Information provision for stroke survivors and their carers.

A stroke is a sudden loss of brain function caused by lack of blood supply. Stroke can lead to death or physical and cognitive impairment and can have long lasting psychological and social implications. Research shows that stroke survivors and their families are dissatisfied with the information provided and have a poor understanding of stroke and associated issues. The primary objective is to assess the effects of active or passive information provision for stroke survivors (people with a clinical diagnosis of stroke or transient ischaemic attack (TIA)) or their identified carers. The primary outcomes are knowledge about stroke and stroke services, and anxiety. We updated our searches of the Cochrane Stroke Group Specialised Register on 28 September 2020 and for the following databases to May/June 2019: the Cochrane Central Register of Controlled Trials (CENTRAL; 2019, Issue 5) and the Cochrane Database of Systematic Reviews (CDSR; 2019, Issue 5) in the Cochrane Library (searched 31 May 2019), MEDLINE Ovid (searched 2005 to May week 4, 2019), Embase Ovid (searched 2005 to 29 May 2019), CINAHL EBSCO (searched 2005 to 6 June 2019), and five others. We searched seven study registers and checked reference lists of reviews. Randomised trials involving stroke survivors, their identified carers or both, where an information intervention was compared with standard care, or where information and another therapy were compared with the other therapy alone, or where the comparison was between active and passive information provision without other differences in treatment. Two review authors independently assessed trial eligibility and risk of bias, and extracted data. We categorised interventions as either active information provision or passive information provision: active information provision included active participation with subsequent opportunities for clarification and reinforcement; passive information provision provided no systematic follow-up or reinforcement procedure. We stratified analyses by this categorisation. We used GRADE methods to assess the overall certainty of the evidence. We have added 12 new studies in this update. This review now includes 33 studies involving 5255 stroke-survivor and 3134 carer participants. Twenty-two trials evaluated active information provision interventions and 11 trials evaluated passive information provision interventions. Most trials were at high risk of bias due to lack of blinding of participants, personnel, and outcome assessors where outcomes were self-reported. Fewer than half of studies were at low risk of bias regarding random sequence generation, concealment of allocation, incomplete outcome data or selective reporting. The following estimates have low certainty, based on the quality of evidence, unless stated otherwise. Accounting for certainty and size of effect, analyses suggested that for stroke survivors, active information provision may improve stroke-related knowledge (standardised mean difference (SMD) 0.41, 95% confidence interval (CI) 0.17 to 0.65; 3 studies, 275 participants), may reduce cases of anxiety and depression slightly (anxiety risk ratio (RR) 0.85, 95% CI 0.68 to 1.06; 5 studies, 1132 participants; depression RR 0.83, 95% CI 0.68 to 1.01; 6 studies, 1315 participants), may reduce Hospital Anxiety and Depression Scale (HADS) anxiety score slightly, (mean difference (MD) -0.73, 95% CI -1.10 to -0.36; 6 studies, 1171 participants), probably reduces HADS depression score slightly (MD (rescaled from SMD) -0.8, 95% CI -1.27 to -0.34; 8 studies, 1405 participants; moderate-certainty evidence), and may improve each domain of the World Health Organization Quality of Life assessment short-form (WHOQOL-BREF) (physical, MD 11.5, 95% CI 7.81 to 15.27; psychological, MD 11.8, 95% CI 7.29 to 16.29; social, MD 5.8, 95% CI 0.84 to 10.84; environment, MD 7.0, 95% CI 3.00 to 10.94; 1 study, 60 participants). No studies evaluated positive mental well-being. For carers, active information provision may reduce HADS anxiety and depression scores slightly (MD for anxiety -0.40, 95% CI -1.51 to 0.70; 3 studies, 921 participants; MD for depression -0.30, 95% CI -1.53 to 0.92; 3 studies, 924 participants), may result in little to no difference in positive mental well-being assessed with Bradley's well-being questionnaire (MD -0.18, 95% CI -1.34 to 0.98; 1 study, 91 participants) and may result in little to no difference in quality of life assessed with a 0 to 100 visual analogue scale (MD 1.22, 95% CI -7.65 to 10.09; 1 study, 91 participants). The evidence is very uncertain (very low certainty) for the effects of active information provision on carers' stroke-related knowledge, and cases of anxiety and depression. For stroke survivors, passive information provision may slightly increase HADS anxiety and depression scores (MD for anxiety 0.67, 95% CI -0.37 to 1.71; MD for depression 0.39, 95% CI -0.61 to 1.38; 3 studies, 227 participants) and the evidence is very uncertain for the effects on stroke-related knowledge, quality of life, and cases of anxiety and depression. For carers, the evidence is very uncertain for the effects of passive information provision on stroke-related knowledge, and HADS anxiety and depression scores. No studies of passive information provision measured carer quality of life, or stroke-survivor or carer positive mental well-being. Active information provision may improve stroke-survivor knowledge and quality of life, and may reduce anxiety and depression. However, the reductions in anxiety and depression scores were small and may not be important. In contrast, providing information passively may slightly worsen stroke-survivor anxiety and depression scores, although again the importance of this is unclear. Evidence relating to carers and to other outcomes of passive information provision is generally very uncertain. Although the best way to provide information is still unclear, the evidence is better for strategies that actively involve stroke survivors and carers and include planned follow-up for clarification and reinforcement.

Crocker TF ，Brown L ，Lam N ，Wray F ，Knapp P ，Forster A ... -  《Cochrane Database of Systematic Reviews》

Information or education interventions for adult intensive care unit (ICU) patients and their carers.

Lewis SR ，Pritchard MW ，Schofield-Robinson OJ ，Evans DJ ，Alderson P ，Smith AF ... -  《Cochrane Database of Systematic Reviews》

Folic acid supplementation and malaria susceptibility and severity among people taking antifolate antimalarial drugs in endemic areas.

Description of the condition Malaria, an infectious disease transmitted by the bite of female mosquitoes from several Anopheles species, occurs in 87 countries with ongoing transmission (WHO 2020). The World Health Organization (WHO) estimated that, in 2019, approximately 229 million cases of malaria occurred worldwide, with 94% occurring in the WHO's African region (WHO 2020). Of these malaria cases, an estimated 409,000 deaths occurred globally, with 67% occurring in children under five years of age (WHO 2020). Malaria also negatively impacts the health of women during pregnancy, childbirth, and the postnatal period (WHO 2020). Sulfadoxine/pyrimethamine (SP), an antifolate antimalarial, has been widely used across sub-Saharan Africa as the first-line treatment for uncomplicated malaria since it was first introduced in Malawi in 1993 (Filler 2006). Due to increasing resistance to SP, in 2000 the WHO recommended that one of several artemisinin-based combination therapies (ACTs) be used instead of SP for the treatment of uncomplicated malaria caused by Plasmodium falciparum (Global Partnership to Roll Back Malaria 2001). However, despite these recommendations, SP continues to be advised for intermittent preventive treatment in pregnancy (IPTp) and intermittent preventive treatment in infants (IPTi), whether the person has malaria or not (WHO 2013). Description of the intervention Folate (vitamin B9) includes both naturally occurring folates and folic acid, the fully oxidized monoglutamic form of the vitamin, used in dietary supplements and fortified food. Folate deficiency (e.g. red blood cell (RBC) folate concentrations of less than 305 nanomoles per litre (nmol/L); serum or plasma concentrations of less than 7 nmol/L) is common in many parts of the world and often presents as megaloblastic anaemia, resulting from inadequate intake, increased requirements, reduced absorption, or abnormal metabolism of folate (Bailey 2015; WHO 2015a). Pregnant women have greater folate requirements; inadequate folate intake (evidenced by RBC folate concentrations of less than 400 nanograms per millilitre (ng/mL), or 906 nmol/L) prior to and during the first month of pregnancy increases the risk of neural tube defects, preterm delivery, low birthweight, and fetal growth restriction (Bourassa 2019). The WHO recommends that all women who are trying to conceive consume 400 micrograms (µg) of folic acid daily from the time they begin trying to conceive through to 12 weeks of gestation (WHO 2017). In 2015, the WHO added the dosage of 0.4 mg of folic acid to the essential drug list (WHO 2015c). Alongside daily oral iron (30 mg to 60 mg elemental iron), folic acid supplementation is recommended for pregnant women to prevent neural tube defects, maternal anaemia, puerperal sepsis, low birthweight, and preterm birth in settings where anaemia in pregnant women is a severe public health problem (i.e. where at least 40% of pregnant women have a blood haemoglobin (Hb) concentration of less than 110 g/L). How the intervention might work Potential interactions between folate status and malaria infection The malaria parasite requires folate for survival and growth; this has led to the hypothesis that folate status may influence malaria risk and severity. In rhesus monkeys, folate deficiency has been found to be protective against Plasmodium cynomolgi malaria infection, compared to folate-replete animals (Metz 2007). Alternatively, malaria may induce or exacerbate folate deficiency due to increased folate utilization from haemolysis and fever. Further, folate status measured via RBC folate is not an appropriate biomarker of folate status in malaria-infected individuals since RBC folate values in these individuals are indicative of both the person's stores and the parasite's folate synthesis. A study in Nigeria found that children with malaria infection had significantly higher RBC folate concentrations compared to children without malaria infection, but plasma folate levels were similar (Bradley-Moore 1985). Why it is important to do this review The malaria parasite needs folate for survival and growth in humans. For individuals, adequate folate levels are critical for health and well-being, and for the prevention of anaemia and neural tube defects. Many countries rely on folic acid supplementation to ensure adequate folate status in at-risk populations. Different formulations for folic acid supplements are available in many international settings, with dosages ranging from 400 µg to 5 mg. Evaluating folic acid dosage levels used in supplementation efforts may increase public health understanding of its potential impacts on malaria risk and severity and on treatment failures. Examining folic acid interactions with antifolate antimalarial medications and with malaria disease progression may help countries in malaria-endemic areas determine what are the most appropriate lower dose folic acid formulations for at-risk populations. The WHO has highlighted the limited evidence available and has indicated the need for further research on biomarkers of folate status, particularly interactions between RBC folate concentrations and tuberculosis, human immunodeficiency virus (HIV), and antifolate antimalarial drugs (WHO 2015b). An earlier Cochrane Review assessed the effects and safety of iron supplementation, with or without folic acid, in children living in hyperendemic or holoendemic malaria areas; it demonstrated that iron supplementation did not increase the risk of malaria, as indicated by fever and the presence of parasites in the blood (Neuberger 2016). Further, this review stated that folic acid may interfere with the efficacy of SP; however, the efficacy and safety of folic acid supplementation on these outcomes has not been established. This review will provide evidence on the effectiveness of daily folic acid supplementation in healthy and malaria-infected individuals living in malaria-endemic areas. Additionally, it will contribute to achieving both the WHO Global Technical Strategy for Malaria 2016-2030 (WHO 2015d), and United Nations Sustainable Development Goal 3 (to ensure healthy lives and to promote well-being for all of all ages) (United Nations 2021), and evaluating whether the potential effects of folic acid supplementation, at different doses (e.g. 0.4 mg, 1 mg, 5 mg daily), interferes with the effect of drugs used for prevention or treatment of malaria. To examine the effects of folic acid supplementation, at various doses, on malaria susceptibility (risk of infection) and severity among people living in areas with various degrees of malaria endemicity. We will examine the interaction between folic acid supplements and antifolate antimalarial drugs. Specifically, we will aim to answer the following. Among uninfected people living in malaria endemic areas, who are taking or not taking antifolate antimalarials for malaria prophylaxis, does taking a folic acid-containing supplement increase susceptibility to or severity of malaria infection? Among people with malaria infection who are being treated with antifolate antimalarials, does folic acid supplementation increase the risk of treatment failure? Criteria for considering studies for this review Types of studies Inclusion criteria Randomized controlled trials (RCTs) Quasi-RCTs with randomization at the individual or cluster level conducted in malaria-endemic areas (areas with ongoing, local malaria transmission, including areas approaching elimination, as listed in the World Malaria Report 2020) (WHO 2020) Exclusion criteria Ecological studies Observational studies In vivo/in vitro studies Economic studies Systematic literature reviews and meta-analyses (relevant systematic literature reviews and meta-analyses will be excluded but flagged for grey literature screening) Types of participants Inclusion criteria Individuals of any age or gender, living in a malaria endemic area, who are taking antifolate antimalarial medications (including but not limited to sulfadoxine/pyrimethamine (SP), pyrimethamine-dapsone, pyrimethamine, chloroquine and proguanil, cotrimoxazole) for the prevention or treatment of malaria (studies will be included if more than 70% of the participants live in malaria-endemic regions) Studies assessing participants with or without anaemia and with or without malaria parasitaemia at baseline will be included Exclusion criteria Individuals not taking antifolate antimalarial medications for prevention or treatment of malaria Individuals living in non-malaria endemic areas Types of interventions Inclusion criteria Folic acid supplementation Form: in tablet, capsule, dispersible tablet at any dose, during administration, or periodically Timing: during, before, or after (within a period of four to six weeks) administration of antifolate antimalarials Iron-folic acid supplementation Folic acid supplementation in combination with co-interventions that are identical between the intervention and control groups. Co-interventions include: anthelminthic treatment; multivitamin or multiple micronutrient supplementation; 5-methyltetrahydrofolate supplementation. Exclusion criteria Folate through folate-fortified water Folic acid administered through large-scale fortification of rice, wheat, or maize Comparators Placebo No treatment No folic acid/different doses of folic acid Iron Types of outcome measures Primary outcomes Uncomplicated malaria (defined as a history of fever with parasitological confirmation; acceptable parasitological confirmation will include rapid diagnostic tests (RDTs), malaria smears, or nucleic acid detection (i.e. polymerase chain reaction (PCR), loop-mediated isothermal amplification (LAMP), etc.)) (WHO 2010). This outcome is relevant for patients without malaria, given antifolate antimalarials for malaria prophylaxis. Severe malaria (defined as any case with cerebral malaria or acute P. falciparum malaria, with signs of severity or evidence of vital organ dysfunction, or both) (WHO 2010). This outcome is relevant for patients without malaria, given antifolate antimalarials for malaria prophylaxis. Parasite clearance (any Plasmodium species), defined as the time it takes for a patient who tests positive at enrolment and is treated to become smear-negative or PCR negative. This outcome is relevant for patients with malaria, treated with antifolate antimalarials. Treatment failure (defined as the inability to clear malaria parasitaemia or prevent recrudescence after administration of antimalarial medicine, regardless of whether clinical symptoms are resolved) (WHO 2019). This outcome is relevant for patients with malaria, treated with antifolate antimalarials. Secondary outcomes Duration of parasitaemia Parasite density Haemoglobin (Hb) concentrations (g/L) Anaemia: severe anaemia (defined as Hb less than 70 g/L in pregnant women and children aged six to 59 months; and Hb less than 80 g/L in other populations); moderate anaemia (defined as Hb less than 100 g/L in pregnant women and children aged six to 59 months; and less than 110 g/L in others) Death from any cause Among pregnant women: stillbirth (at less than 28 weeks gestation); low birthweight (less than 2500 g); active placental malaria (defined as Plasmodium detected in placental blood by smear or PCR, or by Plasmodium detected on impression smear or placental histology). Search methods for identification of studies A search will be conducted to identify completed and ongoing studies, without date or language restrictions. Electronic searches A search strategy will be designed to include the appropriate subject headings and text word terms related to each intervention of interest and study design of interest (see Appendix 1). Searches will be broken down by these two criteria (intervention of interest and study design of interest) to allow for ease of prioritization, if necessary. The study design filters recommended by the Scottish Intercollegiate Guidelines Network (SIGN), and those designed by Cochrane for identifying clinical trials for MEDLINE and Embase, will be used (SIGN 2020). There will be no date or language restrictions. Non-English articles identified for inclusion will be translated into English. If translations are not possible, advice will be requested from the Cochrane Infectious Diseases Group and the record will be stored in the "Awaiting assessment" section of the review until a translation is available. The following electronic databases will be searched for primary studies. Cochrane Central Register of Controlled Trials. Cumulative Index to Nursing and Allied Health Literature (CINAHL). Embase. MEDLINE. Scopus. Web of Science (both the Social Science Citation Index and the Science Citation Index). We will conduct manual searches of ClinicalTrials.gov, the International Clinical Trials Registry Platform (ICTRP), and the United Nations Children's Fund (UNICEF) Evaluation and Research Database (ERD), in order to identify relevant ongoing or planned trials, abstracts, and full-text reports of evaluations, studies, and surveys related to programmes on folic acid supplementation in malaria-endemic areas. Additionally, manual searches of grey literature to identify RCTs that have not yet been published but are potentially eligible for inclusion will be conducted in the following sources. Global Index Medicus (GIM). African Index Medicus (AIM). Index Medicus for the Eastern Mediterranean Region (IMEMR). Latin American & Caribbean Health Sciences Literature (LILACS). Pan American Health Organization (PAHO). Western Pacific Region Index Medicus (WPRO). Index Medicus for the South-East Asian Region (IMSEAR). The Spanish Bibliographic Index in Health Sciences (IBECS) (ibecs.isciii.es/). Indian Journal of Medical Research (IJMR) (journals.lww.com/ijmr/pages/default.aspx). Native Health Database (nativehealthdatabase.net/). Scielo (www.scielo.br/). Searching other resources Handsearches of the five journals with the highest number of included studies in the last 12 months will be conducted to capture any relevant articles that may not have been indexed in the databases at the time of the search. We will contact the authors of included studies and will check reference lists of included papers for the identification of additional records. For assistance in identifying ongoing or unpublished studies, we will contact the Division of Nutrition, Physical Activity, and Obesity (DNPAO) and the Division of Parasitic Diseases and Malaria (DPDM) of the CDC, the United Nations World Food Programme (WFP), Nutrition International (NI), Global Alliance for Improved Nutrition (GAIN), and Hellen Keller International (HKI). Data collection and analysis Selection of studies Two review authors will independently screen the titles and abstracts of articles retrieved by each search to assess eligibility, as determined by the inclusion and exclusion criteria. Studies deemed eligible for inclusion by both review authors in the abstract screening phase will advance to the full-text screening phase, and full-text copies of all eligible papers will be retrieved. If full articles cannot be obtained, we will attempt to contact the authors to obtain further details of the studies. If such information is not obtained, we will classify the study as "awaiting assessment" until further information is published or made available to us. The same two review authors will independently assess the eligibility of full-text articles for inclusion in the systematic review. If any discrepancies occur between the studies selected by the two review authors, a third review author will provide arbitration. Each trial will be scrutinized to identify multiple publications from the same data set, and the justification for excluded trials will be documented. A PRISMA flow diagram of the study selection process will be presented to provide information on the number of records identified in the literature searches, the number of studies included and excluded, and the reasons for exclusion (Moher 2009). The list of excluded studies, along with their reasons for exclusion at the full-text screening phase, will also be created. Data extraction and management Two review authors will independently extract data for the final list of included studies using a standardized data specification form. Discrepancies observed between the data extracted by the two authors will be resolved by involving a third review author and reaching a consensus. Information will be extracted on study design components, baseline participant characteristics, intervention characteristics, and outcomes. For individually randomized trials, we will record the number of participants experiencing the event and the number analyzed in each treatment group or the effect estimate reported (e.g. risk ratio (RR)) for dichotomous outcome measures. For count data, we will record the number of events and the number of person-months of follow-up in each group. If the number of person-months is not reported, the product of the duration of follow-up and the number of children evaluated will be used to estimate this figure. We will calculate the rate ratio and standard error (SE) for each study. Zero events will be replaced by 0.5. We will extract both adjusted and unadjusted covariate incidence rate ratios if they are reported in the original studies. For continuous data, we will extract means (arithmetic or geometric) and a measure of variance (standard deviation (SD), SE, or confidence interval (CI)), percentage or mean change from baseline, and the numbers analyzed in each group. SDs will be computed from SEs or 95% CIs, assuming a normal distribution of the values. Haemoglobin values in g/dL will be calculated by multiplying haematocrit or packed cell volume values by 0.34, and studies reporting haemoglobin values in g/dL will be converted to g/L. In cluster-randomized trials, we will record the unit of randomization (e.g. household, compound, sector, or village), the number of clusters in the trial, and the average cluster size. The statistical methods used to analyze the trials will be documented, along with details describing whether these methods adjusted for clustering or other covariates. We plan to extract estimates of the intra-cluster correlation coefficient (ICC) for each outcome. Where results are adjusted for clustering, we will extract the treatment effect estimate and the SD or CI. If the results are not adjusted for clustering, we will extract the data reported. Assessment of risk of bias in included studies Two review authors (KSC, LFY) will independently assess the risk of bias for each included trial using the Cochrane 'Risk of bias 2' tool (RoB 2) for randomized studies (Sterne 2019). Judgements about the risk of bias of included studies will be made according to the recommendations outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021). Disagreements will be resolved by discussion, or by involving a third review author. The interest of our review will be to assess the effect of assignment to the interventions at baseline. We will evaluate each primary outcome using the RoB2 tool. The five domains of the Cochrane RoB2 tool include the following. Bias arising from the randomization process. Bias due to deviations from intended interventions. Bias due to missing outcome data. Bias in measurement of the outcome. Bias in selection of the reported result. Each domain of the RoB2 tool comprises the following. A series of 'signalling' questions. A judgement about the risk of bias for the domain, facilitated by an algorithm that maps responses to the signalling questions to a proposed judgement. Free-text boxes to justify responses to the signalling questions and 'Risk of bias' judgements. An option to predict (and explain) the likely direction of bias. Responses to signalling questions elicit information relevant to an assessment of the risk of bias. These response options are as follows. Yes (may indicate either low or high risk of bias, depending on the most natural way to ask the question). Probably yes. Probably no. No. No information (may indicate no evidence of that problem or an absence of information leading to concerns about there being a problem). Based on the answer to the signalling question, a 'Risk of bias' judgement is assigned to each domain. These judgements include one of the following. High risk of bias Low risk of bias Some concerns To generate the risk of bias judgement for each domain in the randomized studies, we will use the Excel template, available at www.riskofbias.info/welcome/rob-2-0-tool/current-version-of-rob-2. This file will be stored on a scientific data website, available to readers. Risk of bias in cluster randomized controlled trials For the cluster randomized trials, we will be using the RoB2 tool to analyze the five standard domains listed above along with Domain 1b (bias arising from the timing of identification or recruitment of participants) and its related signalling questions. To generate the risk of bias judgement for each domain in the cluster RCTs, we will use the Excel template available at https://sites.google.com/site/riskofbiastool/welcome/rob-2-0-tool/rob-2-for-cluster-randomized-trials. This file will be stored on a scientific data website, available to readers. Risk of bias in cross-over randomized controlled trials For cross-over randomized trials, we will be using the RoB2 tool to analyze the five standard domains listed above along with Domain 2 (bias due to deviations from intended interventions), and Domain 3 (bias due to missing outcome data), and their respective signalling questions. To generate the risk of bias judgement for each domain in the cross-over RCTs, we will use the Excel template, available at https://sites.google.com/site/riskofbiastool/welcome/rob-2-0-tool/rob-2-for-crossover-trials, for each risk of bias judgement of cross-over randomized studies. This file will be stored on a scientific data website, available to readers. Overall risk of bias The overall 'Risk of bias' judgement for each specific trial being assessed will be based on each domain-level judgement. The overall judgements include the following. Low risk of bias (the trial is judged to be at low risk of bias for all domains). Some concerns (the trial is judged to raise some concerns in at least one domain but is not judged to be at high risk of bias for any domain). High risk of bias (the trial is judged to be at high risk of bias in at least one domain, or is judged to have some concerns for multiple domains in a way that substantially lowers confidence in the result). The 'risk of bias' assessments will inform our GRADE evaluations of the certainty of evidence for our primary outcomes presented in the 'Summary of findings' tables and will also be used to inform the sensitivity analyses; (see Sensitivity analysis). If there is insufficient information in study reports to enable an assessment of the risk of bias, studies will be classified as "awaiting assessment" until further information is published or made available to us. Measures of treatment effect Dichotomous data For dichotomous data, we will present proportions and, for two-group comparisons, results as average RR or odds ratio (OR) with 95% CIs. Ordered categorical data Continuous data We will report results for continuous outcomes as the mean difference (MD) with 95% CIs, if outcomes are measured in the same way between trials. Where some studies have reported endpoint data and others have reported change-from-baseline data (with errors), we will combine these in the meta-analysis, if the outcomes were reported using the same scale. We will use the standardized mean difference (SMD), with 95% CIs, to combine trials that measured the same outcome but used different methods. If we do not find three or more studies for a pooled analysis, we will summarize the results in a narrative form. Unit of analysis issues Cluster-randomized trials We plan to combine results from both cluster-randomized and individually randomized studies, providing there is little heterogeneity between the studies. If the authors of cluster-randomized trials conducted their analyses at a different level from that of allocation, and they have not appropriately accounted for the cluster design in their analyses, we will calculate the trials' effective sample sizes to account for the effect of clustering in data. When one or more cluster-RCT reports RRs adjusted for clustering, we will compute cluster-adjusted SEs for the other trials. When none of the cluster-RCTs provide cluster-adjusted RRs, we will adjust the sample size for clustering. We will divide, by the estimated design effects (DE), the number of events and number evaluated for dichotomous outcomes and the number evaluated for continuous outcomes, where DE = 1 + ((average cluster size 1) * ICC). The derivation of the estimated ICCs and DEs will be reported. We will utilize the intra-cluster correlation coefficient (ICC), derived from the trial (if available), or from another source (e.g., using the ICCs derived from other, similar trials) and then calculate the design effect with the formula provided in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021). If this approach is used, we will report it and undertake sensitivity analysis to investigate the effect of variations in ICC. Studies with more than two treatment groups If we identify studies with more than two intervention groups (multi-arm studies), where possible we will combine groups to create a single pair-wise comparison or use the methods set out in the Cochrane Handbook to avoid double counting study participants (Higgins 2021). For the subgroup analyses, when the control group was shared by two or more study arms, we will divide the control group (events and total population) over the number of relevant subgroups to avoid double counting the participants. Trials with several study arms can be included more than once for different comparisons. Cross-over trials From cross-over trials, we will consider the first period of measurement only and will analyze the results together with parallel-group studies. Multiple outcome events In several outcomes, a participant might experience more than one outcome event during the trial period. For all outcomes, we will extract the number of participants with at least one event. Dealing with missing data We will contact the trial authors if the available data are unclear, missing, or reported in a format that is different from the format needed. We aim to perform a 'per protocol' or 'as observed' analysis; otherwise, we will perform a complete case analysis. This means that for treatment failure, we will base the analyses on the participants who received treatment and the number of participants for which there was an inability to clear malarial parasitaemia or prevent recrudescence after administration of an antimalarial medicine reported in the studies. Assessment of heterogeneity Heterogeneity in the results of the trials will be assessed by visually examining the forest plot to detect non-overlapping CIs, using the Chi2 test of heterogeneity (where a P value of less than 0.1 indicates statistical significance) and the I2 statistic of inconsistency (with a value of greater than 50% denoting moderate levels of heterogeneity). When statistical heterogeneity is present, we will investigate the reasons for it, using subgroup analysis. Assessment of reporting biases We will construct a funnel plot to assess the effect of small studies for the main outcome (when including more than 10 trials). Data synthesis The primary analysis will include all eligible studies that provide data regardless of the overall risk of bias as assessed by the RoB2 tool. Analyses will be conducted using Review Manager 5.4 (Review Manager 2020). Cluster-RCTs will be included in the main analysis after adjustment for clustering (see the previous section on cluster-RCTs). The meta-analysis will be performed using the Mantel-Haenszel random-effects model or the generic inverse variance method (when adjustment for clustering is performed by adjusting SEs), as appropriate. Subgroup analysis and investigation of heterogeneity The overall risk of bias will not be used as the basis in conducting our subgroup analyses. However, where data are available, we plan to conduct the following subgroup analyses, independent of heterogeneity. Dose of folic acid supplementation: higher doses (4 mg or more, daily) versus lower doses (less than 4 mg, daily). Moderate-severe anaemia at baseline (mean haemoglobin of participants in a trial at baseline below 100 g/L for pregnant women and children aged six to 59 months, and below 110 g/L for other populations) versus normal at baseline (mean haemoglobin above 100 g/L for pregnant women and children aged six to 59 months, and above 110 g/L for other populations). Antimalarial drug resistance to parasite: known resistance versus no resistance versus unknown/mixed/unreported parasite resistance. Folate status at baseline: Deficient (e.g. RBC folate concentration of less than 305 nmol/L, or serum folate concentration of less than 7nmol/L) and Insufficient (e.g. RBC folate concentration from 305 to less than 906 nmol/L, or serum folate concentration from 7 to less than 25 nmol/L) versus Sufficient (e.g. RBC folate concentration above 906 nmol/L, or serum folate concentration above 25 nmol/L). Presence of anaemia at baseline: yes versus no. Mandatory fortification status: yes, versus no (voluntary or none). We will only use the primary outcomes in any subgroup analyses, and we will limit subgroup analyses to those outcomes for which three or more trials contributed data. Comparisons between subgroups will be performed using Review Manager 5.4 (Review Manager 2020). Sensitivity analysis We will perform a sensitivity analysis, using the risk of bias as a variable to explore the robustness of the findings in our primary outcomes. We will verify the behaviour of our estimators by adding and removing studies with a high risk of bias overall from the analysis. That is, studies with a low risk of bias versus studies with a high risk of bias. Summary of findings and assessment of the certainty of the evidence For the assessment across studies, we will use the GRADE approach, as outlined in (Schünemann 2021). We will use the five GRADE considerations (study limitations based on RoB2 judgements, consistency of effect, imprecision, indirectness, and publication bias) to assess the certainty of the body of evidence as it relates to the studies which contribute data to the meta-analyses for the primary outcomes. The GRADEpro Guideline Development Tool (GRADEpro) will be used to import data from Review Manager 5.4 (Review Manager 2020) to create 'Summary of Findings' tables. The primary outcomes for the main comparison will be listed with estimates of relative effects, along with the number of participants and studies contributing data for those outcomes. These tables will provide outcome-specific information concerning the overall certainty of evidence from studies included in the comparison, the magnitude of the effect of the interventions examined, and the sum of available data on the outcomes we considered. We will include only primary outcomes in the summary of findings tables. For each individual outcome, two review authors (KSC, LFY) will independently assess the certainty of the evidence using the GRADE approach (Balshem 2011). For assessments of the overall certainty of evidence for each outcome that includes pooled data from included trials, we will downgrade the evidence from 'high certainty' by one level for serious (or by two for very serious) study limitations (risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates, or potential publication bias).

Crider K ，Williams J ，Qi YP ，Gutman J ，Yeung L ，Mai C ，Finkelstain J ，Mehta S ，Pons-Duran C ，Menéndez C ，Moraleda C ，Rogers L ，Daniels K ，Green P ... -  《Cochrane Database of Systematic Reviews》

Information provision for stroke patients and their caregivers.

Forster A ，Brown L ，Smith J ，House A ，Knapp P ，Wright JJ ，Young J ... -  《-》

Psychosocial interventions for preventing and treating depression in dialysis patients.

People with end-stage kidney disease (ESKD) treated with dialysis are frequently affected by major depression. Dialysis patients have prioritised depression as a critically important clinical outcome in nephrology trials. Psychological and social support are potential treatments for depression, although a Cochrane review in 2005 identified zero eligible studies. This is an update of the Cochrane review first published in 2005. To assess the effect of using psychosocial interventions versus usual care or a second psychosocial intervention for preventing and treating depression in patients with ESKD treated with dialysis. We searched Cochrane Kidney and Transplant's Register of Studies up to 21 June 2019 through contact with the Information Specialist using search terms relevant to this review. Studies in the Register are identified through searches of CENTRAL, MEDLINE, and EMBASE, conference proceedings, the International Clinical Trials Register (ICTRP) Search Portal and ClinicalTrials.gov. We included randomised controlled trials (RCTs) and quasi-RCTs of psychosocial interventions for prevention and treatment of depression among adults treated with long-term dialysis. We assessed effects of interventions on changes in mental state (depression, anxiety, cognition), suicide, health-related quality of life (HRQoL), withdrawal from dialysis treatment, withdrawal from intervention, death (any cause), hospitalisation and adverse events. Two authors independently selected studies for inclusion and extracted study data. We applied the Cochrane 'Risk of Bias' tool and used the GRADE process to assess evidence certainty. We estimated treatment effects using random-effects meta-analysis. Results for continuous outcomes were expressed as a mean difference (MD) or as a standardised mean difference (SMD) when investigators used different scales. Dichotomous outcomes were expressed as risk ratios. All estimates were reported together with 95% confidence intervals (CI). We included 33 studies enrolling 2056 participants. Twenty-six new studies were added to this 2019 update. Seven studies originally excluded from the 2005 review were included as they met the updated review eligibility criteria, which have been expanded to include RCTs in which participants did not meet criteria for depression as an inclusion criterion. Psychosocial interventions included acupressure, cognitive-behavioural therapy, counselling, education, exercise, meditation, motivational interviewing, relaxation techniques, social activity, spiritual practices, support groups, telephone support, visualisation, and voice-recording of a psychological intervention. The duration of study follow-up ranged between three weeks and one year. Studies included between nine and 235 participants. The mean study age ranged between 36.1 and 73.9 years. Random sequence generation and allocation concealment were at low risk of bias in eight and one studies respectively. One study reported low risk methods for blinding of participants and investigators, and outcome assessment was blinded in seven studies. Twelve studies were at low risk of attrition bias, eight studies were at low risk of selective reporting bias, and 21 studies were at low risk of other potential sources of bias. Cognitive behavioural therapy probably improves depressive symptoms measured using the Beck Depression Inventory (4 studies, 230 participants: MD -6.10, 95% CI -8.63 to -3.57), based on moderate certainty evidence. Cognitive behavioural therapy compared to usual care probably improves HRQoL measured either with the Kidney Disease Quality of Life Instrument Short Form or the Quality of Life Scale, with a 0.5 standardised mean difference representing a moderate effect size (4 studies, 230 participants: SMD 0.51, 95% CI 0.19 to 0.83) , based on moderate certainty evidence. Cognitive behavioural therapy may reduce major depression symptoms (one study) and anxiety, and increase self-efficacy (one study). Cognitive behavioural therapy studies did not report hospitalisation. We found low-certainty evidence that counselling may slightly reduce depressive symptoms measured with the Beck Depression Inventory (3 studies, 99 participants: MD -3.84, 95% CI -6.14 to -1.53) compared to usual care. Counselling reported no difference in HRQoL (one study). Counselling studies did not measure risk of major depression, suicide, or hospitalisation. Exercise may reduce or prevent major depression (3 studies, 108 participants: RR 0.47, 95% CI 0.27 to 0.81), depression of any severity (3 studies, 108 participants: RR 0.69, 95% CI 0.54 to 0.87) and improve HRQoL measured with Quality of Life Index score (2 studies, 64 participants: MD 3.06, 95% CI 2.29 to 3.83) compared to usual care with low certainty. With moderate certainty, exercise probably improves depression symptoms measured with the Beck Depression Inventory (3 studies, 108 participants: MD -7.61, 95% CI -9.59 to -5.63). Exercise may reduce anxiety (one study). No exercise studies measured suicide risk or withdrawal from dialysis. We found moderate-certainty evidence that relaxation techniques probably reduce depressive symptoms measured with the Beck Depression Inventory (2 studies, 122 participants: MD -5.77, 95% CI -8.76 to -2.78). Relaxation techniques reported no difference in HRQoL (one study). Relaxation studies did not measure risk of major depression or suicide. Spiritual practices have uncertain effects on depressive symptoms measured either with the Beck Depression Inventory or the Brief Symptom Inventory (2 studies, 116 participants: SMD -1.00, 95% CI -3.52 to 1.53; very low certainty evidence). No differences between spiritual practices and usual care were reported on anxiety (one study), and HRQoL (one study). No study of spiritual practices evaluated effects on suicide risk, withdrawal from dialysis or hospitalisation. There were few or no data on acupressure, telephone support, meditation and adverse events related to psychosocial interventions. Cognitive behavioural therapy, exercise or relaxation techniques probably reduce depressive symptoms (moderate-certainty evidence) for adults with ESKD treated with dialysis. Cognitive behavioural therapy probably increases health-related quality of life. Evidence for spiritual practices, acupressure, telephone support, and meditation is of low certainty . Similarly, evidence for effects of psychosocial interventions on suicide risk, major depression, hospitalisation, withdrawal from dialysis, and adverse events is of low or very low certainty.

Natale P ，Palmer SC ，Ruospo M ，Saglimbene VM ，Rabindranath KS ，Strippoli GF ... -  《Cochrane Database of Systematic Reviews》