Types of studies

We will include randomized clinical trials without consideration of publication status, blinding status or language. We will contact the investigators and the authors in order to retrieve relevant data.

We will only include unpublished trials if trial data and methodological descriptions are provided either in written form or by direct contact with the authors.

We will exclude trials using quasi‐randomization and observational studies to study benefits. However, we will establish an appendix enumerating the findings from observational studies regarding adverse effects. We will exclude crossover trials even if they compare high FIO₂ with standard FIO₂ during the perioperative period.

Types of participants

We will include surgical patients aged equal to or greater than 18 years and undergoing acute or elective surgery .

Types of interventions

A high FIO₂ of 60% or above compared with a control FIO₂ of 40% or below during surgery or both during surgery and while in the postanaesthetic care unit.

Types of outcome measures

Electronic searches

We will search the Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library, current issue); SilverPlatter MEDLINE (WebSPIRS) (1950 to date); SilverPlatter EMBASE (WebSPIRS) (1980 to date); SilverPlatter BIOSIS (WebSPIRS) (1993 to date); International Web of Science (1964 to date); Latin American Caribbean Health Sciences Literature (LILACS via BIREME) (1982 to date); the Chinese Biomedical Literature Database; advanced Google, and Cumulative Index to Nursing and Allied Health Literature (CINAHL via EBSCO host) (1980 to date).

We will perform a systematic and sensitive search strategy to identify relevant randomized clinical trials without language or date restrictions. The search will be conducted within six months of the date the draft review is emailed to the editorial office. For specific information regarding our search strategies please see the Appendices (Appendix 2, MEDLINE; Appendix 3, EMBASE; Appendix 4, CENTRAL; Appendix 5, Web of Science; Appendix 6, CINAHL).

We will search for ongoing clinical trials and unpublished studies on the following Internet sites:

1. Current Controlled Trials;

2. ClinicalTrials.gov;

3. www.centerwatch.com;

Searching other resources

We will handsearch the reference list of reviews, randomized and non‐randomized studies, and editorials for additional studies. We will contact the main authors of studies and experts in this field to ask for any missed, unreported or ongoing trials.

Selection of studies

Two authors (JW and CM) will independently evaluate all relevant trials and provide a detailed description of the included and excluded articles under the sections 'Characteristics of included studies' and 'Characteristics of excluded studies', respectively. We will also provide a detailed description of our search results.

Data extraction and management

We will screen the titles and abstracts in order to identify studies for eligibility. JW and CM will independently extract and collect the data on a standardized paper form (Appendix 7). We will not be blinded to the author, institution, or the publication source of trials. We will resolve disagreements by discussion. We will approach all corresponding authors of the included trials for additional information relevant to the review's outcomes measures and risk of bias components. For more specific information please see the section 'Contributions of authors'.

Assessment of risk of bias in included studies

The validity and design characteristics of each trial are to be evaluated. To draw conclusions about the overall risk of bias for an outcome it is necessary to evaluate the trials for major sources of bias, also defined as domains (random sequence generation, allocation concealment, blinding, incomplete outcome data, selective outcome reporting, and other sources of bias). The Cochrane Collaboration’s recommended tool for assessing risk of bias is neither a scale nor a checklist but rather a domain‐based evaluation. Any assessment of the overall risk of bias involves consideration of the relative importance of the different domains (Higgins 2008).

Even the most realistic assessment of the validity of a trial may involve subjectivity since it is impossible to know the extent of bias (or even the true risk of bias) in a given trial. Some domains affect the risk of bias across outcomes in a trial, for example sequence generation and allocation sequence concealment, while others such as blinding and incomplete outcome data may have different risks of bias for different outcomes within a trial. Thus, the risk of bias is not the same for all outcomes in a trial. We will perform separate sensitivity analyses for patient‐reported outcomes (subjective outcomes) and for mortality (Higgins 2008).

We will define the trials as having low risk of bias only if they adequately fulfil the criteria listed in the Cochrane Handbook (Appendix 8) and will perform summary assessments of the risk of bias for each important outcome (across domains) within and across studies. We will apply a 'risk of bias graph' and a 'risk of bias summary figure' (Higgins 2008).

We will present results for all outcomes including adverse events in a 'Summary of findings' (SOF) table (Higgins 2008).

As there is no sufficiently well designed formal statistical method to combine the results of trials with high and low risk of bias, the principle approach to incorporating risk of bias assessments in Cochrane reviews is to restrict meta‐analyses to studies at low (or lower) risk of bias (Higgins 2008). We will use the risk of bias (ROB) table described in the Cochrane Handbook, section 8.5 (Higgins 2008) as a tool for assessing risk of bias in included studies. We will assess the risk of bias in the different domains as described in Appendix 8.

Measures of treatment effect

We will report length of stay in hospital after surgery, in days, as a continuous outcome and the intervention effect as mean difference with 95% confidence interval. All other outcomes are dichotomous and will be reported as relative risks (RR) with 95% confidence limits. For mortality, which we expect will be a rare outcome, the Peto odds ratio (OR) will be calculated. We will also calculate the risk difference (RD) with 95% confidence interval and subsequently numbers needed to treat, if possible.

Unit of analysis issues

Number of events in all binary meta‐analyses, and days in the meta‐analysis of length of stay in hospital after surgery.

Dealing with missing data

We will contact all the first authors and contact persons of the trials that have missing data in order to retrieve the relevant data. A modified intention‐to‐treat (ITT) analysis will be performed including, if possible, all randomized patients who underwent surgery or who did not withdraw their consent before surgery.

ITT analysis is recommended in order to minimize bias in the design, follow up and analysis of the efficacy of randomized clinical trials. It gives a pragmatic estimate of the benefit of a change in treatment policy rather than a measure of the potential benefit in patients who receive treatment exactly as planned (Hollis 1999). Full application of ITT is possible only when complete outcome data are available for all randomized participants. Despite the fact that about half of all published reports of randomized clinical trials state that ITT analysis was used, handling of deviations from randomized allocation varies widely and many trials have missing data for the primary outcome variable.Methods used to deal with this are generally inadequate, potentially leading to bias (Hollis 1999).

Performing an ITT analysis in a systematic review is not straightforward since review authors must decide how to handle outcome data missing from the contributing trials (Gamble 2005). No consensus exists about how missing data should be handled in ITT analyses and different approaches may be appropriate in different situations (Higgins 2008; Hollis 1999).

In cases of missing data, for our primary outcomes we will use a 'complete‐case analysis' by simply excluding all participants with the outcome missing from the analysis. Additionally, we will conduct sensitivity analyses for our primary outcomes by applying best and worst case scenarios.

The best case scenario is: all patients lost to follow up in the high FIO₂ group survived and all patients lost to follow up in the FIO₂ below 40% group died; all patients lost to follow up in the high FIO₂ group did not have a SSI and all patients lost to follow up in the FIO₂ below 40% group did have a SSI. The worst case scenario is: all patients lost to follow up in the high FIO₂ group died and all patients lost to follow up in the FIO₂ below 40% group survived; all patients lost to follow up in the high FIO2 group had a SSI and all patients lost to follow up in the FIO₂ below 40% group did not have a SSI.

Selective outcome reporting occurs when non‐significant results are selectively withheld from publication (Chan 2004). It is defined as the selection, on the basis of the results, of a subset of the original recorded variables for inclusion in the publication of a trial. The most important types of selective outcome reporting are: selective omission of outcomes from reports; selective choice of data for an outcome; selective reporting of analyses using the same data; selective reporting of subsets of the data and selective under‐reporting of data (Higgins 2008). Statistical methods to detect within study selective reporting are still in their infant stage. We will explore selective outcome reporting by comparing publications with their protocols, if the latter are available.

Assessment of heterogeneity

The degree of heterogeneity observed in the results is quantified using diversity (D²) (Wetterslev 2009) and inconsistency factor (I²) statistics, which can be interpreted as the proportion of the total variation observed between the trials that is attributable to differences between trials rather than sampling error (chance) (Higgins 2002). P ≤ 0.10 indicates significant heterogeneity, and the suggested I² statistic thresholds for low, moderate, and high heterogeneity are 25% to 49%, 50% to 74%, and ≥ 75% respectively (Higgins 2003). If I² = 0, we will report the results using the fixed‐effect model only. In the case of I² > 0 we will report the results using both the random‐effects and the fixed‐effect models. However, we believe that there is little value in using a fixed‐effect model in cases of substantial heterogeneity, which we suspect will be present in this review due to inclusion of various patient types, use of adjuvant gases, definitions of SSI, and outcome reporting. So we will emphasize the results from the random‐effects model analysis unless a few trials dominate the meta‐analysis (for example more than 50% of the cumulated fixed weight percentage). Additionally, in cases of I² > 0 (for the mortality and SSI outcomes) we will seek to determine the cause of heterogeneity by performing meta‐regression analyses and relevant subgroup and sensitivity analyses. We aim to combine trial results in a meta‐analysis only when clinical heterogeneity is low to moderate.

Assessment of reporting biases

Publication bias occurs when the publication of research results depends on their nature and direction (Dickersin 1990). We will examine this by providing funnel plots in order to detect either publication bias or a difference between smaller and larger studies (small study effects), expressed as asymmetry of the funnel plot (Egger 1997). In case of asymmetry we will apply the 'Arcsine‐Thompson test' as proposed by Rücker (Rücker 2008).

Funding bias is defined as the biases in the design, outcome, and reporting of industry sponsored research in order to show that a drug has a favourable outcome (Bekelman 2003). Relationships between industry, scientific investigators and academic institutions are widespread and often result in conflicts of interest (Bekelman 2003). We may conduct a sensitivity analysis in order to examine the role of funding bias, if relevant (see Sensitivity analysis).

Data synthesis

We will use Review Manager software (RevMan 5.0) as the statistical software. We will calculate the relative risk (RR) with 95% confidence intervals (CI) for dichotomous variables (binary outcomes). We will also calculate the risk difference (Keus 2009); if the results are similar we will only report the RR. Additionally, we will calculate mean difference (MD) as the measure of absolute change with 95% CI for continuous outcomes. We will use D² (Wetterslev 2009) and I² statistics (Higgins 2002) to describe heterogeneity among the included trials. We will explore causes of substantial heterogeneity by meta‐regression using Comprehensive Meta‐Analysis (CMA version one) and Stata version nine. We will use the Chi² test to provide an indication of heterogeneity between studies, with P ≤ 0.10 considered significant.

Adverse effects may be rare but serious, and hence important (Sutton 2002), when meta‐analysis is applied for combining results from several trials that have binary outcomes (that is event or no event). Firstly, we will apply the Peto odds ratio (POR) in the case of small event proportions. Most meta‐analytic software packages do not include options for analyses to calculate RR when included trials have 'zero events' in both arms (intervention versus control). Exempting these trials from the calculation of RR and CI may lead to overestimation of a treatment effect as the control event proportion may be overestimated. Thus we will perform a sensitivity analysis by applying empirical continuity corrections to our zero event trials as proposed by Sweeting et al (Keus 2009; Sweeting 2004), by applying an imaginary small mortality in both arms.

Meta‐analyses may result in type 1 errors due to sparse data and repeated significance testing when meta‐analyses are updated with new trials (Brok 2008; Brok 2009; Thorlund 2009; Wetterslev 2008; Wetterslev 2009). Systematic errors from trials with high risk of bias, outcome reporting bias, publication bias, early stopping for benefit and small trial bias may result in spurious P values.

In a single trial, interim analysis increases the risk of type 1 errors. To avoid type 1 errors, group sequential monitoring boundaries (Lan 1983) are applied to decide whether a trial could be terminated early because of a sufficiently small P value, that is the cumulative Z curve crosses the monitoring boundary. Sequential monitoring boundaries can be applied to meta‐analyses as well and are called trial sequential monitoring boundaries. In 'trial sequential analysis' (TSA) the addition of each trial in a cumulative meta‐analysis is regarded as an interim meta‐analysis and helps to decide whether additional trials are needed (Wetterslev 2008). So far several meta‐analyses and reviews have been published, including an increasing number of trial results as new trials have been published (Al‐Niaimi 2009; Chura 2007; Qadan 2009). It therefore seems appropriate to adjust new meta‐analyses for multiple testing on accumulating data to control the overall type 1 error risk in cumulative meta‐analysis (Pogue 1997; Pogue 1998; Thorlund 2009; Wetterslev 2008).

The idea in TSA is that if the cumulative Z curve crosses the boundary a sufficient level of evidence is reached and no further trials may be needed. However, there is insufficient evidence to reach a conclusion if the Z curve does not cross the boundary or does not surpass the required information size. To construct the trial sequential monitoring boundaries (TSMB) the required information size is needed and will be calculated as the least number of participants needed in a well‐powered single trial (Brok 2008; Pogue 1998; Wetterslev 2008). We will adjust the required information size for heterogeneity with the diversity adjustment factor (Wetterslev 2009). We will apply TSA, since it prevents an increase of the risk of type 1 error (< 5%) due to potential multiple updating and testing on accumulating data, whenever new trial results are included in a cumulative meta‐analysis (Pogue 1997; Pogue 1998). This provides us with important information in order to estimate the level of evidence on the experimental intervention (Pogue 1997; Pogue 1998; Thorlund 2009). Additionally, TSA provides important information regarding the need for additional trials and their required sample size (Wetterslev 2008; Wetterslev 2009). We will apply trial sequential monitoring boundaries according to an information size suggested by the trials with low risk of bias (Wetterslev 2008; Wetterslev 2009) and an a priori 20% relative risk reduction (RRR) of SSI using a control event proportion suggested by large observational studies and by the pooled estimate of the event proportion in the included trial control groups. As mortality seems low in the trials conducted so far, and hence the ability to detect small intervention effects is low, we will also perform a TSA with an information size estimated based on an a priori 35% RRR of mortality (Wetterslev 2008; Wetterslev 2009).

Subgroup analysis and investigation of heterogeneity

We plan to do the following subgroup analyses by assessing the benefits and harms of high FIO₂:

1. according to the trials using inspiratory oxygen with or without nitrous oxide;

2. according to the trials using inspiratory oxygen with an FiO₂ of 80% or higher compared to trials using an FiO2 equal to or higher than 60% but lower than 80%;

3. according to the trials using a high FiO₂ only during surgery or during both surgery and postoperative care;

4. in participants undergoing abdominal surgery according to type of surgery, that is a) all kind of abdominal surgery, b) procedures requiring laparotomy, c) upper laparotomy if possible, d) lower laparotomy if possible, e) laparoscopic procedures;

5. according to type of surgery (abdominal, orthopaedic, other);

6. according to whether follow up of SSI was within or equal to 14 days or longer than 14 days.

We will only make inferences from the subgroup analyses in terms of implications for clinical practice if the the overall analysis of one of the co‐primary outcomes becomes statistically significant. Where the analyses of the co‐primary outcomes do not become statistical significant, we intend to reference them in 'Implications for research' to provide possible hypothesis generating for further research.

We will compare intervention effects in subgroups using a test of interaction (Altman 2003). We consider P < 0.05 indicative of significant interaction between the high FIO₂ effect on SSI and the subgroup category (Higgins 2008, Chapters 9.6.1 and 9.7).

We will explore the causes of moderate to high heterogeneity using meta‐regression that includes the following covariates, if possible: mean age of trial population at baseline; mean body mass index (BMI) of trial population at baseline; fraction of diabetic patients in the trial population at baseline; fraction of smokers in the trial population at baseline; and fraction of patients with a contaminated or dirty infected surgical field during surgery.

Sensitivity analysis

1. Comparing estimates of the pooled intervention effect in trials with low risk of bias to estimates from trials with high risk of bias (i.e., trials having at least one unclear or high risk of bias component).

2. Comparing estimates of the pooled intervention effect in trials based on different components of risk of bias (random sequence generation, allocation concealment, blinding, follow up, intention to treat).

3. Assessment of the benefits and harms of high FIO₂ by conducting a continuity correction of trials with zero events.

4. Assessment of the benefits and harms of high FIO₂ by conducting sensitivity analyses excluding the smallest or the largest trial.

5. Assessment of the benefits and harms of high FIO₂ when excluding data from trials only published as abstracts.

6. Assessment of the benefits and harms of high FIO₂ when excluding data from trials with commercial funding.

We will calculate RR with 95% CI and apply a complete case analysis, if possible, for the sensitivity and subgroup analyses based on the mortality and SSI primary outcomes.