Intensive blood pressure lowering in patients with acute cerebral hemorrhage; don’t just do something... stand there!

I love me a good negative study. This is especially one that is well conducted in a high impact journal. The results are much more likely to be believed.

These authors of the ATACH-2 trial randomized patients with intraparenchymal hematoma to intensive systolic BP lowering (110 to 140 mm Hg) vs. standard treatment (140-180 mm Hg). They excluded patients with very low GCS and massive hematomas.

They mostly used nicardipine for BP reduction and this had to be started within 4.5 hours of onset of symptoms. The primary outcome was death or disability (mRS 4-6) at 3 months after randomization.

Results?

Patient enrolment was stopped because of futility at the 1000 mark.  The primary outcome was observed in 39% of the intensive-treatment group vs. 38% in standard treatment. As you would imagine, there were more adverse events with intensive treatment.

Of course there were some limitations. Externally validity might be an issue with the drugs used and patient demographics. Treatment didn’t start very early. We could argue over the primary outcome. Most patients weren’t that sick (85% had a GCS of 12-15) so perhaps we can’t extrapolate this to the sicker cohort etc.

Nevertheless, the results look pretty convincing.

They even conducted an ordinal shift analysis. These are all the rage in the stroke thrombolysis literature as they have a high degree of statistical efficiency to find small differences. But even this showed nothing.

So what are we to conclude?

Targeting a systolic BP between 140 to 180 is just fine. As with many things in medicine, we shouldn’t mess around too much. Don’t just do something... stand there!

Covering:

Qureshi, AI, Palesch YY, Barsan WG, et al. Intensive Blood-Pressure Lowering in Patients with Acute Cerebral Hemorrhage. N Engl J Med 2016;375:1033-43.

Therapeutic hypothermia for in-hospital cardiac arrest? Who knows...?

There is some evidence to suggest that therapeutic hypothermia may (or may not) be efficacious for out-of-hospital cardiac arrest (OHCA). But what about cardiac arrest that happens in the hospital (IHCA)? She we bust out the esky and ice blocks?

These authors sought to answer this question by looking at a large registry of 26,183 patients with IHCA to see who did and didn’t get cooled. The primary outcome was survival to hospital discharge. To be clear, this was an observational study and patients were not randomized.

As you can imagine, there were quite substantial differences amongst the group of patients who were offered cooling and those that did not. So it’s a bit like comparing apples to oranges before we even start with therapeutic hypothermia.  

So how do we try to correct for all of this confounding? Throw in some fancy propensity matching!

After adjustment the therapeutic hypothermia was associated with lower in-hospital survival (27.4% vs. 29.2%). Cooling was also worse for most secondary outcomes.

So therapeutic hypothermia is harmful for IHCA?

Answer: we don’t know.

With all of the inherent limitations of this study design, the results are pretty irrelevant. Registry data is notoriously unreliable. Data is often missing, incomplete or just plain wrong. If you start with rotten eggs, you can’t make a very good Pavlova.

In addition, there is no amount of fancy statistics that can reliably account for all of the confounding. Lots of assumptions go into these “adjustments” and we can only correct for what we know and measure accurately. As Donald Rumsfeld said, “...there are also unknown unknowns.”

What are all the variables that make a patient sicker? Have we measured them accurately and precisely? There’s no way...

In the end, this study suggests there is clinical equipoise and it would be ethical to conduct a randomized clinical trial. Certainly this might give us a better answer... but I wouldn’t hold my breath.

For now, we can save our ice for something that really matters... margaritas anyone?

Covering:

Chan PS, Berg RA, Tang Y, et al. Association Between Therapeutic Hypothermia and Survival After In-Hospital Cardiac Arrest. JAMA 2016;316(13):1375-82.

Steroids for refractory shock following cardiac arrest; such promising methods but such poor results

Should we give steroids to patients with OHCA and refractory shock? This is a decent research question. 

If one wants to know the truth, then the double-blind placebo controlled RCT is the absolute pinnacle of research.

The overall methods of this paper are great. Of course no papers are perfect and there were some issues but...

There was a fatal flaw.

It was only powered to include 50 patients! You have got to be kidding me.

It does not take a masters in biostatistics to know that such small numbers will only ever find huge changes in treatment effect. The likelihood of a type II error (false negative study) is massive.

(Just in case you were wondering, they found no difference if patients were given steroids or not)

This was going to be a negative study before they ever started. What were they thinking...? Sometimes I wish I had a time machine so I could go back and shake these people.  

Perhaps I shouldn’t be so critical. Feasibility of such a study is a major problem. These patients are not common and recruitment would have been very challenging. But most researchers anticipate this and choose other study designs and/or make other efforts & compromises. Why conduct research that you know will be flawed and a waste of time?

What should we conclude?

Absolutely nothing. Grumphfpfff...

But there is a good lesson to researchers and to those learning critical appraisal of the literature. Do your homework before you start. Choose a research question and study design that is feasible and has the potential for success.

Covering:

Donnino MW, Anderson LW, Berg KM, et al. Corticosteroid therapy in refractory shock following cardiac arrest: a randomized, double-blind, placebo-controlled trial. Crit Care. 2016 Apr 3;20:82. doi: 10.1186/s13054-016-1257-x.

One in Six Patients Hospitalized with Syncope has a PE? Danger... Danger...

The danger is taking this paper at face value! Never has such an important paper in the NEJM required the reader to exercise such caution with interpretation.

These authors looked to find the prevalence of PE among syncope patients who were admitted to hospital from 11 Emergency Departments in Italy. Che bello!

They performed a systematic workup to investigate PE in all of these 560 patients. Patients with low risk by Wells Score were excluded with a negative D-dimer. All others got mostly CTPA’s and a few VQ scans.

The prevalence of PE was 17.3%!

Holy merda! We need to do a lot more CTPA’s in patients with syncope!

Danger! Danger!

Remember, these were elderly patients with syncope admitted to hospital. If we include all patients with syncope (i.e. discharged from the ED) in the denominator the prevalence drops to 3.75%. But we’re still not done...

Of these admitted elderly patients, 40% had clinical signs of DVT, 20% had active cancer, and 10% had prolonged immobility. Is there any surprise that many of these patients might have a PE?

To be fair, there were 31 patients diagnosed with large PE’s that were admitted to hospital with an alternative diagnosis. This is about 5% of admitted patients or 1% of all patients that presented to the ED. Although this percentage is small, it does emphasize that we should continue to think, keep an open mind and avoid diagnosis momentum. But isn’t this what we should always be doing?

In addition, CTPA is not perfect. How many false positives did they have? And how many small PE’s were simple incidental findings that had absolutely nothing to do with their syncope? What is the number needed to kill by finding incidental “PE’s” and putting elderly patients on anticoagulation? What about other incidental findings, over-diagnosis, and contrast induced nephropathy?

Unfortunately none of the above issues were significantly highlighted in this paper. The authors, peer reviewers and journal editors should be ashamed. Fortunately, the NEJM is usually much better than this.

So what should we do?

Well, we should NOT perform indiscriminate CTPA’s on all patients with syncope. This will cause more harm than good. We should investigate PE if we think we should... keep an open mind; especially if they have risk factors and/or clinical signs & symptoms of DVT/PE.

But most of all, we should stai attento to the dangerous conclusions of this paper!

Covering: 

Prandoni P, Lensing A, Prins M, Sambuca Ilove, et al. Prevalence of Pulmonary Embolism among Patients Hospitalized for Syncope. N Engl J Med 2016;375:1524-31.

No antibiotics for outpatient management of uncomplicated diverticulitis?

Crazy?

A long standing dictum in medicine is the mandatory treatment of acute diverticulitis with antibiotics. However there are now a couple of clinical trials proving that many cases of uncomplicated disease will recover with supportive care alone.

But before we alter our practice, it would be nice to see several studies of high quality evidence providing us a foundation for change. This paper certainly is not high quality evidence but it does add to the body of literature building out of Europe.

This was a descriptive study conducted in two Swedish hospitals that followed a convenience sample of 155 patients diagnosed with CT proven uncomplicated diverticulitis. They were managed without antibiotics and followed up as outpatients.

The mean age of patients was 57 and the mean CRP was 73. The majority had their first presentation of diverticulitis.

How successful was this strategy?

97% did just fine and recovered without complications... wow.

Of course there are some problems with this study design (selection bias, no comparator group, silly power calculation, unnecessary inferential statistics, etc) but it is compelling.

Sure, the literature is starting to look more definitive on this subject, but I’m not sure I have the cojones to change my practice quite yet... call me a eunuch.

I could only imagine having one of my patients return as a failure and have a surgeon castigate (castrate?) me.  In addition, I’m not sure this is the time & place to be making a substantial impact on antibiotics stewardship. Think URTI’s, bronchitis, otitis media, chickens...

I think it’s looking like antibiotics do have some minor effect. The number needed to treat for acute uncomplicated mild disease is probably somewhere between 30 to 50. This might be enough reason to continue our current practice. But, I could be proven wrong.

Covering:

Isacson D, Thorisson A, Andreasson K, et al. Outpatient, non-antibiotic management in acute uncomplicated diverticulitis: a prospective study. In J Colorectal Dis 2015;30:1229-1234.

The 4-way range of motion test to exclude elbow fractures; the Sacramento Elbow Rules?

All kinds of clinical decision instruments have been sprouting up over the past few decades. Perhaps the most famous are the “Ottawa Ankle Rules” dating back to 1992.

There have been several attempts at a decision instrument for the elbow and this is probably why this latest offering was published in a lesser impact journal. Nevertheless, this version is quite promising.

The authors sought to prospectively validate their “4-way range of motion test" for the elbow.

(As an aside... there is no doubt that the lead author Dr David Vinson is a clever dude, but I think he may have failed in the marketing department. Nobody is ever going to remember the “4-way range of motion test,” nor is it very catchy.  So I’m going to call it the Sacramento Elbow Rules until he can think of something better.)

They enrolled a convenience sample of patients 5 years and older with an acute blunt elbow injury if the clinician felt that x-rays of the elbow were indicated. They assessed the performance of the rules compared to the gold standard diagnosis of a fracture or effusion seen on plain radiography.

The 4-way range of motion test... woops, Sacramento Elbow Rules are:

• Full extension to 0°
• Flexion to 90°
• Full supination (with arm flexed at 90°) 
• Full pronation (with arm flexed at 90°)

If the patient could not perform any one of the manoeuvres, they were considered to have failed the rules, thus requiring an x-ray. (To be clear, all patients got x-rays for the purpose of this study.)

Results?

They included 251 patients in their analysis. There were 99 positive x-rays. The test had a sensitivity of 99% (95% CI, 94-100%) and a specificity of 60% (95% CI, 54-69%). This is pretty darn good.

There was one false negative in a 7 year old boy with an undisplaced supracondylar fracture.

It is refreshing to see a paper with such an excellent discussion section. The authors suggest their rules may not be perfect as the lower level of confidence interval (CI) for sensitivity is not as high as 97%. But they wisely mention that a much larger study to narrow down the CI would be challenging and fail on feasibility. What we have is probably good enough especially since a missed subtle fracture is probably of lesser consequence than other high risk clinical scenarios.

I agree. This is probably a decent piece of information that should aid the clinician. It also passes the sniff test (face validity). If a patient can fully extend, flex and supinate & pronate then they probably don’t have a fracture. I’m willing to believe this. No rule is perfect but I think this is ready for prime time. 

Bring on the Sacramento Elbow Rules!

Covering:

Vinson DR, Kann GS, Gaona SD, et al. Performance of the 4-way range of motion test for radiographic injuries after blunt elbow trauma. Am J Emerg Med 2016;34:235-239.

Clearing the C-spine in intoxicated trauma patients. Is a negative CT good enough?

Wouldn’t it be nice to remove the cervical spine collar in an intoxicated trauma patient after negative CT? No more thrashing around, shouting and hassle...

These physician assistant authors out of Portland, Oregon enrolled 1668 adult patients with blunt trauma who underwent cervical spine CT scans in their level 1 trauma centre.

632 (44%) of tested patients were found to be intoxicated. (Intoxication was deemed to positive if the BAL was greater than 0.08g/dl or a positive urine drug screen... ok, not perfect.)

Results?

In these intoxicated patients, the CT missed 5 patients with clinically relevant injury. 4 patients had central cord syndrome and one had an unstable ligamentous injury. All of these patients had obvious neurologic deficits and underwent MRI.

The authors conclude the CT had an overall negative predictive value of 99% for injury. Therefore spine clearance based on a negative CT in intoxicated patients with no gross motor deficit appears to be safe and avoids prolonged and unnecessary immobilization.

My heart wants to believe this conclusion but unfortunately there are some major methodological issues with this paper.

The biggest is incorporation bias. The way they identified cervical spine injury was mostly by CT. So of course the CT will have good test characteristics when it forms a substantial part of the gold standard. Only a minority of patients got MRI’s and clinical status was only followed to discharge. It is quite possible that injuries were missed or declared themselves later.  

The authors seemed to emphasize the negative predictive value (NPV) of the CT. But in cohorts with low prevalence of disease, the NPV always looks good. In fact, the NPV before doing anything was 90%.

A better test characteristic that does not depend on disease prevalence is sensitivity. Obviously it is important for screening tests to be highly sensitive especially when the stakes are high.

What was the sensitivity of the CT?

Only 92%. 

Some might argue that this is not good enough and this paper actually proves the opposite of what it is trying to conclude.

Let the controversy continue!

Covering:

Bush L, Brookshire R, Roche B, et al. Evaluation of Cervical Spine Clearance by Computed Tomography Scan Alone in Intoxicated Patients with Blunt Trauma. JAMA Surg 2016 Sep 1;151(9):807-13. doi: 10.1001/jamasurg.2016.1248

X-ray negative ankle sprains in children. Could this be an occult Salter-Harris fracture?

A child has sprained their ankle.  X-rays are negative but they have tenderness over the growth plate. 

This is an occult Salter-Harris I injury and they must be treated as a fracture!

Not anymore.

These authors out of Canada sought to determine the frequency of these occult injuries by performing ankle MRI’s in 135 children between the ages of 5 to 12 who had negative plain radiography.

Results?

Only 4 out of 135 (3%; 95%CI 0.1-5.9%) had occult Salter-Harris injuries! Turns out they are pretty unusual.

But there was an even more interesting finding in this study. The MRI discovered all kinds of unanticipated injuries despite negative x-rays:

80% with ligamentous injury (ok... no surprise here as they were sprains)

80% with “bone contusions” (goodness this sounds bad)

34% or one third had distal fibular avulsion fractures! (This sounds worse!)

Did patients with these occult injuries fare worse?

No. 

They had the same recovery time as those without these injuries. (But I must clarify that all kids in this study were treated with a “removable air-stirrup brace” as this was in keeping with current practice at participating institutions. Sounds like voodoo medicine to me.)

This goes to prove that the great microscope of the MRI will demonstrate a multitude of findings that probably have no clinical importance. This is better known as overdiagnosis. The major problem with overdiagnosis is clinicians may feel compelled to act (i.e. “overact”) on these findings.

What should we take home from this study?

Occult growth plate injuries after a simple sprain in children is pretty rare. You can probably treat them as a sprain.

MRI’s find all sorts of things that we probably don’t want to know about. Even worse, they may cause harm from overdiagnosis. 

Covering: 

Boutis K, Plint A, Stimec J, et al. Radiographic-Negative Lateral Ankle Injuries in Children. Occult Growth Plate Fracture or Sprain? JAMA Pediatr. 2016;170(1):e154114

Skin Glue to Secure ED Inserted Peripheral IV’s

Believe it or not, skin glue has been studied for securing central venous catheters, epidurals and arterial lines. I must have missed the memo...

Can we glue peripheral IV’s in the ED?

This randomized controlled trial out of Caboolture Hospital in Queensland tried to answer the question. They enrolled 360 adult patients in the ED who were thought to require admission to hospital. They excluded patients who were agitated or had a high likelihood of removing their IV’s.

A study nurse took down the existing IV dressing and patients were randomized to glue vs. standard care. The glue group got 1 drop of cyanoacrylate (Histoacryl) at the IV insertion site and 1 drop under the catheter hub.

The primary outcome was IV failure at 48 hours defined as dislodgement, occlusion, infection, or phlebitis.

Results? The glue group failed 17% of the time and standard care 27%. Thus an absolute difference of 10% or number needed to treat of 10. Not too bad.

Remember that this study enrolled all comers. It did not focus on the high risk IV’s and excluded agitated patients which probably would have demonstrated a greater treatment effect.

Of course no study is perfect and there were some limitations. In addition, small studies can’t make great claims about safety. Nevertheless, I imagine it should be fine.

I would encourage people to view the associated video referenced by the manuscript. It shows the gluing technique and demonstrates the strength of bond very soon after. To me, this seems to have face validity. Who needs evidence... they could have just shown me the video!

There are some questions that remain.

Is it cost effective? It may not be but if used indiscriminately. But perhaps a targeted approach would make it more so.

Can we use other forms of cyanoacrylate such as Dermabond? The authors used Hisoacryl which has a pretty clever dropper so other applicators may get different results.

What should we take away for now?

I think a common sense approach is warranted. Although not specifically studied, I would imagine that we could identify “at risk” IV’s and use glue when thought needed. We would need to ensure that downstream health care providers are aware the IV has been secured with glue and educate inpatient teams about removal. Once again, there is a handy glue removal video.

I would imagine we will get more real world ED experience and studies over time.

Is there nothing glue can’t do?  

Covering:

Bugden S, Shean K, Scott M, et al. Skin Glue Reduces the Failure Rate of Emergency Department-Inserted Peripheral Intravenous Catheters: A Randomized Controlled Trial. Ann Emerg Med. 2016;68:196-201.

Ibuprofen instead of antibiotics for UTI?

Do all women with uncomplicated UTI’s require antibiotics?

Apparently not.

Of course one would expect some UTI’s to resolve spontaneously. Otherwise the human species would have died out thousands of years ago! But in the era of antibiotics, should we adopt a watchful waiting approach?

This double-blind RCT recruited 494 women from one of 42 GP practices in Germany. They were randomized to either ibuprofen or a single dose of fosfomycin.

The primary endpoints were the number of courses of antibiotics and the total burden of symptoms on days 0 to 7.

Results? Two thirds of the ibuprofen group recovered with no antibiotics. Holy smokes!

But unfortunately, they did have higher burden of symptoms as reported on a non-intuitive scale. (To me, they looked pretty similar.) In addition, there were 5 cases of pyelonephritis in the ibuprofen group as compared to 1 in the fosfomycin group.

Urine cultures were positive in about 75% with a pretty low bar of >10² cfu/ml. So who knows if some women never had UTI’s in the first place. Placebo works pretty well for non-bacterial illness. (We know this from treatment of “otitis media” and the Pollyanna phenomenon.) However, I think it is reasonable to assume that many really did have bacterial cystitis.

Another concern is external validity. It is possible that the patients who present to a GP practice are less sick then those who come to the ED. Insert cynical comment here...

So what to do with this information?

There are probably some women with simple UTI symptoms that do not need antibiotics. They will recover just fine with symptomatic therapy. When and in whom to do this is the big question.

The authors suggest a shared decision making strategy with a possible prescription for delayed antibiotics if no improvement. I think this sounds reasonable with some caution.

I also find many doctors make a soft-call diagnosis of UTI and reach for the prescription pad. Perhaps we could wait and see before resorting to antibiotics.

Two thirds better with nothing… pretty impressive.

Covering:

Gagyor I, Bleidorn J, Kochen MK, et al. Ibuprofen versusfosfomycin for uncomplicated urinary tract infection in women: randomisedcontrolled trial. BMJ 2015;351:h6544

HEART Score vs. Gestalt for Diagnosing ACS in the ED?

Clinical decision instruments for sorting out chest pain are nothing new. The latest craze seems to be the HEART score. Who would have thought it helpful to consider the history, ECG, age, risk factors and troponin?

Ok, it seems to have face validity. But is it an improvement upon what we are currently doing? This is an essential question for any decision instrument.

This prospective cohort study out of the Netherlands compared the diagnostic accuracy of the HEART score vs. gestalt in 255 patients.

Results? A whopping 29% of patients had ACS (I think the Dutch have been eating too much cheese.) The HEART score and gestalt seemed to have similar diagnostic accuracy.

Has the HEART score suffered an MI?

Maybe...

To be fair, this study was underpowered and the trends favoured the HEART score. In addition, the doctors specifying their gestalt risk of ACS (low, intermediate, or high) also had to calculate the HEART score! The authors duly noted this and dubbed it possible “influencing bias.” No wonder there was no difference.

As Dr Jerry Hoffman has stated numerous times, clinical decision instruments tend to work poorly in complex disease processes. We are probably never going to come up with a simple and good quality rule that can replace the complexity & nuance of ED chest pain evaluation.

Perhaps the enthusiasm coming from the USA stems from the desire to have some objective quantitative measure charted to justify sending someone home? Shoooooo lawyer you!

Despite the enthusiasm on social media, I’ve never used the HEART score and I know I’m not alone.

Wait a second... history, ECG, age, risk factors and troponin? I take it back... I’ve been using it all the time without knowing! I'm so clever...

Covering:

Visser A, Wolthuis A, Breedveld R, et al. HEART score and clinical gestalt have similar diagnostic accuracy for diagnosing ACS in an unselected population of patients with chest pain presenting to the ED. Emerg Med J 2015;32:595-600.

http://www.ncbi.nlm.nih.gov/pubmed/25217099

Is irrigation of cutaneous abscesses necessary?

It has been long held dogma that one should irrigate the abscess cavity after ED incision and drainage. But as these authors point out, there is no high quality evidence to support this practice.

Unfortunately, this is still the case.

This RCT was conducted in Fresno, California; better known as MRSA country. They enrolled 209 patients with all kinds of abscesses to irrigation vs. no irrigation. This pragmatic design allowed for packing and antibiotics at the discretion of the doctor.

The primary outcome was ‘further intervention’ as defined by repeat I&D, antibiotic change or abscess related hospital admission.

Results? No difference with 15% vs. 13% meeting the primary outcome in the irrigation vs. no irrigation group respectively.

So, we should stop irrigating abscesses!?

Unfortunately, the jury is still out...

This was a small underpowered study with heterogeneous patient population. I don’t think we can make conclusions about the larger pus pockets with lots of necrotic material.

The irrigation was pretty half hearted. This was not standardized and the authors suggest about 100ml was used. Therefore, it is not surprising that such a minor intervention resulted in no difference. Perhaps more aggressive efforts would have achieved better outcomes? Once again, who knows?

Usually randomization evens out the confounders, but for some reason the irrigation group got more packing. In addition, they got more antibiotics at 90% vs. 72% of the time! That’s a lot of antibiotics for cutaneous abscesses and certainly not reflective of my practice (low MRSA prevalence).

The determination of the primary outcome was by 30 day telephone interview. This is far from perfect and could have led to some miscalls. This is better known as non-differential misclassification that can dilute the results towards the null hypothesis. Put another way, this could have watered things down (no pun intended).

The Annals of EM editors capsule summary concludes, “Irrigation of abscesses appears unnecessary after incision and drainage.” I guess this all depends on how you interpret ‘appears.’

In summary, this was a small study that still leaves us with more questions than answers. It gets points for originality. Maybe it's right, but unfortunately we are still in a necrotic mess.

Covering:

Chinnock, B, Hendy GW, Irrigation of Cutaneous Abscesses Does Not Improve Treatment Success. Ann Emerg Med. 2016;67:379-383.

http://www.ncbi.nlm.nih.gov/pubmed/26416494

Isopropyl Alcohol Nasal Inhalation for Nausea in the ED?

Wouldn’t it be great to have something quick, safe, ubiquitous, non-invasive and cheap to give patients with nausea in the ED? How about getting them to sniff on an alcohol wipe?

Yes, you heard me correctly.

But unfortunately, it is probably no better than proper placebo and may cause downstream harm.

There have been some prior studies of alcohol nasal inhalation in the post-operative literature. In addition, aromatherapy has been used in other studies investigating treatments for nausea. So why not bring it to the ED?

This was a randomized double blind, placebo controlled trial performed in a single military ED in Texas. Inclusion criteria were patients aged 18 to 65 with a chief complaint of nausea >3/10 on a numerical rating scale (NRS).

Patients were randomized to hold either an alcohol prep pad or sterile saline wipe about 2.5cm from their nose. They were instructed to nasally inhale deeply for no more than 60 seconds and told to stop if the nausea was completely relieved. This was repeated at the 2 and 4 minute mark if they did not have success.

The primary outcome measure was nausea as reported on the NRS at 10 minutes.

Results? Only 80 patients were recruited but it didn’t matter because there was a huge treatment effect. At ten minutes, the NRS for the alcohol arm dropped from 6 to 3. The placebo had no effect at all. This is great stuff!

But not so fast…

For a placebo to have no effect for nausea is astounding. The vast majority of studies quote about a 30% reduction in nausea when using placebo. The results of this study would have been remarkably different had they used a proper placebo.

Another interesting piece of data was the use of subsequent antiemetics. They were given in only 72% of the placebo group but were required in 89% of the alcohol group. This 17% (95%CI -0.5 to 34.8) increase was not statistically significant but quite clearly worrisome. Could the alcohol sniffing cause paradoxical increased antiemetic requirements?

Probably the biggest argument for skepticism is simple methodology. Small studies demonstrating large treatment effects are usually proven wrong. In statistical speak, this is very likely a type I error.

Despite what you may have heard on the social media echo-chamber of the underqualified, we should not be getting our patients to sniff alcohol. This is unless it is a beautiful glass of Penfolds Grange Hermitage.  

Bon appetit!

Covering:

Beadle KL, Helbling AR, Love SL, et al. Isopropyl AlcoholNasal Inhalation for Nausea in the Emergency Department: A RandomizedControlled Trial. Ann Emerg Med. 2016;68(1):1-9.

Propofol vs. Ketofol for deep procedural sedation in the ED; which is better?

Ketofol exploded on the scene with great enthusiasm over the past decade. But is all the hype worth it?

No.

Most anaesthetists are loath to combine fixed strength drugs in the same syringe. This is akin to combining salt and pepper in the same shaker. (Don’t think about it… I’ve already got the patent.)

Ketofol, a fixed mixture of ketamine and propofol, is theoretically meant to have the advantage of mitigating the side effects of either drug when used alone. So why not.

This Australian double blind randomized controlled trial went far to try to answer the question. They included adults requiring deep procedural sedation supervised by a FACEM.

The primary outcome looking for “respiratory events” was arguably a bit irrelevant. To be fair, researchers try to come up with a feasible question to study. Sometimes the primary outcome is a compromise. But fortunately, they did look at secondary outcomes that are more important.

Results? 573 patients were randomized to propofol or ketofol. 5% in the propofol group and 3% in the ketofol group met the primary outcome. So, no statistical difference.

More patients had self-limited hypotension with propofol. But recovery times were shorter by about 9 minutes.

However, there was a 5% incidence of “severe emergence delirium” in the ketofol group vs. 2% in those that got propofol. 1 in 20 seems concerning to me and probably enough for me to abandon ketofol. 

In the end, I wonder what we are trying to accomplish with ketofol. Either drug works fine when used alone. Procedural sedation is incredibly safe when properly administered. There are times when we should use propofol and times we should use ketamine.

So keep the salt out of the pepper shaker and use either drug alone.  

Covering:

Ferguson I, Bell A, Treston G, et al. Propofol or Ketofol for Procedural Sedation and Analgesia in Emergency Medicine- The POKER Study: A Rondomized Double-Blind Clinical Trial. Ann Emerg Med. 2016 Jul 22. pii: S0196-0644(16)30204-9. doi: 10.1016/j.annemergmed.2016.05.024. [Epub ahead of print]

Does Amiodarone or Lidocaine work for Out-of-Hospital Cardiac Arrest?

Maybe.

Despite advanced life support protocols, there is little evidence that drugs do very much to improve meaningful outcomes after cardiac arrest.

Along with this comes a tremendous effort and trial published in the New England Journal of Medicine. Unfortunately it may not help us too much but, it does provide us with some interesting data to ponder.  

This was a randomized, double blind placebo controlled trial in adults with shock refractory VF or VT that took place in 10 sites in the USA and Canada. (Ian Stiell is one of the authors of course. One cannot conduct a large trial in Canada without his approval.)

The primary outcome was survival to hospital discharge. It was powered to find a 6.3% absolute difference. This was done by a per-protocol analysis rather than intention-to-treat which was fine in this case. They also looked at more important secondary outcomes. You could probably guess what they are…

Results? 37,889 patients were screened for eligibility (holy smokes) and about 3000 patients ultimately randomized to amiodarone, lidocaine or placebo. 70% of the arrests were witnessed and the time to EMS arrival was just over five minutes.

Between the groups, there was no difference in the primary outcome. The absolute difference between amiodarone and placebo was 3.2% (95% CI 0.4 to 7.0.) p=0.08. Nevertheless, this is quite an eyebrow raising trend.

In the pre-specified subgroup of witnessed arrest, the drugs seem to work. At least it was statistically significant with a 5% increase in survival to hospital discharge.

As expected, the conclusion as printed in the NEJM is very measured and reported as a negative trial. However, I’m sure this study will be interpreted in many different ways.

We know that the best predictors of successful outcomes in out-of-hospital cardiac arrest are; witnessed arrest, bystander CPR, and an initial shockable rhythm. It makes sense that an intervention will be more successful in this particular group. So perhaps we should be aggressive.

I don’t think we should be throwing away our drugs quite yet. In fact, I interpret this trial as supporting the existing protocols and use of amiodarone in selected patients. The press release from the NIH seems to agree. However, we could ultimately be proven wrong.

Enjoy,

Covering:

Kudenchuk, PF, Bron SP, Daya M, et al. Amiodarone,Lidocaine, or Placebo in Out-of-Hospital Cardiac Arrest. N Engl J Med2016;374:1711-22.

IV Ketamine vs. Morphine for analgesia in the ED: an RCT

Here we go again...

This is another small study comparing ketamine to morphine conducted by investigators trying to validate their preconceived notions. The lead author has been encouraging the “opiate free ED” for years and now has his home grown “evidence” to back him up.

Perhaps they believe opiates are agents of evil and should be replaced by a drug related to PCP. Let’s have a look further at this evidence.

This was prospective, randomized, double-blind trial of very much a convenience sample of ED patients with acute pain rated >5 on a NRS. The intervention was a K-hole dose of 0.3mg/kg of ketamine vs. morphine at 0.1mg/kg.

The primary outcome was a reduction of pain at 30 minutes.

They had a whopping 45 patients in each group. Pain scores were very similar at baseline at about 8.5 on the NRS. They went down to approximately 4.0 at the 30 minute mark in both groups.

So ketamine is just as good as morphine for acute pain in the ED. Ring the bells!  

Not so fast.

Observer bias was very likely an issue due to lack of blinding. It is very easy to clinically tell the difference between the effects of ketamine vs. morphine. My guess is most of the K-hole group had nystagmus and were babbling away with the fairies. Whether conscious or not, these authors clearly wanted to prove their point.

It could also be argued that they were comparing ketamine to an inadequate straw-man dose of morphine. This opiate is meant to be titrated to effect. 0.1mg/kg is a good starting dose in most patients whereby about half will have adequate analgesia.

Side effects were of course more common in the ketamine group. Not surprising since previous studies have found rates of up to 80%. To be fair, this study demonstrated lower rates but had investigators not blinded to the study hypothesis.

So what are we to do?

Although not specifically investigated in this study, ketamine for analgesia in the ED is probably fine for patients that cannot get adequate doses of opiates or in those chronically habituated.

We should not be replacing a medication that is well established, well known, effective when titrated appropriately and has a perfectly good reversal agent. This is most certainly not with a drug that has questionable efficacy and has a worse side effect profile.

Covering:

Motov S, Rockoff B, Cohen V, et al. Intravenous subdissociative-dose ketamine versus morphine for analgesia in the Emergency Department: a randomized controlled trial. Ann Emerg Med 2015;66:222-229.

http://www.ncbi.nlm.nih.gov/pubmed/25817884

I dare you to Idarucizumab for dabigatran reversal

The major concern over the new oral anticoagulants (NOAC’s) was the lack of a rapid reversal agent. With some pretty clever science comes what many have been waiting for.

This was a randomized double blind placebo controlled trial of 13,429 patients with severe haemorrhagic complications while on dabigatran (Pradaxa). They were randomized to reversal with idarucizumab (Praxbind) or matching placebo. The primary outcome was mortality at 30 days with secondary outcomes of safety and haemorrhage control.

Just kidding... Such a study would never be feasible and some might argue unethical.

Therefore, this was a small unblinded, uncontrolled interim analysis of a larger observational study. As expected, it was sponsored and mostly written by the drug company that stands to make handsome profits if they return positive results.

90 patients on dabigatran who had serious bleeding or required an urgent procedure were given idarucizumab. Most were found to have elevated thrombin or ecarin clotting times at baseline. Evidently, the study drug normalized the test results in 88 to 98% of the patients rather quickly.

So, it seemed to work.

(I’m not going to dwell on the study’s primary outcome measure of “maximum percentage reversal of the anticoagulant effect” as I believe this overstates the real efficacy of idarucizumab. Ok... it was 100% (95% CI 100 to 100). How close were they trying to make the goal post?)

Despite the profound limitations of this study, I will probably give this reversal agent in the rare event I have a suitable patient that meets indications. I think it makes sense.

It is a monoclonal antibody. Unlike activated clotting factors, it is probably safe and unlikely to cause thrombotic events. However we will need to look at phase IV post marketing experience to be sure.

Some quick comments.

This study led to the approval of idarucizumab by the FDA in October 2015 and TGA in June 2016. As of this writing, it is available in some centres in Australia under the Special Access Scheme until Boehringer Ingelheim can get the proper packaging that will satisfy TGA regulations. In a few months it should cost about $3000 a pop.  

Boehringer is probably loving the fact that they can now market dabigatran as having a rapid reversal agent. Cha-ching!

Not to be outdone, the other NOAC’s (rivaroxaban, apixaban) will probably have reversal agents come to market soon (andexonate alfa).

Oh... and the name “idarucizumab?”

Sometimes I wonder if the drug companies purposely make the generic names as confusing as possible so we resort to using the catchy trade names. Sure “Praxbind” is catchy. But so is “I dare you cizumab.” Since two vials are usually given, “I double dare you cizumab!”

Beat that Praxbind!

Covering:

Pollack CV, Reilly PA, Eikelboom J, et al. Idarucizumab for dabigatran reversal. N Engl J Med 2015;373:511-20.

http://www.ncbi.nlm.nih.gov/pubmed/26095746

How to get it wrong: Succinylcholine is associated with increased mortality when used for RSI in patients with severe traumatic brain injury

This is a fantastic study!

It is a fantastically bad study of how to perform research and come to wrong conclusions. It is so awful it makes one’s heart sink.

These authors performed a retrospect data-base review of patients who were intubated in their ED for traumatic brain injury. The main outcome was the difference in mortality when patients were intubated with either rocuronium or succinylcholine.

The results? No difference in mortality was found. Death occurred in 23% in each group.

Not satisfied with negative results, the authors conducted a post-hoc subgroup analysis and found that there was a difference in those with severe TBI. If you torture the data enough, it will talk.

Wooohooo... we can publish something!

They conclude, “in severely brain-injured patients undergoing RSI in the ED, succinlycholine was associated with increased mortality compared to rocurunium.”

This is totally nuts.

Regardless of the crazy analysis, all of the difference could easily be attributed to unmeasured confounding. This was not a randomized trial; therefore the patients given sux were very likely sicker.

Most experienced airway experts will tell you that they reach for sux when they want very rapid intubating conditions in sicker patients as compared to other neuromuscular blockers. Correcting for confounding (especially with a retrospective database) is far from an perfect science.

In the end, this is a small study with a high risk of bias that comes to unbelievable conclusions. Do we really believe a number needed to kill of 5 for succinylcholine in severe TBI!?!

There is so much I haven’t mentioned... the crazy power calculation, mixing association with causation, confusing subgroup analysis with stratification, neglecting the details of biological plausibility etc.

In 2005, John Ioannidis published his famous paper, “Why most published research findings are false.”

This study is a case in point. On so many levels, it is just wrong.

At best, it might raise a hypothesis for prospective testing. However, NOBODY should be changing their practice as a result of this paper.

Covering:

Patanwala AE, Erstad BL, Roe DJ, et al. Succinylchoine is associated with increased mortality when used for rapid sequence intubation of severely brain injured patients in the Emergency Department. Pharmacotherapy. 2016;36(1):57-63.

http://www.ncbi.nlm.nih.gov/pubmed/26799349

(Special thanks to Dr Mark Reeves, FANZCA and Dr Ryan Radeski for providing me with some of their insights. However they take no responsibility for the terrible nature of this post.) 

Efficacy of nasal cannula oxygen as a preoxygenation adjunct in emergency airway management in healthy volunteers

Who would have figured that giving patients more oxygen during simulated emergency airway management results in better oxygenation?

Ok... I’m being overly cynical.

Some clinicians provide extra oxygen through nasal cannula in addition to either a nonrebreather (NRB) or bag-valve mask (BVM) prior to RSI. But does this really matter? Or is it just an extra step in an otherwise stressful situation that could be avoided?

This Australian study randomized 60 young healthy volunteers to either a NRB or BVM with or without a supplemental nasal cannula running at 10L/min. In addition, they also investigated whether the addition of a simulated mask leak changed the results.

The primary outcome was a comparison of end-tidal oxygen between the groups.

Results?

The addition of a nasal cannula to a NRB or BVM did not seem to do much unless there was a mask leak. The BVM achieved higher oxygenation than the NRB. (I don’t think the actual numbers are important, but if you are interested then click on the link to the abstract below.)

The major limitations of this study are obvious. 

Unless you are sadistic, healthy volunteers are not the patients we typical intubate in the ED. The primary outcome was a surrogate marker and not necessarily a meaningful patient oriented one. Looking at real morbidity would have required a much larger study of actual patients.

What should we take from this?

The addition of a nasal cannula might be beneficial (or not) when performing RSI in the ED. This is not great evidence and it probably doesn’t matter in the vast majority of patients. Sure, give it a try when you really want to maximize pre-oxygenation. Also make sure you have a good mask seal.

Pedantic adherence to a supplemental nasal cannula adjunct during RSI is probably silly. But depending on the situation it might make sense and probably won’t hurt.

Covering:

Hayes-Bradley C, Lewis A, Burns B, et al. Efficacy of Nasal Cannula Oxygen as a Preoxygenation Adjunct in Emergency Airway Management. Ann Emerg Med. 2015; Dec 31 [ePub]

http://www.ncbi.nlm.nih.gov/pubmed/26747218

An RCT of ultrasound guided hematoma block vs. procedural sedation for distal radial fracture reduction

This study sought to compare the efficacy of ultrasound guided hematoma block vs. procedural sedation (midazolam/fentanyl) for reduction of distal radius fractures in the ED.

The “primary” outcome was pain on a numerical rating scale recorded at 5, 10 and 15 minutes after reduction. Secondary outcomes looked at satisfaction, early/late complications and time to discharge from the ED.

I liked this paper, but it is impossible to overlook some of their sloppy methods and statistical analysis.  For example, “We don’t need no stinkin power calculation...”

Results?

They randomised 143 patients in to the two groups. In the end, the pain scores were quite similar. But time to discharge was significantly lower in the hematoma block group. And there were more adverse events in the procedural sedation group.

The limitations are several. Single site, only one type of procedural sedation, the outcome measures was perhaps dubious, and given small numbers we definitely can’t make conclusions about rare adverse events (i.e. infections.)

What do we take from this?

Effective hematoma blocks are probably just fine for the reduction of distal radius fractures. They are quicker, simpler, and avoid the nuisance of procedural sedation. (In my opinion, if you can do an “in-plane” ultrasound guided nerve block, then you should have no trouble using the same technique to do a hematoma block.)

Although not addressed in this paper, lots of ED’s in Australia are doing Bier’s blocks. There is no doubt they are highly effective in the reduction of pain. But they probably carry just as much, if not more hassle than a procedural sedation.

So the hematoma block? When done properly it is simple, quick & pretty darn effective. So break a leg (or arm) and give it a try... 

Covering: 

Fathi M, Moezzi M, Abbasi S, et al. Ultrasound-guided hematoma block in distal radial fracture reduction: a randomised clinical trial. Emerg Med J. 2015;32:474-477. 

http://www.ncbi.nlm.nih.gov/pubmed/25016389

Getting back to common sense with an acute pain titration protocol: “Do you want more pain medication?”

The Joint Commission (TJC) is the peak hospital accreditation body in the USA. In the year 2000, they mandated screening pain assessments.  Since then, pain has been considered the “fifth vital sign” and the numerical rating scale (NRS) has taken over ED’s around the world. “Rate your pain 0 to 10?” often bellows through the corridors of the ED. But is this practice asking the wrong question?

Out of the ashes of all this mess comes an interesting study from the Bronx, New York. Hey... fagitaboutit. As can be imagined, this is a very busy and underserved emergency department. So perhaps a pain protocol might be more effective in this setting.

They devised a prospective cohort study of adults with acute severe pain defined as requiring IV opiods. The protocol called for an initial 1mg of hydromorphone (equivalent to 7mg of morphine). About 30 minutes later they asked, “Do you want more pain medication?” This was repeated until they reached a maximum of 4mg of the drug.

They considered the protocol a success if at any time they declined the offer of more pain medication. If they got all 4mg and still wanted more, they failed.

As would be predicted, the success rate was very high. 205 of 207 (99%; 95%CI 97% to 100%) subjects achieved satisfactory analgesia. There were only very few adverse events.   

But this is not why I liked this paper...

They also explored the relationship to a request for more pain mediation with their reported pain score on the NRS.

Perhaps the most interesting part of this study was the results of this comparison. They plotted the relationship graphically. This showed large variability in pain scores when patients requested and declined additional pain medication.

So what are we to take home from all of this?

I think Dr Steve Green sums it up best in the accompanying editorial entitled, “The Numerical Scoring of Pain: This Practice Rates a Zero out of Ten.”

Dr Green’s conclusion is so good that I dare not paraphrase:

The numeric rating scale is helpful for pain research but is inaccurate and counterproductive for standard patient care. TJC mandates that pain be identified and addressed but does not specifically require pain scoring. What happened to the old-fashioned question such as “Are you in pain?” and “Do you want pain medication?” Pain scoring in electronic medical records could be more appropriately replaced with a single yes/no checkbox per encounter: “Was pain evaluated and addressed?” As noted by Walid et al, “The use of the 0-to-10 pain scale... as a sole measure of pain assessment undercuts compassionate communication.” Let’s evaluate pain as the complex, nuanced symptom that it is, rather than oversimplifying it as a single integer of dubious merit. Routine pain scoring is a proven failure and should be abandoned.

Wow... perhaps he should tell us what he really thinks.

Covering:

Chang, AK, Bijur PE, Holden L, et al. Efficacy of an Acute Pain Titration Protocol Driven by Patient Response to a Simple Query: Do You Want More Pain Medication? Ann Emerg Med. 2016;67:565-72.

http://www.ncbi.nlm.nih.gov/pubmed/26074387

A single dose of oral dexamethasone is probably just as good as 5 days of oral prednisolone for acute asthma

Oh... this would make life simpler, so I hope it works.

Dexamethasone has a duration of action up to 72 hours. Therefore several researchers have considered it as a potential agent to streamline the treatment of asthma.

This was a triple blind “non-inferiority” trial looked at single dose of dexamethasone 12mg vs. the usual five days of prednisone (prednisolone can be considered the same). Included patients were adults with mild to moderate asthma discharged home from the ED.

The primary outcome measure was relapse as defined by an unscheduled return to a health care provider within 14 days.  (Ok... this outcome measure is not perfect but probably represented a pragmatic compromise in the design of the study.)

It was powered to an 8% difference between groups.

Why 8%?

Yes, it’s fairly arbitrary. And they provided some nebulous justification. 

Results?

They kind-of, sort-of, almost met inferiority. There was a 2.3% (95% CI -4.1% to 8.6%) absolute difference in the primary outcome of relapse at 14 days, but the confidence interval just barely crossed their pre-specified arbitrary margin of non-inferiority.

So this officially is a negative study. But I don’t really think so. Nor do the study investigators.

I’ll bet the authors are kicking themselves for not ensuring the proper statistical power in order to narrow down their confidence interval. Statistically speaking, the probability of the truth is always closer to the point estimate.  

I also bet the authors are disappointed they didn’t pick a non-inferiority margin higher than 8%!

Either way, I think this is more evidence to suggest that a single dose of dexamethasone is probably just as good as the usual course of prednisone. As we get more evidence, we will surely get a better idea of the true efficacy.

For now, stock up on the dex!

Covering:

Rehrer MW, Liu B, Rodriguez M, et al. A Randomized Controlled Noninferiority Trial of Single Dose of Oral Dexamethasone Versus 5 Days of Oral Prednisone in Acute Adult Asthma. Ann Emerg Med. 2016;67:593-601.

http://www.ncbi.nlm.nih.gov/pubmed/27117874

Intramuscular Ketamine as a Rescue Treatment for Acute Behavioural Disturbance (after getting droperidol) in the ED

This Australian study looked at the use of a knockout dose of ketamine (4-6mg/kg) for the sedation of acute behavioural disturbance in the Emergency Department.

Their protocol generally called for a couple doses of droperidol. This was followed by ketamine if sedation was not adequate.

Out of 1296 patients, they only had to resort to ketamine in 53 (4%) patients.

The ketamine seemed to work and the authors liked it.

The few failures were put down to inadequate low doses of ketamine. There were only very few minor adverse events.

The authors conclude ketamine appears to be a reasonable third-line agent in the sedation of patients with acute behavioural disturbance.

Which is fair enough, but…

This study was not exactly high science or great quality evidence of anything. But at least it demonstrates that the practice of using ketamine for behavioural disturbance is not entirely a fringe concept.

The numbers are small and cannot make claims about safety. This would require much larger numbers to find rare adverse events. Nevertheless, the EM community has had vast experience with ketamine and we generally regard it as being very safe.

Would adjunctive benzodiazepines changed things? A good number of the patients with behavioural disturbance are amped up on psychostimulants and respond well to benzo, benzo, benzo. So who knows?

The fantastic accompanying editorial by Dr Steve Green was entitled, “Let’s Take ‘Em Down witha Ketamine Blow Dart.” Dr Green (aka Dr Ketamine) is largely regarded as the world’s expert on ED use of this drug. He seems to think this is reasonable and it is difficult to argue with such an intellectual badass.

So bring on the knockout dose (4-6mg/kg IM) of ketamine. To emphasize, it should NOT be a first line agent. But it may represent the best option where there truly is a significant risk to patient and caregivers and other options have failed.

Covering:

Isbester GK, Calver LA, Downes MA, et al. Ketamine as a Rescue Treatment for Difficult-to-Sedate Acute Behavioral Disturbance in the Emergency Department. Ann Emerg Med. 2016;67:581-587.

http://www.ncbi.nlm.nih.gov/pubmed/26899459

A 1-hour rule out MI protocol in the era of high sensitive troponin assays; ready for prime time

Studies of the high sensitive troponin assays all demonstrate the same thing. Patients will rule-in for MI much quicker compared to the old conventional assays. The vast majority will do so within a few hours of onset of symptoms.

The lead author of this study, Dr Tobias Reichlin has been working his way down the impact factor ladder with his ongoing research. His most recent offer has been published in the Canadian Medical Association Journal. But don’t let this fool you. This study is important and the final nail in the coffin for the 3 or 6 hour rule-out. 

This multicentre study enrolled 1320 patients presenting to the ED with suspected MI. The algorithm they attempted to validate used a baseline and 1 hour high sensitive troponin T. They looked at the absolute values in addition changes at one hour. Two independent cardiologists adjudicated the final diagnosis with access to all of the information (including troponin values... so ok, there was some incorporation bias with the gold standard.)

Results: The sensitivity and the negative predictive value for ruling out MI was 99.6% and 99.9% respectively. This made up about 60% of their cohort. The rule-in rate was 17%. They also had an indeterminate category that only made up one quarter of the patients overall. I have cut and pasted the algorithm below.

These results are one in a long line of studies demonstrating the same thing. Consistency in the literature is always compelling. The time has come to change our local protocols to allow for the safe rapid rule-out strategy in suitable patients.

Having said this, there is one strong word of caution. Beware the early presenters. Common sense would dictate that the person developing chest pain in the parking lot of the hospital should not undergo a one hour rule-out.

Unfortunately, the manuscript of this paper did a terrible job of describing the proportion of the early presenters. A vague and unhelpful mention was made in the on-line only appendix.

Another contention was the “data snooped” cut-off’s of 12ng/ml and 52ng/ml as their low and high cut-off’s for rule-out or rule-in MI. Of course this came from the earlier derivation study, but I think that 14ng/ml and 50ng/ml should be just fine. This certainly should make it more user friendly without having a substantial impact on test characteristics. Of course this is just my opinion, so there might be differing opinions.

If you are waiting for the AHA/ACC to provide updated guidelines then don’t hold your breath. The Americans have been very slow adopters of the high sensitive troponin assays. It is now up to us to determine what is clearly ready for prime time.

Covering:

Reichlin T, Twerenbold R, Wildi K, et al. Prospective validation of a 1-hour algorithm to rule-out and rule-in acute myocardial infarction using a high sensitive cardiac troponin T assay. Can Med Ass J 2015;187:1-10. doi: 10.1503/cmaj.141349

http://www.ncbi.nlm.nih.gov/pubmed/25869867

Link to the algorithm:  http://www.ncbi.nlm.nih.gov/pmc/articles/PMC4435896/figure/f1-187e243/

Cardiac catheterization for survivors of out of hospital cardiac arrest; on shaky ground?

This well done review and meta-analysis examined the current evidence in support of cardiac catheterization for survivors of out of hospital cardiac arrest.

Let’s cut right to the chase.

For the primary outcome, the acute catheterization group was clearly superior with almost 60% vs. 30% in hospital survival (Odds ratio 2.77 95% CI 2.06-3.72). Survival with good neurological outcome was nearly the same.

Of course the authors conclude that early coronary angiography in patients following OHCA is associated with improved outcomes... which is true of course.

But is all of the evidence on shaky ground?

Perhaps.

All of the studies included in this meta-analysis were observational in nature. From a pure evidence based standpoint, it is possible that all of the difference in survival could be due to selection bias and confounding rather than the real efficacy of the intervention.

All observational studies are challenged by these issues. The best way around this is to conduct a properly blinded and randomized clinical trial. Of course this is not always ethical or feasible.

But there are those who believe there is enough clinical equipoise to warrant a proper experimental trial. A quick look at www.clinicaltrials.gov demonstrates several centres (USA, Spain, Sweden, & Canada) are currently on to it. Let’s hope we get some better data.

Despite lack of definitive efficacy I’m not about to jump out of an airplane without a parachute. Currently, I think it is very reasonable to be aggressive with early angiography in suitable patients. This is especially for those with STEMI’s and/or presumed primary cardiac cause of arrest. 

In the future, let’s hope the ground doesn’t start shaking. 

Covering:

Camuglia AC, Randhawa VK, Lavi S, et al. Cardiac catheterization in associated with superior outcomes for survivors of out of hospital cardiac arrest: Review and meta-analysis. Resuscitation 2014;85:1533-1540. 

http://www.ncbi.nlm.nih.gov/pubmed/25195073

Outcomes of anatomical versus functional testing for coronary artery disease; To CTA or not to CTA... that is the question

A patient with no past history of CAD presents with new symptoms suggestive of cardiac disease. Should we get a CT angiogram (CTA) anatomic test or a functional test such nuclear stress testing, stress ECG or stress echo? Which test is better?

An even more difficult question is how do we measure which test is better? Should we focus on detection of CAD or should we look for outcomes that truly matter and are patient oriented? This is a difficult question to answer. At least these authors tried.

This study randomized 10,003 office based patients mostly in the USA to either initial anatomic or functional testing. The composite primary outcome measure was death, MI, hospitalization for unstable angina, major procedural complication, foot fungus and priapism. Ok, maybe not the last two.

Even with huge statistical power, there was no difference between the two groups. Both had very low rates of the composite outcome at 3% over a median follow up time of two years. However, more patients in the CTA group underwent revascularization 6% vs. 3%. Some would call this a 100% relative increase.

Does anatomical testing (CTA) find more false positives (overdiagnosis) and as such result in morbidity & increased cost from unnecessary treatment? I think these are reasonable questions.

In the end, the vast majority of these patients did just fine. This could be a reflection of the low risk patients in the USA that get included in such studies. The initial tests were positive for CAD in only about 10% of this study population.

How can this help us in the Emergency Department? I’m not so sure. But it is a great study that demonstrates an emphasis on patient oriented outcomes rather than simply looking at test characteristics.

The initial investigation of patients with suspected cardiac disease is high risk. I would imagine that doctors will be following local convention and protocol rather than contemplating philosophical matters at the bedside. This is just my opinion, so perhaps I’m wrong... comments?

Covering:

Douglas PS, Hoffman U, Patel M, et al. Outcomes of Anatomic versus Functional Testing for Coronary Artery Disease. N Engl J Med 2015;372:1291-300.

http://www.ncbi.nlm.nih.gov/pubmed/25773919

Garbage in and garbage out; A systematic review and meta-analysis of acupuncture for angina pectoris

We'll keep this brief...

This “evidence-based study” out of the Journal of Traditional Chinese Medicine used surprisingly good methods looking at the efficacy of acupuncture for a variety of cardiac problems.

But due to fatal flaws, the majority of the details and the conclusion to this paper are irrelevant. Nevertheless it does provide some great opportunity for learning & teaching critical appraisal of the literature.

This systematic review found 21 articles that investigated acupuncture for angina. Unfortunately none of them were blinded, had allocation concealment or had sham acupuncture arms. Therefore all of the proposed benefit could easily be explained by the theatrical placebo of acupuncture. All prior good quality studies of acupuncture using proper blinding have shown it is no better than placebo.

The paper does mention these methodology issues and go so far as to say “all studies were assessed as having a high or moderate risk of bias.” Had they stopped here everything would have been fine. But they made the tragic mistake of proceeding to a meta-analysis and making ludicrous conclusions.

There are some statistical truths. No amount of analysis can remove bias from a study (simple confounding is a different matter). Nor can bias be overpowered by increasing the study size.

Put another way, they completely missed the crucial backbone of meta-analysis. If all you find is rubbish, you don’t combine it in a blender and expect a golden egg to appear. You’ve still got rubbish.

Covering:

Chen J, Ren Y, Tang Y, et al. Acupuncture therapy for angina pectoris: a systematic review. J Tradit Chin Med 2012;32(4):494-501.

http://www.ncbi.nlm.nih.gov/pubmed/23427379