Cholinesterase inhibitors for vascular dementia and other vascular cognitive impairments: a network meta-analysis.

Vascular cognitive impairment (VCI) describes a broad spectrum of cognitive impairments caused by cerebrovascular disease, ranging from mild cognitive impairment to dementia. There are currently no pharmacological treatments recommended for improving either cognition or function in people with VCI. Three cholinesterase inhibitors (donepezil, galantamine, and rivastigmine) are licenced for the treatment of dementia due to Alzheimer's disease. They are thought to work by compensating for reduced cholinergic neurotransmission, which is also a feature of VCI. Through pairwise comparisons with placebo and a network meta-analysis, we sought to determine whether these medications are effective in VCI and whether there are differences between them with regard to efficacy or adverse events. (1) To assess the efficacy and safety of cholinesterase inhibitors in the treatment of adults with vascular dementia and other VCI. (2) To compare the effects of different cholinesterase inhibitors on cognition and adverse events, using network meta-analysis. We searched ALOIS, the Cochrane Dementia and Cognitive Improvement Group's register, MEDLINE (OvidSP), Embase (OvidSP), PsycINFO (OvidSP), CINAHL (EBSCOhost), Web of Science Core Collection (ISI Web of Science), LILACS (BIREME), ClinicalTrials.gov, and the World Health Organization International Clinical Trials Registry Platform on 19 August 2020. We included randomised controlled trials in which donepezil, galantamine, or rivastigmine was compared with placebo or in which the drugs were compared with each other in adults with vascular dementia or other VCI (excluding cerebral autosomal dominant arteriopathy with subcortical infarcts and leukoencephalopathy (CADASIL)). We included all drug doses and routes of administration. Two review authors independently identified eligible trials, extracted data, assessed risk of bias, and applied the GRADE approach to assess the certainty of the evidence. The primary outcomes were cognition, clinical global impression, function (performance of activities of daily living), and adverse events. Secondary outcomes were serious adverse events, incidence of development of new dementia, behavioural disturbance, carer burden, institutionalisation, quality of life and death. For the pairwise analyses, we pooled outcome data at similar time points using random-effects methods. We also performed a network meta-analysis using Bayesian methods. We included eight trials (4373 participants) in the review. Three trials studied donepezil 5 mg or 10 mg daily (n= 2193); three trials studied rivastigmine at a maximum daily dose of 3 to 12 mg (n= 800); and two trials studied galantamine at a maximum daily dose of 16 to 24 mg (n= 1380). The trials included participants with possible or probable vascular dementia or cognitive impairment following stroke. Mean ages were between 72.2 and 73.9 years. All of the trials were at low or unclear risk of bias in all domains, and the evidence ranged from very low to high level of certainty. For cognition, the results showed that donepezil 5 mg improves cognition slightly, although the size of the effect is unlikely to be clinically important (mean difference (MD) -0.92 Alzheimer's Disease Assessment Scale-Cognitive Subscale (ADAS-Cog) points (range 0 to 70), 95% confidence interval (CI) -1.44 to -0.40; high-certainty evidence). Donepezil 10 mg (MD -2.21 ADAS-Cog points, 95% CI -3.07 to -1.35; moderate-certainty evidence) and galantamine 16 to 24 mg (MD -2.01 ADAS-Cog point, 95%CI -3.18 to -0.85; moderate-certainty evidence) probably also improve cognition, although the larger effect estimates still may not be clinically important. With low certainty, there may be little to no effect of rivastigmine 3 to 12 mg daily on cognition (MD 0.03 ADAS-Cog points, 95% CI -3.04 to 3.10; low-certainty evidence). Adverse events reported in the studies included nausea and/or vomiting, diarrhoea, dizziness, headache, and hypertension. The results showed that there was probably little to no difference between donepezil 5 mg and placebo in the number of adverse events (odds ratio (OR) 1.22, 95% CI 0.94 to 1.58; moderate-certainty evidence), but there were slightly more adverse events with donepezil 10 mg than with placebo (OR 1.95, 95% CI 1.20 to 3.15; high-certainty evidence). The effect of rivastigmine 3 to 12 mg on adverse events was very uncertain (OR 3.21, 95% CI 0.36 to 28.88; very low-certainty evidence). Galantamine 16 to 24 mg is probably associated with a slight excess of adverse events over placebo (OR 1.57, 95% CI 1.02 to 2.43; moderate-certainty evidence). In the network meta-analysis (NMA), we included cognition to represent benefit, and adverse events to represent harm. All drugs ranked above placebo for cognition and below placebo for adverse events. We found donepezil 10 mg to rank first in terms of benefit, but third in terms of harms, when considering the network estimates and quality of evidence. Galantamine was ranked second in terms of both benefit and harm. Rivastigmine had the lowest ranking of the cholinesterase inhibitors in both benefit and harm NMA estimates, but this may reflect possibly inadequate doses received by some trial participants and small trial sample sizes. We found moderate- to high-certainty evidence that donepezil 5 mg, donepezil 10 mg, and galantamine have a slight beneficial effect on cognition in people with VCI, although the size of the change is unlikely to be clinically important. Donepezil 10 mg and galantamine 16 to 24 mg are probably associated with more adverse events than placebo. The evidence for rivastigmine was less certain. The data suggest that donepezil 10 mg has the greatest effect on cognition, but at the cost of adverse effects. The effect is modest, but in the absence of any other treatments, people living with VCI may still wish to consider the use of these agents. Further research into rivastigmine is needed, including the use of transdermal patches.

Battle CE ，Abdul-Rahim AH ，Shenkin SD ，Hewitt J ，Quinn TJ ... -  《Cochrane Database of Systematic Reviews》

Withdrawal or continuation of cholinesterase inhibitors or memantine or both, in people with dementia.

Dementia is a progressive syndrome characterised by deterioration in memory, thinking and behaviour, and by impaired ability to perform daily activities. Two classes of drug - cholinesterase inhibitors (donepezil, galantamine and rivastigmine) and memantine - are widely licensed for dementia due to Alzheimer's disease, and rivastigmine is also licensed for Parkinson's disease dementia. These drugs are prescribed to alleviate symptoms and delay disease progression in these and sometimes in other forms of dementia. There are uncertainties about the benefits and adverse effects of these drugs in the long term and in severe dementia, about effects of withdrawal, and about the most appropriate time to discontinue treatment. To evaluate the effects of withdrawal or continuation of cholinesterase inhibitors or memantine, or both, in people with dementia on: cognitive, neuropsychiatric and functional outcomes, rates of institutionalisation, adverse events, dropout from trials, mortality, quality of life and carer-related outcomes. We searched the Cochrane Dementia and Cognitive Improvement Group's Specialised Register up to 17 October 2020 using terms appropriate for the retrieval of studies of cholinesterase inhibitors or memantine. The Specialised Register contains records of clinical trials identified from monthly searches of a number of major healthcare databases, numerous trial registries and grey literature sources. We included all randomised, controlled clinical trials (RCTs) which compared withdrawal of cholinesterase inhibitors or memantine, or both, with continuation of the same drug or drugs. Two review authors independently assessed citations and full-text articles for inclusion, extracted data from included trials and assessed risk of bias using the Cochrane risk of bias tool. Where trials were sufficiently similar, we pooled data for outcomes in the short term (up to 2 months after randomisation), medium term (3-11 months) and long term (12 months or more). We assessed the overall certainty of the evidence for each outcome using GRADE methods. We included six trials investigating cholinesterase inhibitor withdrawal, and one trial investigating withdrawal of either donepezil or memantine. No trials assessed withdrawal of memantine only. Drugs were withdrawn abruptly in five trials and stepwise in two trials. All participants had dementia due to Alzheimer's disease, with severities ranging from mild to very severe, and were taking cholinesterase inhibitors without known adverse effects at baseline. The included trials randomised 759 participants to treatment groups relevant to this review. Study duration ranged from 6 weeks to 12 months. There were too few included studies to allow planned subgroup analyses. We considered some studies to be at unclear or high risk of selection, performance, detection, attrition or reporting bias. Compared to continuing cholinesterase inhibitors, discontinuing treatment may be associated with worse cognitive function in the short term (standardised mean difference (SMD) -0.42, 95% confidence interval (CI) -0.64 to -0.21; 4 studies; low certainty), but the effect in the medium term is very uncertain (SMD -0.40, 95% CI -0.87 to 0.07; 3 studies; very low certainty). In a sensitivity analysis omitting data from a study which only included participants who had shown a relatively poor prior response to donepezil, inconsistency was reduced and we found that cognitive function may be worse in the discontinuation group in the medium term (SMD -0.62; 95% CI -0.94 to -0.31). Data from one longer-term study suggest that discontinuing a cholinesterase inhibitor is probably associated with worse cognitive function at 12 months (mean difference (MD) -2.09 Standardised Mini-Mental State Examination (SMMSE) points, 95% CI -3.43 to -0.75; moderate certainty). Discontinuation may make little or no difference to functional status in the short term (SMD -0.25, 95% CI -0.54 to 0.04; 2 studies; low certainty), and its effect in the medium term is uncertain (SMD -0.38, 95% CI -0.74 to -0.01; 2 studies; very low certainty). After 12 months, discontinuing a cholinesterase inhibitor probably results in greater functional impairment than continuing treatment (MD -3.38 Bristol Activities of Daily Living Scale (BADLS) points, 95% CI -6.67 to -0.10; one study; moderate certainty). Discontinuation may be associated with a worsening of neuropsychiatric symptoms over the short term and medium term, although we cannot exclude a minimal effect (SMD - 0.48, 95% CI -0.82 to -0.13; 2 studies; low certainty; and SMD -0.27, 95% CI -0.47 to -0.08; 3 studies; low certainty, respectively). Data from one study suggest that discontinuing a cholinesterase inhibitor may result in little to no change in neuropsychiatric status at 12 months (MD -0.87 Neuropsychiatric Inventory (NPI) points; 95% CI -8.42 to 6.68; moderate certainty). We found no clear evidence of an effect of discontinuation on dropout due to lack of medication efficacy or deterioration in overall medical condition (odds ratio (OR) 1.53, 95% CI 0.84 to 2.76; 4 studies; low certainty), on number of adverse events (OR 0.85, 95% CI 0.57 to 1.27; 4 studies; low certainty) or serious adverse events (OR 0.80, 95% CI 0.46 to 1.39; 4 studies; low certainty), and on mortality (OR 0.75, 95% CI 0.36 to 1.55; 5 studies; low certainty). Institutionalisation was reported in one trial, but it was not possible to extract data for the groups relevant to this review. This review suggests that discontinuing cholinesterase inhibitors may result in worse cognitive, neuropsychiatric and functional status than continuing treatment, although this is supported by limited evidence, almost all of low or very low certainty. As all participants had dementia due to Alzheimer's disease, our findings are not transferable to other dementia types. We were unable to determine whether the effects of discontinuing cholinesterase inhibitors differed with baseline dementia severity. There is currently no evidence to guide decisions about discontinuing memantine. There is a need for further well-designed RCTs, across a range of dementia severities and settings. We are aware of two ongoing registered trials. In making decisions about discontinuing these drugs, clinicians should exercise caution, considering the evidence from existing trials along with other factors important to patients and their carers.

Parsons C ，Lim WY ，Loy C ，McGuinness B ，Passmore P ，Ward SA ，Hughes C ... -  《Cochrane Database of Systematic Reviews》

Cholinesterase inhibitors for Alzheimer's disease.

Birks J 《Cochrane Database of Systematic Reviews》

Cholinesterase inhibitors for rarer dementias associated with neurological conditions.

Li Y ，Hai S ，Zhou Y ，Dong BR ... -  《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》