The November 2024 Research Roundup

Back for another month of interesting, arcane, important, or baffling articles. As we enter the winter in the Northern hemisphere, and I have little interest in heading outside, I will probably spend more time reading, so these write ups might get longer for the next few months. For now, the weather remains fine, golf season is still in full effect, and so I will be as brief as I know how (not very).

The podcast version of this episode, now available in video on YouTube, can be found here:

Epinephrine in cardiac arrest: It doesn’t work IV, but maybe IM will help?

Palatinus HN, Johnson MA, Wang HE, Hoareau GL, Youngquist ST. Early intramuscular adrenaline administration is associated with improved survival from out-of-hospital cardiac arrest. Resuscitation. 2024 Aug;201:110266. doi: 10.1016/j.resuscitation.2024.110266. Epub 2024 Jun 9. PMID: 38857847

To date, there is no real evidence that epinephrine improves outcomes in cardiac arrest. (It probably increases survival a small amount, but the survivors do not seem to have good neurologic outcomes. See posts here and here for more details.) However, despite the lack of proven benefit, there is an ongoing push to use epinephrine earlier in arrest. This is a before and after study in 1405 out of hospital cardiac arrest patients. The before group received standard ACLS, and took place from 2010-2019. The after group received a 5 mg dose of IM epinephrine concurrent with vascular access attempts, and then otherwise received standard ACLS. Adherence to the study protocol was imperfect, and unfortunately different in the different timeframes (89% in the after and only 70% in the before). The use of IM epinephrine was associated with about a 3 minute decrease in the time it took for the patient to receive their first dose. For the primary outcome of survival to hospital discharge, 11% of the IM group and 7% of the IO/IV group survived, a 4% absolute improvement that was statistically significant. The good news is that survival with good functional outcomes was also improved (6% vs 10%). One problem with studies that take place over more than a decade is that other aspects of care can change as well. For example, patients in the before period probably received ‘therapeutic’ hypothermia, whereas that should have been abandoned by the after period. That change might not matter, but other undescribed changes (such as ECMO) could have a big impact on results. In fact, their baseline data demonstrates some key confounders: the after group had much more bystander CPR (70% vs 56%) and were about 3 years younger on average. Those differences alone could easily explain the association seen. When appraising observational data, it is really important to consider the bulk of the available scientific literature. Seeing as we have large RCTs that fail to show improvement in neurologic outcomes with epinephrine, it is a good bet that this observational data showing an association is biased in some way. This definitely warrants a follow-up RCT, but it isn’t clear how it should impact current clinical practice. Of course, if you really think giving epinephrine is important in cardiac arrest, it makes sense to give it as early as possible, and the IM route should expedite that. (As an analogy, I don’t wait for vascular access to give my first dose of benzodiazepine in status epilepticus.) On the other hand, if like me you are unconvinced by the epinephrine data overall, you probably have better things to do early in a resuscitation than drawing up multiple vials of epinephrine for IM injection. 

Bottom line: This before and after study demonstrates an association between early IM epinephrine and survival from cardiac arrest. However, there are simply too many confounders in this before and after study design to trust the results. This is hypothesis generating, and warrants a follow-up RCT. 

There will be a ton of hype, but please don’t start using this c-spine rule

Leonard JC, Harding M, Cook LJ, Leonard JR, Adelgais KM, Ahmad FA, Browne LR, Burger RK, Chaudhari PP, Corwin DJ, Glomb NW, Lee LK, Owusu-Ansah S, Riney LC, Rogers AJ, Rubalcava DM, Sapien RE, Szadkowski MA, Tzimenatos L, Ward CE, Yen K, Kuppermann N. PECARN prediction rule for cervical spine imaging of children presenting to the emergency department with blunt trauma: a multicentre prospective observational study. Lancet Child Adolesc Health. 2024 Jul;8(7):482-490. doi: 10.1016/S2352-4642(24)00104-4. Epub 2024 Jun 4. PMID: 38843852

This is the derivation and initial validation of the PECARN c-psine rule, and this scares me so much that I am going to put the bottom line up front: you should not be using this rule in your clinical practice. If people start using this rule, it is almost guaranteed to increase imaging and ultimately hurt children. This is a large observational study from the PECARN group with 11,857 children in the derivation group (although 16,206 were eligible and they don’t explain why they missed so many) and 10,573 in the validation cohort (out of 16,061 eligible). Perhaps the most important point to know about this paper is that the study only took place at level 1 pediatric trauma centers, and they only enrolled the highest risk patients (those arriving by EMS, who had a trauma team activation, or in whom in the doctor ordered c-spine imaging.) These are very high risk patients, and look nothing like the patients we normally see, which is probably the biggest reason this rule should not be generalized to normal emergency medicine. They come up with a 9 item rule. There are 4 very high risk features: GCS 3-8, unresponsive on the AVPU scale, requirement for intervention on the ABCs, or a focal neurologic deficit in the ED. These are all very high risk, with at least a 10% chance of c-spine injury, and they suggest a CT in this group. Children who didn’t meet any of the high risk criteria only had a 1.4% risk of c-spine injury (despite being high risk trauma activations), and so the risk is going to be essentially 0 in the populations that the rest of us manage. To catch this last 1.4%, they add 5 criteria: the child volunteering that they have neck pain, any altered mental status, substantial torso injury, substantial head injury, neck tenderness on exam. They suggest x-ray in this group (although that part of the rule isn’t studied at all). The resulting rule is very underwhelming, with a sensitivity of 94% (95% confidence interval down to 90%) and a specificity of only 60%. There are a lot of problems with this study, and you might want to read about them in detail in the full write up, but the big issue is that this rule is essentially guaranteed to increase imaging in children. Unlike the geriatric patients we have learned to worry about, pediatric c-spine injuries are incredibly rare and children are mostly easy to examine. We are not missing these injuries in current practice. We don’t need a rule to help us. And if you take a step back and think about what this rule is saying, it clearly does not help your clinical judgement. No emergency physician would ever order c-spine imagining in an awake patient with no pain, no tenderness, no neurologic deficits, and no other substantial injuries. But that is all the rule says. Unfortunately, the positive predictive value of 3% will end up hurting us, because people will wonder about individual aspects of this rule, and will feel compelled to order tests in children they never would have imaged previously. We can’t know for sure without implementation studies, but I would bet my retirement fund that in every sane country in the world, this rule will dramatically increase the use of imaging in very low risk patients. (If your country is about to appoint RFK Jr. as the head of their FDA, I probably can’t help you.)

Bottom line: This is a big effort by the PECARN group, and we should all be familiar with the results, but it is not ready to be used any any clinical environment, but especially should not be generalized outside of the super high risk patient presenting to the level 1 pediatric trauma center that they describe here. 

Dogma: the great delayer of CT scans everywhere

Soucy Z, Cheng D, Vilke GM, Childers R. Systematic Review: The Role of Intravenous and Oral Contrast in the Computed Tomography Evaluation of Acute Appendicitis. J Emerg Med. 2020 Jan;58(1):162-166. doi: 10.1016/j.jemermed.2019.10.034. Epub 2019 Dec 13. PMID: 31843324

The value of this paper will vary dramatically between hospitals, as radiology groups seem to pick their protocols with a random number generator. This is a systematic review looking at contrast for imaging in appendicitis, as part of a guideline for the American Academy of Emergency Medicine Clinical Guidelines Committee. Oral contrast adds no accuracy to an abdominal CT with IV contrast, but patient care is delayed by an average of 2 hours. They give the following statement a class A rating: “The administration of oral contrast is not required when performing CT of the abdomen and pelvis for the evaluation of AA [acute appendicitis] in adult patients.” It is still unclear how much value IV contrast adds. A noncontrast study has good, but imperfect, test characteristics, with a sensitivity of 93% and a specificity of 96%. They give this statement a class B rating: “CT of the abdomen and pelvis without contrast has excellent test characteristics for the evaluation of AA. Providers can use it for this purpose with confidence.” Unfortunately, there don’t seem to be any studies directly comparing noncontrast CT to contrast. Really, given that we know contrast has no impact on kidney function, there is very little reason to avoid IV contrast. However, it is worth knowing that a noncontrast CT will still be very accurate if required, for example in a patient with a severe contrast allergy. (Whether we should be using contrast allergy protocols is an entirely different area of dogma that I will leave aside for the time being.) Unfortunately, this evidence does you little good if your radiology team is uncomfortable reading scans without contrast, and concludes every report with something like “cannot exclude appendicitis given the lack of contrast.”

Bottom line: This information is not new. I was taught this in residency. However, it might be new to your radiology group, so if they are still using oral contrast (with all of its many problems) it might be worth starting a conversation.

If there are any researchers out there, this review sets the stage for a really valuable RCT. Given the equipoise around IV contrast described here, an RCT randomizing potential appendicitis patients to IV contract or plain CT could simultaneously answer two very important questions: does IV contrast help diagnose appendicitis, but more importantly, does IV contrast have any effect on renal function?

Of course that crinkly paper we use to cover stretchers is useless (although unfortunately this paper does little to prove that)

Chiarlitti N, Graves Z, Lavoie C, Reid RER. Does Examination Table Paper Use Mitigate the Risk of Disease Transmission in a Family Medicine Clinic? Ann Fam Med. 2024 May-Jun;22(3):230-232. doi: 10.1370/afm.3092. PMID: 38806257

I like this little study, although there are definitely some issues. Basically, they had simulated patients apply UV paint to their hands, performed 12 simulated patient encounters either with or without exam table paper (the crinkly paper we often cover stretchers with), and visually examined where patients touched. Not surprisingly, the patients’ hands touched the sides of the stretcher, which is mostly uncovered, more than the middle of the stretcher. I don’t think the numbers matter much, because there are obviously so many flaws. For example, why are we more concerned about the patients’ hands than the rest of their body? What about fluids expelled from the mouth while coughing or sneezing? What about those soiled trousers? The study I would actually want to see is a real world (real patient) study that actually looked at microbial loads with and without these pieces of papers. I would bet a lot of money that these paper coverings do nothing at all, but this study doesn’t prove it. (They do point to the relatively high economic and environmental costs of these coverings, and so a real study is probably warranted.)

Bottom line: There is a lot of dogma throughout all of medicine, but infection control might be the area most saturated.

Mastering the bougie

Barnicle RN, Bracey A, Weingart SD. Managing Emergency Endotracheal Intubation Utilizing a Bougie. Ann Emerg Med. 2024 Jun 22:S0196-0644(24)00232-4. doi: 10.1016/j.annemergmed.2024.04.021. PMID: 38912998

I truly believe if you want to consider yourself an airway expert, you must have mastered the bougie. (We can debate the literature on using a bougie routinely for your first attempt, if you want, but there is no debate that you need to be proficient with the tool.) That being said, although I think I am very good at airway management, intubations are rare enough where I work my that skills are probably decaying, and I doubt I will ever get enough experience to truly master the bougie. This paper, with Scott Weingart as the senior author, dives into bougie use in great detail, explaining not just the advantages and disadvantages, but also breaking down the microskills you will have to master if you want to use the bougie effectively in your practice. When I used to run a simulation lab, I spent a lot of time practicing these skills: especially bougie stabilization while threading the ETT (assuming I would do this alone) and ETT delivery, including manipulating the bevel to manage hang-up on the arytenoids that often happens. Not much to critically appraise here. More of a recommendation for a short paper to read for anyone trying to up their bougie skills.

What HAPPENs when you use a crappy surrogate outcome?

Luo Z, Li Y, Li W, Li Y, Nie Q, Shi Y, Wang J, Ji Q, Han X, Liu S, Li D, Wang S, Li Z, Jia D, Ge H, Xu P, Feng Z, Li F, An F, Tai N, Yue L, Xie H, Jin X, Liu H, Dang Q, Z hang Y, Sun L, Wang J, Huang H, Chen L, Ma Y, Cao Z, Wang C; HAPPEN Investigators. Effect of High-Intensity vs Low-Intensity Noninvasive Positive Pressure Ventilation on the Need for Endotracheal Intubation in Patients With an Acute Exacerbation of Chronic Obstructive Pulmonary Disease: The HAPPEN Randomized Clinical Trial. JAMA. 2024 Sep 16:e2415815. doi: 10.1001/jama.2024.15815. PMID: 39283649

Despite being a big paper, I don’t think this trial has much relevance to the average emergency provider, so I won’t go into too much detail. If you want to learn more, there was a great discussion on the EMCrit podcast. It is an unblinded multicentre RCT from China that randomized 300 adult patients with COPD requiring ongoing BiPAP after 6 hours of use, but not requiring the ICU, to two different ventilation strategies: low intensity (tidal volume target 6-10 mL/kg) or high intensity (10-15 mL/kg). This is a weird population, who seem to have very mild COPD, and I think would be treated without BiPAP in every center I have ever worked in. I would have loved to see a third group without BiPAP for comparison, because it isn’t clear to me BiPAP was required at all, let alone high intensity BiPAP. The fact that they screened 8148 patients to find these 300 highlights how rare and odd this population is. Their primary outcome was a surrogate composite of lab and clinical volumes which they call “need for intubation”, and was better in the high intensity group (5% vs 14%, p=0.004). However, they provide us with data that proves that their surrogate outcome is a useless surrogate. The exact same number of patients were intubated in both groups (3.4% vs 3.9%), and therefore the surrogate “need for intubation” clearly had no bearing on reality, and does not at all indicate a true need for intubation. All of the other clinical outcomes, including mortality, ICU admission, length of stay, and readmission look the same between the two groups. They make a bit of a deal about how a number of the low intensity group had to be switched to the high intensity settings, but that presumes a benefit from high intensity, and just highlights the bias of the authors. Overall, this data demonstrates that higher tidal volumes on BiPAP results in some noticeable physiologic changes, but with no change in clinical outcomes, and is therefore unnecessary. (It does provide some evidence of safety for higher tidal volumes, with aspiration risks below 1% in both groups, so if you think you need high tidal volumes for some reason, I guess this tells you it is likely safe. However, they don’t talk about progression of ARDS, and acute lung injury might be the bigger concern with higher volume positive pressure ventilation.)

Bottom line: Honestly, this paper probably can’t even be implemented in the hospitals I work in, because BiPAP is only done in the ICU, and these are non-ICU patients. I see no reason to use this high intensity ventilation strategy, but seeing as this only happens after 6 hours, that will be a decision for the medical teams. 

So many bad takes on this paper

Coyle C, Shi J, Leonard JC. Antibiotic prophylaxis in pediatric dog bite injuries: Infection rates and prescribing practices. J Am Coll Emerg Physicians Open. 2024 Jun 4;5(3):e13210. doi: 10.1002/emp2.13210. PMID: 38841297

I have covered the evidence for management of dog bites before, with the overall summary being that these wounds should mostly be closed like any other wound, and that prophylactic antibiotics are silly. This is just a retrospective look at current practice, which I would have skipped, except that I heard it talked about in a few places with some comments that sounded ridiculous to me. As far as the paper goes, it is a chart review that identified 672 children with dog bites. 92% of patients were given prophylactic antibiotics, although only 88% filled the prescription. These were almost all for amoxicillin-clavulanate. The results are not presented well, but overall there was no difference in the infection rate between patients given antibiotics and those who were not given antibiotics (5.8% with antibiotics and 3.0% without antibiotics, p=0.28, so favoring no treatment, although you can expect confounding). There also weren’t any obvious differences based on wound management. (Only one patient had skin glue used, and had an infection, which is obviously a very high rate, but it is hard to make much of a single patient.) 

Obviously, this is the kind of paper I would normally skip, if I had not heard antibiotic prophylaxis described as “gospel truth”, as well as a separate podcaster commenting that they think that it would be unethical to run an RCT of this practice. That is absolutely crazy. There is clearly equipoise here, and RCTs have already been done, so to say that it is unethical is nonsensical. More importantly, the entire concept of prophylactic antibiotics makes very little sense. You are proposing giving 100% of patients antibiotics, with their many adverse events, to prevent 5% of patients from needing those same antibiotics in a few days. You can’t use “prevention of antibiotics” as the purported benefit of your treatment plan if 100% of patients are given antibiotics. In order for this treatment plan to make any sense you would have to believe that large numbers of patients are not returning when their wound gets infected, resulting in severe infections and long term complications. That is just not consistent with reality. Furthermore, in all of these studies, the infection rate is identical with prophylaxis, so you are just exposing patients to even more antibiotics with no benefit. As always, clinical judgement should be used. In patients with immunocompromise, or at risk of severe infection, there may be a reasonable argument for prophylaxis, but for the average patient prophylactic antibiotics are completely illogical. Antibiotics have many proven harms, but no proven benefit in this scenario. Instead of arguing that an RCT would be unethical, it makes a lot more sense to stop this practice until there is an RCT actually demonstrating benefit. I do not prescribe prophylactic antibiotics routinely, and talking about them as if they are “gospel” is just silly. 

Bottom line: A lot of people are still using prophylactic antibiotics in dog bites, but the logic behind that strategy (treat 100 patients to avoid the same treatment in 5) makes absolutely no sense. 

Are we on the verge of a paradigm change in medicine?

Cuker A, Kavakli K, Frenzel L, Wang JD, Astermark J, Cerqueira MH, Iorio A, Katsarou-Fasouli O, Klamroth R, Shapiro AD, Hermans C, Ishiguro A, Leavitt AD, Oldenburg JB, Ozelo MC, Teitel J, Biondo F, Fang A, Fuiman J, McKay J, Sun P, Rasko JEJ, Rupon J; BENEGENE-2 Trial Investigators. Gene Therapy with Fidanacogene Elaparvovec in Adults with Hemophilia B. N Engl J Med. 2024 Sep 26;391(12):1108-1118. doi: 10.1056/NEJMoa2302982. PMID: 39321362

This has nothing to do with emergency medicine, but if you get tired of all the negative studies we see in modern medicine, this paper should be a great source of optimism. It is a multicentre phase 3 study of gene therapy for hemophilia B, and unlike a lot of the hype I have been hearing for decades, this actually seemed to work. It is a before and after study, comparing standard prophylaxis with factor IX to gene replacement therapy (and I love the dose: 5×10^11 vector genome copies per kilogram). They included 45 men aged 18-65 with moderately severe or severe hemophilia (factor levels less than 2%). Their primary outcome was bleeding episodes (both treated and untreated, which is the key shortcoming in this unblinded industry run trial), and the results were pretty dramatic. In the “before” period, when men were treated with usual prophylactic factor IX, there was an average of 4.4 bleeding episodes, as compared to only 1.2 with gene therapy (-3.2 episode, 95% CI -5.5 to -0.8, p-0.008). I would be very cautious about an unblinded, nonrandomized trial presented in the New England Journal fully funded, designed, and written by the company that stands to profit from this. On the other hand, the promise of genetics has been on the horizon for a long time now, and this is the first really promising result I have seen in a clinical trial so far. I don’t have to decide whether to use this specific drug, so I can afford to be less skeptical, and just enjoy some overall optimism about the future of medicine. 

Bottom line: This trial has too much financial conflict to be believed on its own, but it seems like we might be on the verge of seeing genetic therapy in clinical practice, and that is exciting. 

Cheesy Joke of the Month

Someone keeps leaving pages of an Agatha Christie novel at my front door. 

It’s a bit of a mystery.