ANNALS OF EMERGENCY MEDICINE JOURNAL CLUB
Is It Still Cool to Cool? Interpreting the Latest Hypothermia for Cardiac Arrest Trial Answers to the March 2014 Journal Club Questions Daniel M. Rolston, MD, MS; Jarone Lee, MD, MPH 0196-0644/$-see front matter Copyright © 2014 by the American College of Emergency Physicians. http://dx.doi.org/10.1016/j.annemergmed.2014.05.008
Editor’s Note: You are reading the 38th installment of Annals of Emergency Medicine Journal Club. This Journal Club refers to the Nielsen et al1 article titled “Targeted Temperature Management at 33 C Versus 36 C After Cardiac Arrest” that was published in The New England Journal of Medicine. Information about journal club can be found at http://www.annemergmed.com/content/ journalclub. Readers should recognize that these are suggested answers. We hope they are accurate; we know that they are not comprehensive. There are many other points that could be made about these questions or about the article in general. Questions are rated “novice,” ( ) “intermediate,” ( ) and “advanced ( ) so that individuals planning a journal club can assign the right question to the right student. The “novice” rating does not imply that a novice should be able to spontaneously answer the question. “Novice” means we expect that someone with little background should be able to do a bit of reading, formulate an answer, and teach the material to others. Intermediate and advanced questions also will likely require some reading and research, and that reading will be sufficiently difficult that some background in clinical epidemiology will be helpful in understanding the reading and concepts. We are interested in receiving feedback about this feature. Please e-mail [email protected] with your comments.
DISCUSSION POINTS 1. The authors reference 2 previous trials that compared therapeutic hypothermia (32 C to 34 C [89.6 F to 93.2 F] for 12 to 24 hours) with standard treatment and “showed a significant improvement in neurologic function and survival with therapeutic hypothermia.” A. What was the treatment effect in the previous 2 studies? What percentage of patients had neurologically intact survival? How many patients would one need to treat with hypothermia to produce 1 additional neurologically intact patient? B. There is good evidence that the presence of an initial shockable rhythm greatly enhances the probability of survival from cardiac arrest. Have any randomized trials demonstrated an improvement in neurologic outcomes in patients whose initial rhythm was pulseless electrical activity or asystole? 2. Previous studies have reported deleterious effects when patients recovering from an out-of-hospital cardiac arrest develop fever, leading authors to question whether Volume 64, no. 2 : August 2014
reported benefits are due to hypothermia or prevention of hyperthermia. The authors conducted a multicenter, international trial that randomized unconscious adults, who had return of spontaneous circulation after out-ofhospital cardiac arrest, to either 33 C or 36 C (91.4 F or 96.8 F) temperature target. A. The current recommendation by many expert consensus groups is to cool out-of-hospital cardiac arrest victims to 32 C to 34 C (89.6 F to 93.2 F) after ventricular fibrillation and possibly other rhythms. The authors did not follow this recommendation for one of the arms of the study. Do you believe there was equipoise? Discuss the importance of equipoise in clinical research. B. Could this trial have been performed in the United States? What additional requirements would the investigators have to complete to receive institutional review board approval for exception from informed consent? C. The authors note the inability to blind the critical care practitioners; however, they were able to blind the assessors providing follow-up neurologic examination. Were the methods used to eliminate the risk of critical care provider bias sufficient? 3. The authors examined the primary outcome of survival time and followed patients up to the end of the trial (ie, 180 days after the enrollment of the last patient) and powered the study to this outcome. A. The trial was designed as a superiority trial to detect a 20% reduction in the hazard ratio for death with hypothermia at 33 C (91.4 F) versus a control group at 36 C (96.8 F). Was the study appropriately powered for this outcome? B. How would the power calculations change if the study design were a noninferiority trial of relative normothermia at 36 C (96.8 F) versus hypothermia at 33 C (91.4 F)? C. What were the secondary outcomes? Discuss the advantages and disadvantages of using composite outcomes in medical research. D. Therapeutic hypothermia causes many physiologic changes and potential dangers to the patient. Therefore, the authors also collected the incidence of predefined serious adverse events up to day 7 in the ICU. Which specific adverse events did they collect? Do you think these Annals of Emergency Medicine 199
Journal Club adverse events and 7-day interval were sufficient? If not, what other events or intervals might you have chosen? E. To evaluate neurologic outcomes, the authors used the Cerebral Performance Category (CPC) and the modified Rankin score (mRS). For scores to be effective, they should be already validated. Have these 2 scores been previously validated? Are there other scores that the authors could have used? 4. For analysis of their results, hazard ratios were used for the analysis of their primary outcome (end of trial mortality), but risk ratios were used to analyze their secondary outcomes (CPC score, mRS). What are the differences between hazard ratios and risk ratios? Why didn’t the authors use hazard ratios for the primary outcome and hazard ratios for secondary outcomes? [Editor’s note: Since the publication of the questions, the wording of this question was changed to be more accurate in regard to hazard ratios.] 5. If you were creating a cardiac arrest protocol in your hospital, what would you set for the target temperature? Do you think the temperature or the protocol is more important for survival?
ANSWER 1
Q1. The authors reference 2 previous trials2,3 that compared therapeutic hypothermia (32 C to 34 C [89.6 F to 93.2 F] for 12 to 24 hours) with standard treatment and “showed a significant improvement in neurologic function and survival with therapeutic hypothermia.”1 Q1.a What was the treatment effect in the previous 2 studies? What percentage of patients had improved neurologically intact survival? How many patients would you need to treat with hypothermia to produce one additional neurologically intact patient? Bernard et al2 conducted an Australian study that randomized 77 cardiac arrest patients to either hypothermia with a goal temperature of 33 C (91.4 F) or normothermia with a targeted temperature of 37 C (98.6 F). The primary outcome in this study was good outcome, which was defined as either normal or minimal disability with discharge to home or moderate disability with discharge to a rehabilitation facility. The bad outcome was considered as either inhospital death or severe disability with discharge to a nursing home. The good outcome proportions in the hypothermia group and normothermia groups were 48.8% and 26.5%, respectively. Therefore, the study’s treatment, the absolute risk reduction for good outcome, was 22.3% (95% confidence interval [CI] 13% to 43%) for the hypothermia group. The number needed to treat, defined as (1/absolute risk reduction [expressed as a decimal, eg, 0.223), was 4.5 patients (95% CI 2.3 to 7.7 patients). This means that, if the study is correct, 4.5 patients need to be treated with a hypothermia protocol for 1 additional patient to have a “good outcome.” The Hypothermia After Cardiac Arrest Study Group published their results in the same issue of The New England Journal of Medicine,3 providing additional evidence supporting 200 Annals of Emergency Medicine
the use of hypothermia. This study enrolled 275 witnessed cardiac arrest patients without return of neurologic function who were randomized to a goal temperature of 32 C to 34 C (89.6 F to 93.2 F), or “normothermia.” The primary outcome was favorable neurologic outcome as measured by a Pittsburgh CPC of 1 to 2 (good performance–moderate disability). In the hypothermia group, 55.1% had good neurologic function compared with 39.4% in the normothermia group. The absolute risk reduction was 15.7%, corresponding to a number needed to treat equal to 6.4 patients (95% CI 4 to 25 patients). The number needed to treat of 4.5 to 6.4 patients to improve neurologically intact survival resulted in strong support for the international adoption of therapeutic hypothermia for comatose cardiac arrest survivors from ventricular tachycardia and ventricular fibrillation. However, several studies questioned the validity of the studies for the widespread application of hypothermia.4-7 Q1.b There is good evidence that the presence of an initial shockable rhythm greatly enhances the probability of survival from cardiac arrest. Have any randomized trials demonstrated an improvement in neurologic outcomes in patients whose initial rhythm was pulseless electrical activity or asystole? Although the evidence for hypothermia with shockable rhythms is much more robust, before the Targeted Temperature Management (TTM) trial there were only 2 randomized controlled trials evaluating hypothermia’s use after cardiac arrest in the nonshockable rhythms of pulseless electrical activity and asystole. The only randomized controlled trial evaluating hypothermia specifically for nonshockable rhythms is a feasibility study from 2001 that used a helmet cooling device. This study randomized 30 patients to hypothermia at 34 C (93.2 F) versus normothermia. Mortality in the hypothermia group was 81.3%, whereas mortality in the normothermia group was 92.9%,8 which was not a statistically significant difference. A 2005 reanalysis of this study showed that neurologically intact survival was 12.5% in the hypothermia group and 0% in the normothermia group.9 Laurent et al10 included 26% of patients with asystole as the initial rhythm in a trial that randomized patients to hemofiltration plus hypothermia, hemofiltration alone, or usual care. The hemofiltration and hemofiltration with hypothermia groups showed statistically improved survival at 6 months (45% and 32%, respectively) versus usual care (21%). These randomized trials do not show a clear benefit for hypothermia in nonshockable rhythms. However, a recent metaanalysis demonstrated improved inhospital mortality without improved neurologic outcome in nonrandomized studies.11 The largest randomized trials before the TTM trial did not include patients with nonshockable rhythms. Bernard et al2 enrolled patients with an initial rhythm of ventricular fibrillation, whereas Hypothermia After Cardiac Arrest3 enrolled patients with an initial rhythm of ventricular tachycardia or ventricular fibrillation. The TTM trial is currently the largest randomized controlled trial including patients with nonshockable rhythms. Pulseless electrical activity was present as the initial rhythm in 7% of patients, whereas witnessed asystole was the initial Volume 64, no. 2 : August 2014
Journal Club rhythm in 12%. Although always requiring a cautious interpretation, subgroup analysis in the supplementary appendix showed no significant difference between 33 C and 36 C (91.4 F to 96.8 F) for shockable or nonshockable rhythms.1
ANSWER 2 Q2. Previous studies have reported deleterious effects when patients recovering from an out-of-hospital cardiac arrest develop fever1,12,13 leading authors to question whether reported benefits are due to hypothermia or prevention of hyperthermia. The authors conducted a multicenter, international trial that randomized unconscious adults, who had return of spontaneous circulation after out-of-hospital cardiac arrest, to either 33 C (91.4 F) or 36 C (96.8 F) temperature target. Q2.a The current recommendation by many expert consensus groups is to cool out-of-hospital cardiac arrest victims to 32 C to 34 C (89.6 F to 93.2 F) after ventricular fibrillation and possibly other rhythms. The authors did not follow this recommendation for one of the arms of the study. Do you believe there was equipoise? Discuss the importance of equipoise in clinical research. Equipoise exists when there is uncertainty in efficacy between different treatment options. When designing studies, researchers have an ethical duty to ensure that the study has equipoise. However, true equipoise is fragile and difficult to attain because once an investigator or clinician has a bias toward one treatment over another, the test of equipoise fails. As a result, in 1987 Freedman14 defined a state of “clinical equipoise.” In clinical equipoise, the state of uncertainty exists “if there is genuine uncertainty within the expert medical community—not necessarily on the part of the individual.”14 Freedman14 changed the focus away from the individual and moved the discussion to the medical community. Then he went further and stated that “an honest, professional disagreement” must exist for clinical equipoise to exist. To satisfy this condition of clinical equipoise, the TTM authors performed a literature review of the evidence quality currently available. This review is published in the TTM trial protocol. They found 5 trials and found that current guidelines on therapeutic hypothermia were based primarily on 2 randomized controlled trials.2,3 Many methodological flaws were found in all the trials, and the Grading of Recommendations Assessment, Development and Evaluation (GRADE) quality of evidence was determined to be “low.”15 The TTM authors also conducted an advanced statistical technique called trial sequential analysis, which is beyond the scope of this answer, and determined that after pooling all the studies, an additional 600 to 800 patients would be required to have adequate power to accept or reject induced hypothermia as a treatment for comatose cardiac arrest survivors. In other words, the authors found that the pooled patients from the trials were not sufficiently powered to examine the outcomes of interest. The lack of fever management in the control arms was another major limitation in the previous studies on induced hypothermia after cardiac arrest. Increased temperature is Volume 64, no. 2 : August 2014
common and associated with worse outcomes within the first 48 hours after cardiac arrest.16 The authors concluded that the combination of low methodological quality of the studies, insufficient power from previous studies, and lack of temperature management was sufficient evidence of clinical equipoise to study both induced hypothermia against no targeted temperature and 2 subfebrile targeted temperatures.1 Q2.b Could this trial have been performed in the United States? What additional requirements would the investigators have to complete in order to receive institutional review board approval for exception from informed consent? This trial was conducted in 36 centers across the world and did not include any centers in the United States. This may be due to the strict requirements that we have here in the United States in terms of acquiring informed consent in the emergency setting. Informed consent is a necessary and important part of protecting human subjects in research trials. There are many historical examples in which lack of informed consent resulted in injury and unethical treatment of human subjects, most notably the Nazi experiments on prisoners and the Tuskegee study in the United States. The components and requirements of informed consent were described previously in the January 2013 Annals of Emergency Medicine Journal Club.17 Critically ill patients, whether in the emergency or critical care setting, are often incapable of making an informed decision about participating in a clinical trial. The critical data needed to improve the resuscitation science often requires recruitment of the patient when the patient is in extremis and unable to consent. This has led to a shortage of well-designed prospective studies in the treatment of emergency and critical care patients. The requirements of what is considered informed consent vary from country to country. Certain countries allow enrollment when patients enter the hospital, but once the patients are cognizant, they can remove themselves and their data set from the project. Other countries, such as the United States, have very strict policies on how to enroll these patients. In 1996, the Food and Drug Administration authorized a pathway for exception from informed consent for research in the emergency setting for prospective trials. The primary requirement is that investigators conduct a community consultation and the results be reviewed by the institutional review board before starting the trial.18 Other requirements include the following: (1) study design, risks, and benefits must be disclosed to the public; (2) study results must be disclosed to the public; (3) an independent oversight committee must be created; (4) procedures to attempt to obtain informed consent either from the patient or the proxy must be followed; (5) a procedure to notify the patient or proxy of their inclusion in a study must be followed; and (6) procedures to remove the patient from the study at the patient’s or proxy’s request must be followed. Q2.c The authors note the inability to blind the critical care practitioners; however, they were able to blind the assessors providing follow-up neurologic examination. Were the methods used to eliminate the risk of critical care provider bias sufficient? Annals of Emergency Medicine 201
Journal Club The authors note the obvious difficulties with blinding the ICU staff to different temperatures; however, they used multiple methods to decrease the risk of bias elsewhere in their study. Excluding the providers taking care of patients at the bedside, all other study participants were blinded to the groups, including everyone from the neurologic assessors to the investigators. In fact, the authors, per their study protocol, wrote the article blinded to group identity. “During the analysis phase, the intervention groups were identified only as 0 and 1, and the manuscript was written and approved by all the authors before the randomization code was broken.” This writing technique is seldom done but is another way of decreasing bias from authors’ conscious and subconscious beliefs about the intervention’s effect. Our search of the literature did not identify any other studies that included blind writing of articles. This blind article writing likely decreases authors’ preconceived opinions on the anticipated results from actually biasing the honest interpretation of the data. Another unique aspect of the trial design was their neurologic prognostication protocol. The authors used mortality as their primary endpoint instead of neurologically intact survival because it is a hard outcome that is less susceptible to bias. After the cooling and rewarming phases, all patients who had not regained consciousness had a standardized neurologic prognostication examination by an external, blinded assessor. The examination incorporated Glasgow Motor Score, pupillary and corneal reflexes, somatosensory evoked potentials (SSEPs), and electroencephalogram (EEG), and the physician gave a recommendation on whether to continue or withdraw to the treating team. There were 4 predefined findings that would allow withdrawal of intensive care: “(1) [b]rain death due to cerebral herniation; (2) severe myoclonus status in the first 24 hours after admission and a bilateral absence of N20-peak on median nerve SSEP; (3) minimum 72 hours after the intervention period: persisting coma with a Glasgow Motor Score 1-2 and bilateral absence of N20-peak on median nerve SSEP; (4) minimum 72 hours after the end of the intervention period: persisting coma with a Glasgow Motor Score 1-2 and a treatment refractory status epilepticus.”1 Neurologic prognostication assessments have been studied previously; however, we were unable to identify a study using a combination of clinical examination with physiologic testing. A recent meta-analysis of cardiac arrest patients treated with hypothermia evaluated Glasgow Motor Score and SSEPs for neurologic prognostication after cardiac arrest.19 Bilateral absence of N20 response (median nerve) to SSEPs at 72 hours was associated with a false-positive rate of 0.007 (95% CI 0.001 to 0.047) for poor neurologic outcome, missing 1 patient of 492 who regained consciousness. Glasgow Motor Score at 72 hours was less reliable, with a false-positive rate of 0.21 (95% CI 0.08 to 0.43). Malignant EEG patterns and status epilepticus were poor prognostic factors after cardiac arrest,20,21 but they were never studied in combination with Glasgow Motor Score at 72 hours to predict neurologic recovery. By requiring 72 hours after intervention for neurologic prognostication and combining multiple assessments of neurologic outcome for withdrawal of 202 Annals of Emergency Medicine
care, the TTM trial decreased the likelihood that a patient with the potential for neurologic recovery would be missed while still providing clear guidelines for all patients. Finally, the TTM study evaluated 2 interventions, targeting 2 temperatures of 33 C (91.4 F) and 36 C (96.8 F). A temperature of 36 C (96.8 F) is more of an active control group, in which a set temperature that prevents fever has to be closely monitored. In comparison, the study by Bernard et al2 and the Hypothermia After Cardiac Arrest study used a control group that targeted a less specific “normothermia.” However, both of these studies used a strict protocol for the supplemental care of patients assigned to both the hypothermia and the normothermia group,2,3 but they did not strictly prevent fever. In medical literature, we may be skeptical if a study compares an intervention to usual care because it is possible that the intervention group receives cointerventions other than the primary intervention that the control group did not receive.22,23
ANSWER 3 Q3. The authors examined the primary outcome of survival time and followed patients up to the end of the trial (ie, 180 days after the enrollment of the last patient) and powered the study to this outcome. Q3.a The trial was designed as a superiority trial to detect a 20% reduction in the hazard ratio for death with hypothermia at 33 C (91.4 F) versus a control group at 36 C (96.8 F). Was the study appropriately powered for this outcome? The trial protocol provided in the supplementary material reveals several calculations of the sample size, with 90% power and a 2-sided significance level (a) of .05. Recall that a is the risk of type I error, which occurs when the null hypothesis is rejected but in reality the null hypothesis is correct. For the TTM trial, the null hypothesis is that targeting a temperature of 33 C (91.4 F) is equal to 36 C (96.8 F) for mortality after cardiac arrest. Type II error (b) is the risk that the null hypothesis is accepted when in reality the null hypothesis is incorrect. For the TTM trial, a type II error occurs if the study is unable to detect a difference between the 2 treatments when in reality cooling to 33 C (91.4 F) is 20% better than 36 C (96.8 F) or vice versa for mortality after cardiac arrest. Type II error often occurs because the trial enrolls fewer patients than planned or is otherwise underpowered. The power is the probability that the null hypothesis is appropriately rejected, and power is equal to 1–b.24,25 As mentioned in the question stem, the sample size was calculated according to a power of 90% for a 20% reduction in the hazard ratio for death, which is the equivalent to an absolute risk reduction in mortality of 11%. This number was calculated according to various estimates of mortality from previous research. As noted in the answer to question 1a, the Hypothermia After Cardiac Arrest trial3 had a 6-month mortality of 55% in the normothermia group and 41% in the hypothermia group, whereas the trial by Bernard et al2 had mortality percentages of 68% and 51%, respectively. One of the examples provided in the protocol estimates the mortality in the 36 C Volume 64, no. 2 : August 2014
Journal Club (96.8 F) group to be 55% versus 44% in the 33 C (91.4 F) group, which would require 856 patients to reject the null hypothesis with 90% power. In the trial, the difference in mortality between the 2 groups was much lower, 49.7% in the 33 C (91.4 F) group and 48.3% in the 36 C (96.8 F) group, for a total difference of 1.4%. This trial was underpowered to demonstrate that a difference of that size was statistically meaningful. As a thought experiment, one could calculate how many patients would be required to have a 90% chance of detecting a 1.4% difference if that were the true value. A little math indicates that more than 53,000 patients would be required for such a study.26 The cost of such a study is difficult to justify, given the small difference this would make in outcome. Q3.b How do the power calculations change if the study design was a non-inferiority trial of relative normothermia at 36 C (96.8 F) versus hypothermia at 33 C (91.4 F)? Although classic trials assume with the null hypothesis that there is no difference between interventions and try to disprove this null hypothesis, equivalence and noninferiority trials do the opposite. Their null hypothesis is that there is a difference (of at least a prespecified size), and they try to disprove this, thereby implying that the difference is smaller than that. One of the main differences in a noninferiority trial is that it is focused only on the inferior side of the bell curve, so a 1-sided a is typically used and set at .025 (half the value of 2-sided significance studies). Additionally, because a noninferiority trial is attempting to reject that there is a difference between the 2 treatments, a noninferiority margin is set before initiation of the study. If one wanted to show that there was not a mortality difference of 1% to 2% or more, with an a of .025 and a power of 90%, one would need between 25,000 and 100,000 patients to do so. In general, for a clinically significant difference of x, it takes more patients to show that A is not different from B (a noninferiority or equivalence trial) and fewer to show that A is different from B (a superiority trial).25,27 Steps in Planning a Trial
Superiority
Noninferiority
Set type I error
An appropriate value, typically 2-sided a¼.05
Set power State clinically important difference Estimate dropout rate/loss to follow-up
1–b, typically 80% to 90% An appropriate value
An appropriate value, typically 1-sided a¼.025 Typically 90% An appropriate value, called a noninferiority margin Same
Depends on difficulty of intervention
Q3.c What were the secondary outcomes? Discuss the advantages and disadvantages of using composite outcomes in medical research. The secondary outcomes of the study were the following: (1) composite outcome of all-cause mortality and poor neurologic function, defined as CPC 3 or 4 at 180 days; (2) composite outcome of all-cause mortality and poor neurologic function, defined as mRS 4 or 5 at 180 days; (3) all-cause mortality at 180 days; (4) CPC at 180 days; (5) mRS at 180 days; and (6) adverse Volume 64, no. 2 : August 2014
events, including bleeding, pneumonia, sepsis, electrolyte disorders, hyperglycemia, hypoglycemia, cardiac arrhythmia, and need for renal replacement therapy.1 Although composite outcomes may be of use when they combine distinct characteristics of a clinical situation, they are seldom used in this way. More commonly, individual rare outcomes are combined with the goal of increasing the event rate and thereby decreasing the required sample size. However, composite outcomes can be misleading and difficult to interpret. Many studies have used them to combine rare but disparate events such as mortality and readmission to the hospital. Because composite outcomes give equal weight to each element, a rare but consequential event could be included with a more common but less important event and false conclusions drawn. Composite outcomes can hide negative and positive effects of individual components, and as a result, each component of the composite outcome must be evaluated individually for clinical utility.28 Q3.d Therapeutic hypothermia causes many physiologic changes and potential dangers to the patient. Therefore, the authors also collected the incidence of predefined serious adverse events up to day 7 in the ICU. Which specific adverse events did they collect? Do you think these adverse events and 7-day time interval were sufficient? If not, what other events or time intervals might you have chosen? Therapeutic hypothermia decreases the metabolic rate of the brain by an estimated 6% to 7% for every 1 C (1.8 F) decrease in temperature.29 Theoretically, this might allow the brain to rest and repair; however, there are also many adverse events that occur as the body temperature decreases. According to previous clinical trials, case series, and experience during the last few decades, these adverse events have been well elucidated and include shivering, coagulopathy, electrolyte losses, glucose dysregulation, sepsis, infection, cold-related renal diuresis, myocardial stunning, and cardiac dysrhythmias.16 The authors collected a comprehensive list of adverse events: bleeding, pneumonia, sepsis, electrolyte disorders, hyperglycemia, hypoglycemia, cardiac arrhythmia, and need for renal replacement therapy. The study protocol had these complications recorded within 24 hours of the event for the first 7 days in the ICU. Since the cooling intervention lasted 36 hours, any identifiable complications should arise within 7 days. The one adverse event that was not listed is shivering. The authors did not list shivering as a collected adverse event; however, in the supplement, the authors report collecting data on shivering and found no difference between the 2 groups.1 Q3.e To evaluate neurologic outcomes, the authors used the CPC and the mRS. For scores to be effective, they should be already validated. Are these 2 scores previously validated? Are there other scores that the authors could have used? The authors used the CPC and the mRS to determine neurologic outcome in their study. Because of its simplicity and ability to separate “good” versus “bad” outcomes, the CPC is used regularly to assess neurologic outcomes in research studies. The CPC was an adaptation of the Glasgow Outcome Scale, Annals of Emergency Medicine 203
Journal Club which was developed to assess outcomes among traumatic brain injury survivors.30 The score rates neurologic ability from 1 to 5. CPC
Function
1 2 3 4 5
Good cerebral performance: able to lead a normal life Moderate cerebral disability: conscious, disabled but independent Severe cerebral disability: conscious, disabled, and dependent Coma/vegetative state: unconscious Brain death
Studies have found that the CPC correlates with quality of life, prognosis, and cognitive, neurologic, and functional outcomes in post–cardiac arrest survivors.31-33 However, interrater reliability of assessors ranged from 0.38 to 0.78.33,34 The authors also used the mRS to assess functional status. Similar to the CPC, the mRS is a scale, but instead the mRS uses a 7-point scale, from 0 to 6.35-37 MRS
Function
0 1
No disability No significant disability: has symptoms that do not interfere with activities Slight disability: unable to carry out all activities Moderate disability: requires help but able to walk independently Moderately severe disability: unable to walk and attend to bodily functions without assistance Severe disability: nonambulatory and requires constant assistance and care Dead
2 3 4 5 6
Unlike the CPC, the mRS is more specific in terms of functional status, disability, symptoms, and level of care required for caregivers. It has been widely studied and validated among stroke patients and frequently used in post–cardiac arrest studies.31,38 Other outcome scales that the authors could have considered were the Glasgow Outcome Scale, Extended Glasgow Outcome Scale, Barthel Index, Functional Activities Questionnaire, and Functional Independence Measure. All these have been validated in non–cardiac arrest populations and have different advantages and disadvantages.31 For example, the Functional Independence Measure is very specific in terms of assessing a patient’s functional status but is time consuming because it requires testing of 18 elements with a score that ranges from 18 to 126.
ANSWER 4 Q4. For analysis of their results, hazard ratios were used for the analysis of their primary outcome (end of trial mortality), but risk ratios were used to analyze their secondary outcomes (CPC score, mRS). What are the differences between hazard ratios and risk ratios? Why didn’t the authors use hazard ratios for the primary outcome and hazard ratios for secondary outcomes? [Editor’s note: Since the publication of the questions, the wording of this question was changed to be more accurate regarding hazard ratios.] 204 Annals of Emergency Medicine
Risk ratios and hazard ratios are related, but there are some important differences. The risk ratio is synonymous with the relative risk and is defined as “the proportion of the original risk that is still present when patients receive the experimental treatment.”39 Because the TTM trial examines the risk ratio for the secondary outcome of a poor neurologic outcome with CPC score of 3 to 5 at 180 days, it provides a good example. Treatment Group
33 C (91.4 F) 36 C (96.8 F) Overall
Risk Ratio ¼
CPC 1–2
CPC 3–5
Total Patients
218 222 440
251 242 493
469 464 933
Probability of CPC 35 in 33 C ¼ Probability of CPC 35 in 36 C
251 469 242 464
¼ 1:02
Hazard ratios differ from risk ratios because a hazard ratio is a statistical estimate of the weighted relative risk or risk ratio over time. Cox proportional hazards models are most frequently used because they can be applied to many clinical study designs.40 In the TTM trial, patients were followed up for 180 days after enrollment of the last patient. Therefore, each patient was in the study for a different amount of time. The first patient in the study was enrolled in November 2010 and therefore had 900 days during which he could die. The last patient had only 180 days of exposure. The hazard ratio attempts to adjust for the differential exposure of each participant. Because not all patients were followed up for the same period, the authors did not calculate a risk ratio for the primary outcome; however, they did provide a risk ratio for mortality at 180 days, which was nearly identical between the 2 groups, at 1.01. To define the hazard ratio more completely, we must understand the hazard rate, which is an estimate of the likelihood that an outcome in question—mortality in the TTM trial—will occur during the next interval divided by the length of that interval. For more visually inclined learners, please refer to Figure 2 from the TTM trial, the Kaplan-Meier curve for survival. The hazard rate is the slope of the tangent line at any point on the graph. The hazard rate or slope is not the same at every point on a Kaplan-Meier curve; however, in proportional hazards regression models (ie, Cox, which was used in the TTM trial) the hazard rate is assumed to be constant over time and hence represents a statistical estimate of the true hazard rate. From the calculated hazard rate from each group, the hazard ratio is used to compare the hazard rate in the treated group versus the hazard rate in the control group. Hazard Ratio ¼
Hazard Rate ðTreatmentÞ Hazard Rate ðControl Þ
Thus, by examining Figure 2 and identifying the similarity between the slopes of the 2 curves, we can understand why the hazard ratio of 1.06 (95% CI 0.89 to 1.28) is not significantly different between the 2 groups for mortality at the end of the trial. Volume 64, no. 2 : August 2014
Journal Club
ANSWER 5 Q5. If you were creating a cardiac arrest protocol in your hospital, what would you set for the target temperature? Do you think the temperature or the protocol is more important for survival? Protocol-driven care using evidence-based medicine has improved patient outcomes in the ICU,41,42 although the recently published Protocolized Care for Early Septic Shock (PROCESS) trial provides contradictory evidence.43 Health care systems innately function more efficiently when caregivers are familiar with the process of caring for a specific patient. Therefore, post–cardiac arrest patients undergoing targeted temperature management, regardless of the temperature choice, should have a process in place to target a temperature in the same manner throughout the institution. Because there are many similarities among cardiac arrest patients, other aspects of their care should be managed in a similar fashion from patient to patient. However, there must also be leeway to allow individualized care of patients. According to the available evidence and the varying opinions in the medical community, clinical equipoise still exists between 33 C (91.4 F) and 36 C (96.8 F), making it difficult to mandate that physicians target either 33 C (91.4 F) or 36 C (96.8 F), and the decision should be left to their own judgment. In the TTM trial, both temperature groups stress the importance of prevention of fever, which has been shown to worsen outcomes in several studies.12,13,44 Additionally, the period of fever prevention extended for up to 72 hours after cardiac arrest in both groups, and Table S6 from the supplementary appendix shows that the median cumulative hours of fever for each patient was 0 and increased to 1 on days 3 to 7.1 According to the TTM study, the salient point is that any post–cardiac arrest protocol that is adopted should aggressively aim to prevent fever. Some patients will tolerate a temperature of 33 C (91.4 F) better than 36 C (96.8 F) and vice versa, and future research will need to guide any changes to the current evidence. Section editors: Tyler W. Barrett, MD, MSCI; David L. Schriger, MD, MPH Author affiliations: From the University of California, Los Angeles, CA (Rolston); and Harvard School of Medicine, Boston, MA (Lee). REFERENCES 1. Nielsen N, Wetterslev J, Cronberg T, et al. Targeted temperature management at 33 C versus 36 C after cardiac arrest. N Engl J Med. 2013;369:2197-2206. 2. Bernard SA, Gray TW, Buist MD, et al. Treatment of comatose survivors of out-of-hospital cardiac arrest with induced hypothermia. N Engl J Med. 2002;346:557-563. 3. Hypothermia After Cardiac Arrest Study Group. Mild therapeutic hypothermia to improve the neurologic outcome after cardiac arrest. N Engl J Med. 2002;346:549-556. 4. Fisher GC. Hypothermia after cardiac arrest: feasible but is it therapeutic? Anaesthesia. 2008;63:885-886. 5. Moran JL, Solomon PJ. Therapeutic hypothermia after cardiac arrest—once again. Crit Care Resusc. 2006;8:151-154.
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6. Pechlaner C, Joannidis M. Therapeutic hypothermia after cardiopulmonary resuscitation—pro and con. Wien Med Wochenschr. 2008;158:627-633. 7. Nielsen N, Friberg H, Gluud C, et al. 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. 8. Hachimi-Idrissi S, Corne L, Ebinger G, et al. Mild hypothermia induced by a helmet device: a clinical feasibility study. Resuscitation. 2001;51:275-281. 9. Hachimi-Idrissi S, Zizi M, Nguyen DN, et al. The evolution of serum astroglial S-100 b protein in patients with cardiac arrest treated with mild hypothermia. Resuscitation. 2005;64:187-192. 10. Laurent I, Adrie C, Vinsonneau C, et al. High-volume hemofiltration after out-of-hospital cardiac arrest: a randomized study. J Am Coll Cardiol. 2005;46:432-437. 11. Kim Y-M, Yim H-W, Jeong S-H, et al. Does therapeutic hypothermia benefit adult cardiac arrest patients presenting with non-shockable initial rhythms? a systematic review and meta-analysis of randomized and non-randomized studies. Resuscitation. 2012;83: 188-196. 12. Bro-Jeppesen J, Hassager C, Wanscher M, et al. Post-hypothermia fever is associated with increased mortality after out-of-hospital cardiac arrest. Resuscitation. 2013;84:1734-1740. 13. Leary M, Grossestreuer AV, Iannacone S, et al. Pyrexia and neurologic outcomes after therapeutic hypothermia for cardiac arrest. Resuscitation. 2013;84:1056-1061. 14. Freedman B. Equipoise and the ethics of clinical research. N Engl J Med. 1987;317:141-145. 15. Guyatt G, Oxman AD, Akl EA, et al. GRADE guidelines: 1. Introduction—GRADE evidence profiles and summary of findings tables. J Clin Epidemiol. 2011;64:383-394. 16. Perman SM, Goyal M, Neumar RW, et al. Clinical applications of targeted temperature management. Chest. 2014;145:386-393. 17. Eucker SA, Barrett TW, Schriger DL. Are 2 drugs better than 1 for acute agitation? a discussion on black box warnings, waiver of informed consent, and the ethics of enrolling impaired subjects in clinical trials: answers to the January 2013 Journal Club Questions. Ann Emerg Med. 2013;61:708-716. 18. Dickert NW, Govindarajan P, Harney D, et al. Community consultation for prehospital research: experiences of study coordinators and principal investigators. Prehosp Emerg Care. 2014;18:274-281. 19. Kamps MJA, Horn J, Oddo M, et al. Prognostication of neurologic outcome in cardiac arrest patients after mild therapeutic hypothermia: a meta-analysis of the current literature. Intensive Care Med. 2013;39:1671-1682. 20. Fugate JE, Wijdicks EFM, Mandrekar J, et al. Predictors of neurologic outcome in hypothermia after cardiac arrest. Ann Neurol. 2010;68:907-914. 21. Taccone FS, Cronberg T, Friberg H, et al. How to assess prognosis after cardiac arrest and therapeutic hypothermia. Crit Care. 2014; 18:202. 22. Schulz KF, Grimes DA. Blinding in randomised trials: hiding who got what. Lancet. 2002;359:696-700. 23. Karanicolas PJ, Farrokhyar F, Bhandari M. Blinding: who, what, when, why, how? Can J Surg. 2010;53:345-348. 24. Sakpal TV. Sample size estimation in clinical trial. Perspect Clin Res. 2010;1:67-69. 25. Julious SA, Campbell MJ. Tutorial in biostatistics: sample sizes for parallel group clinical trials with binary data. Stat Med. 2012;31:2904-2936. 26. Blackwelder WC. “Proving the null hypothesis” in clinical trials. Control Clin Trials. 1982;3:345-353.
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Journal Club 27. Head SJ, Kaul S, Bogers AJJC, Kappetein AP. Non-inferiority study design: lessons to be learned from cardiovascular trials. Eur Heart J. 2012;33(11):1318-1324. 28. Brown AM, Schriger DL, Barrett TW. Annals of Emergency Medicine Journal Club. Outcome measures, interim analyses, and bayesian approaches to randomized trials: answers to the September 2009 Journal Club questions. Ann Emerg Med. 2010;55:216-224.e1. 29. Rosomoff HL, Holaday DA. Cerebral blood flow and cerebral oxygen consumption during hypothermia. Am J Physiol. 1954;179:85-88. 30. Jennett B, Bond M. Assessment of outcome after severe brain damage. Lancet. 1975;1:480-484. 31. Becker LB, Aufderheide TP, Geocadin RG, et al. Primary outcomes for resuscitation science studies: a consensus statement from the American Heart Association. Circulation. 2011;124:2158-2177. 32. Phelps R, Dumas F, Maynard C, et al. Cerebral Performance Category and long-term prognosis following out-of-hospital cardiac arrest. Crit Care Med. 2013;41:1252-1257. 33. Stiell IG, Nesbitt LP, Nichol G, et al. Comparison of the Cerebral Performance Category score and the Health Utilities Index for survivors of cardiac arrest. Ann Emerg Med. 2009;53:241-248. 34. Ajam K, Gold LS, Beck SS, et al. Reliability of the Cerebral Performance Category to classify neurological status among survivors of ventricular fibrillation arrest: a cohort study. Scand J Trauma Resusc Emerg Med. 2011;19:38.
35. Rankin J. Cerebral vascular accidents in patients over the age of 60. II. Prognosis. Scott Med J. 1957;2:200-215. 36. Van Swieten JC, Koudstaal PJ, Visser MC, et al. Interobserver agreement for the assessment of handicap in stroke patients. Stroke. 1988;19:604-607. 37. Bonita R, Beaglehole R. Recovery of motor function after stroke. Stroke. 1988;19:1497-1500. 38. Banks JL, Marotta CA. Outcomes validity and reliability of the modified Rankin scale: implications for stroke clinical trials: a literature review and synthesis. Stroke. 2007;38:1091-1096. 39. Guyatt G, Meade MO, Rennie D, et al. User’s Guide to the Medical Literature: A Manual for Evidence-Based Clinical Practice. 2nd ed. New York: McGraw-Hill Professional; 2008. 40. Spruance SL, Reid JE, Grace M, et al. Hazard ratio in clinical trials. Antimicrob Agents Chemother. 2004;48:2787-2792. 41. Morris AH. Treatment algorithms and protocolized care. Curr Opin Crit Care. 2003;9:236-240. 42. Wendon J. Critical care “normality”: individualized versus protocolized care. Crit Care Med. 2010;38(10 suppl):S590-S599. 43. The ProCESS Investigators. A randomized trial of protocol-based care for early septic shock. N Engl J Med. 2014;370:1683-1693. 44. Zeiner A, Holzer M, Sterz F, et al. Hyperthermia after cardiac arrest is associated with an unfavorable neurologic outcome. Arch Intern Med. 2001;161:2007-2012.
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206 Annals of Emergency Medicine
Volume 64, no. 2 : August 2014
Is It Still Cool to Cool? Interpreting the Latest Hypothermia for Cardiac Arrest Trial Answers to the March 2014 Journal Club Questions Daniel M. Rolston, MD, MS; Jarone Lee, MD, MPH 0196-0644/$-see front matter Copyright © 2014 by the American College of Emergency Physicians. http://dx.doi.org/10.1016/j.annemergmed.2014.05.008
Editor’s Note: You are reading the 38th installment of Annals of Emergency Medicine Journal Club. This Journal Club refers to the Nielsen et al1 article titled “Targeted Temperature Management at 33 C Versus 36 C After Cardiac Arrest” that was published in The New England Journal of Medicine. Information about journal club can be found at http://www.annemergmed.com/content/ journalclub. Readers should recognize that these are suggested answers. We hope they are accurate; we know that they are not comprehensive. There are many other points that could be made about these questions or about the article in general. Questions are rated “novice,” ( ) “intermediate,” ( ) and “advanced ( ) so that individuals planning a journal club can assign the right question to the right student. The “novice” rating does not imply that a novice should be able to spontaneously answer the question. “Novice” means we expect that someone with little background should be able to do a bit of reading, formulate an answer, and teach the material to others. Intermediate and advanced questions also will likely require some reading and research, and that reading will be sufficiently difficult that some background in clinical epidemiology will be helpful in understanding the reading and concepts. We are interested in receiving feedback about this feature. Please e-mail [email protected] with your comments.
DISCUSSION POINTS 1. The authors reference 2 previous trials that compared therapeutic hypothermia (32 C to 34 C [89.6 F to 93.2 F] for 12 to 24 hours) with standard treatment and “showed a significant improvement in neurologic function and survival with therapeutic hypothermia.” A. What was the treatment effect in the previous 2 studies? What percentage of patients had neurologically intact survival? How many patients would one need to treat with hypothermia to produce 1 additional neurologically intact patient? B. There is good evidence that the presence of an initial shockable rhythm greatly enhances the probability of survival from cardiac arrest. Have any randomized trials demonstrated an improvement in neurologic outcomes in patients whose initial rhythm was pulseless electrical activity or asystole? 2. Previous studies have reported deleterious effects when patients recovering from an out-of-hospital cardiac arrest develop fever, leading authors to question whether Volume 64, no. 2 : August 2014
reported benefits are due to hypothermia or prevention of hyperthermia. The authors conducted a multicenter, international trial that randomized unconscious adults, who had return of spontaneous circulation after out-ofhospital cardiac arrest, to either 33 C or 36 C (91.4 F or 96.8 F) temperature target. A. The current recommendation by many expert consensus groups is to cool out-of-hospital cardiac arrest victims to 32 C to 34 C (89.6 F to 93.2 F) after ventricular fibrillation and possibly other rhythms. The authors did not follow this recommendation for one of the arms of the study. Do you believe there was equipoise? Discuss the importance of equipoise in clinical research. B. Could this trial have been performed in the United States? What additional requirements would the investigators have to complete to receive institutional review board approval for exception from informed consent? C. The authors note the inability to blind the critical care practitioners; however, they were able to blind the assessors providing follow-up neurologic examination. Were the methods used to eliminate the risk of critical care provider bias sufficient? 3. The authors examined the primary outcome of survival time and followed patients up to the end of the trial (ie, 180 days after the enrollment of the last patient) and powered the study to this outcome. A. The trial was designed as a superiority trial to detect a 20% reduction in the hazard ratio for death with hypothermia at 33 C (91.4 F) versus a control group at 36 C (96.8 F). Was the study appropriately powered for this outcome? B. How would the power calculations change if the study design were a noninferiority trial of relative normothermia at 36 C (96.8 F) versus hypothermia at 33 C (91.4 F)? C. What were the secondary outcomes? Discuss the advantages and disadvantages of using composite outcomes in medical research. D. Therapeutic hypothermia causes many physiologic changes and potential dangers to the patient. Therefore, the authors also collected the incidence of predefined serious adverse events up to day 7 in the ICU. Which specific adverse events did they collect? Do you think these Annals of Emergency Medicine 199
Journal Club adverse events and 7-day interval were sufficient? If not, what other events or intervals might you have chosen? E. To evaluate neurologic outcomes, the authors used the Cerebral Performance Category (CPC) and the modified Rankin score (mRS). For scores to be effective, they should be already validated. Have these 2 scores been previously validated? Are there other scores that the authors could have used? 4. For analysis of their results, hazard ratios were used for the analysis of their primary outcome (end of trial mortality), but risk ratios were used to analyze their secondary outcomes (CPC score, mRS). What are the differences between hazard ratios and risk ratios? Why didn’t the authors use hazard ratios for the primary outcome and hazard ratios for secondary outcomes? [Editor’s note: Since the publication of the questions, the wording of this question was changed to be more accurate in regard to hazard ratios.] 5. If you were creating a cardiac arrest protocol in your hospital, what would you set for the target temperature? Do you think the temperature or the protocol is more important for survival?
ANSWER 1
Q1. The authors reference 2 previous trials2,3 that compared therapeutic hypothermia (32 C to 34 C [89.6 F to 93.2 F] for 12 to 24 hours) with standard treatment and “showed a significant improvement in neurologic function and survival with therapeutic hypothermia.”1 Q1.a What was the treatment effect in the previous 2 studies? What percentage of patients had improved neurologically intact survival? How many patients would you need to treat with hypothermia to produce one additional neurologically intact patient? Bernard et al2 conducted an Australian study that randomized 77 cardiac arrest patients to either hypothermia with a goal temperature of 33 C (91.4 F) or normothermia with a targeted temperature of 37 C (98.6 F). The primary outcome in this study was good outcome, which was defined as either normal or minimal disability with discharge to home or moderate disability with discharge to a rehabilitation facility. The bad outcome was considered as either inhospital death or severe disability with discharge to a nursing home. The good outcome proportions in the hypothermia group and normothermia groups were 48.8% and 26.5%, respectively. Therefore, the study’s treatment, the absolute risk reduction for good outcome, was 22.3% (95% confidence interval [CI] 13% to 43%) for the hypothermia group. The number needed to treat, defined as (1/absolute risk reduction [expressed as a decimal, eg, 0.223), was 4.5 patients (95% CI 2.3 to 7.7 patients). This means that, if the study is correct, 4.5 patients need to be treated with a hypothermia protocol for 1 additional patient to have a “good outcome.” The Hypothermia After Cardiac Arrest Study Group published their results in the same issue of The New England Journal of Medicine,3 providing additional evidence supporting 200 Annals of Emergency Medicine
the use of hypothermia. This study enrolled 275 witnessed cardiac arrest patients without return of neurologic function who were randomized to a goal temperature of 32 C to 34 C (89.6 F to 93.2 F), or “normothermia.” The primary outcome was favorable neurologic outcome as measured by a Pittsburgh CPC of 1 to 2 (good performance–moderate disability). In the hypothermia group, 55.1% had good neurologic function compared with 39.4% in the normothermia group. The absolute risk reduction was 15.7%, corresponding to a number needed to treat equal to 6.4 patients (95% CI 4 to 25 patients). The number needed to treat of 4.5 to 6.4 patients to improve neurologically intact survival resulted in strong support for the international adoption of therapeutic hypothermia for comatose cardiac arrest survivors from ventricular tachycardia and ventricular fibrillation. However, several studies questioned the validity of the studies for the widespread application of hypothermia.4-7 Q1.b There is good evidence that the presence of an initial shockable rhythm greatly enhances the probability of survival from cardiac arrest. Have any randomized trials demonstrated an improvement in neurologic outcomes in patients whose initial rhythm was pulseless electrical activity or asystole? Although the evidence for hypothermia with shockable rhythms is much more robust, before the Targeted Temperature Management (TTM) trial there were only 2 randomized controlled trials evaluating hypothermia’s use after cardiac arrest in the nonshockable rhythms of pulseless electrical activity and asystole. The only randomized controlled trial evaluating hypothermia specifically for nonshockable rhythms is a feasibility study from 2001 that used a helmet cooling device. This study randomized 30 patients to hypothermia at 34 C (93.2 F) versus normothermia. Mortality in the hypothermia group was 81.3%, whereas mortality in the normothermia group was 92.9%,8 which was not a statistically significant difference. A 2005 reanalysis of this study showed that neurologically intact survival was 12.5% in the hypothermia group and 0% in the normothermia group.9 Laurent et al10 included 26% of patients with asystole as the initial rhythm in a trial that randomized patients to hemofiltration plus hypothermia, hemofiltration alone, or usual care. The hemofiltration and hemofiltration with hypothermia groups showed statistically improved survival at 6 months (45% and 32%, respectively) versus usual care (21%). These randomized trials do not show a clear benefit for hypothermia in nonshockable rhythms. However, a recent metaanalysis demonstrated improved inhospital mortality without improved neurologic outcome in nonrandomized studies.11 The largest randomized trials before the TTM trial did not include patients with nonshockable rhythms. Bernard et al2 enrolled patients with an initial rhythm of ventricular fibrillation, whereas Hypothermia After Cardiac Arrest3 enrolled patients with an initial rhythm of ventricular tachycardia or ventricular fibrillation. The TTM trial is currently the largest randomized controlled trial including patients with nonshockable rhythms. Pulseless electrical activity was present as the initial rhythm in 7% of patients, whereas witnessed asystole was the initial Volume 64, no. 2 : August 2014
Journal Club rhythm in 12%. Although always requiring a cautious interpretation, subgroup analysis in the supplementary appendix showed no significant difference between 33 C and 36 C (91.4 F to 96.8 F) for shockable or nonshockable rhythms.1
ANSWER 2 Q2. Previous studies have reported deleterious effects when patients recovering from an out-of-hospital cardiac arrest develop fever1,12,13 leading authors to question whether reported benefits are due to hypothermia or prevention of hyperthermia. The authors conducted a multicenter, international trial that randomized unconscious adults, who had return of spontaneous circulation after out-of-hospital cardiac arrest, to either 33 C (91.4 F) or 36 C (96.8 F) temperature target. Q2.a The current recommendation by many expert consensus groups is to cool out-of-hospital cardiac arrest victims to 32 C to 34 C (89.6 F to 93.2 F) after ventricular fibrillation and possibly other rhythms. The authors did not follow this recommendation for one of the arms of the study. Do you believe there was equipoise? Discuss the importance of equipoise in clinical research. Equipoise exists when there is uncertainty in efficacy between different treatment options. When designing studies, researchers have an ethical duty to ensure that the study has equipoise. However, true equipoise is fragile and difficult to attain because once an investigator or clinician has a bias toward one treatment over another, the test of equipoise fails. As a result, in 1987 Freedman14 defined a state of “clinical equipoise.” In clinical equipoise, the state of uncertainty exists “if there is genuine uncertainty within the expert medical community—not necessarily on the part of the individual.”14 Freedman14 changed the focus away from the individual and moved the discussion to the medical community. Then he went further and stated that “an honest, professional disagreement” must exist for clinical equipoise to exist. To satisfy this condition of clinical equipoise, the TTM authors performed a literature review of the evidence quality currently available. This review is published in the TTM trial protocol. They found 5 trials and found that current guidelines on therapeutic hypothermia were based primarily on 2 randomized controlled trials.2,3 Many methodological flaws were found in all the trials, and the Grading of Recommendations Assessment, Development and Evaluation (GRADE) quality of evidence was determined to be “low.”15 The TTM authors also conducted an advanced statistical technique called trial sequential analysis, which is beyond the scope of this answer, and determined that after pooling all the studies, an additional 600 to 800 patients would be required to have adequate power to accept or reject induced hypothermia as a treatment for comatose cardiac arrest survivors. In other words, the authors found that the pooled patients from the trials were not sufficiently powered to examine the outcomes of interest. The lack of fever management in the control arms was another major limitation in the previous studies on induced hypothermia after cardiac arrest. Increased temperature is Volume 64, no. 2 : August 2014
common and associated with worse outcomes within the first 48 hours after cardiac arrest.16 The authors concluded that the combination of low methodological quality of the studies, insufficient power from previous studies, and lack of temperature management was sufficient evidence of clinical equipoise to study both induced hypothermia against no targeted temperature and 2 subfebrile targeted temperatures.1 Q2.b Could this trial have been performed in the United States? What additional requirements would the investigators have to complete in order to receive institutional review board approval for exception from informed consent? This trial was conducted in 36 centers across the world and did not include any centers in the United States. This may be due to the strict requirements that we have here in the United States in terms of acquiring informed consent in the emergency setting. Informed consent is a necessary and important part of protecting human subjects in research trials. There are many historical examples in which lack of informed consent resulted in injury and unethical treatment of human subjects, most notably the Nazi experiments on prisoners and the Tuskegee study in the United States. The components and requirements of informed consent were described previously in the January 2013 Annals of Emergency Medicine Journal Club.17 Critically ill patients, whether in the emergency or critical care setting, are often incapable of making an informed decision about participating in a clinical trial. The critical data needed to improve the resuscitation science often requires recruitment of the patient when the patient is in extremis and unable to consent. This has led to a shortage of well-designed prospective studies in the treatment of emergency and critical care patients. The requirements of what is considered informed consent vary from country to country. Certain countries allow enrollment when patients enter the hospital, but once the patients are cognizant, they can remove themselves and their data set from the project. Other countries, such as the United States, have very strict policies on how to enroll these patients. In 1996, the Food and Drug Administration authorized a pathway for exception from informed consent for research in the emergency setting for prospective trials. The primary requirement is that investigators conduct a community consultation and the results be reviewed by the institutional review board before starting the trial.18 Other requirements include the following: (1) study design, risks, and benefits must be disclosed to the public; (2) study results must be disclosed to the public; (3) an independent oversight committee must be created; (4) procedures to attempt to obtain informed consent either from the patient or the proxy must be followed; (5) a procedure to notify the patient or proxy of their inclusion in a study must be followed; and (6) procedures to remove the patient from the study at the patient’s or proxy’s request must be followed. Q2.c The authors note the inability to blind the critical care practitioners; however, they were able to blind the assessors providing follow-up neurologic examination. Were the methods used to eliminate the risk of critical care provider bias sufficient? Annals of Emergency Medicine 201
Journal Club The authors note the obvious difficulties with blinding the ICU staff to different temperatures; however, they used multiple methods to decrease the risk of bias elsewhere in their study. Excluding the providers taking care of patients at the bedside, all other study participants were blinded to the groups, including everyone from the neurologic assessors to the investigators. In fact, the authors, per their study protocol, wrote the article blinded to group identity. “During the analysis phase, the intervention groups were identified only as 0 and 1, and the manuscript was written and approved by all the authors before the randomization code was broken.” This writing technique is seldom done but is another way of decreasing bias from authors’ conscious and subconscious beliefs about the intervention’s effect. Our search of the literature did not identify any other studies that included blind writing of articles. This blind article writing likely decreases authors’ preconceived opinions on the anticipated results from actually biasing the honest interpretation of the data. Another unique aspect of the trial design was their neurologic prognostication protocol. The authors used mortality as their primary endpoint instead of neurologically intact survival because it is a hard outcome that is less susceptible to bias. After the cooling and rewarming phases, all patients who had not regained consciousness had a standardized neurologic prognostication examination by an external, blinded assessor. The examination incorporated Glasgow Motor Score, pupillary and corneal reflexes, somatosensory evoked potentials (SSEPs), and electroencephalogram (EEG), and the physician gave a recommendation on whether to continue or withdraw to the treating team. There were 4 predefined findings that would allow withdrawal of intensive care: “(1) [b]rain death due to cerebral herniation; (2) severe myoclonus status in the first 24 hours after admission and a bilateral absence of N20-peak on median nerve SSEP; (3) minimum 72 hours after the intervention period: persisting coma with a Glasgow Motor Score 1-2 and bilateral absence of N20-peak on median nerve SSEP; (4) minimum 72 hours after the end of the intervention period: persisting coma with a Glasgow Motor Score 1-2 and a treatment refractory status epilepticus.”1 Neurologic prognostication assessments have been studied previously; however, we were unable to identify a study using a combination of clinical examination with physiologic testing. A recent meta-analysis of cardiac arrest patients treated with hypothermia evaluated Glasgow Motor Score and SSEPs for neurologic prognostication after cardiac arrest.19 Bilateral absence of N20 response (median nerve) to SSEPs at 72 hours was associated with a false-positive rate of 0.007 (95% CI 0.001 to 0.047) for poor neurologic outcome, missing 1 patient of 492 who regained consciousness. Glasgow Motor Score at 72 hours was less reliable, with a false-positive rate of 0.21 (95% CI 0.08 to 0.43). Malignant EEG patterns and status epilepticus were poor prognostic factors after cardiac arrest,20,21 but they were never studied in combination with Glasgow Motor Score at 72 hours to predict neurologic recovery. By requiring 72 hours after intervention for neurologic prognostication and combining multiple assessments of neurologic outcome for withdrawal of 202 Annals of Emergency Medicine
care, the TTM trial decreased the likelihood that a patient with the potential for neurologic recovery would be missed while still providing clear guidelines for all patients. Finally, the TTM study evaluated 2 interventions, targeting 2 temperatures of 33 C (91.4 F) and 36 C (96.8 F). A temperature of 36 C (96.8 F) is more of an active control group, in which a set temperature that prevents fever has to be closely monitored. In comparison, the study by Bernard et al2 and the Hypothermia After Cardiac Arrest study used a control group that targeted a less specific “normothermia.” However, both of these studies used a strict protocol for the supplemental care of patients assigned to both the hypothermia and the normothermia group,2,3 but they did not strictly prevent fever. In medical literature, we may be skeptical if a study compares an intervention to usual care because it is possible that the intervention group receives cointerventions other than the primary intervention that the control group did not receive.22,23
ANSWER 3 Q3. The authors examined the primary outcome of survival time and followed patients up to the end of the trial (ie, 180 days after the enrollment of the last patient) and powered the study to this outcome. Q3.a The trial was designed as a superiority trial to detect a 20% reduction in the hazard ratio for death with hypothermia at 33 C (91.4 F) versus a control group at 36 C (96.8 F). Was the study appropriately powered for this outcome? The trial protocol provided in the supplementary material reveals several calculations of the sample size, with 90% power and a 2-sided significance level (a) of .05. Recall that a is the risk of type I error, which occurs when the null hypothesis is rejected but in reality the null hypothesis is correct. For the TTM trial, the null hypothesis is that targeting a temperature of 33 C (91.4 F) is equal to 36 C (96.8 F) for mortality after cardiac arrest. Type II error (b) is the risk that the null hypothesis is accepted when in reality the null hypothesis is incorrect. For the TTM trial, a type II error occurs if the study is unable to detect a difference between the 2 treatments when in reality cooling to 33 C (91.4 F) is 20% better than 36 C (96.8 F) or vice versa for mortality after cardiac arrest. Type II error often occurs because the trial enrolls fewer patients than planned or is otherwise underpowered. The power is the probability that the null hypothesis is appropriately rejected, and power is equal to 1–b.24,25 As mentioned in the question stem, the sample size was calculated according to a power of 90% for a 20% reduction in the hazard ratio for death, which is the equivalent to an absolute risk reduction in mortality of 11%. This number was calculated according to various estimates of mortality from previous research. As noted in the answer to question 1a, the Hypothermia After Cardiac Arrest trial3 had a 6-month mortality of 55% in the normothermia group and 41% in the hypothermia group, whereas the trial by Bernard et al2 had mortality percentages of 68% and 51%, respectively. One of the examples provided in the protocol estimates the mortality in the 36 C Volume 64, no. 2 : August 2014
Journal Club (96.8 F) group to be 55% versus 44% in the 33 C (91.4 F) group, which would require 856 patients to reject the null hypothesis with 90% power. In the trial, the difference in mortality between the 2 groups was much lower, 49.7% in the 33 C (91.4 F) group and 48.3% in the 36 C (96.8 F) group, for a total difference of 1.4%. This trial was underpowered to demonstrate that a difference of that size was statistically meaningful. As a thought experiment, one could calculate how many patients would be required to have a 90% chance of detecting a 1.4% difference if that were the true value. A little math indicates that more than 53,000 patients would be required for such a study.26 The cost of such a study is difficult to justify, given the small difference this would make in outcome. Q3.b How do the power calculations change if the study design was a non-inferiority trial of relative normothermia at 36 C (96.8 F) versus hypothermia at 33 C (91.4 F)? Although classic trials assume with the null hypothesis that there is no difference between interventions and try to disprove this null hypothesis, equivalence and noninferiority trials do the opposite. Their null hypothesis is that there is a difference (of at least a prespecified size), and they try to disprove this, thereby implying that the difference is smaller than that. One of the main differences in a noninferiority trial is that it is focused only on the inferior side of the bell curve, so a 1-sided a is typically used and set at .025 (half the value of 2-sided significance studies). Additionally, because a noninferiority trial is attempting to reject that there is a difference between the 2 treatments, a noninferiority margin is set before initiation of the study. If one wanted to show that there was not a mortality difference of 1% to 2% or more, with an a of .025 and a power of 90%, one would need between 25,000 and 100,000 patients to do so. In general, for a clinically significant difference of x, it takes more patients to show that A is not different from B (a noninferiority or equivalence trial) and fewer to show that A is different from B (a superiority trial).25,27 Steps in Planning a Trial
Superiority
Noninferiority
Set type I error
An appropriate value, typically 2-sided a¼.05
Set power State clinically important difference Estimate dropout rate/loss to follow-up
1–b, typically 80% to 90% An appropriate value
An appropriate value, typically 1-sided a¼.025 Typically 90% An appropriate value, called a noninferiority margin Same
Depends on difficulty of intervention
Q3.c What were the secondary outcomes? Discuss the advantages and disadvantages of using composite outcomes in medical research. The secondary outcomes of the study were the following: (1) composite outcome of all-cause mortality and poor neurologic function, defined as CPC 3 or 4 at 180 days; (2) composite outcome of all-cause mortality and poor neurologic function, defined as mRS 4 or 5 at 180 days; (3) all-cause mortality at 180 days; (4) CPC at 180 days; (5) mRS at 180 days; and (6) adverse Volume 64, no. 2 : August 2014
events, including bleeding, pneumonia, sepsis, electrolyte disorders, hyperglycemia, hypoglycemia, cardiac arrhythmia, and need for renal replacement therapy.1 Although composite outcomes may be of use when they combine distinct characteristics of a clinical situation, they are seldom used in this way. More commonly, individual rare outcomes are combined with the goal of increasing the event rate and thereby decreasing the required sample size. However, composite outcomes can be misleading and difficult to interpret. Many studies have used them to combine rare but disparate events such as mortality and readmission to the hospital. Because composite outcomes give equal weight to each element, a rare but consequential event could be included with a more common but less important event and false conclusions drawn. Composite outcomes can hide negative and positive effects of individual components, and as a result, each component of the composite outcome must be evaluated individually for clinical utility.28 Q3.d Therapeutic hypothermia causes many physiologic changes and potential dangers to the patient. Therefore, the authors also collected the incidence of predefined serious adverse events up to day 7 in the ICU. Which specific adverse events did they collect? Do you think these adverse events and 7-day time interval were sufficient? If not, what other events or time intervals might you have chosen? Therapeutic hypothermia decreases the metabolic rate of the brain by an estimated 6% to 7% for every 1 C (1.8 F) decrease in temperature.29 Theoretically, this might allow the brain to rest and repair; however, there are also many adverse events that occur as the body temperature decreases. According to previous clinical trials, case series, and experience during the last few decades, these adverse events have been well elucidated and include shivering, coagulopathy, electrolyte losses, glucose dysregulation, sepsis, infection, cold-related renal diuresis, myocardial stunning, and cardiac dysrhythmias.16 The authors collected a comprehensive list of adverse events: bleeding, pneumonia, sepsis, electrolyte disorders, hyperglycemia, hypoglycemia, cardiac arrhythmia, and need for renal replacement therapy. The study protocol had these complications recorded within 24 hours of the event for the first 7 days in the ICU. Since the cooling intervention lasted 36 hours, any identifiable complications should arise within 7 days. The one adverse event that was not listed is shivering. The authors did not list shivering as a collected adverse event; however, in the supplement, the authors report collecting data on shivering and found no difference between the 2 groups.1 Q3.e To evaluate neurologic outcomes, the authors used the CPC and the mRS. For scores to be effective, they should be already validated. Are these 2 scores previously validated? Are there other scores that the authors could have used? The authors used the CPC and the mRS to determine neurologic outcome in their study. Because of its simplicity and ability to separate “good” versus “bad” outcomes, the CPC is used regularly to assess neurologic outcomes in research studies. The CPC was an adaptation of the Glasgow Outcome Scale, Annals of Emergency Medicine 203
Journal Club which was developed to assess outcomes among traumatic brain injury survivors.30 The score rates neurologic ability from 1 to 5. CPC
Function
1 2 3 4 5
Good cerebral performance: able to lead a normal life Moderate cerebral disability: conscious, disabled but independent Severe cerebral disability: conscious, disabled, and dependent Coma/vegetative state: unconscious Brain death
Studies have found that the CPC correlates with quality of life, prognosis, and cognitive, neurologic, and functional outcomes in post–cardiac arrest survivors.31-33 However, interrater reliability of assessors ranged from 0.38 to 0.78.33,34 The authors also used the mRS to assess functional status. Similar to the CPC, the mRS is a scale, but instead the mRS uses a 7-point scale, from 0 to 6.35-37 MRS
Function
0 1
No disability No significant disability: has symptoms that do not interfere with activities Slight disability: unable to carry out all activities Moderate disability: requires help but able to walk independently Moderately severe disability: unable to walk and attend to bodily functions without assistance Severe disability: nonambulatory and requires constant assistance and care Dead
2 3 4 5 6
Unlike the CPC, the mRS is more specific in terms of functional status, disability, symptoms, and level of care required for caregivers. It has been widely studied and validated among stroke patients and frequently used in post–cardiac arrest studies.31,38 Other outcome scales that the authors could have considered were the Glasgow Outcome Scale, Extended Glasgow Outcome Scale, Barthel Index, Functional Activities Questionnaire, and Functional Independence Measure. All these have been validated in non–cardiac arrest populations and have different advantages and disadvantages.31 For example, the Functional Independence Measure is very specific in terms of assessing a patient’s functional status but is time consuming because it requires testing of 18 elements with a score that ranges from 18 to 126.
ANSWER 4 Q4. For analysis of their results, hazard ratios were used for the analysis of their primary outcome (end of trial mortality), but risk ratios were used to analyze their secondary outcomes (CPC score, mRS). What are the differences between hazard ratios and risk ratios? Why didn’t the authors use hazard ratios for the primary outcome and hazard ratios for secondary outcomes? [Editor’s note: Since the publication of the questions, the wording of this question was changed to be more accurate regarding hazard ratios.] 204 Annals of Emergency Medicine
Risk ratios and hazard ratios are related, but there are some important differences. The risk ratio is synonymous with the relative risk and is defined as “the proportion of the original risk that is still present when patients receive the experimental treatment.”39 Because the TTM trial examines the risk ratio for the secondary outcome of a poor neurologic outcome with CPC score of 3 to 5 at 180 days, it provides a good example. Treatment Group
33 C (91.4 F) 36 C (96.8 F) Overall
Risk Ratio ¼
CPC 1–2
CPC 3–5
Total Patients
218 222 440
251 242 493
469 464 933
Probability of CPC 35 in 33 C ¼ Probability of CPC 35 in 36 C
251 469 242 464
¼ 1:02
Hazard ratios differ from risk ratios because a hazard ratio is a statistical estimate of the weighted relative risk or risk ratio over time. Cox proportional hazards models are most frequently used because they can be applied to many clinical study designs.40 In the TTM trial, patients were followed up for 180 days after enrollment of the last patient. Therefore, each patient was in the study for a different amount of time. The first patient in the study was enrolled in November 2010 and therefore had 900 days during which he could die. The last patient had only 180 days of exposure. The hazard ratio attempts to adjust for the differential exposure of each participant. Because not all patients were followed up for the same period, the authors did not calculate a risk ratio for the primary outcome; however, they did provide a risk ratio for mortality at 180 days, which was nearly identical between the 2 groups, at 1.01. To define the hazard ratio more completely, we must understand the hazard rate, which is an estimate of the likelihood that an outcome in question—mortality in the TTM trial—will occur during the next interval divided by the length of that interval. For more visually inclined learners, please refer to Figure 2 from the TTM trial, the Kaplan-Meier curve for survival. The hazard rate is the slope of the tangent line at any point on the graph. The hazard rate or slope is not the same at every point on a Kaplan-Meier curve; however, in proportional hazards regression models (ie, Cox, which was used in the TTM trial) the hazard rate is assumed to be constant over time and hence represents a statistical estimate of the true hazard rate. From the calculated hazard rate from each group, the hazard ratio is used to compare the hazard rate in the treated group versus the hazard rate in the control group. Hazard Ratio ¼
Hazard Rate ðTreatmentÞ Hazard Rate ðControl Þ
Thus, by examining Figure 2 and identifying the similarity between the slopes of the 2 curves, we can understand why the hazard ratio of 1.06 (95% CI 0.89 to 1.28) is not significantly different between the 2 groups for mortality at the end of the trial. Volume 64, no. 2 : August 2014
Journal Club
ANSWER 5 Q5. If you were creating a cardiac arrest protocol in your hospital, what would you set for the target temperature? Do you think the temperature or the protocol is more important for survival? Protocol-driven care using evidence-based medicine has improved patient outcomes in the ICU,41,42 although the recently published Protocolized Care for Early Septic Shock (PROCESS) trial provides contradictory evidence.43 Health care systems innately function more efficiently when caregivers are familiar with the process of caring for a specific patient. Therefore, post–cardiac arrest patients undergoing targeted temperature management, regardless of the temperature choice, should have a process in place to target a temperature in the same manner throughout the institution. Because there are many similarities among cardiac arrest patients, other aspects of their care should be managed in a similar fashion from patient to patient. However, there must also be leeway to allow individualized care of patients. According to the available evidence and the varying opinions in the medical community, clinical equipoise still exists between 33 C (91.4 F) and 36 C (96.8 F), making it difficult to mandate that physicians target either 33 C (91.4 F) or 36 C (96.8 F), and the decision should be left to their own judgment. In the TTM trial, both temperature groups stress the importance of prevention of fever, which has been shown to worsen outcomes in several studies.12,13,44 Additionally, the period of fever prevention extended for up to 72 hours after cardiac arrest in both groups, and Table S6 from the supplementary appendix shows that the median cumulative hours of fever for each patient was 0 and increased to 1 on days 3 to 7.1 According to the TTM study, the salient point is that any post–cardiac arrest protocol that is adopted should aggressively aim to prevent fever. Some patients will tolerate a temperature of 33 C (91.4 F) better than 36 C (96.8 F) and vice versa, and future research will need to guide any changes to the current evidence. Section editors: Tyler W. Barrett, MD, MSCI; David L. Schriger, MD, MPH Author affiliations: From the University of California, Los Angeles, CA (Rolston); and Harvard School of Medicine, Boston, MA (Lee). REFERENCES 1. Nielsen N, Wetterslev J, Cronberg T, et al. Targeted temperature management at 33 C versus 36 C after cardiac arrest. N Engl J Med. 2013;369:2197-2206. 2. Bernard SA, Gray TW, Buist MD, et al. Treatment of comatose survivors of out-of-hospital cardiac arrest with induced hypothermia. N Engl J Med. 2002;346:557-563. 3. Hypothermia After Cardiac Arrest Study Group. Mild therapeutic hypothermia to improve the neurologic outcome after cardiac arrest. N Engl J Med. 2002;346:549-556. 4. Fisher GC. Hypothermia after cardiac arrest: feasible but is it therapeutic? Anaesthesia. 2008;63:885-886. 5. Moran JL, Solomon PJ. Therapeutic hypothermia after cardiac arrest—once again. Crit Care Resusc. 2006;8:151-154.
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6. Pechlaner C, Joannidis M. Therapeutic hypothermia after cardiopulmonary resuscitation—pro and con. Wien Med Wochenschr. 2008;158:627-633. 7. Nielsen N, Friberg H, Gluud C, et al. 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. 8. Hachimi-Idrissi S, Corne L, Ebinger G, et al. Mild hypothermia induced by a helmet device: a clinical feasibility study. Resuscitation. 2001;51:275-281. 9. Hachimi-Idrissi S, Zizi M, Nguyen DN, et al. The evolution of serum astroglial S-100 b protein in patients with cardiac arrest treated with mild hypothermia. Resuscitation. 2005;64:187-192. 10. Laurent I, Adrie C, Vinsonneau C, et al. High-volume hemofiltration after out-of-hospital cardiac arrest: a randomized study. J Am Coll Cardiol. 2005;46:432-437. 11. Kim Y-M, Yim H-W, Jeong S-H, et al. Does therapeutic hypothermia benefit adult cardiac arrest patients presenting with non-shockable initial rhythms? a systematic review and meta-analysis of randomized and non-randomized studies. Resuscitation. 2012;83: 188-196. 12. Bro-Jeppesen J, Hassager C, Wanscher M, et al. Post-hypothermia fever is associated with increased mortality after out-of-hospital cardiac arrest. Resuscitation. 2013;84:1734-1740. 13. Leary M, Grossestreuer AV, Iannacone S, et al. Pyrexia and neurologic outcomes after therapeutic hypothermia for cardiac arrest. Resuscitation. 2013;84:1056-1061. 14. Freedman B. Equipoise and the ethics of clinical research. N Engl J Med. 1987;317:141-145. 15. Guyatt G, Oxman AD, Akl EA, et al. GRADE guidelines: 1. Introduction—GRADE evidence profiles and summary of findings tables. J Clin Epidemiol. 2011;64:383-394. 16. Perman SM, Goyal M, Neumar RW, et al. Clinical applications of targeted temperature management. Chest. 2014;145:386-393. 17. Eucker SA, Barrett TW, Schriger DL. Are 2 drugs better than 1 for acute agitation? a discussion on black box warnings, waiver of informed consent, and the ethics of enrolling impaired subjects in clinical trials: answers to the January 2013 Journal Club Questions. Ann Emerg Med. 2013;61:708-716. 18. Dickert NW, Govindarajan P, Harney D, et al. Community consultation for prehospital research: experiences of study coordinators and principal investigators. Prehosp Emerg Care. 2014;18:274-281. 19. Kamps MJA, Horn J, Oddo M, et al. Prognostication of neurologic outcome in cardiac arrest patients after mild therapeutic hypothermia: a meta-analysis of the current literature. Intensive Care Med. 2013;39:1671-1682. 20. Fugate JE, Wijdicks EFM, Mandrekar J, et al. Predictors of neurologic outcome in hypothermia after cardiac arrest. Ann Neurol. 2010;68:907-914. 21. Taccone FS, Cronberg T, Friberg H, et al. How to assess prognosis after cardiac arrest and therapeutic hypothermia. Crit Care. 2014; 18:202. 22. Schulz KF, Grimes DA. Blinding in randomised trials: hiding who got what. Lancet. 2002;359:696-700. 23. Karanicolas PJ, Farrokhyar F, Bhandari M. Blinding: who, what, when, why, how? Can J Surg. 2010;53:345-348. 24. Sakpal TV. Sample size estimation in clinical trial. Perspect Clin Res. 2010;1:67-69. 25. Julious SA, Campbell MJ. Tutorial in biostatistics: sample sizes for parallel group clinical trials with binary data. Stat Med. 2012;31:2904-2936. 26. Blackwelder WC. “Proving the null hypothesis” in clinical trials. Control Clin Trials. 1982;3:345-353.
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Journal Club 27. Head SJ, Kaul S, Bogers AJJC, Kappetein AP. Non-inferiority study design: lessons to be learned from cardiovascular trials. Eur Heart J. 2012;33(11):1318-1324. 28. Brown AM, Schriger DL, Barrett TW. Annals of Emergency Medicine Journal Club. Outcome measures, interim analyses, and bayesian approaches to randomized trials: answers to the September 2009 Journal Club questions. Ann Emerg Med. 2010;55:216-224.e1. 29. Rosomoff HL, Holaday DA. Cerebral blood flow and cerebral oxygen consumption during hypothermia. Am J Physiol. 1954;179:85-88. 30. Jennett B, Bond M. Assessment of outcome after severe brain damage. Lancet. 1975;1:480-484. 31. Becker LB, Aufderheide TP, Geocadin RG, et al. Primary outcomes for resuscitation science studies: a consensus statement from the American Heart Association. Circulation. 2011;124:2158-2177. 32. Phelps R, Dumas F, Maynard C, et al. Cerebral Performance Category and long-term prognosis following out-of-hospital cardiac arrest. Crit Care Med. 2013;41:1252-1257. 33. Stiell IG, Nesbitt LP, Nichol G, et al. Comparison of the Cerebral Performance Category score and the Health Utilities Index for survivors of cardiac arrest. Ann Emerg Med. 2009;53:241-248. 34. Ajam K, Gold LS, Beck SS, et al. Reliability of the Cerebral Performance Category to classify neurological status among survivors of ventricular fibrillation arrest: a cohort study. Scand J Trauma Resusc Emerg Med. 2011;19:38.
35. Rankin J. Cerebral vascular accidents in patients over the age of 60. II. Prognosis. Scott Med J. 1957;2:200-215. 36. Van Swieten JC, Koudstaal PJ, Visser MC, et al. Interobserver agreement for the assessment of handicap in stroke patients. Stroke. 1988;19:604-607. 37. Bonita R, Beaglehole R. Recovery of motor function after stroke. Stroke. 1988;19:1497-1500. 38. Banks JL, Marotta CA. Outcomes validity and reliability of the modified Rankin scale: implications for stroke clinical trials: a literature review and synthesis. Stroke. 2007;38:1091-1096. 39. Guyatt G, Meade MO, Rennie D, et al. User’s Guide to the Medical Literature: A Manual for Evidence-Based Clinical Practice. 2nd ed. New York: McGraw-Hill Professional; 2008. 40. Spruance SL, Reid JE, Grace M, et al. Hazard ratio in clinical trials. Antimicrob Agents Chemother. 2004;48:2787-2792. 41. Morris AH. Treatment algorithms and protocolized care. Curr Opin Crit Care. 2003;9:236-240. 42. Wendon J. Critical care “normality”: individualized versus protocolized care. Crit Care Med. 2010;38(10 suppl):S590-S599. 43. The ProCESS Investigators. A randomized trial of protocol-based care for early septic shock. N Engl J Med. 2014;370:1683-1693. 44. Zeiner A, Holzer M, Sterz F, et al. Hyperthermia after cardiac arrest is associated with an unfavorable neurologic outcome. Arch Intern Med. 2001;161:2007-2012.
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206 Annals of Emergency Medicine
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