The Clinical Effects of Cerebral Near-Infrared Spectroscopy Monitoring (NIRS) Versus No Monitoring in Children and Adults: A Protocol for a Systematic Review With Meta-Analysis and Trial Sequential Analysis

Background Multiple clinical conditions are associated with cerebral hypoxia/ischaemia and thereby an increased risk of hypoxic-ischaemic brain injury. Cerebral near-infrared spectroscopy monitoring (NIRS) is a tool to monitor brain oxygenation and perfusion, and the clinical uptake of NIRS has expanded over recent years. Specically, NIRS is used in the perioperative and neonatal, paediatric, and adult intensive care settings. However, the available literature suggests that clinical benets and harms of cerebral NIRS monitoring are uncertain. As rates of clinically signicant hypoxic-ischaemic brain injuries are typically low, it is dicult for randomised clinical trials to capture a suciently large number of events to evaluate the clinical effect of cerebral NIRS monitoring, when focusing on specic clinical settings. Methods We will conduct a systematic review with meta-analysis and Trial Sequential Analysis to evaluate the benets and harms of clinical care with cerebral NIRS monitoring versus clinical care without cerebral NIRS monitoring in children and adults across all clinical settings. We will only include randomised clinical trials and the primary outcomes are all-cause mortality, moderate or severe persistent cognitive or neurological decit, and proportion of participants with one or more serious adverse events. The review will be conducted according to the methodology described in The Cochrane Handbook for Systematic Reviews of Interventions, including GRADE. An eight-step procedure by Jakobsen et al. will be used to assess if thresholds for statistical and clinical signicance are crossed. As we include trials across multiple clinical settings, there is an increased probability of reaching a sucient information size. However, heterogeneity between the included trials may impair our ability to interpret results to specic clinical settings. In this situation, we may have to depend on subgroup analyses with inherent increased risks of type I and II errors.

An additional Cochrane review from 2017 evaluated the use of cerebral NIRS monitoring in very preterm infants (59). The review included only one randomised clinical trial with a total of 166 participants and found no signi cant differences between the experimental and control participants for neither mortality (12/86 versus 20/80), mild-moderate brain injury by ultrasound (49/80 versus 33/77), or severe brain injury by ultrasound (10/80 versus 18/77) (57).
The trial, however, was not powered to detect a relevant difference on any of these clinical outcomes. Due to the small sample size, lack of group allocation blinding, and the surrogate outcomes being indirectly linked to the clinical outcomes, the authors graded the certainty of evidence as very low to low. The review authors concluded that, based on the available evidence, the effect of cerebral NIRS monitoring in preterm infants cannot be established and that there is a need for additional large-scale randomised clinical trials with clinically relevant primary outcomes (57).
The characteristics of these three reviews are summarised in table 1. Yes Yes Yes cPVL = cystic periventricular leukomalacia, IVH = intraventricular haemorrhage, NIRS = near-infrared spectroscopy, RCTs = randomised clinical trials, POCD = postoperative cognitive decline, POD = postoperative delirium, TCI = transient cerebral ischaemia The motivation and aim of the present meta-analysis The primary purpose of monitoring of cerebral oxygenation is the prevention of hypoxic/ischaemic brain injury. The rates of clinically signi cant hypoxic/ischaemic brain injury, however, are typically low, and large subject numbers are needed to exclude effects of importance (58). Therefore, the purpose of this systematic review with meta-analysis and Trial Sequential Analysis, is to evaluate the bene cial and harmful effects of clinical care with access to cerebral NIRS monitoring versus clinical care without access to cerebral NIRS monitoring, in children and adults across all clinical settings. Since the primary purpose of NIRS monitoring is prevention of brain injury, the majority of the chosen outcomes focuses on this.

Methods
This protocol is in adherence with the Preferred Reporting Items for Systematic reviews and Meta-Analyses for Protocols (PRISMA-P) 2015 (61,62).

Types of studies
We will include randomised clinical trials, irrespectively of publication status, publication type, publication year, or written language. Cluster randomised trials and the rst part, before cross-over, of randomised cross-over trials will also be included. Quasi-randomised studies, and other studies that are not randomised clinical trials will be excluded.

Types of participants
We will include adults and children of all ages, including neonates, irrespectively of sex and comorbidities.

Types of interventions
The experimental intervention will be cerebral NIRS monitoring to guide clinical care, irrespectively of the length of the intervention period and clinical setting.
The control intervention will be no access to cerebral NIRS monitoring. In some trials, participants in the control group will have received cerebral NIRS monitoring to collect data on cerebral oxygenation values during the trial, but where the oxygenation values were unavailable to the clinical staff. In such trials, the control intervention will also be de ned as no access to cerebral NIRS monitoring, as this additional monitoring to collect data, was not a part of the control intervention.
Any co-interventions can be accepted but only if the co-intervention is planned to be delivered similarly in both the experimental and control group.

Outcome measures
Primary outcomes 1. All-cause mortality at maximal follow-up.
2. Moderate or severe, persistent cognitive or neurological de cit, signi cantly affecting daily life, at maximum follow-up (e.g. modi ed Rankin score of three or higher (63), Gross Motor Function Classi cation System level two or higher (64) or Bayley Scale of Infant Development score below minus two standard deviations at two years or later (65)).
3. Proportion of participants with one or more serious adverse events. We will de ne a serious adverse event as any untoward medical occurrence that resulted in either death, was life-threatening, jeopardised the participant, was persistent, led to signi cant disability, hospitalisation, or prolonged hospitalisation (66). As we expect the trialists' reporting of serious adverse events to be heterogeneous and not strictly according to the International Committee of Harmonization-Good Clinical Practice (ICH-GCP) recommendations, we will include the event as a serious adverse, if the trialist either: a) used the term 'serious adverse event' but not refer to ICH-GCP (66), or b) reported the proportion of participants with an event we consider to full-ll the ICH-GCP de nition (e.g. myocardial infarction or hospitalisation). If several of such events are reported, then we will choose the highest proportion reported in each trial.
Secondary outcomes 1. Mild, moderate or severe, temporary or persistent, cognitive or neurological de cit as de ned by the trialists (e.g. postoperative delirium, postoperative cognitive decline, or Bayley Scale of Infant Development score below minus one standard deviations (65)).
2. Quality of life de ned as any validated continuous outcome scale used by the trialists at maximum follow-up.
3. Any evidence of brain damage on imaging as de ned by the trialists at maximal follow-up. 4. Proportion of participants with one or more adverse events de ned as an untoward medical occurrence that did not necessarily have had to have a causal relationship with the intervention, and which is also non-serious (66).
Exploratory outcomes 1. Any evidence of a negative impact on the brain as de ned by the trialists (including mild, moderate or severe, temporary or persistent cognitive or neurological de cits, evidence of brain damage on imaging, or evidence of brain damage on electrophysiological monitoring).

Individual adverse events (66).
Electronic searches Trials will be identi ed through systematic searches within the following databases: Cochrane Central Register of Controlled Trials (CENTRAL), EMBASE, MEDLINE and Science Citation Index Expanded. No language or time restriction will be applied. The reference lists of all relevant trials will be checked as well.
The following MEDLINE search strategy will be used and adapted to other databases: Irvine, CA, USA; Enginmed, Suzhou, China; and Oxyprem, Zürich, Switzerland. Furthermore, we will also identify on-going relevant trials through trial registers in Europe and USA including clinicaltrials.gov.
For ClinicalTrials.gov we will conduct the following search: All trials that are identi ed during the literature search will be uploaded to EndNote (Clarivate, Philadelphia, PA, US). Two authors (MLH and SHS) will screen the titles and abstracts of the identi ed studies. If a study is deemed potentially relevant by the two authors, the full text will be retrieved and assessed for eligibility by the same two authors. If ineligible, the reason for exclusion will be documented. If there is a disagreement between the two authors regarding eligibility or ineligibility, a third author (JCJ) will make the nal decision of inclusion or exclusion. Eligible trials will be included in the systematic review and a Preferred Reporting Items for Systematic Reviews and Meta-Analysis (PRISMA) ow diagram will be included as well. Also, a table displaying the characteristics of excluded studies will be presented in the nal systematic review (67). Analysis of cluster-randomised trials and the rst part, before crossover, of randomised cross-over trials, will be handled as depicted in The Cochrane Handbook for Systematic Reviews of Interventions (68).

Data extraction and management
Once the relevant trials have been included, data extraction will be conducted by the two authors MLH and SHS independently. Any disagreements will be discussed in the author group and a nal decision will be made. The following data will be extracted from each study: General information: title, author(s), year of publication, language of publication, funding sources, potential con icts of interest Methodology: study aim, study design, clinical setting, inclusion and exclusion criteria, type of interventions, cerebral NIRS monitoring unavailable for clinical staff in the control group, outcome measures, time of outcome assessment Sample size: number of participants meeting the criteria for inclusion We will use speci c data extraction forms designed for this purpose. If some of the relevant data is not available in the study report or publication, e.g. if the study does not report all of the prespeci ed outcomes, the trialists will be contacted and asked if they can provide such data. The correspondence with the trialists will be included in the systematic review as an appendix.

Assessment of risk of bias in included studies
Randomised clinical trials with certain methodological aws carry an increased risk of bias (69)(70)(71)(72)(73)(74). Such methodological aws increase the likelihood that the trialists will come to the wrong conclusion by over-or underestimating effect sizes (75). Therefore, it is important to assess the risk of bias in trials included in a systematic review (67). Based on the Cochrane Risk of Bias tool -version 2 (RoB 2) (76) described in The Cochrane Handbook for Systematic Reviews of Interventions (77), we will assess the risk of bias for the following domains: 1) bias arising from the randomisation process, 2) bias due to deviation from intended interventions, 3) bias due to missing outcome data, 4) bias in measurements of outcomes, and 5) bias in selection of the reported results. Risk of bias assessment of the included studies will be conducted by the two authors MLH and SHS, who independently will transfer data into the Stata le. Any disagreement between their assessments will be discussed and, if necessary, a nal decision will be made by a third author (JCJ).
Bias arising from the randomisation process A trial will be considered at low risk of bias if the allocation sequence was adequately concealed (e.g. performed by an on-site locked computer, a central independent unit or sealed, identical envelopes), AND there are no baseline imbalances between the experimental and control group (if any appeared, they must be compatible with chance), AND the allocation sequence generation was adequate (e.g. generated by a computer random numbers generator, a random numbers table, tossing a coin, shu ing cards or drawing lots -the latter three methods will only be considered low risk of bias if the sequence generation was conducted by an independent person with no involvement in the trial), OR if a description of the method for allocation sequence generation is missing.
described for the trial, AND baseline imbalances across intervention groups appear to be by chance, OR if no information is available to answer any of the signalling questions.
A trial will be considered at high risk of bias if investigators were aware of the allocation sequence (70), OR if the method for allocation concealment was not described, AND if baseline imbalance suggest a problem with the randomisation process.
Furthermore, trials where the generation was not at random, or quasi-randomised, will be considered high risk of bias and excluded from the review (73,78) Bias due to deviation from intended interventions A trial will be considered at low risk of bias if participants and clinical staff -and parents in paediatric trials -were unaware of the group allocation during the trial, OR if they were aware of the group allocation during the trial, but any deviation from the intended intervention re ected normal clinical practice, OR if they were aware of group allocation, but any deviation from the intended intervention was unlikely to in uence the outcomes, AND no trial participants were analysed on the basis of the received intervention, instead of on the basis of their randomised allocation group.
A trial will be considered of some concerns if participants and clinical staff -and parents in paediatric trials -were aware of group allocation, AND no information is available regarding deviations from normal clinical practice, which potentially could impact the outcomes AND the deviations from clinical practice were imbalanced between the intervention groups, OR some trial participants were analysed on the basis of the received intervention instead of on the basis of randomised allocation group, but it was deemed as insu cient to signi cantly alter the intervention effect estimate.
A trial will be considered at high risk of bias if participants and clinical staff -and parents in paediatric trials -were aware of group allocation (75,79), AND there were deviations from intended interventions which were unbalanced between the intervention groups, AND likely to affect the outcomes, OR some participants were analysed on the basis of the received intervention instead of on the basis of randomised group allocation, AND it was deemed as su cient to signi cantly alter the intervention effect estimate.
Bias due to missing outcome data A trial will be considered at low risk of bias if there is no missing outcome data, OR if the proportion of missing outcome data is similar between the intervention groups, AND the reasons for missing outcome data are similar, OR if there is evidence that the missing outcomes do not make an important difference to the estimate of the intervention effect (e.g. sensitivity analyses such as 'best-worst, worst-best' case scenario analysis).
A trial will be considered of some concerns if the amount of missing outcome data is unclear, OR there is unclear information regarding the proportion of missing data between intervention groups, AND reason for missing outcome data between intervention groups is unclear, AND there is no evidence that the missing outcome data do not make an important difference to the estimate of the interventions effect (e.g. lack of sensitivity analyses such as 'best-worst, worst-best' case scenario analysis).
A trial will be considered at high risk of bias if the amount of missing data is high (more than 5%), AND missing outcome data between the intervention groups differ, OR the reason for missing outcome data between intervention groups differ, AND there is no evidence that the missing outcome data do not make an important difference to the estimate of the interventions effect (e.g. lack of sensitivity analyses such as 'best-worst, worst-best' case scenario analysis) (73).

Bias in measurement of outcomes
A trial will be considered at low risk of bias if the outcome assessors were blinded to group allocation, OR if the outcome assessors were not blinded to group allocation, but it was deemed that knowledge of group allocation was unlikely to in uence outcome assessment.
A trial will be considered of some concerns if there is no available information to evaluate whether outcome assessors were blinded to group allocation AND if such knowledge could in uence outcome assessment.
A trial will be considered at high risk of bias if outcome assessors were not blinded to group allocation AND it is deemed likely that knowledge of group allocation was likely to in uence outcome assessment (75,80).

Bias in selection of the reported result
A trial will be considered at low risk of bias if the outcome data reported are unlikely to have been selected based on the results of multiple outcome measurements (e.g. different scales to measure the outcome, multiple assessors of the outcome, different time points for assessment of the outcome) within the outcome domain, AND if the outcome data reported are unlikely to have been selected based on the results from multiple outcome analysis.
A trial will be considered of some concerns if it is uncertain whether the outcome data reported have been selected based on the results of multiple outcome measurements (e.g. different scales to measure the outcome, multiple assessors of the outcome, different time points for assessment of the outcome) within the outcome domain OR from multiple outcome analysis.
A trial will be considered at high risk of bias if the reported outcome data are likely to have been selected based on the results of multiple outcome measurements (e.g. different scales to measure the outcome, multiple assessors of the outcome, different time points for assessment of the outcome) within the outcome domain OR from multiple outcome analysis.
Overall risk of bias The included trials will be considered as overall in low risk of bias or high risk of bias. A trial will be considered as overall low risk of bias if the trial is judged as low risk of bias in ALL the above domains. If the trial is considered at high risk of bias, or to be of some concern, in any of the above domains, the trial will be considered as overall in high risk of bias. Within each trial, each outcome result will be assessed for bias, based on the three domains 'bias due to missing outcomes', 'bias in measurements of outcomes', and 'bias in selection of the reported result'. Thus, we will be able to assess not only risk of bias in each trial, but also for each outcome. Additionally, the Grading of Recommendations, Assessment, Development and Evaluation (GRADE) assessment will be used to assess the quality of the body of evidence for all outcomes and summarised in a Summary of Findings The primary conclusion will be based on the analysis of our primary outcome results in all trials assessed as having an overall low risk of bias (58).

Assessment of bias in conducting the systematic review
The systematic review will be conducted according to this protocol. Any deviation in the conduct will be reported in the section 'Differences in the methodology between protocol and review' in the systematic review.

Measures of treatment effect
Dichotomous outcomes For dichotomous outcomes we will calculate risk ratios (RRs) with 95% con dence intervals (CIs) and Trial Sequential Analysis-adjusted CIs (58,82).

Continuous outcomes
For continuous outcomes, i.e. 'Quality of Life', we will calculate the standardised mean difference with a 95% CI and a Trial Sequential Analysis-adjusted CI (58,82).

Handling missing data
We will use the intention-to-treat data from the included trials for both dichotomous and continuous outcomes. For trials with missing or unclear outcome data, the trial authors will be contacted by MLH with JCJ as 'cc'. The trial authors will be requested to provide missing outcome data or to elaborate on unclear outcome data. All correspondence will be attached to the systematic review in an appendix. If it is not possible to obtain missing outcome data, we will not impute the missing data for the primary analysis. Instead, this will be done in the sensitivity analyses.

Data synthesis
All data analyses will be conducted in STATA 16.1 (StataCorp LLC, College Station, Texas, USA). The meta-analysis will be conducted as recommended in The Cochrane Handbook for Systematic Reviews of Interventions (83). For outcomes where data is only available from one trial, the results will be narratively described. If one or more of the included trials reports on multiple intervention arms, we will only include the relevant arms. Furthermore, the population in the control group will be halved for such studies, if two of the comparisons are included in the meta-analysis. An eight-step procedure by Jakobsen et al. will be used to assess if thresholds for statistical and clinical signi cance are crossed (58).
Step onemeta-analysis Fixed-effect and random-effects meta-analysis will be used to estimate the effect of the intervention (84,85). The most conservative point estimate from the two analyses will be used. If the point estimates are similar, the one with the widest CI will be used (58).
Step twoassessment of heterogeneity Statistical heterogeneity will be evaluated by using I 2 statistics, with a threshold for signi cant heterogeneity at p < 0.1 (86), and by visual inspection of forest plots. Clinical heterogeneity will be assessed by evaluating the characteristics of the included trials based on the PICO model (Participants, Interventions, Comparisons, Outcomes). Any signs of heterogeneity will be explored in the subgroup analyses.
Step threeaccounting for multiplicity Since we report on three primary outcomes, a p-value below 0.025 will be considered statistically signi cant for each of the primary outcomes (58).
Step four -Trial Sequential Analysis To control the risks of type I and II errors (87), all primary outcomes will undergo Trial Sequential Analysis and the required meta-analysis information size as well trial sequential boundaries for bene t, harm, and futility will be established (88). If the required number of randomised participants to achieve su cient power is not reached, the con dence interval for the point estimates will be adjusted accordingly by the Trial Sequential Analysis Program (82,88). A relative risk reduction of 20% will be used as the anticipated intervention effect for each primary outcome, an alpha of 2.5% will be used as the acceptable risk of type 1 errors and a beta of 10% will be used as the acceptable risk of type 2 errors.
For cumulative Z-scores that reach below 50% of the diversity-adjusted Trial Sequential Analysis required information size (or sample size), we will downgrade imprecision by two levels for the GRADE assessments (see section on 'Summary of ndings table'). For cumulative Z-scores that reach between 50% to 100% of the diversity-adjusted Trial Sequential Analysis required information size (or sample size), we will downgrade imprecision by one level for the GRADE assessments. For cumulative Z-scores that cross the monitoring boundaries for bene t, futility, or harm, we will not downgrade imprecision for the GRADE assessments.
Step ve -Bayes factor The Bayes factor (89) will be calculated for all primary outcomes and 0.1 will be used as threshold for signi cance (58). An anticipated risk reduction of 20% will be used when calculating the Bayes factor (58).
Step sixsubgroup and sensitivity analysis The following subgroup analyses will be conducted, if possible: 1) Comparison of the intervention effect between trials at overall low to high risk of bias.
2) Comparison of the intervention effect between trials assessing different clinical settings: neonatal intensive care, paediatric intensive care, children during surgery, adult intensive care, and adults during surgery.
3) Comparison of trials without support from the medical device industry compared to trials at risk of such support (71).

4)
Comparison of trials where participants in the control group underwent cerebral NIRS monitoring, but where the oxygenation values were unavailable to the clinical staff, compared to trials where participants in the control group did not undergo cerebral NIRS monitoring at all.
To quantify the potential impact of missing outcome data, the following two sensitivity analysis will be conducted on the three primary outcomes.
1) 'Best-worst case' scenario: we will assume that all participants lost to follow-up in the experimental group either died, suffered from 'moderate or severe persistent cognitive or neurological de cit' or had 'one or more serious adverse events', while all participants lost to follow-up in the control group experienced these events.
2) 'Worst-best case' scenario: we will assume that all participants lost to follow-up in the experimental group suffered died, suffered from 'moderate or severe persistent cognitive or neurological de cit' or had 'one or more serious adverse events', while all participants lost to follow-up in the experimental group did not experience any of these events.
Step sevenassessment of risk of publication bias If at least ten trials are included in the meta-analysis, we will create funnel plots and visually inspect them to assess any potential publication bias. As an additional measure, we will evaluate the funnel plot asymmetry by conducting the Harbord test (90) for dichotomous outcomes and the Egger test for continuous outcome (91).
Step eightassessment of clinical signi cance If the data analyses show statistically signi cant effects of the intervention, we will also assess whether the results are clinically signi cant. The assessment of clinical signi cance will be based on the de nitions of minimal important differences (see 'Trial Sequential Analysis'), the Summary of Findings Table (see  section on 'Summary of Findings table') as well as a thorough evaluation of bene cial and harmful outcomes. Furthermore, we will calculate the numberneeded-to-treat for all dichotomised outcomes (58).

Summary of ndings table
To present the ndings for the pre-speci ed primary, secondary and exploratory outcomes, we will create and include a 'Summary of ndings' table in the systematic review as recommended in the Cochrane Handbook for Systematic Reviews of Interventions (92). The Grading of Recommendations, Assessment, Development and Evaluations (GRADE) approach will be used to assess and rate the quality of the body of evidence, i.e. the certainty in the range of an effect estimate for all pre-speci ed outcomes (81). The GRADE approach evaluates the body of evidence based on the ve following considerations: 1) risk of bias assessment (76,93), 2) heterogeneity or inconsistency of results (94), 3) imprecision of the effect estimates due to wide CIs (95), 4) indirectness of evidence (96), and 5) publication and for-pro t bias (97). Imprecision will be assessed using Trial Sequential Analysis (58). To assess for-pro t bias, we will search for information regarding industry funding for each trial and trial author. If a trial, or an author, is sponsored by the industry, we will judge the trial as in high risk of for-pro t bias. To conduct the rating, we will use the online tool GRADEpro software (www.gradepro.org). The reasons for any up-or down-grading of the certainty of evidence will be described and justi ed in details in the systematic review (92).
As we expect heterogeneity due to the various clinical settings and wide age span of participants in the included studies within this systematic review, we will also create summary of ndings tables for the subgroup analysis within each of the different clinical settings (e.g. neonatal intensive care trials, paediatric intensive care trials, adult intensive care trials and perioperative care trials).

Strengths
The present review has several methodological strengths. First, the methodology is prede ned and registered on PROSPERO before any literature search has been conducted, since this decreases the risk of selective outcome reporting bias of the systematic review (98,99). Any changes to the protocol originating during the peer-review or systematic review process will be described in the systematic review in the section "Differences in the methodology between protocol and review." Second, the protocol includes a thorough description of the methodology which relies on the principles and methods outlined in The Cochrane Handbook for Systematic Reviews of Interventional Research, including a risk of bias assessment of all included studies as a tool to consider systematic errors (100). Third, we plan to use the eight-step procedure by Jakobsen et al. to assess statistical and clinical signi cance for each of the prespeci ed outcomes, which increases the validity of the systematic review (58). The eight-step procedure includes Trial Sequential Analyses, which controls for random errors by establishing if a su cient information size has been reached (82) and whether the boundaries for futility, bene t, or harm have been crossed (88).
These analyses will assist us in determining the need for downgrading due to imprecision.

Limitations
Our review also has important methodological limitations. During the last decade, clinical research of NIRS monitoring has increased rapidly, primarily during surgery but also in the intensive care setting (40,41,57). Parallel to this, the clinical uptake of NIRS monitoring has grown as well (38,39). As all randomised clinical trials evaluating the use of cerebral NIRS monitoring to guide clinical care, irrespectively of age or clinical setting, are eligible for this systematic review, we expect to include trials across various clinical elds. Since the population and study setting will then differ between included trials, there is a potential for both statistical and clinical heterogeneity. We will therefore conduct subgroup analyses on the different populations and clinical settings, e.g. subgroup analyses on studies within neonatal intensive care, paediatric intensive care, adult intensive care, and perioperative monitoring during surgery.
Another limitation of this review is the potential lack of ability to directly affect clinical decision making. The primary analysis will rely on all included trials, irrespective of clinical setting or population. This increases the probability of reaching a su cient information size (82). Although, due to the expectedly large clinical heterogeneity between included trials, it will be di cult to interpret and extrapolate the results of the primary analysis directly to a speci c clinical setting. This issue will be less of a problem in the subgroup analyses. However, there is a possibility that we will not reach a su cient information size for these analysis, thus making it di cult to interpret the results due to high risks of type I and II errors (82).
If the analysis reveals that the intervention has a bene cial effect on any of the prespeci ed outcomes, it will rather be an encouragement to continue the conduct of randomised clinical trials within each clinical setting, in order to reach a su cient information size.

Availability of data and materials
All data generated or analysed will be included in the systematic review.

Competing interests
The authors declare that they have no competing interests.

Funding
This study is funded as part of the SafeBoosC-III project (safeboosc.eu). The Elsass Foundation supports the SafeBoosC-III project through an unconditional and unrestricted grant of DKK 2,700,000.00; the Svend Andersen Foundation with an unconditional and unrestricted grant of DKK 1,000,000.00; and Aage and Johanne Louis-Hansen Foundation with an unconditional and unrestricted grant of DKK 1,000,000,00. These funding sources had no role in the design of this study and will not have any role during its execution, analyses, interpretation of the data, or decision to submit results.
Authors contribution MLH, SHS, JCJ, CG and GG and contributed to the concept and design of this protocol, drafted the manuscript and will give nal approval of the version to be published. EK, JM, WB, MF, AA, TA revised the manuscript critically for important intellectual content, and will give nal approval of the version to be published.