Why Observational Data for tPA is Flawed

Much is made of retrospective comparisons derived from registry data in acute ischemic stroke.  The most egregious of these attempt to match a subgroup of tPA-treated folks with a control group not receiving tPA.

This publication, from an Austrian stroke registry, pulls 890 patients from 54,917 with mild (NIHSS <5) symptoms to perform a comparison matched on many clinical features.  In their matched comparison, 41% of tPA-treated patients were better off, 30% were identical on mRS, and 29% favored non-treatment.  Therefore, these authors declare there is an overall shift towards favorable outcome with tPA.

What is wrong with drawing anything but hypothesis-generating conclusions from this data (or, any retrospective, observational data)?  While the authors control for a few factors, there are many pre-existing comorbid conditions influencing treatment or non-treatment with tPA.  For example, a patient with advanced metastatic cancer will almost certainly be excluded from treatment with tPA – and certainly have poor 3-month functional outcomes – but that comorbid state cannot not be captured by this registry.  Then, just as we saw in IST-3, patients who are treated with tPA frequently receive more vigilant initial stroke care.  Adherence to clinical pathways as well as the control of hyperglycemia, fever, and swallowing dysfunction have profound effects on subsequent death and disability far exceeding the effect size supposed for tPA.  This registry, taking place over the course of a decade of evolving stroke care, cannot control for follow-up treatment and therapy.

This is, essentially, why all retrospective, observational comparisons are almost guaranteed to favor the tPA cohort.

Just as an added note – for anyone considering responding directly to the authors in the pages of Stroke – you will be charged $35 for typesetting for an electronic-only publication which then resides behind a paywall.  Traditional scientific journals are for profit, not for science – that’s where FOAMed comes in!

“Thrombolysis in Patients With Mild Stroke: Results From the Austrian Stroke Unit Registry”
http://stroke.ahajournals.org/content/early/2014/01/30/STROKEAHA.113.003827.abstract

My ACEP tPA Policy Critique

As some of you are aware, there is controversy regarding the use of tPA for acute ischemic stroke.  To this end, ACEP has opened up public comment for their recent relevant Clinical Policy Statement.

The comment form, however, is a bit of an odd and onerous format.  To spark discussion, to provide inspiration – and for public feedback/comment/correction – here are a few points from the initial draft of my response:
Page 225, Line 3, author list:
Area of Content / Concept – Conflict of Interest in Guideline Development Group (GDG)
The Institute of Medicine publishes recommendations regarding the composition and conflict of interest disclosures of a Clinical Practice Guideline (CPG) writing panel.  This tPA policy statement falls short on several accounts, most importantly:
Standard 2.1:  
The disclosures listed by the authors only narrowly address their direct financial relationships, but do not describe non-commercial, intellectual, and patient/public activities pertinent to the scope of the CPG.  For instance, authors do not fully describe their relationships with FERNE, a pharmaceutical-supported organization, nor other indirect and intellectual activities relevant to the CPG.
Standard 2.3:
The recommendation states members of the GDG should not participate in marketing activities or advisory board of entities whose interests are affected by the recommendations.  This standard does not appear to be met.
Standard 2.4:
Whenever possible, GDG members should not have COI.  If this is not possible, members with COIs should represent only a minority.  The chair, or co-chair, should not have COI.  This standard does not appear to have been met.
Standard 3.1:
The GDG should be multidisciplinary with methodological experts, clinicians, and patients.  The GDG members appear to be primarily clinicians and administrators, rather than patients and methodologic experts.
Standard 7:
The external review process is only briefly described, and the guideline was not open to public comment until this 60-day period.
Additional comments on the integrity of CPG come from a recent BMJ article, “Ensuring the integrity of clinical practice guidelines:  a tool for protecting patients.”  The recommendations from this publication are similar to the IOM recommendations, with the addition the GDG members ought to represent diverse viewpoints regarding the topic in question.  It does not appear this CPG represented any point of view other than a pro-tPA viewpoint.  The ACEP tPA clinical policy was evaluated using the “red flag” methodology by this article and found to be lacking.
Based on the COIs identified in this GDG, the output lacks face validity.
Page 227, Line 23:
Area of Content / Concept – Patient Management Recommendations
The guideline specifies offering IV tPA to acute ischemic stroke patients within 3 hours to be a Level A recommendation.  A Level A recommendation, according to the methodology of the CPG, states this indicates “Generally accepted principles for patient management that reflect a high degree of clinical certainty.”
The evidentiary table cites several articles as Class I evidence specifically relevant to the 3 hour timeframe (NINDS, ECASS II, and ATLANTIS B 0-3).  NINDS, by all accounts, shows benefit, while the effect size is debated by many based on the baseline characteristics of the treatment groups.  ECASS II is a negative trial; it is inappropriate to apply a subgroup analysis consisting of the 158 patients treated within 3 hours as the same level of Class I evidence.  The ATLANTIS B publication cited is also a very small subgroup analysis of a heavily modified trial stopped early for futility, and should not be considered the same level of Class I evidence.
Notably missing from this evidentiary table is ATLANTIS Part A – cited in the text, but apparently not considered as contributory to the CPG.  This is randomized, placebo-controlled evidence stopped early due to patient harms in the tPA cohort.  This merits inclusion in the evidentiary table as evidence of the harms of IV tPA.
The Lees meta-analysis, among others performed prior to 2010, is appropriately level II evidence.  However, it should be noted there are significant methodologic concerns associated with performing a meta-analysis that includes trials stopped early by their sponsors for futility or harms alongside trials allowed by their sponsors to run to their conclusion.  The evidentiary table notes “some of the analyzed studies were industry supported.”  To be more precise, all of the listed studies have substantial COI with industry – including employees of the sponsoring corporations listed among study authors – except NINDS, where the COI is minimized.
The remaining observational evidence is not relevant to a Level A recommendation.  The Hill and Wahlgren Phase IV studies are not placebo-controlled and only offer substantially limited, indirect, adjusted comparisons to a non-tPA treated population regarding safety and effectiveness.
My point, therefore, is NINDS is unique in support of tPA.  It is irresponsible to base a Level A treatment recommendation on a single positive study with a disputed effect size, whose results cannot be considered externally valid to current stroke practice.  NINDS – along with most evidence cited here – describes use in controlled trial environments of academic stroke centers supported by stroke neurologists.  There is insufficient evidence to support its general effectiveness, compared with standard treatment, in community Emergency Medicine.  Additionally, the observational evidence cited in the evidentiary table clearly describes a heterogenous acute stroke population, with varying levels of sICH risk, mortality risk, and capacity to benefit.  A CPG should not make a global recommendation for treating such a heterogenous disease without providing tools for physicians to communicate individualized risks and benefits.  Unfortunately, the placebo-controlled data are of insufficient quantity and quality to guide therapy.
A demonstration of the dangers of basing treatment decisions on small trials and small effect sizes is based in statistical theory.  Dr. Ioannidis demonstrates how “Most published research findings are false”, a hypothesis apparently borne out by “A decade of reversal:  an analysis of 146 contradicted medical practice.”
Furthermore, a Level A recommendation constitutes “generally accepted principles” with a “high degree of clinical certainty”.  If this were, indeed, the case, tPA for acute ischemic stroke would not be a controversial therapy 18 years past its introduction.  Respected U.S. Emergency Medicine experts in critical appraisal and knowledge translation, e.g., Jerome Hoffman, David Schriger, David Newman, Anand Swaminathan, and many others feel tPA for stroke remains an unproven and inadequately described therapy for acute ischemic stroke.  Indeed, Dr. Swaminathan ably debates Dr. Jagoda, one of the authors of this Clinical Policy in podcast, hosted by Scott Weingart.

Citation:  http://emcrit.org/podcasts/tpa-for-ischemic-stroke-debate/

Lest ACEP consider these objections simply a vocal minority or lunatic fringe, it should be noted active debate continues in the international literature as well.  Just last year, the BMJ posted a “Head to Head” debate regarding the proven efficacy of tPA in acute ischemic stroke.  An unscientific poll accompanying the article reported a slim majority of respondents did not feel tPA was proven effective.

Citation:  http://www.bmj.com/content/347/bmj.f5215

Additionally, there remains disagreement between international professional societies regarding the use of tPA in acute ischemic stroke.  While several countries endorse its use, others, such as Australia and New Zealand, remain concerned the strength of the evidence does not support widespread use.

Citations:
http://bit.ly/1nY6P18
http://bit.ly/1gRpYRs

In summary, the evidence does not support a Level A recommendation for tPA for ischemic stroke within 3 hours.

There is no reasonable justification for anything higher than a Level B recommendation – and even then, a caveat stating this has never been demonstrated as efficacious compared to usual therapy outside of controlled clinical trial environments.  Physicians may consider offering this therapy based on comfort, diagnostic certainty, supporting resources, and institutional commitment, but it should not be considered the standard of care.

Page 227, Line 28:
Area of Content / Concept – Patient Management Recommendations
The Level B recommendation given to IV tPA is inappropriate given the lack of unbiased evidence in support of treatment beyond the 3 hour time window.  This therapy is not approved in the U.S. and the Class I evidence regarding the 3-4.5 hour time window is conflicting.  ECASS, ECASS II, and ECASS III are manufacturer-sponsored studies of which only ECASS III demonstrated benefit.  ATLANTIS, also manufacturer-sponsored, enrolled patients similar to the NINDS criteria and showed harms beyond 5 hours, futility in the 3-5 hour window, and no usable insights in the 0-3 hour timeframe.  As Clark and Madden note, “Keep the three hour tPA window: the lost study of Atlantis” – ECASS III alone is not enough to refute prior evidence of either futility or harm.  There is a reason why the FDA still has not approved IV tPA beyond 3 hours.
ECASS III is also flawed regarding a baseline imbalance of prior stroke included in the placebo arm.  The absolute difference in percentage of patients with prior stroke is identical to the effect size offered by IV tPA.  Even more concerning regarding the internal validity of the findings, ECASS III offers this COI statement:
Supported by Boehringer Ingelheim.
Dr. Hacke reports receiving consulting, advisory board, and lecture fees from Paion, Forest Laboratories, Lundbeck, and Boehringer Ingelheim and grant support from Lundbeck; Dr. Brozman, receiving consulting and lecture fees from Sanofi- Aventis and consulting fees and grant support from Boehringer Ingelheim; Dr. Davalos, receiving consulting fees from Boeh- ringer Ingelheim, the Ferrer Group, Paion, and Lundbeck and lecture fees from Boehringer Ingelheim, Pfizer, Ferrer Group, Paion, and Bristol-Myers Squibb; Dr. Kaste, receiving consulting and lecture fees from Boehringer Ingelheim; Dr. Larrue, receiv- ing consulting fees from Pierre Fabre; Dr. Lees, receiving con- sulting fees from Boehringer Ingelheim, Paion, Forest, and Lund- beck, lecture fees from the Ferrer Group, and grant support from Boehringer Ingelheim; Dr. Schneider, receiving consulting fees from the Ferrer Group, D-Pharm, BrainsGate, and Stroke Treat- ment Academic Industry Round Table (STAIR) and lecture fees from Boehringer Ingelheim and Trommsdorff Arzneimittel; Dr. von Kummer, receiving consulting fees from Boehringer Ingel- heim and Paion and lecture fees from Boehringer Ingelheim and Bayer Schering Pharma; Dr. Wahlgren, receiving consulting fees from ThromboGenics, lecture fees from Ferrer and Boehringer Ingelheim, and grant support from Boehringer Ingelheim; Dr. Toni, receiving consulting fees from Boehringer Ingelheim and lecture fees from Boehringer Ingelheim, Sanofi-Aventis, and Novo Nordisk; and Drs. Bluhmki, Machnig, and Medeghri, being employees of Boehringer Ingelheim.
As I did not mention it previously, the meta-analysis by Lees also supplies this relevant COI statement:
KRL, RvK, DT, MK, and WH report honoraria from Boehringer Ingelheim for their roles in conduct of the ECASS trials. KRL reports honoraria from Lundbeck and Thrombogenics. DT reports honoraria from Novo-Nordisk, Pfizer, Sanofi-Aventis, and Boehringer Ingelheim. EB is an employee of Boehringer Ingelheim. RvK and JCG report being consultants to Lundbeck. GWA reports being a consultant to Lundbeck and Boehringer Ingelheim. SMD reports honoraria from Boehringer Ingelheim.
Confident translation in policy of clinical trial evidence having this level of COI is simply not reasonable.

Finally, it should also be noted the updated meta-analysis by Wardlaw accompanying the publication of IST-3 no longer shows a statistically significant benefit for alive and independent for the 3-6h time frame – moving from OR 1.17 (1.00 – 1.36) to OR 1.07 (0.96 – 1.20).  This ought to be viewed as regression to the mean as the sample size continues to increase.  Considering thrombolytic trials for myocardial infarction enrolled 140,000 patients, rather than the ~3500 tPA patients from the trials included in the Wardlaw meta-analysis, this should serve as a warning regarding the inadequacy of current evidence.

In summary, treatment beyond 3 hours can only be recommended based on “expert” (e.g., the sponsored mouthpieces of industry) opinion, should be considered only as part of prospective research, and absolutely not be recommended or implied to be standard of care.
Page 232, Line 28:
Area of Content / Concept – NINDS Exclusion Criteria
There is no mention of oral anticoagulation in these treatment recommendations, other than reference to the NINDS exclusion criteria regarding PTT and PT.
The safety of tPA given concomitant use of coumadin and the novel oral anticoagulants (direct thrombin inhibitors, factor Xa inhibitors) is not established.  Contradictory findings from meta-analyses and systematic reviews suggest increased risk of bleeding, even with INR <1.6.  Any CPG recommending offering IV tPA is remiss in excluding mention of these commonly prescribed medications in the population most at risk for stroke.
tPA cannot yet be considered safe when considered in the setting of anticoagulation, despite the NINDS inclusion criteria, in the absence of high-quality data on the subject.
Citations:

All NSAIDs are Created Equally . . . Right?

A guest post by Anand Swaminathan (@EMSwami) of EM Lyceum and Essentials of EM fame.

It’s been more than 10 years since Merck made headlines regarding the increased risk of atherothrombotic events with it’s drug rofecoxib (Vioxx) and 3 years since the almost $1 billion settlement regarding the drug. Over this time period, physicians have questioned the use of all non-steroidal anti-inflammatory drugs (NSAIDs) in patients with increased risk of coronary artery disease. Rofecoxib and its brethren were developed in the 1990’s as alternatives to the traditional NSAIDs (tNSAIDs). These newer drugs only inhibited COX-2 and theoretically would lead to less gastrointestinal bleeding since inhibition of COX-1 is believed to lead to this side effect. Based on this pathophysiologic theory and strong marketing, the drugs became widely prescribed. Unfortunately for our patients, saving the gut may compromise the heart. Or is it actually that all NSAIDs, regardless of which COX they inhibit, raises the risk?

This research group performed a meta-analysis of a large number of trials looking at both NSAIDs vs. placebo (280 trials) and one NSAID vs. another NSAID (474 trials). All of the studies look at length of use of at least four weeks but many had longer treatment durations. So, what did they find? When compared to placebo, coxibs (COX-2 inhibitors), diclofenac and ibuprofen all increased the risk of major coronary events but naproxen did not:
Coxibs RR (CI)
Diclofenac RR (CI)
Ibuprofen RR (CI)
Naproxen RR (CI)
Major Vascular Events
1.37 (1.14 – 1.66)
1.41 (1.12 – 1.78)
1.44 (0.89 – 2.33)
0.93 (0.69-1.27)
Major Coronary Events
1.76 (1.31-2.37)
1.70 1.19-2.41)
2.22 (1.10 – 4.48)
0.84 (0.52 – 1.35)
Gastrointestinal Complications
1.81 (1.17-2.81)
1.89 (1.16-3.09)
3.97 (2.22-7.10)
4.22 (2.71-6.56)

Additionally, it didn’t matter which coxib they looked at: all of them increased major coronary events. The coxibs did, however, do what they were supposed to do; the risk of gastrointestinal bleeding was lower in comparison to tNSAIDs like ibuprofen and naproxen.

Does this change what we should do? Can we give NSAIDs to older patients without fearing a major coronary event or death from an MI? The numbers here are small but important. For every 1000 patients allocated to a coxib, three more had major vascular events and one of these events would be fatal. That’s an absolute increase of 0.1% in comparison to placebo. Small increased risk but avoidable. Why not give naproxen instead? In fact, NSAIDs like ibuprofen interfere with the binding of aspirin negating its cardioprotective effects if the two are taken together. Naproxen doesn’t have this issue.
The relative safety in terms of major vascular events associated with naproxen versus ibuprofen was recently written about by the FDA and reported by the Associated Press here –

http://hosted.ap.org/dynamic/stories/U/US_PAIN_RELIEVERS_SAFETY?SITE=AP&SECTION=HOME&TEMPLATE=DEFAULT

I think the bottom line here isn’t much of a surprise. If you can, avoid NSAIDs in patients with cardiac risk factors. Ibuprofen isn’t a safe alternative. If you need to give an NSAID for whatever reason, use naproxen and use short courses of therapy.
“Vascular and upper gastrointestinal effects of non-steroidal anti-inflammatory drugs: meta-analyses of individual participant data from randomized trials”

Appendicitis Week Continues

As compared to the previously critiqued publication, I am rather pleased with the protocol described by these authors.

This is a clinical pathway for appendicitis from Children’s in Memphis prospectively evaluated for diagnostic accuracy.  They’ve taken the idealist route – risk-stratification, followed by discharge, ultrasound, or pediatric surgery evaluation.  These authors use the Pediatric Appendicitis Score, dropping patients into buckets based on scores 1-3, 4-7, and 8-10.  Most interestingly, there is no role for CT scanning in this pathway unless specifically requested by the consulting surgeon.

In this study, 196 children completed the full clinical pathway – 44 were in the low-risk group, 119 in the moderate-risk, and 33 in the high-risk group.  Almost all the low-risk patients were discharged from the Emergency Department with a telephone call follow-up, and only one patient had a callback – for what was eventually diagnosed as an omental infarct.  In the high-risk group, all 33 patients were admitted, and all 28 patients who were taken to the OR by surgery had appendicitis.  The 119 patients in the moderate-risk group are much more interesting.  33 of 119 ultimately had ultrasounds supporting a diagnosis of appendicitis, and all were confirmed in the OR.  However, the remainder of these patients either were discharged without ultrasound, or had negative ultrasounds.  There were, ultimately, 5 cases of appendicitis in the moderate-risk group, despite a negative ultrasound.

This is the main flaw in external validity of their protocol – what to do with a moderate-risk patient with a negative ultrasound?  Per the authors, the more concerning cases were admitted – either to surgery or pediatrics, depending on level of suspicion for an alternative diagnosis – or discharged with telephone follow-up.  I think many folks, when faced with this level of uncertainty, proceed to CT scan – but, amazingly, only 13 kids in this cohort were subjected to diagnostic or therapeutic radiation.  This statistic alone validates the protocol – and the cultural and operations changes necessary to make it work.  By having a safety net of follow-up calls in place for patients discharged from this clinical pathway, the pressure for an immediate diagnosis is eliminated.

It is a small sample size, and it requires providers to increase their comfort level with diagnostic uncertainty – but it certainly seems rational and promising.

“Prospective Evaluation of a Clinical Pathway for Suspected Appendicitis”
http://www.ncbi.nlm.nih.gov/pubmed/24379237

Open the Data

There is a committee within the Institute of Medicine charged with examining the issues associated with data sharing after randomized controlled trials.

Data-sharing, without question, reflects a dire need.  From companies behaving badly – such as Merck with Vioxx, or Roche with Tamiflu – to inadvertent errors in analysis, protecting the health of patients requires more than simple peer review of documents prepared for pharmaceutical corporations by medical communication professionals.

Jeff Drazen, in this editoral, makes a call for feedback to the IOM.  Oddly, his main concern is – how long ought the original authors of a study be allowed exclusive access to trial data?  Would open data disincentivize researchers to perform clinical investigations, knowing their academic and commercial benefit would likely be curtailed?  On the flip side, we have seen publication of trial data be massively delayed – see ATLANTIS Part A, withheld for seven years – by pharmaceutical companies concerned with protecting their business interests.

It is a complicated and subtle issue, to be sure, but appropriate transparency is almost certainly an improvement over the current situation.  Full details, and how to leave feedback, are at:
http://www.iom.edu/activities/research/sharingclinicaltrialdata.aspx

“Open Data”
http://www.nejm.org/doi/full/10.1056/NEJMe1400850 (open access)

Intermediate Lactate Values, Lowering the Bar for Cryptic Shock

A guest post by Rory Spiegel (@CaptainBasilEM) who blogs on nihilism and the art of doing nothing at emnerd.com.

Serum lactate has been the darling of Emergency Medicine/Critical Care since Manny Rivers first introduced EGDT to the Emergency Department. Since then we have used it as a screening tool, a means to guide therapy and even to prognosticate outcomes. Despite our universal acceptance of its utility, very little high quality data has been published on its diagnostic properties. I reviewed this evidence in more depth in a past post and will limit this to the question, “Can serum lactate identify a group of patients who are in cryptic shock, despite clinically appearing well?” The Surviving Sepsis Campaign recommends using a lactate level of 4 mmol/L as the threshold for identifying cryptic shock, but lactate has a continuous curvilinear association with mortality and a 4 mmol/L threshold seems like an arbitrary cutoff.

In an attempt to answer this question Puskarich et al conducted a systematic review, published in the Journal of Critical Care, examining the ability of intermediate lactate values (2.0-3.9 mmol/L) to predict cryptic shock and death. Eight studies were included in this review. A total of 11,062 patients with intermediate lactate levels were examined. The authors appropriately decided that given the heterogeneity of these datasets, a formal meta-analysis was not appropriate. Instead they settled for descriptive statistics of each individual trial. In summary they found patients with intermediate lactate values who were normotensive had a 30 day mortality rate of 14.9% (mortality in individual trials ranged from 3.2-16.4%). Obviously the patients with intermediate lactate levels that were concurrently hypotensive fared far worse (30 day mortalities of 35-37%).

This review fails to define the clinical utility of the association between elevated lactate levels and risk of death.  In the few studies included in this review which published diagnostic test characteristics, lactate performed surprisingly poorly. Howell et al found lactate had an AOC of 0.71 for predicting 30 day mortality. Shapiro et al reported a similar AOC of 0.67. In fact in the Shapiro study when a cutoff of 2.5 mmol/L was used as screening tool for cryptic shock, it had a sensitivity of 59% and a specificity of 71%. Even a threshold of 4 mmol/L though very specific (92%) had a sensitivity of 36%, a far lower sensitivity than one would be traditionally accepted for a screening test.

More importantly, this data does not allow us to determine how a lactate threshold of 2.5 mmol/L  performs in the true cryptic shock patient. This is the patient who has end organ hypoperfusion without any clinically obvious signs. In most of the patients with elevated lactates, they appear clinically ill and thus the lactate is only confirming what we already know, that this patient needs aggressive intervention. If lactate is to prove useful as a true screening tool (at whatever threshold), it should be able to identify the patient clandestinely experiencing septic shock before any obvious signs of of end-organ damage (AMS, hypotension, AKI) become apparent. Unfortunately we have little data supporting its use in this manner. Even the secondary analysis of the Jones trial, finding similar mortalities between hypotensive patients and normotensive patients with elevated lactate (above 4mmol/L), fails to impress. Although the cryptic shock patients were not hypotensive in the strictest sense, they were by no means physiologically normal. On the contrary they were older, more tachycardic, with faster respiratory rates, and experienced significantly more intra-abdominal infections (30% vs 16%) than their hypotensive counterparts. And though they were not hypotensive (<90 mmHg), their blood pressures were not necessarily normal. The median blood pressure in the cryptic shock group was 108mmHG with an IQR of 92-126. To put it simply, these patients were sick. They did not require a lactate level to identify them as in need of aggressive therapy. There was nothing cryptic about them….

“Prognosis of Emergency Department Patients with Suspected Infection and Intermediate Lactate Levels: A Systematic Review”
http://www.jccjournal.org/article/S0883-9441(14)00002-1/abstract

Zero-Miss or High-Yield for Appendicitis?

In a persistently befuddling contradiction, the same specialty that sometimes needs to be physically restrained from pan-CT-ing every trauma patient is simultaneously concerned about the negative appendectomy rate.  Maximum sensitivity in one instance, maximum specificity in the other.

An avenue that has been bludgeoned to death many a time is the utility of the WBC for diagnosis of appendicitis.  This study in Pediatrics out of U.C. Davis, again, attempts to establish test-thresholds for WBC to with the ultimate goal of reducing the negative appendectomy rate.  At U.C. Davis, similar to national rates, 2.6% of children taken for appendectomy were demonstrated to have a normal appendix.  They observe that neutrophil counts and overall WBC counts were within the normal range in over 80% of these patients, and describe a potential management strategy to improve their negative appendectomy rate.  For WBC <9,000 or <8,000, the negative appendectomy rate could be improved to 0.6% or 1.2% – as long as the surgeons were content with a sensitivity of 92% to 95%.

Thus the conundrum.  How many cases of appendicitis are you willing to allow to progress to perforation – associated with not-insignificant morbidity – in order to minimize the negative appendectomy rate?  Considering up to 20% of appendicitis will have a normal WBC count – despite addressing an important problem – the solution presented by these leukocytosis cut-offs does not appear to provide the ultimate answer.

“Use of White Blood Cell Count and Negative Appendectomy Rate”
http://pediatrics.aappublications.org/content/133/1/e39.abstract

Can We Escape Antibiotics in Sore Throat?

Yes.  And no.

It is well-established complications of acute sore throat are incredibly rare.  The likelihood of a patient developing the most concerning of suppurative complications – a peritonsillar abscess or “quinsy” – is less than a fraction of a percent.  Rheumatic fever is virtually eliminated in the United States.  Yet, as we see from this British cohort, over half of patients visiting primary care received a prescription for antibiotics.

This is study reports on a combination of several, prospectively gathered cohorts presenting with acute sore throat to British primary care practices.  Comprising 14,610 adults, only 5,243 escaped the physicians office without an antibiotic prescription, while the remainder received immediate or delayed antibiotics.  Suppurative complications across all cohorts – peritonsillar abscess, sinusitis, otitis media, and cellulitis – ranged from 0.1% to 0.6%.

Unfortunately, this is not a randomized trial – the patients who were given antibiotics by their physician had much more severe initial clinical presentations.  This means, unfortunately, there is no information in this data set describing the actual protective effect of antibiotics without making statistical contortions.  The main value, however, is in describing the futility of clinical judgement for selecting patients for antibiotics.  Of all the various clinical features recorded prospectively for each patient, only severe ear pain and severely inflamed tonsils were significant predictors of suppurative complications – with ORs of 3.02 and 1.92, respectively.  However, these still constituted hundreds of patients with symptoms who otherwise did not progress.  High scores on the Centor and FeverPAIN criteria were similarly, minimally predictive.

In the end, it is ultimately apparent antibiotics confer some protective effect.  The absolute benefit, however, will represent just a handful of patients out of thousands.  The authors sum it up just as nicely as I might:

“Since a policy of liberal antibiotic prescription for sore throat to prevent complications is highly unlikely to be cost effective, and clinicians cannot rely on clinical targeting to predict most complications, clinicians will need to rely on strategies such as safety netting or delayed prescription in managing the low risk of suppurative complications.”

“Predictors of suppurative complications for acute sore throat in primary care: prospective clinical cohort study”
http://www.bmj.com/content/347/bmj.f6867 (open access)

ACEP Clinical Policy on tPA Up For Comment

At ACEP13, the Council voted to reconsider the clinical policy statement regarding tPA for acute ischemic stroke.  As part of that resolution, the policy was to be opened up for a sixty-day public comment period.
And, the moment you’ve all been waiting for – it’s up!  Follow this link to read more, download the clinical policy statement, and leave your comments:

Ignore This Fixed-Dose Philosophy For Morphine

Emergency physicians are legendary for poor control of pain in the Emergency Department, with many factors challenging optimal care.  One solution – and one I’ve taught in the ED – is to use a weight-based approach to dosing.  This works out to 0.1-0.15 mg/kg of morphine or equivalent as an initial starting dose.

These authors gather 300 patients – 100 non-obese, 100 obese, and 100 morbidly obese – who all received a 4mg intravenous dose of morphine for median initial pain levels of ~8 on a scale to 10.  Upon reassessment a median of ~1 hour after administration, the median pain level in all groups had fallen to 2 or 3.  This somewhat tailors along with other work, which observed substantial numbers of patients with adequate response following even doses of morphine of less than 4mg.  The authors therefore conclude:

“BMI does not predict the analgesic response to a single dose of intravenous morphine in the ED. This is true even for patients who are morbidly obese. We suggest using fixed doses rather than weight-based doses of morphine for acute pain in obese patients.”

However, this retrospective study fails to capture and control for many of the other factors associated with opiate response, including age, substance abuse history, pre-hospital pain control – along with all the other contextual factors lost through chart abstraction.  Additionally, patients at Maricopa Medical Center in Phoenix are not hardly generalizable to, well, nearly anywhere in the world.

Ultimately, this limited study leads to an erroneous, and potentially harmful conclusion that weight-based doses are unnecessary.  Aggressive, titrated or weight-based, pain control is not in any fashion refuted by this work.

“Analgesic response to morphine in obese and morbidly obese patients in the emergency department.”
http://www.ncbi.nlm.nih.gov/pubmed/23314209