November 2012 Critical Care Journal Club

Mehta S, Burry L, Cook D, Fergusson D, et al. Daily sedation interruption in mechanically ventilated critically ill patients cared for with a sedation protocol.  JAMA 2012;308:1985-92. Abstract

This study was a multi-center, randomized controlled trial that compared protocolized sedation with protocolized sedation plus daily sedation interruption.  The protocol used to titrate benzodiazepine and opioid infusions incorporated a validated scale (Sedation-agitation Scale (SAS) or Richmond Agitation Sedation Scale (RASS) in order to maintain a comfortable but arousable state.  Four hundred and thirty mechanically ventilated, critically ill patients were recruited from medical and surgical ICUs in 16 institutions in North America.  The study showed no benefit in the group that underwent daily sedation interruption - length of intubation was 7 days, length of ICU stay was 10 days and length of hospital stay was 20 days in both groups.  There was no significant difference in the incidence of delirium (53 vs. 54%) or in unintentional extubation (5 vs. 6%).  However, nurses felt sedation interruption significantly increased their workload (visual analogue scale 4.22 vs. 3.80 p=0.001). Sedation interruption was also associated with higher mean daily doses of sedation drugs, and more daily boluses of benzodiazepines and opioids – for instance, the cumulative dose of midazolam in the interruption group was increased by 20 mg per day.

This study has strong internal validity.  It was a large multicenter RCT.  The outcomes were clinically important.  The main outcome comparisons between the two groups were so strikingly negative that they scarcely needed calculation of p-values.  There was no way to practically blind daily sedation interruptions, and the nursing estimate of workload could clearly have been biased by this, but the findings in this regard are consistent with common sense.  I think our nurses would agree that sedation interruption in critically-ill patients can be time-consuming and often require more medication boluses to re-establish sedation than they would have required had the infusion simply been continued.   Our delirium quality improvement working group is currently discussing this paper in our efforts to improve our ICU standard for sedation management.    

Yunos NM, Bellomo R, Hegarty C, Story D, Ho L, Bailey M.  Association between a chloride-liberal vs chloride-restrictive intravenous fluid administration strategy and kidney injury in critically ill adults.  JAMA  2012;308;1566-72. PDF

 This study was a historically-controlled cohort study, based on the hypothesis that administration of supraphysiological quantities of chloride in IV solutions such as normal saline may be detrimental to kidney function.  The authors compared a period of time in which chloride-liberal IV fluids were readily available in their ICU vs. an intervention period, a year later, in which a bundle of chloride-restricted intravenous fluids (lactated ringer’s solution (LR), Plasmalyte, and salt-poor 20% albumin) were available.  A total of 1533 critically-ill patients were included.  The authors found that chloride administration decreased dramatically in the intervention period and that patients treated with the chloride-restricted bundle had a smaller increase in creatinine (22.6 umol/L vs. 14.8 umol/L; p=0.03); a decrease in the incidence of acute kidney injury/failure (14% vs. 8%; p<0.001); and a decrease in the use of renal replacement therapy (10% vs. 6.4%; p=0.005).

This study had an interesting hypothesis, but was very poorly designed.   It provides a good example of what Sir Austin Bradford Hill meant when he bemoaned our over-reliance on P-values in studies that have extremely weak experimental designs.  The methodological shortcomings of the study include: 1) This was an observational study – a cohort study with historical controls.  One of the main threats to validity in this type of study is bias – many things besides the IV fluid bundle are likely to have changed in this ICU, and the patients they admitted, over the course of a year.  The authors make no attempt to report on these changes.  2) The intervention was bundled.  All such studies (including Dr. River’s study on goal-directed therapy for sepsis) are fundamentally flawed because they cannot determine the specific intervention that is associated with the outcome.  The bundle might include harmful interventions that cannot be teased-out.  In this specific case, it would have been much better to simply concentrate on replacing saline with LR. 3) The study was unblinded.  Although the authors claim it would have been difficult to blind, this just isn’t true – bags of isotonic IV solution could have been provided without the clinicians knowing whether they contained saline or LR.  Lack of blinding could have biased the decision whether or not to start dialysis in some patients. 4) The main outcome measures were either: laboratory surrogates (increase in creatinine), based on laboratory surrogates (incidence of acute kidney injury), or prone to bias (decision to start dialysis).  The difference in the increase in creatinine is statistically significant, but clinically meaningless.  The protective effect of the chloride-restrictive strategy was to mitigate the increase in creatinine by only 8 umol/L or 0.1 mg/dL.  In some patients this small change would have caused them to be reclassified into a worse RIFLE category of renal function, but it certainly doesn’t seem likely to qualitatively impact their well-being.  5)  The use of time-to-event analysis, Kaplan Meier curves, and Cox proportional hazards modeling is inappropriate for the outcome of acute renal injury.  These statistical techniques are highly powerful for showing the statistical significance of whether an intervention can delay an outcome, but do not necessarily show whether it can prevent the outcome.   Our clinical goal should be to prevent, not just delay by a few days, the onset of acute kidney injury.  The inappropriate use of these statistical techniques provides false statistical power in this situation.  This study therefore provides no useful information for clinicians besides the interesting hypothesis the authors began with.

Serpa Neto A, Cardoso SO, Manetta JA, et al.  Association between use of lung-protective ventilation with lower tidal volumes and clinical outcomes among patients without acute respiratory distress syndrome.  JAMA 2012;308:1651-9. PDF

The authors performed a meta-analysis based on twenty articles indentified in their literature search, in which patients without ARDS were treated by two ventilator strategies – one with lower and one with higher tidal volumes.  Primary outcome analysis showed that lower tidal volumes were associated with a decrease in lung injury development [RR 0.33 95%CI 0.23-0.47] and lower mortality [RR 0.64 95%CI 0.46-0.89].

In my opinion, the study was critically flawed by the study selection.  Randomized and non-randomized observational studies were included.  Five observational studies accounted for approximately 85% of the patients in the primary analysis of lung injury.  Many of the randomized studies had significant methodological flaws, such as failure to observe the principle of intention-to-treat.  Fourteen of the studies were carried out in the operating room – these were combined with six studies from MICUs and SICUs.  The median duration of intervention mechanical ventilation in the included studies was less than seven hours.  Seven of the studies did not use 6mL/Kg ideal body weight as their “low-tidal volume” intervention.  Five of the included studies didn’t report the duration of patient outcome follow-up, and four reported follow-up of less than eight hours!   The validity of meta-analyses is largely based on the selection of comparable studies with high individual internal validity – this meta-analysis fails both criteria.  

The pathophysiological principle that provides the rationale for low-tidal ventilation is the observation that the number of functional alveoli is significantly reduced in ARDS.  Therefore, even relatively “typical” tidal volumes delivered by a mechanical ventilator will overinflate the healthiest parts of the ARDS-beset lung.  It is more difficult to understand the biological plausibility of how a few hours of typical tidal volumes delivered to predominantly normal lungs in the operating room could cause increased lung injury and mortality.   It is especially difficult to look at outcomes such as mortality among studies with as little as 3 hours of follow-up.  It’s my opinion that this study doesn’t add to our understanding of how best to mechanically ventilate patients without ARDS in the O.R. or in our ICUs.  However the question of how to calculate the optimal tidal volume for patients without ARDS that require mechanical ventilation is very important.  It will require prospective randomized controlled trials in the ICU and (separately) in the operating room to answer. 

Pereira TV, Horwitz RI, loannidis JP.  Empirical evaluation of very large treatment effects of medical interventions.  JAMA  2012;308:1676-84. PDF

The authors reviewed the Cochrane Database of Systematic Reviews, and identified 85,000 meta-analysis forest plots in which a medical intervention was evaluated in relation to an outcome – any outcome from mortality to surrogate laboratory outcomes.  [Recall that a forest plot is a graphical display that illustrates the relative effect size and estimate precision, of a particular outcome in a group of studies included in a meta-analysis].  The authors found 13,397 forest plots in which at least a single study demonstrated a “very large” treatment effect (an odds ratio greater than 5.0 or less than 0.2).  Sixty percent of the time, very large treatment effects were observed in the first study of a particular intervention.  Studies with very large treatment effects were generally small trials, -the results were based on a median of less than twenty patient events.  Studies with very large treatment effects were also much less likely to address mortality, and more likely to address surrogate laboratory outcomes than other trials.  Over ninety percent of the time, very large treatment effects became significantly more modest as subsequent studies were added into meta-analyses.  The authors were only able to find a single study, among 228,000 clinical trials, in which an intervention had a large beneficial effect on mortality, with strong methodological and statistical aspects [a study on ECMO for newborns with severe respiratory failure].

My thanks to the authors on their exhaustive and well-designed study.  Most medical research studies that demonstrate very large treatment effects are spurious – the vast majority represents substantial overestimations of potential patient benefit.  It’s not surprising that purported large treatment benefits are more likely to be related to surrogate laboratory outcomes.  Studies based on surrogate outcomes are generally not helpful in making treatment decisions to begin with.  I guess it comes down to something my Dad once taught me – “If it sounds too good to be true, it probably is”.

Robert A. Raschke, MD

Associate Editor, Critical Care Medicine

Reference as: Raschke RA. November 2012 critical care journal club. Southwest J Pulm Crit Care 2012;5:292-5. PDF

October 2012 Critical Care Journal Club

Dr. Raschke was out of town when Critical Care Journal Club was held this month. Dr. Tom Bajo, the senior critical care physician at Good Samaritan, moderated the journal club. We reviewed 5 articles and 1 editorial.

Thiele H, Zeymer U, Neumann FJ. Intraaortic balloon support for myocardial infarction with cardiogenic shock. N Engl J Med 2012 ;367:1287-96. Abstract

This is an important article for those who manage myocardial infarction with cardiogenic shock. The ACA/AHA guidelines recommend intraaortic balloon counterpulsation as a class I treatment for cardiogenic shock complicating acute myocardial infarction. However, the evidence is based mainly on registry data, and there is a paucity of randomized clinical trials. In this randomized, prospective, open-label, multicenter trial, 600 patients with cardiogenic shock complicating acute myocardial infarction were randomized to intraaortic balloon counterpulsation or no intraaortic balloon counterpulsation. All patients were expected to undergo early revascularization (by means of percutaneous coronary intervention or bypass surgery) and to receive the best available medical therapy. At 30 days, there were no significant differences in mortality or secondary end points or in process-of-care measures, including the time to hemodynamic stabilization, the length of stay in the intensive care unit, serum lactate levels, the dose and duration of catecholamine therapy, and renal function. This suggests that the urgency to use intraaortic balloon counterpulsation in patients with cardiogenic shock complicating acute myocardial infarction is low since it apparently does not alter any meaningful outcome.

O'Connor CM, Rogers JG. Evidence for overturning the guidelines in cardiogenic shock. N Engl J Med 2012;367:1349-50. Abstract

This is an accompanying editorial of the Thiele study above. It reviews and accepts the findings. The editorial suggests that the ACA/AHA and other guidelines recommending intraaortic balloon counterpulsation need to be revised.

Garcia T, Rios M, Paiva JA. Predictors of severity in deep neck infections admitted to the intensive care unit. Anaesth Intensive Care 2012;40:832-7. Abstract

This retrospective study from Portugal reported on the results of 54 adult patients admitted for surgical drainage of deep neck infections and admitted to the intensive care unit (ICU) during a period of 52 months. A complicated course was defined as ICU stay >8 days, reintubation, tracheostomy, renal replacement therapy, critical illness, myopathy or mortality. Variables associated with the 30 patients (56%) who had a complicated course were a parapharyngeal or retropharyngeal location (as opposed to a peritonsillar location) and an elevated APACHE II, SAPS II or SOFA score. The article emphasizes that the risk of complications from neck infection remain high and that those with the above characteristics bear careful observation.

Luyt CE, Combes A, Becquemin MH, et al. Long-term Outcomes of Pandemic 2009 Influenza A(H1N1)-Associated Severe ARDS. Chest 2012:583-592. Abstract

No data on long-term outcomes of survivors of 2009 influenza A(H1N1) (A[H1N1])-associated ARDS are available. This study compared the 1-year outcomes of survivors of A(H1N1)-associated ARDS, according to use or no use of extracorporeal lung assist (ECLA), using its need as an ARDS severity surrogate. ECLA and no-ECLA group patients had comparable outcomes with minor lung disabilities with diminished diffusion capacities. However, most had psychologic impairment and poorer health-related quality of life than a sex- and age-matched general population group. This demonstrates that extracorporeal lung assistance appears to do no long-term harm in this group of patients above that induced by the underlying influenza. Although the majority of patients of patients recover physiologically, psycholigic impairment continues to be a major complication of a severe ICU illness.

Ross EA, Reisfield GM, Watson MC, Chronister CW, Goldberger BA. Psychoactive "bath salts" intoxication with methylenedioxypyrovalerone. Am J Med 2012;125:854-8. Abstract

The Good Samaritan ICU group has seen a number of patients admitted for abuse of “bath salts”. This is a good review for those who might care for these patients. Bath salts contain the “designer” drug methylenedioxypyrovalerone (MDPV) which has recently classified as a controlled substance in the United States but is still illegally available via the Internet. MDPV is a synthetic central nervous system stimulant and is taken to produce a cocaine- or methamphetamine-like high. Clinicians need to be especially vigilant in that MDPV is not detected by routine drug screens and overdoses can be life-threatening. Administered via oral ingestion, nasal insufflation, smoking, intravenous or intramuscular methods, or the rectum, the intoxication lasts 6 to 8 hours and has high addictive potential. Symptoms are similar to the sympathetic stimulation seen with cocaine or methamphetamine overdose and include tachycardia, hypertension, arrhythmias, hyperthermia, sweating, rhabdomyolysis, and seizures to those as severe as stroke, cerebral edema, cardiorespiratory collapse, myocardial infarction, and death. Behavioral effects include panic attacks, anxiety, agitation, severe paranoia, hallucinations, psychosis, suicidal ideation, self-mutilation, and behavior that is aggressive, violent, and self-destructive. Treatment is principally supportive and focuses on counteracting the sympathetic overstimulation, including sedation with intravenous benzodiazepines, seizure-prevention measures, intravenous fluids, close (eg, intensive care unit) monitoring, and restraints to prevent harm to self or others. Clinical presentation is often complicated by coingestion of other psychoactive substances that may alter the treatment approach.

Goodwin AJ. Critical care clinical trials: getting off the roller coaster. Chest. 2012;142:563-7.  Abstract    

Incorporation of evidence-based medicine into everyday practice is one method to optimize care; however, intensivists have struggled to define optimal practices because clinical trials in the ICU have yielded conflicting results. The net effect is that hospitals, physicians, and staff have expended tremendous time and resources implementing new protocols that incorporate emerging evidence from the medical literature, only to remove such protocols a few years later when validation trials fail to confirm the initial results. Recent examples in which this “roller coaster” has occurred include the use of corticosteroids in septic shock, tight glucose control, and, most recently, activated protein C in severe sepsis. Dr. Goodwin explains this recurring phenomenon on publication bias and the law of diminishing returns. It is well established that a publication bias exists such that trials showing a significant positive effect tend to be published more than trials which show no effect. The law of diminishing returns states that as multiple new interventions are used simultaneously, the benefit of each individual intervention decreases and, therefore, is harder to detect. The question then remains: What can we do to avoid the frustrating cycle of changing ICU practice based on one study only to change back a few years later when a trial with conflicting results is published? Dr. Goodwin suggests the critical care community, as a group, use a critical eye when evaluating new studies. Before implementation, validate single-center or other provocative studies need to be validated using nonindustry financial support and multicenter comparative effectiveness studies. Our group of fellows and attendings overwhelmingly agreed. However, it was pointed out that with the ever increasing numbers of guidelines (>15,000 listed in the National Guideline Clearinghouse), the loss of physician autonomy, the direction of healthcare by the under-qualified and nonresponsible, and with the bundling of guidelines there appears to be little that an individual critical care physician can do. In the end, it is important to remember that just because an intervention was published, it is not necessarily standard of care. Only we, as critical care physicians, should establish that standard of care.

Richard A. Robbins, MD

Thomas M. Bajo, MD

Reference as: Robbins RA, Bajo TM. October 2012 critical care journal club. Southwest J Pulm Crit Care 2012;5:220-2. PDF

September 2012 Critical Care Journal Club

We had a great group of attending discussants at this J club – thanks to all who participated including Drs. Jay Blum, Al Thomas, Clement Singarajah, Rick Robbins, Tom Bajo, Huw Owen Reece, and Roxanne Garcia Orr.   

Winters B, Custer J, Galvagno SM Jr, et al.  Diagnostic errors in the intensive care unit: a systematic review of autopsy studies.  BMJ Qual Saf 2012 Jul 24. [Epub ahead of print] Abstract

The authors reviewed 45 years of autopsy studies of ICU patients to determine the most common missed diagnoses.  Thirty-one studies including 5863 autopsies were included. Eight percent revealed a missed diagnosis with an adverse impact survival that would likely have changed therapy.  More than 80% of these were vascular events (such as pulmonary embolism or acute myocardial infarction) and infections.  Strangely, the authors detail all diagnostic categories except infection – this seems to have been an oversight error on their part. 

The authors extrapolated their data to conclude that 34,000 patients per year might die in the ICU from missed diagnoses.  But this calculation is based on the false assumption that there is nothing special about patients who ultimately undergo autopsy.  Many physicians specifically request autopsy because they want to find out if they missed anything.  Extrapolation of data with this selection bias would likely greatly overestimate deaths due to missed diagnoses.

There was some controversy between us in regards to the intent of this research.  Some felt that it was a condemnation of clinicians by pathologists, looking through the retrospect-o-scope to find our shortcomings.  Others pointed out that we often make mistakes as clinicians - even the best of us miss things.  It’s best to accept this and try to learn from it.  Experienced clinicians in the discussion all agreed that throughout their careers, few autopsies revealed important findings – and almost never determined a cause of death that wasn’t clinically suspected.  But most could remember a case or two that surprised them.  This paper should not be used as an indictment of bedside care by policy-makers, but as a reminder to physicians to maintain an open-minded and inquisitive diagnostic approach.

Choi SH, Hong SB, Ko GB, et al.  Viral infection in patients with severe pneumonia requiring intensive care unit admission. Am J Respir Crit Care Med 2012;186:325-32. Abstract

This article was thoroughly flawed, but it prompted a very interesting discussion.  This cohort study analyzed microbiological studies performed on critically ill patients with pneumonia (CAP and HCAP combined) and concluded that 36% of patients had a bacterial pneumonia and 36% had a viral pneumonia – most commonly rhinovirus.  Only 58% of the patients in the cohort underwent bronchoalveolar lavage.   The authors assumed any potentially pathogenic organism isolated was the cause of pneumonia.  However, many of the microbiological tests performed did not establish causality.  No one would argue that influenza virus in the bronchoalveolar lavage of a patient with pneumonia is clearly pathogenic, the same cannot be said for finding rhinovirus in a nasal swab.  Previous studies that used autopsies and microbiological examination of lung tissue obtained at autopsy have shown that bacteria isolated from BAL are often not causative of pneumonia.     

Dr. Thomas pointed out that widespread use of the term “Community-acquired pneumonia” might have the deleterious effect of mindlessly lumping together clinically distinct pneumonia syndromes instead of using bedside clinical skills to make a sound diagnosis.  We call everything “CAP”, give the recommended empirical antibiotics, and then depend on the lab to sort it out for us.  This point was emphasized when a resident asked when anti-influenza treatment should be given empirically for CAP – the answer is: when the clinical syndrome is consistent with influenza -for instance, in a patient with fever, dry cough, myalgias, arthalgias and headache.   This presentation is distinct from classic pneumococcal pneumonia, Pneumocystis jiroveci pneumonia, and coccidioidomycosis – although all 3 could be diagnosed as CAP upon presentation. 

We all agreed that the study was interesting in the aspect of pointing out how little we know about pneumonia.  It’s certainly possible that many patients admitted for CAP and urgently treated with antibiotics do not have bacterial pneumonia.  But a consistent microbiological approach and rigorous interpretation of the results will be required to sort this out in a valid analysis.

Pulido JN, Afessa B, Masaki M, et al.  Clinical spectrum, frequency and significance of myocardial dysfunction in severe sepsis and septic shock.  Mayo Clinic Proc 2012;87:620-8.  Abstract

We reviewed this article briefly.  This is a cohort study that reviewed echocardiographic findings of 100 patients with septic shock.  The thing that caught my attention when I screened this article was that the authors found that the 64% of patients with sepsis had myocardial dysfunction, and that many presented with isolated right ventricular dysfunction (31%) or with left ventricular diastolic dysfunction (37%). I had always thought that acute cardiomyopathy of sepsis was primarily a disease of left ventricular systolic dysfunction, but in this study, this was the least frequent finding - only 27%. 

Unfortunately, the patients in the cohort did not all have echocardiograms prior to their presentation, so it was unclear how many of them might simply have chronic left ventricular diastolic dysfunction unrelated to sepsis.  This confusion wasn’t helped but the lack of completeness in report of the follow-up echocardiograms.  The authors state that left ventricular systolic function often repaired, but don’t mention the outcomes in patients with diastolic dysfunction – if diastolic dysfunction had been shown to acutely resolve, that would have supported the idea that it might have been caused by sepsis.

It would have also been interesting to report the pulmonary status of the patients with acute right heart dysfunction – you couldn’t help wondering whether these patients had severe ARDS causing right ventricular dysfunction.  Altogether, the study was thought-provoking, but was not properly designed to make convincing conclusions.  

Ely EW, Skrobik Y.  Point/counterpoint editorials:  Should benzodiazepines be avoided in mechanically-ventilated patients?  (both sides of the debate).  Chest 2012;142:281-7. No abstract available.

It was great to have Dr. Huw Owen Reece with us to discuss this article – Dr. Owen Reece has ongoing interest in this area of study, and has worked on reducing delirium in our ICU.  There was no clear winner in this debate.  Both authors agree that adequate sedation is beneficial, and that excessive sedation is harmful. It’s possible that any of the drugs we currently use could cause or worsen delirium if given inappropriately.  Our faculty generally agreed with Dr. Ely that the pharmacokinetic and pharmacodynamics properties of some of the newer sedative hyponotics (such as propofol and dexmethetomidine) are favorable, and seem less likely to cause excessive sedation.  Future studies will be needed to see whether this clearly translates into a lower incidence of ICU delirium and reduced ICU length of stay.

Bellomo R, Kellum JA, Ronco C. Acute kidney injury.  Lancet  2012;380:756-66.  Abstract

This article is highly recommended reading for residents and fellows, but it reads like a chapter in a Critical Care textbook, and we will not attempt to summarize it here – it just has too much meat in it.  We have previously reviewed articles by Bellomo and we appreciate his skeptical approach to clinical dogma.

Bellomo points out that our traditional clinical diagnosis of “acute tubular necrosis” (ATN) - resulting from a reduction in renal blood flow due to the hemodynamic changes of sepsis - is likely an incorrect diagnosis in most patients.   The diagnosis of ATN is based on pathological findings that are almost never confirmed in septic patients with renal failure.  If ATN were due to a temporary reduction in renal perfusion, it should resolve as rapidly as any other case of prerenal failure.  Studies have increasingly shown that the pathogenesis of acute kidney injury is far more complex than we used to think, and terms like ATN should likely be discarded.

Bellomo also argues for earlier use of renal replacement therapy to manage fluid overload in septic patients with oliguria or anuria, pointing out that even moderate fluid overload can contribute to morbidity and mortality.  He postulates that a congested state may be directly related to the causation of acute kidney injury.   We know from reviewing some of Bellomo’s other recent papers in Journal Club that he challenges the dogma of aggressive fluid resuscitation in septic shock – this article furthers that argument.

We digressed a little - discussing our typical approach of aggressive fluid resuscitation of septic shock.  Our clinical impression is that goal-directed resuscitation tends to result in fluid overload in many patients.  We often find ourselves implementing massive diuresis of patients once their blood pressure recovers (often after vasopressors are discontinued).  Many articles we have reviewed over the past year add to our growing impression that this approach is of unclear benefit, and possible harm. 

Robert Raschke MD MS

Associate Editor, Critical Care Medicine

Reference as: Raschke RA. September 2012 critical care journal club. Southwest J Pulm Crit Care 2012;5:193-6. PDf

August 2012 Critical Care Journal Club

Dr. Raschke took a well-deserved vacation, and in his absence we did another quick-fire critical care journal club reviewing 7 articles.

Davies AR, Morrison SS, Bailey MJ, Bellomo R, Cooper DJ, Doig GS, Finfer SR, Heyland DK; for the ENTERIC Study Investigators and the ANZICS Clinical Trials Group. A multicenter, randomized controlled trial comparing early nasojejunal with nasogastric nutrition in critical illness. Crit Care Med 2012;40:2342-8. (Click here for abstract)

This was a randomized control trial, which enrolled 181 patients from multiple medical-surgical ICUs to receive either nasojejunal or nasogastric nutrition.  The number of patients selected for this study provided an 80% power to detect a 12% difference in mean energy delivery.  Inclusion criteria for the study were patient that were admitted to the ICU, needing mechanically ventilated, narcotic drips for sedation as well as elevated gastric residuals (>150ml).  Patients were excluded if patient had abnormal anatomy or imminent death.  

Of the 1453 patients who met inclusion criteria only 181 patients were enrolled in the study.  Patients were randomized to both groups via computer-generated randomization schedule.  Of the 91 patients randomized to receive nasojejunal feeding, only 76 patients had successful placement of nasojejunal tube placement at 48 hours.  The study showed that the estimated energy requirements were 72% for early nasojejunal feeding and 71% for the nasogastric feeding.   A blinded panel diagnosed ventilator-associated pneumonia in 18 patients with nasojejunal group versus 19 patients in the nasogastric group.  Both these finding were not statistically significant.  Despite similar risk for major bleeding of 2% there was a slight increase risk of minor bleeds in patients treated with early nasojejunal feeding. 

Overall this was a good study with good internal validity.  Limitations identified by this study were the conservative definition of elevated gastric residual and the delay of enrolling patients into the study.  These limitations may have indentified only mildly symptomatic patients or patients who were beyond the time of maximal gastric feeding intolerance.

Although based on sound theory of providing jejunal feedings to avoid risk of pneumonia as well as improving absorptive ability, this large RCT study shows conflicting results compared to previous studies. Early nasojejunal nutrition did not increase energy delivery or reduce the incidence of pneumonia in critically ill patients. 

Heemesh Seth, DO

Kalil AC, Larosa SP. Effectiveness and safety of drotrecogin alfa (activated) for severe sepsis: a meta-analysis and metaregression. Lancet Infect Dis 2012. Epub ahead of print. Available at: http://www.ncbi.nlm.nih.gov/pubmed/22809883 (accessed 8/22/12). (Click here for abstract)

Last month the Critical Care Journal Club focused on drotrecogin alfa (Xigris®) and the problems associated with interpreting the data, especially the original PROWESS study, which contributed to Eli Lilly withdrawing the drug (1). Just when drotrecogin appeared to be a dead issue this study was published which performed a meta-analysis of 47,223 patients with sepsis from 9 controlled trials and 16 single group studies. The results showed a significant mortality reduction similar to the original PROWESS trial. However, mortality in patients who were treated with drotrecogin alfa in the 16 single group studies (41.3%) was much higher than that was reported in the PROWESS trial (29.7%). The study concluded that there is a relative risk reduction of 18% in hospital mortality with drotrecogin alfa. This is in conjunction with the original PROWESS trial.

Although this study shows similar results to the original PROWESS trail, I am skeptical that this would change our clinical practice based on the deep distrust that was developed over the course of last decade against the true clinical benefit and the manufacturer of the drug. Inclusion of data that is tainted in a meta-analysis leads to conclusions that are also tainted.

Suresh Uppalapu, MD

Perner A, Haase N, Guttormsen AB, et al. Hydroxyethyl starch 130/0.42 versus ringer’s acetate in severe sepsis. N Engl J Med 2012; 367:124-34. (Click here for abstract)

I liked this article.  Few interventions have proven to improve mortality and outcomes in the ICU over the past several decades, so investigating our current unproven practices for evidence basis seems only logical.  This ensures our current practices are actually beneficial, and helps eliminate those that only seem like good options just because they are available.

The authors correctly point out the conflicting data regarding the use of hydroxyethyl starch (HES) in sepsis volume resuscitation, as evident in the Cochrane review 2011 “Colloids versus Crystalloids for fluid resuscitation in critically ill patients” (2). In that review, they found 17 randomized controlled trials with mortality data comparing HES with crystalloids (n = 1172) with a pooled RR = 1.18 (95% CI 0.96 to 1.44).  Although not significant, it implies a mortality risk with the use of HES, leading the authors to recommend against the use of HES (or any other colloid) for resuscitation of critically ill patients with trauma, burns or following surgery. 

With the concerns over accelerated renal failure with the use of HES in previous trials, a definitive study about the use of HES in sepsis resuscitation was needed.  This trial fills that gap. 804 patients with severe sepsis were randomly assigned to fluid resuscitation with either 6% HES 130/0.42 (Tetraspan) or Ringer’s acetate. Patients with severe sepsis assigned to fluid resuscitation with HES 130/0.42 had an increased risk of death at day 90 and were more likely to require renal-replacement therapy.

I also liked that they used the lower molecular weight HES, which has been referred to as “3^rd-Generation Starch” implying a better safety profile than previous starches; asked centers to follow “international guidelines” for resuscitation reflecting real-world practices; and allowed patients with acute kidney injury, which better represents actual practices in ICU settings today.  The trial was large, multi-centered, randomized and well matched, and blinded.  Overall good study design and implementation.

This trial has, for me, clinched the idea that using HES colloid for volume resuscitation is a poor choice compared to alternative crystalloids.  The finding that HES increased mortality and worsened renal failure is consistent with previous trials and independent review trends, lending more credibility to the outcomes.  We should continue evaluating current practices for evidence-basis to ensure our intended outcomes are the actual outcomes.

Elijah M. Poulos, MD

Lee TH. Care redesign-a path forward for providers. N Engl J Med 2012; 367:466-72. (Click here for first 100 words of article)

We were confused about this editorial. Dr. Lee describes a system for improving healthcare where a team decides what patient centered outcome needs improvement, develops an improvement strategy centered on evidence based medicine, and measures the outcome. Although there are several good points within the editorial, details are missing and what is implied is a much rosier version of healthcare decision making than really exists.

Although Dr. Lee correctly points out that “health care is intended to help people, not just provide a commodity as inexpensively as possible”, details such as who will decide which outcomes need improvement; what strategy should be adopted; and what measure(s) will be used to determine success are either not present or only vaguely described.  Increasingly, we have medical decisions from a “team” consisting predominately of nonclinicians. Although Dr. Lee also correctly points out that “simply adapting another institution’s checklist would probably have limited value”, a number of organizations such as the JCAHO, IHI and the Centers for Medicare and Medicaid are mandating exactly that-a checklist whose success is measured by a meaningless surrogate. For example, administration of the 23-polyvalent pneumococcal vaccine is a “quality measure” whose success is measured by the percentage of patients who have the vaccine administered. Yet, pneumococcal vaccine appears ineffective in adults (3). Patient-centered measures such as the incidence of pneumonia and its resultant morbidity and mortality are not measured. Developing a strategy for improving the frequency of pneumococcal vaccination is straightforward and easy. Improving patient-centered outcomes is much harder. Strategizing from a group of nonclinicians concerned with political gain, or worse, paid bonuses based on the frequency of pneumococcal vaccine administration seems unlikely to adopt or improve patient-centered outcomes.

Unfortunately, Dr. Lee describes an ideal healthcare decision process that does not exist at most institutions. Furthermore, the process described will be corrupted to undermine physician autonomy, encourage the adoption of interventions that are cheaper but inferior or ineffective, and divert blame away from poor decisions made by nonclinicians. This is not a step forward but several steps backwards.

Tonya Whiting, DO

Richard A. Robbins, MD

Berg DD, Berg RA. When should rescue breathing be removed from the ABCs of CPR? Crit Care Clin 2012;28:155-65. (Click here for access to full text of article)

The authors review the evidence for using hands-only CPR for out-of-hospital cardiac arrest and conclude that for adults; hands-only CPR is the treatment of choice. Most adult out-of-hospital arrests are due to cardiac arrythmias and this approach makes sense since the patient has a “reservoir” of oxygen in the lung and chest compressions provide some ventilation. Ventilation is daunting for most laymen performing CPR and makes them reluctant to initiate the CPR process, especially if it involves mouth to mouth ventilation. The authors review the studies and a meta-analysis which support the use of hands-only CPR only. However, they point out that in children and inpatient adults that asphyxia is more frequent and that assisted ventilation is probably necessary because the oxygen “reservoir” is depleted.

The authors also discuss whether rescue ventilation is necessary for Emergency Medical Services (EMS) providers. The outcomes for out-of-hospital CPR from EMS in Tucson and Phoenix had been dismal. A clue to a potential reason was that the EMS protocols unintentionally lead to interruptions and delays in chest compressions (assessing airway, breathing and circulation, placing the automated external defibrillator pads, waiting for rhythm analysis, endotracheal intubation, and so forth). Replacing these protocols with 200 uninterrupted preshock chest compressions, passive oxygen insufflation and delayed endotracheal intubation resulted in a significant increase in survival from 1.8% to 5.4% (4).

I have often watched as inpatient CPR mimics the prior EMS protocols, i.e., overly focusing on obtaining an airway to the detriment of chest compressions. Since many of the EMS technicians are fairly good at performing endotracheal intubation and are probably better than many of the inpatient CPR responders, it makes one wonder if a similar protocol should be studied for inpatient CPR.

Richard A. Robbins, MD

Marik PE, Flemmer M, Harrison W. The risk of catheter-related bloodstream infection with femoral venous catheters as compared to subclavian and internal jugular venous catheters: a systematic review of the literature and meta-analysis. Crit Care Med 2012;40:2479-85. (Click here for abstract) 

This article reviews the incidence of catheter-related bloodstream infections with femoral catheters compared to other sites. Although earlier studies showed a lower risk of catheter-related bloodstream infections when the internal jugular was compared to the femoral site, recent studies show no difference in the rate of catheter-related bloodstream infections between femoral and subclavian or internal jugular sites. This is the same conclusion we came to earlier this year when we published our review of the Institute of Health Care (IHI) guidelines for prevention of central line associated blood stream infection (5). Use of nonfemoral sites is an integral part of the IHI Central Line Bundle according to their website which still touts nonfemoral insertion (6). It is time IHI revised their guidelines to reflect the evidence.

Richard A. Robbins, MD

Layios N, Lambermont B, Canivet JL, et al. Procalcitonin usefulness for the initiation of antibiotic treatment in intensive care unit patients. Crit Care Med 2012;40:2304-9. (Click here for abstract)

Procalcitonin has received much attention as a potential biomarker leading to improved diagnosis of bacterial infection and appropriate use of antibiotics. Studies investigating procalcitonin-guided management of sepsis in the ICU have shown reduction in duration of antibiotics, but mixed effects on ICU length of stay, and no effect on mortality.  We previously reviewed one of these articles in the June 2012 Critical Care Journal Club and promised to keep an eye on procalcitonin as more research comes along (7). These authors tested the usefulness of procalcitonin serum level for the reduction of antibiotic consumption in intensive care unit patients. Patients were randomized into two groups: one using the procalcitonin results (procalcitonin group, n=258) and one being blinded to the procalcitonin results (control group, n=251). Surprisingly, knowing the procalcitonin level at the initiation of antimicrobials did not reduce antibiotic consumption in the ICU. As previously promised we will continue to follow the procalcitonin story.

Richard A. Robbins, MD

References

1. Raschke RA. July 2012 critical care journal club. Southwest J Pulm Crit Care 2012;5:54-7.
2. Perel P, Roberts I.  Colloids versus crystalloids for fluid resuscitation in critically ill patients.  Cochrane Database Syst Rev 2011;3;CD000567.
3. Moberley SA, Holden J, Tatham DP, Andrews RM. Vaccines for preventing  pneumococcal infection in adults. Cochrane Database Syst Rev. 2008 Jan 23;(1):CD000422.
4. Bobrow BJ, Clark LL, Ewy GA, et al. Minimally interrupted cardiac resuscitation by emergency medical services for out-of-hospital cardiac arrest. JAMA 2008;299:1158–65.
5. Hurley J, Garciaorr R, Luedy H, et al. Correlation of compliance with central line associated blood stream infection guidelines and outcomes: a review of the evidence. Southwest J Pulm Crit Care 2012;4:163-73.
6. http://app.ihi.org/imap/tool/#Process=e876565d-fd43-42ce-8340-8643b7e675c7 accessed 8-23-12.
7. Raschke RA. June 2012 critical care journal club. Southwest J Pulm Crit Care 2012;5:20-3.

Reference as: Seth H, Uppalapu S, Poulos EM, Whiting T, Robbins RA. August 2012 critical care journal club. Southwest J Pulm Crit Care 2012;5:138-43. (Click here for a PDF version)

July 2012 Critical Care Journal Club

Over the past thirty years or so, we have seen multiple therapies related to sepsis management that appeared beneficial in initial clinical trials but were later found to be useless or even harmful. Examples include goal-directed resuscitation to achieve maximal oxygen delivery, steroids for ARDS, tight glycemic control, and adrenal replacement therapy, among others.  An overview of the history of evidence-based critical care medicine provides a strong argument for humility and caution. The story of Xigris provides another chapter for the fellows to consider as they move forward in their careers, and are asked to appraise new therapies that come along.

The story of activated protein C – also designated as drotrecogin alfa (recombinant) - or Xigris® began with stellar expectations. The PROWESS trial was published in the NEJM in 2001 (1). It was a randomized controlled trial that enrolled 1690 patients, comparing 28-day survival of patients treated with Xigris vs. placebo in the treatment of severe sepsis. The study was prematurely stopped at an interim analysis when it was observed that the mortality of the placebo group was significantly higher than that of the treatment group (30.8 vs. 24.7% - p=0.005). The risk of serious bleeding with Xigris (an antithrombotic agent) was found to be 3.5% versus 2% with placebo (p=0.06).

Tonya Whiting – our fellow that reviewed PROWESS – is in good company when she concluded that the results were believable.  PROWESS seemed to be well-designed and had apparent strong internal validity. I remember feeling the same way back in 2001. I am always skeptical about new therapies, but I had to grudgingly admit that Xigris seemed to work – albeit in a select group of patients. 

But the first time I gave Xigris to a patient, they suffered an intracranial hemorrhage.

I double-checked the safety data from PROWESS. The drug seemed to be relatively safe – with a serious bleeding rate not statistically significantly greater than placebo. Xigris was backed by the highest level of empirical support as an evidence-based-practice. It had editorial support from the NEJM.  It had elegant biological plausibility. Over the next ten years, some observational studies seemed to confirm efficacy (2-4), and the drug was determined to be cost-effective (5). Yet even before this supporting evidence began to accumulate, the underpinnings of PROWESS began to unravel.

The FDA approved Xigris in 2001 – but only for that subgroup of patients with an APACHE II score > 25. We were initially surprised that the FDA would make a decision based on a post-hoc subgroup analysis, but we didn’t initially know about numerous irregularities in the study design of PROWESS (6) that were not reported in the original NEJM publication. These were reviewed by Eli Poulos.  Inclusion/exclusion criteria of PROWESS were changed midway through the study, in order to eliminate patients with significant non-sepsis related diseases and increase the power of the study.  Sites with lower recruitment were dropped from the study. The production process for the drug itself was changed, and it was uncertain whether the agent used at the end of the study was identical to that used at the beginning.  Even the placebo was changed. The apparent benefit of Xigris appreciably increased after these protocol changes were made (6,7).  

The FDA advisory board deadlocked in a ten-to-ten vote over whether or not to approve the drug, yet moved ahead with provisional approval. The FDA was likely under pressure not to unduly restrict potentially life-saving treatments for the highly publicized illness of sepsis. 

Our group began to use Xigris with some trepidation, in order to comply with evidence-based practice. We strictly observed the exclusion criteria used in PROWESS, and APACHE II severity scoring as recommended by the FDA. We found that patients only occasionally met these criteria in our busy ICU.

This caution was widespread, and initial sales of Xigris were no doubt disappointing. Heemesh Seth reviewed an editorial from the NEJM regarding the marketing campaign Eli Lilly subsequently implemented to boost sales (8). Eli Lilly provided a $1.8 million grant to fund a task force on “Values, Ethics and Rationing in Critical Care” reportedly to posit the concept that it was unethical to withhold Xigris from septic patients based on cost considerations.  This debate over the “rationing” of Xigris made it to the pages of the Wall Street Journal (Sept 2003). Eli Lilly also provided over 90% of the funding for The Surviving Sepsis Campaign, launched in October 2002 to create guidelines for the treatment of sepsis.  Many of the international experts who formulated the recommendations of this group had significant outside financial relationships with Eli Lilly. In the initial publication of the treatment guidelines in 2002, the Surviving Sepsis campaign assigned a higher evidence-rating for Xigris in the treatment of sepsis than it did for antibiotics or intravenous fluids. As subsequent prospective trials began to raise important concerns regarding the safety and efficacy of Xigris (see below), these concerns were repeatedly and conspicuously absent from published recommendations of the Surviving Sepsis campaign. In 2004, Eli Lilly started a program of offering unrestricted grants to institutions for implementing Surviving Sepsis Campaign patient management bundles. Sales of Xigris doubled over this period to greater than $200 million per year.

But over the next three years, clinical trials cast increasing doubt on the efficacy of Xigris – these were reviewed by Suresh Uppsala. The ADDRESS trial was a randomized controlled trial that enrolled 2640 patients with severe sepsis and low risk of mortality (9). It showed no difference in 28-day mortality (17 vs. 18% p=0.3).  The ENHANCE trial was an open-label study with no control group that showed that the mortality of patients receiving Xigris for severe sepsis was 25% and that the risk of serious bleeding was 6.5% (10)  - almost twice as high as reported in PROWESS. The RESOLVE trial was a randomized controlled trial that enrolled 477 children with severe sepsis and showed no difference in mortality, and a 4.6% risk of intracranial hemorrhage (11).

Our group, and likely many others, had already abandoned use of Xigris long before publication of the PROWESS -SHOCK trial last May. The conclusions were anticlimactic. The trial enrolled 1697 patients with septic shock and randomized them to treatment with Xigris or placebo.  Mortality at 28-days was 26.4 vs. 24.2% (p=0.3) (12). The rate of serious bleeding in the treatment group was only about 1%, and not significantly different than the rate in the placebo group.  These results were a Godsend to Eli Lilly.  Xigris was already dead in the water clinically. The extremely low rate of bleeding in the study is likely to diffuse questions about how many patients might have been harmed by Xigris over the past decade. 

The authors of PROWESS-SHOCK explicitly state “We cannot explain the inconsistency between our findings and the reduction in mortality at 28 days that was observed in the PROWESS study.”

But we are owed an explanation.  

We have been struggling with how to use this drug beneficially at the bedside for over a decade – now it seems most likely to many of us that it never had any benefit at all.  It appears that we have spent upwards of a billion dollars on Xigris.  Many of us worry that we may have caused serious harm to our patients by giving the drug.  Such risks must sometimes be taken when well-intentioned medical research moves forward in fits-and-starts.  But the published account in this case suggests that our patients may have been placed at increased risk for financial gain. Particularly disturbing was the apparent attempt to create guidelines to increase sales. It sounds grandiose to suggest, but I can’t help but wonder why Eli Lilly isn’t being asked to explain this story to a Congressional investigative committee.  

Robert Raschke MD MS

Associate Editor, Critical Care Medicine. 

References

1. Bernard GR, Vincent JL, Laterre PF, LaRosa SP, Dhainaut JF, Lopez-Rodriguez A, Steingrub JS, et al.  Efficacy and safety of recombinant human activated protein C for severe sepsis.  New Engl J Med 2001;344:699-709.
2. Hodder RV, Hall R, Russell JA, Fisher HN, Lee B. Early drotrecogin alpha administration in severe sepsis is associated with lower mortality: A retrospective analysis of the Canadian ENHANCE cohort.  Crit Care  2009;13:R78.
3. Sadaka F, O'Brien J, Migneron M, Stortz J, Vanston A, Taylor RW..  Activated protein C in septic shock: A propensity-matched analysis.  Crit Care 2011;15:R89.
4. Rowan KM, Welch CA, North E, Harrison DA.  Drotrecogin alfa (activated): Real-life use and outcomes for the UK.  Crit Care  2008;12:R58.
5. Manns BJ, Lee H, Doig CJ, Johnson D, Donaldson C..  An economic evaluation of activated protein C treatment for severe sepsis.  New Engl J Med 2002;347:993-1000.
6. FDA briefing document: anti-infective advisory committee Drotrecogin alfa (activated) [Recombinant human activated protein C (rhAPC)]  Xigris.  BLA#125029/0, Sept 12, 2001.
7. Alaniz C.  An update on activated protein C (Xigris) in the management of sepsis.  PT 2010;35:504-529.
8. Eichacker PQ, Natanson C, Danner RL.  Surviving Sepsis – Practice guidelines, marketing campaigns and Eli Lilly. N Engl J Med 2006;355:1640-2.
9. Abraham E, Laterre PF, Garg R, Levy H, Talwar D, Trzaskoma BL, François B, et al.  Drotrecogin alfa (activated) for adults with severe sepsis and a low risk of death.  New Engl J Med 2005;353:1332-41. 
10. Vincent JL, Bernard GR, Beale R, Doig C, Putensen C, Dhainaut JF, Artigas A, et al.  Drotrecogin alfa (activated) treatment in severe sepsis from the global open-label trial ENHANCE: further evidence for survival and safety and implications for early treatment.  Crit Care Med 2005;33:2266-77.
11. Nadel S, Goldstein B, Williams MD, Dalton H, Peters M, Macias WL, Abd-Allah SA, et al.  Drotrecogin alfa (activated) in children with severe sepsis: a multicentre phase III randomised controlled trial. Lancet 2007;369:836-43.
12. Ranieri VM, Thompson BT, Barie PS, Dhainaut JF, Douglas IS, Finfer S, Gårdlund B, et al.  Drotrecogin alfa (activated) in adults with septic shock.  New Engl J Med 2012;366:2055-64.    

Reference as: Raschke RA. July 2012 critical care journal club. Southwest J Pulm Crit Care 2012;5:54-7. (Click here for a PDF version of the journal club)