Research Roundup for January 2025

Do you change your practice when new evidence is published? Will these articles change your practice? Will you read them? Does anyone read them? I don’t know, but here is another month of my reading summarized. 

For the regular readers, you will have noticed I have taken a few weeks off. February is also likely to be pretty slow. That is partly because I do occasionally need to take time away from this hobby that so utterly dominates the hours in my days, but also because I have been spending a lot of time on a few longer form projects. So you can expect more good content in the future, but please excuse a few lighter months in the meantime.

Airway, breathing, cellphone: a new vital sign?

Garcia SI, Jacobson A, Moore GP, Frank J, Gifford W, Johnson S, Lazaro-Paulina D, Mullan A, Finch AS. Airway, breathing, cellphone: a new vital sign? Int J Emerg Med. 2024 Nov 22;17(1):177. doi: 10.1186/s12245-024-00769-0. PMID: 39578750

If a patient is actively scrolling on their phone, might that be a sign that they are less sick? This paper describes a prospective cohort of 292 adult patients who had their cell phone use recorded at the time of initial encounter, and compared that to patient disposition. It is a well designed observational study, with both providers and patients blinded to the study. (Cell phone use was recorded by scribes.) Most patients (89%) were not using their cell phone at the time of first encounter (which seems high to me). Among patients using the cell phone, 94% were discharged home, as compared to only a 64% discharge rate among those who were not using their phone. The odds ratio for discharge among cell phone users was therefore both clinically and statistically significant (OR 8.4 95% CI 1.96-36) The admission rate here is very high, when compared to my community emergency practice, and I am not sure if that is the result of being a tertiary center, or because its an American study. Despite being a well designed trial, there are a number of factors that limit the value of this finding. In general, I have a very hard time adopting any observational research done in America to my own practice, because medicine there just looks nothing like medicine in the rest of the world. There is also a ton of complexity that isn’t captured here. In my population, many patients have their cellphones in hand because they need someone on the other end to help translate. I also see patients clinging to their cell phone because it contains all the information about their current complex treatment at the cancer centre. Of course there are patients watching YouTube – even some adult patients who continue to watch YouTube throughout our entire encounter – but the point is that this is a more complex behavior than is captured by “cell phone yes or no”. They don’t share any information by demographics, and there is good reason to believe that phone use might vary dramatically by age. I also wonder about the basic theoretical underpinning for this hypothesis. Although it is true that most patients with renal colic are in too much pain to scroll instagram, distraction is a great tool for managing pain and stress. When I am at my sickest, I try to find any way I can to distract myself, and the modern day crack of social media is a great way to do that. (Although I have not been recently admitted to hospital, so I guess that doesn’t tell you much.) My point is, I could easily imagine a U shaped curve, where both the really healthy and the really sick have increased cell phone use. Finally, just looking at phone use at a single point in time could be problematic. I imagine there are some complex social factors at play when waiting for a doctor. Some people might consider it rude to be on a phone when the doctor enters the room, but if you work in a department with very long wait times, I imagine patients might start caring a lot less about those social niceties.

Bottom line: This is a well done observational study that demonstrates an association between cell phone use and disposition to home, but I think the complexity really highlights the difficulty of making strong conclusions from observational data. I can’t imagine that this data is clinically helpful. (I would be worried if people were using this as a data point to make medical decisions.)

Hyponatremia: Are we all doing this wrong?

Ayus JC, Moritz ML, Fuentes NA, Mejia JR, Alfonso JM, Shin S, Fralick M, Ciapponi A. Correction Rates and Clinical Outcomes in Hospitalized Adults With Severe Hyponatremia: A Systematic Review and Meta-Analysis. JAMA Intern Med. 2024 Nov 18:e245981. doi: 10.1001/jamainternmed.2024.5981. PMID: 39556338

This is far from perfect data, but it feels like it could (and maybe should) lead to practice changes in the emergency medicine community. When managing hyponatremia, the primary concern (at least as far as I have always been taught) is osmotic demyelination syndrome. We are warned not to correct the sodium too quickly, because the neurologic outcomes can be awful. However, demyelination is very rare, and apparently there is a lot of data that suggests correcting sodium too slowly can increase mortality! This is a systematic review and meta-analysis that includes 16 studies encompassing 11,811 patients. The looked at either severe hyponatremia, defined as a sodium less than 120 mEq/L, or severe symptomatic hyponatremia, defined as a sodium less than 125 mEq/L plus “severe symptoms, including cardiorespiratory distress, seizures, Glasgow Coma Scale ≤8, or decreased level of consciousness).” They looked at 4 different speeds of sodium correction (>12 mEq, ≥8-10 mEq/L,<8 or 6-10 mEq/L, or <4-6 mEq/L in 24 hours). Faster correction was associated with a significant improvement in mortality. They estimate that for every 1000 patients treated, there are 32 fewer deaths if you are ‘fast’ rather than ‘slow’ and 221 fewer deaths if you are ‘fast’ rather than ‘very slow’. Hospital length of stay is also shorter if you go faster. This data doesn’t find a statistical difference in rates of osmotic demyelination syndrome, but it does look a little bit higher the faster you go. However, their point is that the numbers are at least an order of magnitude less than the mortality numbers. (Their estimates equate to  0.5 cases of demyelination syndrome per 1000 patients treated when comparing rapid to slow treatment, or 2 cases per 1000 when comparing rapid to very slow.) Of course, this is all observational data, and not data designed to answer this question, so we need to be cautious in our interpretations. There is evidence of confounding in the data, with sicker patients (CHF, cirrhosis, metastatic cancer) getting corrected slower, whether on purpose or because they are harder to correct. On the other hand, we do this all the time in medicine, focusing on one specific outcome and losing track of the overall status of the patient. In this case, as much as demyelination is an important outcome, it appears that we have been overly afraid of a very rare outcome, to the point that we might be increasing mortality. This definitely warrants follow-up RCTs, but in the meantime, I think the data is convincing enough to tell us that we should potentially be correcting sodium faster than we have historically been taught.

Bottom line: This meta-analysis of observational data shows an association between slower sodium correction in severe hyponatremia and increased mortality. These results are not definitive, but considering the rarity of demyelination, and the magnitude of the mortality results, this should probably influence clinical practice until we get the proper RCTs.

Full post here.

WOMAN is so negative

WOMAN-2 Trial Collaborators. The effect of tranexamic acid on postpartum bleeding in women with moderate and severe anaemia (WOMAN-2): an international, randomised, double-blind, placebo-controlled trial. Lancet. 2024 Oct 26;404(10463):1645-1656. doi: 10.1016/S0140-6736(24)01749-5. PMID: 39461792

This trial is not actually all that relevant to emergency physicians, but seeing as I still see TXA recommended in every postpartum hemorrhage talk, I decided to include it as a reminder that all of the evidence so far pretty clearly demonstrates no value of TXA in PPH. WOMAN-2 is a preventative trial, comparing TXA to placebo prophylactically in 15,068 women with baseline moderate to severe anemia who were in labour. There was no difference in their primary outcome, with 7.0% of the TXA group and 6.6% of the placebo group experiencing postpartum hemorrhage (RR 1·05, 95% CI 0·94–1·19). “Deaths or near misses” occurred in 1.6% of the TXA group vs 1.8% of the placebo group. There were no differences in any of the secondary outcomes. There were no vascular occlusive events (ie, pulmonary embolism, deep vein thrombosis, stroke, or myocardial infarction) reported in either group. The major limitation of this trial is that harms were obviously not measured correctly, which has been a consistent theme throughout the TXA literature. None of the big TXA trials has convincingly captured the harms of TXA, but this is the easiest trial to prove that point. They have a cohort of over 15,000 women in the immediate postpartum period, and they didn’t find a single vascular occlusive event in the entire cohort? How is that possible?! The rate of PE and DVT alone is approximately 10-15 per 10,000 deliveries. We should have had more than 20 in a study this large. The only way to have 0 events is to have your eyes closed. I think this is a consistent theme in all of the TXA literature, and why no one should feel comfortable making the claim that “TXA is safe” based on the data we have.

Bottom line: The WOMAN 2 trial is a large double-blind RCT that shows no benefit of TXA in the prevention of postpartum hemorrhage, which fits with all of the existing literature demonstrating no role for TXA in the management of postpartum hemorrhage. 

Full blog post here.`

But what about this positive meta-analysis?

Ker K, Sentilhes L, Shakur-Still H, Madar H, Deneux-Tharaux C, Saade G, Pacheco LD, Ageron FX, Mansukhani R, Balogun E, Brenner A, Prowse D, Arribas M, Ahmadzia H, Chaudhri R, Olayemi O, Roberts I; Anti-fibrinolytics Trialists Collaborators Obstetric Group. Tranexamic acid for postpartum bleeding: a systematic review and individual patient data meta-analysis of randomised controlled trials. Lancet. 2024 Oct 26;404(10463):1657-1667. doi: 10.1016/S0140-6736(24)02102-0. PMID: 39461793

In the same issue as the last paper, there was a systematic review that concluded “tranexamic acid reduces the risk of life-threatening postpartum bleeding”. Obviously, that doesn’t fit with my summary above, which was that all of the existing research is pretty clearly negative, so we better have a look. They include 54,404 patients from five RCTs, and they conclude that “life threatening bleeding” is decreased with TXA from 0.85% to 0.65% (p=0.008). Obviously the first problem is that although this is statistically positive, the difference is miniscule, with the baseline risk being less than 1%, and the number needed to treat being 500. Another big issue is that the primary outcome – “life threatening bleeding” – is a composite outcome defined as death or any surgical or procedural intervention from bleeding. The components of the outcomes are not equal, although I think both are valuable. Oddly, they don’t report on simple mortality anywhere in the review. They talk about 24 hour mortality (0.5% vs 0.7%) and “death due to bleeding” (0.5% vs 0.7%), but those clearly aren’t the most important overall outcomes. They don’t find any statistical increase in thrombotic events, but as I said above, there is a concern that adverse events are being missed in these trials, because the PE rate is 0.08% with TXA and 0.09% with placebo, which is less than half of what you would expect.

Bottom line: With some massive trials, we are able to find a statistical difference, but with such a miniscule clinical difference in a composite outcome, it is not at all clear that there is a benefit here that could outweigh harm (as safe as TXA is, all medications have harms). 

If you want to read more about the individual trials of TXA in PPH, check on the blog post “Does TXA work for everything? For anything?“

More negative TXA research

Yassi N, Zhao H, Churilov L, Wu TY, Ma H, Nguyen HT, Cheung A, Meretoja A, Mai DT, Kleinig T, Jeng JS, Choi PMC, Duc PD, Brown H, Ranta A, Spratt N, Cloud GC, Wang HK, Grimley R, Mahawish K, Cho DY, Shah D, Nguyen TMP, Sharma G, Yogendrakumar V, Yan B, Harrison EL, Devlin M, Cordato D, Martinez-Majander N, Strbian D, Thijs V, Sanders LM, Anderson D, Parsons MW, Campbell BCV, Donnan GA, Davis SM; STOP-MSU Trial Investigators. Tranexamic acid versus placebo in individuals with intracerebral haemorrhage treated within 2 h of symptom onset (STOP-MSU): an international, double-blind, randomised, phase 2 trial. Lancet Neurol. 2024 Jun;23(6):577-587. doi: 10.1016/S1474-4422(24)00128-5. Epub 2024 Apr 20. PMID: 38648814

I have covered TXA relatively extensively (probably too extensively for the value of the product) in the past, including previous negative trials in intracerebral hemorrhage. I was therefore surprised to see a phase 2 trial on the topic, especially a large multicentre phase 2 trial, but that is exactly what the STOP-MSU trial is. It is a double blind RCT from 25 sites in Australia, Finland, New Zealand, Taiwan, and Vietnam. They enrolled 201 adult patients with spontaneous intracerebral hemorrhage, a GCS 8 or above, and not taking any form of anticoagulation, and randomized them to standard dose TXA or matching placebo. The primary outcome was hematoma growth at 24 hours. I think this is probably a very poor surrogate outcome, because although there is an association between hematoma growth and clinical outcomes in observational trials, we now have many large RCTs in which there was a difference in hematoma growth, but absolutely no difference in clinical outcomes like mortality or neurologic function, which really should cast doubt on the value of this surrogate outcome. For what it is worth, there was no difference in the primary outcome, but the confidence intervals are huge, and the point estimate actually looked better in the placebo group (38% vs 43%, aOR 1.31 95% CI 0.72 – 2.4). That being said, the absolute increase in hematoma size was only a mean of 2 mL in both groups. Mortality and neurologic outcomes look the same, but major thrombotic events were 3 times higher with TXA (1% vs 3%), but that difference is not statistical in such a small trial. Overall, this trial confuses me. I am not sure why you would classify this as a phase 2 trial, when there is already lots of research in this area. For example, the TICH 2 trial was an RCT with more than 2300 patients showing no benefit of TXA in nontraumatic intracranial hemorrhage. Another problem is that they changed their sample size many times, but it is odd to me that they went through the massive effort of organizing a 5 country 25 site placebo controlled RCT to only enroll 200 patients. Finally, using a surrogate outcome makes sense for a 200 patient trial, but it doesn’t make sense overall. At this point, we understand the basics of TXA, and surrogates absolutely should not change practice. Research needs to focus on real clinical outcomes to provide value. Despite the limitations, the conclusions are clear: this fits with all the available evidence to date that TXA has no role for patients with blood in their heads.

Bottom line: This is an international multi-centre phase 2 placebo controlled RCT that demonstrated no benefit in terms of hematoma growth when comparing TXA to placebo in patients with spontaneous intracerebral hemorrhage. 

Epipens don’t work? (Not so fast)

Sim M, Sharma V, Li K, Gowland MH, Garcez T, Shilladay C, Pumphrey R, Patel N, Turner PJ, Boyle RJ. Adrenaline Auto-Injectors for Preventing Fatal Anaphylaxis. Clin Exp Allergy. 2024 Oct 9. doi: 10.1111/cea.14565. Epub ahead of print. PMID: 39383344

I heard this paper discussed rather un-skeptically on a popular science podcast, so I decided to look it up. Considering the lack of clinical trials involving adrenaline in anaphylaxis, this encompasses a huge amount of data, from demographics, to animal studies, and pharmacokinetics. The underlying concern seems to be that despite a massive increase in the rate of anaphylaxis diagnosis, and therefore a massive increase in the rate of epinephrine autoinjector prescriptions, the rate of fatal anaphylaxis has remained flat over the decades. My guess, as we have discussed before, is that this is simply proving that anaphylaxis is massively overdiagnosed in modern medicine. The authors, instead, worry that epinephrine auto-injectors may be ineffective. I think that is clearly an overcall of messy data, and in fact, they present a human case control series comparing fatal anaphylaxis to near-fatal, and all survivors received IM epinephrine within 5 minutes of symptoms onset, as compared to none of the patients who died. However, as far as auto-injectors go, the current dose is completely ascientific, inherited from an era before evidence based medicine. In the emergency department, almost all of us use higher dose IM epinephrine (I would think 0.5 mg is the standard dose now), so why are the autoinjectors still using 0.3 mg? They present a load of data that suggests variable absorption of IM epinephrine, and more importantly an unpredictable cardiovascular response with no clear impact on blood pressure (and just a slight increase in heart rate). An RCT comparing different auto-injector doses is probably warranted, although I am very reluctant to give pharmaceutical companies a new reason to patent and therefore increase the prices on these devices. Another interesting question is what we should do in the hospital, where IV access is readily available. These authors suggest that an IV infusion might be a better option than an IM dose. I certainly move rapidly to an IV infusion in sick patients, but given the extent to which we overcall anaphylaxis, and the generally fantastic outcomes, combined with potential adverse events when errors are made given epinephrine intravenously, it seems like it would be a mistake to make this routine practice. At the end of the day, this paper might just be a lot of words without saying anything clinically relevant, but I found it an interesting read, and I am not sure how I would interpret this data if my child had anaphylaxis. Perhaps we need to be counseling people to carry more than one epi-pen, and to be ready to give multiple doses to better approximate the therapy they would receive in hospital? Then again, given the exorbitant price gouging we have seen with these auto-injectors (which were initially developed using public funds for the military in the 1960s), asking people to spend more on these also seems problematic.

Bottom line: I dont know.

Profundus

Morello F, Bima P, Castelli M, Capretti E, de Matos Soeiro A, Cipriano A, Costantino G, Vanni S, Leidel BA, Kaufmann BA, Osman A, Candelli M, Capsoni N, Behringer W, Capuano M, Ascione G, Leal TCAT, Ghiadoni L, Pivetta E, Grifoni S, Lupia E, Nazerian P; PROFUNDUS Study Investigators. Diagnosis of acute aortic syndromes with ultrasound and d-dimer: the PROFUNDUS study. Eur J Intern Med. 2024 Oct;128:94-103. doi: 10.1016/j.ejim.2024.05.029. Epub 2024 Jun 12. PMID: 38871565

Many people sent me the PROFUNDUS study to review, but it took me a while to get motivated, because even a quick glance at the abstract made it clear that this was not going to be practice changing. Diagnosing aortic dissection is hard, and unlike other conditions, it is certainly possible that the ideal diagnostic strategy requires us to image more, not less. However, I don’t know that that is true, and unless someone gets a sense of the test and treatment thresholds and the current imaging and miss rates, all aortic dissection diagnostic studies will suffer from a lack of an appropriate standard against which to compare. This is a prospective observational trial from 12 emergency departments in 5 countries looking at a protocol to attempt to ‘rule out’ aortic dissection. Their protocol involved classifying patients as low or high risk based on the combination of the ADD score and an extensive ultrasound examination. Low risk patients then had a DDimer sent. Any patient in this high risk category, or low risk plus a DDimer over 500 ng/mL was supposed to get a CT angiogram. The inclusion criteria for this trial is incredibly broad: any thoracic, back, abdominal pain, syncope, or organ perfusion deficit within 14 days. That means that close to 100% of emergency department patients could have this rule applied, and with a specificity of 52%, this rule would dramatically increase the number of patients getting CTs. (This is a European study, so they actually imaged an appropriately high risk cohort despite the wide inclusion criteria.) The fact that everyone with any of these symptoms has a DDimer sent, and that imaging is recommended for anyone with a DDimer over 500 mg/mL means that I would probably have to add at least 5 extra aorta CTs on every single shift. This isn’t just conjecture. Less than half of the patients that entered this algorithm were ruled out, meaning more than half needed a CT scan. They screened 3022 patients and enrolled 1979, of whom 176 (8.9%) were diagnosed with aortic dissection, which makes this a very high risk population (and unlikely to be representative of the population that would ultimately have such a protocol applied to them). 85% had a low risk ADD score, and ultrasound reclassified 6% as high risk. DDimer was positive in another 640 of the low risk patients, and so at the end of the day their algorithm suggested CT imaging in 52% of all patients. In fact, a bunch of the low risk patients had advanced imaging anyway, so this protocol only avoided imaging in 41% of patients (and remember how wide their inclusion criteria were). The result is a sensitivity of 100% (95% CI to 98%) and a specificity of 52% (95% CI 50-55%). Although the 100% sensitivity is good, the real question is how this rule changes overall practice, and considering the massive range of patients this could be applied to, and the very low specificity, this rule will definitely increase imaging (and probably increase it dramatically). This protocol, with fairly intense echo requirements that most ED physicians may not currently be comfortable with, is also very time intensive. ED physician time is a scarce resource in most settings, and extra time spent doing bedside ultrasound on a low risk aortic dissection patient is time taken away from other patients in the department. As I said at the outset, increasing imaging for aortic dissection might be reasonable, but we just don’t know. You can’t change practice based on a trial like this, that is designed only to look at the sensitivity. We need to know how this protocol changes practice. We need to know how many extra studies it adds for every extra aortic dissection diagnosed. Without comparisons to current practice and basic clinical judgement, it is impossible to judge either the harms or benefits of this rule, and therefore this type of research should only be looked at by researchers planning future studies, and not clinicians. 

The big problem with aortic dissection is that the presentations seem to vary dramatically. At least half of patients seem to present with obvious dissection, with symptoms straight out of the textbook. Those patients don’t need rules or protocols like this. A significant minority seem to have very unusual or subtle symptoms. I have a family member who had a dissection from the coronaries to the iliacs and the only symptom was weeks of night sweats (the dissection was caught on a CT looking for infectious causes of symptoms). In the sea of vague and undifferentiated symptoms in the emergency department, it isn’t clear that rules or protocols can help with those patients either, because if we apply these rules to every patient, we will have to image a huge percentage of our population. 

Bottom line:  The diagnosis of aortic dissection is very hard, but this protocol is not ready to be used in clinical practice.

Dr Casey Parker has a good critical appraisal of this article, with extra ultrasound expertise, available here: https://www.youtube.com/watch?v=j_ejoaVynXI&ab_channel=CaseyParker

Side effects of decision rules, or the law of unintended consequences

Weber EJ, Carlton EW. Side effects of decision rules, or the law of unintended consequences. Emerg Med J. 2019 Jan;36(1):2-3. doi: 10.1136/emermed-2018-208151. Epub 2018 Oct 25. PMID: 30361207

As a short, toned down version of my “decision rules are ruining medicine” rant, I was bound to enjoy this essay. It is probably too toned down, over-estimating the benefit that rules are currently bringing to medicine, and under-estimating the harms, but at least they are shining light on the harms (which is something most people ignore). They state “The primary goal for all of these rules is to avoid missed diagnosis. When deriving decision rules, researchers often set out to achieve one overarching goal—a sensitivity approaching 100%, often at the cost of specificity. This means that a number of patients who do not need the tests will still get them.” Despite being endorsed by people who don’t understand the underlying science at places like Choosing Wisely, decision rules increase test use. That might be OK if baseline clinical judgement sucked, and we needed these rules to help us avoid misses. Unfortunately, for most rules, the best evidence available is that our judgement is at least as good as the rule. Therefore, rules just increase overall testing with no benefit. The authors also point out the massive unintended consequences for patients who are not captured by the rules. Once a rule has been designed, physicians feel compelled to test everyone who falls out of the strict parameters of that rule, which is insane. This is why so many patients over 65 are getting completely unnecessary head CTs. “The most striking (and expensive) example of this is the recommendation by a number of societies to perform CT scans in all patients with head injury who are anticoagulated. There are even recommendations to scan twice for the rare complication of late bleeding. But where is the data? In fact, as described in the expert practice review by Mason et al, the AHEAD study, the largest prospective observational study of patients with head injury anticoagulated with warfarin, found little support for either of these practices.” “The absence of evidence should not immediately trigger a non-evidence-based recommendation to fill the gap but rather suggests that physicians should practice based on their knowledge, experience and a bit of gestalt.”

Bottom line: I am not the only person telling you that decision rules are increasing testing and causing a lot of harm. Be cautious and thoughtful. 

Killer antibiotic stewardship

Dark P, Hossain A, McAuley DF, Brealey D, Carlson G, Clayton JC, Felton TW, Ghuman BK, Gordon AC, Hellyer TP, Lone NI, Manazar U, Richards G, McCullagh IJ, McMullan R, McNamee JJ, McNeil HC, Mouncey PR, Naisbitt MJ, Parker RJ, Poole RL, Rostron AJ, Singer M, Stevenson MD, Walsh TS, Welters ID, Whitehouse T, Whiteley S, Wilson P, Young KK, Perkins GD, Lall R; ADAPT-Sepsis Collaborators. Biomarker-Guided Antibiotic Duration for Hospitalized Patients With Suspected Sepsis: The ADAPT-Sepsis Randomized Clinical Trial. JAMA. 2024 Dec 9. doi: 10.1001/jama.2024.26458. PMID: 39652885

Despite being a huge multicenter effort, I really don’t think this trial should have been allowed to proceed as designed. It is a 3 group trial looking at procalcitonin or CRP (versus standard care) as an approach to decrease antibiotics in 2760 adult patients in the ICU with sepsis. The fatal flaw with the study is that they used a non-inferiority design for the primary safety outcome of mortality, and decided to use a cut-off of 5.4%. In other words, they assumed that as long as you could cut down on antibiotics a little bit, you would be fine with up to a 5.39% increase in mortality. That is ridiculous, and therefore it was obvious before the trial was even run that these results should not be applied clinically. As far as results go, they did see a decrease in antibiotic use (by 0.9 days) with procalcitonin, but not CRP. However, mortality was 1.5% higher in the procalcitonin group, and so although their ridiculous stats allow them to conclude that treatment is “non-inferior”, the only fair conclusion, based on this research in isolation, is that their strategy will result in more dead patients, but will save a few doses of ceftriaxone. That being said, I am not even sure it would save a few doses of ceftriaxone, because the trial design was heavily biased to show a decrease in antibiotic use. The computer message sent to the standard care group was identical to the message in the high procalcitonin group, and therefore clinicians could easily be convinced to continue antibiotics in patients they would have otherwise stopped. I have absolutely no idea how this trial design got past funders, ethics boards, and the JAMA editorial board, but it should never have been run as designed, and the results very clearly indicate that this procalcitonin strategy should not be used in clinical practice.

Bottom line: If you are willing to risk a substantial increase in mortality, you can cut back on antibiotic use by following a patient’s procalcitonin.

Full post here.

Cheesy Joke of the Month

Why did no one laugh when the King farted?

Because noble gases don’t cause a reaction