The use of procalcitonin to guide antibiotic therapy has been gradually increasing over the past several years – driven, in no small part, by increased recognition of the harms of antibiotic overuse. However, what evidence we have regarding its utility is primarily derived from manufacturer-sponsored trials – including virtual carpet-bombing of the literature by their sponsored representatives.

So, what happens when the manufacturer isn’t part of the trial?

No benefit.

This is the ProACT trial, an individual-randomized comparison between a procalcitonin-guided arm and “usual care” in patients with suspected lower respiratory tract infection for whom the indication for antibiotics is unclear. Physicians caring for patients randomized to the procalcitonin arm were provided results tied to antibiotic use recommendations – “strongly discouraged”, “discouraged”, “encouraged”, “strongly encouraged” – on initial presentation in the Emergency Department, and then in serial fashion for those admitted to the hospital. In those in the “usual care” arm, procalcitonin results were obtained, but not provided to the treating clinicians.

Then: Across 14 hospitals and 1,656 patients, there were no statistically significant differences between antibiotic-free days or adverse outcomes between the two arms. Done? Done.

Except, as skeptical as I might be regarding procalcitonin-guided therapy, there are big holes in these data as the definitive word on its disutility. Unlike other trials, these centers provided only passive guidance to clinicians regarding the procalcitonin algorithm. This resulted in only 72.9% of physicians adhering to protocol, with the greatest numbers of violations being antibiotic use in patients for whom it were discouraged, including 30% of those for whom antibiotic use was “strongly discouraged”:

Even though the “per-guideline” analysis also shows no difference, this is mostly because the bulk of the procalcitonin “per-guideline” population were those who appropriately received antibiotics – effectively eliminating the possibility of showing a difference in antibiotic use.

There are a few signals within these data reflecting the potential advantages of a procalcitonin-guided algorithm, should the protocol actually be followed. There were small differences in prescribing favoring the procalcitonin arm for almost every final clinical diagnosis – excepting about 15% absolute advantages for “acute bronchitis” and for those with non-specific diagnoses. It is likely these represented the cases for which the appropriateness of antibiotics was lowest, and probably also represent the majority of protocol violations. That said, one could easily make the argument this advantage only exists as a result of culturally-ingrained poor antibiotic prescribing habits for these sorts of borderline cases.

In short, these data clearly show there is no advantage to introducing procalcitonin into practice specifically in the fashion demonstrated here – but these cannot be generalized to say a different implementation or application of procalcitonin has no value.  There is work yet to be done for both proponents and skeptics of its value.

“Procalcitonin-Guided Use of Antibiotics for Lower Respiratory Tract Infection”

Wake Up and Smell the tPA

What happens when you wake up and you’re paralyzed from a stroke? Well, usually nothing. “Unknown time of onset” takes you – for better or worse – out of the game for alteplase, but not necessarily for endovascular therapy should a large-vessel occlusion be identified. Those large vessel occlusions, in the setting of a favorable CT perfusion profile, seem to benefit from endovascular therapy.

But, getting back to the “wake up stroke” – these have had our neurologists gnashing their teeth for some time. They have hypothesized many of these strokes have occurred just before waking and might otherwise be eligible for treatment. Absent reliable presenting information regarding the time of onset, these authors look to MRI – using presence of DWI lesion without corresponding FLAIR signal as a surrogate for tissue viability/stroke recency. Exclusion criteria in addition to the usual alteplase culprits were extremes of age, premorbid functional disability, NIHSS >25, thrombectomy candidates, and those with infarct volumes greater than 1/3rd the MCA territory. The primary outcome was 0 or 1 on the mRS at 90 days, like most trials.

These authors in this multicenter, placebo-controlled planned to enroll 800 patients, but ran out of money after five years and 503 patients. To get to these 503, the authors needed to screen 1362 potential strokes. These 859 exclusions were for various reasons, but over half were because the FLAIR matched the DWI lesion – indicated a completed infarct. Another 137 had negative DWI – i.e., not stroke – and various others had hemorrhage, failed to meet criteria for infarct size, or a scattering of other exclusions. Even despite these exclusions, another 79 snuck through as protocol violations, including 48 who should have been excluded based on imaging criteria.

Now, the meat: About 95% of those included were of the “wake up” variety, nearly all from overnight sleep. Baseline clinical features were generally well-matched. Median NIHSS was 6 in each group, although median lesion volume on DWI was 2.0 mL in the alteplase cohort as compared to 2.5 with placebo. At 90 days, 53.3% of the alteplase cohort achieved an mRS of 0-1 as compared with 41.8% with placebo. Bleeding complications, as typical, favored the placebo cohort – with absolute advantages ranging from 1.6% to 3.6%, depending on the definition of hemorrhage used. Death at 90 days also favored placebo at 1.2% versus 4.1%.

It is difficult to know what to do with these data unless your system is specifically equipped to replicate the conditions of this trial with rapid MRI. Even then, there are some oddities and specific warnings to unpack. If adhering to this protocol, the majority of patients screened will not be eligible for treatment. The number of patients who had completed their infarction was similar to those who had DWI/FLAIR mismatch, and another third had other imaging or clinical findings excluding them from treatment. Incorporating MRI into workflow may not yet represent a high-value approach.

Then, the authors performed a pre-specified subgroup analysis stratifying based on NIHSS – and the 109 analyzed patients with a NIHSS >10 did terrible. Only 13.5% of those in the tPA cohort and 12.3% of those receiving placebo achieved mRS 0 or 1. Unpacking these stratifications further, the authors provide us a whole host of breakdowns:

Generally, not too much should be read into these secondary outcomes, but they are useful for generating equipoise for other investigations.  That said, these data should be at least a useful cautionary tale regarding the value of tPA in the setting of mild, but disabling stroke – as these 175 patients represent at least six times more patients than from NINDS, and are of higher quality evidence than any of the Get With the Guidelines publications trying to build the case for tPA in mild stroke.

One takeaway that should definitely not be generated from this is: “well, if there’s an absolute increase in good outcome of 12% on those screened with MRI, then treating all ‘wake up’ patients after screening with just CT could generate about a 6% absolute benefit, and that should be offered to patients.”  Unfortunately, I suspect we will hear such calls – probably based on parsing out the low NIHSS patients in the subgroups above, and trying to toss out the ~30% with a large-vessel occlusion identified on MRA as patients who should be triaged to endovascular.  Again, trying to pick and choose the secondary outcomes that suit your narrative is fraught with peril, and the fact remains such a treatment strategy is also likely to generate harms greater than those seen in this trial.  These data ought to have a very narrow application – but shareholders and executives don’t realized dividends when alteplase isn’t flying off the shelves for expanded indications.

“MRI-Guided Thrombolysis for Stroke with Unknown Time of Onset”

Snacking Before Bedtime

How long before a procedural sedation is fasting required? You know, of course, the American Society of Anesthesiologists guidelines specify: a mini- mum fasting period of 2 hours for clear liquids, 4 hours for breast milk, 6 hours for infant formula and light meals, and 8 hours for solids containing meat or fatty foods.

Of course, anecdotally – if anecdotally means hundreds of thousands of safe sedations – Emergency Physicians have known these restrictions are nonsense.

But, guidelines are best written off published evidence – so, we have a pre-planned analysis of the relationship between fasting time and vomiting from a Canadian cohort study of pediatric sedation. With 6,295 sedations included in their analysis, almost half of whom did not meet solids fasting guidelines, these authors found no relationship between fasting time and vomiting. There were, even, only six instances of intra-procedure vomiting, and fasting duration ranged from 1.7 hours to 17.5 hours – but they all received ketamine. None of the intra-procedure, or ~300 peri-procedural episodes of vomiting, resulted in pulmonary aspiration. No relationship was found between fasting time and any other type of adverse event, either.

So, another useful piece of literature to wave around in committee meetings – both to eliminate any fasting restrictions, and, again, to help demonstrate the safety of EP-performed procedural sedation.

“Association of Preprocedural Fasting With Outcomes of Emergency Department Sedation in Children”