Types of studies

We will include all randomized controlled trials (RCTs)  and quasi RCTs irrespective of their language or publication status(published, unpublished or in abstract form) and evaluate the effects of including quasi‐RCTs in sensitivity analyses for the components of the risk of bias.   

We will include RCTs that report surrogate/physiological outcomes, provided data on any of the outcomes described in this systematic review are available.

Types of participants

We will include adult patients admitted to an ICU for invasive mechanical ventilation with a diagnosis of acute respiratory failure or acute on chronic respiratory failure and fulfilling the criteria for ALI/ARDS as defined by the American‐European Consensus Conference (Bernard 1994). We will also evaluate studies published prior to 1994 to establish consistency with this definition.

We will exclude the following.

1. Pediatric population as defined by the authors (unless they constitute less than 10% of the sample in each arm).

2. Trials evaluating ventilation for patients with chronic respiratory failure (obstructive sleep apnoea, chronic neuromuscular disorders etc.).  

3. Patients treated only with non‐invasive respiratory support. Use of non‐invasive ventilatory support prior to invasive ventilatory support would not preclude inclusion to the trial.

Types of interventions

PCV or pressure controlled inverse ratio ventilation or an equivalent pressure controlled model compared with volume controlled ventilation or an equivalent volume controlled mode.

Types of outcome measures

Electronic searches

Searching other resources

Selection of studies

Two authors (BC, JVP) will independently scan the titles and abstracts identified by the search strategy. We will evaluate the full text of the potentially relevant articles to determine if they meet the eligibility criteria to be considered in the review. We will consider trials meeting the criteria for inclusion (randomized trials comparing pressure versus volume controlled ventilation) for inclusion provided one of the stated outcomes described in the protocol is presented. In case of any ambiguity or insufficient data, we will contact the authors of the articles for further clarification and additional information. We will resolve any disagreement by consensus or by consulting the senior author (GJ). We will scrutinize each trial report to ensure that multiple publications from the same trial are included only once, and will link all such reports to the original trial or study report in the reference list of included studies. We will exclude studies that do not meet the criteria and document the reason for exclusion.

Data extraction and management

BC and JVP will independently extract data using pre‐tested data extraction forms (see Appendix 6), and PT will independently validate this process. We will extract the following information from each included study.

1. General information: title, authors, source, contact address, country, published or unpublished, language, and year of publication.

2. Trial characteristics including design and quality assessment criteria as detailed below.

3. Participants: inclusion and exclusion criteria, sample size, baseline characteristics, number of patients allocated to each group. We will also record Acute Physiology and Chronic Health Evaluation (APACHE) and Simplified Acute Physiology Score (SAPS II/APACHE II) and the lung compliance at admission.

4. Interventions: whether pressure or volume controlled ventilation; the baseline plateau pressure and tidal volume set at admission; Inspiratory time (Ti/T total) during which the tidal volume will be delivered.

5. Co‐interventions: we will record co‐interventions that may influence outcome in this subset of patients(e.g.: steroids, inhaled nitric oxide) if the data are provided. If we observe significant heterogeneity in the primary analysis pertaining to the intervention, we will perform a sensitivity analysis to assess the effect of co‐interventions.

6. Outcomes: in‐ICU mortality, in‐hospital mortality, and mortality at longest follow‐up; extra‐pulmonary organ failure; ICU length of stay (mean ± SD); hospital length of stay (mean ± SD); duration of ventilation; quality of life post discharge; infective complications; barotrauma; numbers experiencing each outcome; time to onset of each outcome; and number of dropouts and withdrawals with reasons.

For every outcome, we will extract the number analyzed and the number randomized in each treatment group to allow for the assessment of losses to follow up. We will resolve any disagreements about data extraction by referring to the trial report and by discussion. We also have a third author (PT) to adjudicate should disagreements not be resolved through discussion. Where data are insufficient or missing, we will attempt to contact the trial authors.

For continuous outcomes, we will extract the arithmetic mean values, standard deviations, and the number of participants on whom the outcome was assessed in each of the trial arms. We will note whether the numbers assessed in the trial were the number of participants that completed the trial or the number randomized. If medians have been reported we will extract ranges, or interquartile ranges.

Assessment of risk of bias in included studies

Two authors (BC and JVP) will assess the methodological quality of each trial on the following six components: sequence generation, allocation concealment, blinding or masking, incomplete outcome data, selective outcome reporting, and other biases. For each of these components, we will assign a judgment regarding the risk of bias as 'yes', 'no', or 'unclear' (Higgins 2008b). The judgement for each entry involves answering a question, with 'Yes' answers indicating low risk of bias, 'No' indicating high risk of bias, and 'Unclear' indicating either lack of information or uncertainty over the potential for bias. For example, if the precise mode of allocation concealment is not stated and not obtainable from trial authors, then the trial would be judged as unclear for the risk of bias in this domain. We will attempt to contact the trial authors for clarification when methodological details are unclear. Blinding of clinicians or research personnel would not be feasible in this study. If statisticians are blinded to the results, it would be recorded. We will record follow‐up to be adequate if more than 90% of the randomized participants were included in the final analysis, inadequate if less than or equal to 90% were included, or unclear if this information is not available from the report or trial authors. We will record these assessments in the 'Risk of Bias' tables (Appendix 7) in RevMan 2008, and summarize them in a 'Risk of bias' graph and summary figures. We will use these assessments to perform a sensitivity analysis based on methodological quality when appropriate. We will resolve any conflicts in assessment through discussion and the third author (PT) will independently validate these assessments.

Measures of treatment effect

When outcomes are dichotomous we will use risk ratios; when outcomes are continuous, we will use the mean difference, each with 95% confidence intervals (95% CI).

Unit of analysis issues

If included trials are randomized by clusters and if the results have been adjusted for clustering, we will combine the adjusted measures of effects of these cluster‐randomized trials. If results have not adjusted from clustering, we will attempt to adjust the results for clustering, by multiplying the standard errors of the estimates by the square root of the design effect where the design effect is calculated as D_Eff = 1 + (M ‐ 1) ICC, where M is the average cluster size and ICC is the intra‐cluster coefficient. If this is not possible, we will not combine data in a meta‐analysis, but will present the results in an additional table.

If outcomes are reported both at baseline and at a follow‐up or at trial endpoints, we will extract both the mean change from baseline and the standard deviation of this mean for each treatment group, as well as the same for end‐point data. We will use end‐point data preferentially, but will combine end‐point and change scores for outcomes from trials for each comparison if end‐point data are not available.

If count data are reported in trials, we will extract the total number of events in each group and the total amount of person‐time at risk in each group. We will also record the total number of participants in each group. If this information was not available, we shall attempt to extract alternative summary statistics such as rate ratios and confidence intervals, if available. if count data were presented as dichotomous outcomes, we will extract the number of participants in each intervention group and the number of participants in each intervention group who experienced at least one event. If count data are presented as continuous outcomes or as a time‐to‐event outcomes, we will attempt to extract the same information as outlined for continuous and time‐to‐event outcomes.

If time‐to‐event outcomes are reported, we will extract the estimates of the log hazard ratio and its standard error. If standard errors are not available we will extract alternative statistics such as confidence intervals or P values.

Dealing with missing data

We will attempt to obtain missing data from trial authors. Where possible, we will extract data to allow an intention‐to‐treat analysis in which all randomized participants are analyzed in the groups to which they were originally assigned. If there is discrepancy in the number randomized and the numbers analyzed in each treatment group, we will calculate the percentage loss to follow‐up in each group and report this information. If drop‐outs exceed 10% for any trial, we will assign the worse outcome to those lost to follow up for dichotomous outcomes and assess the impact of this in sensitivity analyses with the results of completers.

For continuous data that are missing standard deviations, we will either calculate these from other available data such as standard errors, or will impute them using methods suggested in Higgins 2008a . We will not make any assumptions about loss to follow‐up for continuous data and will analyze results for those who complete the trial.

Assessment of heterogeneity

We will assess heterogeneity between the trials by visual examination of the forest plot to check for overlapping confidence intervals, using the Chi² test for homogeneity and a 10% level of significance, and the I² statistic to assess inconsistency (the percentage of the variability in effect estimates that is due to heterogeneity rather than sampling error). We acknowledge that thresholds for interpreting I² can be misleading, as the interpretation depends on  several factors such as  the (i) magnitude and direction of effects and (ii) strength of evidence for heterogeneity (e.g. P value from the Chi² test, or a confidence interval for I²). When interpreting I², we will be guided by (Deeks 2008) that: 

• 0% to 40%: might not be important;

• 30% to 60%: may represent moderate heterogeneity;

• 50% to 90%: may represent substantial heterogeneity;

• 75% to 100%: represents considerable heterogeneity

Since this statistical assessment of heterogeneity using the above guidelines poses problems in terms of overlapping ranges of I² (e.g. 35% and 55%), in general we shall interpret a value of I² of 50% or greater to denote substantial heterogeneity, and detail below measures to deal with substantial heterogeneity.

Assessment of reporting biases

We will assess all included studies' adequacy of reporting of data for pre‐stated outcomes and for selective reporting of outcomes. We will note judgements based on the risk of selective reporting in the 'Risk of bias' tables that follows each study in Characteristics of included studies. We will also report risk of selective outcome reporting in the results under Assessment of risk of bias in included studies.

We will attempt to identify published, un‐published and on‐going trials by our search methods. We will assess the likelihood of potential publication bias using funnel plots, provided that there are at least ten trials. We will use a funnel plot for the primary outcome to provide a visual assessment of whether treatment estimates are associated with study size. We will use a test based on arcsine transformation of observed risks, with explicit modelling of between‐study heterogeneity (Rücker 2008), and seek statistical advice on using the version of the arcsine test including random‐effects (AS+RE) when Tau ₂ is more than 1.0.

Data synthesis

We will synthesize dichotomous data using pooled and weighted risk ratios. We will combine continuous data summarized by arithmetic means and standard deviations using the mean differences. If continuous data have been summarized using geometric means, we will combine them on the log scale using the generic inverse variance method and report them on the natural scale.

We will compare count data using rate ratios when the total number of events in each group and the total amount of person‐time at risk in each group are available, or by relative risks or mean difference if data are presented in dichotomous or continuous forms respectively. Hazard ratios from survival data will be combined on the log scale using the inverse variance method and presented on the natural scale.

One author (BC) will enter data using RevMan 2008; JVP and PT will independently check the veracity of the data entered. If data can be meaningfully combined, we will pool risk ratios of the comparisons for dichotomous outcomes using the inverse variance. We will pool the mean difference between comparisons for continuous outcomes using the inverse variance method; we will calculate both estimates with their 95% confidence intervals (CI). We will estimate pooled effects for rare events (frequency of complications or adverse events) using the Peto odds ratio (Higgins 2008a ).

Continous data for outcomes such as duration of ventilation may be skewed where the mean is not at the centre of the distribution. If data from trials are skewed and this not considerable, we will use this data in meta‐analysis. If the skew is considerable (ratio of the observed mean minus lowest possible value divided by the SD‐ is less than one), then we will try and obtain appropriate data summaries or log‐transform the data from all included studies and use the generic inverse variance method to pool data. If this is not possible, then we will present this data in an additional table.

Subgroup analysis and investigation of heterogeneity

We will uniformly use the random‐effects model (DerSimionian 1986) for assessment of treatment effects given that the random‐effects model is a more conservative estimate of treatment effects compared with the fixed‐effects (DeMets 1987). If we observe heterogeneity, this will be explored further.

If we have sufficient data, we will undertake the following subgroup analyses for each comparison.

1. ARDS versus ALI at entry to study.

2. Studies looking at the mean tidal volume delivered with pressure limited and volume limited modes. We will adopt a threshold of 6 ml/kg as the desired target tidal volume and compare it with those studies in which this target was not met.

3. Incidence of barotrauma between ventilatory supports with and without pressure limitation.

4. Mortality in hospital versus in ICU and at longest follow‐up.

5. Trials using the American European Consensus Conference criteria to define ARDS/ALI versus other definitions.

We will formally compare the effects between subgroups using the methods described in Deeks 2001.

Sensitivity analysis

We will perform a sensitivity analysis to investigate the effects of the interventions from trials at low risk of bias.

We will also undertake sensitivity analyses if trials report dropout rates of 10% or greater, to ascertain differences in outcomes of intention to treat (ITT) analysis (all dropouts will be assigned to the worst outcome for dichotomous outcomes) and analysis of completers. If the results of this analyses differ significantly with relation to direction of effect, we will perform two additional analyses: a) a best‐case scenario favouring pressure controlled ventilation, i.e., none of the dropouts in this group had the unfavourable outcome, but all dropouts from the volume controlled group had the worst outcome; b) a worst‐case scenario favouring control, i.e., all the dropouts from the pressure controlled group had the unfavourable outcome, but none from the volume‐controlled group had this poor outcome.