The Role of Pharmaceutical Innovation in Clinical Practice Guidelines for Chronic Diseases.

Over the last 25 years, clinical practice guidelines have emerged as a means to standardize and improve care. As pharmaceutical innovations develop, guidelines are updated to incorporate new interventions. However, the extent to which pharmacotherapies are represented as treatment options in guideline recommendations has not been well elucidated. This study aimed to quantify the role pharmacotherapy has played in clinical practice guidelines across a range of chronic diseases over the past 20 years. Clinical practice guidelines published from 2000 to 2021 were identified for five chronic diseases: ischemic heart disease (IHD), non-small cell lung cancer (NSCLC), chronic obstructive pulmonary disease (COPD), Alzheimer's disease (AD), and type 2 diabetes (T2D). Guidelines were reviewed and data on treatment recommendations were collected, including the type of intervention, line of therapy, and, for pharmacotherapies, year of regulatory approval and year of inclusion in guidelines. In total, 92 clinical practice guidelines were reviewed. Among the 184 discrete recommended interventions across the five disease areas, 146 (79.3%) were pharmacotherapies, 21 (11.4%) were behavioral modifications, 6 (3.3%) were surgical interventions, and 11 (6%) were other interventions. Across guidelines, when a line of therapy was specified, behavioral modifications and pharmacotherapies were most frequently recommended as first-line interventions, whereas surgical interventions were more often recommended for subsequent lines of treatment. The time from regulatory approval of novel pharmacotherapies to inclusion in guideline recommendations varied considerably by disease area and geography. Across the reviewed disease areas, behavioral interventions and pharmacotherapies are shown to be critical components of clinical practice. Over the last 20 years, novel pharmaceutical innovations have been incorporated into clinical practice guideline recommendations; however, with varying speeds of adoption. Given the increasing pace of pharmacologic innovation, timely updates of clinical practice guidelines are critical to evolving the standard of care and practicing evidence-based medicine.

Roach M ，Land N ，Hernandez J ，Rau R ，Chou JW ，Hickson SS ，Rollmann DF ，Maclean JR ... -  《-》

The future of Cochrane Neonatal.

Cochrane Neonatal was first established in 1993, as one of the original review groups of the Cochrane Collaboration. In fact, the origins of Cochrane Neonatal precede the establishment of the collaboration. In the 1980's, the National Perinatal Epidemiology Unit at Oxford, led by Dr. Iain Chalmers, established the "Oxford Database of Perinatal Trials" (ODPT), a register of virtually all randomized controlled trials in perinatal medicine to provide a resource for reviews of the safety and efficacy of interventions used in perinatal care and to foster cooperative and coordinated research efforts in the perinatal field [1]. An effort that was clearly ahead of its time, ODPT comprised four main elements: a register of published reports of trials; a register of unpublished trials; a register of ongoing and planned trials; and data derived from pooled overviews (meta-analyses) of trials. This core effort grew into the creation of the seminal books, "Effective Care in Pregnancy and Childbirth" as well as "Effective Care of the Newborn Infant" [2,3]. As these efforts in perinatal medicine grew, Iain Chalmers thought well beyond perinatal medicine into the creation of a worldwide collaboration that became Cochrane [4]. The mission of the Cochrane Collaboration is to promote evidence-informed health decision-making by producing high-quality, relevant, accessible systematic reviews and other synthesized research evidence (www.cochrane.org). Cochrane Neonatal has continued to be one of the most productive review groups, publishing between 25 tpo to 40 new or updated systematic reviews each year. The impact factor has been steadily increasing over four years and now rivals most of the elite journals in pediatric medicine. Cochrane Neonatal has been a worldwide effort. Currently, there are 404 reviews involving 1206 authors from 52 countries. What has Cochrane done for babies? Reviews from Cochrane Neonatal have informed guidelines and recommendations worldwide. From January 2018 through June 2020, 77 international guidelines cited 221 Cochrane Neonatal reviews. These recommendations have included recommendations of the use of postnatal steroids, inhaled nitric oxide, feeding guidelines for preterm infants and other core aspects of neonatal practice. In addition, Cochrane Reviews has been the impetus for important research, including the large-scale trial of prophylactic indomethacin therapy, a variety of trials of postnatal steroids, trials of emollient ointment and probiotic trials [6]. While justifiably proud of these accomplishments, one needs to examine the future contribution of Cochrane Neonatal to the neonatal community. The future of Cochrane Neonatal is inexorably linked to the future of neonatal research. Obviously, there is no synthesis of trials data if, as a community, we fail to provide the core substrate for that research. As we look at the current trials' environment, fewer randomized controlled trial related to neonates are being published in recent years. A simple search of PubMed, limiting the search to "neonates" and "randomized controlled trials" shows that in the year 2000, 321 randomized controlled trials were published. These peaked five years ago, in 2015, with close to 900 trials being published. However, in 2018, only 791 studies are identified. Does this decrease represent a meaningful change in the neonatal research environment? Quite possibly. There are shifting missions of clinical neonatology at academic medical institutions, at least in the United States, with a focus on business aspects as well as other important competing clinical activities. Quality improvement has taken over as one of the major activities at both private and academic neonatal practices. Clearly, this is a needed improvement. All units at levels need to be dedicated to improving the outcomes of the sick and fragile population we care for. However, this need not be at the expense of formal clinical trials. It is understandable that this approach would be taken. Newer interventions frequently relate to complex systems of care and not the simple single interventions. Even trials that might traditionally have been done as randomized controlled trials, such as the introduction of a new mode of ventilation, are in reality complex challenges to the ability of institutions to create systems to adapt to these new technologies. Cost of doing trials has always been a barrier. The challenging regulatory and ethical environment contributes to these problems as well [7]. Despite these barriers, how does the research agenda of the neonatal community move forward in the 21st Century? We need to reassess how we create and disseminate our research findings. Innovative trial designs will allow us to address complex issues that we may not have tackled with conventional trials. Adaptive designs may allow us to look at potentially life-saving therapies in a way that feel more efficient and more ethical [8]. Clarifying issues such as the use of inhaled nitric oxide in preterm infants would be greatly served if we even knew whether or not there are hypoxemic preterm infant who would benefit from this therapy [9]. Current trials do not suggest so, yet current practice tells us that a significant number of these babies will receive inhaled nitric oxide [10-13]. Adaptive design, such as those done with trials of extracorporeal membrane oxygenation (ECMO), would allow us to quickly assess whether, in fact, these therapies are life-saving and allow us to consider whether or not further trials are needed [14,15]. Our understanding that many interventions involve entire systems approaches does not relegate us only to doing quality improvement work. Cluster designs may allow us to test more complex interventions that have usually been under the purview of quality improvement [16-18]. Cluster trials are well suited for such investigations and can be done with the least interruption to ongoing care. Ultimately, quality improvement is the application of the best evidence available (evidence-based medicine is "what to do" and evidence-based practice is "how to do"). [19,20]. Nascent efforts, such as the statement on "embedding necessary research into culture and health" (the ENRICH statement) call for the conduct of large, efficient pragmatic trials to evaluate neonatal outcomes, as in part called for in the ALPHA Collaboration [21,22]. This statement envisions an international system to identify important research questions by consulting regularly with all stakeholders, including patients, public health professionals, researchers, providers, policy makers, regulators, funders of industry. The ENRICH statement envisions a pathway to enable individuals, educational institutions, hospitals and health-care facilities to confirm their status as research-friendly by integrating an understanding of trials, other research and critical thinking and to teaching learning and culture, as well as an engagement with funders, professional organizations and regulatory bodies and other stake holders to raise awareness of the value of efficient international research to reduce barriers to large international pragmatic trials and other collaborative studies. In the future, if trials are to be done on this scale or trials are prospectively designed to be analyzed together, core outcome measures must be identified and standardized. That clinical trials supply estimates of outcomes that are relevant to patients and their families is critical. In addition, current neonatal research evaluates many different outcomes using multiple measures. A given measure can have multiple widely used definitions. Bronchopulmonary dysplasia (or chronic lung disease just to add to the confusion) quickly comes to mind [23,24]. The use of multiple definitions when attempting to measure the same outcome prevents synthesis of trial results and meta-analysis and hinders efforts to refine our estimates of effects. Towards that end, Webbe and colleagues have set out to develop a core outcome set for neonatal research [25]. Key stakeholders in the neonatal community reviewed multiple outcomes reported in neonatal trials and qualitative studies. Based on consensus, key outcome measures were identified, including survival, sepsis, necrotizing enterocolitis, brain injury on imaging, retinopathy or prematurity, gross motor ability, general cognitive ability, quality of life, adverse events, visual impairment or blindness, hearing impairment or deafness, chronic lung disease/bronchopulmonary dysplasia. Trials registration has to be a continued focus of the neonatal community. Trials registration allows for systematic reviewers to understand whether or not reporting bias has occurred [26]. It also allows for transparent incorporation of these core outcome measures. Ultimately, trials registration should include public reporting of all of these core outcomes and, in the future, access to data on an individual level such that more sophisticated individual patient data meta-analysis could occur. Lastly, there is no reason to see clinical trials and quality improvement as separate or exclusive activities. In fact, in the first NICQ Collaborative, conducted by Vermont Oxford Network, participation in a trial of postnatal steroids was considered part of the quality improvement best practices as opposed to simply choosing an as-of-yet unproven approach to use of this potent drug [27]. What role will Cochrane Neonatal play as we move forward in the 21st Century? As the neonatal community moves forward with its' research agenda, Cochrane Neonatal must not only follow but also lead with innovative approaches to synthesizing research findings. Cochrane Neonatal must continue to work closely with guideline developers. The relationship between systematic review production and guideline development is clearly outlined in reports from the Institute of Medicine [28,29]. Both are essential to guideline development; the systematic review group culling the evidence for the benefits and harms of a given intervention and the guideline group addressing the contextual issues of cost, feasibility, implementation and the values and preferences of individuals and societies. Most national and international guidelines groups now routinely use systematic reviews as the evidence basis for their guidelines and recommendations. Examples of the partnership between Cochrane Neonatal and international guideline development can be seen in our support of the World Health Organization (WHO) guidelines on the use of vitamin A or the soon to be published recommendations from the International Liaison Committee on Resuscitation (ILCOR) on cord management in preterm and term infants [30]. In the future, we need to collaborate early in the guideline development process so that the reviews are fit for purpose and meet the needs of the guideline developers and the end users. Towards this end, all Cochrane Neonatal reviews now contain GRADE assessments of the key clinical findings reported in the systematic review [31]. Addition of these assessments addresses the critical issue of our confidence in the findings. We are most confident in evidence provided by randomized controlled trials but this assessment can be can be downgraded if the studies that reported on the outcome in question had a high risk of bias, indirectness, inconsistency of results, or imprecision, or where there is evidence of reporting bias. Information provided by GRADE assessments is seen as critical in the process of moving from the evidence to formal recommendations [32]. We need to explore complex reviews, such as network (NMA) or multiple treatment comparison (MCT) meta-analyses, to address issues not formally addressed in clinical trials [33]. In conditions where there are multiple effective interventions, it is rare for all possible interventions to have been tested against each other [34]. A solution could be provided by network meta-analysis, which allows for comparing all treatments with each other, even if randomized controlled trials are not available for some treatment comparisons [34]. Network meta-analysis uses both direct (head-to-head) randomized clinical trial (RCT) evidence as well as indirect evidence from RCTs to compare the relative effectiveness of all included interventions [35]. However, Mills and colleagues note that the methodological quality of MTCs may be difficult for clinicians to interpret because the number of interventions evaluated may be large and the methodological approaches may be complex [35]. Cochrane Neonatal must take a role in both the creation of such analyses and the education of the neonatal community regarding the pitfalls of such an approach. The availability of individual patient data will make more sophisticated analyses more available to the community. Although the current crop of individual patient data meta-analyses (including the reviews of elective high frequency ventilation, inhaled nitric oxide and oxygen targets) have not differed substantially from the findings of the trials level reviews (suggesting that, in fact, sick neonates are more alike that unalike), there still will be a large role for individual patient data meta-analysis, at least to end the unfound conclusions that these therapies are effective in various subgroups (be it issues of sex, disease severity, or clinical setting) [36-39]. Future trials should take a lesson from the NeOProM Collaborative [37,39]. Given the difficulty in generating significant sample size and creating funding in any single environment, trials with similar protocols should be conducted in a variety of healthcare settings with an eye towards both study level and individual patient level meta-analysis at the conclusion of those trials, allowing for broader contribution to the trials data, more rapid accrual of sample size, and more precise results. We need to educate the neonatal community regarding the use and abuse of diagnostic tests. Diagnostic tests are a critical component of healthcare but also contribute greatly to the cost of medical care worldwide. These costs include the cost of the tests themselves and the costs of misdiagnosis and treatment of individuals who will not benefit from those treatments. Clinicians may have a limited understanding of diagnostic test accuracy, the ability of a diagnostic test to distinguish between patients with and without the disease or target condition [41,42]. Efforts such as Choosing Wisely have tried to identify these deficiencies [40]. As Cochrane has increased the general literacy of both the medical and general population regarding the interpretation of the results of interventions on various diseases, so should Cochrane move forward and improve the understanding of diagnostic testing. We need to become more efficient at creating and maintaining our reviews. The time spent to produce systematic reviews is far too great. In average, it takes between 2½ to 6½ years to produce a systematic review, requiring intense time input for highly trained and expensive experts. Innovations in the ways in which we produce systematic reviews can make the review process more efficient by outsourcing some of the tasks or crowdsourcing to machine learning. We need to let the crowd and machine learning innovations help us sort the massive amounts of information needed to conduct systematic reviews. It can also allow for "live" updating of critical reviews where the research landscape is quickly changing [43]. Lastly, Cochrane Neonatal must focus more on users of the reviews and not necessarily authors of the reviews. Current Cochrane programming speaks of Cochrane training with an eye towards developing the skills of individuals who will conduct systematic reviews. While this is clearly needed and laudable, the fact of the matter is that most of the community will be "users" of the reviews. Individuals who need to understand how to use and interpret the findings of systematic reviews. These review users include clinicians, guideline developers, policy makers and families. Incorporation of GRADE guidelines has been a huge step in adding transparency to the level of uncertainty we have in our findings. From a family's perspective, we need to overcome the environment of mistrust or misunderstanding of scientific evidence and how we convey what we know, and our uncertainty about what we know, to parents and families.

Soll RF ，Ovelman C ，McGuire W 《-》

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》

Guideline for the management of chronic obstructive pulmonary disease--2011 update.

Abdool-Gaffar MS ，Ambaram A ，Ainslie GM ，Bolliger CT ，Feldman C ，Geffen L ，Irusen EM ，Joubert J ，Lalloo UG ，Mabaso TT ，Nyamande K ，O'Brien J ，Otto W ，Raine R ，Richards G ，Smith C ，Stickells D ，Venter A ，Visser S ，Wong M ，COPD Working Group ... -  《SAMJ SOUTH AFRICAN MEDICAL JOURNAL》

An estimate of rate of deviation from NCCN guideline recommendations for central nervous system imaging in trials forming basis for drug approval in first line advanced non-small cell lung cancer (NSCLC).

It is unknown whether and to what degree trials submitted to the US FDA to support drug approval adhere to NCCN guideline-recommended care in their baseline and surveillance CNS imaging protocols. We sought to characterize the frequency with which the trials cited in US FDA drug approvals for first line advanced NSCLC between 2015 and 2020 deviated from NCCN guideline-recommended care for baseline and surveillance CNS imaging. Retrospective observational analysis using publicly available data of (1) list of trials cited by the FDA in drug approvals for first line advanced NSCLC from 2015 to 2020 (2) individual trial protocols (3) published trial data and supplementary appendices (4) archived versions of the NCCN guidelines for NSCLC from 2009 to 2018 (the years during which the trials were enrolling). Estimated percentage of trials for first line advanced NSCLC leading to FDA approval which deviated from NCCN guideline-recommended care with regards to CNS baseline and surveillance imaging. A total of 14 studies that had been cited in FDA drug approvals for first line advanced NSCLC met our inclusion criteria between January 1, 2015 and September 30, 2020. Of these trials, 8 (57.1%) deviated from NCCN guidelines in their baseline CNS imaging requirement. The frequency of re-assessment of CNS disease was variable amongst trials as well, with 9 (64.3%) deviating from NCCN recommendations. The trials supporting US FDA drug approvals in first line advanced NSCLC often have CNS imaging requirements that do not adhere to NCCN guidelines. Many trials permit alternative, substandard methods and the proportion of patients undergoing each modality is uniformly not reported. Nonstandard CNS surveillance protocols are common. To best serve patients with advanced NSCLC in the US, drug approvals by the FDA must be based on trials that mirror clinical practice and have imaging requirements consistent with current US standard of care.

Sharp J ，Prasad V 《BMC CANCER》