Types of studies

We will consider randomised controlled trials that relate to the early management of haemorrhage (within the first 24 hours of injury) with blood products (red blood cells, whole blood, fresh frozen plasma, platelets, cryoprecipitate, including lyophilised plasma, lyophilised platelets, and liquid plasma) in injured patients. We will only include trials that were prospectively registered, unless the final report was published before 2010.

Types of participants

We will include adults and children (with no age restriction) with major bleeding caused by trauma.

Patients with major bleeding will be defined as those with active bleeding and shock, those who require activation of the major haemorrhage protocol, or those predicted to bleed, using a scoring system for haemorrhage in trauma, or as otherwise described by the study authors. We will exclude trials that assessed isolated burns injuries, due to the different mechanism of injury.

Types of interventions

A variety of transfusion strategies is currently used in trauma haemorrhage, but consensus is lacking. Interventions will be examining different ways of using blood products (blood transfusion strategies) in acute bleeding due to trauma. We will consider all trials that are comparing two transfusion strategies, including the following examples:

• Goal‐directed strategy of laboratory clotting tests versus viscoelastic haemostatic assay

• Different ratios of blood products e.g. a transfusion strategy with fresh frozen plasma (FFP), platelets, and red blood cells in a 1:1:1 unit ratio compared to FFP, platelets, and red blood cells in a 1:1:2 ratio).

• Whole blood versus individual blood components

Each blood transfusion strategy must include at least one of: red blood cells or a blood component (FFP, cryoprecipitate, whole blood, platelets, lyophilised or liquid plasma, or lyophilised platelets), and must not contain only recombinant or plasma derived single factor, or multiple coagulation factor concentrates, such as fibrinogen concentrate, prothrombin complex concentrate, and recombinant FVIIa, since these interventions are covered elsewhere (Fabes 2013). There is no standardised transfusion strategy for major bleeding in trauma. The 2016 guidelines from the National Institute for Health and Clinical Excellence (NICE) recommend initial empirical transfusion of red cells and FFP in a 1:1 ratio (NICE 2016). The 2016 European Trauma Society Guidelines recommend transfusion to keep haemoglobin at 70 to 90 g/L, and FFP or fibrinogen replacement in patients with massive bleeding; if further plasma is administered, an optimal plasma to red blood cell ratio of at least 1:2 is suggested. The European guidelines also suggest a threshold‐based approach to platelet transfusion (Rossaint 2016). Both guidelines recommend starting transfusions within 24 hours of injury.

Examples of blood transfusion strategies for trauma patients with major bleeding include:

• blood component transfusion guided by laboratory or global haemostatic tests;

• FFP to platelets to red blood cells in 1:1:1 ratio;

• FFP to platelets to red blood cells in 1:1:2 ratio;

• FFP to red blood cells in 1:2 ratio;

• two pools of early cryoprecipitate, then FFP to red cells in 6:4 ratio;

• modified whole blood;

• individual or combination transfusion of any of the following blood components: red cells, FFP, platelets, cryoprecipitate, lyophilised plasma, lyophilised platelets, and liquid plasma.

We will consider all trials, including placebo‐controlled trials, where the comparator is a non‐blood component (e.g. fluid resuscitation). An example of placebo‐controlled trials might be studies evaluating blood products that are not the current standard, e.g. early cryoprecipitate with empirical transfusion versus saline placebo and empirical transfusion. We recognise that placebo‐controlled trials may be challenging for studies of blood components.

Types of outcome measures

Electronic searches

We will search the following databases for randomised controlled trials (RCTs):

• Cochrane Central Register of Controlled Trials (CENTRAL, The Cochrane Library, current issue; Appendix 1);

• MEDLINE Ovid (1946 to present; Appendix 2);

• Embase Ovid (1974 to present; Appendix 3);

• PubMed (in‐process and epublications ahead of print only; Appendix 4);

• Transfusion Evidence Library (1950 to present; Appendix 5);

• Web of Science Conference Proceedings Citation Index – Science (CPCI‐S, 1990 to present; Appendix 6);

• ClinicalTrials.gov;

• World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP).

The Cochrane Injuries Group will search the two ongoing trial registries. We have listed the search strategies for the other databases in the appendices. We will combine searches in MEDLINE and Embase with adaptations of RCT filters suggested in Chapter 6 of the Cochrane Handbook for Systematic Reviews of Interventions (Lefebvre 2011). We will not limit searches by language, year of publication, or publication type.

We will report the number of papers retrieved, assessed, included, and excluded in the review. We will seek translators for potential reports published in languages other than English.

Searching other resources

We will handsearch the reference lists of included studies to identify further relevant studies, and contact lead authors of the included studies to identify any unpublished material, missing data, or information about ongoing studies.

Selection of studies

One review author (CD) will initially screen all search results for relevance against the eligibility criteria and discard all titles that are clearly irrelevant. Two review authors (HW, NC) will independently screen the remaining titles and abstracts. We will obtain the full texts of reports that appear to be eligible, or of which we are unsure, to determine their ultimate relevance. We will seek further information from the trial authors when articles contain insufficient data to make a decision about eligibility. We will resolve differences of opinion through discussion and consensus, and consult with a third review author (SS) if necessary.

Data extraction and management

Two review authors (HW, JB) will independently extract data onto study‐specific data extraction forms. They will pilot the forms on two relevant RCTs, and adjust the form as necessary after discussion. Throughout the data extraction process, they will resolve any disagreement by discussion with a third review author (NC). If agreement cannot be reached, they will consult with a fourth author (SS).

The review authors will not be blinded to the names of authors, institutions, journals, or outcomes of the trials. If considered relevant, they will request copies of the trial protocols from the trial authors.

Data will include:

1. Trial details: review author’s name; year; date of data extraction; first author of study; author’s contact address (if available); objectives of the trial; country of origin; clinical setting; number of centres; recruitment dates; method of sequence generation; allocation concealment; blinding (of clinicians, participants, and outcome assessors); inclusion and exclusion criteria; definition of major haemorrhage; definition of coagulopathy; comparability of groups; length of follow‐up; use of intention‐to‐treat analysis; funding source.

2. Participant data: age; gender; mechanism of injury (blunt or penetrating trauma); isolated traumatic brain injury; percentage of patients on anticoagulant or anti‐platelet therapy; Injury Severity Score (ISS); total number of participants recruited; total number randomised; total number analysed for endpoints; losses to follow‐up and dropouts.

3. Interventions: nature of experimental and control interventions; timing, dosage and route of intervention; compliance to interventions; additional interventions given including tranexamic acid.

4. Outcomes: primary and secondary outcomes; outcome cutoffs; incomplete outcome data; conclusions reported.

Assessment of risk of bias in included studies

Two review authors will independently assess bias using the Cochrane tool. To assess risk of bias, we will address the following questions in the 'Risk of bias' table for each included study (Higgins 2011).

1. Was the allocation sequence adequately generated?

2. Was allocation adequately concealed?

3. Was knowledge of the allocated intervention adequately prevented (i.e. blinded) throughout the study for participants, study personnel, and outcome assessors?

4. Were incomplete outcome data adequately addressed for the main outcome?

5. Are reports of the study free of selective outcome reporting?

We will report 'Risk of bias' domains 2, 3, 4, and 5 separately for each of the two main outcomes, and where data allow, for the secondary outcomes.

We will categorise individual studies as being at low, high, or unclear overall risk of bias according to the following:

• low risk of bias ‐ all domains were at low risk of bias (plausible bias unlikely to seriously alter the results);

• unclear risk of bias ‐ one or more domains had an unclear risk of bias (plausible bias that raises some doubt about the results); or

• high risk of bias ‐ one or more domains were at high risk of bias (plausible bias that seriously weakens confidence in the results).

We anticipate that knowledge of the allocated intervention will be difficult to blind from clinicians and participants. However, we believe that it would be possible to blind knowledge of the allocated intervention from outcome assessors. We will bear these considerations in mind when assessing risk of bias for domain 3 above. We will record all quotes from studies separately from our judgement in the 'Risk of bias' table.

Measures of treatment effect

We will calculate risk ratios (RR) for dichotomous data outcomes with 95% confidence intervals (CI). Where the number of observed events is small (less than 5% of sample per group), and where trials have balanced treatment groups, we will report the Peto odds ratio (OR) with 95% CI (Deeks 2011). We will express treatment effects for continuous data outcomes as mean differences (MD) with 95% CI; if the outcomes are measured using different scales, we will use standardised mean differences (SMD) with 95% CI.

Unit of analysis issues

We anticipate that the patient will be the unit of analysis.

We do not expect to encounter any cluster‐randomised trials, but if we do identify any, we will treat them in accordance with the advice given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will treat multi‐arm trials in accordance with the advice given in Chapter 16 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

Dealing with missing data

We will attempt to contact the trial authors to obtain missing data or to clarify unclear data. For each included study, we will record the number of participants lost to follow‐up. Where possible, we will analyse data on an intention‐to‐treat basis, but if there are missing data, we will present per‐protocol analyses. Where standard deviations are not reported, we will try to determine these from standard errors, confidence intervals, or exact P values.

Assessment of heterogeneity

We will use the I² statistic to quantify the possible degree of heterogeneity of treatment effects between trials. We will assume moderate heterogeneity when the I² is higher than 50% and considerable heterogeneity when it is higher than 80%. Due to the nature of the studies, we expect moderate heterogeneity, therefore, in the first instance, we will use a random‐effects model. We will explore potential causes of heterogeneity by sensitivity and subgroup analysis (Deeks 2011).

Assessment of reporting biases

Although every effort will be made to identify unpublished studies, we will assess publication bias using funnel plots, provided there are at least 10 studies included in each meta‐analysis.

Data synthesis

If studies are considered sufficiently homogeneous, we will conduct a meta‐analysis, according to Cochrane recommendations (Deeks 2011). We will enter data into Review Manager 5 (Review Manager 2014) for statistical analysis.

Where meta‐analysis is feasible, we will use the random‐effects model for pooling the data. For dichotomous outcomes we will use the Mantel‐Haenszel method or the Peto method as necessary, and the inverse variance method for continuous outcomes, according to the recommendations of Chapter 9 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011). If heterogeneity is found to be above 80%, we will not perform a meta‐analysis, but will perform a qualitative analysis, grouping similar transfusion strategies, and commenting on the results as a narrative.

A network meta‐analysis would not be appropriate due to issues with transitivity.

Subgroup analysis and investigation of heterogeneity

If there are sufficient data, we will perform subgroup analyses to see if there are significant differences in treatment effect:

1. Children versus adults for patients treated with the same protocol (since different definitions of coagulopathy apply).

2. Studies of older adults (over 65 years of age) compared with younger adults, since older patients are more likely to have co‐morbidities, such as cardiovascular disease, and possible differences in efficacy of transfusion interventions.

3. Studies of patients with traumatic brain injury, in view of the effect of a central nervous system injury on coagulopathy, and the possible differences in efficacy of interventions in this group.

If we identify any other subgroup effects, we will clearly identify them as hypothesis‐generating. We will use the test for subgroup differences provided in Review Manager 5, to establish whether the subgroups are statistically significantly different from one another.

Sensitivity analysis

If data are available, we will perform sensitivity analyses to explore aspects of trial and review methodology. These will include exploring the effects of removing trials at high or unclear risk of the following domains of bias:

1. selection bias (reflecting lack of confirmation of random sequence generation and allocation concealment);

2. detection bias (reflecting lack of assessor blinding);

3. attrition bias, such as from high levels of missing data.

We will perform trial sequential analysis to explore the robustness of any statistically significant effects found for the review's primary outcomes that did not meet the expected sample size.