The Case of the Balanced Solution


Saline-based resuscitation strategies were first proposed as far back as 1831 during the Cholera Epidemic. In an article published in the Lancet in 1831, Dr. O’Shaughnessy suggests the use of injected salts into the venous system as a means of combating the dramatic dehydration seen in patients afflicted with this bacterial infection(1). Saline’s potential harms were first observed in post-surgical patients who after receiving large volumes of saline based resuscitation fluids during surgery were found to have a hyperchloremic acidosis (2). Though these changes appear transient and clinically trivial, it is theorized that when applied to the critically ill, the deleterious effects on renal blood flow may increase the rate of permanent renal impairment and even death. Unfortunately, no large prospective trials have demonstrated this hypothesis to be anything more than physiological reasoning. Small prospective trials have exhibited trivial trends in decreased renal blood flow, kidney function, and increased acidosis, though these perturbations were fleeting and of questionable clinical relevance (3, 4, 5, 6, 7). A larger retrospective study, bringing all the biases such trials are known to carry, demonstrated small improvements in mortality of ICU patients treated with a balanced fluid strategy, though it failed to demonstrate improvements in renal function (the theoretical model used to support balanced fluid administration) (8). In 2012 Yonus et al were the first to attempt to prospectively answer this question in an ICU population. Published in JAMA, on first glance the results seemed to vindicate those in support of the use of balanced fluids (9). Yet despite its superficial success, a closer look reveals this trial does little to demonstrate the deleterious effects of chloride-rich resuscitative strategies. In a recent publication in Intensive Care Medicine, Yonus et al re-examine this question in the hopes of once again demonstrating the benefits of balanced fluid strategies for the resuscitation of the critically ill (10).

In the original publication Yonus et al, using a prospective open-label before and after cohort design, hoped to demonstrate that use of balanced fluids in ICU patients would lead to improved renal function and decreased administration of renal replacement therapy (RRT). For the initial 6-month period fluid administration was left entirely to the whims of the treating intensivist. This was followed by a 6-month span during which ICU staff were trained and educated on the evils of chloride-rich solutions and the benefits of a more balanced approach to fluid selection. Following this smear campaign on normal saline and its high-chloride co-conspirators, authors spent the next 6-months recording fluid administration and subsequent patient outcomes. The authors’ co-primary outcomes were the increase in creatinine levels above baseline during ICU stay and the incidence of acute kidney injury (AKI) as defined by the RIFLE(Risk, Injury, Failure, Loss, End-stage) criteria. Secondary outcomes listed by the authors included the need for RRT, ICU length of stay, and mortality (9).

As far as convincing ICU staff that balanced solutions were beneficial, the authors’ experiment was an overwhelming success. 1,533 patients were examined, 760 patients during the 6-month control period and 773 patients during the subsequent 6-month intervention period. The total amount of normal saline used over the two periods was 2,411L and 52L respectively. Likewise the total chloride administration decreased by a total of 144,504 mmol, or by 198 mmol/patient (9).

On face value the study appears to have been a success, demonstrating statistically significant benefits for both primary outcomes. During the intervention period patients experienced a statistically lower rise in creatinine levels, 14.8 μmol/L (95% CI, 9.8-19.9 μmol/L) than during the control period 22.6 μmol/L (95% CI, 17.5-27.7 μmol/L). Authors also found a 5.6% absolute decrease in the rate of RIFLE defined kidney injury and kidney failure in patients during the intervention period when compared to those in the control period (9).

These seemingly positive results should be tempered by the fact that while statistically significant, the differences are, for the most part, clinically irrelevant. A 7.8 μmol/L increase in creatinine translates to an approximately 0.09 mg/dl difference between the control and intervention periods, which is hardly clinically pertinent. The 5.6% difference in rate of AKI was primarily powered by the 3.3% difference in rate of the less severe RIFLE class, kidney injury. When kidney failure was examined alone, unaccompanied by this statistical augmentation, the difference was found to be statistically insignificant (9).

Even the 3.7% absolute decrease in RRT in the intervention period (10.0% vs 6.3%) is hard to conclusively attribute to the balanced fluid strategy, given the open nature of the trial design and the fact that these benefits did not translate into either a decrease in the rate of long term dialysis requirements or mortality. Furthermore the annual rates of RRT during the control and intervention periods are almost identical (7.4% vs 7.9%). In fact, the rates of RRT in the years bookmarking this study are highly variable, which speaks to the potential for unmeasured bias and the cyclic nature of random chance causing the observed differences in these groups, rather than the intervention in question. It is important to remember that though RRT appears to be a finite objective endpoint, it is largely dependent on the treating physician’s subjective judgement. In an open label design such as this, in which the authors are clearly in favor of one intervention over another, the potential for bias affecting this outcome is evident (9).

In a secondary analysis of their data set, Yunos et al hoped to address some of these uncertainties. In this manuscript, published in Intensive Care Medicine in 2014, the authors added an additional 6 months of patient data to both the control and intervention periods, with the intention to demonstrate that the positive findings of their initial publication were due to the favorable influences of balanced fluids. The control period was expanded to include patient data (n=716) from the 6-month period prior to the study’s original start date. The authors then incorporated an additional 6 months of data to the intervention group (n=745) after its original stop date. Overall the two augmented periods ran from February 2007 to February 2008 and August 2008 to August 2009. The authors again found success. And though their primary endpoints remained of questionable clinical significance, the magnitude of their triumph was certainly more impressive (10).

With the addition of this 12-month period of data, the authors boast a 4.8% absolute decrease in the rate of moderate or severe kidney injury as compared to the control. Though the absolute difference in the rate of RRT decreased from 3.6% to 3.0%, when the additional patients were added to the analysis, the difference still remained statistically significant (10). Interestingly, despite both the added control and intervention groups regressing to the mean, the overall magnitude of benefit reported by the authors seemed to increase. This slight of hand was achieved not by some complex form of statistical wizardry, but rather simply lowering the bar for what the authors defined as success.

In their original manuscript, Yunos et al used the RIFLE criteria to define the varying degrees of AKI. Conversely in the more recent publication, AKI was evaluated using the Kidney Disease: Improving Global Outcomes (KDIGO) scale. Despite its grandiose title, in reality this scale is essentially the amalgamation of the previous two scales traditionally used to define AKI (the RIFLE and AKIN criteria). Creators of the KDIGO criteria hoped to identify a greater proportion of patients who would benefit from RRT, and thus created a novel tool by incorporating both definitions of AKI (11). Of course, as is typical with any diagnostic tool, augmenting its sensitivity is achieved by sacrificing its specificity.

Such is the case for the KDIGO score. Not surprisingly, when examined, the KDIGO score identified significantly more patients in renal failure than either the RIFLE or AKIN criteria. In a trial published by Critical Care in 2014, Luo et al compared RIFLE, AKIN and KDIGO’s abilities to identify clinically important AKI (12). They found that the use of the KDIGO criteria identified more overall patients as having AKI (51% compared to 46.9% and 38.4% respectively) as well as classified an larger subset of patients as being in failure (16% compared to 13.8% and 12.8% respectively). Despite the increased yield, no difference was seen in each respective criterion’s abilities to predict death (AOC were 0.738, 0.746, 0.757 respectively). It is still unclear whether the additional patients identified using the KDIGO criteria benefit from early aggressive management of their subtle renal impairment or are harmed from the invasive interventions performed in hopes of treating pathology that would likely resolve without interference. What is clear is that changing from the more conservative RIFLE criteria to the more liberal KDIGO, makes interpreting the clinical relevance of Yunos et al’s results difficult.

In the 2014 publication by Yunos et al, the absolute difference in AKI is similar to that described in the 2012 publication (4.8% vs 5.6%), but unlike their original population there is a shift to a more severe spectrum of renal impairment. Using the KDIGO criteria authors found significantly more stage 3 AKI than in their original publication. In the original manuscript the difference in RIFLE failure (class 3) AKI failed to reach clinical significance. In their updated cohort the authors now cite a statistically significant decrease in the rate of KDIGO class 3 AKI (the equivalent of RIFLE failure). The original trial states an absolute difference in the rate of RIFLE class 3 AKI of 2.1%. In their more recent document Yunos et al now cite a 4% (14% vs 10%) absolute decrease in KDIGO stage 3 AKI. Likewise the original manuscript states an absolute difference of 3.3% in the rate of RIFLE class 2 AKI. In the more recent document this same difference is now stated to be only 2%. Clearly the use of the KDIGO criteria has shifted the severity of the cohort in an alarming fashion. This increase in class 3 AKI may be a more accurate interpretation of reality, but given that these differences did not translate into a decrease in either long-term dialysis or mortality, its clinical relevance is unlikely.

Even these clinically questionable differences cannot be directly attributed to the more balanced fluid strategy utilized during the intervention period. It is equally likely the multiple biases introduced by a before and after study design were responsible. Using a multivariant regression model, Yunos et al hoped to account for many of these biases. On initial presentation authors seem to be vindicated in their assertions that these differences in renal function were due to the change in fluid administration. When the addition of the extended control and intervention periods were included in the multivariable analysis, the rate of KDIGO stage 2 and 3 AKI and RRT remained statistically significant. This benefit was powered completely by the initial cohort, the addition of the extended cohorts served only to regress these benefits towards the mean. The odds ratio in the original cohort for preventing AKI was 1.68 (1.28-2.21). When the extended groups were incorporated the odds ratio falls to 1.32 (1.11-1.58).  In fact a thorough examination comparing the four time periods uncovers the initial results are hardly as robust as they originally appear.  When the extended time period is examined alone (control vs intervention), there was no difference between in the incidence of AKI or RRT. Additionally when the extended control is compared to the original intervention period, the decrease in difference in AKI remains significant but the rate of RRT is no longer statistically significant. There is even a statistically significant increase in the rate of AKI when the original intervention period is compared to the extended intervention period. In fact this is the very same difference in both AKI and RRT that is observed when comparing the original control group to the extended intervention group (10) . Essentially, though it was the authors intent to validate the findings of their initial study, the inconsistent benefits demonstrated in the extended cohort do just the opposite.  These differences seem to be due more to random chance than any beneficial effects of a balanced fluid strategy.

The interpretation of medical literature very rarely is as straightforward as we would like to imagine. Much like searching for truth in a magic mirror, so often it serves only to confirm our own beliefs and supports our incredulities. And yet if we are to claim to be authentic curators of truth in medicine, it is important we apply just as much academic rigor when examining topics which we support as we do with those we distrust. A balanced approach to fluid administration has a strong physiological base to support its use. But physiologic reasoning has led us down many blind paths and dark alleys. It is only when we shine the light of critical research we reveal which are dead ends and which lead us and our patients to a better place. Currently we are uncertain as to whether the success of a balanced fluid strategy is due to its chloride-sparring effects or due to the uncontrollable bias introduced by a non-randomized, unblinded trial design, with serious potential for the Hawthorne effect. It may very well be that any fluid in excess is harmfull and “balanced” fluids high in acetate and lactate have their very own unintended consequences when administered in high volumes. The SPLIT trial (scheduled to be published in 2015) may validate our beliefs in the superiority of a balanced fluid strategy, but until then it is important we resist the urge to become quite so dogmatic with our cries of indignation towards chloride-rich solutions.

 A brief disclosure: I am, in fact, overwhelmingly and irredeemably in favor of the Stewart approach to acid-base disorders. although there is no convincing evidence directly demonstrating its superiority over the more traditional Henderson-Hasselbalch model, its elegance and intuitive nature make it perfect for the swirling chaos and uncertainty of the Emergency Department. As such it is not hard to imagine that the more judicious administration of fluid, specifically those high in chloride content, would benefit our patients by reducing hyperchloremic acidosis and the concomitant renal failure. I am however, less enthused by the evidence supporting this premise.

-A special thanks to Anand Swaminathan (@EMSwami) for his thoughts and guidance during the writing of this post.

-As always a special thanks to my ever patient wife, Rebecca Talmud(@DinosaurPT), for her editorial wizardry without which this blog would be the unstructured ramblings of a madman.

Sources Cited:

  1. O’Shaugnessy, WB (1831). “Proposal for a new method of treating the blue epidemic cholera by the injection of highly-oxygenated salts into the venous system”. Lancet 17 (432): 366–71
  2. Scheingraber S, Rehm M, Sehmisch C, Finsterer U. Rapid saline infusion produces hyperchloremic acidosis in patients undergoing gynaecologic surgery. Anesthesiology. 1999;90:1265–1270
  3. Quilley CP, Lin Y-S, McGiff JC. Chloride anion concentration as a determinant of renal vascular responsiveness to vasoconstrictor agents. Br J Pharmacol. 1993;108:106–110
  4. Hansen PB, Jensen BL, Skott O. Chloride regulates afferent arteriolar contraction in response to depolarization. Hypertension. 1998;32:1066–1070.
  5. O’Malley CM, Frumento RJ, Hardy MA, Benvenisty AI, Brentjens TE, Mercer JS, Bennett-Guerrero E. A randomized, double-blind comparison of lactated Ringer’s solution and 0.9% NaCl during renal transplantation. Anesth Analg. 2005;100:1518–1524
  6. Waters JH, Gottlieb A, Schoenwald P, Popovich MJ, Sprung J, Nelson DR. Normal saline versus lactated Ringer’s solution for intraoperative fluid management in patients undergoing abdominal aortic aneurysm repair: an outcome study. Anesth Analg. 2001;93:817–822.
  7. Hatherill M, Salie S, Waggie Z, Lawrenson J, Hewitson J, Reynolds L, Argent A. Hyperchloraemic metabolic acidosis following open cardiac surgery. Arch Dis Child. 2005;90:1288–1292
  8. Raghunathan K, Shaw A, Nathanson B, Stu ̈ rmer T, Brookhart A, Stefan MS, Setoguchi S, Beadles C, Lindenauer PK (2014) Association between the choice of IV crystalloid and in-hospital mortality among critically ill adults with sepsis. Crit Care Med 42:1585–1591
  9. Yunos NM, Bellomo R, Hegarty C, Story D, Ho L, Bailey M (2012) Association between a chloride-liberal vs chloride-restrictive intravenous fluid administration strategy and kidney injury in critically ill adults. JAMA 308:1566–1572
  10. Yunos NM, Bellomo R, Glassford N, Sutcliffe H, Lam Q, Bailey M. Chloride-liberal vs. chloride-restrictive intravenous fluid administration and acute kidney injury: an extended analysis. Intensive Care Med. 2014.
  12. Luo X, Jiang L, Du B, et al. A comparison of different diagnostic criteria of acute kidney injury in critically ill patients. Crit Care. 2014;18:(4)R144.



A Secondary Examination of The Adventure of the Cardboard Box-Addendum

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Published in the NEJM on December 17th 2014, ushered in with the inflated fanfare only the medical industry capable of, MR CLEAN marks the first successful trial of interventional therapy for acute ischemic stroke. In direct contrast to IMS-3, SYNTHESIS and MR RESCUE, MR CLEAN is a significantly positive trial.  The authors demonstrated success in their primary outcome, “improved neurological outcomes at 90 days” with an adjusted odds ratio of 1.67  (95% confidence interval [CI], 1.21 – 2.30). (1). Why MR CLEAN was positive when the three trials that came before were negative is still unclear. As discussed in my previous post (as well as far more elegant posts on and it may be due to better equipment, faster symptom onset to recanulization times, and the incorporation of CT angiography to identify a cohort of patients who would truly benefit from these invasive interventional strategies. Conversely it may simply be due to the traditional therapy group performing so poorly.

A closer look at the results from MR CLEAN reveal that though the interventional group outperformed the placebo group by a significant amount (an absolute increase of the number of patients alive and independent by 13.5%) compared to its peers, its performance was far from exceptional. In the IMS-3 trial, 40.2% patients in the control arm (tPA alone) were alive and independent at 90 days compared to only 32.6% of the patients in the intervention arm of the MR CLEAN trial (1,2). Even the placebo groups in NINDS and ECASS-3 who received no reperfusion therapies had better outcomes than the patients receiving interventional therapies in the MR CLEAN trial. 26% and 45.5% of the control patients in the NINDS and ECASS-3 trials respectively had a mRS of 0 or 1 at 90 days (3,4). Compared to only 11.6% of the patients in the interventional arm of MR CLEAN.

Though it is difficult and not completely appropriate to compare groups from different trials, it does call into question the reasons for MR CLEAN’s staggering success. It may very well have been the patients in the MR CLEAN cohort were far sicker than the earlier stroke trials, (though both their presenting NIHSS and 90 day mortality rates seem quite similar). It may be that the utilization of CT angiography to select patients for recruitment excluded the majority of the stroke mimics who were included in these earlier trials, and will universally have good outcomes (this seems to be the answer given by the authors when queried by Dr. Ryan Radecki). The subgroup analysis, which indicated only the patients with a NIHSS of greater than 20 demonstrated a statistically significant benefit from endovascular therapy, seems to support this supposition (1). The authors point to a meta-analysis of the six trials examining endovascular therapy for acute ischemic stroke as additional proof (5). In this analysis by Fargen et al, published in the J NeuroIntervent Surg, the authors examine the subgroup of patients with radiographically confirmed large vessel occlusion (LVO). Similar to MR CLEAN, patients receiving endovascular therapy had better outcomes at 90 days (a mRS of 0-2 38.3% vs 25.8% respectively ). Even in this combined cohort with radiographically confirmed LVO, outcomes were not as dire as those observed in the MR CLEAN trial.

MR CLEAN’s success may be attributed to the advancements in both procedural proficiency and technological prowess. But it is equally likely that the whimsy of random chance was responsible for these impressive results. On a final note it is important to remember that all of the trials examining endovascular therapy in acute ischemic stroke were compared to a control group that included the administration of IV tPA, an intervention whose own efficacy is very much in doubt. Although the rate of adverse events in the intervention arm of MR CLEAN did not differ significantly from those given IV tPA, this is only because alteplase comes with its own terrifying set of unpleasantries. When compared to a true placebo group, I am certain the rate of symptomatic intracranial hemorrhage and new ischemic stroke (7.7% and 5.6% respectively) would appear far more concerning.

Given the universal failure of the previous three trials examining the very same question, surely more confirmatory evidence is required before investing the unimaginable resources required to support the vast infrastructure needed to make interventional therapy a reality. Since MR CLEAN’s success was announced at the 9th annual World Stroke Conference in Istanbul held in October 2014, two trials examining endovascular therapy in acute ischemic stroke, ESCAPE and EXTEND IA, have halted enrollment early for benefit. It will be interesting to see if these premature stoppages were because of preplanned interim analyses or if MR CLEAN’s success influenced their early termination. I hope we invest the time and resources required to answer these questions with the methodological rigor they deserve. It would be frustratingly tragic to once again be forced to practice with continual doubt because we halted all further investigations out of the fear of discovering that reality is not as promising as the false-truth gained from interpreting only the data that pleases us.

Sources Cited:

  1. The MR CLEAN Investigators. A Randomized Trial of Intraarterial Treatment for Acute Ischemic Stroke. N Engl J Med, December 17, 2014.
  2. Broderick JP, Palesch YY, Demchuk AM, et al. Endovascular therapy after intravenous t-PA versus t-PA alone for stroke. N Engl J Med. 2013;368(10):893-903.
  3. Tissue plasminogen activator for acute ischemic stroke. The National Institute of Neurological Disorders and Stroke rt-PA Stroke Study Group. N Engl J Med. 1995;333(24):1581-7.
  4. Hacke W, Kaste M, Bluhmki E, et al. Thrombolysis with alteplase 3 to 4.5 hours after acute ischemic stroke. N Engl J Med. 2008;359(13):1317-29.
  5. Fargen KM,
Neal D, Fiorella DJ, et al. J NeuroIntervent Surg Published Online First: [please include Day Month Year] doi:10.1136/ neurintsurg-2014-011543.

A Case of Identity Part Two


Our standards for acceptable benefit of antiplatelet agents in the management of ACS have become deplorably low. When ISIS-2 was first published we defined success only by aspirin’s ability to affect mortality. The number commonly cited, 2.4%, only describes aspirin’s absolute benefit to decrease death (1). In the one trial that examined its properties to prevent further infarction, published in the NEJM in 1988, aspirin demonstrated additional capabilities to decrease myocardial infarction as well as save lives (2). If in ISIS-2, aspirin had performed as poorly as clopidogrel did in its efficacy defining study, the CURE trial, it may have never gained the stature it currently holds in the management of ACS (3). To date aspirin has been the only antiplatelet agent that has demonstrated a consistent and clinically relevant mortality benefit. Despite the obvious benefits, it was not long before we turned towards other agents in an attempt to supplement aspirin’s antiplatelet properties. The concept of dual antiplatelet therapy so appealing, its theoretical basis so believable, it soon became a perfunctory part of our management strategy for patients presenting to the Emergency Department with ACS.

Our current concept of dual antiplatelet therapy was first defined in 1996 with the publication of the CAPRIE trial. Published in The Lancet in November of 1996, this trial was the first of many to indicate clopidogrel’s efficacy in finding clinically irrelevant reductions of methodologically deceitful composite endpoints (4). So began the era of dual antiplatelet therapy in which, based off weak endpoints and statistical chicanery, clopidogrel and its post-patent clones have bullied and fibbed their way to success.

Throughout the literature examining clopidogrel in a multitude of ACS cohorts of varying degrees of severity, its vaulted dual anti-platelet capabilities have never demonstrated a clinically relevant mortality benefit. Its success has been powered by the reduction of non-fatal MIs, the majority of which are peri-procedural troponin leaks of questionable clinical significance. The only clinically relevant endpoint clopidogrel has consistently demonstrated is a 1% absolute increase in serious bleeding. Despite these mediocre capabilities, Bristol-Meyer, through sheer force of will and marketing prowess, catapulted their drug to the forefront of pharmaceutical sales for over a decade. The true level of clopidogrel’s mundanity has been discussed in a previous post. The more important question for Emergency Physicians is, does the upstream administration of P2Y12 inhibitors provide added benefit over only administering these medications after confirming appropriate coronary anatomy during catherization?

Upstream use of P2Y12 inhibitors in ACS is commonly believed to be beneficial as it deters thrombus formation through additional inhibition of platelet adherence vs the singular capabilities of aspirin alone. Despite a dearth of evidence validating this claim and reasonable data stating otherwise, this practice has been routinely implemented since the publication of the CURE trial over a decade ago.

So is there a role for dual antiplatelet therapy in today’s Emergency Department?

Two recent publications sought to address this very question. The more methodologically ambitious of these trials was a systematic review and meta-analysis published in the BMJ in October of 2014 in which Bellemain-Appaix et al attempted to examine all the literature addressing the potential benefit of upstream use of P2Y12 inhibitors in NSTEMI patients undergoing PCI (5). Much to the chagrin of the authors, only one trial included (the recently published ACCOAST trial) specifically examines this specific inquiry. The authors, not to be dissuaded, attempted a piecemeal collection of various subgroups from a number of trials that seemed to meet their entry criteria. This resulted in a statistically and clinically heterogeneous cohort whose subsequent data should probably not have been combined into a single analysis. Nevertheless the authors plunged ahead examining the NSTEMI patients in both the CREDO and CURE trials, as well as the subset of patients in the ACUITY trial who were pre-treated with clopidogrel. Also including the entire cohort from the ACCOAST trial, the only trial included examining prasugrel. Combining these trials with the data from three observational cohorts, the authors collected information on 32,838 patients.

Contrary to most trials attempting to examine potential benefit in the use of P2Y12 inhibitors, these authors set aside the traditional composite endpoint (stroke, MI, or cardiovascular death) and looked exclusively at mortality and major bleeding. The authors found no mortality benefit in either the entire cohort, the subgroup of patients from the RCTs, or in the group that underwent PCI. Conversely, an increased risk of bleeding was observed in patients treated with upstream P2Y12 inhibitors. No difference was seen in the rate of stroke, myocardial infarction or urgent revascularization. However when a composite outcome the authors termed “adverse cardiac outcomes” was measured, they found a small reduction in risk (odds ratio 0.84, CI 0.72-098). As with all individual trials examined, this composite benefit is powered by a small increase in myocardial infarctions, that when examined alone did not reach statistical significance (odds ratio of 0.81, CI 0.64- 1.03). When the subgroup of patients who underwent PCI was isolated this decrease in “adverse cardiac events” was no longer significant (odds ratio 0.83, CI 0.99-0.1.03). This speaks more to the drastic decrease in sample size (32,383 to 17,545), decreasing the statistical power to detect clinically irrelevant differences, than a meaningful difference between those who undergo PCI compared to those who do not (5).

Unfortunately the clinical heterogeneity between the trials included in this meta-analysis is quite high. The trials included span different eras and different strategies in the overall management of patients experiencing NSTEMIs. It is questionable whether they should have been included in a formal analysis at all. Fortunately one does not require the above stated statistical manipulations to reach the same conclusions garnered by the authors. Each trial that examined the efficacy of upstream use of P2Y12 inhibitors failed to identify any clinically meaningful benefit.

The CURE trial was the earliest trial included in this analysis. This trial paved the way for clopidogrel’s use in the Emergency Department simply by utilizing composite endpoints of questionable clinical significance and a sample size large enough to bully even the smallest deviation from placebo towards statistical relevance. Published in NEJM in 2001, the authors claimed a statistically significant 2.1% absolute decrease in cardiovascular death and myocardial infarction (MI). This difference was completely powered by the 1.5% absolute difference in MIs, the majority of which were type IV MIs (peri-procedural). This small reduction is of questionable clinical consequence as the mortality rate between groups was identical at 30 days (1.0% vs 1.1%) as well as at the end of follow up (2.3% vs 2.4%)(mean of 8 months)(3).

The CREDO trial sought to answer the question of whether treatment with clopidogrel prior to angiography was beneficial, examined patients scheduled for urgent cardiac cathertization. Patients were randomized to upstream administration of clopidogrel or placebo 3-24 hours prior to cath. All patients received daily clopidogrel following PCI. Like CURE before it, the CREDO authors found no clinically important benefit to the upstream use of clopidogrel. No statistical difference was recorded in the rates of death, stroke or MI at 28 days between the placebo and upstream clopidogrel groups. The authors claim success in the statistical significance of a secondary endpoint, the per-protocol analysis of the 1-year outcomes, noting a 2% absolute reduction in the rate of death, MI, and stroke. Similar to CURE, this difference was powered by the 1.9% reduction of MIs. Interestingly, statistical significance is lost upon examining any of the three endpoints individually, or when the same composite endpoint is analyzed using the authors’ primary outcome and more statistically appropriate methodology, the intention-to-treat analysis. As is typical with all P2Y12 inhibitor trials there was a 1% increase in major bleeding events in both the CURE and CREDO trials, the vast majority of which were related to subsequent CABG procedures after coronary anatomy revealed less than ideal conditions for stent placement (6).

Neither of these trials are methodologically ideal to address the question, in the modern Emergency Department does the upstream use of P2Y12 inhibitors result in improved patient oriented benefits? In the CURE trial less than half the patients (43.8%) underwent coronary angiography and only 21.2% received PCI. In the CREDO trial only 67% of the patients were actually having an enzyme defined NSTEMI (3,6)

The final RCT included in the Bellemain-Appaix et al meta-analysis, the ACCOAST trial, is far more relevant. Using modern PCI techniques and standards, Montalescot et al specifically examined whether upstream administration of prasugrel was beneficial when compared to its administration in the cath lab after visualizing the coronary anatomy. The recent marketing disaster that was the publication of the TRILOGY trial, a completely negative study comparing prasugrel to clopidogrel in patients with ACS, was the first obstacle in prasugrel’s race to fill the post-patent void at the top of the antiplatelet hierarchy. ACCOAST was an attempt to regain the momentum lost with TRILOGY’s failure. Authors randomized 4,033 patients with NSTEMI in the Emergency Department to either 30 mg of prasugrel 2-48 hours prior to PCI or placebo. Following visualization of the anatomy during angiography and stent placement when appropriate, the prasugrel group received the remaining 30 mg of the 60 mg loading dose that is recommended by Eli Lilly. The placebo group received the full 60 mg dose of prasugrel at the time of PCI if stent placement was thought to be beneficial. The authors failed to demonstrate a benefit in upstream administration of prasugrel when compared to its administration in the cath lab, with no difference in cardiovascular death, myocardial infarct, stroke, urgent revascularization or glycoprotein IIb/IIIa bailout (10.8% vs 10.8%). As is consistent with the rest of the literature examining the use of P2Y12 inhibitors, the pretreatment group was found to have approximately 1% increase in major bleeding. Most due to an increase in bleeding during CABG (20.7% vs 13.7%)(7).

Finally, what about the added benefit of dual antiplatelet therapy in the hyperacute patient? What is the benefit of P2Y12 inhibitors in patients with a time dependent lesion? In an article published in September 2014 in the NEJM, Montalescot et al examined this very question. The authors of the “Administration of Ticagrelor in the Cath Lab or in the Ambulance for New ST Elevation Myocardial Infarction to Open the Coronary Artery (ATLANTIC)” trial randomized patients to a 180 mg loading dose of ticagrelor in either the ambulance on the way to the hospital or in the cath lab prior to angiography. The authors and their benefactors, AstraZeneca, hoped to demonstrate that upstream use of ticagrelor was an important addition to the management of these hyperacute patients. Though they included patients with ST-elevation MIs up to 6 hours after symptom onset, the majority of patients were identified within 70 minutes of symptom onset (well within the time dependent portion of STEMI pathology)(8).

A total of 1,862 patients were randomized to either pre-hospital or in-hospital treatment. The authors selected the unfortunate clinically irrelevant measures of the proportion of patients who did not have 70% or greater resolution of ST-segment elevation before PCI, and the proportion of patients who did not meet the criteria for TIMI flow grade 3 in the infarct-related artery at angiography before PCI as their co-primary endpoints. Thankfully we were saved the discussion of why neither of these metrics translated into patient oriented outcomes as the authors failed to find a difference between the pre-hospital and in-hospital groups. Nor was there a difference in the more traditional composite endpoint (rate of cardiovascular deaths, MIs, strokes, urgent revascularizations, or definitive stent thrombosis) so commonly used in P2Y12 inhibitor trials (4.5% vs 4.4%). In an altogether unsurprising twist, the authors claim this trial a success after dredging up a single secondary endpoint from the many measured that achieved a p-value of significance. Patients who received pre-hospital administration of ticagrelor experienced a smaller rate of definitive stent thrombosis when compared to patients receiving the drug in the cath lab (0.2% vs 1.2%). This difference seemed to have no clinical relevance as there was no difference in the rate of myocardial infarction or death at 30 days between the groups. In fact the mortality rate in the pre-hospital group was alarmingly higher, though the 1.3% absolute difference (3.3% vs 2.0%) in 30-mortality failed to reach statistical significance(8).

As is the case with any in depth examination of the literature supporting the use of P2Y12 inhibitors we are left entirely underwhelmed. From as far back as the CURE trial the theoretical benefits of dual antiplatelet therapy have consistently lacked evidentiary support of clinically relevant patient oriented outcomes. Even the small industry manipulated advantages seemingly evaporate when drugs are compared to their own administration downstream in the cath lab once suitable anatomy has been defined. Recently published trials examining long-term use of P2Y12 inhibitors after stent placement have been far from stellar (9,10). Both a meta-analysis and large RCT demonstrated that even in cases of anatomically confirmed disease with stent placement, these medications offer very limited benefits over aspirin therapy alone and in some cases even demonstrate a small increase in mortality (0.5% increase in all-cause mortality). This is not a case where more evidence is required. It is time we reexamine the utility of dual anti-platelet therapy in the Emergency Department. Clearly we now have convincing data that upstream use of P2Y12 inhibitors whether administered pre-hospital or in the Emergency Department do not provide any patient oriented benefits and can only lead to harm. In fact the only benefit that can be gained by maintaining this dual anti-platelet delusion is to ensure the well being of the pharmaceutical companies whose lies and manipulation have led us down this fool’s path in the first place.

Sources Cited:

  1. Randomized trial of intravenous streptokinase, oral aspirin, both, or neither among 17,187 cases of suspected acute myocardial infarction: ISIS-2. ISIS-2 (Second International Study of Infarct Survival) Collaborative Group. Lancet. 1988;2(8607):349-60.Heparin, Aspirin or Both NEJM
  2. Théroux P, Ouimet H, Mccans J, et al. Aspirin, heparin, or both to treat acute unstable angina. N Engl J Med. 1988;319(17):1105-11.
  3. Yusuf S, Zhao F, Mehta SR, et al. Effects of clopidogrel in addition to aspirin in patients with acute coronary syndromes without ST-segment elevation. N Engl J Med. 2001;345(7):494-502.
  4. A randomised, blinded, trial of clopidogrel versus aspirin in patients at risk of ischaemic events (CAPRIE). CAPRIE Steering Committee. Lancet. 1996;348(9038):1329-39.
  5. Bellemain-Appaix Anne, Kerneis Mathieu, O’Connor Stephen A, Silvain Johanne, Cucherat Michel, Beygui Farzin et al. Reappraisal of thienopyridine pretreatment in patients with non-ST elevation acute coronary syndrome: a systematic review and meta-analysis BMJ 2014; 349:g6269
  6. Steinhubl SR, Berger PB, Mann JT, et al. Early and sustained dual oral antiplatelet therapy following percutaneous coronary intervention: a randomized controlled trial. JAMA. 2002;288(19):2411-20.
  7. Montalescot G, Bolognese L, Dudek D, et al. Pretreatment with prasugrel in non-ST-segment elevation acute coronary syndromes. N Engl J Med. 2013;369(11):999-1010.
  8. Montalescot G, Hof AW, Lapostolle F, et al. Prehospital Ticagrelor in ST-Segment Elevation Myocardial Infarction. N Engl J Med. 2014
  9. Mauri L, Kereiakes DJ, Yeh RW, et al. Twelve or 30 Months of Dual Antiplatelet Therapy after Drug-Eluting Stents. N Engl J Med. 2014
  10. Sammy Elmariah MD,Laura Mauri MD,Gheorghe Doros PhD,Benjamin Z Galper MD,Kelly E O’Neill BS,Prof Philippe Gabriel Steg MD,Prof Dean J Kereiakes MD,Dr Robert W Yeh MD. Extended duration dual antiplatelet therapy and mortality: a systematic review and meta-analysis. The Lancet – 16 November 2014

A Secondary Examination of The Adventure of the Cardboard Box


In November of 1995 stroke care as we know it drastically and permanently changed. With the publication of NINDS-2 the NEJM ushered in the interventional era of acute ischemic stroke (1). No longer were we powerless in our management of these patients. Finally we could offer them more than an aspirin to chew on, a corner to sit in, and an appointment with a neurologist in the morning.  And yet NINDS-2 was not the first trial examining thrombolytic therapy for acute ischemic stroke. In fact three trials were published prior to NINDS-2 all of which were negative (NINDS-1, MAST-I, ECASS-1) with two finding an increase in mortality in patients given thromblytics (1,2,3). With the publication of NINDS-2 all this was forgotten. NINDS-2 was impressively positive, demonstrating a 13% absolute increase in patients who were given tPA that were alive and independent (mRS of 0 or 1) at 90 days (1). Supporters justified the 6% absolute increase in symptomatic intracranial hemorrhage by arguing that it did not increase 90-day mortality (21% vs 17%). Despite these impressive results there were still three negative trials to account for. What made NINDS-2 different than all the trials that came before it? Was it the agent? Supporters claim that tPA was the superior thrombolytic and we should ignore all trials studying other agents. Was it time? NINDS examined patients who received tPA within 180 minutes of symptom onset (half in under 90 minutes); two of the earlier trials examined patients who received thrombolytc therapy over a much broader treatment window. Was it the patient population? The authors of NINDS used very strict selection criteria to determine which patients were acceptable candidates. There was of course a fourth reason proposed by a less enthusiastic contingent, that being random chance. This more skeptical party posited that an intervention that possesses little or no efficacy, if studied enough times would eventually demonstrate positive results simply by chance alone. They reminded the more eager supporters of tPA therapy that though the findings of NINDS-2 may be true, taking these results at face value without further validation was not only bad science, but even worse medicine. Despite these warnings the FDA fast tracked the approval of tPA for acute ischemic stroke in under 3-hours and all other trials attempting to validate this benefit were abandoned. As Elliot Grosbard, Genentech scientist, said in internal communications in regards to further trials comparing streptokinase to tPA for acute coronary syndrome;

 We do not know how another trial would turn out, and if we don’t come out ahead we would have a terribly self inflicted wound… (another study) may be a good thing for America, but it wouldn’t be a good thing for us.

Four consecutive trials were published following NINDS (all examining time windows greater than 3 hours) all six were negative and four demonstrating harm (4,5,6,7,8.9). It wasn’t until the 2008 publication of ECASS-3 that another trial examining thrombolytics for ischemic stroke demonstrated benefit (10). These benefits though not as impressive as NINDS-2 were convincing enough to make us forget the seven other negative trials examining similar time windows. Unlike NINDS-2 we were unable to claim ECASS-3 was different than these other negative trials examining similar patients during similar time windows. So instead, we just ignored them. Like our nostalgia for our endless childhood summers we have chosen to selectively interpret the literature that confirms our biases. Remembering only the fireworks, campfire tales, and days spent in the crashing waves of the Atlantic Ocean, we conveniently forget the sun burnt shoulders, poison ivy scorched legs and the tattered knees so commonly acquired during childhood adventures. This tunnel-vision has (mis)guided stroke care for the last two decades. Investigators continue to role the dice, ignoring all numbers that do not suit their purposes.

19 years after the publication of NINDS changed stroke management, the Multicenter Randomized Clinical Trial of Endovascular Treatment for Acute Ischemic Stroke in the Netherlands (given the unfortunate acronym MR CLEAN) once again threatens to overthrow the infrastructure of stroke care (11). The results of this multi-center trial comparing endovascular therapy to standard care were presented at the 9th annual World Stroke Conference in Istanbul held in October 2014. Though these results were not published, with the fanfare NINDS-2 experienced after its initial announcement, it difficult not to see the similarities between these two trials. Like NINDS-2, this is the first trial to show benefit of a novel therapy in acute ischemic stroke. Like NINDS, these results are in direct contrast to the 3 trials published to date examining endovascular interventions for acute ischemic stroke.

On February 7th 2013, NEJM published 3 articles all examining the efficacy of endovascular treatment for acute ischemic stroke. All 3 trials were universally negative each one failing to demonstrate benefit in their own unique manner (12,13,14). These trials were instantly discredited by endovascular apologists stating a number of reasons why they should be ignored. For one they enrolled the wrong patients. These trials primarily used only a non-contrast CT to select patients appropriate for endovascular therapies. Most experts argue this is not the optimal imaging technique for selecting patients for endovascular interventions and all patients should have undergone CT-angiography before enrollment. These trials examined endovascular therapy during the wrong time period. Proponents of these interventions argued that time-to-clot retrieval was far longer than their current standards and these delays erased any benefits endovascular therapy may have provided. Finally and most importantly these trials used the wrong equipment. The Merci retrieval device was prominently featured in all three of these initial trials. A device that most interventionists now consider antiquated and, in a number of small trials demonstrated suboptimal performance when compared to newer devices used currently by most interventionists.

In direct contrast to these results, MR CLEAN is a significantly positive trial. Although the official manuscript has yet to be published a great deal can be garnered from the poster presentation abstract, press release and previously published protocol and statistical analysis plan (11, 15, 16). MR CLEAN is a multicenter randomized clinical trial comparing endovascular treatments for acute ischemic stroke conducted in the Netherlands. Using the prospective open label, blinded endpoint (PROBE) design comparing patients randomized to receive either endovascular treatment (consisting of intra-arterial tPA or urokinase followed by clot retrieval) or standard therapy (91% of which received intravenous tPA alone). Over a 5-year period, authors enrolled 500 patients aged 18 years or older with acute ischemic stroke and a symptomatic anterior proximal artery occlusion, which could be treated within 6 hours after stroke onset.

The authors found patients randomized to endovascular treatment were more likely to have improved neurological outcomes at 90 days with an adjusted odds ratio of 1.67 (95% confidence interval [CI], 1.21 – 2.30). Though there was a significantly higher rate of adverse reactions in the endovascular group (47% vs 42%), these rates did not seem to affect either 90 day neurological outcomes or morality (21%vs 22%). If you were to use the NINDS-2 definition of good neurological outcomes (mRS of 0 or 1), endovascular treatment would have demonstrated a 14% absolute increase in patients alive and independent at 90 days, with a number needed-to-treat (NNT) of 7.

So why was MR CLEAN positive when the 3 trials which came before were negative? Was it the patients? It is true that the authors of MR CLEAN were far more selective in the patients they included. In fact authors required patients to have an occlusion of distal intracranial carotid artery or middle cerebral artery(M1, M2) or anterior cerebral artery (A1) demonstrated with CT angiography (CTA), magnetic resonance angiography (MRA) or digital subtraction angiography (DSA) before they were enrolled in the trial. Was it time? Patients received both IV tPA and endovascular treatments far faster than any of the patients in IMS-3, Synthesis or MR RESCUE. In the MR CLEAN trial patients received their IV tPA on average 85 to 87 minutes after symptom onset and underwent endovascular therapy 196 to 204 minutes after symptom onset. Was it the devices used? In contrast to the initial 3 trials, 97% of the endovascular interventions performed in the MR CLEAN cohort utilized a modern retrievable stent device. Or was it just the random fickle nature of fortune that provided us with these impressive results?

Currently we do not have the full publication of MR CLEAN, so a detailed analysis of the results proves difficult. That being said there are a number of interesting points we can take away from the published protocol and results presented during the 9th annual stroke conference. Firstly the authors claim success in their primary outcome, which they define as “the score on the mRS at 90 days” (11,15). They claim this benefit by citing an adjusted odds ratio of 1.67 (95% confidence interval [CI], 1.21 – 2.30). What are we to take from this odds ratio? What exactly were they measuring and what imbalances were they attempting to adjust that randomization would not account for? In the statistical analysis portion of their protocol the authors only slightly expand on the vague nature of this outcome. The authors used an ordinal analysis in an attempt to quantify the benefits of endovascular therapy over the entire mRS. They then decided to further adjust these outcomes using multivariable logistic regression in an attempt “adjust for chance imbalances in main prognostic variables between intervention and control group”. The specific variables they chose to adjust for were age, stroke severity (NIHSS), time since onset, previous stroke, atrial fibrillation, carotid top occlusion and diabetes mellitus (11). This is the same statistical wizardry used in IST-3 to magically transform a decidedly negative trial into a statistically positive one (17). MR CLEAN marks the first time this type of statistical analysis was used as a trial’s primary end point rather than a secondary experimental, trial saving outcome.

To be clear this trial was an overwhelming success and this analysis is in no way intended to take away from these findings. Rather to question whether an adjusted ordinal analysis is the appropriate outcome to assess efficacy. We have discussed the problems with ordinal analyses in depth in a prior post, but briefly it is an attempt to granularize the data so as to detect smaller changes in outcomes than the more tradition dichotomous cutoff (mRS 0,1, or 2 vs 3,4,5,or 6) is capable of detecting. On face value this seems like a noble pursuit, but logistically presents a number of problems when employed in a trial. Most importantly, is an ordinal analysis an appropriate measure of functional outcomes? Ordinal analysis is an attempt to examine shifts across an entire functional scale. Minute changes in outcomes that would be missed by a dichotomous measurement. To do so one has to assume flawlessness of the collection process and intrinsic reliability of the functional assessment tool. We know that the reliability of the mRS is questionable at best. In fact when two neurologists assess the same patient their results will often differ by up to 2 points (19).

The MR CLEAN 90 day mRS data was assessed using a structured phone interview conducted by a trained research nurse. This trial employed an open design where the patients were not blinded to their group assignments, using an outcome scale of questionable reliability, collected by a phone interview. Authors then utilized a secondary adjustment for variables that should have been controlled by the randomization process. (11) This data is far from flawless. To think you can granularize such data and then extract meaningful outcomes is certainly an error in judgment. Such analysis should be reserved for secondary measures only after a more robust means of appraisal has proven fruitful.

Like all the stroke literature this leaves us trying to compare the soft endpoints of functional neurological outcomes to the hard endpoints of mortality and intracranial hemorrhage (ICH). Despite its success, like NINDS before it, MR CLEAN failed to demonstrate a mortality benefit for endovascular therapies in acute ischemic stroke. The mortality at 90 days was 21% and 22% respectively (15). Add to that a 5% increase in the rate of serious adverse events (47% vs 42%) in the endovascular therapy group. Despite the claim that the newer endovascular devices were safer and caused less bleeds the rate of clinically relevant ICH was statistically equivalent to the patients who received IV tPA alone (6.0% vs 5.2%) (15). This is the same rate of ICH seen in both the IMS-3 and Synthesis trials in which the MERCI retrieval devices were the primary means of clot retrieval (12,13). Furthermore there was a concerning increase in the rate of secondary ischemic strokes in a different vascular territory (5.6% vs 0.4%) and the number of hemicraniectomies performed (6.0 vs 4.9%) in the endovascular treatment group, though given the overall functional outcomes at 90 days were markedly improved in the endovascular therapy group these strokes may not be clinically relevant (15).

So why did endovascular interventions perform so much better in MR CLEAN than in any of the 3 trials that came before it? Was it the modern devices that create superior reperfusion with fewer complications? Interestingly the rate of recanulization in the intervention group at 24 hours was approximately 80% compared to 32% in the IV tPA group alone (15). When compared to the 24 hour recanulization rates in IMS-3 the intervention group were found to have approximately 80% with similar recanulizations rates in the IV tPA group as MR CLEAN (35%) (12). Furthermore the rates of ICH and secondary ischemic infarction seem to be no less than what was observed during IMS-3 and SYNTHESIS. Seemingly these newer devices add little as far as objective effectiveness. Was it time to reperfusion? Patients in MR CLEAN received both IV tPA administration as well as endovascular therapy incredibly fast. So fast that some may question the trial’s external validity. Despite the fact that patients in MR CLEAN underwent both IV and mechanical reperfusion significantly earlier than patients in IMS-3 and Synthesis, earlier treatment with endovascular therapy did not appear to improve outcomes (15). In fact in MR CLEAN, patients who received IV tPA therapy greater than 120 minutes after their symptom onset did better when randomized to the endovascular intervention arm. Conversely when patients received IV tPA prior than 120 minutes after symptom onset, endovascular therapy demonstrated no added benefit. In both IMS-3 and SYNTHESIS no temporal benefit could be demonstrated for patients receiving endovascular therapy (12,12). Was it the patients MR CLEAN selected that made a difference? Though MR CLEAN required CT angiographic proof of a large vessel occlusion, the resulting population seems very similar to the patients in IMS-3. The median age and presenting NIHSS was fairly similar (65-66 vs 68-69 and 17-18 vs 16-17 respectively) (12,15). Even the variation in stroke location was similar with the large majority of the clots located in the M1 segment of the middle cerebral artery (MCA), followed by a third found in the carotid artery terminus and a small minority found in the M2 segment of the MCA.

A few final thoughts of interest, the authors measured change in NIHSS at 24-hour and 1-week intervals. It will be interesting if these findings are expanded upon in the published document, but as far as I can tell from the data presented at the conference, the difference in NIHSS scores between the groups was 2.3 points at 24 hours and 2.9 points at 1 week. I cannot tell if this difference reached statistical significance but seemingly it is under the threshold of a 4-point improvement on the NIHSS that was deemed clinically relevant by the authors of NINDS in their original publication(1). If this data does prove to be accurate than it means that the anecdotal stories of patients rising from the cath lab table shortly after clot removal, was just that, anecdote. Finally it is important to point out that this trial compared endovascular treatment to standard care, which for all intents and purposes was IV tPA (91% of the control group received IV tPA). It is by no means certain that IV tPA provides any added benefit over placebo alone and some skeptics, such as myself, think there is a suggestion of harm. An additional control group, comparing placebo to both IV tPA and endovascular therapy is needed. In the subgroup analysis though endovascular therapy performed better than standard care in patients who received tPA, these benefits were not seen when IV tPA was withheld.

Surely we are left with more uncertainty than when we started this line of investigation. Thankfully there are a number of studies currently underway that may provide us the clarity we require. MR CLEAN is the first trial to demonstrate the potential benefits endovascular therapy may provide, but one trial should not define the standard of care, especially when multiple trials have concluded quite the opposite. The cost and resources needed to create an infrastructure capable of delivering patients to the endovascular suite with the swiftness seen in this cohort would be extraordinary. We should require more than an ambiguous odds ratio, bolstered by further needless statistical adjustments to justify these costs.

Sources Cited:

  1. Tissue plasminogen activator for acute ischemic stroke. The National Institute of Neurological Disorders and Stroke rt-PA Stroke Study Group. N Engl J Med. 1995;333(24):1581-7.
  2. Randomised controlled trial of streptokinase, aspirin, and combination of both in treatment of acute ischaemic stroke. Multicentre Acute Stroke Trial–Italy (MAST-I) Group. Lancet. 1995;346(8989):1509-14.
  3. Hacke W, Kaste M, Fieschi C, et al. Intravenous thrombolysis with recombinant tissue plasminogen activator for acute hemispheric stroke. The European Cooperative Acute Stroke Study (ECASS). JAMA. 1995;274(13):1017-25.
  4. Thrombolytic therapy with streptokinase in acute ischemic stroke. The Multicenter Acute Stroke Trial–Europe Study Group. N Engl J Med. 1996;335(3):145-50.
  5. Donnan GA, Davis SM, Chambers BR, et al. Streptokinase for acute ischemic stroke with relationship to time of administration: Australian Streptokinase (ASK) Trial Study Group. JAMA. 1996;276(12):961-6.
  6. Hacke W, Kaste M, Fieschi C, et al. Randomised double-blind placebo-controlled trial of thrombolytic therapy with intravenous alteplase in acute ischaemic stroke (ECASS II). Second European-Australasian Acute Stroke Study Investigators. Lancet. 1998;352(9136):1245-51.
  7. Clark WM, Wissman S, Albers GW, Jhamandas JH, Madden KP, Hamilton S. Recombinant tissue-type plasminogen activator (Alteplase) for ischemic stroke 3 to 5 hours after symptom onset. The ATLANTIS Study: a randomized controlled trial. Alteplase Thrombolysis for Acute Noninterventional Therapy in Ischemic Stroke. JAMA. 1999;282(21):2019-26.
  8. Clark WM, Albers GW, Madden KP, Hamilton S. The rtPA (alteplase) 0- to 6-hour acute stroke trial, part A (A0276g): results of a double-blind, placebo-controlled, multicenter study: Thrombolytic Therapy in Acute Ischemic Stroke Study investigators. Stroke. 2000; 31: 811–816.
  9. Hacke W, Furlan AJ, Al-rawi Y, et al. Intravenous desmoteplase in patients with acute ischaemic stroke selected by MRI perfusion-diffusion weighted imaging or perfusion CT (DIAS-2): a prospective, randomised, double-blind, placebo-controlled study. Lancet Neurol. 2009;8(2):141-50.
  10. Hacke W, Kaste M, Bluhmki E, et al. Thrombolysis with alteplase 3 to 4.5 hours after acute ischemic stroke. N Engl J Med. 2008;359(13):1317-29.
  11. Fransen PS, Beumer D, Berkhemer OA, et al. MR CLEAN, a multicenter randomized clinical trial of endovascular treatment for acute ischemic stroke in the Netherlands: study protocol for a randomized controlled trial. Trials. 2014;15:343.
  12. Broderick JP, Palesch YY, Demchuk AM, et al. Endovascular therapy after intravenous t-PA versus t-PA alone for stroke. N Engl J Med. 2013;368(10):893-903.
  13. Ciccone A, Valvassori L, Nichelatti M, et al. Endovascular treatment for acute ischemic stroke. N Engl J Med. 2013;368(10):904-13.
  14. Kidwell CS, Jahan R, Gornbein J, et al. A trial of imaging selection and endovascular treatment for ischemic stroke. N Engl J Med. 2013;368(10):914-23.
  16. Dipple et al. WSC-1158  Results of the multicenter randomized clinical trial of endovascular treatment for acute ischemic stroke in The Netherlands. The MR CLEAN Investigators. International Journal of Stroke. Volume 9, Issue S3 ,October 2014 Pages 16–40
  17. Sandercock P, Wardlaw JM, Lindley RI, et al. The benefits and harms of intravenous thrombolysis with recombinant tissue plasminogen activator within 6 h of acute ischaemic stroke (the third international stroke trial [IST-3]): a randomised controlled trial. Lancet. 2012;379(9834):2352-63.
  18. Saver JL: Novel end point analytic techniques and interpreting shifts across the entire range of outcome scales in acute stroke trials. Stroke 2007, 38:3055–3062.
  19. Banks et al. Outcomes validity and reliability of the modified Rankin scale: implications for stroke clinical trials: a literature review and synthesis. Stroke. 2007 Mar;38(3):1091-6. Epub 2007 Feb 1.

The Science (Fiction) of FOAM


If you want to know how we practiced medicine 5 years ago, read a textbook. If you want to know how we practiced medicine 2 years ago, read a journal. If you want to know how we practiced medicine last year, go to a (good) conference. If you want to know how we practice medicine now and in the future, listen to the conversations in the hallway and use #FOAMed.

                                                                                                                 – Joseph Lex, MD

What if ideas in their purest form possessed mass and energy? A subatomic structure with a specific resonance that dictated each idea’s physical properties. The power and influential reach determined not by the stature of those that spoke them, or the influences of the media agent that disperses them, but by the intrinsic nature of the ideas themselves. Ideas that when set to vibrate at the perfect frequency would propagate across worlds influencing all they touched.

What if a few insightful souls recognized the power of these ideas. Realizing they possess a mass and density of their own and as such have an inherent value. In an unequaled moment of altruism these visionaries decided that rather than imprison these ideas behind walls, restricting their access to those with the monetary means to afford their worth, they would spread them freely throughout the world. Allowing the intrinsic capabilities of each idea to determine the distance travelled. Harnessing technology they propagated these ideas across the globe.

These ideas and their newly defined substance then did something that for the past 200 years was thought to be impossible. They created new ideas…

Creating matter from nothing, they defied the Law of Conservation of Mass. Ideas begot ideas and a movement was born. It wasn’t until June 2012 in a pub in Dublin, Ireland over an appropriately inspirational pint of Guinness that FOAM was officially given its name, but it has been alive long before this. Long before Osler first opened the halls of McGill University for all to learn, before Hippocrates and his students published their Corpus, before even our ancient ancestors painted on the walls of caves on the Island of Sulawesi FOAM was there.

Each year for one week a physical manifestation of the FOAM movement is held. Though the geographic location fluctuates from year to year, the concept remains unchanged. It is a rallying point for all the ideas that have been released into the world. A beacon for those who champion these ideas. The organic amalgamation of the free open market of social media and the like-minded brilliance of practitioners who understand that above all, the sharing of knowledge is key. It is a celebration of FOAM, a movement that creates students, teachers, mentors, and most importantly friends. It is SMACC 2015.


Registration Opens November 5th/6th

The Case of the Anatomic Heart

16-3_staticOur obsession with diagnostic certainty has led us down many false paths and blind alleyways in the history of medicine. This statement has never been more true than when spoken in regards to cardiovascular health. The small successes that we have obtained when treating the highest acuity patients have been enthusiastically and incorrectly applied across the entire spectrum of coronary artery disease. Focusing too much on the anatomical definition of this disease state has limited our true understanding of the pathological process causing heart disease and in turn limiting our comprehension of how best to intervene. Despite a large body of evidence contradicting the theory, we have held fast to the “clogged pipe” model.

PCI found its initial success in the treatment of ST elevation myocardial infarctions, the most clinically obvious pathological end result of cardiovascular disease. In such cases we discovered that this invasive procedure was only slightly better than our systemic attempts to open the stenotic vessel using aspirin and thrombolytic therapy (1). In fact most data comparing PCI to thrombolytics in patients suffering from acute ST elevation MIs revealed that you had to treat close to 50 people with cardiac catheterization for one to benefit (1). Considering that thrombolytic therapy is only moderately better than aspirin alone, maybe the pedestal we have currently reserved for PCI in the management of ACS is not deserved (2).

The COURAGE trial, appropriately named for challenging the doctrine that coronary artery disease is best managed through invasive techniques, compared the efficacy of PCI vs “optimal” medical management in patients with stable coronary artery disease (3). The authors randomized patients with EKG evidence of ischemia at rest or ischemia induced by some form of provocative testing, with at least one culprit lesion of 70% occlusion or greater, to either PCI or medical management. Essentially the very patients we hope to identify through admission and provocative testing. No difference was found in the rates of death or MI during the follow up period (median 4.6 years) in the patients who received PCI vs those who underwent medical management (3).

These findings are consistent throughout the literature examining PCI vs medical management in patients with stable coronary artery disease. In a meta-analysis by Stergiopoulos et al of all 13 trials examining this question no difference could be found between medical management or aggressive interventional procedure (4). Even patients that are enzyme positive but otherwise clinically stable, no definitive benefits have been demonstrated with aggressive utilization of PCI. In fact when urgent PCI is empirically mandated, there is an increase in early mortality (5). In Emergency Department patients who have been ruled out for acute disease by EKG and enzymes, further evaluations for anatomic disease not only identify diminishingly small amounts of true positives but the interventions proposed do not result in clinically meaningful improvements in outcomes. Clearly we have overreached our meager successes and applied a crash procedure to a far different pathology than where it originally found it’s success.

This obvious lack of efficacy has not gone unnoticed. Many have suggested the need for a more refined method of identifying high risks lesions that would benefit from an invasive approach. Fractional Flow Reserve (FFR) is a technique that has been proposed as the answer to clarify which lesions would benefit from stent placement. This invasive technique is performed in concert with standard PCI and allows the interventionalist to assess the flow of blood before and after the stenotic lesion. These values are turned into a ratio in the hopes of numerically quantifying coronary flow. Anything under 0.80 is determined to be an ischemic stenosis and as such would benefit from the placement of a stent. Despite its physiologic plausibility, trials examining its efficacy have been less than stellar. The initial two studies, DEFER and FAME, comparing FFR-guided PCI to traditional PCI demonstrated a decreased rate of myocardial infarctions at 2 year follow-up (6,7). Initially these results seem to be in favor of FFR guided PCI but upon closer inspection the data reveals that the difference in the groups primarily consisted of a decrease in procedure related events. Suggesting that the only benefit FFR provides is to inhibit the ocular-stenotic reflex, quite prevalent in the modern Interventional Cardiologist (8). Neither of these studies address the important question, how does FFR-guided PCI compare to conservative medical management alone?

Introducing FAME-2. Like COURAGE before it, FAME-2 sought to answer the question whether FFR adds anything to medical management alone. The preliminary data was published in 2012 after the trials was halted prematurely (9), but the official 2-year follow-up results were recently published in the NEJM (10). Authors randomized patients with angiographic stentable lesions, with either classic anginal symptoms or positive findings on provocative testing after a negative ED workup, to either standard medical management or FFR-guided PCI. The authors utilized a composite endpoint of cardiovascular death, MI, or urgent revascularization. The trial was stopped early after enrolling only half its intended sample size, 1220 patients, due to an unacceptable number of events that occurred in the medical management group. Taken at face value this seems like an overwhelming approval of FFRs clinical utility. Long awaited proof that downstream testing after a negative ED workup results in clinically important benefits. A justification for the substantially large quantity of low-risk patients we admit to the hospital each day. Despite these seemingly positive results this trial does not justify our risk adverse strategy. Though there was a 11.4% absolute difference in the rate of primary events (8.1% vs. 19.5%) that occurred between the groups, this margin consisted entirely of an increased frequency of urgent revascularizations. There was no difference in the number of deaths or MIs that occurred between the groups. The majority of these excess revascularizations were due to persistent symptoms, demonstrating this claimed efficacy was primarily due to our biases rather than any overwhelming benefit of FFR-guided PCI.

Clearly FFR does not provide us with the clarity we seek. Even the theoretical ground FFR stands upon is thin as the ischemic threshold we currently use was derived by comparing FFR values to a gold standard of non-invasive perfusion imaging, a test with questionable clinical value (11). FFR may very well still play a role in the management of coronary artery disease, but its relevance in the management of ACS is insignificant.

How this changes the long-term management of coronary artery disease is unclear, but what is becoming increasingly apparent is an anatomic definition of coronary disease, following a negative Emergency Department work up for the diagnosis of ACS, provides no further clinical benefit. A number of trials have demonstrated that the addition of angiography or CT angiography add nothing to further risk stratify these patients (12-16). The rate of true positive disease in this cohort is diminishingly low (17). Even when the rare patient is found to truly have anatomically defined disease, direct invasive interventions add little clinical benefit over aggressive medical therapy. Anatomic investigation may very well remain an important component in the management of cardiovascular disease. Not to identify those patients that would truly benefit from cardiac catheterization, but to distinguish which patients require aggressive medical management. Surely this is not a priority in the Emergency Department evaluation of ACS.

More than ever we require a practical outlook when it comes to resource application in Emergency Medicine. Trying harder and doing more rarely lead to improved patient oriented outcomes. In the case of Emergency Department management of ACS it is imperative we admit that our current strategy has failed. We are striving to identify an exceedingly rare population in the hopes of offering an intervention which provides insignificant patient oriented benefits. Despite our technical mastery, technological advances, and intellectual mashinations, PCI remains a crash procedure that has only demonstrated proven benefit in the sickest cohorts of CAD. Outside the confines of ST- elevation MI we have yet to identify a population who consistently benefit from this invasive approach to management. Continually insisting on titling against the massive windmill that is Heart Diseae with a lance poorly equipped for this purpose, has led us too far down the path of madness. Surely its time to turn around and start the long walk back to sanity…

Sources Cited:

  1. Cucherat M, Bonnefoy E, Tremray G. Primary angioplasty ver-sus intravenous thrombolysis for acute myocardial infarction. Cochrane Database Syst Rev. 2000;2:CD001560.


  1. ISIS-2 (Second International Study of Infarct Survival) Collaborative Group. Randomised trial of intravenous streptokinase, oral aspirin, both, or neither among 17,187 cases of suspected acute myocardial infarction: ISIS-2.  Lancet. 1988;2(8607):349-60.


  1. Boden WE, O’rourke RA, Teo KK, et al. Optimal medical therapy with or without PCI for stable coronary disease. N Engl J Med. 2007;356(15):1503-16.
  2. Stergiopoulos K, Brown DL. Initial Coronary Stent Implantation With Medical Therapy vs Medical Therapy Alone for Stable Coronary Artery Disease: Meta- analysis of Randomized Controlled Trials. Archives of Internal Medicine 2012 Feb;172(4):312
  3. Mehta SR, Cannon CP, Fox KA, et al. Routine vs selective invasive strategies in patients with acute coronary syndromes: a collaborative meta-analysis of randomized trials. JAMA. 2005;293(23):2908-17.
  4. Pijls NH, van Schaardenburgh P, Manoharan G, et al. Percutaneous coronary intervention of functionally nonsignificant stenosis: 5-year follow-up of the DEFER Study. J Am Coll Cardiol 2007;49:2105-2111
  5. Tonino PA, De bruyne B, Pijls NH, et al. Fractional flow reserve versus angiography for guiding percutaneous coronary intervention. N Engl J Med. 2009;360(3):213-24.
  6. Bradley SM, Spertus JA, Kennedy KF, et al. Patient selection for diagnostic coronary angiography and hospital-level percutaneous coronary intervention appropriateness: insights from the national cardiovascular data registry. JAMA Intern Med. 2014;174(10):1630-9.
  7. De bruyne B, Pijls NH, Kalesan B, et al. Fractional flow reserve-guided PCI versus medical therapy in stable coronary disease. N Engl J Med. 2012;367(11):991-1001.
  8. De bruyne B, Fearon WF, Pijls NH, et al. Fractional flow reserve-guided PCI for stable coronary artery disease. N Engl J Med. 2014;371(13):1208-17.
  9. Pijls NH, De Bruyne B, Peels K, et al. Measurement of fractional flow reserve to assess the functional severity of coronary-artery stenoses. N Engl J Med 1996;334:1703-1708
  10. deFilippi CR, Rosanio S, Tocchi M, et al. Randomized comparison of a strategy of predischarge coronary angiography versus exercise testing in low-risk patients in a chest pain unit: in-hospital and long-term outcomes. J. Am. Coll. Cardiol. 2001;37(8):2042-2049
  11. Goldstein JA, Gallagher MJ, O’Neill WW, Ross MA, O’Neil BJ, Raff GL. A randomized controlled trial of multi-slice coronary computed tomography for evaluation of acute chest pain. J Am Coll Cardiol. 2007;49(8):863-71
  12. Goldstein JA, Chinnaiyan KM, Abidov A, et al. The CT-STAT (Coronary Computed Tomographic Angiography for Systematic Triage of Acute Chest Pain Patients to Treatment) trial. J Am Coll Cardiol. 2011;58(14):1414-22
  13. Hoffmann U, Truong QA, Schoenfeld DA, et al. Coronary CT angiography versus standard evaluation in acute chest pain. N Engl J Med. 2012;367(4):299-308
  14. Litt HI, Gatsonis C, Snyder B, et al. CT angiography for safe discharge of patients with possible acute coronary syndromes. N Engl J Med. 2012;366(15):1393-403
  15. Hermann LK, Newman DH, Pleasant WA, et al. Yield of routine provocative cardiac testing among patients in an emergency department-based chest pain unit. JAMA Intern Med. 2013;173(12):1128-33.


“The Adventure of the Sussex Vampire”

midline picture

A brief forethought. This post we will stray from the usual whimsical rants regarding recent literature in Emergency Medicine. Instead we will focus on the far more practical topic of the insertion of  the Midline catheter. Of note, I am overwhelmingly biased in favor of these devices and have taken such a fanciful liking to them I can’t possible be an objective critic. With this in mind…


The dichotomy that is venous access has become far more ambiguous since the establishment of ultrasound (US) to identify vascular targets. Prior to US, admission to the circulatory system was gained via superficial peripheral veins located by direct visualization, palpation or through central veins large enough to cannulate by blindly sticking a needle in the area of their anticipated anatomic location.

Since employing US to sonographically identify a deeper set of peripheral veins, the clear-cut boundaries that once separated central and peripheral access have become blurred. Not only has US improved our success in both these traditional techniques (1,2), it has introduced a new target for our blood hungry beveled needle tips to pursue. A larger set of peripheralmidline2 veins that were once too deep for direct visualization and too small for blind exploration now, thanks to US, have become an appealing target. To our surprise and dismay these deep peripheral lines are far less durable than their size and integrity would suggest (3). In fact, the rate of line failure within the first 24-hours (46%) is unacceptably high for clinical use (3,4).

This failure is due, more likely to a deficit in our equipment rather than a deficiency in these anatomic structures. Our current line of peripheral catheters is not designed to access such deep vessels. These catheters were intended to cannulate superficial veins. When employed on deeper veins they typically do not have adequate length to sufficiently seat the catheter tip in the vessels. This creates two problems. First the catheter will often become dislodged by even the smallest movement from the patient, as the elastic recoil of the soft tissue surrounding the precariously placed catheter pulls it from its target vessel. Second the steep trajectory taken to ensure the catheter reaches these vessels often results in the needle damaging the posterior wall of the vessel. This would not be of great importance if the catheter possessed the necessary length to thread beyond the damaged endothelium. Unfortunately even our long peripheral catheters lack the required length and end up sitting right next to this damaged portion of the vessels. These deficits have led to an abnormally high failure rate.

The deep venous or Midline catheters offer a viable solution to these obstacles. A number of recent studies have demonstrated the successful use of a small wire to thread a single lumen catheter into the deep veins of the upper extremity. This technique allows for secure access to these deeper vessels, avoiding the risks associated with central line insertion. These studies, examining the insertion of such lines, have confirmed their superior durability when compared to standard catheters and far fewer line related infections than observed with central venous catheterization(7).

The most recent of these trials, by Meyer et al, examines the use of arterial catheters inserted into either the cephalic or basilic veins (5). In this study’s participating hospital it was routine for the ICU to provide “line consultations”, during which the Critical Care physician would be called to the ward to obtain venous access on particularly difficult patients. Difficult access was defined in this cohort as three failed attempts to insert a peripheral line by an experienced nurse. After which all lines were inserted by a single operator, the study’s second author, Dr. Pierrick Cronier, using either 18 or 20 gauge arterial catheters that were 8 to 11 cm in length. Catheters were placed using the Seldinger technique under full aseptic conditions.

All 29 lines were placed successfully, the majority in the basilic vein (66%) and the remainder in the cephalic vein (34%). Only three catheters were removed early. One was accidently removed by the patient up until which point it had been functioning normally. The remaining two catheters were removed due to absence of blood return and were found to be occluded. Two additional catheters were found to be colonized with coagulase.  Using ultrasound, no thrombophlebitis was visualized on any catheter prior to their removal.

The small sample size and use of a single skilled operator limit the conclusions that can be drawn from such a study and thus this trial does very little to answer the more pertinent questions Emergency Physicians have regarding the use of Midlines.

What is the optimal catheter for Midline insertion?

In the Meyer et al cohort the authors studied catheters intended for arterial use (5). In earlier cohorts both Elia et al and Mills et al employed single lumen central venous catheters of varying sizes (12 and 15 cm respectively) with equal success. While others have used catheters specifically designed for Midline insertion (3,6,7), no one study directly compares the various catheter choices, but all demonstrate similar efficacy and safety profiles in their independent cohorts. There is a Goldilocks effect in the sense that the longer the catheter inserted the greater the durability of the line, and yet if the catheter tip extends proximally enough to be seated in the subclavian vein, the rate of catheter related infections approaches numbers associated with the use of central line catheters (8). Seemingly no one catheter type appears superior to any other. It is important to remember that unlike central lines we are inserting catheters into much smaller, thin walled vessels and thus should choose a catheter insertion kit nimble enough to navigate such delicate structures.

Can vasopressors be safely administered through Midline catheters?

Most of the trials examining Midline catheters focused on the rate of successful insertion and line safety. All of these trials examining Midlines treated them as if they were peripheral lines (3,4,5,6,7), and as such there is no specific evidence evaluating the safety of administering vasopressor medication. This lack of evidence does not invalidate their use. The mostmidline3 commonly cited concern is that due to the depth of these venous structures, a delay in recognition of an infiltrative event may occur causing significant damage before the infusion could be stopped. This would be a valid concern except that unlike their more superficial cousins, Midlines very rarely infiltrate. When compared to traditionally inserted peripheral lines, Midlines fail far less often and in far different ways. Peripheral lines tend to infiltrate or become dislodged because of the short distance between insertion site and distal catheter tip in conjunction with the delicate nature of the vessels. Conversely Midlines fail later in their course, primarily due to distally located occlusions. The failure rate of Midline catheters is approximately 14% with a median time to failure of 6.19 days (3). In all the cohorts examining the insertion and use of Midlines only two infiltrative events occurred. In Mills et al, this event transpired directly after a difficult insertion performed by one of their less experienced practitioners (6). In El-Shafey et al, a single Midline catheter infiltrated shortly after its insertion (4). Both of these events occurred soon after insertion and quickly became clinically obvious. The much feared “occult” infiltration, has yet to manifest in any cohort examining the use of Midline catheters. That being said it is important to note that all Midlines are not created equal. The small tortuous vein in which one experiences great difficulty threading a catheter is a far different line than a large easily compressible vein that threads easily with adequate blood return.

Finally the generalizability of these trials is limited by the expertise of the practitioners inserting these lines. The majority of these trials called upon a few experienced practitioners to perform each catheterization. Only one trial, Elia et al, utilized a variety of practitioners (attendings, residents and nurses) with varying levels of experience (3). This variability is reflected in the lower success rate when compared to similar cohorts (86% vs 93% and 100%) (5,6). From my personal experience there is a learning curve when first beginning to insert these types of lines. The delicate act of threading the wire is far more difficult than the insertion of a central line. Because of the small size of these vessels there is a greater likelihood for the tip of the needle to become dislodged when detaching the syringe. Once this skill is perfected the placement of the lines becomes far simpler.

Our threshold for changing practice is frustratingly fickle. We have accepted that the use of US to identify deeper peripheral vessels will both improve peripheral line insertion and decrease the need for central line placement. Yet our success is limited by our use of traditional techniques and unsuitable equipment neither of which were intended to cannulate such deep vasculature. Likewise we incorrectly apply the rules that govern superficial peripheral vasculature to these deeper more durable vessels. In order to optimize our success with US guided peripheral access, it is imperative we realize these vessels are unlike their more superficial brethren and we must adapt our ideology, methods and tools accordingly.

Sources Cited:

 1. Leung J, Duffy M, Finckh A. Real-time ultrasonographically-guided internal jugular vein catheterization in the emergency department increases success rates and reduces complications: a randomized, prospective study. Ann Emerg Med. 2006;48(5):540-7.

2. Costantino TG, Parikh AK, Satz WA, Fojtik JP. Ultrasonography-guided peripheral intravenous access versus traditional approaches in patients with difficult intravenous access. Ann Emerg Med. 2005;46(5):456-61.

3. Elia F, Ferrari G, Molino P, et al. Standard-length catheters vs long catheters in ultrasound-guided peripheral vein cannulation. Am J Emerg Med. 2012;30(5):712-6.

4. Eid Mohamed El-Shafey, Tarek F. Tammam. Ultrasonography-Guided Peripheral Intravenous Access: Regular Technique Versus Seldinger Technique in Patients with Difficult Vascular. European Journal of General Medicine. 2012; Vol. 9, No. 4 .

5. Meyer P, Cronier P, Rousseau H, et al. Difficult peripheral venous access: Clinical evaluation of a catheter inserted with the Seldinger method under ultrasound guidance. J Crit Care. 2014;29(5):823-7.

6. Mills CN, Liebmann O, Stone MB, Frazee BW. Ultrasonographically guided insertion of a 15-cm catheter into the deep brachial or basilic vein in patients with difficult intravenous access. Ann Emerg Med. 2007;50(1):68-72.

7. Mermel LA, Parenteau S, Tow SM. The risk of midline catheterization in hospitalized patients. A prospective study. Ann Intern Med. 1995; 123:841-4.

8. Kearns PJ, Coleman S, Wehner JH. Complications of long arm-catheters: a randomized trial of central vs peripheral tip location. JPEN J Parenter Enteral Nutr. 1996;20(1):20-4.

A Case of Shadows


In medicine we frequently propagate half-truths and unsubstantiated certainties. Thus, truth is a relative experience, dependent primarily on how we choose to define it rather than any concrete state of reality. Increasingly we have favored a technological definition of truth over that of the clinical perspective. As such we are driven to act in disease states that are often best treated by blissful ignorance. Where we draw the line of clinical relevance and subclinical disease seems dependent on our own comfort with uncertainty. Given this current culture, it is not surprising that bedside ultrasound (US) has become a popular tool to evaluate the majority of ailments that may show up in the Emergency Department. With our expanding technical skills, so to has our comfort in using this modality to make clinical decisions. At this point, such a level of technical proficiency has been achieved that we have outpaced the literature base to guide these decisions. Until recently the majority of the literature addressing bedside US has been limited by its use of surrogate endpoints and disease oriented definitions of success. Thus we stand at a crossroads in Emergency Medicine. This is not intended to discredit bedside US as a modality but rather a commentary on its user, and our inability to separate clinically relevant reality from the pixilated truth we see on our monitors. To ask the question, how exactly should we determine our sonographic definition of truth?

A recent article published in The Lancet Respiratory Medicine, by Laursen et al, is the first randomized controlled trial examining the utilization of bedside US effects on patient outcomes (1). Up until the publication of this article, the efficacy of US was evaluated through studies addressing its diagnostic accuracy. US was compared to a more traditional diagnostic tool often using an impossible gold standard. In many cases US proved comparable or even superior to the traditional diagnostic modality. These types of studies helped us define the potential utility of bedside US, but we have outgrown these humble beginnings. What is now required are trials examining the patient centered effects of the incorporation of bedside US into our practice.

The findings of the Laursen trial were covered in more detail in my previous post found on EM Literature Of Note and examined in an even more expert fashion by Simon Carly on The St. Emlyn’s blog. I have included an excerpt from my post as a summation of these findings:

Authors randomized patients presenting to the ED with signs or symptoms concerning for a respiratory etiology to either a standard work up as determined by the treating physician or the addition of POCUS performed by a single experienced operator. The US protocol consisted of sonographic examination of the heart, lungs and lower extremity deep veins to identify possible causes of patients’ symptoms. The authors’ primary outcome was the percentage of patients with a correct presumptive diagnosis 4 hours after presentation to the Emergency Department as determined by two physicians blinded to ED POCUS findings, but with access to the records of the entire hospital stay.

Using this POCUS protocol the authors found stunning success in their primary endpoint. Specifically, the rate of correct diagnoses made at 4-hours in the POCUS group was 88% compared to 63.7% in the standard work up group. Furthermore 78% of the patients in the POCUS group received “appropriate” treatment in the Emergency Department compared to 56.7% in the standard work up group.

Though promising, these benefits did not translate into improvements in true patient oriented benefits. Though not statistically significant, the observed in-hospital and 30-day mortality trended towards harm in the POCUS arm (8.2% vs 5.1% and 12% vs 7% respectively). Nor was there any meaningful difference in length of stay or hospital-free days between those in the POCUS group and those in the control group. Even more concerning, was the significant increase in downstream testing that occurred in patients randomized to the POCUS group. Specifically the amount of chest CTs (8.2% vs 1.9%), echocardiograms (10.1% vs 3.8%) and diagnostic thoracocenthesis (5.7% vs 0%).

It is important to note the pathologies found in the POCUS group were not false positives. These patients had additional diagnostic tests confirming the validity of the bedside findings. As such this is not a question of technical competency, but rather a question of clinical relevancy. The significant increase in diagnostic proficiency found in the POCUS group did not result in improved patient oriented outcomes, in fact there were significant trends towards harm in both hospital and 30-day mortality. This, of course, may be statistical whimsy. Future trials may show this to be nothing more than the random noise generated by a small sample size , but these findings are concerning for a certain degree of overdiagnosis.

The Laursen trial is not a solitary signal standing out from a crowd of contrary data. There have been signs throughout the US literature demonstrating the potential for over-diagnosis and though not definitive this study certainly supports this hypothesis. When US is compared to CXR for the diagnosis of pneumonia, it reveals far more pathology (2). Does this mean we have been missing a large portion of pneumonias in otherwise well appearing patients or is this an example of overdiagnosis. Likewise US is a far more sensitive modality for identifying pneumothoraxes when compared to CXR (3). And yet like pneumothraxes that are discovered on CT but not seen on CXR, there is question of whether such lesions require any intervention at all. What we do with this information is hard to say. None of these trials are robust enough to draw definitive conclusions. Despite their many flaws surely we can no longer say with overwhelming certainty that ultrasound is free and harmless. As with any other test it is only as good as the practitioners who use it.

A recent article by Kenji et al, published in The Journal of Critical Care, revealed bedside US to be a far more successful tool when used to guide care (4). These authors, utilizing a before and after design, examined the use of bedside echocardiography (echo) to guide resuscitative strategies in ICU patients presenting with pressor-dependent shock. Patients were prospectively evaluated over a 1-year period, the first 6-month being the standard care group and the following 6-month the echo guided group. The standard care group used the “Surviving-Sepsis-Protocol” to guide resuscitation, while the echo-guided group followed a protocol involving evaluation of cardiac function and ICV collapsibility. Echo evaluations where conducted by one of three intensivists with expertise in the use of bedside echocardiography. None of the physicians performing the echo exams were the primary physicians caring for the patients, but rather made recommendations based off their findings. These recommendations were consistent with one of four scenarios:
1. If LV function was normal and IVC full, fluid was stopped and pressors continued
2. If LV function was normal and IVC was collapsible, a fluid bolus of 20-40 ml/kg was administered
3. If LV function was impaired and IVC was collapsible, 10-20 ml/kg was administered and dobutamine was initiated
4. IF LV function was impaired and IVC was full, fluid was restricted and dobutamine was initiated.

The primary outcome the authors examined was 28-day mortality. Secondary endpoints measured were the amount of fluid administered over the first four days of treatment, organ dysfunction and days free of renal replacement therapy. A total of 220 patients were examined (110 in the standard therapy group and 110 in the echo-guided group). The vast majority of the patients evaluated were in vasodialatory shock, followed by a small minority in cardiogenic shock and a handful of patients in mixed or hemorrhagic shock.  25% of the patients in the echo-guided group were found to have severely impaired left ventricular function. Only 35% were deemed to require fluid augmentation as determined by IVC collapsibility. As such, patients in the echo guided group received significantly less fluid over the first day of therapy (49 ml/kg vs 66 ml/kg) and were more likely to be started on dobutamine therapy than those in the standard care group (22% vs 12%).

28-Day mortality was 66% vs 56% in the standard and echo guided groups respectively. This 10% difference reached statistical significance with a P-Value of 0.04. Furthermore patients in the echo-guided group had a more days free of renal replacement therapy (RRT) and less grade 3 acute kidney injury (AKI).

This trial is by no way without its limitations. The before and after design and small sample size, not to mention the questionable efficacy of dobutamine, limit the strength of the conclusions that can be drawn. Despite these drawbacks, like the Laursen et al trial, the Kenji trial sets an important precedence in the US literature. Rather than examining US’s utility using a surrogate disease oriented endpoint both of these trials investigated the effect US had on patient oriented outcomes, specifically mortality.
Though these two trials are examining to very different aspects of bedside ultrasonography, their distinction serves to illustrate our point appropriately. In the Laursen et al trial all patients presenting with respiratory signs or symptoms underwent a protocolized ultrasonographic investigation independent of individual presentations. This shotgun distribution of sound waves is the equivalent of throwing a bunch of labs at a belly pain patient and seeing what sticks. Finding something on US and then retrospectively fitting the patients to these findings will inevitably lead us down many false paths. Kenji et al also used a standardized protocol, but unlike the Laursen trial, they asked a specific clinical question pertinent to the patient’s presentation and used US to answer this question.

As with any form of testing, the acuity of the patient and the pretest probability of disease determine the performance of the investigation. Even the most specific tests, if used on the wrong population will identify more false positives than true disease. It is my belief that bedside US is even more susceptible to these conditional circumstances. In the crashing trauma patient US becomes an invaluable tool to swiftly rule out tension pathology as the cause of the physiological insult (3). Conversely when used in a patient with a more clinically benign presentation the high sensitivity we so recently relied on becomes a detraction as it is now is prone to finding pneumothoraxes of little clinical relevance. Overall the sensitivity of US in the identification of appendicitis is fair, but as the disease process progresses and the clinical suspicion increases the sensitivity of the test becomes far more clinically useful (5). The EFAST Exam when applied to patients with traumatic injury has a poor sensitivity for identifying injury (6,7), but when used to identify the cause of a crashing trauma patient’s hypotension it is clinically invaluable (8). Interestingly in the hypotensive patient where the pretest probability of clinically relevant pathology is extremely high, the potential for overdiagnosis from empirically applying standardized screening protocols such as the EFAST or RUSH exam becomes much less relevant.

How do we move forward? US has been traditionally examined as a diagnostic test, meaning its utility is routinely compared to a gold standard. US studies of pneumonias, pneumothoraxes, appendicitis, or peritoneal injury are commonly evaluated against CT. Bedside echo is typically compared to comprehensive echocardiography as interpreted by an “expert Cardiologist”, and measurements of fluid responsiveness are likened to invasive hemodynamic monitoring. Each of these gold standards possesses their own flaws. CT scans are prone to overdiagnosing (3,4), Cardiologists disagree with each other as often as they disagree with the Emergency Physicians when diagnosing heart failure (9), and invasive hemodynamic measurements used to judge US’s ability to assess fluid responsiveness have not shown to improve patient oriented outcomes when examined clinically(10). We need to utilize patient relevant outcomes when evaluating the use of bedside US in order to assess its true value as a diagnostic tool. Future research should randomize patients with US+, CXR- pneumonias to antibiotic therapy or placebo, compare conservative management to chest tube insertion in patients found to have pneumothoraxes on US but not CXR, and assesse fluid responsiveness in the hemodynamically volatile patient by examining mortality outcomes when US findings are used to guide therapy.

It is an exciting time in the world of point-of-care US. There are great minds with extraordinary vision pushing this field forward everyday. It is a privilege to experience this progression. But as technology advances and the quality of our point-of-care machinery improves, overdiagnosis will become an ever more imperative concern. If we choose to stick our heads in the sand, holding fast to unquestionable certainty found in our pareidolic interpretation of shadows, we will surely redefine medical truth for the worst. Like CTPA once changed the diagnosis of pulmonary embolism from a clinically relevant dangerous disease to a primarily irrelevant disease oriented definition, point-of-care US will identify a large quantity of subclinical disease of questionable clinical bearing. Conversely, if we choose to continue to question the proper application of point-of-care US and focus not only on our procedural expertise but on our medical stewardship we will progress the field of bedside US and improve patient care. If we are to claim clinical expertise our knowledge must extend beyond the technical proficiencies and integrate the wisdom needed to interpret these shadows?

Sources Cited:


  1. Laursen et al. Point-of-care ultrasonography in patients admitted with respiratory symptoms: a single-blind, randomised controlled trial The Lancet Respiratory Medicine – 1 August 2014 ( Vol. 2, Issue 8, Pages 638-646
  2. Bourcier et al. Performance comparison of lung ultrasound and chest x-ray for the diagnosis of pneumonia in the ED. Am J Emerg Med. 2014;32(2):115-8.
  3. Alrajab et al. Pleural ultrasonography versus chest radiography for the diagnosis of pneumothorax: review of the literature and meta-analysis. Crit Care. 2013;17(5):R208.
  4. Kanji et al. Limited echocardiography-guided therapy in subacute shock is associated with change in management and improved outcomes. J Crit Care. 2014;29(5):700-5.
  5. Bachur et al. The effect of abdominal pain duration on the accuracy of diagnostic imaging for pediatric appendicitis. Ann Emerg Med. 2012;60(5):582-590.e3.
  6. Quinn et al. What is the utility of the Focused Assessment with Sonography in Trauma (FAST) exam in penetrating torso trauma?. Injury. 2011;42(5):482-7.
  7. Becker et al. Is the FAST exam reliable in severely injured patients?. Injury. 2010;41(5):479-83.
  8. Laselle et al. False-negative FAST examination: associations with injury characteristics and patient outcomes. Ann Emerg Med. 2012;60(3):326-34.e3.
  9. Januzzi et al. The N-terminal Pro-BNP investigation of dyspnea in the emergency department (PRIDE) study. Am J Cardiol. 2005;95(8):948-54.
  10. Harvey et al. Assessment of the clinical effectiveness of pulmonary artery catheters in management of patients in intensive care (PAC-Man): a randomised controlled trial. Lancet. 2005;366(9484):472-7.

A Secondary Analysis of the Adventure of the Crooked Man


Removing a cervical collar in the early aftermath of a traumatic injury is becoming an increasingly difficult task. With ever more sensitive imaging modalities we have progressively devalued the traditional methods used to evaluate the integrity of the spinal column in favor of more technologically advanced ones. Despite decades of success in treating this pathology, and clear evidence that clinically relevant spinal injuries present with obvious clinical signs, we have let anecdotal evidence get the best of us. With this in mind, we now turn to the enigma that is the neurologically intact patient with persistent midline tenderness with no evidence of pathology on cervical CT.

As we concluded in our previous post, in the neurologically intact patient with persistent midline tenderness, MRI identifies far more injuries than CT. In a cohort of 178 prospectively gathered patients with isolated persistent midline tenderness and a negative CT, Auckland et al reported 78(44%) with injuries identified on MRI (1). Although the majority required no intervention, 33(18.5%) required use of a collar and 5(2.8%) required surgical management. These findings taken at face value are concerning to say the least, and do not fit with our clinical experience. In fact there is reasonable evidence demonstrating this increased signal found on MRI is merely the noise of an overly sensitive test applied to an extraordinarily low risk population. MRI is prone to overcalling pathology. Even a surprising number of asymptomatic healthy controls, with no history of acute trauma, will have radiologically significant pathology found on MRI (2). Furthermore when findings on MRI are compared to the injuries identified during surgical exploration, MRI demonstrates a propensity for identifying lesions where none exist (specificities ranging from 59.0 to 80.5%) (3,4). Given this, it no longer seems appropriate to consider MRI the gold standard for defining disease in acute spinal trauma. Rather we should examine clinical follow-up and functional patient oriented outcomes. Simply put, what would happen to these patients if we just left well enough alone?

A recent article published in JAMA Surgery by Resnick et al attempted to examine this very question (5). The authors investigated the utility of MRI in patients with persistent midline tenderness or sensory deficits and normal CT findings. Only instead of using MRI as the gold standard they used the patients’ discharge diagnosis. In this prospectively gathered cohort the authors included all patients with a GCS of 15, who were not intoxicated, and had no distracting injuries. Of the 830 patients included in this trial, 164 (19.8%) had cervical spine injuries. 23 (2.8%) of these were deemed clinically significant, all were identified on the initial CT scan. Only 15 (2.2%) of the patients had injuries identified exclusively on the MRI, none of which were deemed clinically relevant.

Unfortunately due to the pragmatic nature of this trial, not all patients received an MRI. The decision was left up to each individual treating physician. Ultimately 100 of the 830 patients received an MRI during their hospital stay. The most common reasons an MRI was ordered were equivocal findings on CT followed by persistent midline tenderness, or sensory deficits concerning enough for the treating physician to require further investigations. Similar to the Ackland study, 46% of the patients who underwent MRI imaging were found to have additional findings that were not seen by CT. The majority of these were ligamentous and soft tissue injuries and none altered clinical management. Like the Ackland study, the MRI identifies far more pathology, very little of which is clinically relevant.

Compared to MRI, CT was 90.9% (CI from 85.3-94.8%) sensitive for identifying cervical spine injury. When discharge diagnosis was used as the gold standard, Resnick et al assert 100% sensitivity and specificity for diagnosing clinically important cervical spine injuries. Unfortunately long term follow-up to test the validity of these findings was not performed. Nor were there a sufficient number of patients with serious cervical injuries in this cohort to claim 100% sensitivity with any certainty (Confidence interval as low as 85.1%). A total of 5 patients were discharged home wearing C-collars for comfort, the rest of the patients had their collars removed before discharge. Of the patients with negative CTs and persistent midline tenderness, removing the collar prior to discharge did not result in catastrophic injury. There were not any reports of patients readmitted to these medical centers with obvious cervical spinal injuries. We are unable to determine how these patients did in the short term after discharge. There may, though unlikely, have been a catastrophic injury missed that presented to a different hospital. It is also unclear if any minor injuries that may have benefited from earlier intervention went undetected, though this later scenario is even less likely as C-collar use for comfort has for the most part been debunked as a useful therapy (6).

How we use this information is still not entirely clear. All midline tenderness is not created equal. There is a certain degree of clinical judgment that should be applied when evaluating these patients. Maybe patients with persistent tenderness who are unable to actively range their necks through 45 degrees of rotation (a retrospective application of the Canadian S-Spine Rule) are more concerning. Maybe those with bilateral paresthesia are those who merit further investigation. Maybe, like the Ackland study demonstrated, patients with severe cervical spondylosis on CT scan cannot be cleared by this modality. Performing MRIs on the majority of these patients will lead to a significant increase in pathological diagnoses. Most of these will be of little clinical significance and the few true positives are likely to reveal themselves clinically during the patients stay in the Emergency Department. If we insist on imaging all patients with persistent pain or tenderness, we risk exposing a group of patients, the large majority of which are without true clinical disease, to potentially harmful interventions. Some will be asked to follow-up with spine surgeons for further downstream testing. Some will be given a hard collar for 10 weeks and exposed to all the associated morbidity. Others will be exposed to surgical procedures that may very well not be clinically required. All will be turned into patients, given a label, diagnosed with a disease that’s major determinants of long term prognosis are patients’ mental well being and financial security (7).

We live in a world of ever advancing medical technology. A world where the boundaries between states of disease and health are becoming increasingly less defined. It is easy to demonize non-specific laboratory investigations like D-Dimer or procalcitonin for their intellectual dishonesty. Likewise the CT scan is an equally natural scapegoat because of its accessibility and the obvious concerns of radiation. Although each of these culprits are responsible in their own way for the crisis we currently face, the real perpetrator of overdiagnosis is information and the ambiguity it hurls at us. We have clearly demonstrated that modern medicine in its current form is incapable of standing idle. Our desire to act far overwhelms our powers of reason. Though the current data cannot definitively negate the utility of MRI in the neurologically intact patient with persistent midline tenderness, we can say its indications are few and far between. Used empirically it will surely lead to far more harm than good.

Sources cited:

  1. Ackland HM,Cameron PA,Varma DK, et al.Cervical spine magnetic resonance imaging in alert, neurologically intact trauma patients with persistent midline tenderness and negative computed tomography results. Ann Emerg Med. 2011 ; 58 : 521 – 30.
  2. Anderson, S et al Are there cervical spine findings at MR imaging that are specific to acute symptomatic whiplash injury? A prospective controlled study with four experienced blinded readers. Radiology. 2012 Feb;262(2):567-75. doi: 10.1148/radiol.11102115. Epub 2011 Dec 20.
  3. Rhin, J et al. Using Magnetic Resonance Imaging to Accurately Assess Injury to the Posterior Ligamentous Complex of the Spine: A Prospective Comparison of the Surgeon and Radiologist. J. Neurosurgery Spine. 12;391-396
  4. Rhin, JA et al. Assessment of the Posterior Ligamentous Complex Following Acute Cervical Trauma. J Bone Joint Surg Am. 2010 Mar;92(3):583-9.
  5. Resnick S et al. Clinical Relevance of Magnetic Resonance Imaging in Cervical Spine Clearance: A Prospective Study. JAMA Surg. Published online July 30, 2014.
  6. Verhagen AP et al. Conservative treatments for whiplash. Cochrane Database of Systematic Reviews 2007, Issue 2
  7. Outcomes at 12 Months After Early Magnetic Resonance Imaging in Acute Trauma Patients With Persistent Midline Cervical Tenderness and Negative Computed Tomography. SPINE.  2013; Volume 38, Number 13:1068–1081.

“The Adventure of the Red-Headed League”

pic1A peasant traveling home at dusk sees a bright light traveling along ahead of him. Looking closer, he sees that the light is a lantern held by a ‘dusky little figure’, which he follows for several miles. All of a sudden he finds himself standing on the edge of a vast chasm with a roaring torrent of water rushing below him. At that precise moment the lantern-carrier leaps across the gap, lifts the light high over its head, lets out a malicious laugh and blows out the light, leaving the poor peasant a long way from home, standing in pitch darkness at the edge of a precipice.

                                            -Welsh tale describing Will-o-the-Wisp


So much of what we do in Emergency Medicine is translating shades of grey into dichotomous patient oriented decisions. Truth in medicine is a fluid, tenuous state, very rarely encountered in the chaos of the Emergency Department. More often than not we are forced to act in varying states of uncertainty. Naturally we search out specific data points in this fog of ambiguity that we believe will provide guidance through the unknown. And yet, some of these beacons are just as likely to lead us astray as they are to provide safe passage.

One such variable is a history of loss of consciousness (LOC) in a patient suffering from a minor head trauma. Despite a multitude of contradictory data, LOC has persisted in the mind of the practitioner (often times in isolation) as a relevant branch-point in deciding who does and does not require further downstream investigations (2). The most recent excavation of the PECARN dataset, published in JAMA Pediatrics, should serve to remind us that just because a variable is found to have a statistical association to the endpoint in question, this does not necessarily mean it is a useful factor to guide clinical decision- making (2).

In this latest dive into the PECARN dataset, Lee et al set out to examine how influential LOC was in predicting clinically significant traumatic brain injury (ciTBI). In the original derivation and validation cohort, by Kupperman et al, LOC was identified as one of the six variables with a strong enough predictive value to be included in the formal decision rule (1). The original PECARN data set was a mammoth undertaking, which prospectively evaluated 42,412 pediatric patients presenting to the Emergency Department after experiencing a minor head injury. Of this group only 780 patients (1.8%) were found to have any evidence of TBI on CT. Only 376 (0.9%) of these patients had injuries of clinical relevance, of which only 60 patients (0.14%) required any form of neurosurgical intervention. Given this extremely low rate of ciTBI, one could argue that the PECARN authors had already identified a cohort of patients at incredibly low risk for relevant injury and any further risk stratification would be futile. Despite this the original authors derived and internally validated two age specific (< 2 years old and> 2 years old) decision rules that boasted negative predictive values of 100% and 99.95% respectively. This data set remains the most robust clinical decision rule derived to date in the pediatric population despite lacking sufficient external validation, incomplete follow up (1/5 of the 64.7% of the patients who did not undergo definitive testing were lost to follow-up), and the fact that the rule was outperformed by physician’s unstructured judgment (1).

Lee et al sought to improve, at least conceptually, on the diagnostic characteristics of the PECARN decisions rules by addressing the added value isolated LOC provides in identifying patients with ciTBI. The authors defined isolated LOC in two specific fashions. In one, termed PECARN-isolated LOC, they identified patients who experienced LOC without any of the other factors that make up the PECARN decision rules. The second utilized the expanded definition of LOC, which included predictors from other commonly used decision rules for head injury (Nexus 2, the New Orleans criteria, and the Canadian head CT rule). It is important to note that the expanded definition of LOC did not include mechanism of injury as a relevant predictor of ciTBI (2).

Of the 42,412 patients, 6,286 (15.4%) were found to have suspected or confirmed LOC. An interesting side note was that out of the 6,286 patients with LOC, 5,010 had a head CT performed, the majority of which the treating physician recorded the history of LOC as being the primary reason for the scan (demonstrating that even in this cohort LOC was considered a clinically important factor for predicting injury). Of the patients with a history of LOC, PECARN-isolated LOC was present in 2,780 (47.5%) patients. In the subgroup of patients with PECARN-isolated LOC, the incidence of TBI on CT was 1.9% and the incidence of ciTBI was 0.5%.  Unfortunately the expanded definition of isolated LOC was far less useful as only 576 (9.4%) of patients with LOC met its’ criteria, most likely do to the inclusion of “any traumatic scalp findings” as a relevant predictor. Of those that did meet these impossible standards, only 0.9% were found to have TBI on CT and 0.2% of these patients had a clinically relevant injury. In the PECARN cohort if LOC was used independently as a decision point for head CT, the sensitivity and specificity of identifying ciTBI would be 49.5% and 85.4% respectively. Clearly not the beacon of light we presume.

What is important to remember is that a statistically significant odds ratio found by using a multifactorial regression model does not directly translate into a clinically useful predictor. Multifactorial regression in all its forms is a statistical attempt to isolate the effect of one variable’s ability to predict the outcome in question. Essentially it is the graphical illustration (the slope of the line indicating the strength of the association) of how one variable affects another while a mathematical attempt is made to control for other factors (3). Despite its statistical authority, finding an independent association between a variable and the outcome in question is not the same as studying a group of patients otherwise well with the exception of the variable in question (LOC for example). Moreover the odds ratio that is typically reported as the result of a multifactorial regression model does not intuitively explain the clinical relevance of this correlation (3).

The utility of isolated LOC for predicting clinically significant TBI seems to have undergone this very mathematical augmentation. Although LOC has consistently demonstrated a statistically independent association with ciTBI, when applied clinically in patients with isolated LOC its predictive value is minimal. During the derivation cohort of the Canadian head CT rule Steill et al found LOC was independently associated with ciTBI (4). However when used clinically they found only 0.4% of patients with LOC had a clinically relevant ciTBI requiring intervention, and most of these could be identified simply by assessing the patient’s mental status in the ED (5). In the NEXUS 2 cohort, LOC was identified as a predictor of ciTBI but failed to maintain clinical relevance when assessed using a multifactorial model (6). Additionally if LOC was used to decide which patients in this cohort would receive further imaging it would have resulted in a sensitivity and specificity of 48% and 63% respectively (6).  In the original PECARN cohort the predictors that identified the bulk of the patients with ciTBI were altered mental status (AMS) or clinically obvious signs of skull fractures. These factors alone identified the bulk of patients with ciTBI. If patients did not present altered or with obvious signs of skull fracture, then their risk of ciTBI was incredibly low (0.9% in the under 2 years old group and 0.8% in the over 2 years old group). The remainder of the predictors found in the PECARN decisions rules, including LOC, did very little to further risk stratify patients (1).

What this can be reduced down to is our fear of the clinically occult head bleed. Based on the idea that the skull is a lead box blocking the transmission of potential chaos within from our external eye until it’s too late to intervene. This fear is driven by anecdote passed down from attending to resident in some form of modern-day oral history. Clearly these stories are not supported by the literature and the reality is these cases of clinically occult intracranial bleeding are rare and often identifiable by high-risk features (elderly, anticoagulant use, etc). A history of LOC in an otherwise well-appearing patient provides us with little guidance in identifying these rare cases. Moreover the lack of LOC does not safely eliminate the risk of significant injury. Often times its absence will give us a false sense of security and like the solitary peasant, lead us far from home, standing in pitch darkness on the edge of a cavernous precipice…


Sources Cited:

  1. Kuppermann  N, Holmes  JF, Dayan  PS,  et al; Pediatric Emergency Care Applied Research Network (PECARN).  Identification of children at very low risk of clinically-important brain injuries after head trauma: a prospective cohort study. Lancet. 2009;374(9696):1160-1170.
  2. Lee LK, Monroe D, Bachman MC, et al. Isolated Loss of Consciousness in Children With Minor Blunt Head Trauma. JAMA Pediatr. Published online July 07, 2014. doi:10.1001/jamapediatrics.2014.361.
  3. Barrett, Tyler W. et al. Is the Golden Hour Tarnished? Registries and Multivariable Regression. Annals of Emergency Medicine , Volume 56 , Issue 2 , 188 – 200
  4. Stiell IG, Wells GA, Vandemheen K.  et al.  The Canadian CT Head Rule for patients with minor head injury.  Lancet. 2001;357:1391-1396
  5. Stiell IG, Clement CM, Rowe BH, et al. Comparison of the Canadian CT Head Rule and the New Orleans Criteria in Patients With Minor Head Injury. JAMA. 2005;294(12):1511-1518. doi:10.1001/jama.294.12.1511
  6. Mower WR, Hoffman JR, Herbert M, et al, Developing a Decision Instrument to Guide Computed Tomographic Imaging of Blunt Head Injury Patients. J Trauma. 2005 Oct;59(4):954-9. (Nexus II)