Target Temperature Management After Cardiac Arrest

Detailed statistical analysis plan for the Target Temperature Management after Out-of-hospital Cardiac Arrest trial

1. Introduction The Target temperature management after out-of-hospital cardiac arrest, a randomised, parallel-group, assessor-blinded clinical trial (the TTM-trial) is the largest trial to date in post-cardiac arrest treatment and in temperature management in the intensive care setting. To prevent outcome reporting bias and data driven analysis results, the International Conference on Harmonisation of Good Clinical Practice and others have recommended that clinical trials should be analysed according to a pre-specified plan [1]. Leading experts in the critical care community have advocated that this should not only be a recommendation but rather a prerequisite [2]. Here we describe the statistical analysis plan that has been finalised while data collection in the TTM-trial still is on going, and to which all data analyses in the main publication of the TTM-trial results will adhere. The steering group of the TTM-trial unanimously approved the statistical analysis plan December 3rd 2012, patient recruitment at 950 patients was completed January 10th 2013, and the final follow-up is predicted to occur in the beginning of July 2013, after which the database will be locked and then analysed.
2. Trial overview The TTM-trial is a multicentre, multinational, outcome assessor-blinded, parallel group, randomised clinical trial comparing two strict target temperature regimens of 33°C and 36°C in adult patients, who have sustained return of spontaneous circulation and are unconscious after out-of-hospital cardiac arrest, when admitted to hospital. The study background, design, and rationale have previously been published [3, 4]. The TTM-trial protocol (current version 3.3) has been available online on www.ttm-trial.org since the start of the trial. The trial is registered at clinicaltrials.gov NCT01020916 and is endorsed by the European Clinical Research Infrastructure Network and the Scandinavian Critical Care Trials Group.
3. Objective The primary aim of the TTM-trial is to compare the effects of two strict target temperature protocols for the first 36 hours of hospital stay after resuscitation from out-of-hospital cardiac arrest (4 hours for achieving the target temperature, 24 hours of maintenance of target temperature, and 8 hours of rewarming). The null hypothesis is that there is no difference in survival until the end of trial (180 days from randomisation of the last patient) with a target temperature of 33°C compared to 36°C. To demonstrate or reject a Hazard Ratio difference of 20% between the groups, equivalent to approximately one months difference in median survival time assuming proportional hazards in the groups during the observation time, a sample size of 900 patients would be necessary with a type-1 error risk of 5% and a type-2 error risk of 10%. To allow for patients lost-to-follow up the target population is set to 950 patients.
4. Stratification and design variables The only stratification variable used is trial site (hospital). Pre-defined design variables allowing for an adjusted analysis of the primary outcome, and pre-defined subgroup analyses are: age, gender, first presenting cardiac rhythm (shockable or non-shockable), duration of cardiac arrest, and presence of shock at admission.
5. Definition of the efficacy variables The outcomes are defined as primary, secondary and exploratory (tertiary in the trial protocol). Only primary and secondary outcomes will be analysed for the first published report of the TTM-trial due to the complexity of the exploratory outcomes, and thus a need for separate publications.

Primary outcome The primary outcome is survival until end of trial, which will be 180 days from randomisation of the last patient.

Secondary outcomes including adverse events The main secondary outcomes are the composite outcomes of

1. poor neurological function defined as Cerebral Performance Category (CPC) 3 or 4, or death (CPC 5); and
2. poor neurological function defined as modified Rankin Scale (mRS) 4 or 5, or death (mRS 6) evaluated at 180 days (+/- 14 days) from randomisation.

The number of study participants in each category of CPC and mRS will be reported separately.

The following adverse events are included in the secondary outcomes: bleeding, pneumonia, electrolyte disorders, hyperglycemia, hypoglycaemia, cardiac arrhythmia, myoclonic or tonic-clonic seizures, renal replacement therapy. Definitions for the adverse events have been described earlier [4].

Other secondary outcomes are Cerebral Performance Category at intensive care unit and hospital discharge, and best Cerebral Performance Category during entire trial period.

Exploratory outcomes Neurological function at 180 days defined with CPC, mRS, Informant Questionnaire on Cognitive Decline in the Elderly (IQCODE), Mini mental state exam (MMSE) and two simple questions: 1a. In the last two weeks, did you require help from another person for your every day activities? (If yes: 1b. Is this a new situation following the heart arrest?), and 2. Do you feel you have made a complete mental recovery after your heart arrest? [4].

Quality of life defined with Short-Form 36.

1. Data points Baseline variables

• Sex
• Age
• Comorbidities*
• Chronic heart failure (NYHA 3 or worse)
• Previous acute myocardial infarction
• Ischaemic heart disease
• Previous cardiac arrhythmia
• Previous cardiac arrest
• Arterial hypertension
• Previous transient ischaemic attack or stroke
• Epilepsy
• Diabetes mellitus
• Asthma or chronic obstructive pulmonary disease
• Chronic hemo- or peritoneal dialysis
• Hepatic cirrhosis
• Haematological malignancy
• Other malignancy
• Acquired immune deficiency syndrome
• Alcoholism
• Intravenous drug abuse
• Other immunodeficiency
• Pre-morbid Cerebral Performance Category (CPC)
• Previous percutaneous coronary intervention
• Previous coronary bypass grafting
• Previous valvular surgery
• Implantable cardioverter-defibrillator and or pacemaker
• Age
• Pre-hospital variables
• Location of cardiac arrest
• Bystander witnessed arrest
• Bystander cardiopulmonary resuscitation (CPR)
• First monitored rhythm at arrival of emergency medical service
• Use of active compression-decompression device
• Time from cardiac arrest to start of basic life support
• Time from arrest to start of advanced life support
• Time from arrest to return of spontaneous circulation
• Data on admission
• First measured temperature (tympanic)
• Glasgow Coma Scale (combined score)
• pH
• Lactate
• Shock on admission
• Acute ST-elevation infarction or novel left bundle branch block
• A comorbidity will only be reported if the frequency is above or equal to 5% in any of the intervention groups. Pre-morbid CPC will be reported regardless of the frequency.

Intervention period variables Core temperature primarily measured in the urinary bladder will be reported per hour during the 36 hours of the intervention period.

Neurological prognostication and withdrawal of care Number and proportion of patients still comatose at 72 hours after the end of the intervention period that underwent neurological prognostication by a blinded physician. Number of patients, who did not survive until neurological prognostication and their presumed cause of death, including limitations in care and reasons for that. Number of patients with electroencephalogram, somatosensory evoked potentials, magnetic resonance imaging, computed tomography of the head.

Concomitant cardiological treatments Number of patients receiving coronary angiography, percutaneous coronary intervention and coronary bypass grafting, divided in three time groups (immediately after admission, during intervention or when sedated in the intensive care unit, and after regaining consciousness. Number of patients receiving intra aortic balloon pump, other mechanical assist device, temporary pacemaker, permanent pacemaker and implantable cardioverter-defibrillator.

Other descriptive variables Number of days in intensive care unit and days on mechanical ventilation during the index ICU-admission and days in hospital within the index admission will be reported.

1. General analysis principles
2. Analyses will be conducted according to the modified intention-to-treat principle [5] if not otherwise stated.
3. All tests of significance will be two-sided with a maximal type-1 error risk of 5%
4. The primary analyses of primary and secondary outcomes will be those of the modified intention-to-treat population adjusted for the protocol specified stratification variable [6] and if necessary using data sets generated using multiple imputations (see below). An unadjusted analysis and an analysis adjusting for both stratification and predefined design variables will be carried out as sensitivity analyses. Other analyses may also be done using e.g. a slightly different population. If the results of these analyses are not consistent with the primary analyses this will be discussed. Nevertheless, the conclusions of the study will still be those based on the primary analyses.
5. The tests for interaction between the intervention and each design variable used to identify subgroups are exploratory.
6. Risks will be reported as hazard ratios or risk ratios with 95% confidence interval (CI) or with limits as stated under point 6.
7. If there is data missingness for a specified primary or secondary outcome of less than 5% we will perform a complete case analysis without imputing missing values. If there is a missingness of more than 5% we will perform Little's test. If the test indicates that the complete case data set is a random sample we will continue without imputing missing values and analyse the complete cases. If Little's test indicates that the data set of complete cases is not a random sample of the total data set we will report the point estimates and their 95% confidence limits applying a worst/best scenario imputation for the missing values. If the worst/best case analyses allow for the same conclusion we will not perform multiple imputation. However, if the worst/best case imputation provides different conclusions, multiple imputation will be performed, creating 10 imputed data sets under the assumption of missingness at random. The result of the trial will be the pooled intervention effect and 95% CI of the analyses of the data sets after multiple imputation.

Primarily the observed P-values of the primary and five secondary outcomes will be presented. However, multiplicity, a possibly reason for spurious statistically significant P-values, may be a problem when the result of several outcomes are presented. We therefore want to present a supplemental analysis being the result with P-values adjusted for multiplicity according to the fall-back procedure [7]. The P-values adjusted for multiplicity will be presented and discussed in relation to the unadjusted P-values. This adjustment may be needed to control the overall probability of a type 1 error (rejection of a null hypothesis that is actually true) and keep the family wise error rate below 0.05 as required by most regulatory agencies. This will be done by specifying the weights of the hypotheses assigned to them according to their importance. The sequence in which the hypotheses will be tested and their individual weights (in parentheses) will be: the primary outcome (0.50), first secondary outcome (0.25), second secondary outcome (0.0625), third secondary outcome (0.0625), fourth secondary outcome (0.0625), and fifth secondary outcome (0.0625). The multiplicity problem is further illuminated in the Discussion section.

1. Statistical analyses Trial profile Flow of study participants will displayed in a CONSORT diagram as shown in Box 1 [8]. Number of screened patients who fulfilled study inclusion criteria and the number included in the primary and secondary analyses as well as all reasons for exclusions in primary and secondary analyses will be reported.

Primary outcome Frequencies and percentages per group, as well as hazard ratios with 95% CI will be reported. The primary outcome will be analysed using Cox-regression with adjusting variables indicated below. The proportional hazard assumption across treatment groups will be checked by testing if there is an interaction between intervention and time and by plotting cumulative hazard functions for intervention groups.

1. The first analysis of the primary outcome, adjusted for the stratification variable, will be on the patients that met the inclusion criteria and did not meet the exclusion criteria at time of randomisation. Patients who did not meet inclusion criteria and did not receive the intervention (temperature management) and was erroneously randomised will be excluded according to the modified intention to treat principle.
2. The second analysis on the primary outcome will be on patients that met the inclusion criteria and did not meet the exclusion criteria and did not have any major protocol violations (per-protocol analysis).
3. The third analysis on the primary outcome will be an analysis adjusted for both the stratification variable and the design variables.
4. The above analyses will be repeated with sites grouped as a variable indicating whether the patient has been allocated by the 2 sites having allocated most patients or one of the other sites (which would be approximately ¼ of the trial population).

Secondary outcomes including adverse events Frequencies and percentages per group, as well as risk ratios with 95% CI will be reported. A standard Chi2-test will be used to assess the effect of treatment on binary and categorical outcomes. For the adjusted primary analyses logistic regression analysis will be used. Wilcoxon-Mann-Whitney's test will be used for continuous outcomes. There will only be reported significance testing on the composite outcomes mortality and poor neurological outcome versus survival with good neurological outcome; not on the individual sub-scores of CPC and mRS. For adverse events there will be a Chi2-test on having one or more adverse events versus having no adverse events. If there is a significant difference between treatment groups in occurrence of adverse events we will try to delineate which of the events that drive this difference. However we acknowledge the low power for performing analyses in this case.

Characteristics of patients with baseline comparisons Description of baseline characteristics listed above will be presented by treatment group. Discrete variables will be summarized by frequencies and percentages. Percentages will be calculated according to the number of patients where data are available. Where values are missing, the actual denominator will be stated.

Continuous variables will be summarised using standard measures of central tendency and dispersion, either using mean +/- standard deviation for data with normal distribution or median and inter quartile range for non-normally distributed data.

Intervention period variables The mean values of the actual measured temperature in the two intervention groups will be displayed in a graph with mean, +/- 2 standard deviations.

Neurological prognostication and withdrawal of care, concomitant cardiological treatments and other descriptive variables

Description of baseline characteristics listed above will be presented by treatment group without significance testing. Discrete variables will be summarized by frequencies and percentages. Percentages will be calculated according to the number of patients where data are available. Where values are missing, the actual denominator will be stated.

Continuous variables will be summarised using standard measures of central tendency and dispersion, either using mean +/- standard deviation for data with normal distribution or median and inter quartile range for non-normally distributed data.

1. Outline of figures and tables Figure 1 will be a CONSORT flow chart as specified above. Figure 2 will be a temperature graph for the two groups with hour 0 to 36 on the x-axis and mean temperature with +/- 2 standard deviations on the y-axis.

Figure 3 will be a Kaplan-Meier plot of survival in the two groups during the trial period (32 months).

Figure 4 will be a Forest plot of intervention effects stratified for the design variables: age dichotomised around the median, gender, duration of cardiac arrest dichotomised around the median, initial cardiac rhythm shockable or non-shockable, and presence or absence of cardiogenic shock at admission to hospital.

All tables will report variable according to randomisation groups:

Table 1 and 2 will report background variables. Table 3 will report intensive care unit and hospital stay variables. Table 4 will report adverse events. Table 5 will report 180-day outcomes for survival/mortality and neurological function with CPC and mRS.

1. Discussion With this statistical analysis plan we present the different analyses in the main publication of the TTM-trial to avoid risks of outcome reporting bias and data driven results. Of the pre-specified outcomes in the trial we choose to report only primary and secondary in the main publication, because of the complexity of the detailed neurological outcomes and quality of life that constitutes the exploratory outcomes, requiring separate publications.

We would like to emphasise that the main secondary outcome being the composite outcome of poor neurological function and mortality at 180 days after cardiac arrest will be of great importance in a situation of a neutral outcome in the primary outcome, when interpreting the results and deriving clinical implications from the TTM-trial. As survival is an outcome with low risk of bias, not prone to competing risks, and earlier trials and registry data indicate a lower sample size needed to show the same risk reduction when the composite outcome of mortality and poor neurological function is used (compared to mortality/survival), this was the fundament for the order of the outcomes. The composite outcome of poor neurological function and mortality will hopefully benefit by an increased power with respect to the possibility of finding or rejecting a significant signal when the trial is powered for survival, which would require a larger sample size.

Comments on the multiplicity problem

There are one primary and 5 secondary outcomes to be assessed:

• Primary outcome: survival
• Secondary outcomes

1. Neurological (CPC): binary quantity
2. Neurological (mRS): binary quantity
3. Adverse event: binary quantity
4. Cerebral performance category measured at specified point in time: binary quantity
5. Best cerebral performance during specified period: binary quantity Thus there are six significance tests. These have to be adjusted for multiplicity to control the probability of a type-1-error (rejection of a null hypothesis that is true). One way to diminish this risk would be to deal with the six outcomes as one group using a data driven adjustment of the P-values. The most powerful procedure based on the raw P-values is probably that of Hommel [7].

An alternative (the fixed sequence procedure) would be to specify the sequence of the hypotheses testing in advance. (Primary outcome, first secondary outcome, second secondary outcome, - - -, fifth secondary outcome.) In this latter case no multiplicity adjustment will be needed. Then each test will be done at the 0.05 level of significance in the specified order. However, as soon as a test is non-significant the remaining null hypotheses will be accepted without test.

For instance if the primary outcome and the first secondary outcome are significant at the 0.05 level and the second secondary outcome (neurological function measured with mRS) is insignificant, the null hypotheses corresponding to the secondary outcomes 3, 4 and 5 will be accepted without test.

A third approach is the so-called fall back procedure where the fixed hypothesis testing sequence is also used. However, if a test is insignificant, the procedure does not stop but the next hypothesis is tested at a reduced level of significance. This procedure also allows one to weight the hypotheses according to their importance and likelihood of being rejected.

Hommel's procedure is sensitive to the P-values of the last three tests while the fall back procedure is not. Since the first and second of the secondary outcomes probably will produce similar P-values it appears logical to place most of the weights on the primary and the first secondary outcome.

Based on these considerations the analyses in the TTM-trial will be presented with unadjusted P-values as well as adjusted for multiplicity using the fall back procedure.

1. Conclusion To conclude this article describes the principle for how the TTM-trial will be analysed and presented in the first and main publication. With this we minimise the risk for data driven results and outcome reporting bias.

References

1. Dwan K, Gamble C, Williamson PR, Altman DG: Reporting of clinical trials: a review of research funders' guidelines. Trials 2008, 9: 66-77.
2. Finfer S, Bellomo R: Why publish statistical analysis plans? Crit Care Resusc 2009, 11(1):5-6.
3. Nielsen N, Friberg H, Gluud C, Herlitz J, Wetterslev J: Hypothermia after cardiac arrest should be further evaluated-A systematic review of randomised trials with meta-analysis and trial sequential analysis. Int J Cardiol. 2011, 151:333-341.
4. Nielsen N, Wetterslev J, al-Subaie N, Andersson B, Bro-Jeppesen J, Bishop G, Brunetti I, Cranshaw J, Cronberg T, Edqvist K, Erlinge D, Gasche Y, Glover G, Hassager C, Horn J, Hovdenes J, Johnsson J, Kjaergaard J, Kuiper M, Langørgen J, Macken L, Martinell L, Martner P, Pellis T, Pelosi P, Petersen P, Persson S, Rundgren M, Saxena M, Svensson R, Stammet P, Thorén A, Undén J, Walden A, Wallskog J, Wanscher M, Wise MP, Wyon N, Aneman A, Friberg H: Target temperature management after out-of-hospital cardiac arrest-a randomized, parallel-group, assessor-blinded clinical trial-rationale and design. Am Heart J. 2012, 163:541-548.
5. Fergusson D, Aaron SD, Guyatt G, Hérbert P: Post-randomisation exclusions: the intention-to-treat principle and excluding patients from analysis. BMJ 2002, 325:652-654
6. Kahan BC, Morris TP: Reporting and analysis of trials using stratified randomisation in leading medical journals: review and reanalysis. BMJ 2012, 344:e5840
7. Dmitrienko A, Tamhane AC, Bretz F (editors): Multiple testing Problems in Pharmaceutical Statistics. New York: CRC Press/Chapman \& Hall; 2010
8. Moher D, Schulz KF, Altman D: The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomized trials. JAMA 2001, 285:1987-1991.