with specific expertise in HFOV, review methodology and biostatistics.

On-line Supplement List of Elements Detailed Methods Section eappendix 1. Tidal Volume Derivation eappendix 2. Calculation of Respiratory System Compliance eappendix 3. Calculation of Body Mass Index eappendix 4. OSCAR Trial Calculation of Acute Kidney Injury eappendix 5. Uniform Definition of Study Day 1 eappendix 6. Classification of Barotrauma at Baseline for the OSCAR Trial Detailed Methods Section METHODS The study team included investigators from 6 clinical trials of HFOV and individuals with specific expertise in HFOV, review methodology and biostatistics. Literature search and study selection This review includes randomized trials comparing HFOV to conventional ventilation among adults with ARDS (as defined by the original study investigators); it excludes trials in which the experimental HFOV protocol incorporated a secondary intervention (e.g., prone ventilation, inhaled nitric oxide, tracheal gas insufflation) that is not typical of HFOV. Using a duplicate, independent review process, with no restriction on language of publication, two reviewers searched the following sources for eligible studies, and resolved disagreements by consensus: the Cochrane Central Register of Controlled Trials (The Cochrane Library 2015, Issue 11), MEDLINE (1948 to December 2015), EMBASE (1980 to December 2015), clinicaltrials.gov and controlled-trials.com. They manually searched the reference lists from included studies and conference proceedings of the American College of Chest Physicians (1994 to 2015), American Thoracic Society (1994 to 2015), European Society of Intensive Care Medicine (1994 to

2015), and the Society of Critical Care Medicine (1994 to 2015). From the outset, we excluded 1 trial (N=125) that interrupted conventional ventilation to apply HFOV for multiple short periods,(1) and a very small second trial (N=28) that did not capture some key variables for this review.(2) This review includes, therefore, 4 multicenter trials originating in the US (MOAT; N=148),(3) Netherlands (emoat; N=61),(4) UK (OSCAR; N=795),(5) and Canada (OSCILLATE; N=548).(6) Risk of bias assessments Using the same duplicate and independent review process, we assessed the risk of bias of included studies using the Cochrane Risk of Bias instrument.(7) We abstracted information describing study randomization and allocation concealment,(8) post randomization withdrawals and losses to follow-up, crossovers between assigned groups, blinding of outcome assessors, and early stopping for benefit.(9) Database development We generated a standardized database for each trial, with uniform data definitions and including as many variables as possible. To harmonize data, we retrospectively collected Acute Physiology and Chronic Health Evaluation (APACHE)(10) scores at ICU admission for 527/548 (96%) participants in the OSCILLATE trial, where it had been previously collected at time of randomization. Other missing variables were derived from existing variables; full details are available in the online supplement (eappendices 1-6). For example, we derived missing plateau pressure values from peak pressure values using a conversion factor generated from an independent ARDS trial database E2

(N=980)(11) that showed excellent correlation (R 2 0.81) between plateau and peak pressures. If more than 20% of observations for a single variable were unavailable from 1 of the 2 largest trials, we excluded that variable from the database and study analyses (e.g., baseline diagnosis of sepsis, hemodynamic changes at study initiation, and vasopressor therapy). After combining the 4 standardized databases, if greater than 5% of observations of any variable were missing we tested whether missingness was associated with mortality or with the effect of HFOV on mortality. For example, the baseline duration of hospitalization was missing for 10% of patients, and mortality differed between patients with and without these data (P=0.04). We did not include this variable in the analyses. Analysis of patient outcomes and subgroups We compared HFOV versus conventional ventilation on the primary outcome of 30- day mortality, the longest follow-up common to all trials. We assumed for 2 studies that any patients discharged before day 30 remained alive at day 30.(4, 6) We tested this assumption within the database of the largest trial and found no exceptions among the 166 (21%) patients discharged before day 30.(5) We used mixed-effects logistic regression multi-level modelling that accounted for clustering of individual outcomes within treatment centers and within studies. Specifically, the models included random effects of intercept and treatment slope, thereby providing estimates of the variation among centers in outcome prevalence and treatment effects. Because there were only 4 trials, the study specific intercept and treatment effect E3

slope were modelled as fixed effects estimating the difference in outcome prevalence and treatment effect of each study. We adjusted for 3 prognostic variables - age, APACHE II score, and baseline duration of ventilation using fixed effects. To determine if the effect of HFOV on 30-day mortality differed across subgroups, we pre-specified 3 patient variables as potential effect modifiers: the ratio of partial pressure of arterial oxygen to fraction of inspired oxygen (PaO 2 :FiO 2 ), estimated respiratory system compliance (eappendix 2), and body mass index (eappendix 3). We entered these variables separately into the base model as fixed effects and tested for an interaction with treatment. We explored the hypothesis that HFOV may be superior to traditional high tidal volume ventilation strategies but inferior to low tidal volume ventilation. We could not analyze tidal volume as a patient variable because HFOV patients did not have tidal volume measurements; therefore we approached tidal volume as a hospital variable. We reasoned that the average tidal volume on study day 1 in each hospital could capture the degree of lung protection employed for study patients at each hospital, recognizing the limitations that this is a post-randomization variable, it assumes a homogeneous treatment of all control patients at a given hospital, and it is confounded by severity of lung injury. For each hospital, among control group patients only, we determined the average tidal volume (measured in ml/kg predicted body weight [PBW]; eappendix 1) on the first day after randomization (eappendix 5). We added this variable into our primary model as a hospital variable, controlling for patient PaO 2 :FiO 2. We also explored the hypothesis that more experience with study-specific HFOV protocols would lead to improved mortality among patients randomized to HFOV. We E4

tested for this association, comparing mortality by quartile of enrolment order among patients randomized to the HFOV arm in each center. We again used mixed-effects logistic regression, adjusting for trial, age, APACHE II score and duration of mechanical ventilation prior to enrolment. We also addressed the impact of HFOV on one secondary outcome, barotrauma (which was truncated at 28 days in one trial).(6) These analyses excluded patients with barotrauma present at baseline (eappendix 6). The mixed-effects logistic regression model accounted for clustering within trials and hospitals as described above, plus one adjustment variable, baseline PaO 2 :FiO 2, as a fixed effect. We assessed for 3 potential effect modifiers on the effect of HFOV on barotrauma: PaO 2 :FiO 2, respiratory system compliance, and body mass index. Because we had to estimate the prevalence of baseline barotrauma in the OSCAR trial, we performed a sensitivity analysis whereby this trial was excluded from the barotrauma analysis. All analyses classified patients according to their random allocation. Logistic regression models addressing assumed linearity, which we tested using both the Pearson goodness of fit test and the Hosmer and Lemeshow test; otherwise the regression models applied categorical data using quartiles. Despite negligible missing data in the merged database, we performed each analysis five times, using 5 random imputations of missing data and thus report a pooled odds ratio and corresponding P-value for each analysis.(12) For all analyses, we applied a nominal threshold P-value of 0.05 to denote statistical significance. Analysts used Stata version 8.2 (StataCorp, College Station, Tex) and SAS version 9.4 (SAS Institute Inc, Cary, NC). E5

eappendix 1. Tidal Volume Derivation Several analyses in this review include tidal volume data. Tidal volumes during mechanical ventilation were measured at the bedside for all studies except the OSCAR trial, which calculated tidal volume as minute ventilation divided by total respiratory rate. For the purpose of this review, we reasoned that for patients receiving pressure support or pressure control modes of ventilation, the calculated value would be less susceptible to reporting biases in situations where low tidal volumes were difficult to achieve. The OSCILLATE trial, which included a high rate of pressure control mode, also recorded minute ventilation and respiratory rate data. Therefore, this review uses calculated tidal volumes during ventilation in pressure support or pressure control mode in the OSCILLATE trial. In the rare situation when that data was missing, this review converted reported tidal volumes to calculated tidal volumes with the use of correction factors derived from an independent randomized trial data set of 980 patients with ARDS in many of the OSCILLATE hospitals.(11) There were correction factors for each mode of ventilation (pressure support and pressure control), both at study baseline and during the study. For example, the following figure shows the derivation of a correction factor to convert reported tidal volume during pressure control ventilation on study day 1 to calculated tidal volumes. The MOAT2 and EMOAT trials did not report calculated values of tidal volume, and used primarily volume assist control ventilation. We did not convert tidal volume data from these studies. Vt vs. MV/total RR, n=359, Corr. Coef.=0.90, R-square=0.81 vt 900 700 500 300 100 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 Regression Equation: vt = 78.79938 + 816.3231*vt_C LOVS - DAY 1, DATA FORM 3.1/3 THIRD COLUMN, on PC only vt_c eappendix 2. Calculation of Respiratory System Compliance Calculations of respiratory system compliance employed the formula: E6

Vt / (Pplat PEEP) where Vt is tidal volume, Pplat is plateau airway pressure and PEEP is positive end expiratory pressure. This review used tidal volume data as described in Appendix A. Where plateau pressure data was missing, we derived missing plateau pressure values from peak pressure values using a conversion factor generated from an independent ARDS trial database (N=980) 1 that showed excellent correlation (R 2 0.81) between plateau and peak pressures. eappendix 3. Calculation of Body Mass Index This review determined body mass index (BMI) according to the formula: BMI = (actual weight in kg) / (height in m) 2 eappendix 4. OSCAR Trial Classification of Acute Kidney Injury Most analyses of this review are adjusted for admission APACHE II scores, which typically requires the classification of kidney injury as acute or non-acute. Determinations of APACHE II scores in the OSCAR trial omitted the classification of kidney injury as acute versus non-acute. This omission systematically assigns lower values of APACHE II scores to OSCAR trial participants; the expected result is a false impression of worse patient outcomes in the OSCAR trial at a given severity of lung injury. To address this concern, we derived a decision rule to convert APACHE II scores among OSCAR patients with kidney injury at baseline: i. Patients with elevated serum creatinine who were identified as chronic dialysis patients were classified as having non-acute kidney injury. ii. Patients with elevated serum creatinine who were identified as acute dialysis patients were classified as having acute kidney injury. iii. Of the remaining 156 patients with elevated serum creatinine, those meeting any one of the following conditions were therefore classified as having acute kidney injury: a. Received new dialysis on study days 1, 2 or 3; b. Baseline urine output was less than 12 ml/kg in 24 hours. eappendix 5. Uniform Definition of Study Day 1 Some analyses of this review included respiratory data from study day 1, which was defined differently across the 4 studies. To apply a uniform definition of day 1, and thus employ unbiased data from the distinct studies for these analyses, we identified the earliest post-randomization time of data collection that was common across studies. The earliest post-randomization data collection in the OSCAR trial occurred on the first morning following randomization; therefore, we classified data collected at this time from all studies as Day 1 data. eappendix 6. Classification of Barotrauma at Baseline for the OSCAR Trial Since baseline barotrauma was not reported in the OSCAR trial, we categorized OSCAR patients retrospectively using categorical data related to hospital and ICU admission diagnoses, cause of respiratory failure, and related free text provided by admitting clinical E7

teams. Based on this data, one reviewer (MM) identified 48 (6%) of patients in the OSCAR trial for whom the risk of baseline barotrauma or chest tube presence was judged to be at least moderate. For each patient, 6 reviewers independently rated the likelihood of baseline barotrauma (or chest tube presence) as definite, high, medium, or low (kappa 0.32 indicates moderate agreement). In light of this limited level of agreement, we were conservative in our classification of patients as having barotrauma at baseline. Patients with >1 low probability ratings were classified as not having barotrauma. Otherwise, when most ratings indicated a high likelihood of baseline barotrauma we classified a patient as having barotrauma (or a chest tube) at baseline. References 1. Mentzelopoulos SD, Malachias S, Zintzaras E, Kokkoris S, Zakynthinos E, Makris D, Magira E, Markaki V, Roussos C, Zakynthinos SG. Intermittent recruitment with high-frequency oscillation/tracheal gas insufflation in acute respiratory distress syndrome. European Respiratory Journal 2012;39:635 647. 2. Shah S, Findlay GP. Prospective Study Comparing HFOV Versus CMV in Patients with ARDS. Intensive Care Med 2004;30:S84. 3. Derdak S, Mehta S, Stewart TE, Smith T, Rogers M, Buchman T, Carlin B, Lowson S. High frequency oscillatory ventilation for acute respiratory distress syndrome: A randomized controlled trial. American Journal of Respiratory and Critical Care Medicine 2002;166:801 808. 4. Bollen CW, Van Well GTJ, Sherry T, Beale RJ, Shah S, Findlay G, Monchi M, Chiche J-D, Weiler N, Uiterwaal CSPM, Van Vught AJ. High frequency oscillatory ventilation compared with conventional mechanical ventilation in adult respiratory distress syndrome: a randomized controlled trial [ISRCTN24242669]. Crit Care 2005;9:R430 9. 5. Young D, Lamb SE, Shah S, Mackenzie I, Tunnicliffe W, Lall R, Rowan K, Cuthbertson BH, OSCAR Study Group. High-frequency oscillation for acute respiratory distress syndrome. N Engl J Med 2013;368:806 813. 6. Ferguson ND, Cook DJ, Guyatt GH, Mehta S, Hand L, Austin P, Zhou Q, Matté A, Walter SD, Lamontagne F, Granton JT, Arabi YM, Arroliga AC, Stewart TE, Slutsky AS, Meade MO. High-frequency oscillation in early acute respiratory distress syndrome. N Engl J Med 2013;368:795 805. 7. Higgins JPT, Altman DG, Gøtzsche PC, Jüni P, Moher D, Oxman AD, Savovic J, Schulz KF, Weeks L, Sterne JAC, Cochrane Bias Methods Group, Cochrane Statistical Methods Group. The Cochrane Collaboration's tool for assessing risk of bias in randomised trials. BMJ 2011;343:d5928 d5928. 8. Chalmers TC, Celano P, Sacks HS, Smith H. Bias in treatment assignment in controlled clinical trials. N Engl J Med 1983;309:1358 1361. 9. Montori VM, Devereaux PJ, Adhikari NKJ, Burns KEA, Eggert CH, Briel M, Lacchetti C, Leung TW, Darling E, Bryant DM, Bucher HC, Schünemann HJ, Meade MO, Cook DJ, Erwin PJ, Sood A, Sood R, Lo B, Thompson CA, Zhou Q, Mills E, Guyatt GH. Randomized trials stopped early for benefit: a systematic review. JAMA 2005;294:2203 2209. E8

10. Knaus WA, Draper EA, Wagner DP, Zimmerman JE. APACHE II: a severity of disease classification system. Crit Care Med 1985;13:818 829. 11. Meade MO, Cook DJ, Guyatt GH, Slutsky AS, Arabi YM, Cooper DJ, Davies AR, Hand LE, Zhou Q, Thabane L, Austin P, Lapinsky S, Baxter A, Russell J, Skrobik Y, Ronco JJ, Stewart TE, for the Lung Open Ventilation Study I. Ventilation Strategy Using Low Tidal Volumes, Recruitment Maneuvers, and High Positive End-Expiratory Pressure for Acute Lung Injury and Acute Respiratory Distress Syndrome: A Randomized Controlled Trial. JAMA 2008;299:637 645. 12. Sterne JAC, White IR, Carlin JB, Spratt M, Royston P, Kenward MG, Wood AM, Carpenter JR. Multiple imputation for missing data in epidemiological and clinical research: potential and pitfalls. BMJ 2009;338:b2393 b2393. E9