Types of studies

We will include the following types of studies.

• Randomised trials.

• Non‐randomised trials with at least two intervention sites and two control sites.

• Controlled before‐after studies that have at least two intervention and two control sites.

• Interrupted time series studies that have a defined point of time when the intervention occurred and must have a minimum of three points before and after the intervention.

Types of participants

We will include healthcare professionals providing care to patients who suffer major trauma (e.g. Injury Severity Score ≥ 15). We will exclude studies that include patients who predominantly suffer fragility fractures and those who have not been admitted to hospital.

Types of interventions

The intervention of interest will be the establishment of an organised trauma system compared to non‐trauma system care (current normal standard care for most LMICs). An organised trauma system is defined as a pre‐planned approach to the provision of the spectrum of trauma services, including but not limited to, injury prevention and control initiatives, timely transport from the scene of the injury to the trauma care facility, availability of trauma care providers and services when needed, and rehabilitation (WHO 2013).

Types of outcome measures

Electronic searches

The Cochrane EPOC Group Information Specialist will develop the search strategies in consultation with the review authors. We will search the Cochrane Database of Systematic Reviews (CDSR) and the Database of Abstracts of Reviews of Effects (DARE) for primary studies included in related systematic reviews.

We will search the following databases (from inception).

• Cochrane Central Register of Controlled Trials (CENTRAL), including the Cochrane EPOC Group's Specialised Register.

• MEDLINE (from 1946) In‐Process and other non‐indexed citations, OvidSP.

• Embase (from 1974), OvidSP.

• Cumulative Index to Nursing and Allied Health Literature (CINAHL) (from 1980), EbscoHost.

• Directory of Online African Journals (DOAJ).

We will use two methodology search filters to limit retrieval to appropriate study designs: a modified version of the Cochrane Highly Sensitive Search Strategy (sensitivity‐and precision‐maximising version‐2008 revision; Lefebvre 2011) to identify randomised trials (Higgins 2011), and a Cochrane EPOC Group methodology filter to identify non‐randomised trial designs.

Searching other resources

Selection of studies

We will download all titles and abstracts retrieved by electronic searching to a reference management database and remove duplicates. Two review authors (MM and BS) will independently screen titles and abstracts for inclusion. We will code all the potentially eligible studies as either 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. We will retrieve the full‐text study reports/publications. Two review authors (MM and BS) will independently screen the full‐text articles and identify studies for inclusion. We will identify and record reasons for exclusion of the ineligible studies. We will resolve any disagreement through discussion or, if required, we will consult a third review author (TH). We will list excluded studies with reasons for exclusion in the 'Characteristics of excluded studies' tables. We will collate multiple reports of the same study so that each study, rather than each report, is the unit of interest in the review. In addition, we will provide any information we can obtain about ongoing studies. We will record the selection process in sufficient detail to complete a PRISMA flow diagram (Liberati 2009), and a 'Characteristics of excluded studies' tables.

Data extraction and management

We will use a standard data collection form adapted from the Cochrane EPOC Group for extracting study characteristics and outcome data (EPOC 2013a). Two review authors (MM and BS) will independently extract the following study characteristics from included studies and transfer the information into Review Manager 5 (RevMan 5) (RevMan 2014).

• Methods: study design, number of study centres and location, study setting, withdrawals, date of study, and follow‐up

• Participants: number, mean age, age‐range, gender, severity of condition, diagnostic criteria, inclusion criteria, exclusion criteria, and other relevant characteristics

• Interventions: intervention components, comparison, and fidelity assessment

  • We will use the template for intervention description and replication (TIDieR) criteria to asses completeness of reporting interventions (Hoffman 2014); we will use the following criteria

    • Brief name of the intervention

    • Description of rationale, theory, or goal of essential elements to the intervention

    • Description of physical or informational material used for the intervention

    • Description of each of the procedures, activities or processes used in the intervention, including enabling or supporting activities

    • Description of providers (background, expertise, training)

    • Mode of delivery of the intervention (face‐to‐face, by telephone, internet)

    • Description of location(s) infrastructure or relevant features of where intervention occurred

    • Description of: frequency, intensity, duration of the intervention

    • If intervention is tailored or adapted, describe why, when, and how

    • If intervention was modified, description of the changes

    • How well was their intervention planned (if fidelity or adherence was assessed describe how, by who, and if strategies for maintaining fidelity were employed)

    • How well was the intervention actually carried out, description of how the intervention adhered to the plan

• Outcomes: main and other outcomes specified and collected, and time points reported

  • For economic outcome of studies focusing on resource utilisation only, we will use the guidance provided by the Cochrane and Campbell Economic Methods Group (methods.cochrane.org/economics), that includes the following selected criteria

    • Is the chosen time horizon appropriate to include relevant costs and consequences?

    • Is the actual perspective chosen appropriate?

    • Are all important and relevant costs for each alternative identified?

    • Are all costs measured appropriately in physical units?

    • Are all important variables, whose values are uncertain, appropriately subjected to sensitivity analysis?

    • Do the conclusions follow from the data reported?

    • Does the study discuss the generalisability of the results to other settings and patient/client groups?

    • Does the article indicate that there is no potential conflict of interest of study researcher(s) and funder(s)?

    • Are ethical and distributional issues discussed appropriately?

• Notes: funding for trials, notable conflicts of interest of trial authors, and ethical approval

Two review authors (MM and BS) will independently extract outcome data from included studies. We will note in the 'Characteristics of included studies' tables if outcome data were reported in an unusable way. We will resolve disagreements by consensus or by involving a third review author (TH).

Assessment of risk of bias in included studies

Two review authors (MM and BS) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), and the guidance from the Cochrane EPOC Group (EPOC 2013b). We will resolve any disagreement by discussion or by involving a third review author (TH). We will assess the risk of bias according to the following domains.

For randomised trials, non‐randomised trials, and controlled before‐after studies, we will assess the following domains.

• Random sequence generation.

• Allocation concealment.

• Blinding of participants and personnel.

• Blinding of outcome assessment.

• Incomplete outcome data.

• Selective outcome reporting.

• Baseline outcomes measurement.

• Baseline characteristics.

• Other bias.

For interrupted time series studies, we will assess the following.

• If the intervention is independent of other changes.

• If the shape of the intervention effect is prespecified.

• If the intervention is unlikely to affect data collection.

• If knowledge of the intervention is adequately prevented.

• If incomplete outcome data are adequately addressed.

• If the study is free from selective outcome reporting.

• If the study is free from other risks of bias.

We will judge each potential source of bias as either high, low, or unclear and provide a quote from the study report together with a justification for our judgment in the 'Risk of bias' table. We will summarise the 'Risk of bias' judgements across different studies for each of the domains listed. We will consider blinding separately for different key outcomes, where necessary. Where information on risk of bias relates to unpublished data or correspondence with a trial author, we will note this in the 'Risk of bias' table. When considering treatment effects, we will take into account the risk of bias for the studies that contribute to that outcome.

Measures of treatment effect

We will estimate the effect of the intervention using the following.

• Risk ratios (RRs), adjusting for baseline differences for dichotomous data, together with the appropriate associated 95% confidence interval (CI).

• Mean difference (MD) or standardised mean difference (SMD) for continuous data, together with the 95% CI.

Where appropriate, measurement of treatment effect will use the same scale (i.e. quality of life, disability scales). We will ensure that an increase in scores for continuous outcomes can be interpreted in the same way for each outcome, explain the direction to the reader, and report where the directions were reversed, if this was necessary.

Unit of analysis issues

We will perform analysis at the same level as the allocation for the intervention and control group to avoid unit of analysis errors. For clustering designs, such as cluster‐randomised trials, we will perform analysis, adjusting for clustering. We will extract and re‐analyse results not adjusted for clustering. If we find a unit of analysis error, and there is insufficient information to allow re‐analysis, we will contact the original study authors to obtain necessary information; if we are unsuccessful, we will not report the CI and P value, and we will describe the incident as a 'unit of analysis error'.

Dealing with missing data

We will state missing data on the collection and extraction form; if data are missing at random, we will ignore their absence and perform analysis. If data are not missing at random, we will contact the original study authors for additional information; if unsuccessful, we will perform a sensitivity analysis to detect the impact of missing data (Higgins 2011).

Assessment of heterogeneity

We will investigate heterogeneity by visual inspection of forest plots and the Chi² test. Where there is no substantial heterogeneity (I² statistic is less than 50%) we will perform a meta‐analysis (Higgins 2011). If we identify substantial heterogeneity and if there are an adequate number of included studies (more than 10), we will perform subgroup analyses for prespecified subgroups that are either of the following.

• High‐income country (HIC) settings and low‐ and middle‐income country (LMIC) settings.

• Adult trauma patients and paediatric trauma patients.

Assessment of reporting biases

We will assess reporting bias by performing the following.

• We will compare the outcome of studies plotted in a matrix for indicating unreported outcomes.

• We will search protocols, abstracts, or trial registries in databases, such as PubMed, and compare listed outcomes with the reported ones in the related published studies.

• We will compare the methods with result sections of published studies to detected unreported outcomes.

We will contact primary authors to supply the missing information, and if unsuccessful, we will perform a sensitivity analysis (Higgins 2011).

Data synthesis

We will pool data from studies we judge to be clinically homogeneous using RevMan 5 (RevMan 2014). We will undertake meta‐analyses only when this is meaningful, i.e. if the treatments, participants, and the underlying clinical question are similar enough for pooling to make sense. When we encounter skewed data we will note that the data are skewed and consider the implication of this. Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons must be entered into the same meta‐analysis, we will halve the control group to avoid double‐counting.

We do not plan to conduct a full economic analysis given the marked variation in studies we will uncover and the inherent risk of significant heterogeneity. Therefore, in accordance with Cochrane guidelines, we will provide a narrative summary of economic results instead of performing pooled analyses.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses.

• HIC settings and LMIC settings.

• Adult trauma patients and paediatric trauma patients.

The rationale for the first subgroup analysis is that HIC settings and LMIC settings differ in both human and physical resources. Such differences will almost certainly result in heterogeneity and require separate analyses.

The rationale for the second subgroup analysis is that patients of different ages have particular needs, and therefore require different resources, and this may lead to different outcomes.

For both subgroup analyses, we will assess the following.

• Patient outcomes

• Adverse effects or harms

We will apply a test of interaction to assess statistically significant differences between subgroups.

Sensitivity analysis

We will perform sensitivity analyses by employing multiple imputation methods (Higgins 2011), when the following occur.

• There are 'data missing not at random', and if efforts to obtain additional information from primary study authors are unsuccessful.

• If there are studies with high risk of bias included.

• When we have performed re‐analysis (i.e. in a cluster‐randomised trial where the intracluster correlation coefficient was not considered initially) for checking the stability of our results.