rumbold: overall supervision.

Mizuki Takegata: data extraction, 'Risk of bias' assessment.

Rintaro Mori: statistical support, overall supervision.

Sources of support

Internal sources.

• The Grant of National Center for Child Health and Development 27B‐10, 26A‐5, Japan.

External sources

The National Research Center for Child Health and Development, Japan receives government funding (AMED No.27300101) from the Clinical Research Program for Child Health and Development, AMED, Japan to support the Cochrane Pregnancy and Childbirth Satellite in Japan

Declarations of interest

Alice Rumbold is an investigator on the Australian Collaborative Trial of Supplements with vitamin C and vitamin E for the prevention of pre‐eclampsia ( Rumbold 2006 ). This trial is included in this review but its eligibility for inclusion, trial quality assessments and data extraction were carried out independently by two of the review authors not involved in the original trial.

Erika Ota: none known.

Olukunmi O Balogun: none known.

Katharina da Silva Lopes: none known.

Yo Takemoto: none known.

Mizuki Takegata: none known.

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Schmidt 2001 {published data only}

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Summit 2008 {published data only}

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Sunawang 2009 {published data only}

• Sunawang, Utomo B, Hidayat A, Kusharisupeni, Subarkah. Preventing low birthweight through maternal multiple micronutrient supplementation: a cluster‐randomized, controlled trial in Indramayu, West Java . Food & Nutrition Bulletin 2009; 30 ( 4 ):S488‐95. [ PubMed ] [ Google Scholar ]

Tofail 2008 {published data only}

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Van den Broek 2006 {published data only}

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Villar 2009 {published data only}

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West 2011 {published data only}

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West 2014 {published data only}

• Gernand AD, Schulze KJ, Nanayakkara‐Bind A, Arguello M, Shamim AA, Ali H, et al. Effects of prenatal multiple micronutrient supplementation on fetal growth factors: a cluster‐randomized, controlled trial in rural Bangladesh . Plos One 2015; 10 ( 10 ):e0137269. [ PMC free article ] [ PubMed ] [ Google Scholar ]
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Wibowo 2012 {published data only}

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• Zagre NM, Desplats G, Adou P, Mamadoultaibou A, Aguayo VM. Prenatal multiple micronutrient supplementation has greater impact on birthweight than supplementation with iron and folic acid: a cluster‐randomized, double‐blind, controlled programmatic study in rural Niger . Food and Nutrition Bulletin 2007; 28 ( 3 ):317‐27. [ PubMed ] [ Google Scholar ]

Zeng 2008 {published data only}

• Cao Y, Wang T, Zeng L. Risk of childhood malnutrition at 24 months related to small for gestational age and low birth weight in rural Western China . Annals of Nutrition & Metabolism 2013; 63 ( Suppl 1 ):556, Abstract no: PO619. [ Google Scholar ]
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References to studies excluded from this review

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Dawson 1962 {published data only}

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Sucrose for analgesia in newborn infants undergoing painful procedures

Affiliation.

• 1 Nursing Research, The Hospital for Sick Children, 555 University Avenue, Toronto, ON, Canada, M5G 1X8.
• PMID: 27420164
• PMCID: PMC6457867
• DOI: 10.1002/14651858.CD001069.pub5

Background: Administration of oral sucrose with and without non-nutritive sucking is the most frequently studied non-pharmacological intervention for procedural pain relief in neonates.

Objectives: To determine the efficacy, effect of dose, method of administration and safety of sucrose for relieving procedural pain in neonates as assessed by validated composite pain scores, physiological pain indicators (heart rate, respiratory rate, saturation of peripheral oxygen in the blood, transcutaneous oxygen and carbon dioxide (gas exchange measured across the skin - TcpO2, TcpCO2), near infrared spectroscopy (NIRS), electroencephalogram (EEG), or behavioural pain indicators (cry duration, proportion of time crying, proportion of time facial actions (e.g. grimace) are present), or a combination of these and long-term neurodevelopmental outcomes.

Search methods: We used the standard methods of the Cochrane Neonatal. We performed electronic and manual literature searches in February 2016 for published randomised controlled trials (RCTs) in the Cochrane Central Register of Controlled Trials (CENTRAL; The Cochrane Library, Issue 1, 2016), MEDLINE (1950 to 2016), EMBASE (1980 to 2016), and CINAHL (1982 to 2016). We did not impose language restrictions.

Selection criteria: RCTs in which term or preterm neonates (postnatal age maximum of 28 days after reaching 40 weeks' postmenstrual age), or both, received sucrose for procedural pain. Control interventions included no treatment, water, glucose, breast milk, breastfeeding, local anaesthetic, pacifier, positioning/containing or acupuncture.

Data collection and analysis: Our main outcome measures were composite pain scores (including a combination of behavioural, physiological and contextual indicators). Secondary outcomes included separate physiological and behavioural pain indicators. We reported a mean difference (MD) or weighted MD (WMD) with 95% confidence intervals (CI) using the fixed-effect model for continuous outcome measures. For categorical data we used risk ratio (RR) and risk difference. We assessed heterogeneity by the I(2) test. We assessed the risk of bias of included trials using the Cochrane 'Risk of bias' tool, and assessed the quality of the evidence using the GRADE system.

Main results: Seventy-four studies enrolling 7049 infants were included. Results from only a few studies could be combined in meta-analyses and for most analyses the GRADE assessments indicated low- or moderate-quality evidence. There was high-quality evidence for the beneficial effect of sucrose (24%) with non-nutritive sucking (pacifier dipped in sucrose) or 0.5 mL of sucrose orally in preterm and term infants: Premature Infant Pain Profile (PIPP) 30 s after heel lance WMD -1.70 (95% CI -2.13 to -1.26; I(2) = 0% (no heterogeneity); 3 studies, n = 278); PIPP 60 s after heel lance WMD -2.14 (95% CI -3.34 to -0.94; I(2) = 0% (no heterogeneity; 2 studies, n = 164). There was high-quality evidence for the use of 2 mL 24% sucrose prior to venipuncture: PIPP during venipuncture WMD -2.79 (95% CI -3.76 to -1.83; I(2) = 0% (no heterogeneity; 2 groups in 1 study, n = 213); and intramuscular injections: PIPP during intramuscular injection WMD -1.05 (95% CI -1.98 to -0.12; I(2) = 0% (2 groups in 1 study, n = 232). Evidence from studies that could not be included in RevMan-analyses supported these findings. Reported adverse effects were minor and similar in the sucrose and control groups. Sucrose is not effective in reducing pain from circumcision. The effectiveness of sucrose for reducing pain/stress from other interventions such as arterial puncture, subcutaneous injection, insertion of nasogastric or orogastric tubes, bladder catherization, eye examinations and echocardiography examinations are inconclusive. Most trials indicated some benefit of sucrose use but that the evidence for other painful procedures is of lower quality as it is based on few studies of small sample sizes. The effects of sucrose on long-term neurodevelopmental outcomes are unknown.

Authors' conclusions: Sucrose is effective for reducing procedural pain from single events such as heel lance, venipuncture and intramuscular injection in both preterm and term infants. No serious side effects or harms have been documented with this intervention. We could not identify an optimal dose due to inconsistency in effective sucrose dosage among studies. Further investigation of repeated administration of sucrose in neonates is needed. There is some moderate-quality evidence that sucrose in combination with other non-pharmacological interventions such as non-nutritive sucking is more effective than sucrose alone, but more research of this and sucrose in combination with pharmacological interventions is needed. Sucrose use in extremely preterm, unstable, ventilated (or a combination of these) neonates needs to be addressed. Additional research is needed to determine the minimally effective dose of sucrose during a single painful procedure and the effect of repeated sucrose administration on immediate (pain intensity) and long-term (neurodevelopmental) outcomes.

Publication types

• Meta-Analysis
• Research Support, N.I.H., Extramural
• Research Support, Non-U.S. Gov't
• Systematic Review
• Administration, Oral
• Analgesics / administration & dosage*
• Infant, Newborn
• Infant, Premature
• Pain / physiopathology
• Pain / prevention & control*
• Pain Measurement
• Punctures / adverse effects
• Randomized Controlled Trials as Topic
• Sucrose / administration & dosage*

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• Canadian Institutes of Health Research/Canada

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• Volume 13, Issue 11
• Determinants of practice for providing decision coaching to facilitate informed values-based decision-making: protocol for a mixed-methods systematic review
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• http://orcid.org/0000-0002-4704-4401 Birte Berger-Höger 1 ,
• http://orcid.org/0000-0001-6761-7548 Krystina B Lewis 2 , 3 ,
• http://orcid.org/0009-0000-0738-7744 Katherine Cherry 4 ,
• http://orcid.org/0000-0003-2646-0227 Jeanette Finderup 5 , 6 ,
• Janet Gunderson 7 ,
• http://orcid.org/0000-0002-0938-1343 Jana Kaden 1 ,
• http://orcid.org/0000-0001-7367-2009 Simone Kienlin 8 , 9 ,
• http://orcid.org/0000-0002-9051-3621 Anne C Rahn 10 ,
• http://orcid.org/0000-0002-9715-8634 Lindsey Sikora 11 ,
• http://orcid.org/0000-0002-2681-741X Dawn Stacey 2 , 3 ,
• http://orcid.org/0000-0002-8687-3149 Anke Steckelberg 12 ,
• http://orcid.org/0000-0002-3295-5106 Junqiang Zhao 2
• 1 Institute of Public Health and Nursing Research , Faculty 11 Human and Health Sciences, University of Bremen , Bremen , Germany
• 2 School of Nursing , Faculty of Health Sciences, University of Ottawa , Ottawa , Ontario , Canada
• 3 Clinical Epidemiology Program , Ottawa Hospital Research Institute , Ottawa , Ontario , Canada
• 4 Department of Nephrology , Austin Health , Heidelberg , Melbourne , Australia
• 5 Department of Renal Medicine and Department of Clinical Medicine , Aarhus University Hospital , Aarhus , Denmark
• 6 Research Centre for Patient Involvement , Aarhus University & Central Region , Aarhus , Denmark
• 7 Patient partner with the Saskatchewan Centre for Patient-Oriented Research and the Strategy for Patient-Oriented Research's (SPOR) Chronic Pain Network, Cochrane, and the Evidence Alliance. Committee member for the Canadian Arthritis Patient Alliance , Saskatchewan , Western Canada , Canada
• 8 Department of Health and Caring Sciences , Faculty of Health Sciences, UiT The Arctic University of Norway , Langnes , Norway
• 9 Department of Medicine and Healthcare , South-Eastern Norway Regional Health Authority , Hamar , Norway
• 10 Nursing Research Unit, Institute for Social Medicine and Epidemiology , University of Lübeck , Lübeck , Germany
• 11 Health Sciences Library , University of Ottawa , Ottawa , Ontario , Canada
• 12 Institute of Health and Nursing Science , Faculty of Medicine, Martin-Luther-University of Halle-Wittenberg , Halle (Saale) , Germany
• Correspondence to Dr Birte Berger-Höger; birte.berger-hoeger{at}uni-bremen.de

Introduction Decision coaching is a non-directive approach to support patients to prepare for making health decisions. It is used to facilitate patients’ involvement in informed values-based decision-making and use of evidence-based health information. A recent systematic review revealed low certainty evidence for its effectiveness with and without evidence-based information. However, there may be opportunities to improve the study and use of decision coaching in clinical practice by systematically investigating its determinants of practice. We aim to conduct a systematic review to identify and synthesise the determinants of practice for providing decision coaching to facilitate patient involvement in decision-making from multiple perspectives that influence its use.

Methods and analysis We will conduct a mixed-methods systematic review guided by the Cochrane’ Handbook of Systematic Reviews. We will include studies reporting determinants of practice influencing decision coaching with or without evidence-based patient information with adults making a health decision for themselves or a family member. Systematic literature searches will be conducted in Medline, EMBASE, Cochrane CENTRAL and PsycINFO via Ovid and CINAHL via EBSCO including quantitative, qualitative and mixed-methods study designs. Additionally, experts in the field will be contacted.

Two reviewers will independently screen and extract data. We will synthesise determinants using deductive and inductive qualitative content analysis and a coding frame developed specifically for this review based on a taxonomy of barriers and enablers of shared decision-making mapped onto the major domains of the Consolidated Framework for Implementation Research. We will assess the quality of included studies using the Mixed Methods Appraisal Tool.

Ethics and dissemination Ethical approval is not required as this systematic review involves only previously published literature. The results will be published in a peer-reviewed journal, presented at scientific conferences and disseminated to relevant consumer groups.

PROSPERO registration number CRD42022338299.

• Decision Making
• Patient Participation
• Systematic Review

This is an open access article distributed in accordance with the Creative Commons Attribution Non Commercial (CC BY-NC 4.0) license, which permits others to distribute, remix, adapt, build upon this work non-commercially, and license their derivative works on different terms, provided the original work is properly cited, appropriate credit is given, any changes made indicated, and the use is non-commercial. See:  http://creativecommons.org/licenses/by-nc/4.0/ .

http://dx.doi.org/10.1136/bmjopen-2022-071478

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STRENGTHS AND LIMITATIONS OF THIS STUDY

We will use the rigorous methodology in accordance with the Cochrane handbook and the results will be reported as stated by the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) statement.

All members of the team are involved in a coproduction approach throughout the conduct of the systematic review, from the development of the research question to the dissemination of findings.

The search algorithm was developed by an information specialist and peer reviewed by a second librarian according to the Peer Reviewed Electronic Search Strategy (PRESS) guidelines.

No language restriction will be applied in the selection of the studies.

A considerable amount of heterogeneity in the design and the quality of studies is expected which will be carefully considered in terms of the generalisability and the comparability of the results.

Introduction

Making health decisions about treatment or screening interventions is increasingly complex, as many options with different benefit–harm profiles are available. These options could present serious yet different impact on health outcomes and quality of life that patients may value differently. 1–3 In many cases, uncertainty exists about the harms and benefits of options, as the evidence is limited. In addition, individuals differ in how they trade-off the potential outcomes of the various options they face. 1 2 What is known is that patients want to be involved in decisions about their health. 4 5

Shared decision-making occurs when health professionals and patients share information about all available options and their potential harms and benefits, and consider patients’ values and preferences when making the decision. 6 7 In the last decades, many efforts have been made to implement shared decision-making into routine care in different countries, yet a large gap remains between full implementation and current clinical practice. 8 Interventions to facilitate shared decision-making and improve decision quality, targeting patients or health professionals or both, include patient decision aids (PDA), question prompt sheets, decision coaching and training. 9 Some interventions are designed to prepare patients and health professionals for the consultations, while others are designed to be used during the consultation. Currently, there is low certainty evidence that these interventions increase shared decision-making in clinical practice. 9

PDAs provide current evidence-based information in a comprehensive, transparent and balanced manner for patients facing a health decision. 10–12 They explicitly state the decision that needs to be made, provide evidence-based information about the condition, present the options including probabilities of benefits and harms that might occur and the scientific uncertainties underlying the evidence. PDAs often include exercises for value clarification to weigh harms and benefits and, therefore, clarify patients’ preferences for the outcomes of the various options. 12

Decision coaching is a non-directive approach to help patients to prepare for making health decisions. 13 Trained health professionals provide decision coaching to patients who are making a health decision to develop the patient’s skills in (1) thinking about the options, (2) preparing for discussing the decision in a consultation with his or her health professional and (3) implementing the chosen option. 14 15 Therefore, it might facilitate shared decision-making and use of evidence-based PDAs. Systematic reviews on shared decision-making interventions have shown that decision coaching is important to empower patients and enhance their autonomy. 9 14 16

Single studies have demonstrated the effectiveness and feasibility of decision coaching. 17–19 When paired with a PDA, decision coaching improved patients’ understanding of, and participation in, their care, enhanced informed decisions and reduced costs. 12–14 16 A recently published systematic review of 28 randomised controlled trials (RCTs) synthesising the effectiveness of decision coaching yielded low certainty evidence on knowledge when combined with evidence-based information, including PDA. 15 It was not possible to establish strong conclusions for other outcomes such as preparation for decision-making, decision self-confidence, feeling informed, clear values or feeling supported. No adverse effects (eg, decision regret, anxiety) were identified. In addition, in a realist review, Zhao et al highlighted the lack of systematic studies investigating the factors that could facilitate or hinder the implementation of decision coaching. 20

Despite the low certainty of the evidence for decision coaching, the results are promising and there are no identified harms. In fact, there may be opportunities to improve the research studies evaluating decision coaching and its use in clinical practice by considering the determinants of practice influencing its use. Determinants of practice are defined as potential barriers or enablers for the implementation of new practices. Process evaluations have revealed various barriers and enablers of decision coaching at the level of patients, decision coaches, health professionals and health system 17 18 (see table 1 ). Process evaluations are single studies (not a synthesis) and can often accompany RCTs to further understand the outcomes. While RCTs focus on the summative evaluation (efficacy or effectiveness), a process evaluation focuses on the formative aspects of an intervention, 21 which offers more information on the implementation process, how different structures and resources were used, the role, participation and reasoning of different actors, contextual factors and how all these might have impacted the outcomes. 22

• View inline

Examples of determinants of practice for providing decision coaching at the level of patient and/or family, decision coach, health professional and health system

While determinants of practice of implementing shared decision-making have been widely described, 1 22–29 determinants of practice of implementing decision coaching as an intervention to facilitate shared decision-making have not yet been systematically investigated.

We aim to conduct a systematic review to identify and synthesise the determinants of practice for providing decision coaching and the contexts within which it is used to facilitate patient involvement in decision-making from multiple perspectives.

Methods and analysis

We will conduct a mixed-methods systematic review guided by the Cochrane’ Handbook of Systematic Reviews. 30 Qualitative, quantitative and mixed-methods data will be synthesised through a convergent integrated approach for mixed-methods systematic reviews. 31 Our protocol is reported according to the Preferred Reporting Items for Systematic Reviews and Meta-Analyses Protocols (PRISMA-P) reporting guidelines (see online supplemental file 1 ) and registered in PROSPERO (Registration No. CRD42022338299).

Supplemental material

Patient and public involvement.

We will follow a coproduction approach throughout the conduct of the systematic review, from the development of the research question to the dissemination of findings. We aimed to build a diverse research team in which different roles (patient partners (JG), practitioners (KC and JF) and researchers (BB-H, JK, KBL, SK, ACR, DS, AS and JZ), genders, countries (Australia (KC), Canada (DS, KBL and JG), China (JZ), Denmark (JF), Germany (BB-H, JK, ACR and AS) and Norway (SK)) and career stages (trainees (JK, SK and JZ), early-career (BB-H, KBL and ACR), senior researchers (AS, DS and JF)) have been considered. Our patient partner with lived experience of decision-making for healthcare conditions for herself and family members and partnering has experience in systematic reviews including those about decision support interventions (JG). The team’s practitioners include advanced practice nurses who use decision coaching in their clinical practice (KC and JF). The team includes researchers with a profound expertise in the field of decision coaching (BB-H, JF, JK, SK, KBL, ACR, DS, AS and JZ), implementation research (BB-H, KBL and DS) and the conduct of systematic reviews (JF, SK, KBL, ACR, DS and JZ).

Conceptual model

We will use Pel-Littel et al ’s recently published taxonomy of barriers and enablers for the implementation of shared decision-making to guide the data extraction, synthesis and interpretation steps of our review. 27 We have selected this taxonomy as it is a derivative of Joseph-Williams et al ’s systematically developed taxonomy for patient reported barriers and enablers of shared decision-making aiming to inform implementation work alongside efforts to address client, clinician and organisational aspects of shared decision-making. 24 It was extended with organisational factors (health organisations), social factors (health settings, interdisciplinary team) and policy factors (health system, health government) and includes barriers and enablers from different perspectives (eg, patients and health professionals).

Subsequently, we will link our results to the Consolidated Framework for Implementation Research 2.0 (CFIR 2.0). 32 This is a comprehensive implementation framework describing determinants of implementation, which provides a comprehensive taxonomy of specific constructs related to 5 major domains, subdivided into 40 constructs, which could have an impact on implementation: the innovation itself, inner setting (setting in which the innovation is implemented), outer setting (setting in which the inner setting exists, eg, hospital system, state), individuals and implementation process. The CFIR 2.0 is suitable for our review as it comprises all socioecological levels of implementation: individuals, organisation, community, system and policy.

Inclusion criteria

We used the PICOS (Population, Intervention, Comparison, Outcomes and Setting) framework to guide our eligibility criteria.

People aged 18 and older making a decision for themselves or others, health professionals, health administrators, health decision-makers, government policy-maker or other stakeholders (including researchers, not for profit organisations), who report determinants of practice for providing decision coaching with or without evidence-based information.

Types of interventions

We will include decision coaching with adults preparing to make a health decision for themselves or an adult family member (substitute decision-maker) combined with or without evidence-based patient information such as PDAs. Consistent with the Cochrane Review decision coaching definition and eligibility criteria of Jull et al , 15 the interventions to be included will fulfil the following criteria (1) delivered person to person (ie, not automated), whether face to face, by telephone or via the internet; (2) delivered by a health professional who is trained in decision coaching or uses a protocol; (3) helped patients prepare to make a health decision (diagnostic, treatment or screening) with or without an evidence-based patient information (eg, PDA) and (4) comprised non-directive support in preparation for decision-making.

We will exclude articles that describe health professionals who are making the decision with, or on behalf of, the patient; are not trained in decision coaching or does not use a protocol; those who provide genetic counselling; are recommending a specific treatment; or are not described as having direct interests in providing decision coaching (eg, family members/substitute decision-maker of the person making the decision). We will also exclude articles that describe automated support or decision coaching for groups. Further, we will exclude studies evaluating hypothetical decisions, decisions about advanced care planning, decisions about participation in research and lifestyle changes in the absence of a health condition.

Types of comparisons

We will include any study with or without a comparison group.

Types of outcomes

Studies reporting determinants of practice for providing decision coaching in the results section of the manuscripts will be included. Any supplemental materials that present results will also be consulted. Studies only reporting efficacy outcome measures of decision coaching and/or shared decision-making such as decisional conflict 33 will be excluded.

Types of studies

We will include any study design reporting original data related to the development, piloting, evaluation and implementation of decision coaching, including process evaluations. Knowledge syntheses, commentaries, editorials, unpublished studies and non-peer-reviewed studies will be excluded, but their reference lists will be searched for additional primary studies. No language or year restrictions will be applied.

Information sources and search strategy

With the guidance of an academic librarian (LS), we have designed a search strategy which was peer reviewed by a second librarian according to the Peer Reviewed Electronic Search Strategy (PRESS) guidelines. 34 We will conduct the search in the following databases: Medline, EMBASE, Cochrane CENTRAL and PsycINFO (all via Ovid) and CINAHL via EBSCO from database inception to current search dates. Our search strategy will be based on Jull et al ’s 15 systematic review on the effectiveness of decision coaching supplemented with a focus on determinants of practices (eg, barriers and enablers) including all study designs (see online supplemental file 2 ). We will follow the guidance for searching using PRISMA-S.

In addition, we will contact experts in the field and authors of included studies to further inquire about studies that may have been missed, for example, the International Patient Decision Aid Standards Collaboration list serve, International Shared Decision Making Society list serve, conference proceedings and the Shared Decision-Making Facebook Group. We will also search PROSPERO, JBI, Open Science and ClinicalTrials.gov (international prospective register of systematic reviews) databases for any ongoing studies on this topic.

Study selection

The systematic review management tool Covidence ( www.covidence.org ) will be used to manage the two-stage screening-process. First, two reviewers will independently screen titles and abstracts for relevance by indicating whether they are included or excluded based on the PICOS eligibility criteria. Only titles and abstracts rated as excluded by both reviewers will be excluded. Reviewers will not know whether they are reviewing as the first or second. At the full text level, all articles will be screened for eligibility by two reviewers. Discrepant ratings will be resolved by consensus to determine which articles are included or excluded. Consensus will be reached by discussion or through the consultation of a third author. The study selection process will be documented in a PRISMA flow diagram. 35

Data collection

Two reviewers will independently extract study data using a pretested data extraction form based on a taxonomy of shared decision-making barriers and enablers. The form will include study information (title, authors, country of origin, language, study year, year of publication, journal), study characteristics (objectives, study design, data collection methods, participant types, setting, phase of complex intervention research according to the Medical Research Council (MRC) Framework 36 , characteristics of the intervention (who delivered the intervention, framework for decision coaching intervention development, framework for decision coaching implementation, framework/taxonomy used (if any) for determining or analysing barriers and enablers), results (barriers and enablers) and from whose perspective (patient, family, health professional, decision coach, third party observer). Inconsistencies in the extracted data will be discussed among reviewers until consensus is reached, or through the consultation of a third author.

We expect heterogeneity of study designs, settings, interventions and participants, and hence suspect it will not be appropriate to pool quantitative data. We will follow a convergent integrated approach of data synthesis and integration. 31 We will group study results regardless of its design by findings addressing the same phenomenon. Relevant quantitative data will be qualitatised via narrative interpretation into textual descriptions. If a narrative interpretation of data is required and ambiguities in the interpretation occur, we will contact the authors for clarification.

We will synthesise barriers and enablers using deductive and inductive content analysis 37 using our shared decision-making coding frame, which will be considered by the MRC framework of complex interventions which comprises development, piloting, evaluation and implementation. 36 Relevant text sequences from included articles will be extracted. The analysis will be carried out in the following four steps by at least two coders.

In step 1, the extracted data segments will be deductively coded into one of the predefined categories in our shared decision-making coding frame. We will also include an ‘other’ category for data that falls outside of these predefined categories.

In step 2, we will inductively analyse the categorised data (step 1) into emerging themes and subthemes specifically related to decision coaching (data-driven development of categories).

In step 3, the finalised coding guide will be applied on the entire dataset. In this step, coders will decide whether a reported factor will be categorised as a barrier or enabler or both.

In step 4, the results will be summarised by category. We will rank order the reported barriers and enablers according to the frequency of studies that reported them. In the case that one study presents the same barrier and enabler several times, the barrier or enabler will be counted once. The analysis will consider the different perspectives. When a study reported multiple perspectives (eg, patient and health professionals), and different participant types reported the same barrier or enabler, we will count the factor once for each participant type.

In the case of multiple publications reporting the same study, for example, reporting different perspectives (patients, clinicians, observers); study designs (RCTs, process evaluations), we are going to count it as one study about the same intervention.

If it is unclear whether the factor is a barrier or enabler, we will contact study authors for confirmation.

In step 5, in order to link our results to the field of implementation science and to derive potential implementation strategies, we will map our coding frame to the major domains of the Consolidated Framework for Implementation Science 2.0. 32 For example, the barrier of ‘extra effort that has to be made by patients for additional consultations with the decision coach and health team’ identified in table 1 would be mapped on the individual’s domain of the CFIR.

Quality assessment

Two independent reviewers will assess the methodological quality of all included studies with the Mixed Method appraisal tool (MMAT). 38 The MMAT is used to appraise the methodological quality of studies with diverse designs (qualitative, quantitative and mixed-methods research) included in systematic mixed studies reviews. The MMAT tool includes 2 screening questions and 19 items corresponding to 5 methodological domains: qualitative research, RCTs, non-randomised studie, quantitative descriptive studies and mixed-methods studies. The reliability of the MMAT varied by criterion, from fair to perfect. 39 If consensus could not be reached, a third author will be consulted. In cases of unclear reporting, the related items will be rated as unclear. A summary of the results of the methodological quality of the included studies will be presented in the final report.

This systematic review aims to synthesise determinants of practice for decision providing coaching to facilitate patient involvement in informed values-based decision-making. The findings from this review will contribute to an enhanced understanding of the determinants of practice influencing the implementation of decision coaching and help to refine programme theories of such complex interventions. To overcome barriers and successfully implement future decision coaching, it will be crucial to consider determinants of practice from the beginning of intervention development. The early consideration of these determinants will help to develop interventions with implementation strategies that can be properly evaluated, widely adopted and maintained in real world settings. 36

There remains a need for effective interventions facilitating the use of shared decision-making. One way to prepare patients for consultation and to empower them to participate in decision-making is decision coaching. However, the current evidence of the efficacy and effectiveness of decision coaching is low. 15 One reason for this is the high degree of heterogeneity in the design and evaluation of these complex interventions. Thus, we need to understand the contribution of different programme components towards its effectiveness and its influencing factors. Considering the logic of complex interventions, a successful implementation is a prerequisite for its effectiveness. The results of this systematic review could also inform the design of future evaluation and implementation studies, including process evaluations, of decision coaching evaluated in research studies and used in practice.

However, as previously mentioned, we expect a considerable amount of heterogeneity in the design and the quality of studies. We will have to carefully consider the impact of heterogeneity on the generalisability and the comparability of the results.

Ethics and dissemination

Given that this systematic review involves collecting and analysing previously published literature, ethical approval is not required. The results of this systematic review will be published in a peer-reviewed journal, presented in scientific conferences and disseminated within relevant consumer groups, for example, through the decision coaching webpage https://decisionaid.ohri.ca .

Ethics statements

Patient consent for publication.

Not applicable.

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Supplementary materials

Supplementary data.

This web only file has been produced by the BMJ Publishing Group from an electronic file supplied by the author(s) and has not been edited for content.

• Data supplement 1
• Data supplement 2

BB-H and KBL are joint first authors.

Contributors BB-H and KBL contributed equally to this paper. Both conceived the study design and wrote the first draft of the manuscript. LS was responsible for the development of the search strategy. KC, JF, JG, JK, SK, ACR, DS, AS and JZ read the manuscript and made substantive contributions to the design and revision of the manuscript. All authors have approved the final manuscript and agreed both to be personally accountable for the author’s own contributions and to ensure that questions related to the accuracy or integrity of any part of the work, even ones in which the author was not personally involved, are appropriately investigated, resolved and the resolution documented in the literature.

Funding Open Access funding enabled and organised by Project DEAL.

Disclaimer The funder had no influence on the content of the article.

Competing interests None declared.

Patient and public involvement Patients and/or the public were involved in the design, or conduct, or reporting, or dissemination plans of this research. Refer to the Methods and analysis section for further details.

Provenance and peer review Not commissioned; externally peer reviewed.

Supplemental material This content has been supplied by the author(s). It has not been vetted by BMJ Publishing Group Limited (BMJ) and may not have been peer-reviewed. Any opinions or recommendations discussed are solely those of the author(s) and are not endorsed by BMJ. BMJ disclaims all liability and responsibility arising from any reliance placed on the content. Where the content includes any translated material, BMJ does not warrant the accuracy and reliability of the translations (including but not limited to local regulations, clinical guidelines, terminology, drug names and drug dosages), and is not responsible for any error and/or omissions arising from translation and adaptation or otherwise.

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• Published: 16 November 2023

Methods, strategies, and incentives to increase response to mental health surveys among adolescents: a systematic review

• Julia Bidonde   ORCID: orcid.org/0000-0001-7535-678X 1 ,
• Jose F. Meneses-Echavez   ORCID: orcid.org/0000-0003-4312-6909 1 , 2 ,
• Elisabet Hafstad   ORCID: orcid.org/0009-0001-6296-410X 1 ,
• Geir Scott Brunborg   ORCID: orcid.org/0000-0002-1382-2922 3 , 4 &
• Lasse Bang   ORCID: orcid.org/0000-0002-3548-5234 3  

BMC Medical Research Methodology volume  23 , Article number:  270 ( 2023 ) Cite this article

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This systematic review aimed to identify effective methods to increase adolescents’ response to surveys about mental health and substance use, to improve the quality of survey information.

We followed a protocol and searched for studies that compared different survey delivery modes to adolescents. Eligible studies reported response rates, mental health score variation per survey mode and participant variations in mental health scores. We searched CENTRAL, PsycINFO, MEDLINE and Scopus in May 2022, and conducted citation searches in June 2022. Two reviewers independently undertook study selection, data extraction, and risk of bias assessments. Following the assessment of heterogeneity, some studies were pooled using meta-analysis.

Fifteen studies were identified, reporting six comparisons related to survey methods and strategies. Results indicate that response rates do not differ between survey modes (e.g., web versus paper-and-pencil) delivered in classroom settings. However, web surveys may yield higher response rates outside classroom settings. The largest effects on response rates were achieved using unconditional monetary incentives and obtaining passive parental consent. Survey mode influenced mental health scores in certain comparisons.

Conclusions

Despite the mixed quality of the studies, the low volume for some comparisons and the limit to studies in high income countries, several effective methods and strategies to improve adolescents’ response rates to mental health surveys were identified.

Peer Review reports

Globally, one in seven adolescents (aged 10–19 years) experiences a mental disorder, accounting for 13% of the health burden in this age group [ 1 ]. The Global Burden of Diseases Study reports that anxiety disorders, depressive disorders and self-harm are among the top ten leading causes of adolescent health loss [ 2 ]. Understanding the magnitude and determinants of mental health problems among adolescents may inform initiatives to improve their health.

Survey research methods are often used to investigate the prevalence and incidence of mental health problems and associated risk factors and outcomes [ 3 , 4 , 5 ]. Prevalence estimates are based on responses from a sample of the target population. A major priority is to ensure that invited adolescents participate in the survey. In survey research, the response rate (also known as completion rate or return rate) is a crucial metric that indicates the proportion of individuals who participated in the survey divided by the total number of people in the selected sample. Non-response reduces the sample size and statistical precision of the estimates and may also induce non-response bias [ 6 , 7 ]. Consequently, survey response rate is often considered an indicator of the quality and representativeness of the obtained data [ 6 , 8 ].

Non-response is a particular concern in surveys of adolescents as this age-group is hard to reach and motivate to participate in research. Furthermore, response rates for health-related surveys are declining [ 3 , 5 ]. For example, the response rate for a repeated household survey conducted in the US dropped by 35 percentage points between 1971 and 2017 [ 9 ]. Similarly, response rates for the National Health and Nutrition Examination Survey (NHANES) dropped by 15 percentage points from 2011/2012 to 2017/2018 [ 10 ]. There is an increasing need for surveys to be designed and administered in ways that maximise response rates. Multiple published reviews [ 11 , 12 , 13 ] provide evidence of methods and strategies to increase response rates (primarily among adults). These point to several factors associated with increased response rate, including the use of monetary incentives, short questionnaires and notifying participants before sending questionnaires. However, none of these focuses specifically on adolescent samples. Survey characteristics may impact response rates differently in adult and adolescent samples due to age-specific attitudes. For example, adolescents may find web surveys more acceptable and appealing than telephone or postal surveys. Attitudes towards incentives or the topic of surveys (e.g., mental health) may also differ between adults and adolescents. Furthermore, surveys of adolescents are often conducted in class-room settings which exerts a strong contextual influence on response rates. Such contextual factors may moderate the effect of methods and strategies that have been shown to influence response rates among adults.

Features that boost response rates may also influence the mental health outcomes obtained. For example, web-based surveys may improve response rates due to the relative ease of participation when compared with in-person surveys. But they may also impact mental health scores, leading to higher or lower estimates of the prevalence of mental health problems. For example, this can occur because of reluctance to disclose mental health problems to an interviewer, or because web-surveys elicit careless responses. Some studies suggest that mental health indicators differ according to the mode of data collection [ 14 , 15 , 16 ]. Consequently, we need to know which strategies and methods improve adolescents' response rates to mental health surveys and how these might impact mental health scores.

Many factors may positively affect response rates in surveys, including how potential participants are approached and informed about the survey (e.g., pre-notifications), incentives (e.g., financial compensation), data collection mode (e.g., web-based vs. paper-and-pencil), survey measure composition and design (e.g., questionnaire length), using follow-up reminders, and practical issues such as time and location [ 11 , 16 ].

This review aims to identify effective methods and strategies to increase adolescents’ response rates (which may improve the quality of information gathered) to surveys that include questions about mental health, alcohol, and substance use. It also explores how different modes of survey delivery may impact on mental health scores. To accommodate recent trends in technological improvements and attitudes we focus on studies that have been published after 2007. By choosing 2007 we covered advances in technology since the development of the smart phone, and the literature after a previous review [ 13 ] whose search was completed in 2008. Furthermore, to provide the best quality evidence we focus on studies with randomised controlled designs.

This systematic review used the Cochrane approach to methodology reviews [ 17 ]. The full protocol was peer reviewed and is publicly available [ 18 ], but was not registered. The review is reported according to the PRISMA guidelines [ 19 ]. Amendments to the protocol can be found in Additional file 7 : Appendix G.

Eligibility criteria

This review evaluates the effectiveness of survey methods, strategies, and incentives (hereafter “survey mode”) to improve adolescents’ response rates for surveys containing mental health, alcohol, and substance use questions. Adolescents were defined as those aged 12–19 years. It focuses on research conducted in a community setting published since 2007 (when smart phones were introduced). The outcome measures are:

Survey response rates: the percentage of individuals who returned a completed survey, by survey mode;

Mental health variation (i.e., self-reported prevalence) by survey mode. For example, depression scores or alcohol use rates reported for survey modes;

Participant variations (e.g., gender differences) in self-reported mental health scores by survey mode.

Additional file 1 : Appendix A present the review’s eligibility criteria and a glossary of definitions.

Search strategy

One information specialist (EH) developed the search strategy, and a second peer reviewed it using the six domains of the PRESS guidelines [ 20 ]. Following a pilot search in the Cochrane Central Database of Controlled Clinical Trials (Wiley), an adapted search strategy was run in APA PsycINFO (Ovid), MEDLINE (Ovid) and Scopus (Elsevier) on May 13, 2022. Backwards and forwards citation searching were undertaken with last searches undertaken on June 28, 2022. Full searches are presented in Additional file 2 : Appendix B.

Study selection

We deduplicated records in EndNote and screened records in EPPI Reviewer 4 [ 21 ]. Two reviewers (JB, JFME) independently piloted the screening, using machine learning functions in EPPI-Reviewer combined with human assessment (see Additional file 2 : Appendix B). Randomised controlled trials (RCTs) and non-randomised studies of interventions were screened first, and once we identified more than five (pre-specified) RCTs, screening for other study designs was stopped. The two reviewers screened titles and abstracts, and then each relevant full text, independently against the eligibility criteria. A third reviewer adjudicated disagreements. Figure  1 shows the search and screening, and Additional file 2 : Appendix B lists the excluded studies.

PRISMA diagram for the study identification and selection

For studies reported in several documents, all related documents were identified and grouped together to ensure participants were only counted once.

Data extraction

The two reviewers conducted double independent data extraction into Excel forms. A third reviewer adjudicated disagreements. We piloted data extraction on five studies (see Additional file 3 : Appendix C).

Risk of bias (quality assessment)

The two reviewers assessed studies’ risk of bias (RoB) independently using Cochrane’s RoB 2.0 [ 22 ]. Any financial and non-financial conflicts of interest reported in the studies were collected as a separate bias category outside of RoB 2.0 (see Additional file 3 : Appendix C).

Data synthesis

The protocol provides full details of the planned data synthesis [ 18 ]. We present a summary here.

We grouped studies by the type of survey modes. When two or more studies reported the same outcome and survey modes were deemed sufficiently homogeneous, we checked that the data direction permitted pooling. Where necessary to make the values meaningful, we arithmetically reversed scales. We included studies in the meta-analyses regardless of their RoB rating.

To assess statistical heterogeneity, we first checked our data for mistakes and then used the Chi 2 test (threshold P  < 0.10) and the I 2 statistic following Cochrane Handbook recommendations [ 23 ]. In cases of considerable statistical heterogeneity (I 2  > 70%) we did not conduct meta-analysis. Where there was less heterogeneity (I 2  <  = 70%), we performed random effects meta-analysis using Review Manager 5.4.1. We also assessed studies’ clinical and methodological heterogeneity (participants, survey processes, outcomes, and other study characteristics) to determine whether meta‐analysis was appropriate.

Where statistical pooling was not feasible, we followed the Synthesis Without Meta-analysis guideline to report the results narratively [ 24 ]. For dichotomous outcomes (e.g., response rates and adolescents’ self-reported alcohol use) we calculated odds ratios (ORs) and their 95% confidence intervals (CIs) to estimate between-mode differences. We used the default weighting technique (e.g., Mantel–Haenszel) for dichotomous outcomes in RevMan software. For continuous outcomes, we estimated the difference between survey modes using Mean Differences (MDs) or Standardized Mean Differences (SMDs) if the same outcome was measured with different questionnaires. The standard deviation was not modified [ 25 ]. We planned subgroup analyses and a GRADE assessment [ 18 ]. Amendments to the protocol are in Additional file 7 : Appendix G.

Search and screening results

Database searches retrieved 12,054 records. We removed 1,892 duplicates. EPPI-reviewer 4 marked 6,841 records as ineligible (see Additional file 2 : Appendix B). The team screened the titles and abstracts of 3,321 records and the full text of 48 documents, identifying ten eligible documents. Citation searches on ten eligible documents retrieved a further 740 records, which yielded six eligible documents. We identified one further document from reference lists. In total, this review included 15 studies (17 documents). Additional file 2 : Appendix B shows the excluded studies. We did not identify any studies in languages we could not translate.

Figure  1 shows the PRISMA diagram.

Details of included studies

Table 1 provides details of the included studies and Additional file 3 : Appendix C shows the data extraction tables. The age distribution of participants in the studies varied, but most were aged 14 to 16 years. A smaller proportion of participants were aged < 14 years or > 16 years. The sex distribution in studies were generally even and ranged from 32% [ 26 ] to 58% [ 27 ]. Studies were conducted in both rural and urban areas and included a range of national and racial/ethnic representation. Although most studies took place within school settings, four of them [ 26 , 28 , 29 , 30 ] were conducted in non-school environments. All the studies involved community (i.e., non-clinical) samples, but we note that the Pejtersen’s study [ 26 ] focused on a group of vulnerable children and youth.

The fifteen studies investigated six comparisons:

Paper-and-pencil (PAPI) survey administration versus web administration ( n  = 9 in 10 documents)

Telephone interviews versus postal questionnaires ( n  = 2)

Active versus passive parental consent ( n  = 1)

Web first versus in-person first interviews ( n  = 1)

Vouchers versus no vouchers ( n  = 1 in 2 documents)

Internal supervision versus external supervision ( n  = 1)

Risk of bias

Overall, study authors provided little information on their research methods resulting in several unclear domains that raised concerns about risk of bias. The main issues identified related to the randomisation process, measurement of the outcomes, and selective reporting of results. We classified three cluster RCTs [ 31 , 32 , 38 , 40 ] and three parallel RCTs [ 26 , 35 , 37 , 39 ] as high RoB. There were some concerns with nine [ 14 , 16 , 27 , 28 , 29 , 30 , 33 , 34 , 36 ] parallel RCTs (see Additional file 4 : Appendix D). RoB for each study is presented below.

This section presents the study results and the meta-analyses. Additional file 6 : Appendix F contains additional forest plots. We describe the results narratively without prioritization or hierarchy. We did not contact study authors for missing/additional data. Caution is advised when interpreting the meta-analyses because of studies’ quality/RoB and imprecision.

The considerable statistical heterogeneity (I 2  > 70%) in the data for the two largest comparisons (1 and 2) precluded a meta-analysis of response rates. The studies showed divergent effect estimates, which may be explained by their different outcome measures. There were differences inherent to the study designs with cluster RCTs adjusted for clustering. There were important differences in the survey implementation procedures, including different interfaces, skipped questions, confidentiality measures and different degrees of supervision. Ignoring these considerations would have resulted in pooled analyses prone to misleading inferences.

Comparison 1: paper-and-pencil versus web-based administration mode

Nine studies (ten documents) compared PAPI surveys to web-based surveys [ 14 , 16 , 30 , 31 , 32 , 33 , 34 , 35 , 36 , 37 ]. The studies included one cluster RCT with high RoB, three RCTs with high RoB and five RCTs with RoB concerns.

Response rate

Five studies reported response rate [ 16 , 30 , 31 , 32 , 34 , 37 ]. Three studies reported between-group differences [ 30 , 31 , 32 , 34 ], but because of considerable heterogeneity (I 2  > 90%) we present the effect estimates for each study separately (Fig.  2 ). Van de Looij-Jansen [ 16 ] reported a narrative summary rather than outcome data. Trapl [ 37 ] reported a 100% response rate.

Odds ratios for various survey delivery mode comparisons: Adolescents’ response rates (results not pooled)

Denniston [ 31 ], reported a cluster RCT in two documents [ 31 , 32 ] and accounted for clustering in the analyses. Therefore, we did not conduct design effect adjustment [ 41 ]. The odds of response increased by nearly 80% for PAPI compared with a web mode (OR 0.22, 95% CI 0.19 to 0.26; n  = 7747). Participants could skip questions in some of the modes (“with skip patterns”). Treated as an independent intervention arm, the group “on your own” web without skip patterns had the lowest response rate (28%; 559/1997) compared with the other web formats (in-class web without skips and with skips) and markedly lower odds of response relative to PAPI (OR 0.04, 95% CI 0.03 to 0.04). Low odds of response affect the pooled rates among the web survey modes. The pooled response rate for the two web in-class modes (with and without skips) was 90.7%, which was no different to the PAPI response rate (OR 0.94, 95% CI 0.78 to 1.14; n  = 5750).

Mauz [ 30 ] explored three survey modes that we combined into an “overall web mode”. Each mode included varying proportions of participants receiving PAPI surveys or web surveys (see Table 1 ), but separate data for web participants were not reported. The odds of response decreased by nearly 70% when using PAPI compared with a web mode (OR 0.29, 95% CI 0.23 to 0.38; n  = 1195) [ 30 ].

Miech [ 34 ] found evidence of no effect on response rates for PAPI compared with web mode (electronic tablets) (OR 1.03, 95% CI 0.97 to 1.08; n  = 41,514).

Van de Looij-Jansen [ 16 ] reported an overall response rate of 90%, with no difference between PAPI or web modes (data not reported) and Trapl [ 37 ] reported 100% response rate.

Mental health variation by mode of survey delivery

Nine studies (ten documents) reported between-modes variations in point estimates for various mental health and substance use scores at the time of survey completion [ 14 , 16 , 30 , 31 , 32 , 33 , 34 , 35 , 36 , 37 ].

Two studies (considerable heterogeneity: I 2  = 82%) of Dutch adolescents from secondary schools in rural and urban areas reported between-modes variations for adolescents’ mental health scores (Fig.  3 ) [ 16 , 35 ]. Raat [ 35 ] reported that for the mental health subscale of the Child Health Questionnaire (CHQ-CF), PAPI mode participants had slightly lower scores compared with web users (MD -1.90, 95% CI -3.84 to 0.04; n  = 933). Conversely, van de Looij-Jansen [ 16 ] reported no between-mode variations in self-reported total scores for the Strength and Difficulties Questionnaire (SDQ). Boys tended to report better mental health scores when completing surveys using PAPI than the web (MD 1.0, 95% CI -0.10 to 2.10; n  = 279).

Mean differences for paper-and-pencil versus web administration survey delivery modes: Adolescents’ self-reported mental health

Two studies estimated between-mode variations for adolescents’ self-reported psychological wellbeing scores [ 16 , 30 ]. Mauz [ 30 ] reported the number of adolescents experiencing favourable psychological wellbeing, expressed as t values, using the KIDSCREEN (the Health-Related Quality of Life Questionnaire for Children and Adolescents aged from 8 to 18 years, Questionnaires—kidscreen.org). The narrative findings indicated that psychological wellbeing was the same for both PAPI and web-based questionnaire modes (PAPI 50.5% vs web 49.3% ( n  = 1194), P  = 0.07 adjusted with Bonferroni correction). Similarly, van de Looij-Jansen [ 16 ] reported no between-mode variations in mean scores of adolescents’ self-reported psychological wellbeing obtained from nine items about feelings and moods from the CHQ-CF (MD pooled for boys and girls -0.97, 95% CI -3.21 to 1.28; n  = 531) (Fig.  4 ).

Mean differences for paper-and-pencil versus web administration survey delivery modes: Adolescents’ psychological wellbeing (nine items about feelings and moods derived from the CHQ-CF)

Denniston [ 31 ] found evidence of no between-mode estimate variations for adolescents’ self-reported sadness (OR 1.02, 95% CI 0.90 to 1.15; n  = 5786) or suicide attempts (OR 1.01, 95% CI 0.83 to 1.24; n  = 5786) measured using the Youth Risk Behavior Surveys [ 31 , 32 ].

Hamann [ 33 ] found evidence of no between-mode estimate variations for adolescents’ self-reported anxiety (MD 1.65, 95% CI -5.18 to 8.48; n  = 56) or depression (MD 0.78, 95% CI -1.54 to 3.10; n  = 56) measured using the Spence Children’s Anxiety Scale (SCAS) and the German version of the Children’s Depression Inventory (CDI) [ 33 ].

Six studies (7 documents) reported adolescents’ self-reported lifetime alcohol use [ 14 , 30 , 31 , 32 , 34 , 36 , 37 ]. Lygidakis [ 14 ] reported on adolescents who said they “ have been drunk ” and therefore we did not pool this study with studies of lifetime use. In Lygidakis [ 14 ], lifetime estimates of self-reported alcohol use were 11% lower in the PAPI group compared with the web survey group (OR 0.89, 95% CI 0.79 to 1.00; n  = 190). A pooled analysis of five studies [ 30 , 31 , 32 , 34 , 36 , 37 ] suggested that the odds of alcohol lifetime use were 13% higher among adolescents completing the web survey compared with those using PAPI (OR 1.13, 95% CI 1.00 to 1.28; n  = 49,554); substantial heterogeneity was observed (I 2  = 59%) (Fig.  5 ).

Odds ratios for paper-and-pencil versus web administration of surveys: Adolescents’ self-reported lifetime alcohol use

A pooled analysis of two studies, Denniston [ 31 ] and Trapl [ 37 ], showed evidence of no between-mode estimate variations for adolescents’ self-reported marijuana use (OR 1.05, 95% CI 0.93 to 1.18; n  = 6,061) (Fig.  6 ).

Pooled estimate variations for paper-and-pencil versus web administration of surveys: Adolescents’ self-reported lifetime marijuana use

Participant variation by mode of survey delivery

Gender was the only participant characteristic for which the included studies reported disaggregated data. We calculated estimate variations by gender within studies rather than between survey mode comparisons.

In Van de Looij-Jansen [ 16 ], boys tended to report better mental health scores than girls for total mental health score, emotional symptoms, and psychological well-being. The largest and more precise difference was for emotional symptoms (pooled MD for both survey modes -1.31, 95% CI -1.64 to -0.98; n  = 531), whereas the mental health total scores reported with the PAPI version of the SDQ proved to be the least precise (MD -0.30, 95% CI -1.54 to 0.94; n  = 261). The absence of statistical heterogeneity in the results for emotional symptoms and psychological well-being suggests that boys reported better scores than girls regardless of the survey mode (Fig.  7 ).

Mean difference by gender for paper-and-pencil and web administration of surveys: Adolescents’ self-reported mental health outcomes

In Raghupathy [ 36 ], the odds of reporting lifetime alcohol use increased by more than one half in girls (OR 1.61, 95% CI 0.99 to 2.62; n  = 339). Less precise estimate variations were observed when using PAPI vs web mode (Fig.  8 ).

Odds ratios for gender variations for paper-and-pencil and web administration of surveys: Adolescents’ self-reported lifetime alcohol use

Comparison 2: telephone interview vs postal questionnaires

Two studies reported outcome data for this comparison ( n  = 2322) [ 28 , 29 ]. Trained interviewers performed the telephone interviews in both studies. Interviewers in Erhart [ 29 ] used computer-assisted telephone interviews whereas in Wettergren [ 28 ] interviewers were trained to read the questions aloud and record participants’ answers. There were concerns for RoB for both studies.

We did not pool the response rates due to considerable heterogeneity (I 2  > 90%); the studies are presented separately [ 28 , 29 ]. The studies reported opposing results (Fig.  2 ). Erhart [ 29 ] reported a 41% completion rate for telephone interviews compared with 46% for postal questionnaires (OR 0.82, 95% CI 0.68 to 1.00; n  = 1,737), whereas Wettergren [ 28 ] reported a response rate of 77% for telephone interviews and 64% for postal questionnaires (OR 1.89, 95% CI 1.32 to 2.72; n  = 585).

The studies evaluated the effect of differences in survey mode on estimate variations of adolescents’ self-reported mental health measured by the SDQ total score [ 29 ] and the mental health component of the RAND 36-Item Short Form Health Survey (SF-36) measure [ 28 ]. We converted the data in Wettergren [ 28 ] to a zero to 10 scale to obtain a more homogenous pooled analysis. In the meta-analysis, adolescents reported 1.06 points better mental health when a telephone interview was used (MD 1.06, 95% CI 0.81 to 1.30; n  = 1,609) (Fig.  9 ).

Pooled mean difference for survey delivery by telephone interview versus postal questionnaires: Adolescents’ self-reported mental health

Wettergren [ 28 ] found evidence of no estimate variation for adolescents’ self-reported anxiety (MD -0.60, 95% CI -1.21 to 0.01; n  = 580) and a small estimate variation for self-reported depression on the Hospital Anxiety and Depression Scale (HADS) favouring telephone interviews relative to postal questionnaires (MD -0.50, 95% CI -0.94 to -0.06; n  = 585).

Wettergren [ 28 ] reported participants’ gender differences in self-reported estimate variations of mental health (SF-36) alongside anxiety and depression (both measured with the HADS). Boys tended to report better mental health (SF-36) and anxiety (HADS) scores than girls, with the largest gender difference in anxiety (MD -1.85, 95% CI -2.42 to -1.28, n  = 585) [ 28 ]. Postal questionnaires seem to result in a larger gender difference in self-reported mental health scores compared with telephone questionnaires (I 2  = 53%). No differences between survey modes were observed for anxiety scores (I 2  = 0%). Boys and girls reported similar depression scores (MD -0.07, 95% CI -0.49 to 0.35; I 2  = 0%) for both survey modes (Fig.  10 ).

Pooled mean differences by gender for survey delivery by post and telephone: Adolescents’ self-reported mental health

Comparison 3: active vs passive parental consent.

One cluster RCT compared schools randomised into groups where adolescents required active parental consent to undertake the survey or where passive parental consent was accepted [ 38 ]. The study had high RoB.

District schools assigned to passive parental consent achieved a response rate of 79% compared to 29% achieved by schools assigned to active consent mode ( p  = 0.001, number of participants per mode not reported) [ 38 ].

Courser [ 38 ] did not report any mental health variation or participant variations by survey mode.

Comparison 4: web first vs in-person first survey versions

One RCT [ 27 ] investigated the order of survey delivery. One group of students was offered an in-person survey, with web follow-up in case of non-response. A second group was asked to complete a web survey first, with in-person survey in case of non-response. There are some concerns over the study’s RoB.

McMorris [ 27 ] found evidence of no difference in response rates between adolescents completing a web survey first or an in-person survey first (OR 0.57, 95% CI 0.24 to 1.31; n  = 386) (Fig.  2 ).

McMorris [ 27 ] found evidence of no difference on adolescents’ self-reported lifetime alcohol use (OR 0.84, 95% CI 0.55 to 1.27; n  = 359) or lifetime marijuana use (OR 0.65, 95% CI 0.41 to 1.01; n  = 359) between the two survey modes. McMorris [ 27 ] did not report on participant variations by survey mode.

Comparison 5: voucher vs no voucher

One RCT [ 26 ] (reported in two documents) investigated whether an unconditional monetary incentive (a supermarket voucher) increases the response rate among vulnerable children and youths receiving a postal questionnaire [ 26 , 39 ]. The study was classified as high RoB.

Pejtersen [ 26 ] found that the monetary incentive yielded a response rate of 76% versus 43% without the incentive (OR 4.11, 95% CI 2.43 to 6.97; n  = 262) (Fig.  2 ).

The study also found that offering a voucher made no difference to adolescents’ self-reported emotional symptoms compared with no voucher (MD -0.70, 95% CI -1.58 to 0.18; n  = 156) measured using the emotional symptoms subscale of the SDQ [ 26 , 39 ]. Pejtersen [ 26 ] did not report on participant variations by survey mode.

Comparison 6: internal versus external supervision

One Swiss cluster-RCT evaluated the effect of external supervision (by a senior student or researcher) compared to internal supervision (by the teacher) when students completed online interviews [ 40 ]. The study was classified as high RoB.

Walser [ 40 ] only reported outcomes relevant to mental health variations, finding evidence of no variations in adolescents’ self-reported lifetime alcohol use according to the survey mode (OR 1.08, 95% CI 0.79 to 1.47; n  = 1,197).

Subgroup and sensitivity analyses

There were too few studies, and no quasi-RCTs, to complete the planned subgroup and sensitivity analyses.

Reporting bias assessment

We could not assess reporting biases, because too few studies were available (i.e., less than 10 studies) for each comparison [ 23 ].

Certainty assessment

We opted not to perform a GRADE assessment due to the limited quantity of studies for each comparison under consideration and the mixed quality of studies.

This review identified fifteen RCTs that investigated six different comparisons among adolescents. Although the included studies were of mixed quality, several effective methods and strategies to improve adolescents’ response rates to mental health surveys were identified. Findings show that response rates varied with survey mode, consent type, and incentives.

Comparisons of web versus PAPI mode yielded discrepant findings that must be interpreted in relation to survey delivery context. One study showed that postal invitations to a web survey was associated with higher response rates compared to PAPI mode [ 30 ], possibly due to the additional effort required to return the completed PAPI survey by post. In contrast, there were no significant differences in response rates for web and PAPI modes conducted in classrooms during school hours [ 16 , 31 , 32 , 34 ]. However, one study showed that inviting adolescents to complete a web survey on their own (at home within 2–3 weeks following the invitation) dramatically decreased response rates compared with completing PAPI or web surveys at school (28% vs. ~ 90%) [ 31 , 32 ]. These findings show that response rates may vary according to both delivery mode and context. A previous meta-analysis showed that web surveys yield lower response rates (on average 12 percentage points) than other modes [ 12 ]. However, this review did not focus specifically on adolescents. More studies are needed to determine whether response rates among adolescents differ between web and PAPI surveys delivered outside school.

Conflicting evidence was found for telephone interview surveys compared to postal PAPI surveys. One study found significantly higher response rates (77% vs 64%) for telephone interview surveys [ 28 ], while another found significantly but marginally (48% vs. 43%) higher response rates for postal PAPI surveys [ 29 ]. The reasons for these opposing findings are unclear, but other contextual factors may play a role such as the age of the studies (conducted before 2010) reflecting potential time related differences in attitudes towards telephone interviews and postal PAPI surveys. One study [ 27 ] found that response rates did not differ significantly when comparing a web survey and follow-up in-person interview for non-responders with in-person interview and follow-up web survey for non-responders. Administering a web survey first is a cost-saving approach which is unlikely to adversely impact adolescents’ response rates.

One study showed that unconditional monetary incentives (i.e., voucher) increased response rates by 33 percentage points [ 26 ], supporting a prior review on postal surveys [ 42 ]. Interestingly, evidence favours monetary incentives unconditional on response compared with similar incentives conditional on response to improve response rates [ 11 , 42 ]. In contrast, a recent meta-analysis [ 12 ] concluded that incentives had no effect on response rates in web surveys. These discrepant findings may indicate that incentives matter less for response rates in web surveys compared to other modes. Our review also identified one study showing that passive parental consent achieved more than double the response rate of active consent (79% vs. 29%) [ 38 ]. A prior meta-analysis of studies found similar evidence in favour of passive parental consent [ 43 ]. If ethical and data protection considerations permit, using passive parental consent may boost response rates substantially.

Survey mode influenced mental health scores in certain comparisons. We found no evidence of effect on self-reported mental health scores (across a range of measures) between PAPI and web surveys [ 16 , 30 , 31 , 32 , 34 , 35 , 36 , 37 ]. However, our pooled analysis of lifetime alcohol use showed 13% higher use when a web mode was used compared to a PAPI mode. This could possibly be attributed to differential response rates, for example if heavy drinkers are less likely to respond to a PAPI compared to web survey. In contrast, two studies indicated that lifetime marijuana use did not differ between web and PAPI survey modes [ 31 , 32 , 37 ]. The reasons for such differences are unclear and should be further researched. Telephone interview compared with postal PAPI surveys was associated with slightly better mental health scores [ 28 , 29 ]. These differences were quite small and probably of limited practical significance [ 28 ]. Nonetheless, survey designers should be aware that adolescents may report fewer mental health problems in telephone interviews. Such findings may be due to differential response rates as already mentioned, for example if those with mental health problems are less likely to respond to telephone surveys compared to PAPI surveys. Another reason may be that adolescents are less willing to report such problems directly to another person. The added anonymity of non-telephone surveys may encourage adolescents to provide more genuine responses to sensitive questions concerning their mental health. A study that compared supervision by either teachers or researchers during an in-class web survey [ 40 ] found no significant differences in mental health scores, which suggests that the choice of supervision personnel does not impact responses.

There was little evidence of differences between gender and survey characteristics on mental health scores. While several studies highlighted that males report better mental health than females [ 16 , 28 ], there was no indication that specific survey modes impacted males’ and females’ mental health differentially (i.e., no interaction effect). Many studies did not report mental health scores separately for males and females.

Our review complements earlier reviews of factors that influence response rates [ 11 , 12 , 42 , 43 , 44 ]. Together, these reviews provide useful information regarding how to design surveys to maximise response rates. The extent to which their findings are generalizable to adolescents in recent decades is unclear. Our own review show that relatively few studies have focused specifically on adolescents. Nevertheless, many of our findings are in line with those outlined in previous reviews. One outstanding question is whether web surveys yield lower response rates than other modes also for adolescents. The studies included in our review highlights the need to consider contextual factors when comparing response rates between surveys. For example, survey mode may have less impact on response rates in class-room settings. Our findings highlight the need for more studies to provide high-quality evidence of methods and strategies to ensure adequate response rates in mental health surveys of adolescents. This is particularly important given the present worldwide focus on adolescent mental health and the decreasing response rates in surveys.

Although we found relevant RCTs, they were of insufficient quality to draw firm conclusions. The studies in some comparisons showed considerable heterogeneity and meta-analysis was not feasible for most comparisons. For several comparisons, only one or two studies were available. In RCTs where one survey mode was superior to another, the results need to be confirmed with better conducted (and/or reported) studies.

The studies had a range of differences that reduce the comparability of studies and the generalisability and strength of our findings. Various questionnaires were used, differing greatly in content, length, and appearance. Questionnaires were managed in different ways, for example some used skips to ensure confidentiality, and some did not permit the questions to be read aloud during interview. Different methods were used to deliver questionnaires: postal, in the classroom, or sent to parents. The studies investigated a mix of outcomes using a range of tools and with study-specific adaptations in some cases.

The median publication year of the studies is 2010. The inclusion of older RCTs may mean that in a world of high internet and smart phone usage, the applicability of the earlier findings may be weakened.

Key strengths of this review include the team’s expertise in synthesis methods, topic area, information retrieval, and machine learning. We identified a substantial number of RCTs in adolescent populations, some with many participants, using an extensive search in databases augmented by forwards and backwards citation searching.

Although it is not usually common practice to search for outcomes in literature searches for reviews of effect of interventions [ 45 ], given the challenges of searching for this review topic, we considered it necessary to reduce the screening burden by including the concept of outcomes in our search. This approach may have lowered the search sensitivity where authors did not mention outcomes of interest in the abstract [ 46 ] and may also have introduced publication bias, because outcomes with positive results might be more likely to reported in the abstract than negative results [ 47 ]. Our citation searches should have mitigated both issues somewhat since they rely on publications citing each other, rather than containing specific words.

The review used machine learning for study selection reducing the study selection workload by 95%. Our experience confirms the widely documented potential of automated and semi-automated methods to improve systematic review efficiency [ 48 , 49 ]. The workload savings enabled us to spend more time in discussions with content experts.

The review results are affected by statistical heterogeneity in the analyses, which may be due to methodological and clinical heterogeneity in the variables, as well as the large variability in the design and conduct of the studies. There were not enough studies to explore heterogeneity using subgroup and sensitivity analyses, nor to test for publication bias. In many instances, results come from a single study, which greatly reduces the applicability of the findings considering none of the studies had low RoB.

We limited eligible studies to those undertaken in high income countries and as a result we cannot generalize our findings to low- or middle-income countries. The body of evidence comes from nationwide surveys in schools in the USA and Europe.

Implications for research

There is a need for more evidence on how best to identify records which report research into modes of data collection.

Some of the analyses showed unexpected results which might merit further research. These include lifetime alcohol use being higher when a web survey was used compared to PAPI, although there was no difference for lifetime marijuana use. Also, the evidence of differences in reported mental health for telephone compared with web surveys merit further investigation. Whether and in what situations web surveys yield poorer response rates compared to other modes in adolescents should also be investigated in future studies.

The absence of research evidence on the impact of survey mode on mental health scores by gender or other demographic characteristics, suggests this area could merit research.

There is a need for research that could better reflect the current situation where adolescents’ use of the internet and smart phones is widespread.

Implications for practice

Survey designers must balance practical concerns against the sampling, non-response and measurement error associated with specific design features. This review, and others, highlight methods and strategies that may improve survey response rates among adolescents with minimal impact on the assessment of mental health status [ 11 , 12 , 42 ]. Based on the poor reporting in the included studies, authors should be encouraged to register their trials and make their protocols publicly available. Authors and journal editors should follow the CONSORT reporting guidelines [ 50 ].

Despite the absence of low RoB studies, few studies for some comparisons and the focus on research undertaken in high income countries, there are methods and strategies that could be considered for improving survey response rates among adolescents being surveyed about mental health and substance use. For example, the use of monetary incentives may lead to higher response rates. Our review show that survey mode has limited impact on response rates in surveys delivered in school settings. Outside school settings, web surveys may be superior to other modes, but more research is needed to determine this. More studies using controlled designs are needed to further identify effective methods and strategies to ensure adequate response rates among adolescents. Some studies indicate that mental health scores may differ between certain survey modes. Finally, there was limited evidence on any differences between gender and survey characteristics on mental health scores.

Availability of data and materials

The templates for data collection, the extracted data and the data used for all of the analyses are available from the main author upon reasonable request.

Abbreviations

Preferred Reporting Items for Systematic Reviews and Meta-Analyses

Randomised controlled trial

Standardized mean difference

Grading of Recommendations, Assessment, Development, and Evaluations

Mean difference

Paper-and-pencil

Child Health Questionnaire

Children’s Depression Inventory

Spence Children’s Anxiety Scale

RAND 36-Item Short Form Health Survey

Hospital Anxiety and Depression Scale

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Acknowledgements

The Department of Child and Development and the Division of Health Services within the Norwegian Institute of Public Health funded this project. We thank our colleagues Dr. Simon Lewin and Dr. Chris Ross for their time and Ingvild Kirkehei for reviewing the search strategy.

Open access funding provided by Norwegian Institute of Public Health (FHI) The authors report no funding sources.

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Julia Bidonde, Jose F. Meneses-Echavez & Elisabet Hafstad

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Geir Scott Brunborg & Lasse Bang

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L.B: Conceptualization (equal); Formal Analysis (equal); Writing – Original Draft Preparation (equal); Writing – Review & Editing (equal). J.B: Conceptualization (lead); Data Curation (lead); Formal Analysis (lead); Investigation (lead); Methodology (lead); Project Administration (lead); Supervision (lead); Validation (lead); Visualization (equal); Writing – Original Draft Preparation (lead); Writing – Review & Editing (lead). G.S.B: Conceptualization (equal); Formal Analysis (equal); Writing – Original Draft Preparation (equal); Writing – Review & Editing (equal). E.H: Conceptualization (equal); Investigation (equal); Methodology (equal); Writing – Original Draft Preparation (equal); Writing – Review & Editing (equal). J.F.M-E: Conceptualization (equal); Data Curation (equal); Formal Analysis (equal); Investigation (equal); Methodology (equal); Validation (equal); Visualization (lead); Writing – Original Draft Preparation (equal); Writing – Review & Editing (equal). All authors read and approved the final manuscript.

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Supplementary Information

Additional file 1..

Eligibility criteria and Glossary.

Additional file 2.

Search strategies and lists of excluded studies.

Additional file 3.

Detailed data extraction for the included studies.

Additional file 4.

Risk of bias assessment.

Additional file 5.

PRISMA checklist.

Additional file 6.

Additional Forest plots.

Additional file 7.

Protocol changes.

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Bidonde, J., Meneses-Echavez, J.F., Hafstad, E. et al. Methods, strategies, and incentives to increase response to mental health surveys among adolescents: a systematic review. BMC Med Res Methodol 23 , 270 (2023). https://doi.org/10.1186/s12874-023-02096-z

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Systematic review article, efficacy and safety of anisodine hydrobromide injection for acute ischemic stroke: a systematic review and meta-analysis.

• 1 School of Sports Medicine and Health, Chengdu Sport University, Chengdu, Sichuan, China
• 2 Postdoctoral Workstation, Affiliated Sport Hospital of Chengdu Sport University, Chengdu, Sichuan, China
• 3 State Key Laboratory of Southwestern Chinese Medicine Resources, Chengdu University of Traditional Chinese Medicine, Chengdu, Sichuan, China
• 4 Sichuan Academy of Chinese Medicine Science, Chengdu, Sichuan, China
• 5 Institute of Laboratory Animal Sciences, Sichuan Provincial People’s Hospital, University of Electronic Science and Technology of China, Chengdu, Sichuan, China

Background: Acute ischemic stroke (AIS) is a leading cause of death and disability worldwide. This study aimed to evaluate the efficacy and safety of anisodine hydrobromide (Ani) injection in the treatment of AIS.

Methods: Randomized controlled trials (RCTs) based on Ani injection for the treatment of AIS were retrieved from both Chinese and English databases. The retrieval period was from the databases’ inception to May 2023. The Cochrane Collaboration Risk of Bias Tool was used to assess the methodological quality. The outcome indicators were analyzed using RevMan 5.3 software.

Results: We included the findings of 11 RCTs encompassing 1,337 patients with AIS. Our meta-analysis revealed that Ani injection supplementation significantly reduced the National Institutes of Health Stroke Scale [MD = −1.53, 95%CI = (−1.94, −1.12), p < 0.00001], modified Rankin Scale [MD = −0.89, 95%CI = (−0.97, −0.81), p < 0.00001], and the relative time to peak [SMD = −0.81, 95%CI = (−1.08, −0.55), p < 0.00001] significantly. Additionally, Ani injection significantly increased the Barthel Index [MD = 10.65, 95%CI = (4.30, 17.00), p = 0.001], relative cerebral blood volume [SMD = 0.28, 95%CI = (0.02, 0.53), p = 0.03], and clinical efficacy [RR = 1.2, 95%CI = (1.08, 1.34), p = 0.001]. No statistically significant difference in the rate of adverse events was observed between the Ani injection supplemental group and the control group.

Conclusion: Based on currently published evidence, Ani injection was found to be effective and safe in improving AIS outcome. Nevertheless, limitations of the included RCTs still exist, and thus, more multi-center, large-sample, high-quality RCTs are required to further verify the efficacy and safety of Ani injection in patients with AIS.

Systematic Review Registration: [ https://www.crd.york.ac.uk/prospero/display_record.php?ID=CRD42023427591 ], identifier [PROSPERO 2023 CRD42023427591].

1 Introduction

Acute ischemic stroke (AIS) is characterized by ischemia, hypoxic necrosis, and softening of the brain tissue due to a sudden interruption of the cerebral blood supply with inadequate collateral circulation, resulting in a series of symptoms of neurological dysfunction ( Zhang et al., 2020 ). AIS is the most common type of cerebral stroke, accounting for approximately 70% of all strokes. Worldwide, AIS is a leading cause of death and disability ( Wang et al., 2019 ). In China, the mortality rate of hospitalized AIS patients within 1 month of onset is approximately 2.3%–3.2%, the 1-year mortality rate after onset is 14.4%–15.4%, and the disability rate is 33.4%–33.8% ( Wang et al., 2013 ; Wang et al., 2017 ). The associated socioeconomic burden of AIS is huge; for example, the annual expenditure related to AIS, including long-term rehabilitation and unemployment, is estimated to be £ 25.6 billion in the United Kingdom ( Robert et al., 2020 ). Therefore, AIS has become a major global health concern.

At present, regular treatment of AIS consists of a multidisciplinary approach. Treatment management for AIS includes drug therapy, limb rehabilitation, language training, psychological rehabilitation, and health education ( Trialists’Collaboration, 2013 ). Intravenous thrombolysis with recombinant tissue-type plasminogen activator (rtPA) and endovascular therapy have been the mainstay treatments for AIS in recent years ( Powers et al., 2018 ). Both therapeutic strategies aim to rescue ischemic brain tissue with viable potential by recanalization of occluded cerebral arteries and reperfusion of the ischemic penumbra ( Robert et al., 2020 ). Nevertheless, the number of patients with AIS who are eligible for such reperfusion strategies remains low due to the narrow time window of reperfusion therapy ( Rodrigues et al., 2016 ; Bhaskar et al., 2018 ). More specifically, the therapeutic effect is heavily time dependent; therefore, the stroke symptom onset should be recorded accurately as a clock time to avoid treatment failure. Intravenous thrombolysis and endovascular thrombectomy for AIS patients with an unclear onset time require further exploration ( Qiang et al., 2017 ). Furthermore, clinical evidence has shown that only patients with large vessel occlusive-type AIS are candidates for endovascular therapy, which accounts for less than 20% of AIS cases ( Yasha et al., 2019 ). Symptomatic intracranial hemorrhage after thrombolysis and endovascular treatment in patients with AIS is a major complication that is associated with a devastating clinical outcome. The high frequency of intracranial hemorrhage poses a huge challenge to the clinical management of AIS ( Seet and Rabinstein, 2012 ; Hao et al., 2017 ). In addition, as a serious complication of vascular recanalization, ischemia–reperfusion injury in the setting of cerebral ischemia following vascular restoration occurs because of a complex series of events, which can evoke parenchymal brain damage ( Nour et al., 2013 ). Therefore, novel therapeutic strategies are urgently required to improve the efficacy and safety of AIS treatment.

A tenet of traditional folk medicine in China is that herbs possess the ability to treat various diseases. Modern researchers have demonstrated that compounds in these medicinal herbs, which consist of multiple ingredients, have multiple pharmacological actions, which are compatible with the complex pathogenesis of diverse human diseases ( Chen et al., 2022 ). For many years in China, various traditional folk herbs have been applied in the treatment of AIS based on the theory of promoting blood circulation and removing blood stasis ( Gong and Sucher, 2002 ). In-depth studies have elucidated the underlying mechanisms of the therapeutic effect of traditional medicinal herbs, which involve the inhibition of excitotoxicity, inflammation, oxidative damage, ionic imbalances, apoptosis, and so on, in the pathophysiological process of AIS ( Sucher, 2006 ). A meta-analysis including 191 clinical trials involving 22 types of traditional Chinese medicine has demonstrated the improvement of neurological deficits after administration ( Wu et al., 2007 ).

Anisodus tanguticus (Maxim.) Pascher, also named “Tang Chuan Na Bao” in Ethnologue, one of the indigenous Chinese ethnological plants of the Solanaceae, is mainly grown in the Qinghai–Tibet Plateau ( Liu et al., 2005 ). In traditional Chinese medical theory, A. tanguticus possesses the traditional characteristics of nature of a warm, bitter flavor and functions to activate the blood to remove stasis ( Chen et al., 2022 ). Anisodine, a tropane alkaloid extracted from the root of A. tanguticus , has been used as an ingredient in the compound preparation for treating ischemic stroke in China for more than a decade due to its significant properties of vasoactivity and improvements in microcirculation. To improve the chemical instability, researchers have developed a hydrobromide form of anisodine ( Liu et al., 2020 ). Recently, anisodine hydrobromide (Ani) injection has been used in the clinical setting for the treatment of AIS in China. Multiple clinical studies have demonstrated the neuroprotective effect of Ani in AIS, which can not only alleviate neurological impairment and reduce dependency in activities of daily living but also improve the cerebral collateral circulation and increase cerebral tissue blood flow perfusion in ischemic areas ( Zou et al., 2018 ; Zhang, 2022 ). Basic research has revealed that, as a central muscarinic cholinergic receptor blocker, the neuroprotective and cerebral circulation-promoting effect of Ani injection in the treatment of AIS can be correlated to the pharmacological actions of anti-oxidative damage, anti-inflammation, inhibition of neuronal apoptosis, and amelioration of hemorheological changes through regulation of the nitric oxide synthase system, preventing Ca 2+ influx, decreasing IL-6 serum levels, and modulating angiogenic factors. Furthermore, the ability of Ani to activate the ERK1/2 signaling pathway and regulate ATPase activity is also a key underlying mechanism of action ( Chen et al., 2017 ; Wang et al., 2017 ; Chen et al., 2017d ; Xu et al., 2020 ; Zeng et al., 2021 ).

The impact of Ani injection on patients with AIS has been investigated in many clinical trials. In 2021, the earliest meta-analysis conducted by Wang et al. (2021) reported that Ani may have a positive effect in the treatment of ischemic stroke. However, the subjects included in Wang’s study were patients with ischemic stroke at various stages, including both the acute stage and the convalescent stage. In addition, the study objective of several included randomized controlled trials (RCTs) focused on the synergistic effect of Ani combined with acupuncture or butylphthalide. There were certain limitations without further assessment targeting each specific clinical stage (including the acute stage of ischemic stroke) and the pure effect of Ani injection. Therefore, the present study aimed to systematically collect the current clinical evidence regarding Ani injection in the treatment of the acute stage of ischemic stroke and, more specifically, evaluate its efficacy and safety. We hope this meta-analysis and systematic review will provide an accurate and reliable evidence-based reference for its rational use in the clinic.

2.1 Study registration

This meta-analysis was performed in strict accordance with the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) and was registered in PROSPERO (CRD42023427591).

2.2 Search strategy

Both English databases (including EMBASE, PubMed, Cochrane library, and Web of Science) and Chinese databases (including CNKI, VIP, Wanfang, and Chinese Biomedical Literature Database) were searched comprehensively from the date of their respective inception to May 2023 for the identification of eligible data. The following terms used in the search are a combination of MESH terms and free-text words: (“Anisodine hydrobromide injection” (Text word) OR “Anisodine hydrobromide” (Text word) OR “Anisodine” (Text word) AND [“Acute ischemic stroke” (Text Word) OR “ischemic stroke” (MESH) OR “brain ischemia” (MESH) OR “stroke” (MESH) OR “cerebral infarction” (MESH) OR “Cerebrovascular ischemia” (Text word) OR “Infarction, Anterior Cerebral Artery” (Text word) OR “Infarction, Middle Cerebral Artery” (Text word) OR “Infarction, Posterior Cerebral Artery” (Text word) OR “Apoplexy” (Text word)]. Potential studies in the reference lists of valid studies were also considered as information sources.

2.3 Inclusion and exclusion criteria

The inclusion criteria were as follows: 1) patients with AIS, regardless of age, gender, and disease stage; 2) parallel RCTs of Ani injection for AIS patients published in English or Chinese databases; 3) control group treated with regular therapies, while Ani injection was not applied in the control group; and 4) the trial groups were treated with Ani injection, used alone or in combination with the same regular therapies used in the control groups, regardless of the dose or duration of administration.

The exclusion criteria were as follows: 1) cerebral hemorrhage in patients with AIS; 2) reviews, letters, conference reports, cohort studies, case reports, cross-over studies, and animal studies; 3) duplicate studies or those with no comparison group; 4) literature without essential information or unable to obtain the related data; and 5) the trial group underwent acupuncture.

2.4 Outcome measures

In this systematic review and meta-analysis, the primary outcomes were as follows: National Institutes of Health Stroke Scale (NIHSS), modified Rankin Scale (mRS), and Barthel Index (BI). The secondary outcomes were computed tomography parameters (CTP), effective rate, and adverse events.

2.5 Study selection and data extraction

All electronic bibliographic databases mentioned above were scanned with a pre-designed search strategy. Duplicate articles were removed first. Next, two independent reviewers reviewed the titles and abstracts of the studies to select appropriate studies according to the eligibility criteria. The full texts of the selected studies were downloaded for further assessment. Three initial articles were used as a pilot to establish a standard extraction form, which contains the following domains: study information (title, first author, language, magazine, and year of publication), participant information (e.g., age, sex ratio, sample size, and disease course), intervention information (e.g., type, duration, frequency, and dose of treatment in the trial and control groups), and outcome indexes (primary outcomes and secondary outcomes). Reasons for the exclusion of ineligible studies were identified and recorded. Available data were extracted by two independent reviewers from the full texts. The two reviewers addressed disagreements through discussion or via consultation with a third reviewer.

2.6 Quality assessment

The Cochrane Collaboration Risk of Bias Tool in the Cochrane Handbook for Systematic Reviews of Interventions ( Higgins et al., 2022 ) was used by two independent researchers to evaluate the methodological quality. According to the Cochrane Handbook, the risk of bias assessment was divided into seven domains: random sequence generation (selection bias), allocation concealment (selection bias), blinding of participants and personnel (performance bias), blinding of outcome assessment (detection bias), incomplete outcome data (attrition bias), selective reporting (reporting bias), and other bias. Each domain in the included RCTs was marked according to a low risk of bias, high risk of bias, or an unclear risk of bias. Disagreement between the two researchers was arbitrated by a third researcher.

2.7 Statistical analysis

The RevMan 5.3 software was used for meta-analysis. The relative risk ( RR ) was used as the effect index for the dichotomous variables, and the mean differences ( MD ) or standardized mean difference ( SMD ) were used as the effect index for continuous variables. The confidence interval ( CI ) of each effect index was set to 95%. The I 2 statistic was adopted to assess the heterogeneity. If I 2 > 50%, there was heterogeneity between the studies, and the random-effect model was selected; otherwise, the fixed-effect model was utilized. The heterogeneity was explained by sensitivity analysis or subgroup analysis. In addition, descriptive analysis was performed if the clinical data provided by the included studies were incomplete and could not be systematically evaluated. Potential publication bias was evaluated through a funnel plot.

3.1 Study selection

The PRISMA flowchart of the literature screening process is presented in Figure 1 . Initially, according to the search strategy, a total of 179 studies were obtained through retrieval from multiple databases; after the deletion of 85 duplicate publications, the remaining 94 articles were screened. After examination of the titles and abstracts, 58 irrelevant studies were removed. The full texts of the 36 remaining articles were assessed for eligibility. Preclinical studies ( n = 10), non-RCTs ( n = 3), and studies that did not meet the inclusion or met the exclusion criteria ( n = 12) were excluded. Finally, 11 studies were included in the meta-analysis ( Zou et al., 2018 ; Wang et al., 2020 ; Dong et al., 2021 ; Li et al., 2021 ; Zhang et al., 2021 ; Jiang et al., 2022 ; Kang, 2022 ; Zhang, 2022 ; Zhang et al., 2022 ; Zhou, 2022 ; Yan et al., 2023 ).

FIGURE 1 . PRISMA flowchart for literature screening.

3.2 Study characteristics

A total of 1,337 patients with AIS were included in the meta-analysis, including 668 patients in the trial group and 669 patients in the control group. All included studies were conducted in China. The sample size in each included study ranged from 21 to 193. The shortest treatment duration of an Ani injection was 7 days, and the longest was 30 days. The time period from AIS symptom onset to hospital admission was ≤72 h in all studies. Regarding the outcome measurements, the NIHSS was adopted in all studies ( Zou et al., 2018 ; Wang et al., 2020 ; Dong et al., 2021 ; Li et al., 2021 ; Zhang et al., 2021 ; Jiang et al., 2022 ; Kang, 2022 ; Zhang, 2022 ; Zhang et al., 2022 ; Zhou, 2022 ; Yan et al., 2023 ), five studies used the mRS ( Wang et al., 2020 ; Dong et al., 2021 ; Kang, 2022 ; Zhang, 2022 ; Zhang et al., 2022 ), four studies used the BI ( Zou et al., 2018 ; Jiang et al., 2022 ; Zhang et al., 2022 ; Zhou, 2022 ), three studies reported the CTP ( Zou et al., 2018 ; Zhang et al., 2022 ; Zhou, 2022 ), two studies mentioned the effective rate ( Kang, 2022 ; Yan et al., 2023 ), and adverse events were described in seven studies ( Zou et al., 2018 ; Dong et al., 2021 ; Li et al., 2021 ; Zhang et al., 2021 ; Jiang et al., 2022 ; Zhang, 2022 ; Zhang et al., 2022 ), while three studies reported the adverse rate ( Dong et al., 2021 ; Li et al., 2021 ; Zhang et al., 2021 ). The characteristics of the included studies are presented in Table 1 .

TABLE 1 . Characteristics of included studies.

3.3 Risk of bias of the included studies

The assessment of bias risk of each eligible study was performed according to the Cochrane bias risk tool. Nine of the included studies mentioned grouping by a random method, three of which specified that a random sequence was generated through the random number table method ( Dong et al., 2021 ; Li et al., 2021 ; Zhou, 2022 ). None of these studies referred to information on allocation concealment, blinding of participants and personnel, or blinding of the outcome assessment; therefore, all the studies were rated as having an unclear risk of bias in these three sections. All other bias evaluation risks were unclear. The results of the risk of bias assessment are presented in Figures 2 , 3 . See the supplementary document of Supplementary Material for rating bias ( Supplementary Table S1 ).

FIGURE 2 . Risk of bias graph.

FIGURE 3 . Risk of bias summary.

3.4 Outcome measures

3.4.1 national institutes of health stroke scale.

Eleven studies included the NIHSS score, of which one study ( Zhang, 2022 ) did not report the post treatment NIHSS score; this data could not be extracted from the existing information. Thus, ten articles ( Zou et al., 2018 ; Wang et al., 2020 ; Dong et al., 2021 ; Li et al., 2021 ; Zhang et al., 2021 ; Jiang et al., 2022 ; Kang, 2022 ; Zhang et al., 2022 ; Zhou, 2022 ; Yan et al., 2023 ) with 1,305 participants were included in the meta-analysis regarding the NIHSS score. The heterogeneity test results showed that p < 0.0001, I 2 = 75%, and there was significant heterogeneity among the studies. Therefore, a random-effect model was adopted. The pooled results of the post-treatment NIHSS score indicated that compared with the control group, Ani injection could significantly reduce the NIHSS score after treatment [MD = −1.53, 95%CI = (−1.94, −1.12), p < 0.00001], as shown in Figure 4 .

FIGURE 4 . A meta-analysis of the NIHSS.

In these studies, the NIHSS score was evaluated at different treatment time periods, which ranged from 7 days to 90 days of treatment. Therefore, we used treatment duration to conduct further NIHSS evaluations (7 days, 14 days, and ≥30 days) as the criteria for the subgroup analysis. The results of the subgroup analysis are shown in Figure 4 . It can be clearly seen that at the different time periods of 7 days, 14 days, and ≥30 days for implementing the NIHSS assessment, the NIHSS score of the experimental group was significantly lower than that of the control group [MD = −1.03, 95%CI = (−1.72, −0.33), p = 0.004; MD = −1.38, 95%CI = (−1.86, −0.89), p < 0.00001; MD = −2.45, 95%CI = (−3.39, −1.52), p < 0.00001, respectively]. The result of the subgroup differences ( p = 0.05, I 2 = 66.2%) indicated that this subgrouping factor might be a source of heterogeneity in the overall meta-analysis regarding the NIHSS score.

3.4.2 Modified Rankin Scale

Five studies reported the mRS score; however, the data could not be extracted from one study ( Dong et al., 2021 ) due to the provided data being dichotomous. Thus, a total of four studies ( Wang et al., 2020 ; Kang, 2022 ; Zhang, 2022 ; Zhang et al., 2022 ) were included. The results of the heterogeneity test demonstrated that p = 0.81 and I 2 = 0%; no significant heterogeneity was observed. Using the fixed-effect model, the results of the meta-analysis showed that the mRS score in the experimental group was significantly lower than that of the control group [MD = −0.89, 95%CI = (−0.97, −0.81), p < 0.00001], as shown in Figure 5 .

FIGURE 5 . A meta-analysis of mRS.

3.4.3 Barthel index

Four studies ( Zou et al., 2018 ; Jiang et al., 2022 ; Zhang et al., 2022 ; Zhou, 2022 ) included the BI score. A meaningful increasing effect of Ani treatment was observed with the BI score level from the meta-analysis [MD = 10.65, 95%CI = (4.30, 17.00), p = 0.001]. Meanwhile, a significance between heterogeneity was observed ( p < 0.00001, I 2 = 96%); thus, a random-effect model was adopted for the meta-analysis ( Figure 6 ). The test for subgroup differences between trials that adopted the BI measurement [two RCTs ( Zhang et al., 2022 ; Zhou, 2022 )] [MD = 5.82, 95%CI = (4.07, 7.57), p < 0.00001] and modified BI measurement [two RCTs ( Zou et al., 2018 ; Jiang et al., 2022 )] [MD = 15.10, 95%CI = (2.62, 27.59), p = 0.02] was non-significant ( p = 0.15, I 2 = 52%) ( Figure 6 ).

FIGURE 6 . A meta-analysis of BI.

3.4.4 CT parameters

Three studies ( Zou et al., 2018 ; Zhang et al., 2022 ; Zhou, 2022 ) reported the CTP, including relative cerebral blood flow (rCBF), relative cerebral blood volume (rCBV), relative time to peak (rTTP), and relative mean transit time (rMTT). The SMD was used as a summary statistic due to the consistency of the units in these studies being unclear. The pooled results indicated no statistically significant differences in the rCBF [SMD = 0.27, 95%CI = (−0.47, 1.01), p = 0.48] and rMTT [SMD = −0.71, 95%CI = (−2.20, 0.79), p = 0.35] between the Ani injection and the conventional therapy group and showed large heterogeneity ( p = 0.0006, I 2 = 87%; p < 0.00001, I 2 = 96%, respectively) ( Figures 7 , 8 ). The effect of Ani injection on rCBF and rMTT, however, was not substantial. After sensitivity analysis by deleting one study ( Zhang et al., 2022 ), the overall effect of Ani injection on rCBF and rMTT was significantly changed [SMD = 0.68, 95%CI = (0.40, 0.97), p < 0.00001; SMD = −1.57, 95%CI = (−1.89, −1.25), p < 0.00001, respectively]. Heterogeneity in both outcomes was also significantly reduced to 0%, which suggested that this study ( Zhang et al., 2022 ) might be the source of the heterogeneity of the rCBF and rMTT data. Both the rCBV and rTTP levels were significantly changed by Ani injection therapy [SMD = 0.28, 95%CI = (0.02, 0.53), p = 0.03; SMD = −0.81, 95%CI = (−1.08, −0.55), p < 0.00001, respectively] without between-study heterogeneity ( p = 0.36, I 2 = 3%; p = 0.90, I 2 = 0%, respectively) ( Figures 9 , 10 ).

FIGURE 7 . A meta-analysis of rCBF.

FIGURE 8 . A meta-analysis of rMTT.

FIGURE 9 . A meta-analysis of rCBV.

FIGURE 10 . A meta-analysis of rTTP.

3.4.5 Clinical efficacy

Two studies ( Kang, 2022 ; Yan et al., 2023 ) reported the clinical effective rate, which was evaluated according to the NIHSS score for stroke patients. The heterogeneity test results showed that there was no significant heterogeneity among these studies ( p = 0.82, I 2 = 0%); therefore, the fixed-effect model was adopted. The pooled results showed that the effective rate of the Ani injection-treated group was significantly better than that of the conventional therapy group [RR = 1.2, 95%CI = (1.08, 1.34), p = 0.001] ( Figure 11 ).

FIGURE 11 . A meta-analysis of clinical efficacy.

3.4.6 Adverse events

A total of seven articles ( Zou et al., 2018 ; Dong et al., 2021 ; Li et al., 2021 ; Zhang et al., 2021 ; Jiang et al., 2022 ; Zhang, 2022 ; Zhang et al., 2022 ) recorded adverse reactions, of which two ( Zhang, 2022 ; Zhang et al., 2022 ) reported that no adverse events occurred during treatment and two ( Zou et al., 2018 ; Jiang et al., 2022 ) reported mild side effects, including dry mouth and facial flushing; these symptoms had completely disappeared after slowing down the drip rate.

The other three articles ( Dong et al., 2021 ; Li et al., 2021 ; Zhang et al., 2021 ) reported the incidence of adverse reactions. Using the random-effect model ( p = 0.12, I 2 = 53%) for the meta-analysis, the pooled results showed that there were no significant differences between the Ani injection supplemental group and the control group [RR = 1.25, 95%CI = (0.52, 3.03), p = 0.62] ( Figure 12 ). Dong et al. (2021) observed 12 cases of dry mouth and facial flushing in the experimental group and 8 cases of nausea and vomiting in the control group. Zhang et al. (2021) reported 6 cases of nausea, vomiting, dry mouth, and facial flushing in the control group and 2 cases of nausea and vomiting in the experimental group. Li et al. (2021) found 2 cases of elevated alanine aminotransferase (ALT), 2 cases of dizziness, 3 cases of weakness, and 6 cases of gastrointestinal reactions in the experimental group and 1 case of elevated ALT, 1 case of weakness, and 4 cases of gastrointestinal reactions in the control group. Table 2 presents the adverse reactions of the involved studies.

FIGURE 12 . A meta-analysis of the rate of adverse events.

TABLE 2 . Summary of adverse events of the involved studies.

3.5 Publication bias

A funnel plot was conducted to assess the publication bias of 10 trials or more. Thus, the 10 included studies that included available NIHSS score data were used for publication bias assessment, as shown in Figure 13 . The shape of the funnel plot of the NIHSS showed the moderate symmetry between the included studies, which indicated that the potential of publication bias was low.

FIGURE 13 . Funnel plot for the publication bias of the NIHSS.

4 Discussion

4.1 summary of findings.

A total of 11 RCTs were included in this meta-analysis. Combined with conventional therapy, Ani injection was used to treat 1,337 patients with AIS. The NIHSS, mRS, BI, CTP, effective rate, and adverse events were evaluated in the analysis. According to the findings, the NIHSS score of Ani injection therapy was much lower than that of conventional therapy alone. Other primary indicators showed that Ani injection significantly reduced the mRS score and increased the BI score. The secondary outcome indicators revealed that treatment with Ani injection increased the rCBV, reduced the rTTP, and improved the clinical efficacy, with significant differences observed. The pooled analysis of the included studies failed to identify a significant change in the rCBF, rMTT, and rate of adverse reactions.

Subgroup analyses indicated that at the different time periods of 7 days, 14 days, and ≥30 days for implementing the NIHSS assessment, the NIHSS score of the Ani treatment group was considerably decreased. Furthermore, the subgrouping factor might be a source of significant heterogeneity for the NIHSS. Subgroup analyses on the BI score based on the BI assessment method (original BI and modified BI) suggest that regardless of the BI assessment method used, Ani treatment exhibits an advantage in significantly increasing the BI score. However, the subgroup analysis of BI did not identify the source of heterogeneity; significant heterogeneity may be associated with factors such as small sample sizes and few included studies.

A sensitivity analysis of rCBF and rMTT suggested that the pooled results are not robust and that the study of Zhang et al. (2022) might be the source of rCBF and rMTT heterogeneity.

In the risk of bias section, the quality assessment of the current included studies showed that allocation concealment, blinding of participants and employees, and blinding of the outcome assessment, as well as other forms of bias, were not disclosed in any of the included studies, which suggested that the certainty of evidence in the included RCTs was not high. Consequently, the results of the meta-analysis may be influenced, and our findings based on the current evidence should be considered carefully in the clinic. More precise RCTs are needed to further validate the curative effect of Ani injection in patients with AIS.

4.2 Interpretation

Traditional Chinese herbal medicines have a long history of clinical application in treating various vascular diseases, with distinctive theories and rich practices ( Hung et al., 2015 ; Hao et al., 2017 ). Products from traditional Chinese medicinal herbs have been widely described in various ancient medicine systems for treating ischemic stroke, myocardial infarction, and so on ( Hung et al., 2015 ). Anisodine is one of the most important ingredients of the tropane-type alkaloids extracted from the traditional folk medicinal herb A. tanguticus , with significant biological activities for promoting blood circulation and removing blood stasis ( Meng et al., 2023 ). Pharmaceutical products containing anisodine are frequently used in the clinic for the treatment of vascular diseases, including ischemic stroke ( Zou et al., 2018 ), retinal artery occlusion ( Wu et al., 2016 ), ischemic optic neuropathy ( Zhang et al., 2019 ), and cerebral small vessel disease ( Gui et al., 2019 ). Ani injection has been developed for improved chemical stability and is a promising treatment for AIS.

Poor perfusion of brain tissue caused by the abrupt interruption or reduction of cerebral blood flow is the etiology of AIS, which can then induce ischemic hypoxic necrosis, clinically manifesting as different degrees of neurological impairment ( Brott and Bogousslavsky, 2000 ). The molecular mechanism of AIS can be summarized as a complex series of ischemic cascades, characterized by cellular bioenergetic failure, excitotoxicity, excessive intraneuronal accumulation of Na + , Cl − , and Ca 2+ , oxidative damage, inflammatory reaction, mitochondrial injury, and, finally, cell death ( Rosenblum, 1997 ; Brouns and De Deyn, 2009 ). Guidelines for the management of AIS have been reported by various countries ( Swain et al., 2008 ; Di et al., 2019 ; Powers et al., 2019 ); the fundamental goals of the intervention have been focused on restoring or increasing the blood supply to the brain and blockading or slowing of the cerebral ischemic cascade ( Olsen et al., 1983 ; Escuret, 1995 ; Brott and Bogousslavsky, 2000 ). The conventional therapy adopted in the 11 included studies varied across different care settings, including general management (such as respiratory and oxygen intake, cardiac monitoring and cardiac disease management, temperature control, blood pressure control, blood sugar control, and nutritional support, etc.) and specific treatment (thrombolysis, antiplatelet drugs, anticoagulants, statins, defibrase, and diuretics, etc.). Nevertheless, the narrow treatment window and hemorrhagic complications have limited the utilization and therapeutic effect of conventional therapy.

Recent studies have revealed that in addition to the recanalization of the large cerebral vessels, the restoration of normal vasomotor function around the ischemic area, the improvement in micro-perfusion, and neuronal cell protection are crucial for the treatment of cerebral infarction and are closely related to the prognosis of AIS ( Tuttolomondo et al., 2009 ; Shuaib et al., 2011 ; Bang et al., 2015 ). As a central muscarinic cholinergic antagonist, Ani can effectively relieve vasospasm, open closed arterioles and the anterior capillary sphincter, and restore the perfusion of brain tissue ( Wang et al., 2018 ). Research has demonstrated that following Ani administration, the microvascular autonomic motion reappears in the small intestinal wall micro-artery ischemia model, with a significant increase in microvascular amplitude, blood velocity, and flow ( Zhang et al., 2019 ). Through the establishment of a hypoxia/reoxygenation (H/R)-induced brain microvascular endothelial cell injury model, Ani injection has been shown to suppress H/R-induced hypoxia-inducible transcription factor 1(HIF-α) over-expression, nitric oxide (NO), and reactive oxygen species (ROS) production, and all these effects were dependent on M4-AchR ( Zeng et al., 2021 ). Additionally, Ani has multiple non-cholinergic effects, including cell protective effects, autophagy ( Chen et al., 2017b ), attenuating neuronal cell death and apoptosis ( Chen et al., 2017d ), alleviating oxidative stress damage and decreasing Ca 2+ accumulation ( Chen et al., 2017 ; Wang et al., 2017 ; Chen et al., 2017e ), and inhibiting membrane lipid peroxidation ( Zhao and Chen, 2010 ), thereby alleviating cell damage caused by ischemia and hypoxia. Further studies have found that Ani can decrease the Longa rodent stroke scores and cerebral infarction area in middle cerebral artery occlusion (MCAO) rats ( Chen et al., 2017c ). Moreover, the underlying mechanism of the effect of Ani on AIS can also be attributed to the ability to improve hemorheology and resist platelet aggregation so as to improve cerebral microcirculation disorders ( Xu et al., 2020 ).

4.3 Strengths and limitations

In short, based on current evidence, Ani injection therapy was found to be effective and safe in patients with AIS. The positive effect of Ani injection may be attributed to the ability of Ani to penetrate the blood–brain barrier and act as a non-specific muscarinic cholinergic receptor antagonist, competing with acetylcholine in the central nervous system, resulting in increased cerebral blood supply and neuroprotection effects ( Liu et al., 2020 ; Jiang et al., 2022 ). The results of this meta-analysis demonstrated that the efficacy of Ani injection in the treatment of AIS was superior to that of conventional therapy; however, several limitations still exist. First, the sample size of the included RCTs was small, so the subgroup analysis and publication bias assessment could not be conducted for all indicators, which may have affected the accuracy and reliability of the results. Second, all trials lacked a precise description of the allocation concealment and blinding methods (for participants, personnel, and outcome assessments); the description of random sequence generation was also missed in some studies. As a consequence, the general methodological quality of the studies was not satisfactory. Third, the longest intervention duration in all the articles was 90 days, and there was a lack of long-term follow-up visits for more than 90 days after treatment, which was insufficient to assess the long-term impact of Ani therapy on the health of patients. Additionally, all the included RCTs were conducted in China; therefore, it is necessary to utilize multi-regional clinical trials for Ani treatment evaluation in different regions of the world in the future to provide strong evidence for the efficacy and safety of Ani treatment in patients with AIS.

5 Conclusion

Taken together, the meta-analysis results from the included RCTs revealed that Ani injection is effective and safe in the treatment of patients with AIS, with positive impacts on the NIHSS, mRS, BI, rCBV, rTTP, and clinical efficacy. However, due to limitations in the number and quality of included studies, more multi-center, large-sample, high-quality RCTs are needed for further verification of the efficacy and safety of Ani injection in treating AIS.

Data availability statement

The original contributions presented in the study are included in the article/ Supplementary Material , further inquiries can be directed to the corresponding authors.

Author contributions

YW: Data curation, Formal Analysis, Methodology, Writing–original draft. FW: Conceptualization, Investigation, Writing–review and editing. PH: Data curation, Investigation, Writing–review and editing. BH: Funding acquisition, Supervision, Writing–review and editing. YH: Funding acquisition, Supervision, Writing–review and editing. YL: Conceptualization, Formal Analysis, Funding acquisition, Methodology, Writing–original draft.

The author(s) declare financial support was received for the research, authorship, and/or publication of this article. This work was supported by the Natural Science Foundation of Sichuan Province (No. 2022NSFSC1529), S&T Project of Sichuan Provincial Administration of Traditional Chinese Medicine (No. 2021MS519), and the Fund of Key Laboratory for Sports Medicine of Sichuan Province and General Administration of Sport (No. 2023-A032).

Conflict of interest

The authors declare that the research was conducted in the absence of any commercial or financial relationships that could be construed as a potential conflict of interest.

Publisher’s note

All claims expressed in this article are solely those of the authors and do not necessarily represent those of their affiliated organizations, or those of the publisher, the editors and the reviewers. Any product that may be evaluated in this article, or claim that may be made by its manufacturer, is not guaranteed or endorsed by the publisher.

Supplementary material

The Supplementary Material for this article can be found online at: https://www.frontiersin.org/articles/10.3389/fphar.2023.1290755/full#supplementary-material

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Keywords: acute ischemic stroke, anisodine hydrobromide injection, systematic review, meta-analysis, efficacy

Citation: Wang Y, Wan F, Hu P, He B, Hu Y and Liu Y (2023) Efficacy and safety of anisodine hydrobromide injection for acute ischemic stroke: a systematic review and meta-analysis. Front. Pharmacol. 14:1290755. doi: 10.3389/fphar.2023.1290755

Received: 08 September 2023; Accepted: 30 October 2023; Published: 15 November 2023.

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Copyright © 2023 Wang, Wan, Hu, He, Hu and Liu. This is an open-access article distributed under the terms of the Creative Commons Attribution License (CC BY). The use, distribution or reproduction in other forums is permitted, provided the original author(s) and the copyright owner(s) are credited and that the original publication in this journal is cited, in accordance with accepted academic practice. No use, distribution or reproduction is permitted which does not comply with these terms.

*Correspondence: Yunlu Liu, [email protected] ; Yushi Hu, [email protected] ; Benxiang He, [email protected]

† These authors have contributed equally to this work and share first authorship

This article is part of the Research Topic

Women in Ethnopharmacology: 2023