Research Roundup for April 2025

I took a few months off. (Well, not so much off, but as stuck in other EBM rabbit holes.) I am sure some were happy for the empty inbox, but if you enjoy nerdy conversation about subpar medical research, this is your luck day.

Yeah, I guess you could give calcium. Or you could just do nothing.

Az A, Sogut O, Dogan Y, Akdemir T, Ergenc H, Umit TB, Celik AF, Armagan BN, Bilici E, Cakmak S. Reducing diltiazem-related hypotension in atrial fibrillation: Role of pretreatment intravenous calcium. Am J Emerg Med. 2025 Feb;88:23-28. doi: 10.1016/j.ajem.2024.11.033. Epub 2024 Nov 17. PMID: 39577214

This is single centered, double-blind, placebo controlled RCT looking at pretreatment with calcium to prevent hypotension in patients receiving IV diltiazem for atrial fibrillation. They compared 2 doses of calcium chloride (90 mg and 180 mg) to placebo, and measured blood pressures at 5, 10, and 15 minutes. They don’t use statistics to compare the groups to each other, but rather to their own baseline, which is odd, but by 15 minutes both the placebo and 90 mg group had decreases in blood pressure while the 180 mg group did not. That is the headline news, but if you dig deeper, I think there are multiple reasons to be cautious about the application of this data. Although there might be statistical differences, the mean systolic blood pressure in all groups stayed above 115 at all time points, and there were no differences between the groups in terms of hypotension or adverse events, and so this is almost certainly not clinically important. That makes sense, as clinically important hypotension is very rare with diltiazem. In addition, they used a large and rapid bolus of diltiazem. They gave 0.25mg/kg as a bolus over 2 minutes. For the average adult, that means pushing about 20 mg. Although that is a common cose, there is really no need to be that aggressive. I usually start with lower doses, or give this 0.25 mg/kg dose over a much longer time frame, and I essentially never see clinically significant hypotension. Finally, it is unclear why they chose calcium chloride, but it would only take a single severe necrosis after extravasation to negate any value seen here, and this trial is not at all powered for rare but important outcomes.

An additional note raised by Scott Weingart is related to the significant whole body burning that is often caused by calcium chloride. Honestly, in awake patients I have almost exclusively used calcium gluconate in my career, so I have not seen this phenomenon. His contention is that calcium chloride raises the blood pressure of all patients, not just patients treated with calcium channel blockers, but that the effect has nothing to do with calcium channels and everything to do with pain. Pain is probably not your vasopressor of choice, so if you just want vasoconstriction, use something else. I highlight this point to raise an important point about critical appraisal: you need some degree of clinical knowledge to assess science, and so clinicians really need to read papers and not just rely on eggheads to do it for them.

More details here. 

Bottom line: Calcium probably has some minor hemodynamic effects, but when diltiazem is used correctly, adverse events are incredibly rare, and therefore there is really no reason for prophylaxis.

Speaking of diltiazem, does it cause patients to bleed to death?

Ray WA, Chung CP, Stein CM, Smalley W, Zimmerman E, Dupont WD, Hung AM, Daugherty JR, Dickson A, Murray KT. Serious Bleeding in Patients With Atrial Fibrillation Using Diltiazem With Apixaban or Rivaroxaban. JAMA. 2024 May 14;331(18):1565-1575. doi: 10.1001/jama.2024.3867. PMID: 38619832

I was asked about this paper, and although it took me many months to get to, this is proof that I do respond to questions about individual papers. Based on the fact that diltiazem is a strong inhibitor of CYP3A4, which is a major metabolic pathway for DOACs, this study looks at bleeding risk in patients on rivaroxaban and apixaban for atrial fibrillation, and subsequently started on either metoprolol or diltiazem. It uses the massive American medicare database (although that means it is inherently not a representative sample), and includes 204,155 patients, 53,275 on whom were started on diltiazem and 150,880 were started on metoprolol. (The drastically different group sizes is a hint that metoprolol is not an adequate control, and that there will be significant confounding.) For the primary outcome of bleeding-related hospitalization and death with recent evidence of bleeding, diltiazem was associated with worse outcomes (60 vs 50 events per 1000 person-years; HR 1.21). The ‘per-thousand patient years’ is not a super-intuitive framing, but this is equivalent to 1 extra  ‘bleeding-related hospitalization or death with recent evidence of bleeding’ for every hundred patients treated with diltiazem for a year. It is a small difference, but big enough to consider if we thought it was real, but this data is certainly not convincing. This is not randomized data, and patients are not started on diltiazem and metoprolol for the same indications. This is not just a comparison of patients on a CYP3A4 inhibitor to patients not on one. There were significant differences between the two groups, which makes sense because beta-blockers are preferentially used in patients with known coronary artery disease, prior MI, or CHF. They don’t report how many patients in each group were on aspirin, but 6% more of the metoprolol group “met criteria for asa therapy”. In addition, 2% more of the metoprolol group was on other antiplatelet medications, such as clopidogrel or ticagrelor. That difference alone could easily explain the difference seen in bleeding, and is a far more likely explanation than CYP3A4 inhibition. That is not to say there couldn’t be a difference between the groups, and if the pharmacology people think this CYP3A4 thing is a big enough deal, they should try to study this with reasonable methodology, but highly confounded data like this is basically meaningless.

Bottom line: There is an association between diltiazem and increased bleeding in patients on DOACs (as compared to metoprolol), but this is almost certainly the result of obvious confounders, so I can’t see any reason to change current practice. 

Shameless self promotion, which I am obviously only doing for the sake of my co-authors

Morgenstern J, Radecki R, Westafer L, Niforatos JD, Atkinson P. CJEM debate: clinical decision rules-thinking beyond the algorithm. CJEM. 2025 Feb 3. doi: 10.1007/s43678-025-00870-0. PMID: 39900742

Self promotion? Sure, but I think the topic is important, and anytime I get to create academic content with this brilliant group of people, I am going to share it widely. Lauren Westafer is objectively smarter than me, and is on the opposite side of this debate, which should make me very nervous. Her co-author Josh Niforatos is awesome too. However, they are also embedded in a healthcare system that is such an outlier from the rest of the world that I think their interpretation ends up somewhat biased. For example, despite my argument that the PECARN head injury rule should not be used based on the fact that we are missing high quality implementation data and that it appears to be significantly worse than just clinical judgement, there is a low quality before and after study that demonstrated a decrease in CT usage with the PECARN rule. However, that study had a baseline rate of CT of 21%, and the rule only decreased imaging to 15%. Both of those numbers are insanely high, and highlight the problem with extrapolating medical data from the American context. I work in busy community emergency departments with about 20-30% of patients being paediatric, and head injury being among the most common presentations. I have ordered fewer than 10 CT heads (and perhaps fewer than 5) in my 14 years career. Baseline American practice is dramatically different from practice elsewhere in the world. These CT imaging rates are multiple orders of magnitude different from my practice. Decision tools tend to standardize practice, but standardizing towards current American practice would be disastrous. That is why I truly believe that decision rules are ruining medicine. 

A comparison between 2 therapies I don’t have access to for PE

Jaber WA, Gonsalves CF, Stortecky S, Horr S, Pappas O, Gandhi RT, Pereira K, Giri J, Khandhar SJ, Ammar KA, Lasorda DM, Stegman B, Busch L, Dexter DJ 2nd, Azene EM, Daga N, Elmasri F, Kunavarapu CR, Rea ME, Rossi JS, Campbell J, Lindquist J, Raskin A, Smith JC, Tamlyn TM, Hernandez GA, Rali P, Schmidt TR, Bruckel JT, Camacho JC, Li J, Selim S, Toma C, Basra SS, Bergmark BA, Khalsa B, Zlotnick DM, Castle J, O’Connor DJ, Gibson CM; PEERLESS Committees and Investigators*. Large-Bore Mechanical Thrombectomy Versus Catheter-Directed Thrombolysis in the Management of Intermediate-Risk Pulmonary Embolism: Primary Results of the PEERLESS Randomized Controlled Trial. Circulation. 2025 Feb 4;151(5):260-273. doi: 10.1161/CIRCULATIONAHA.124.072364. Epub 2024 Oct 29. PMID: 39470698

This is an open label multicenter RCT comparing mechanical thrombectomy to catheter directed thrombolysis in 550 adult patients with intermediate risk pulmonary embolism. Although the composite outcome is statistically positive, there was no difference in any of the clinical outcomes. Mortality, intracranial hemorrhage, and major bleeding were all the same. There was a slight improvement in escalation of care and ICU use with thrombectomy, but both of those outcomes are highly biased in an unblinded trial, and should clearly be ignored. Catheter directed thrombolysis is given over 12-24 hours, so there is lots of time for abnormal vital signs to make the doctors think something else should be done. Furthermore, hospital rules will often require patients to be in the ICU the entire time they receive thrombolysis even if they don’t need it clinically. These are not true clinical differences, but inherent biases. The real problem with this trial, however, is the lack of a true control group. At this point we have absolutely no evidence that either of these invasive techniques helps patients. Not a shred of evidence. It is ridiculous that they didn’t include a comparison to standard care, either anticoagulation alone, or systemic thrombolysis. Without a proper control group, we have no idea whether these procedures were helpful. We know for sure that they are expensive and invasive. Therefore, before any further work is done, we really need to ensure they are helping.

Bottom line: At this point there is absolutely no evidence that mechanical thrombectomy or catheter directed thrombolysis help patients. There might be times where they are reasonable, even without evidence, such as in a very sick patient with contraindications to systemic thrombolysis. However, neither of these procedures should be used routinely until we see real evidence.

The full write up of this paper is here. 

We go into the management of intermediate and high risk PE at length on this recent Emergency Medicine Cases podcast, and I have a write up of more evidence here. 

People still use the physical exam?! To confirm ETT placement??!!

Hansel J, Law JA, Chrimes N, Higgs A, Cook TM. Clinical tests for confirming tracheal intubation or excluding oesophageal intubation: a diagnostic test accuracy systematic review and meta-analysis. Anaesthesia. 2023 Aug;78(8):1020-1030. doi: 10.1111/anae.16059. Epub 2023 Jun 16. PMID: 37325847

This paper was added because my podcast co-host Casey Parker wanted to rant about airway confirmation. At the time that I am writing this, I have no idea what he is going to say, so you can tune into the podcast to see whether I put my foot in my mouth. This is a systematic review and meta-analysis of clinical exam findings for confirming tracheal intubation. The 5 findings they looked at were ETT misting, lung auscultation, 5-point auscultation, chest rise, bougie hang-up, and the esophageal detector device. They admit the esophageal detector device is not a clinical exam finding, but they include it because of its simplicity and low cost, and therefore importance in low resource settings. This is a high quality systematic review and meta-analysis, following the methodology you would want for systematic reviews, but of course the fatal flaw of most SRMAs is poor quality data in the underlying studies. Apparently there are no human studies looking at the accuracy of bougie hang-up, so we get no results (which is sad because it was the only one I was interested in.) As you might expect, none of these tests are good enough (especially when you account for the 95% confidence intervals), although I was somewhat surprised the numbers were as good as reported. That being said, what number you look at really matters. The sensitivities are universally high, but when confirming tube placement, the number I really care about is what the authors call the “false positive rate”, which is when the ETT is in the esophagus but the test suggests it is in the trachea. Misting occurs 69% of the time with an esophageal intubation! Anyone who looks at ETT misting is clearly making a big mistake. Lung auscultation and 5 point auscultation will be false positive about 15% of the time, which is much too high for a critical decision. Oddly, they leave out the one clinical exam finding that I find truly useful in the era of video laryngoscopy: direct visualization. I leave my video laryngoscope in place while the ETT is being secured, and so I can usually say (absent a heavily soiled airway) with 100% accuracy that the tube is still sitting between the cords, because I can see it there. Of course, none of that really matters, because the clinical exam is clearly a waste of time. You should immediately be checking all tubes with waveform capnography, which is far more accurate, and makes everything else a waste of time. I don’t work in extremely low resource settings, and I don’t know the cost of capnography, but capnography is clearly the standard of care, and it would require pretty extreme circumstances to warrant falling back on any of these other techniques. 

Bottom line: The only test you should use to confirm endotracheal tube position is waveform capnography. 

The ETT as a poor man’s LMA?

Markham T, AlFarra AS, Tejani M, Tate DJ, Barrera JE, Paladugu S, Saroukhani S, Jiang Y. Effectiveness of Ventilation via an Endotracheal Tube in Pharynx Versus a Facemask in Patients With Potentially Difficult Airway: A Randomized, Crossover, and Blind Trial. Anesth Analg. 2025 Feb 1;140(2):280-289. doi: 10.1213/ANE.0000000000007273. Epub 2024 Dec 20. PMID: 39705182

This is a randomized cross-over study comparing bag valve mask ventilation to a technique they call TTIP (endotracheal tube in the pharynx) in 147 paralyzed patients with potentially difficult airways. The TTIP technique involves placing an endotracheal tube in the pharynx, and then pinching the lips closed around the tube to create a seal, and pinching the nose closed with your other hand. (You are essentially using the ETT like an LMA, but that of course begs the question of why you wouldn’t just use the perfectly designed tool for this exact scenario, rather than this more difficult MacGyver technique.) The success rates of TTIP and mask ventilation were 93.4% (127/136) and 84.6% (115/136), respectively (P = .02). They eliminated a handful of patients due to “equipment failure”, but it seems to me that equipment failure is core to the purpose of this trial, and those patients definitely should have been included. A major strength of this study is that they used 2 hand, ideal BVM technique, so I think this represents the ideal BVM results (although that can obviously vary dramatically between clinicians.) One major issue with people considering extrapolating from this paper into real life is that they are looking at “potentially difficult airways”, which are probably very different from the airways one actually encounters in a can’t intubate can’t oxygenate scenario. I am not sure these results will translate (consider the impact of a soiled airway, for example). Another issue might be their choice of comparison. I would be more interested in how this compared to the rescue device we are already using: the LMA. Another minor point is that the gold standard – the first 3 breaths on waveform capnography – might fail differently in these 2 techniques.

Perhaps my biggest problem with this paper comes in the introduction. They set up the need for this technique by stating that anesthesiologists are only successful 35% of the time when performing front of neck access, and they quote the NAP4 audit. In NAP4, surgical front of neck access was actually 100% successful, whereas messing around with an angiocath was what resulted in the dismal success rates that they quote. They are taking the wrong lesson away from NAP4. We are incredibly good at front of neck access as long as we use the correct tool, which is a scalpel. Honestly, there was a time early in my career when I was obsessed with airway hacks. I wanted every possible tool that could potentially stave off disaster. This is undoubtedly a cool trick, and I trust a true airway master to pick the right scenario to pull this out. However, for the vast majority of providers, it seems far more likely that it is going to be a distraction in a seconds matters life threatening scenario. Just use an LMA. If the LMA doesn’t work, just cut the neck. I think you want to keep high acuity low occurrence procedures/algorithms as simple as possible.

Bottom line: We generally suck at BVM, so looking for alternatives, especially in difficult patients (obese with a beard), makes sense. However, I am not sure BVM is the correct comparison for this technique, as it appears to me more of a replacement for an LMA. For now, I will just use an LMA. 

Finally, a problem I can solve easily: air pollution

Lutsey PL, Misialek JR, Young MT, Berman J, Leiser CL, Pope ZC, Cushman M, Folsom AR, Kaufman JD. Air pollution is associated with increased risk of venous thromboembolism: the Multi-Ethnic Study of Atherosclerosis. Blood. 2025 Mar 6;145(10):1089-1096. doi: 10.1182/blood.2024026399. PMID: 39652776

Air pollution is a known risk factor for atherosclerosis, and there are many mechanistic reasons to think it might also be tied to venous thromboembolism. The MESA trial is a prospective observational trial with 6814 patients, originally designed to compare air pollution exposure to atherosclerosis in the United States. This paper uses that same data to assess VTE risk, although they eliminate some patients with missing data, as well as those taking anticoagulants, leaving them with a study population of 6651. The average age was 62 and half were female. There were 248 VTE events (3.7%) over the 16 year study period. It is very unclear to me if they predefined the pollution thresholds they thought would be relevant, but there was a consistent association (with a HR between 1.4 and 2.4) between VTE and three of their measures of air pollution. (Ozone did not seem to have an effect.) One major limitation of my critical appraisal is that I don’t really understand the models they are using for air pollution. Google tells me this data is about as good as it gets, but I don’t know the uncertainty baked into these numbers. The bigger limitation will be confounding. Populations that live in areas with poor air quality often have numerous other risk factors, the biggest probably being income and access to health care. These confounders seem pretty clear in table 1, when comparing the highest and lowest quartiles of air pollution, with clear differences in education level, age, ethnicity, second hand smoke exposure, and physical activity. Finally, one might ask what an emergency physician is supposed to do with this data? This is not the only health implication of air pollution. I spent a lot of time recently reading about the fascinating association between air pollution and intelligence – although I can’t remember if those papers made their way into these summaries. I believe pollution is bad, but whether we can tackle that badness medically is a different question altogether.

Bottom line: There are limitations that significantly limit certainty, but there seems to be an association between air pollution and VTE (among numerous other health implications). 

It is finally time to use ketamine for seizures?

Othman AA, Sadek AA, Ahmed EA, Abdelkreem E. Combined Ketamine and Midazolam Versus Midazolam Alone for Initial Treatment of Pediatric Generalized Convulsive Status Epilepticus (Ket-Mid Study): A Randomized Controlled Trial. Pediatr Neurol. 2025 Mar 22;167:24-32. doi: 10.1016/j.pediatrneurol.2025.03.011. Epub ahead of print. PMID: 40186980

I have spent a lot of time with the status epilepticus literature, and although ketamine has always made theoretical sense, I have left it out of my early algorithm because there really isn’t good clinical data.  This is a double blind placebo controlled RCT comparing ketamine to placebo, given at the same time as midazolam as the first line medication in 144 children between 6 months and 16 years with generalized convulsive status epilepticus from a single hospital in southern Egypt. Ketamine was dosed at 2 mg/kg over 2 minutes and midazolam at 0.2 mg/kg over 2 minutes. A second dose of midazolam was given without ketamine for ongoing seizures, and then their status algorithm completely falls apart – not giving anything else until 20 and 40 minutes into the seizure, which is absolutely crazy. These patients already had incredibly long seizures by the time they were enrolled, with a median of 34 minutes of untreated seizures prior to hospital arrival, which puts them in a very different category than all the patients we are seeing. (Theoretically, the GABA receptors required for benzos to work start disappearing between 15 and 20 minutes, and therefore you would expect midazolam to be far less effective in this cohort than it is in patients seizing for only 5 minutes, which, as we will see, is exactly what happened in this study.) The primary outcome was cessation of seizure by 5 minutes after the first medication dose, and ketamine was dramatically better than placebo (76% vs 21%, p<0.001), but these numbers should be throwing massive red flags. The fact that midazolam only stopped 20% of seizures in the control group is abysmal. It is unheard of, and just does not fit with other available literature. Usually, our first line benzo is about 70-80% successful, which is what we saw with the ketamine group here. In other words, the ‘benefit’ seen in this trial might not be a positive in the ketamine group, but a massive negative, for some reason, in the control group. The difference between the groups is a lot smaller in patients with seizures less than 30 minutes, and I wonder if it would completely disappear if we focused on patients with seizures less than 10 minutes. Considering this is a single center trial from southern Egypt, with dramatically different results than we are used to seeing, I think we need to be very cautious about extrapolating these results. I don’t think that this means that ketamine is a first line seizure medication. That being said, this is better data that is available for propofol, which I currently recommend as the second line agent in status epilepticus, so I think there is clearly an argument that ketamine could be incorporated in the algorithm somewhere. At this point, I am just not sure where. (Although, if you want to focus on evidence-based medicine, the best argument is almost certainly for phenobarbital.) 

Bottom line: When used very late in status epilepticus, ketamine plus midazolam is better than midazolam alone, but we should be cautious of the limitations of this small single center study looking at a very different population than we are used to treating.

Weingart disagrees with my interpretation of this study. I think there will be a debate on an upcoming episode of his podcast, if you are interested in more. 

One Policy to Rule Them All

Spellberg B. The Policy to Override Policies-One Policy to Rule Them All. JAMA Intern Med. 2024 Dec 1;184(12):1408-1409. doi: 10.1001/jamainternmed.2024.4625. PMID: 39401007

From what Iunderstand, Canada is far better than America when it comes to policies, rules, and regulations that impact your daily practice of medicine. That being said, “it is hospital policy” still remains a common barrier preventing good patient care in my practice. (Sometimes there really is a hospital policy. Sometimes this is just an excuse that is impossible to refute at 2am on a Saturday, and so just used as a way to end all reasonable discussion.) In that context, I love this paper. He starts with an unbelievable (but real) story of a patient who was mugged, had a broken leg, and needed surgery. Hospital policy required patients to have valid identification to proceed with surgery. The patient’s wallet had been stolen in the mugging, and therefore the patient could not be brought to the operating room, to the incredible ire of the entire clinical team. Most conflicts are not quite this stupid, but the fact that I can see this happening in real life (and not just a Monty Python sketch) tells you how bad hospital management can sometimes be. When policies and rules are presented rigidly by management, clinical staff are rightly afraid to break them, even if they are obviously interfering with good patient care. No one wants to risk losing their job just for one patient. Frustrated by such scenarios, and recognizing that patients are so complex that no policy, no matter how well written, could ever cover every possible clinical scenario, this hospital developed “the policy to override policies”. The policy allows any staff member to override any policy given that:

• “Both the staff member and their supervisor have a shared reasonable belief, and document their rationale, that the override is in the best interest of the patient or staff in that instance. A reasonable belief is “one that is likely to be agreed with by other similarly qualified people under similar circumstances.”
• After the acute situation resolves, the supervisor must notify their manager about the override so consideration can be given regarding a possible revision to the relevant policy to preclude the need for a future repeat override.
• The override can only be done by staff whose profession is specific to the policy in question (ie, only nurses can override nursing policies, only pharmacists can override pharmacy policies, only physicians can override physician policies).” I will admit, this last part makes me nervous, as good patient care is not profession specific, and I am not sure there is anything that falls outside of the purview of the person writing the orders and taking ultimate responsibility for the patient. Rules that allow someone at home, who has never seen or spoken to the patient, to override the physician’s judgement are very problematic. 

I think this is amazing. I would take a job at this hospital in a second. They are not only putting patient care first, but also striving to constantly improve, by identifying and improving flawed policies. I don’t think I have ever worked in a place with this much common sense, compassion, and commitment to patient safety. They say that the policy is rarely used, but anecdotally has empowered staff to solve problems in real time, knowing they are supported by the hospital. This is a policy that every hospital should adopt. If you work in an administrative role, copy and paste this policy (perhaps adjusting point 3), and get it implemented as soon as possible. 

Cheesy Joke of the Month

What did one tectonic plate say when he bumped into the other?

Sorry! My fault.