This article outlines the statistical analysis plan for the Plasma-Lyte 148 versus Saline (PLUS) study, which is a prospective multicentre, parallel-group, concealed, blinded, randomised controlled trial to determine whether fluid resuscitation and therapy with a balanced crystalloid solution (Plasma-Lyte 148) decreases 90-day mortality in critically ill patients requiring fluid resuscitation compared with the same treatment using 0.9% sodium chloride (saline). ¹

This study is endorsed by the Australian and New Zealand Intensive Care Society Clinical Trials Groups (ANZICS CTG). The approach of publication of a statistical analysis plan before the analysis of data has been used for previous randomised controlled trials conducted by the ANZICS CTG, ² including the Crystalloid versus Hydroxyethyl Starch Trial (CHEST), ³ the Augmented versus Routine Approach to Giving Energy Trial (TARGET), ⁴ and the Intensive Care Unit Randomised Trial Comparing Two Approaches to Oxygen Therapy (ICU-ROX). ⁵ The use of a pre-specified statistical analysis plan in the PLUS study demonstrates that the study is being conducted with a high degree of transparency and should reduce the risk of analysis bias arising from knowledge of the study findings emerging during analysis of the study data. ^{2, 6}

The statistical analysis plan for the PLUS study was developed by the study statistician (LB), the chief investigator (SF), and the project manager (SM), and approved by the PLUS study Management Committee, and released on a pre-print server ⁷ before completion of study recruitment.
 

The PLUS study is a prospective, multicentre, parallel-group, concealed, blinded, randomised controlled trial, which will be conducted in 40–50 intensive care units (ICUs) in Australia and New Zealand. The PLUS study will test the hypothesis that in a heterogeneous population of critically ill adults, random assignment to Plasma-Lyte 148 for intravascular volume resuscitation and crystalloid fluid therapy in the ICU results in different 90-day all-cause mortality compared with random assignment to 0.9% saline for the same treatment.
 

The study was prospectively registered on ClinicalTrials.gov (NCT02721654) and the protocol has been published previously. ¹
 

All patients who are admitted to one of the study ICUs will be screened for study eligibility. Patients who fulfil all of the inclusion criteria and none of the exclusion criteria will be eligible for the study (Table 1).
 

Permuted block randomisation with variable block sizes, stratified by site will occur via a password-protected, secure website. Following successful randomisation, each patient will be assigned a unique patient study number and will be assigned to receive either Plasma-Lyte 148 or 0.9% saline (blinded study treatment). Study participants, treating clinicians, study investigators and data collectors will be blinded to treatment allocation.
 

Each study participant will receive either Plasma-Lyte 148 or 0.9% saline alone for all resuscitation episodes and for all compatible intravenous crystalloid therapy while in the ICU (for up to 90 days). Other crystalloid fluids may be used as carrier fluids for the infusion of any drug for which either Plasma-Lyte 148 or 0.9% saline is considered incompatible; in such instances, 5% glucose will be used whenever possible to minimise exposure to open-label Plasma-Lyte 148 and 0.9% saline. Aside from the study treatment, patient management will be otherwise unaffected, and the treating clinicians will be free to provide whatever medical care is deemed best and necessary for the patient.
 

The primary outcome is death from all causes within 90 days after randomisation. The secondary outcomes are shown in Table 2.
 

The study was originally designed to recruit 8800 participants to have 90% power to detect a 2.9% reduction in 90-day mortality in the study population; this is less than the reduction in mortality reported in database studies. These calculations assumed a base mortality rate of 23% and 2% of patients lost to follow-up. Following the advent of the coronavirus disease 2019 (COVID-19) pandemic, the study Management Committee, in conjunction with the study sponsor (the George Institute for Global Health, Australia) faced suspension of non-COVID-19 clinical research in many of the study hospitals and significant uncertainty over prospects for future recruitment. The Australian National Health and Medical Research Council, the major study funder, was approached for further funding to keep the study running for longer but did not have the funds or a mechanism to allocate additional funding. Consequently, power calculations were undertaken to assess the impact of ceasing recruitment on 31 December 2020, a date 60 days before the expiry of the current batch of study fluids. Both the initial and revised power calculations are detailed in Table 3. Assuming 2% of patients lost to follow-up, the revised plan is to include ~5000 patients, which provides 90% power to detect a hypothesised absolute difference of 3.8 percentage points (ie, one percentage point more than originally intended), and 80% power to detect a hypothesised absolute between-group difference of 3.3 percentage points (ie, 0.4 percentage points more than originally intended) at α = 0.05.

Analyses will be conducted on an intention-to-treat basis. The intention-to-treat population is all patients randomised regardless of whether they receive study treatment, and includes patients for whom there are no data available due to absence or revocation of consent. To comply with relevant laws, data for which consent was not obtained or was withdrawn will be excluded from the analyses and subject to sensitivity analyses using missing data imputations.

A sensitivity analysis of the primary outcome will be conducted after sequentially (and cumulatively) excluding the following patients:

All tests are to be two-sided, with a nominal level of a set at 5%. Analyses of the primary outcome (all-cause mortality at 90 days) will be unadjusted for multiplicity; however, we will control the family-wise error rate across secondary outcomes using a Holm–Bonferroni correction. ⁸ No other multiplicity adjustment will be applied.
 

The flow of patients through the trial will be displayed in a CONSORT ⁹ (Consolidated Standards of Reporting Trials) diagram. The report will include the number of screened patients who met study inclusion criteria and the number of patients who were included, and reasons for exclusion of non-included patients. A separate figure will describe their consenting status.

In addition, we will create a chart showing, for each day between days 1–90, the proportion of patients in each arm who fall into one these five categories:

The figure will consist of two (one plot per arm) stacked bar charts with one bar per day and, within each bar, the proportion of patients in each category (summing to 100%).

 

Baseline characteristics (Table 4) will be presented by treatment group. Discrete variables will be summarised by frequencies and percentages. Percentages will be calculated according to the number of patients for whom data are available. Continuous variables will be summarised using mean and standard deviation (SD) together with the median and interquartile range (IQR).
 

Fluid details, laboratory values and measures of organ dysfunction collected daily will be summarised using descriptive statistics (mean [SD], median [IQR], minimum and maximum for continuous variables, or number and percentages for categorical variables) and plots (mean plots or bar charts) per day. For continuous variables, the overall mean per treatment arm and overall difference (and 95% confidence interval [CI]) between treatment arms will be calculated using a repeated-measure linear mixed model with a fixed effect of treatment, a fixed categorical effect of time (study day), a fixed interaction between treatment and time, a fixed continuous effect of the baseline value, a random site effect (to model within-site correlations), and a random patient effect (to model within-patient correlations). Binary and ordinal variables will be analysed using a similar modelling approach but using logistic regression and ordinal logistic regression, respectively, in place of linear regression and with the between treatment differences estimated as odds ratio (OR) and 95% CI. While these metrics are subject to competing risks due to patients who die or are discharged from the ICU before Day 7, these analyses are aimed at describing the intervention process rather than estimate its effect and, therefore, we will not adjust for competing risks or impute for missing data.
 

The primary analysis will be conducted without imputation of missing data. The primary endpoint is the proportion of participants dead at 90 days. To account for stratification by site and maximise power, ¹⁰ the main analysis will be performed using logistic regression, with treatment allocation as a fixed effect and site as a random effect. ¹¹ The effect of the intervention will be presented as the OR of death and 95% CI. Crude proportions by treatment arm will also be reported with an unadjusted OR and 95% CI and a χ² test Pvalue. For ease of interpretation, risk difference and 95% CIs will also be presented. The adjusted OR and 95% CI will be converted to an adjusted risk difference and 95% CI using the Hummel and Wiseman method described by Reeve. ¹²

Adjusted analyses will be performed by adding the following covariates to the main logistic regression model: sex, Acute Physiology and Chronic Health Evaluation (APACHE) II score at randomisation (as a continuous variable), presence of sepsis, and source of admission (postoperative v other). The adjusted treatment effect will be reported as the adjusted OR and 95% CI.
 

Six pre-specified subgroup analyses (Table 5) will be carried out irrespective of whether there is a significant treatment effect on the primary outcome. The analysis for each subgroup will be performed by adding the subgroup variable as well as its interaction with the intervention as fixed effects to the main logistic regression model. Within each subgroup, summary measures will include raw counts and percentages within each treatment arm, as well as the OR for treatment effect with a 95% CI. The results will be displayed on a forest plot including the P value for heterogeneity corresponding to the interaction term between the intervention and the subgroup variable.
 

If more than 3% of patients from the intention-to-treat population are excluded from the analysis of death at Day 90 due to missing data, missing data will be imputed using “worst-best” and “best-worst” case scenarios. In the “worst-best” scenario, the “worst” outcome (ie, dead at Day 90) will be assigned to all patients missing the outcome in one treatment group, and the “best” outcome (ie, alive at Day 90) will be assigned to all patients missing the outcome in the other treatment group. The “best-worst” scenario corresponds to the reverse assignment of outcomes. If these two extreme scenarios lead to the same conclusions, no further imputation of missing data will be performed. In case of inconsistent conclusions; that is, where one scenario leads to a statistically significant difference and not the other or where the two are significant but in different directions, we will further explore the impact of missing data by performing multiple imputations using fully conditional specification. ¹³ The imputation model will include death at 90 days, the randomised treatment arm, study site, all baseline data and all variables collected during Days 1–7. Binary variables (eg, vital status at 90 days) will be imputed using an ordinal logistic model, categorical variables using a discriminant function method and continuous variables using linear regression. One-hundred sets of imputed data will be created and analysed using the methods described for the analysis of the primary end point.
 

The primary mortality analysis will be replicated to compare the proportions of patients who died at ICU discharge, hospital discharge, and at Day 28. For these analyses, no adjusted or subgroup analyses will be performed. Causes (proximate and underlying) and places of death (by Day 90) will be categorised and the distribution will be compared between the two treatment arms using a 𝑥²  test. An analysis of time to death by treatment group will be censored at Day 90 or at the time when the patient was last known to be alive, whichever occurs earlier. A Kaplan–Meier plot will be used to describe survival rates and derive median and quartiles of time to death. Differences in survival will be tested using a Cox model with a random site effect (ie, using a shared-parameter frailty model). ¹⁴

Serum creatinine. The overall mean serum creatinine value per treatment arm and overall difference (and 95% CI) between treatment arms over Days 1–7 will be calculated using a repeated-measure linear mixed model, as described in the section on analysis of daily data. In addition, peak creatinine level and maximum post-randomisation increase in creatinine level will be analysed using an analysis of covariance adjusted on the baseline creatinine value and including a fixed effect of treatment and a random effect of site. These analyses will be performed without imputing missing data; however, to assess the potential impact of informative missing data due to early discharge or death, we plan to describe creatinine values between Days 1–7 separately according to when patients died or were discharged alive. Fourteen profiles, or strata, will thus be created according to the day when the patient died or was discharged (Days 1–7) and separately for those who died versus those who were discharged alive (×2). For each of these 14 profiles, we will describe the daily creatinine values using non-parametric cubic splines. In case of a clear indication that the creatinine trajectories differ according to the profile, we will consider re-running the repeated-measure linear model using a pattern-mixture approach adjusted by profile.

Durations and time to discharge. The hospital length of stay, ICU length of stay, duration of mechanical ventilation, and duration of treatment with vasoactive drugs will be analysed as the number of days alive and free of outcome (eg, days alive and free of mechanical ventilation or days alive and free/outside of ICU). Days alive and free of outcome will be calculated between randomisation and Day 90 and will therefore have values comprised between 0 and 90 days. They will be summarised using means (SDs), median (IQRs), minimum and maximum and compared between treatment groups using a linear regression with a fixed effect of the treatment group and a random effect of site. As a sensitivity analysis, we will allocate zero “free days” to patients who die by Day 90. Mechanical ventilation and treatment with vasoactive drugs are only expected to occur while in the ICU. Therefore, once discharged from the ICU, patients will be assumed to be free of respiratory support and vasopressors. While in the ICU, missing daily values (eg, unknown mechanical ventilation status) will be handled as follows:

Time to discharge alive from index ICU and time to discharge alive from index hospital admission will be summarised using cumulative incidence functions treating mortality as a competing risk. Medians and quartiles of time to discharge will be obtained from the cumulative incidence functions. The effect of the intervention will be estimated as the hazard ratio (Plasma-Lyte 148 divided by 0.9% saline) and 95% CI obtained from a Cox model of the cause-specific hazard, which estimates the risk of discharge in subjects who are still alive and have not yet been discharged. ¹⁵ To model potential within-site correlations due to stratification, we will use a shared-parameter frailty Cox model with a fixed effect of treatment and a random site effect. ¹⁴

New treatment with renal replacement therapy and vasoactive drugs. Comparison of proportions of patients newly treated with renal replacement therapy and of patients treated with vasoactive drugs will be summarised by treatment arm and compared using a logistics regression analysis analogous to that used for the primary outcome.

Quality of life. The information obtained from the Five-level EuroQol five dimensions (EQ-5D-5L) questionnaire will be used to conduct a cost–utility analysis at 6 months after randomisation and to report quality of life by treatment group and by subgroups. The cost utility analysis forms part of an extended program of health economic and outcomes research to be conducted after publication of the main trial findings.

Safety outcomes. Adverse drug reactions deemed possibly, probably or definitely related to study treatment as determined by the treating physician at site will be summarised as the number and proportion of patients experiencing at least one event. These will be summarised by category of event and overall numbers of events. In addition to the number of patients with at least one event, we will report the total number of events. Proportions of patients with adverse drug reactions will be compared between treatment arms using Fisher exact test, both overall and by category. This will be repeated for serious adverse drug reactions. A listing of all adverse drug reactions will be reported in an Online Appendix.