Prophylactic anticoagulants for people hospitalised with COVID-19.

Coronavirus disease 2019 (COVID-19) is a serious disease caused by severe acute respiratory syndrome coronavirus 2 (SARS-CoV-2). The primary manifestation is respiratory insufficiency that can also be related to diffuse pulmonary microthrombosis in people with COVID-19. This disease also causes thromboembolic events, such as pulmonary embolism, deep venous thrombosis, arterial thrombosis, catheter thrombosis, and disseminated intravascular coagulopathy. Recent studies have indicated a worse prognosis for people with COVID-19 who developed thromboembolism. Anticoagulants are medications used in the prevention and treatment of venous or arterial thromboembolic events. Several drugs are used in the prophylaxis and treatment of thromboembolic events, such as heparinoids (heparins or pentasaccharides), vitamin K antagonists and direct anticoagulants. Besides their anticoagulant properties, heparinoids have an additional anti-inflammatory potential, that may affect the clinical evolution of people with COVID-19. Some practical guidelines address the use of anticoagulants for thromboprophylaxis in people with COVID-19, however, the benefit of anticoagulants for people with COVID-19 is still under debate. To assess the effects of prophylactic anticoagulants versus active comparator, placebo or no intervention, on mortality and the need for respiratory support in people hospitalised with COVID-19. We searched CENTRAL, MEDLINE, Embase, LILACS and IBECS databases, the Cochrane COVID-19 Study Register and medRxiv preprint database from their inception to 20 June 2020. We also checked reference lists of any relevant systematic reviews identified and contacted specialists in the field for additional references to trials. Randomised controlled trials (RCTs), quasi-RCTs, cluster-RCTs and cohort studies that compared prophylactic anticoagulants (heparin, vitamin K antagonists, direct anticoagulants, and pentasaccharides) versus active comparator, placebo or no intervention for the management of people hospitalised with COVID-19. We excluded studies without a comparator group. Primary outcomes were all-cause mortality and need for additional respiratory support. Secondary outcomes were mortality related to COVID-19, deep vein thrombosis (DVT), pulmonary embolism, major bleeding, adverse events, length of hospital stay and quality of life. We used standard Cochrane methodological procedures. We used ROBINS-I to assess risk of bias for non-randomised studies (NRS) and GRADE to assess the certainty of evidence. We reported results narratively. We identified no RCTs or quasi-RCTs that met the inclusion criteria. We included seven retrospective NRS (5929 participants), three of which were available as preprints. Studies were conducted in China, Italy, Spain and the USA. All of the studies included people hospitalised with COVID-19, in either intensive care units, hospital wards or emergency departments. The mean age of participants (reported in 6 studies) ranged from 59 to 72 years. Only three included studies reported the follow-up period, which varied from 8 to 35 days. The studies did not report on most of our outcomes of interest: need for additional respiratory support, mortality related to COVID-19, DVT, pulmonary embolism, adverse events, and quality of life. Anticoagulants (all types) versus no treatment (6 retrospective NRS, 5685 participants) One study reported a reduction in all-cause mortality (adjusted odds ratio (OR) 0.42, 95% confidence interval (CI) 0.26 to 0.66; 2075 participants). One study reported a reduction in mortality only in a subgroup of 395 people who required mechanical ventilation (hazard ratio (HR) 0.86, 95% CI 0.82 to 0.89). Three studies reported no differences in mortality (adjusted OR 1.64, 95% CI 0.92 to 2.92; 449 participants; unadjusted OR 1.66, 95% CI 0.76 to 3.64; 154 participants and adjusted risk ratio (RR) 1.15, 95% CI 0.29 to 2.57; 192 participants). One study reported zero events in both intervention groups (42 participants). The overall risk of bias for all-cause mortality was critical and the certainty of the evidence was very low. One NRS reported bleeding events in 3% of the intervention group and 1.9% of the control group (OR 1.62, 95% CI 0.96 to 2.71; 2773 participants; low-certainty evidence). Therapeutic-dose anticoagulants versus prophylactic-dose anticoagulants (1 retrospective NRS, 244 participants) The study reported a reduction in all-cause mortality (adjusted HR 0.21, 95% CI 0.10 to 0.46) and a lower absolute rate of death in the therapeutic group (34.2% versus 53%). The overall risk of bias for all-cause mortality was serious and the certainty of the evidence was low. The study also reported bleeding events in 31.7% of the intervention group and 20.5% of the control group (OR 1.8, 95% CI 0.96 to 3.37; low-certainty evidence). Ongoing studies We found 22 ongoing studies in hospital settings (20 RCTs, 14,730 participants; 2 NRS, 997 participants) in 10 different countries (Australia (1), Brazil (1), Canada (2), China (3), France (2), Germany (1), Italy (4), Switzerland (1), UK (1) and USA (6)). Twelve ongoing studies plan to report mortality and six plan to report additional respiratory support. Thirteen studies are expected to be completed in December 2020 (6959 participants), eight in July 2021 (8512 participants), and one in December 2021 (256 participants). Four of the studies plan to include 1000 participants or more. There is currently insufficient evidence to determine the risks and benefits of prophylactic anticoagulants for people hospitalised with COVID-19. Since there are 22 ongoing studies that plan to evaluate more than 15,000 participants in this setting, we will add more robust evidence to this review in future updates.

Flumignan RL ，Tinôco JDS ，Pascoal PI ，Areias LL ，Cossi MS ，Fernandes MI ，Costa IK ，Souza L ，Matar CF ，Tendal B ，Trevisani VF ，Atallah ÁN ，Nakano LC ... -  《Cochrane Database of Systematic Reviews》

Anticoagulants for people hospitalised with COVID-19.

The primary manifestation of coronavirus disease 2019 (COVID-19) is respiratory insufficiency that can also be related to diffuse pulmonary microthrombosis and thromboembolic events, such as pulmonary embolism, deep vein thrombosis, or arterial thrombosis. People with COVID-19 who develop thromboembolism have a worse prognosis. Anticoagulants such as heparinoids (heparins or pentasaccharides), vitamin K antagonists and direct anticoagulants are used for the prevention and treatment of venous or arterial thromboembolism. Besides their anticoagulant properties, heparinoids have an additional anti-inflammatory potential. However, the benefit of anticoagulants for people with COVID-19 is still under debate. To assess the benefits and harms of anticoagulants versus active comparator, placebo or no intervention in people hospitalised with COVID-19. We searched the CENTRAL, MEDLINE, Embase, LILACS and IBECS databases, the Cochrane COVID-19 Study Register and medRxiv preprint database from their inception to 14 April 2021. We also checked the reference lists of any relevant systematic reviews identified, and contacted specialists in the field for additional references to trials. Eligible studies were randomised controlled trials (RCTs), quasi-RCTs, cluster-RCTs and cohort studies that compared prophylactic anticoagulants versus active comparator, placebo or no intervention for the management of people hospitalised with COVID-19. We excluded studies without a comparator group and with a retrospective design (all previously included studies) as we were able to include better study designs. Primary outcomes were all-cause mortality and necessity for additional respiratory support. Secondary outcomes were mortality related to COVID-19, deep vein thrombosis, pulmonary embolism, major bleeding, adverse events, length of hospital stay and quality of life. We used standard Cochrane methodological procedures. We used Cochrane RoB 1 to assess the risk of bias for RCTs, ROBINS-I to assess risk of bias for non-randomised studies (NRS) and GRADE to assess the certainty of evidence. We meta-analysed data when appropriate. We included seven studies (16,185 participants) with participants hospitalised with COVID-19, in either intensive care units, hospital wards or emergency departments. Studies were from Brazil (2), Iran (1), Italy (1), and the USA (1), and two involved more than country. The mean age of participants was 55 to 68 years and the follow-up period ranged from 15 to 90 days. The studies assessed the effects of heparinoids, direct anticoagulants or vitamin K antagonists, and reported sparse data or did not report some of our outcomes of interest: necessity for additional respiratory support, mortality related to COVID-19, and quality of life. Higher-dose versus lower-dose anticoagulants (4 RCTs, 4647 participants) Higher-dose anticoagulants result in little or no difference in all-cause mortality (risk ratio (RR) 1.03, 95% CI 0.92 to 1.16, 4489 participants; 4 RCTs) and increase minor bleeding (RR 3.28, 95% CI 1.75 to 6.14, 1196 participants; 3 RCTs) compared to lower-dose anticoagulants up to 30 days (high-certainty evidence). Higher-dose anticoagulants probably reduce pulmonary embolism (RR 0.46, 95% CI 0.31 to 0.70, 4360 participants; 4 RCTs), and slightly increase major bleeding (RR 1.78, 95% CI 1.13 to 2.80, 4400 participants; 4 RCTs) compared to lower-dose anticoagulants up to 30 days (moderate-certainty evidence). Higher-dose anticoagulants may result in little or no difference in deep vein thrombosis (RR 1.08, 95% CI 0.57 to 2.03, 3422 participants; 4 RCTs), stroke (RR 0.91, 95% CI 0.40 to 2.03, 4349 participants; 3 RCTs), major adverse limb events (RR 0.33, 95% CI 0.01 to 7.99, 1176 participants; 2 RCTs), myocardial infarction (RR 0.86, 95% CI 0.48 to 1.55, 4349 participants; 3 RCTs), atrial fibrillation (RR 0.35, 95% CI 0.07 to 1.70, 562 participants; 1 study), or thrombocytopenia (RR 0.94, 95% CI 0.71 to 1.24, 2789 participants; 2 RCTs) compared to lower-dose anticoagulants up to 30 days (low-certainty evidence). It is unclear whether higher-dose anticoagulants have any effect on necessity for additional respiratory support, mortality related to COVID-19, and quality of life (very low-certainty evidence or no data). Anticoagulants versus no treatment (3 prospective NRS, 11,538 participants) Anticoagulants may reduce all-cause mortality but the evidence is very uncertain due to two study results being at critical and serious risk of bias (RR 0.64, 95% CI 0.55 to 0.74, 8395 participants; 3 NRS; very low-certainty evidence). It is uncertain if anticoagulants have any effect on necessity for additional respiratory support, mortality related to COVID-19, deep vein thrombosis, pulmonary embolism, major bleeding, stroke, myocardial infarction and quality of life (very low-certainty evidence or no data). Ongoing studies We found 62 ongoing studies in hospital settings (60 RCTs, 35,470 participants; 2 prospective NRS, 120 participants) in 20 different countries. Thirty-five ongoing studies plan to report mortality and 26 plan to report necessity for additional respiratory support. We expect 58 studies to be completed in December 2021, and four in July 2022. From 60 RCTs, 28 are comparing different doses of anticoagulants, 24 are comparing anticoagulants versus no anticoagulants, seven are comparing different types of anticoagulants, and one did not report detail of the comparator group. When compared to a lower-dose regimen, higher-dose anticoagulants result in little to no difference in all-cause mortality and increase minor bleeding in people hospitalised with COVID-19 up to 30 days. Higher-dose anticoagulants possibly reduce pulmonary embolism, slightly increase major bleeding, may result in little to no difference in hospitalisation time, and may result in little to no difference in deep vein thrombosis, stroke, major adverse limb events, myocardial infarction, atrial fibrillation, or thrombocytopenia.  Compared with no treatment, anticoagulants may reduce all-cause mortality but the evidence comes from non-randomised studies and is very uncertain. It is unclear whether anticoagulants have any effect on the remaining outcomes compared to no anticoagulants (very low-certainty evidence or no data). Although we are very confident that new RCTs will not change the effects of different doses of anticoagulants on mortality and minor bleeding, high-quality RCTs are still needed, mainly for the other primary outcome (necessity for additional respiratory support), the comparison with no anticoagulation, when comparing the types of anticoagulants and giving anticoagulants for a prolonged period of time.

Flumignan RL ，Civile VT ，Tinôco JDS ，Pascoal PI ，Areias LL ，Matar CF ，Tendal B ，Trevisani VF ，Atallah ÁN ，Nakano LC ... -  《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》

Prophylactic anticoagulants for non-hospitalised people with COVID-19.

The coronavirus disease 2019 (COVID-19) pandemic has impacted healthcare systems worldwide. Multiple reports on thromboembolic complications related to COVID-19 have been published, and researchers have described that people with COVID-19 are at high risk for developing venous thromboembolism (VTE). Anticoagulants have been used as pharmacological interventions to prevent arterial and venous thrombosis, and their use in the outpatient setting could potentially reduce the prevalence of vascular thrombosis and associated mortality in people with COVID-19. However, even lower doses used for a prophylactic purpose may result in adverse events such as bleeding. It is important to consider the evidence for anticoagulant use in non-hospitalised people with COVID-19. To evaluate the benefits and harms of prophylactic anticoagulants versus active comparators, placebo or no intervention, or non-pharmacological interventions in non-hospitalised people with COVID-19. We used standard, extensive Cochrane search methods. The latest search date was 18 April 2022. We included randomised controlled trials (RCTs) comparing prophylactic anticoagulants with placebo or no treatment, another active comparator, or non-pharmacological interventions in non-hospitalised people with COVID-19. We included studies that compared anticoagulants with a different dose of the same anticoagulant. We excluded studies with a duration of under two weeks. We used standard Cochrane methodological procedures. Our primary outcomes were all-cause mortality, VTE (deep vein thrombosis (DVT) or pulmonary embolism (PE)), and major bleeding. Our secondary outcomes were DVT, PE, need for hospitalisation, minor bleeding, adverse events, and quality of life. We used GRADE to assess the certainty of the evidence. We included five RCTs with up to 90 days of follow-up (short term). Data were available for meta-analysis from 1777 participants. Anticoagulant compared to placebo or no treatment Five studies compared anticoagulants with placebo or no treatment and provided data for three of our outcomes of interest (all-cause mortality, major bleeding, and adverse events). The evidence suggests that prophylactic anticoagulants may lead to little or no difference in all-cause mortality (risk ratio (RR) 0.36, 95% confidence interval (CI) 0.04 to 3.61; 5 studies; 1777 participants; low-certainty evidence) and probably reduce VTE from 3% in the placebo group to 1% in the anticoagulant group (RR 0.36, 95% CI 0.16 to 0.85; 4 studies; 1259 participants; number needed to treat for an additional beneficial outcome (NNTB) = 50; moderate-certainty evidence). There may be little to no difference in major bleeding (RR 0.36, 95% CI 0.01 to 8.78; 5 studies; 1777 participants; low-certainty evidence). Anticoagulants probably result in little or no difference in DVT (RR 1.02, 95% CI 0.30 to 3.46; 3 studies; 1009 participants; moderate-certainty evidence), but probably reduce the risk of PE from 2.7% in the placebo group to 0.7% in the anticoagulant group (RR 0.25, 95% CI 0.08 to 0.79; 3 studies; 1009 participants; NNTB 50; moderate-certainty evidence). Anticoagulants probably lead to little or no difference in reducing hospitalisation (RR 1.01, 95% CI 0.59 to 1.75; 4 studies; 1459 participants; moderate-certainty evidence) and may lead to little or no difference in adverse events (minor bleeding, RR 2.46, 95% CI 0.90 to 6.72; 5 studies, 1777 participants; low-certainty evidence). Anticoagulant compared to a different dose of the same anticoagulant One study compared anticoagulant (higher-dose apixaban) with a different (standard) dose of the same anticoagulant and reported five relevant outcomes. No cases of all-cause mortality, VTE, or major bleeding occurred in either group during the 45-day follow-up (moderate-certainty evidence). Higher-dose apixaban compared to standard-dose apixaban may lead to little or no difference in reducing the need for hospitalisation (RR 1.89, 95% CI 0.17 to 20.58; 1 study; 278 participants; low-certainty evidence) or in the number of adverse events (minor bleeding, RR 0.47, 95% CI 0.09 to 2.54; 1 study; 278 participants; low-certainty evidence). Anticoagulant compared to antiplatelet agent One study compared anticoagulant (apixaban) with antiplatelet agent (aspirin) and reported five relevant outcomes. No cases of all-cause mortality or major bleeding occurred during the 45-day follow-up (moderate-certainty evidence). Apixaban may lead to little or no difference in VTE (RR 0.36, 95% CI 0.01 to 8.65; 1 study; 279 participants; low-certainty evidence), need for hospitalisation (RR 3.20, 95% CI 0.13 to 77.85; 1 study; 279 participants; low-certainty evidence), or adverse events (minor bleeding, RR 2.13, 95% CI 0.40 to 11.46; 1 study; 279 participants; low-certainty evidence). No included studies reported on quality of life or investigated anticoagulants compared to a different anticoagulant, or anticoagulants compared to non-pharmacological interventions. We found low- to moderate-certainty evidence from five RCTs that prophylactic anticoagulants result in little or no difference in major bleeding, DVT, need for hospitalisation, or adverse events when compared with placebo or no treatment in non-hospitalised people with COVID-19. Low-certainty evidence indicates that prophylactic anticoagulants may result in little or no difference in all-cause mortality when compared with placebo or no treatment, but moderate-certainty evidence indicates that prophylactic anticoagulants probably reduce the incidence of VTE and PE. Low-certainty evidence suggests that comparing different doses of the same prophylactic anticoagulant may result in little or no difference in need for hospitalisation or adverse events. Prophylactic anticoagulants may result in little or no difference in risk of VTE, hospitalisation, or adverse events when compared with antiplatelet agents (low-certainty evidence). Given that there were only short-term data from one study, these results should be interpreted with caution. Additional trials of sufficient duration are needed to clearly determine any effect on clinical outcomes.

Santos BC ，Flumignan RL ，Civile VT ，Atallah ÁN ，Nakano LC ... -  《Cochrane Database of Systematic Reviews》

Prophylaxis of thromboembolism during therapy with asparaginase in adults with acute lymphoblastic leukaemia.

The risk of venous thromboembolism is increased in adults and enhanced by asparaginase-based chemotherapy, and venous thromboembolism introduces a secondary risk of treatment delay and premature discontinuation of key anti-leukaemic agents, potentially compromising survival. Yet, the trade-off between benefits and harms of primary thromboprophylaxis in adults with acute lymphoblastic leukaemia (ALL) treated according to asparaginase-based regimens is uncertain.  OBJECTIVES: The primary objectives were to assess the benefits and harms of primary thromboprophylaxis for first-time symptomatic venous thromboembolism in adults with ALL receiving asparaginase-based therapy compared with placebo or no thromboprophylaxis. The secondary objectives were to compare the benefits and harms of different groups of primary systemic thromboprophylaxis by stratifying the main results per type of drug (heparins, vitamin K antagonists, synthetic pentasaccharides, parenteral direct thrombin inhibitors, direct oral anticoagulants, and blood-derived products for antithrombin substitution). We conducted a comprehensive literature search on 02 June 2020, with no language restrictions, including (1) electronic searches of Pubmed/MEDLINE; Embase/Ovid; Scopus/Elsevier; Web of Science Core Collection/Clarivate Analytics; and Cochrane Central Register of Controlled Trials (CENTRAL) and (2) handsearches of (i) reference lists of identified studies and related reviews; (ii) clinical trials registries (ClinicalTrials.gov registry; the International Standard Randomized Controlled Trial Number (ISRCTN) registry; the World Health Organisation's International Clinical Trials Registry Platform (ICTRP); and pharmaceutical manufacturers of asparaginase including Servier, Takeda, Jazz Pharmaceuticals, Ohara Pharmaceuticals, and Kyowa Pharmaceuticals), and (iii) conference proceedings (from the annual meetings of the American Society of Hematology (ASH); the European Haematology Association (EHA); the American Society of Clinical Oncology (ASCO); and the International Society on Thrombosis and Haemostasis (ISTH)). We conducted all searches from 1970 (the time of introduction of asparaginase in ALL treatment). We contacted the authors of relevant studies to identify any unpublished material, missing data, or information regarding ongoing studies. Randomised controlled trials (RCTs); including quasi-randomised, controlled clinical, cross-over, and cluster-randomised trial designs) comparing any parenteral/oral preemptive anticoagulant or mechanical intervention with placebo or no thromboprophylaxis, or comparing two different pre-emptive anticoagulant interventions in adults aged at least 18 years with ALL treated according to asparaginase-based chemotherapy regimens. For the description of harms, non-randomised observational studies with a control group were eligible for inclusion.  DATA COLLECTION AND ANALYSIS: Using a standardised data collection form, two review authors independently screened and selected studies, extracted data, assessed risk of bias for each outcome using standardised tools (RoB 2.0 tool for RCTs and ROBINS-I tool for non-randomised studies) and the certainty of evidence for each outcome using the GRADE approach. Primary outcomes included first-time symptomatic venous thromboembolism, all-cause mortality, and major bleeding. Secondary outcomes included asymptomatic venous thromboembolism, venous thromboembolism-related mortality, adverse events (i.e. clinically relevant non-major bleeding and heparin-induced thrombocytopenia for trials using heparins), and quality of life. Analyses were performed according to the guidelines of the Cochrane Handbook for Systematic Reviews of Interventions. For non-randomised studies, we evaluated all studies (including studies judged to be at critical risk of bias in at least one of the ROBINS-I domains) in a sensitivity analysis exploring confounding.  MAIN RESULTS: We identified 23 non-randomised studies that met the inclusion criteria of this review, of which 10 studies provided no outcome data for adults with ALL. We included the remaining 13 studies in the 'Risk of bias' assessment, in which we identified invalid control group definition in two studies and judged outcomes of nine studies to be at critical risk of bias in at least one of the ROBINS-I domains and outcomes of two studies at serious risk of bias. We did not assess the benefits of thromboprophylaxis, as no RCTs were included. In the main descriptive analysis of harms, we included two retrospective non-randomised studies with outcomes judged to be at serious risk of bias. One study evaluated antithrombin concentrates compared to no antithrombin concentrates. We are uncertain whether antithrombin concentrates have an effect on all-cause mortality (risk ratio (RR) 0.55, 95% confidence interval (CI) 0.26 to 1.19 (intention-to-treat analysis); one study, 40 participants; very low certainty of evidence). We are uncertain whether antithrombin concentrates have an effect on venous thromboembolism-related mortality (RR 0.10, 95% CI 0.01 to 1.94 (intention-to-treat analysis); one study, 40 participants; very low certainty of evidence). We do not know whether antithrombin concentrates have an effect on major bleeding, clinically relevant non-major bleeding, and quality of life in adults with ALL treated with asparaginase-based chemotherapy, as data were insufficient. The remaining study (224 participants) evaluated prophylaxis with low-molecular-weight heparin versus no prophylaxis. However, this study reported insufficient data regarding harms including all-cause mortality, major bleeding, venous thromboembolism-related mortality, clinically relevant non-major bleeding, heparin-induced thrombocytopenia, and quality of life. In the sensitivity analysis of harms, exploring the effect of confounding, we also included nine non-randomised studies with outcomes judged to be at critical risk of bias primarily due to uncontrolled confounding. Three studies (179 participants) evaluated the effect of antithrombin concentrates and six studies (1224 participants) evaluated the effect of prophylaxis with different types of heparins. When analysing all-cause mortality; venous thromboembolism-related mortality; and major bleeding (studies of heparin only) including all studies with extractable outcomes for each comparison (antithrombin and low-molecular-weight heparin), we observed small study sizes; few events; wide CIs crossing the line of no effect; and substantial heterogeneity by visual inspection of the forest plots. Although the observed heterogeneity could arise through the inclusion of a small number of studies with differences in participants; interventions; and outcome assessments, the likelihood that bias due to uncontrolled confounding was the cause of heterogeneity is inevitable. Subgroup analyses were not possible due to insufficient data.  AUTHORS' CONCLUSIONS: We do not know from the currently available evidence, if thromboprophylaxis used for adults with ALL treated according to asparaginase-based regimens is associated with clinically appreciable benefits and acceptable harms. The existing research on this question is solely of non-randomised design, seriously to critically confounded, and underpowered with substantial imprecision. Any estimates of effect based on the existing insufficient evidence is very uncertain and is likely to change with future research.

Rank CU ，Lynggaard LS ，Als-Nielsen B ，Stock W ，Toft N ，Nielsen OJ ，Frandsen TL ，Tuckuviene R ，Schmiegelow K ... -  《Cochrane Database of Systematic Reviews》