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Cochrane Database of Systematic Reviews
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Perceptions and experiences of the prevention, detection, and management of postpartum haemorrhage: a qualitative evidence synthesis.
Postpartum haemorrhage (PPH), defined as blood loss of 500 mL or more after childbirth, is the leading cause of maternal mortality worldwide. It is possible to prevent complications of PPH with timely and appropriate detection and management. However, implementing the best methods of PPH prevention, detection and management can be challenging, particularly in low- and middle-income countries. Our overall objective was to explore the perceptions and experiences of women, community members, lay health workers, and skilled healthcare providers who have experience with PPH or with preventing, detecting, and managing PPH, in community or health facility settings. We searched MEDLINE, CINAHL, Scopus, and grey literature on 13 November 2022 with no language restrictions. We then performed reference checking and forward citation searching of the included studies. We included qualitative studies and mixed-methods studies with an identifiable qualitative component. We included studies that explored perceptions and experiences of PPH prevention, detection, and management among women, community members, traditional birth attendants, healthcare providers, and managers. We used three-stage maximum variation sampling to ensure diversity in terms of relevance of the study to the review objectives, richness of data, and coverage of critical contextual elements: setting (region, country income level), perspective (type of participant), and topic (prevention, detection, management). We extracted data using a data extraction form designed for this review. We used thematic synthesis to analyse and synthesise the evidence, and we used the GRADE-CERQual (Confidence in the Evidence from Reviews of Qualitative research) approach to assess our confidence in each finding. To identify factors that may influence intervention implementation, we mapped each review finding to the Theoretical Domains Framework (TDF) and the Capability, Motivation, and Opportunity model of Behaviour change (COM-B). We used the Behaviour Change Wheel to explore implications for practice. We included 67 studies and sampled 43 studies for our analysis. Most were from low- or middle-income countries (33 studies), and most included the perspectives of women and health workers. We downgraded our confidence in several findings from high confidence to moderate, low, or very-low confidence, mainly due to concerns about how the studies were conducted (methodological limitations) or concerns about missing important perspectives from some types of participants or in some settings (relevance). In many communities, bleeding during and after childbirth is considered "normal" and necessary to expel "impurities" and restore and cleanse the woman's body after pregnancy and birth (moderate confidence). In some communities, people have misconceptions about causes of PPH or believe that PPH is caused by supernatural powers or evil spirits that punish women for ignoring or disobeying social rules or for past mistakes (high confidence). For women who give birth at home or in the community, female family members or traditional birth attendants are the first to recognise excess bleeding after birth (high confidence). Family members typically take the decision of whether and when to seek care if PPH is suspected, and these family members are often influenced by trusted traditional birth attendants or community midwives (high confidence). If PPH is identified for women birthing at home or in the community, decision-making about the subsequent referral and care pathway can be multifaceted and complex (high confidence). First responders to PPH are not always skilled or trained healthcare providers (high confidence). In health facilities, midwives may consider it easy to implement visual estimation of blood loss with a kidney dish or under-pad, but difficult to accurately interpret the amount of blood loss (very low confidence). Quantifying (rather than estimating) blood loss may be a complex and contentious change of practice for health workers (low confidence). Women who gave birth in health facilities and experienced PPH described it as painful, embarrassing, and traumatic. Partners or other family members also found the experience stressful. While some women were dissatisfied with their level of involvement in decision-making for PPH management, others felt health workers were best placed to make decisions (moderate confidence). Inconsistent availability of resources (drugs, medical supplies, blood) causes delays in the timely management of PPH (high confidence). There is limited availability of misoprostol in the community owing to stockouts, poor supply systems, and the difficulty of navigating misoprostol procurement for community health workers (moderate confidence). Health workers described working on the maternity ward as stressful and intense due to short staffing, long shifts, and the unpredictability of emergencies. Exhausted and overwhelmed staff may be unable to appropriately monitor all women, particularly when multiple women are giving birth simultaneously or on the floor of the health facility; this could lead to delays in detecting PPH (moderate confidence). Inadequate staffing, high turnover of skilled health workers, and appointment of lower-level cadres of health workers are key challenges to the provision of quality PPH care (high confidence). Through team-based simulation training, health workers of different cadres (doctors, midwives, lay health workers) can develop a shared mental model to help them work quickly, efficiently, and amicably as a team when managing women with PPH (moderate confidence). Our findings highlight how improving PPH prevention, detection, and management is underpinned by a complex system of interacting roles and behaviours (community, women, health workers of different types and with different experiences). Multiple individual, sociocultural, and environmental factors influence the decisions and behaviours of women, families, communities, health workers, and managers. It is crucial to consider the broader health and social systems when designing and implementing PPH interventions to change or influence these behaviours. We have developed a set of prompts that may help programme managers, policymakers, researchers, and other key stakeholders to identify and address factors that affect implementation and scale-up of interventions to improve PPH prevention, detection, and management.
被引量：2 发表：1970
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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).
被引量：- 发表：1970
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Provision and uptake of routine antenatal services: a qualitative evidence synthesis.
Antenatal care (ANC) is a core component of maternity care. However, both quality of care provision and rates of attendance vary widely between and within countries. Qualitative research can assess factors underlying variation, including acceptability, feasibility, and the values and beliefs that frame provision and uptake of ANC programmes.This synthesis links to the Cochrane Reviews of the effectiveness of different antenatal models of care. It was designed to inform the World Health Organization guidelines for a positive pregnancy experience and to provide insights for the design and implementation of improved antenatal care in the future. To identify, appraise, and synthesise qualitative studies exploring:· Women's views and experiences of attending ANC; and factors influencing the uptake of ANC arising from women's accounts;· Healthcare providers' views and experiences of providing ANC; and factors influencing the provision of ANC arising from the accounts of healthcare providers. To find primary studies we searched MEDLINE, Ovid; Embase, Ovid; CINAHL, EbscoHost; PsycINFO, EbscoHost; AMED, EbscoHost; LILACS, VHL; and African Journals Online (AJOL) from January 2000 to February 2019. We handsearched reference lists of included papers and checked the contents pages of 50 relevant journals through Zetoc alerts received during the searching phase. We included studies that used qualitative methodology and that met our quality threshold; that explored the views and experiences of routine ANC among healthy, pregnant and postnatal women or among healthcare providers offering this care, including doctors, midwives, nurses, lay health workers and traditional birth attendants; and that took place in any setting where ANC was provided.We excluded studies of ANC programmes designed for women with specific complications. We also excluded studies of programmes that focused solely on antenatal education. Two authors undertook data extraction, logged study characteristics, and assessed study quality. We used meta-ethnographic and Framework techniques to code and categorise study data. We developed findings from the data and presented these in a 'Summary of Qualitative Findings' (SoQF) table. We assessed confidence in each finding using GRADE-CERQual. We used these findings to generate higher-level explanatory thematic domains. We then developed two lines of argument syntheses, one from service user data, and one from healthcare provider data. In addition, we mapped the findings to relevant Cochrane effectiveness reviews to assess how far review authors had taken account of behavioural and organisational factors in the design and implementation of the interventions they tested. We also translated the findings into logic models to explain full, partial and no uptake of ANC, using the theory of planned behaviour. We include 85 studies in our synthesis. Forty-six studies explored the views and experiences of healthy pregnant or postnatal women, 17 studies explored the views and experiences of healthcare providers and 22 studies incorporated the views of both women and healthcare providers. The studies took place in 41 countries, including eight high-income countries, 18 middle-income countries and 15 low-income countries, in rural, urban and semi-urban locations. We developed 52 findings in total and organised these into three thematic domains: socio-cultural context (11 findings, five moderate- or high-confidence); service design and provision (24 findings, 15 moderate- or high-confidence); and what matters to women and staff (17 findings, 11 moderate- or high-confidence) The third domain was sub-divided into two conceptual areas; personalised supportive care, and information and safety. We also developed two lines of argument, using high- or moderate-confidence findings:For women, initial or continued use of ANC depends on a perception that doing so will be a positive experience. This is a result of the provision of good-quality local services that are not dependent on the payment of informal fees and that include continuity of care that is authentically personalised, kind, caring, supportive, culturally sensitive, flexible, and respectful of women's need for privacy, and that allow staff to take the time needed to provide relevant support, information and clinical safety for the woman and the baby, as and when they need it. Women's perceptions of the value of ANC depend on their general beliefs about pregnancy as a healthy or a risky state, and on their reaction to being pregnant, as well as on local socio-cultural norms relating to the advantages or otherwise of antenatal care for healthy pregnancies, and for those with complications. Whether they continue to use ANC or not depends on their experience of ANC design and provision when they access it for the first time.The capacity of healthcare providers to deliver the kind of high-quality, relationship-based, locally accessible ANC that is likely to facilitate access by women depends on the provision of sufficient resources and staffing as well as the time to provide flexible personalised, private appointments that are not overloaded with organisational tasks. Such provision also depends on organisational norms and values that overtly value kind, caring staff who make effective, culturally-appropriate links with local communities, who respect women's belief that pregnancy is usually a normal life event, but who can recognise and respond to complications when they arise. Healthcare providers also require sufficient training and education to do their job well, as well as an adequate salary, so that they do not need to demand extra informal funds from women and families, to supplement their income, or to fund essential supplies. This review has identified key barriers and facilitators to the uptake (or not) of ANC services by pregnant women, and in the provision (or not) of good-quality ANC by healthcare providers. It complements existing effectiveness reviews of models of ANC provision and adds essential insights into why a particular type of ANC provided in specific local contexts may or may not be acceptable, accessible, or valued by some pregnant women and their families/communities. Those providing and funding services should consider the three thematic domains identified by the review as a basis for service development and improvement. Such developments should include pregnant and postnatal women, community members and other relevant stakeholders.
被引量：70 发表：1970
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Interventions to reduce ambient particulate matter air pollution and their effect on health.
Ambient air pollution is associated with a large burden of disease in both high-income countries (HICs) and low- and middle-income countries (LMICs). To date, no systematic review has assessed the effectiveness of interventions aiming to reduce ambient air pollution. To assess the effectiveness of interventions to reduce ambient particulate matter air pollution in reducing pollutant concentrations and improving associated health outcomes. We searched a range of electronic databases with diverse focuses, including health and biomedical research (CENTRAL, Cochrane Public Health Group Specialised Register, MEDLINE, Embase, PsycINFO), multidisciplinary research (Scopus, Science Citation Index), social sciences (Social Science Citation Index), urban planning and environment (Greenfile), and LMICs (Global Health Library regional indexes, WHOLIS). Additionally, we searched grey literature databases, multiple online trial registries, references of included studies and the contents of relevant journals in an attempt to identify unpublished and ongoing studies, and studies not identified by our search strategy. The final search date for all databases was 31 August 2016. Eligible for inclusion were randomized and cluster randomized controlled trials, as well as several non-randomized study designs, including controlled interrupted time-series studies (cITS-EPOC), interrupted time-series studies adhering to EPOC standards (ITS-EPOC), interrupted time-series studies not adhering to EPOC standards (ITS), controlled before-after studies adhering to EPOC standards (CBA-EPOC), and controlled before-after studies not adhering to EPOC standards (CBA); these were classified as main studies. Additionally, we included uncontrolled before-after studies (UBA) as supporting studies. We included studies that evaluated interventions to reduce ambient air pollution from industrial, residential, vehicular and multiple sources, with respect to their effect on mortality, morbidity and several air pollutant concentrations. We did not restrict studies based on the population, setting or comparison. After a calibration exercise among the author team, two authors independently assessed studies for inclusion, extracted data and assessed risk of bias. We conducted data extraction, risk of bias assessment and evidence synthesis only for main studies; we mapped supporting studies with regard to the types of intervention and setting. To assess risk of bias, we used the Graphic Appraisal Tool for Epidemiological studies (GATE) for correlation studies, as modified and employed by the Centre for Public Health Excellence at the UK National Institute for Health and Care Excellence (NICE). For each intervention category, i.e. those targeting industrial, residential, vehicular and multiple sources, we synthesized evidence narratively, as well as graphically using harvest plots. We included 42 main studies assessing 38 unique interventions. These were heterogeneous with respect to setting; interventions were implemented in countries across the world, but most (79%) were implemented in HICs, with the remaining scattered across LMICs. Most interventions (76%) were implemented in urban or community settings.We identified a heterogeneous mix of interventions, including those aiming to address industrial (n = 5), residential (n = 7), vehicular (n = 22), and multiple sources (n = 4). Some specific interventions, such as low emission zones and stove exchanges, were assessed by several studies, whereas others, such as a wood burning ban, were only assessed by a single study.Most studies assessing health and air quality outcomes used routine monitoring data. Studies assessing health outcomes mostly investigated effects in the general population, while few studies assessed specific subgroups such as infants, children and the elderly. No identified studies assessed unintended or adverse effects.The judgements regarding the risk of bias of studies were mixed. Regarding health outcomes, we appraised eight studies (47%) as having no substantial risk of bias concerns, five studies (29%) as having some risk of bias concerns, and four studies (24%) as having serious risk of bias concerns. Regarding air quality outcomes, we judged 11 studies (31%) as having no substantial risk of bias concerns, 16 studies (46%) as having some risk of bias concerns, and eight studies (23%) as having serious risk of bias concerns.The evidence base, comprising non-randomized studies only, was of low or very low certainty for all intervention categories and primary outcomes. The narrative and graphical synthesis showed that evidence for effectiveness was mixed across the four intervention categories. For interventions targeting industrial, residential and multiple sources, a similar pattern emerged for both health and air quality outcomes, with essentially all studies observing either no clear association in either direction or a significant association favouring the intervention. The evidence base for interventions targeting vehicular sources was more heterogeneous, as a small number of studies did observe a significant association favouring the control. Overall, however, the evidence suggests that the assessed interventions do not worsen air quality or health. Given the heterogeneity across interventions, outcomes, and methods, it was difficult to derive overall conclusions regarding the effectiveness of interventions in terms of improved air quality or health. Most included studies observed either no significant association in either direction or an association favouring the intervention, with little evidence that the assessed interventions might be harmful. The evidence base highlights the challenges related to establishing a causal relationship between specific air pollution interventions and outcomes. In light of these challenges, the results on effectiveness should be interpreted with caution; it is important to emphasize that lack of evidence of an association is not equivalent to evidence of no association.We identified limited evidence for several world regions, notably Africa, the Middle East, Eastern Europe, Central Asia and Southeast Asia; decision-makers should prioritize the development and implementation of interventions in these settings. In the future, as new policies are introduced, decision-makers should consider a built-in evaluation component, which could facilitate more systematic and comprehensive evaluations. These could assess effectiveness, but also aspects of feasibility, fidelity and acceptability.The production of higher quality and more uniform evidence would be helpful in informing decisions. Researchers should strive to sufficiently account for confounding, assess the impact of methodological decisions through the conduct and communication of sensitivity analyses, and improve the reporting of methods, and other aspects of the study, most importantly the description of the intervention and the context in which it is implemented.
被引量：26 发表：1970
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Strategies to improve the implementation of workplace-based policies or practices targeting tobacco, alcohol, diet, physical activity and obesity.
Given the substantial period of time adults spend in their workplaces each day, these provide an opportune setting for interventions addressing modifiable behavioural risk factors for chronic disease. Previous reviews of trials of workplace-based interventions suggest they can be effective in modifying a range of risk factors including diet, physical activity, obesity, risky alcohol use and tobacco use. However, such interventions are often poorly implemented in workplaces, limiting their impact on employee health. Identifying strategies that are effective in improving the implementation of workplace-based interventions has the potential to improve their effects on health outcomes. To assess the effects of strategies for improving the implementation of workplace-based policies or practices targeting diet, physical activity, obesity, tobacco use and alcohol use.Secondary objectives were to assess the impact of such strategies on employee health behaviours, including dietary intake, physical activity, weight status, and alcohol and tobacco use; evaluate their cost-effectiveness; and identify any unintended adverse effects of implementation strategies on workplaces or workplace staff. We searched the following electronic databases on 31 August 2017: CENTRAL; MEDLINE; MEDLINE In Process; the Campbell Library; PsycINFO; Education Resource Information Center (ERIC); Cumulative Index to Nursing and Allied Health Literature (CINAHL); and Scopus. We also handsearched all publications between August 2012 and September 2017 in two speciality journals: Implementation Science and Journal of Translational Behavioral Medicine. We conducted searches up to September 2017 in Dissertations and Theses, the WHO International Clinical Trials Registry Platform, and the US National Institutes of Health Registry. We screened the reference lists of included trials and contacted authors to identify other potentially relevant trials. We also consulted experts in the field to identify other relevant research. Implementation strategies were defined as strategies specifically employed to improve the implementation of health interventions into routine practice within specific settings. We included any trial with a parallel control group (randomised or non-randomised) and conducted at any scale that compared strategies to support implementation of workplace policies or practices targeting diet, physical activity, obesity, risky alcohol use or tobacco use versus no intervention (i.e. wait-list, usual practice or minimal support control) or another implementation strategy. Implementation strategies could include those identified by the Effective Practice and Organisation of Care (EPOC) taxonomy such as quality improvement initiatives and education and training, as well as other strategies. Implementation interventions could target policies or practices directly instituted in the workplace environment, as well as workplace-instituted efforts encouraging the use of external health promotion services (e.g. gym membership subsidies). Review authors working in pairs independently performed citation screening, data extraction and 'Risk of bias' assessment, resolving disagreements via consensus or a third reviewer. We narratively synthesised findings for all included trials by first describing trial characteristics, participants, interventions and outcomes. We then described the effect size of the outcome measure for policy or practice implementation. We performed meta-analysis of implementation outcomes for trials of comparable design and outcome. We included six trials, four of which took place in the USA. Four trials employed randomised controlled trial (RCT) designs. Trials were conducted in workplaces from the manufacturing, industrial and services-based sectors. The sample sizes of workplaces ranged from 12 to 114. Workplace policies and practices targeted included: healthy catering policies; point-of-purchase nutrition labelling; environmental supports for healthy eating and physical activity; tobacco control policies; weight management programmes; and adherence to guidelines for staff health promotion. All implementation interventions utilised multiple implementation strategies, the most common of which were educational meetings, tailored interventions and local consensus processes. Four trials compared an implementation strategy intervention with a no intervention control, one trial compared different implementation interventions, and one three-arm trial compared two implementation strategies with each other and a control. Four trials reported a single implementation outcome, whilst the other two reported multiple outcomes. Investigators assessed outcomes using surveys, audits and environmental observations. We judged most trials to be at high risk of performance and detection bias and at unclear risk of reporting and attrition bias.Of the five trials comparing implementation strategies with a no intervention control, pooled analysis was possible for three RCTs reporting continuous score-based measures of implementation outcomes. The meta-analysis found no difference in standardised effects (standardised mean difference (SMD) -0.01, 95% CI -0.32 to 0.30; 164 participants; 3 studies; low certainty evidence), suggesting no benefit of implementation support in improving policy or practice implementation, relative to control. Findings for other continuous or dichotomous implementation outcomes reported across these five trials were mixed. For the two non-randomised trials examining comparative effectiveness, both reported improvements in implementation, favouring the more intensive implementation group (very low certainty evidence). Three trials examined the impact of implementation strategies on employee health behaviours, reporting mixed effects for diet and weight status (very low certainty evidence) and no effect for physical activity (very low certainty evidence) or tobacco use (low certainty evidence). One trial reported an increase in absolute workplace costs for health promotion in the implementation group (low certainty evidence). None of the included trials assessed adverse consequences. Limitations of the review included the small number of trials identified and the lack of consistent terminology applied in the implementation science field, which may have resulted in us overlooking potentially relevant trials in the search. Available evidence regarding the effectiveness of implementation strategies for improving implementation of health-promoting policies and practices in the workplace setting is sparse and inconsistent. Low certainty evidence suggests that such strategies may make little or no difference on measures of implementation fidelity or different employee health behaviour outcomes. It is also unclear if such strategies are cost-effective or have potential unintended adverse consequences. The limited number of trials identified suggests implementation research in the workplace setting is in its infancy, warranting further research to guide evidence translation in this setting.
被引量：- 发表：1970
