Sunday 30 August 2015

The End of Tamsulosin (and Nifedipine) for Ureteral Colic

The evidence for offering tamsulosin to patients with ureteral colic was never very robust. It was comprised mostly small single centre studies of dubious quality. Nevertheless, tamsulosin seemed to be embraced by the urologists who then demanded that we give it to our patients being discharged from the ED. I was always a bit uneasy that this would be of any benefit and often thought of it as a stalling tactic by my consulting colleagues. I also knew that patients would bear the expense of the prescription not covered by insurance (Australian PBS).

We now have the most definitive evidence to show that tamsulosin does not work as medical expulsive therapy for ureteral colic. We can officially stop the silliness.

This multicenter, randomized trial randomized 1167 patients in the UK to either tamsulosin, nifedipine or placebo. The primary outcome was the proportion of patients who did not need further intervention for stone clearance within 4 weeks of randomization.

Say what you will about the primary outcome measure but at least it is pragmatic and does not mandate further radiation by serial imaging.

The bottom line? In all treatment groups, 80% needed no further intervention at 4 weeks. There were no real trends of any benefit anywhere. Tamsulosin and nifedipine did nothing to facilitate stone passage.

Of course one could get picky about the study design, secondary outcome measures, safety measures, external validity and other details. But the message is pretty darn clear. Medical expulsive therapy is now dead.

I believe the authors summarize best:

“Seekers of evidence often have to decide whether to base treatment decisions on a meta-analysis of several small low-quality trials typically showing larger treatment differences, or one large high quality trial with a smaller effect size or finding no effect... Our judgment is that the results of our trial provide conclusive evidence that the effect of both tamsulosin and nifedipine in increasing the likelihood of stone passage as measured by the need for intervention is close to zero. “

“...further trials involving these agents for increasing spontaneous stone passage rates will be futile.”

This is about as good as it gets.

Pickard R, Starr K, MacLennan G, et al. Medical expulsive therapy in adults with ureteral colic: a multicentre, randomised, placebo-controlled trial. Lancet 2015;386:341-349.

Saturday 29 August 2015

Point-of-Care Ultrasound for Detection of Acute Pulmonary Edema: A Meta-analysis

Picture this.

A 60 year old male with a prior history of CHF and COPD is brought to your ED by ambulance in respiratory distress. On exam, he looks sick and is wheezing.  While waiting for a portable x-ray, you give him sublingual nitrates, frusemide, salbutamol (albuterol), steroids and morphine as you really have no idea what the heck is going on. BiPAP is getting set up. But what if you had a tool at the bedside that could give the diagnosis in seconds?

Bring on lung ultrasound. Answer in seconds? Well, maybe.

This systematic review and meta-analysis tried to determine the sensitivity and specificity of ultrasound using B-lines in diagnosing acute cardiogenic pulmonary edema (ACPE) in patients presenting to the ED with acute shortness of breath.

The authors conducted an impressive study with an excellent search of the literature, quality assessment and analysis of the data. This was really well done.

This study design is good for generating statistical power and getting summary estimates. However the Achilles heel of any meta-analysis is publication bias and the potential for the garbage-in and garbage-out phenomenon. No matter how much one performs a beautiful study, one is always limited by the quality of the original data. Put another way, two third graders do not make a sixth grader.

Skipping right to the results- they found seven studies to combine. After some serious number crunching they gave summary estimates of the sensitivity to be 94% (95% CI 81-98%), specificity 92% (95% CI 84-96%), positive likelihood ratio 12.4 and negative likelihood ratio was 0.06.

These are impressive numbers! But unfortunately, there are some big limitations.

Ultrasound does not have “fixed” test characteristics. Studies of ultrasound are usually done by a group of experts in motivated centres. But in real life, the sensitivity and the specificity change with each person that picks up the probe as experience is variable. So it is a bit silly to report results to a couple of decimal places when it is really going to change substantially according to operator experience. In addition, I would imagine there would be some spectrum bias- i.e. the test works better in patients that are sicker.

This meta-analysis included only two studies conducted in Emergency Departments. Both were small and heterogeneous. What if there were other unpublished small studies that were negative? The results could be quite different.

In the end, we really don’t know the answer. But I think it probably works ok with experienced point-of-care sonographers in with respiratory distress.

More research on this application of ED ultrasound would be fantastic but unfortunately will suffer from many of the limitations noted above. (I didn't even mention issues with the gold standard). It may be that we will remain stuck with limited good quality evidence. Therefore we will rely on experience, common sense and consensus. Eminence based medicine anyone? And while you're there pass me the ultrasound machine.

Deeb, M, Barbic Skye, Featherstone R, et al. Point-of-care Ultrasonography for the Diagnosis of Acute Pulmonary Edema in Patients Presenting with Acute Dyspnea: A Systematic Review and Meta-Analyisis. Acad Emerg Med 2014;21:844:852

Friday 28 August 2015

Antibiotic Therapy for Appendicitis- Time for a Paradigm shift?

The answer is yes... probably

Surgical treatment of appendicitis has traditionally been as linked as fish and chips (or perhaps burgers and fries). But it looks like the steadfast notion is finally being demolished.

There have been a bunch of studies over the past decade looking at the success of antibiotic therapy alone for the treatment of appendicitis. These small studies with mixed research methods have pretty much all said the same thing. Most of the time you can get away with antibiotics but a small proportion of patients will eventually get their appendix out anyway over the ensuing few months due to recurrence.

Now along comes the largest randomized trial trying to definitively answer the question. This was a non-inferiority RCT out of Finland that enrolled patients aged 18-60 with CT proven uncomplicated appendicitis. Patients were randomized to antibiotics alone vs. traditional appendectomy. The antibiotic group got three days of IV ertapenem (a big gun carbapenem) followed by a week of oral levofloxacin and metronidazole. Shortly afterward these patients had C diff diarrhea and disulfuram reactions... why would I make this up?

The primary outcome of importance was success of antibiotic treatment without having to get an appendectomy during a one year follow up period. They chose a fairly arbitrary non-inferiority margin of 24% but the authors seem to appropriately dismiss this in the end anyway.

As expected, the surgical group did pretty well. They had the expected minor complications and these Finnish patients were back to work in a median of 19 days. None of their appendixes grew back.

The antibiotic group also faired pretty well and were back to work in 7 days. But by the end of the one year follow up, 27% ended getting their appendixes out anyway.

One could interpret the outcomes in a couple of ways. Is 73% success by one year good enough? What do you think? Or probably more importantly, what do our patients think?

Regardless of what health care professionals believe, I believe it is time for patients to become involved in shared decision making. The data is now fairly robust and can’t be ignored any longer. It is time for us to consider non-surgical treatment for uncomplicated appendicitis as a valid treatment option and offer this to our patients.  

(As an aside, we probably don’t need to resort to such crazy heavy hitting antibiotics. Some studies have just used oral Augmentin. But in the end, this will be a judgement call and extrapolating from existing literature.)

Old habits die hard. This is especially true for surgeons who love their knives. After all, “cold steel heals.” But perhaps the push needs to come before the surgeons get involved. Is 73% good enough? Let’s ask our patients before we call man with knife.

Salminen P, Paajanen H, Rautio T, et al. Antiobiotic Therapy vs. Appendectomy for Treatment of Uncomplicated Acute Appendicitis. The APPAC Randomized Clinical Trial. JAMA. 2015;313(23):2340-2348.

Thursday 27 August 2015

MR CLEAN: A Randomized Trial of Interventional Stroke therapy (or rescue therapy for highly selected stroke patients after getting tPA)

As a medical community, we are clearly focused on trying to do something to help those with acute ischemic stroke. There is no doubt that this is a common and devastating disease but an effective up ED treatment to benefit the majority of patients has met with failure.

This is not for lack of trying.

Thrombolysis clearly has mixed reviews and is only indicated in a very small percentage of patients. Prior interventional trials published in 2013 were negative. But times change and perhaps technology improves. So along comes Mr Clean.

This was an RCT performed in 16 centres in the Netherlands comparing interventional treatment to “usual care.” But to be clear from the beginning, usual care meant tPA the vast majority of times. Patients were enrolled within 6 hours of onset of symptoms and had to have a proximal clot demonstrated by formal imaging.

90% of all the patients got tPA at a median time of about 90 minutes from stroke onset before they were randomized in to the study. In fact, the median time to randomization was 200 minutes. Therefore this study really was looking at interventional therapy as a rescue option after tPA. Do you think they would have proceeded with interventional therapy if the patient was demonstrating significant early improvement in the ED? Of course not. This was a sicker and highly selected group of patients that did quite poorly in the end.

The primary outcome measure was looking at the odds ratio in an ordinal shift analysis of the modified Rankin score at 90 days. You got that? This type of analysis has been all the rage in the stroke literature recently as it provides some statistical efficiency to find differences. The only challenge is most clinicians have no idea how to interpret this result. How do we translate this outcome measure in to a meaningful one that we can use when engaging in informed decision making? But to be fair, they did report simpler secondary outcome measures.

The results? It seemed to work as in this highly selected patient population in these motivated study centres. The odds ratio for the primary outcome was 1.67 (95% CI 1.21 to 2.30). Who really knows what that means?  There was an absolute difference of 13.5% in the rate of functional independence (mRs 0 to 2) in favour of the intervention 32.6% vs. 19.1%. So, a number needed to treat of about 7.

What should we take home from this? Interventional therapy might work in a few highly selected patients with proximal clots that fail thrombolysis. Of course the patient must present to an experienced centre that provides this high level of service. One might be tempted to extrapolate these results to other patient populations. But caution should certainly be in order as prior studies of less selected patients have not met with positive results. Beware indication creep.

In the end, this really will not help many patients. On average, this study enrolled about 10 patients per year per centre (500 patients over 3 years in 16 centres). Should we be focusing huge amounts of time, effort and money to benefit so few patients? Should we be focusing efforts elsewhere? Who knows?

Berkhemer OA, Fransen PSS, Beumer D, et al. A Randomized Trial of Intraarterial Treatment for Acute Ischemic Stroke. N Engl J Med 2015;372:11-20.

Thursday 7 May 2015

Epistaxis treatment using injectable form of tranexamic acid topically: why not

 I've done my share of bootlegging. Up 'ere, if you engage in what the federal government calls 'illegal activity,' but what we call 'just a man tryin' to make a livin' for his family sellin' moonshine liquor,' it behooves oneself to keep his wits. Long story short, we hear a story too good to be true... it ain't.       Lt Aldo Raine “Inglourious Basterds” 2009

This study out of Tehran, Iran looked at using the injectable form of tranexamic acid (TXA) to control uncomplicated anterior epistaxis.

This was a single centre unblinded randomized controlled trial. In the experimental group a 15cm piece of cotton pledget was soaked in tranexamic acid (500mg/5ml) and was inserted in the nostril. It was removed shortly after it was determined that the bleeding had stopped. The control group had standard anterior nasal packing that was removed after 3 days.

216 patients were randomized and there was no loss to follow up. The methods did not really specify a primary outcome but they did report numerous “efficacy variables.”

Within 10 minutes of treatment, the bleeding had stopped in 71% of the TXA group compared with 31% of the control. In addition, 95% of those treated with TXA were discharged from the ED in 2 hours or less compared to 6% in the controls.

This treatment effect is way too good to be true. There must have been some systematic bias that accounted for the profound differences in early discharge of the TXA group. This is never really explained in the discussion section of the paper. 

The numerous grammatical errors in the text do make the paper appear a bit sloppy and hard to read. It should be the job of the journal editor to ensure that these errors do not make it to print. But heck, this isn't exactly a high impact journal.

Unfortunately, this study excluded complicated epistaxis. These are precisely the patients who may require some extra finesse and it would be nice to know if there was some efficacy of TXA in this population.

Despite all of this, I think the notion of topical TXA treatment for epistaxis is compelling. Many other large studies over decades have shown it to be reasonably safe. Not only is TXA unlikely to cause harm but it is dirt cheap. We have vials of TXA in my ED that cost $6 a vial.

The bottom line? I think it is reasonable to try the injectable form of TXA topically as an adjunct to help control epistaxis. Why not?  But please don’t expect the miracle cure that this paper purports.


Zahed R, Moharamzadeh P, AlizadehArasi S, et al. A new and rapid method for epistaxis treatment using injectable form of trenexamic acid topically: a randomized controlled trial. Am J Emerg Med 2013; 31:1389-1392.

Yes you can perform RSI through an intraosseous line

Not every research question can be answered by a randomized controlled trial. Often they are not feasible or ethical and out of necessity other study designs are utilized.  I like this clever little study investigating whether one can use an intraosseous line for induction of anaesthesia.

Where else would you conduct this study other than Afghanistan? This was a prospective observational study of previously healthy young patients (mostly soldiers) who had just suffered severe trauma. Upon presentation to a British combat hospital, 34 patients underwent RSI using an IO line.

These patients were quite sick with a median injury severity score of 25. As expected, the predominant mechanism of injury was blast.

First pass intubation success rate was 97% (95% CI 81%-100%) with mostly great visualization of the cords.

One could reasonably argue that this study has some limitations. The numbers were small. Mostly young previously healthy soldiers would make external validity an issue. Perhaps they were looking at the wrong primary outcomes and they should have focused on time to intubation and/or relaxation.

But given the big picture, I think they put in a decent effort. Research on resuscitation is always challenging and getting numbers is hard. How many IO lines have you put in? Most health care practitioners would have other priorities when caring for a very sick patient (who has just been blown up) rather than focusing attention on ticking boxes on a study form. In the end, I think their outcome measures were quite pragmatic.

Sure, this study is not definitive evidence but I think it is enough to suggest the efficacy of the IO route for rapid sequence induction.


Barnard EBG, Moy, RJ, Kehoe AD, et al. Rapid sequence induction of anaesthesia via the intraosseous route: a prospective observational study. Emerg Med J. 2014 Jun 24. pii: emermed-2014-203740. doi: 10.1136/emermed-2014-203740. [Epub ahead of print]

Wednesday 6 May 2015

Research Misconduct Identified by the US FDA Remains Hidden- Fraud Under the Rug

Every year the US Federal Drug Administration inspects several hundred clinical sites performing biomedical research on humans. They classify their inspections mostly as “no action indicated” but occasionally discover a severe problem they label as “official action indicated” or OAI.

The worst of these OAI’s could include submission of false information and/or failure to report adverse events.

The author of this paper is a profession or journalism from NYU with a special interest in research misconduct. With much of his graduate students doing the leg work, he attempted to find the OAI’s, describe the violations and determine whether subsequent published articles acknowledged the FDA’s findings. One would think that the FDA had ethical and or legal obligations to make these serious infractions public.

Without going in to too many specifics, they found it quite difficult to even find the OAI’s as there is no public repository for this information. In addition, the FDA reports they discovered were highly redacted. This made it hard to determine what infractions were related to actual articles in the peer reviewed literature. Nevertheless they found 78 publications that resulted from trials in which the FDA found significant violations. How many of these papers mentioned the FDA’s concerns? Only 4%.

There are numerous examples of transgressions listed in the paper. My favourite was a researcher who pled guilty to fraud and criminally negligent homicide in the conduct of a trial. She was sentenced to 71 months in prison. Although this was clearly documented by the FDA, there is no mention of any of this in the published studies based on her trial.

How could all of this happen? It turns out the FDA does not officially make OAI’s public. They don’t tell journal editors nor do they link their discovered information back to The author of this paper makes some very sensible suggestions on how the FDA might improve their processes. Fortunately it looks like they might be listening.

All of this might sound a bit like a conspiracy theory. But fraud in medical research is a real entity and very easy to execute. There are strong incentives in our “publish or perish” climate to resort to devious means of research. This says nothing of bias, spin and the billions of dollars that pharmaceutical industry stand to profit from research that goes their way.

What are we to take home from all of this? At the core of biomedical research lurks a perverse incentive encouraging fraud and it happens more than we like to know. Be sceptical of studies that look to good to be true. Sorry, but sometimes data is simply made up.

Hopefully the FDA will change their ways.


Seife C. Research Misconduct Identified by the US Food and Drug Administration; Out of Sight, Out of Mind, Out of the Peer-Reviewed Literature. JAMA Intern Med 2015 Apr 1; 175(4):567-77.

Does over-reliance on pulse oximetry lead to increased hospitalization of infants with bronchiolitis?

This was a unique study out of a single paediatric care ED in Toronto, Canada. The authors were obviously of the opinion that they were admitting too many children to hospital that could otherwise go home based on low pulse ox readings. Does a single number change our practice?

The study design involved a little deception. (Who doesn't like a little deception?) Infants with moderate bronchiolitis were randomized in a double blind fashion to getting an accurate pulse oximetry measurement vs. one that displayed a result 3% points higher than the real measurement. In case you are wondering, they had the manufacturer alter the machines and they bribed the ethics committee (okay... I made that last bit up).

The primary outcome was hospitalization within 72 hours. There were other common sense secondary outcome measurements.

213 infants were randomized and there was no loss to follow-up. 41% of patients with the true oximetry group were hospitalized as compared to 25% in the altered oximetry group. Absolute difference 16% or NNT to prevent a hospitalization is 7. The overall strategy seemed pretty safe. Wow, pretty compelling results.

But before you consider throwing away your pulse oximeter, consider the following. The mean true pulse ox reading in all of the patients enrolled was about 97%. Very few of these infants were really that sick with a mean respiratory rate about 50. Only 28 infants in this study had true readings below 94%. There probably is no problem when you are considering a pulse ox of 97% being inaccuragely displayed as 100%. So this study is clearly not powered to investigate safety.

Nevertheless, I think this study is quite interesting and emphasizes a key point. Are we too reliant on single numbers when it comes to patient treatment decisions? The answer is probably yes.


Schuh S, Freedman S, Coates A, et al. Effect of Oximetry on Hospitalization in Bronchiolitis. A Randomized Clinical Trial. JAMA. 2014;312(7):712-718.

Friday 30 January 2015

Is Epinephrine (Adrenalin) During Cardiac Arrest Associated with Worse Outcomes?

Answer: yes of course.

But does it cause worse outcomes? Who knows- and this study does not help us find the answer.

This was registry review over a 12 year period at a single centre in Paris designated as a “cardiac arrest receiving hospital.” They looked at non-traumatic out of hospital cardiac arrest with ROSC. They compared the group that got adrenalin to those that didn't. The primary outcome measure was favourable neurologic outcome at discharge from hospital.

As you could guess, the cohort that got adrenalin was sicker in every possible way. They were less likely to be witnessed arrests, less bystander CPR and less likely to have initial shockable rhythms. By their very nature, they were more prolonged arrests.

Therefore it should come as no surprise that the adrenalin group did much worse. Only 17% of the adrenalin group had a good outcome vs. 63% that did not get adrenalin. Of course the authors recognized this bias and performed all kinds of adjustments, regression analysis, propensity modelling and bootstrapping. When was the last time you bootstrapped?

Given the study design, these adjustments are all very appropriate. But it should be emphasized that a lot of assumptions go in to this analysis and it is far from perfect.

After adjustments, the authors conclude that the use of adrenalin was negatively associated with favourable neurological outcome. They were careful not to address causation and rightfully suggest further study.

Should this study change our practice? No.

This was not an RCT and can really only raise a hypothesis for further study. I think a properly powered RCT would certainly be feasible. But the late Ian Jacobs tried this in Australia and ran in to a huge political & “ethical” roadblock. Nevertheless, this is more evidence that suggests that adrenalin may cause more harm than benefit.  I hope we will find a definitive study one day.


Dumas F, Bougouin W, Geri G, et al. Is Epinephrine During Cardiac Arrest Associated with Worse Outcomes in Resuscitated Patients. J Am Coll Cardiol 2014;64:2360-2367.

Delayed Sequence Intubation: We did it, we liked it and thought it was cool

Congratulations to Dr Scott Weingart for putting his money where his mouth is and publishing something that is genuinely challenging to study.

How would we ideally design a study to look at the efficacy of DSI? Would we do a large blinded randomized trial comparing DSI to standard rapid sequence intubation with a primary outcome of mortality? Such a study would be near impossible to conduct as it would be totally unfeasible to recruit such large numbers and couldn't be blinded. Therefore we do the best we can.

This study was not an RCT but rather a prospective observational study in a convenience sample of patients in whom DSI was thought to be indicated. They were all given ketamine to facilitate oxygenation before intubation. The primary outcome was improvement in the oxygen saturations during DSI.

In general, it looks like DSI works. Saturations increased from about 90% up to 99% just prior to intubation. There were even two patients with asthma where intubation was avoided.

Critics might argue that this was not a trial, had a convenience sample with small numbers and used a non-patient oriented outcome measure. But good luck finding better evidence! Three large hospitals were only able to recruit a total of 62 patients over a year and a half. It would probably take me two hundred years to recruit enough patients at my hospital to conduct a properly powered RCT looking at small changes in patient oriented outcomes.

I think this is enough evidence to change practice. I doubt we will ever get better data. It seems to work and is probably safer than standard RSI in suitable patients. Yes, this study is far from hard science but I think it is a game changer. Thanks Scott.


Weingart SD, Trueger NS, Wong N, et al. Delayed Sequence Intubation: A Prospective Observational Study. Ann Emerg Med 2014 Oct 23. pii: S0196-0644(14)01365-1. doi: 10.1016/j.annemergmed.2014.09.025. [Epub ahead of print]