Lunacy in a tertiary ED: A study of the association between moon cycles and violence

Of course, we have all heard the full moon makes people barking mad and creates chaos in the ED.

“It must be a full moon!”

This study out of Melbourne looked at ED patient records over 3 years and compared the rate of “occupational violence and aggression” with the lunar cycle divided into quarters; new moon, first quarter, full moon and third quarter. Then they performed logistic regression to determine the association between the cycle and rates of violence.

In the end, they had 184,059 patients who presented to the ED over three years. It turns out that violence and aggression was NOT associated with a full moon but it was statistically associated with the first quarter (adjusted OR 1.38; P<0.01) and the third quarter (adjusted OR 1.29, P=0.03).

Well, there you have it…

In the discussion, the authors provide physiologic justification for the observed association based on some brilliant quotes from “prominent astrologers Dana Gerhardt and Dane Rudhyar.”

But the rational side of us knows this is completely nuts… just as we know that the transit of Venus doesn’t cause urinary retention and a meteor shower doesn’t cure syphilis.

This article appeared in Emergency Medicine Australasia. It did not appear in a predatory journal or the Christmas edition of BMJ. It was delivered in “dead pan” without even a hint of a wink at the end.

But the authors knew exactly what they were doing. And it provides us with a couple of valuable lessons.

Statistics can get things wrong.

I’m sure if the authors looked at the association of astrological birth signs (i.e. ISIS-2) with violence they would have found some statistically significant results; Capricorn and Leo were hot heads, but Gemini calm as a cucumber.

We need to be reasonably skeptical of the medical literature. Much of what gets published turns out to be false. 

Thanks to these authors for getting it right… wink… wink…

 

Covering:

Teung T, O’Reilly G, Mitra B, Olaussen A. Lunacy in a tertiary emergency department: A 3 year cohort study of the association between moon cycles and occupational violence and aggression. Emerg Med Aus. https://doi.org/10.1111/1742-6723.13601

 

 

  

Comparison of oral ibuprofen and acetaminophen with either analgesic alone for pediatric patients with acute pain. A crash landing...

You would think we should know the answer to this question already. But officially we don’t, and this paper adds absolutely nothing to our understanding.

This single-centre randomised, double-blind trial compared the analgesic efficacy of a combination of ibuprofen (10mg/kg) plus acetaminophen (15mg/kg) to either medication alone for the treatment of mostly acute traumatic pain in children. 

The primary outcome was pain scores at 60 minutes.

They concluded that the reduction in pain scores was similar between all groups. No difference...

The study design was quite good. But like a plane with no wings, there was a fatal flaw.

They only included 30 patients in each treatment arm!!!

Huh?

They provided a crazy power calculation, but it clearly does not pass the sniff test.

30 patients would have only enough power to find large changes in treatment effect making this at high risk for a type II error- or a false negative study. (A quick check of Clinicatrials.gov shows the study was originally intended to enrol 125 patients in each arm.)

I’m surprised the ethics committee approved such a study as it could never adequately answer the research question it proposed. I’m also surprised it got published, albeit in a lesser impact factor journal.

I strongly suspect the peer reviewers snuck the last sentence in to the abstract, “…but the trial was underpowered to demonstrate the analgesic superiority of the combination of oral ibuprofen plus acetaminophen in comparison with each analgesic alone.”

If this was the case, then why was the study conducted?

 

Covering

Motov S, Butt M, Masoudi A, et al. Comparison of oral ibuprofen and acetaminophen with either analgesic alone for pediatric emergency department patients with acute pain. J Emerg Med. 2020;58:725-732.[Link to article]

An RCT comparing antibiotics vs. surgery for appendicitis- the CODA trial

This is a big deal… the largest RCT comparing antibiotics vs. surgery for appendicitis and has closed the lid on this research question.

This non-blinded, pragmatic trial included adults with mostly image proven appendicitis in 25 centers in the USA. They excluded sick patients with shock, diffuse peritonitis, severe phlegmon, free air (microperforations were ok), neoplasm a few other things.

The antibiotic group got IV for 24 hours followed by oral tablets for 10 days.

The primary outcome was an overall health questionnaire at 30 days. Secondary outcomes were rate of appendicectomy in the antibiotic arm, complications, return to work etc.

The decision to perform appendicectomy in the antibiotic arm was up to the treating clinician.

Results?

1552 patients were enrolled from May 2016 to February 2020.

Antibiotics were non-inferior to appendectomy based on the 30-day health status. In the antibiotic group, 29% underwent appendicectomy by 90 days. (Those with appendicoliths were more likely to eventually get surgery). Half of the patients randomized to antibiotics were discharged from the Emergency Department!

I would imagine that the rate of appendicectomy could have been lower in this study given it was unblinded… the surgeons struggling to put their scalpels down after decades of surgical dogma.

Of course, this is not the first RCT’s looking at antibiotics for appendicitis. The message is consistent and it is clear where we stand. Antibiotics successfully treat acute uncomplicated appendicitis, but a small percentage (30-40%) of patients eventually get their appendix out.

It is now evident that we need to present patients with treatment options for appendicitis in a shared decision-making process

Yes, old habits die hard. But kneejerk surgery for appendicitis is now a stinking corpse.

 

Covering:

Flum DR, Davidson GH, Monsell Se, et al. A Randomized Trial Comparing Antibiotics with Appendectomy for Appendicitis. N Engl J Med. 2020 Oct 5. doi: 10.1056/NEJMoa2014320. Epub ahead of print. PMID: 33017106. [link to article]

Haloperidol for the treatment of headache in the Emergency Department... better than nothing

 

Usually randomized, double-blind, placebo-controlled trials are considered the best study design to truly answer a research question. But sometimes they are inappropriate.

Do you ever think we will see placebo used in a study on bacterial meningitis?

When a standard well accepted treatment exists, it is usually thought unethical to use placebo. This is where non-inferiority or equivalence trials come in- i.e. comparing a new drug to existing therapy.

But perhaps they grown them tougher in Michigan…

This randomized, double-blind, placebo-controlled trial compared haloperidol 2.5mg IV to matching placebo for ED patients with acute headache. The primary outcome measure was the change in VAS at 60 minutes.

Results?

118 patients were enrolled at a single large ED in Michigan. The trial was stopped after an unplanned interim analysis. A little bit naughty…

The reported pain dropped 4.77 units in the haloperidol group and only 1.87 in the placebo arm. Treatment with rescue ketorolac 30mg IV was required in 78% of the time with placebo and 31% with haloperidol. There were few side effects of haloperidol that were easily treated.

Ok, I willing to believe that haloperidol is better than nothing...thanks…

 

Covering

McCoy JJ, Aldy K, Arnall E, Peterson J. Treatment of headache in the Emergency Department: haloperidol in the acute setting (THE-HA Study): A randomized clinical trial. J Emerg Med. 2020;59:12-20. [link to article]

 

 

 

Propofol for migraine in the ED: A pilot controlled trial

Really?!?

This was an open label pseudo-randomized trial of propofol (1mg/kg) vs. standard therapy for migraine in a single busy ED in Melbourne. 

Patients were included if the treating doctor thought they would require intravenous medication.

Patients were excluded if there was not a resuscitation bay available and a few other things.

The primary outcome was time to discharge from the ED or short stay unit. This is obviously not a patient-oriented outcome and subject to bias due to lack of blinding.

Results?

Over 28 months they enrolled 30 patients (one excluded in analysis due to missing data).

The time to discharge was about 5 hours in the propofol arm and 9 hours in the usual care arm. (P=0.021). The authors conclude that patients go home quicker.

There are some MAJOR problems with this study, mostly to do with study design, safety, efficacy, feasibility, and ethics.

There are substantial challenges to using propofol for migraine. It requires a set up for deep procedural sedation. It needs senior clinicians, airway nurses, and a resuscitation room for probably 30 minutes at a minimum. What are the harms to all the other patients in the ED that we are now potentially neglecting?

It is self-evident that the clinicians considered this as they were only able to enroll one patient a month for a common condition in a busy tertiary hospital.

In addition, with only 30 patients enrolled it cannot make any claims about efficacy or safety. Of the 15 patients who got propofol, six patients required additional medications. Two patients required airway maneuvers to maintain oxygenation & ventilation.

I am a bit surprised this study was granted ethical approval. But obviously there are differing opinions.

For now, please do NOT give propofol for migraine!

 

Covering:

Mitra B, Roman C, Mercier E, et al. Propofol for migraine in the emergency department: A pilot randomised controlled trial. Emerg Med Aus 2020;32:542-547. [link to article]

 

 

 

Dexamethasone in Hospitalized Patients with COVID-19- Preliminary Report

Beyond supportive care, we currently don’t have much to treat COVID-19. Remdesivir might decrease hospital length of stay. But we have found no medications that save lives.

The unprecedented RECOVERY trial involves 176 NHS organizations in the UK and are answering clinical questions at an lightning pace. This adaptive RCT has been looking at the use of dexamethasone, hydroxychloroquine, lopinovir/rotonavir, tocilizumab, and convalescent plasma.

This “preliminary report” is publishing the data on dexamethasone.

The background is COVID-19 often results in some immune mediated lung injury. Could steroids mitigate this? Or might they may cause harm by inducing immunosuppression?

6425 hospitalized patients with COVID-19 were randomized in a 1:2 fashion to dexamethasone vs. usual care.

The primary outcome was all-cause mortality at 28 days. They had a bunch of prespecified secondary outcomes.

The dose of dexamethasone was 6mg/day for 10 days.

Results?

Mean age was 66. Median days from symptom onset was 8 days. 16% of them were intubated and 60% were getting supplemental oxygen. 24% had no oxygen requirements.

Overall, 23% of patients randomized to dexamethasone died while 25% died in the usual care group for a number needed to treat (NNT) of about 35. (Rate ratio 0.83, 95% CI 0.75-0.93; P less than 0.001)

But it seemed to work the best in the sickest patients. Those who were intubated had an absolute mortality reduction of 12% for an NNT of 8. Those only on supplemental oxygen derived small benefit at a 3% reduction.

Unfortunately, it appears there is a trend toward harm in patient not requiring oxygen with a number needed to kill of about 26.

With the multitude of crap quality studies being rushed to publication, this is an absolute breath of fresh air. Prior to the final manuscript, this study has already changed the guidelines around the world.

Bottom line?

Intubated patients should get dexamethasone. We should probably give it to sicker patients on oxygen, but avoid it in everyone else.

Of course, this could all change tomorrow…

 

Covering:

Horby P, Lim WS, Emberson JR, et al. Dexamethasone in Hospitalized Patients with COVID-19- Preliminary Report. NEJM. 2020,  DOI: 10.1056/NEJMoa2021436 [link to full text article]

 

Five-year follow-up of antibiotic therapy for uncomplicated appendicitis in the APPAC Randomized Clinical Trial

Long term outcomes are important when trying to understand the usefulness of a non-surgical approach to appendicitis. If all the patients eventually fail and have an appendicectomy, then what is the point?

The Appendicitis Acuta (APPAC) trial out of Finland randomized 530 patients with CT proven uncomplicated acute appendicitis to antibiotics vs. open appendicectomy. Now we have some 5-year data.

The cumulative incidence of appendicitis was 27% at year one, 34% year two, 35% year three, 37% year four and finally 39% by 5 years.

The five year overall surgical complication rate (SBO, surgical infection, incisional hernias, and abdominal pain) was 24%.

These are good statistics to consider when considering shared decision-making.

But there are a few things to remember.

• All patients got CT prior to randomization to ensure uncomplicated illness. (i.e no perforation, abscess, appendicolith or suspicion of tumor.)
• They excluded children and adults over the age of 60
• They used some crazy C diff inducing doses of antibiotics including an IV carbapenem for 3 days followed by an oral fluoroquinolone and metronidazole. (But Augmentin has been used in other studies.)
• Patients had open appendicectomies. Laparoscopic surgery would be expected to have a lower surgical complication rate.

What’s the take home?

There is now more and more literature consistently demonstrating the decent efficacy of antibiotic therapy for uncomplicated appendicitis. Decades of surgical tradition is hard to change. But it is getting to the point where patients will need to participate in discussions regarding treatment options.

 

Covering:

Salminen P, Tuominen R, Paajanen H, et al. Five-Year Follow-up of Antibiotic Therapy for Uncomplicated Acute Appendicitis in the APPAC Randomized Clinical Trial. JAMA. 2018;320:1259-65. [link to article]

 

Electrical vs pharmacological cardioversion for ED patients with acute atrial fibrillation

This was in fact two RCT’s.

The primary one was comparing conversion to sinus rhythm between a drug-before-shock strategy vs. shock only for cardioversion of acute (<48 hours) atrial fibrillation. The second was a nested RCT comparing anterioposterior vs. anterolateral pad placement.

They enrolled about 400 patients. Half were randomised to procainamide infusion before an attempt at DC cardioversion. The other half got matching placebo followed by DC cardioversion.

Both strategies were highly effective in conversion to sinus rhythm at 96% with drug/shock vs. 92% for shock only (95%CI 0-9; p=0.07). Pad placement didn’t matter.

Of note, the procainamide worked for half of the patients and they were able avoid electricity and procedural sedation.

But not emphasized in the paper was the success of doing nothing. Many patients self-reverted during their ED stay and even with placebo infusion. Perhaps we should adopt a wait-and-see approach as suggested by the Dutch and Doyle?

There are a few things to note.

They reported no adverse events at follow up. (But there was one case of “cardiac arrest” when they forgot to hit the sync button… woops!) As per prior similar studies, it looks safe.

The cohort was a bit younger (mean age 60) and most had AF for less than 12 hours. Therefore, care should be taken when extrapolating this study to older patients with longer duration of AF.

11% of patients returned to the ED with recurrent AF within 14 days. This very likely underrepresents the amount of recurrence. Which begs the question of why bother…

There was a trend towards efficacy with the drug shock group with NNT of 25 for more successful overall conversion. This makes physiological sense.

Of course, the biggest issue is procainamide is not officially available in Australia and in some other countries. The authors suggest other antiarrhythmics might be useful.

Overall, I think this is compelling evidence to a consider a drug/shock strategy. But I still think doing nothing might be even better. Time for shared decision making.

 

Covering:

Steill I, Sivlotti M, Taljaard M, et al. Electrical vs pharmacological cardioversion for emergency department patients with acute atrial fibrillation (RAFF2): a partial factorial RCT. Lancet 2020;395:339-49. [link to article]

Multicenter Emergency Department Validation of the Canadian Syncope Risk Sore

Syncope Rules?

We all love syncope with its ubiquity and complexity. Most causes are benign but the needle in the haystack may be fatal. Wouldn’t it be nice to have a good clinical decision instrument to help us out?

These researchers sought to validate the Canadian Syncope Risk Score (see below) among 3819 patients that presented across 9 ED’s in Canada.

The risk score is mostly a quantification of what we evaluate already. History, ECG, ED diagnosis and troponin (if performed). Score ranges from -3 to 11 and patients are put into one of five categories; very low, low, medium, high or very high risk.

The primary outcome was “30-day serious outcomes” as determined during medical record review, telephone follow up, return visits, and coroners’ database.

Results?

The proportion of patients with serious outcomes increased from 0.3% in the very low risk group to 51% in the very high risk group.

This seems ok but I’m not so sure this “rule” will gain traction.

First, it’s too complicated to commit to memory. We would need to refer to MDCalc which will decrease its utility.

Second, it hasn’t formally been compared to what we already do… which is gestalt. (However, some may argue that it is already heavily reliant on gestalt.) It is possible that following the rule could make things worse. 

Third, we know rules tend to perform less well in complex disease processes. This is why doctors have not been replaced by robots… yet.

How might I use the rule?

Probably how we use most rules; something we can write in the medical record to support a decision we have already made. This might sound cynical, but gestalt is probably the best rule.

 

Covering:

Thiruganasambandamoorthy V, Sivilotti M, Le Sage N, et al. Multicenter Emergency Department Validation of the Canadian Syncope Risk Score. JAMA Intern Med. 2020;180:737-44. [link to article]

 

 

Apixaban for the Treatment of DVT/PE Associated with Cancer

Most DVT’s and PE’s in patients with cancer are treated with low molecular weight heparin. As if the malignancy was not enough, now they will get painful daily injections often for the rest of their life.

Seems cruel… why not just use a DOAC?

In turns out, there was no good evidence that they could be used in this population and there was some concern about increased bleeding.

Sounds like a good reason for a clinical trial?

These authors performed a randomized open-label noninferiority trial comparing apixaban to daltiparin in over 1000 patients in 119 centres in Europe, Israel and the USA.

They excluded patients with any CNS malignancy, leukemia, basal and squamous cell skin cancers, or if they were high risk of bleeding.

The primary outcome was recurrent DVT/PE during the trial period.

Results?

Recurrent DVT/PE occurred in 5.6% of the apixaban group and 7.9% of the daltiparin group. This met their non-inferiority margin but was not quite enough to claim superiority (p=0.09). Major bleeding was the same in both groups.

All good?!?

Maybe…

There was a trend towards more “clinically relevant” non-major bleeding with apixaban at 9% compared to 6% . This should lead to some caution as they already excluded those with high risk of bleeding.

Although the authors claim this was an “investigator-initiated” trial, it was funded by a “Bristol-Myers Sqibb-Pfizer Alliance.” In addition, there is an impressive list of author conflicts of interest- lecture & consulting fees, grant money, travel expenses, advisory board fees, etc. etc.

Either way, this trial published in the NEJM will be considered “high quality evidence” and will change the guidelines. Hopefully it's right.

Covering:

Agnelli G, Becattini C, Meyer G, et al. Apixaban for the Treatment of Venous ThromboemolismAssociated with Cancer. N Engl J Med 2020;382:1599-607. [Link to article]

Early self-proning in awake, non-intubated patients in the ED: A single ED’s Experience during the COVID-19 pandemic

This pilot study was carried out at the crazy Lincoln Medical Center, New York City. Located in the Bronx, it is the third busiest ED in the United States. In the grips of a pandemic, it is the perfect place to study potential treatments of COVID-19.

Awake proning has been shown to be beneficial in patients with ARDS and anecdotal reports have suggested it may be helpful for patients with coronavirus.

This pilot study enrolled a convenience sample of 50 patients who presented to their ED with hypoxia without resolution despite supplemental oxygen and who were capable of self-proning. They excluded patients who were NFR, getting NIV or intubated in the prehospital setting. All were eventually confirmed as COVID positive.

They termed these patients the “happy hypoxemics” as they generally looked quite well without respiratory distress despite having low oxygen saturation.

Results?

The median SpO2 at triage was 80% and this improved to 84% with supplemental oxygen. After 5 minutes of proning the saturation increased to 94%!

18 of the 50 patients eventually required intubation; 13 of those (24%) within the first 24 hours.

This pilot study has lots of limitations; no control group, no idea if proning resulted in meaningful patient-oriented outcomes. Nevertheless, it has adequately raised the hypothesis for a clinical trial.  A search of www.clinicaltrials.gov shows there are now several in progress.

Could there be harm from self-proning? It is possible. But these authors recommend proning until we get better quality evidence to inform practice. They have typical protocols whereby patients are asked to rotate about every 30 to 120 minutes.

Proning support cushions are already being sold in the USA. You can get one for US$164! I would not be surprised if a device manufacturer comes out with a human rotisserie device. No joke… watch this space!

Covering:

Caputo ND, Strayer R, Levitan R. Early Self-Proning in Awake, Non-intubated Patients in the Emergency Department: A Single ED’s Experience during the COVID-19 Pandemic. Acad Emerg Med. 2020;27(5):375-378 [link to full text article]

Intranasal ketamine for analgesia prior to digital nerve block- A double blind RCT!!??

Wow…

This was reportedly a double blind RCT of intranasal ketamine 50mg vs. saline placebo prior to performance of digital nerve blocks at a single centre in Iran. All the blocks were done by one doctor (listed as the third out of seven authors).

The primary outcome was reduction of pain during the block as measured on a visual analogue scale (VAS).

Results?

Exactly 100 patients were enrolled. Block pain was less in the group that got IN ketamine 28mm vs. 47mm (P less than 0.001) on the VAS. Side effects were reported to be “trivial.” This pain reduction persisted at the 45-minute mark at 21mm vs 43mm (P less than 0.001).

The authors conclude, “… IN Ketamine can be effective in reducing pain in patients with acute pain, without adding significant side effects.”

I doubt that many of us would consider giving ketamine prior to a digital nerve block. It does seem rather excessive and puts the patient at risk of side effects. (Reminds me of propofol for migraine) Perhaps we might consider inhaled nitrous oxide or intranasal fentanyl?

Unfortunately, there are a few problems and red flags with this study.

• The final study methods differ quite substantially from those listed in the trial registry found here.  The primary outcome was different, no power calculation, measuring tool different, etc.
• Intranasal ketamine burns and tastes bad. This could have unmasked blinding resulting in measurement bias.
• Data was collected in 2014. Why did it take 5 years to get published? I’m guessing it was rejected for publication from numerous journals.
• In the manuscript, there are numerous grammatical and spelling errors. What does a sloppy manuscript say about the conduct of the study?
• Why did patients continue to report substantial pain after the nerve block? Most of these blocks should have been successful at complete analgesia.
• Side effects were likely under-reported

Regardless of this study's conduct or limitations, I’m not a big fan of intranasal ketamine. Not great bang-for-buck and an undesirable side effect profile. In addition, we have experience with other drugs that are more efficacious.

Covering

Nejati A, Jalili M, Abbasi S, et al. Intranasal ketamine reduces pain of digital nerve block; a double blind randomized clinical trial. Am J Emer Med. 2019;27:1622-1626.

Targeted Temperature Management for Cardiac Arrest with Nonshockable Rhythm

The literature regarding cooling of comatose survivors of cardiac arrest is mixed. But even more controversial is the role of therapeutic hypothermia in the group of patients with non-shockable rhythm.

Enter the HYPERION trial published in the high impact New England Journal of Medicine.

This mammoth effort was an open-label pragmatic RCT comparing hypothermia (33 degrees) vs normothermia (37 degrees) in comatose survivors of cardiac arrest with non-shockable rhythms (PEA or asystole).

As if PEA and asystole were not bad enough, they excluded the sicker patients who would have highly likely died anyway- regardless of cooling or no cooling. These were patients who had no CPR for >10 minutes, CPR for more than 60 minutes, those with high vasopressor requirements etc.

The primary outcome was a good one; survival with a favorable day-90 neurologic outcome. This was defined as independent & able to perform ADL’s (CPC score 1-2). Unfortunately, it was possibly poorly determined by a single blinded psychologist by phone interview.

Results?

Over 4 years, 581 patients were included from 25 French ICU’s. On day 90, 10.2% of the hypothermia group vs. 5.7% of the normothermia had a good outcome (difference 4.5% 95%CI 0.1 to 8.9; P=0.04 and a NNT of 22.) Overall mortality did not differ between the groups at 80%.

Cooling wins!?

Despite the results, I am a bit less enthusiastic about this one.

The literature is still conflicting, and this is far from overwhelming data.

The primary result has a fragility index of 1. If only one of the patients that did well in the hypothermia group were reclassified as unfavorable at 90 days, the results would not have been statistically significant… we would be talking about a negative trial.

There are other issues with the measurement of the primary outcome, external validity and a few other things.

In the end, it is probably fine if your ICU wants to cool these patients. But please make sure it does not distract & get in the way of providing adequate resuscitation and supportive care. Stay cool (or not) and do the right things first.

Covering:

Lascarrou JB, Merdji H, Le Gouge, A, et al. Targeted Temperature Management for Cardiac Arrest with Non-Shockable Rhythm. New Engl J Med; 2019: 381:2327-2337. [link to article]

Compassionate use of Remdesivir for Patients with Severe Covid-19

It is a sign of the times when an article of such low-quality evidence is published in the New England Journal of Medicine. We are obviously desperate to get some information regarding therapy for Covid-19.

Compassionate use, or properly termed “expanded use,” is when patients can request a not yet FDA approved drug outside of a clinical trial.

This industry funded and written study reports on 53 patients with severe Covid-19 that got expanded use remdesivir in the USA, Europe and Japan.

Short answer… they got it and they got better.

Of course, we have no idea if remdesivir did anything. This was not a trial. There was no control group, no randomization, no blinding, nothing, zip, nada.

But fear not. Gilead Sciences, the manufacturer of remdesivir, is currently conducting a large phase 3 randomized clinical trial. They plan to enroll 6000 patients at 179 sites and have it finished by a “holy shit fast” May 2020!

Fortunately, most of their recruiting sites are based in the USA where there is plenty of patients to study. (Thanks Donald). Studies out of China have now been suspended or terminated due to low patient numbers.

A search of www.clinicaltrails.gov indicates the primary outcome of the phase 3 trial is an odds ratio of improvement on a 7-point ordinal scale. This type of analysis has incredible statistical efficiency. Along with 6000 patients, this study will have the power to demonstrate miniscule differences in patient outcomes.

Do you know what else Gilead Sciences developed?

Tamiflu.

Gilead licensed the drug to Roche in 1996 on return for royalties. Despite hardly any evidence of efficacy, it was a blockbuster that saw the world stockpile billions worth during H1N1.

Now if there was just some other global scare that might sell remdesivir? Hmmmm….

Ok, I am being paranoid. But I do think we need to be careful when this study is soon published and not let emotions & politics trump science. (Pun intended.)

Nevertheless, I genuinely hope this drug works. We have antivirals that have cured hepatitis C. We’ve put the brakes on HIV. In theory, remdesivir looks quite promising. It is an RNA polymerase inhibitor specifically designed to treat coronaviruses. Perhaps there is some hope.

So, watch this space.

But be skeptical.

Covering

Grein J, Ohmagari N, Shin D, et al. Compassionate use of Remdesivir for Patients with Severe Covid-19. N Engl J Med 2020 [E pub ahead of print] [link to full text]

Hydroxychloroquine in patients with COVID-19: an open-label un-peer reviewed RCT

We want to rapidly know as much as we can about COVID-19. In the current pandemic, researchers are rushing to complete studies and often prematurely release the results on MedRxiv (pronounced “med-archive”) before they have even undergone a process of peer review.

Of course, this can be good news for rapid dissemination of information, but it can also be rather harmful if bad studies get pushed without proper scrutiny.

This multicenter RCT from china included 150 patients with COVID-19. They got hydroxychloroquine (open label) vs. standard care. The primary outcome was clearance of the virus at 28 days.

They concluded, “…adding hydroxychloroquine to the current standard-of-care in patient with COVID-19 does not increase virus response but accelerate the alleviation of clinical symptoms.” (Yes, you read that correctly).

They go on to say that the alleviation of symptoms may due to the anti-inflammatory properties of hydroxychloroquine and less lymphopenia. The authors suggest clinicians might consider it in symptomatic patients with elevated CRP and or lymphopenia because it might prevent disease progression in high risk patients.

Unfortunately, this conclusion is wrong.

Their primary outcome was negative, but at with such small numbers was at risk of a Type I error. Hidden in the manuscript, the authors mention that they wanted to enroll close to 400 patients but had to give up when recruitment fell short.

The median time from symptom onset to getting hydroxychloroquine was 16 days. For most antivirals to work, they need to be given early.

But what about the claim that the medication reduces clinical symptoms?

This comes from one of fourteen post-hoc subgroup analysis in 28 patients that was “statistically significant” with hazard ratio 95%CI of 1.09 to 71.3.

Peer reviewers will easily spot this inappropriate claim that came about through a process known as data dredging or P-hacking. 

What should we conclude?

Unfortunately, nothing.  

This was an underpowered biased study that made some silly claims based on an unadjusted post-hoc subgroup analysis.

We still don't know if hydroxychloroquine helps or harms.

Covering:

Tang W, Cao Z, Han M, et al. Hydroxychloroquine in patients with COVID-19: an open-label, randomized, controlled trial. MedRxiv [link to un-peer reviewed manuscript]

Conservative vs interventional Treatment for Spontaneous Pneumothorax: Don’t just do something… stand there!

This study in the New England Journal of Medicine is going to change how we treat spontaneous pneumothorax. If you haven’t read it, you should.

(Disclaimer: the lead author, Dr Simon Brown is a colleague of mine at the Royal Hobart Hospital. He is bigger than me and knows where I live. Hmmmm….)

By way of background, there are conflicting guidelines regarding the treatment of primary spontaneous pneumothorax. The Americans are quite aggressive with intervention, the British less so. Any time you see such variation, it usually means there is no high-quality evidence to inform practice.

Fortunately, we now have that evidence.

The Primary Spontaneous Pneumothorax (PSP) trial was a prospective randomised open-label non-inferiority study that enrolled 316 patients in 39 hospitals in Australia & New Zulund over 6 years.

They included stable patients between the ages of 14-50 with at least a 32% (sum of interpleural distance greater than 6cm) primary spontaneous pneumothorax.

Those randomised to “intervention” had a <12 French Seldinger style chest tube placed. They got a repeat chest x-ray in one hour. If the lung was re-expanded and there was no air leak, they clamped the tube. Another x-ray was taken 4 hours later. If all was fine, the tube was pulled and the patient discharged. If not, they got admitted.

The “conservative” arm was observed for 4 hours and a repeat chest x-ray was taken. If they did not require oxygen and they were walking around comfortably, they could be discharged. However, intervention could be allowed for if the patient had clinically significant symptoms despite adequate analgesia, couldn’t walk, unwilling to continue, became unstable or if the chest x-ray was getting worse.

The primary outcome was full lung expansion by 8 weeks. There were lots of arguably more important secondary outcomes.

Results?

As expected, patients were generally young, male and thin. Half were smokers.

Mean pneumothorax size was 65%! Holy crap… that’s big.

For the primary outcome, 98% of the intervention arm had full lung re-expansion at 8 weeks vs. 94% in the conservative arm. This was within their prespecified non-inferiority margin of -9% as such, this is a positive study.

However, even more impressive are the secondary outcomes in favour of a conservative approach.

85% of patients randomised to conservative management got no intervention. The intervention arm had many more adverse events (26% vs. 8%) mostly related to the chest tube. Mean time to resolution of symptoms was 15 days in both groups. Recurrent pneumothorax was double in the intervention arm; 16% vs. 8%.

Median hospital length of stay was 3.8 days in the intervention group compared to 0.2 in the conservative arm!

All of this is quite a good argument for us to change our practice.

For what it is worth, the manuscript goes into length regarding the limitations of loss to follow-up. Even going so far as to perform an analysis assuming all of them were treatment failures making this study “fragile.” While perhaps technically correct, I think this was overzealous peer review that was ultimately biased.

A 26-year-old male, who got no treatment and feels fine is probably less likely to follow up as directed. However, patients in the intervention arm (who got painful tubes and spent 4 days in hospital) were more likely to return for the 8-week visit.

What’s the take home point?

Looks like we’ll be doing less chest tubes in stable patients with primary spontaneous pneumothorax.

 

Bummer… I like putting in chest tubes.

Covering:

Brown S.G.A, Ball E.L, Perrin K, Conservative versus Interventional Treatment for Spontaneous Pneumothorax. N Eng J Med. 2020;382:405-15. [link to article]

Diagnosis of PE with D-Dimer Adjusted to Clinical Probability- A game changer!

Intern, “the D-dimer just came back at 0.6… what should I do?”

Me, “… faaaaaaaaaaaaaaaaaaaaaaaaarrrrrrrk!”

Fortunately, this study is probably a game changer.

These Canadian’s conducted a prospective study in which PE was considered to be ruled out if the pretest clinical suspicion was low (Well’s score0-4) and a D-dimer of less than 1.0mg/L or if the clinical suspicion was moderate (Well’s score 4.5-6) and D-dimer less than 0.5mg/L.

Just over two thousand patients were enrolled. Their overall rate of PE was 7.4%.

Of the 1325 patients with low or moderate clinical suspicion for PE and a negative D-dimer (as above), NONE (95%CI 0.0 to 0.29%) of them had venous thromboembolism during the 3-month follow up.   

This is amazing.

Once again, two-thirds of all patients were excluded from imaging and the diagnostic performance of this strategy was perfect.

Furthermore, this publication from the NEJM is one in line of papers supporting the notion of adjusting D-dimer thresholds. Consistency in the literature is reassuring.

Slam dunk?

Ok… no studies are perfect. What were the two major limitations?

The quality of a study looking at diagnostic performance of a test is only as good its gold standard. Unfortunately, patients that were ruled out by this strategy did not have definitive imaging. This study relied on 3-month follow up (sometimes by telephone) and may have led to the underdiagnosis of PE.

Secondly, there were 34 deaths during follow-up.

Yikes!

But they claim, “no deaths were attributed by the central adjudication committee to pulmonary embolism.” Table S5 in the supplementary appendix shows that most died of cancer or cardiovascular disease. I very much doubt many (if any) of the deaths had autopsy performed. We all know PE can be quite tricky to diagnose. I still wonder if some of these deaths were due to missed PE.

Despite these limitations, I still think adjusting D-dimer thresholds makes sense. And now it is supported by numerous studies published in high impact journals.

Intern, “the D-dimer just came back at 0.6… what should I do?”

Me, “Never order a D-dimer without asking me first!”

Oh… I meant, “send them home…” And hopefully they don’t die of “cancer.”

Covering:

Kearon C, de Wit, Parpia S, et al. Diagnosis of Pulmonary Embolism with D-dimer Adjusted to Clinical Probability. N Engl J Med 2019;381:2125-34. [link to article]

Roc vs. Sux for RSI… a storm in a teacup

Far too much time and effort has been spent debating the winner of the rocuronium vs. succinylcholine contest. But it is a bit too hard to ignore this paper claiming to be the first RCT of these drugs in an emergency setting.

This was a multicenter, non-inferiority RCT of 1248 patients with out-of-hospital cardiac arrest in France. Tout bon!

Rocuronium dosed at 1.2m/kg was compared to succinylcholine at 1mg/kg. The authors note the patients were blinded to the assigned drugs. Yes… really… Patients with no health insurance were excluded. Yes… really…

About 90% of the intubations were conducted by a specialist emergency doctor. They only used direct laryngoscopy (no video) and half the time intubated in some pretty creative places… i.e. on the ground.

The primary outcome was first pass intubation success rate. Hardly a patient oriented outcome, but at least it is reasonably objective and measurable. They also looked at some secondary outcomes.

A non-inferiority margin of 7% was chosen.

Results?

It turns out that rocuronium was not non-inferior to succinylcholine!

Howzat…?

First pass success rate was 79% in the sux group vs. 74% in the roc group. The difference in the 95% confidence interval was up to 9%. This is greater than their non-inferiority margin.

Sux is the winner!

Not really.

There were more adverse events in the succinylcholine group.

Unfortunately, this study will not end the Sux vs. Roc debate. C'est la vie... But either way it doesn’t really matter.

Both drugs are fine. And in your practice, you can always use both.

Don’t forget some contraindications to giving sux (mostly hyperkalemia) and don’t forget to provide post intubation sedation after giving a proper dose of roc.

Covering:

Buihard B, Chollet-Xemard C, Lakhnati P, et al. Effect of Rocuronium vs Succinylcholine on Endotracheal Intubation Success Rate Among Patients Undergoing Out-of Hospital Rapid Sequence Intubation. JAMA 2019;322(23):2303-2312 [link to article]