GCS 8 obviously doesn’t mean intubate (in tox or otherwise)

Although it made a bit of a splash when published, this article really didn’t interest me. Obviously, GCS 8 doesn’t mean intubate. I didn’t think anyone was simplistic enough to practice medicine based on a jingle. Clearly trajectory matters. If a patient’s GCS hit 8 and they are on a clinical course where you expect them to continue to deteriorate, with no hope of short term recovery, of course intubation makes sense. (Even in this case, I am never calculating an actual GCS.) However, that doesn’t describe the vast majority of our ED patients. I see many post-ictal patients with a GCS of 3 or 4, and I obviously don’t intubate, as they will improve rapidly. Many of my COPD patients present with CO2 narcosis, and their initial GCS is at or below 8, but they improve rapidly with noninvasive as their CO2 comes down. And most obviously to anyone who has ever worked a Saturday overnight shift in the ED, there are many short lived toxins that will cause significant depression in GCS, but which are managed entirely with a nasal airway and raising the head of the bed, if anything at all. I thought it was obvious that these patients should never be intubated. However, a few recent conversations have made it clear that this is not obvious to everyone, and seeing as I had to read this paper for a journal club anyway, we might as well discuss it here.

The paper

Freund Y, Viglino D, Cachanado M, Cassard C, Montassier E, Douay B, Guenezan J, Le Borgne P, Yordanov Y, Severin A, Roussel M, Daniel M, Marteau A, Peschanski N, Teissandier D, Macrez R, Morere J, Chouihed T, Roux D, Adnet F, Bloom B, Chauvin A, Simon T. Effect of Noninvasive Airway Management of Comatose Patients With Acute Poisoning: A Randomized Clinical Trial. JAMA. 2023 Dec 19;330(23):2267-2274. doi: 10.1001/jama.2023.24391. PMID: 38019968 NCT04653597

The Methods

This is a multicenter, unblinded, randomized trial from 20 emergency departments and 1 ICU in France. (16 of the emergency departments included EMS enrollment, with physicians on scene with EMS.)

Patients

Adult patients with a clinical suspicion of acute poisoning and a GCS less than 9.

Patients were excluded if they were pregnant, incarcerated, had an immediate need for intubation (defined as respiratory distress, clinical suspicion of any brain injury, seizure, and shock). They were also excluded if there was a suspicion of cardiotropic drug poisoning (β-blockers, calcium-channel inhibitors, or angiotensin-converting enzyme inhibitors), or if there was intoxication with a single toxic substance that could be reversed (opioids and benzodiazepines).

Intervention

Intubation was withheld unless an emergency intubation criterion was met.

Comparison

The decision to intubate was left at the discretion of the treating emergency physician.

Shared procedures

From a clinical intervention standpoint, the trial was considered over after 4 hours, and the physicians could do whatever they wanted at that point. 

There were some standard operating procedures for intubations, including using either etomidate or ketamine, succinylcholine or rocuronium, and maintaining a SpO2 of 100% for 2 minutes prior to intubation. 

Outcome

The primary outcome was a hierarchical composite end point of in-hospital death, length of ICU stay, and length of hospital stay, truncated at 28 days.

The Results

They randomized a total of 237 patients, with some exclusions for consent issues, and so the study population is 225.

The median GCS at enrollment was 6. About 2/3rds of the patients were intoxicated with ethanol. Overall intubation rates were lower in the intervention group (16% vs 58%). 

The composite primary outcome was improved in the intervention compared with the control group, with a win ratio of 1.85 (95% CI, 1.33-2.58; P < .001).

There were no deaths in either group. 

ICU length of stay (0 hours vs 24 hours) and hospital length of stay (22 hours vs 37 hours) were both shorter in the intervention group. 

My thoughts

There are a number of aspects of this study that I find bizarre. Based on social media, some of that might just be explained by wildly divergent patterns of practice in this patient population around the world. 

I have a number of problems with the population of this study, and therefore the generalizability. First of all, 67% of these patients were intoxicated with alcohol. I don’t think I have ever intubated someone for alcohol intoxication in my career. I don’t think I would ever consider intubating for alcohol intoxication. (Remember that trauma is a separate exclusion.) That severely limits the generalizability of these results, because I didn’t think “is it safe to leave drunk patients un-intubated” was really even a question. (A quick survey of decades of police ‘drunk tanks’ would have settled that question.)

Moreover, I think their exclusions are very odd. Respiratory distress is defined as an oxygen saturation less than 90% despite nasal cannula, but they make no mention of positioning or nasal airways, which are usually the only important interventions in intoxicated patients. (This is an airway issue, not an oxygenation issue.) Shock was a systolic less than 90 after a 1 L bolus, but how does plastic in the trachea help shock? Why would that need to be an exclusion here? I am assuming that seizures were excluded because those patients never need to be intubated, but they aren’t clear on that point. Finally, although completely unproven, they make no mention of the one reason I occasionally consider intubation toxicology patients: other interventions, such as charcoal or whole bowel irrigation. 

Even the general exclusion of any patients with an “immediate need for intubation” is somewhat problematic. For safety reasons, I understand why some such exclusion is required, but the “immediate need for intubation” is incredibly subjective, and sort of the entire point of this trial. Did these patients really need to be intubated? Without a much more regimented protocol to ensure that airway maneuvers were attempted first, I don’t think readers can be convinced that any of these patients actually required intubation. (Consider that 67% of these patients definitely would not have been intubated anywhere I have worked.) That is problematic, because excluding patients requiring intubation basically undermines the entire purpose of this trial. If you exclude all (or even most) of the patients who look like they need intubation, aren’t you basically guaranteeing the trial is going to show no benefit from intubation?

The exclusion of patients requiring the intervention happens in many trials. We have seen it in trials of fluids, and many other airway trials. When the intervention in question has no evidence of benefit, allowing for these exclusions just lets the biases of the clinicians shape the trial population in a completely unnecessary way. If your exclusion criteria are going to include “need for the intervention under study”, I think you need an incredibly strict protocol to determine that need. 

It is a minor point, but I found the inclusion of a single ICU in a study with 20 emergency departments very strange. If ICU patients are important, why not include more ICUs? But are undifferentiated patients really making their way to the ICU? Is intubation really an ICU decision for most tox patients? (I guess that is system dependent.) 

Beyond all the patient population issues, the point that utterly ruins this trial for me is that they declared the intervention over at 4 hours. Why? Does that make sense to anyone? Do poisoned patients never deteriorate after 4 hours? Is the airway magically cleared for all toxins by the 4 hour mark? I rarely intubate poisoned patients, but my one concern (and what I was hoping this trial would address) is the safety beyond my shift. Often, patients are left to sleep things off, with less than 1:1 nursing. A couple aspirations at 8 hours would completely change these results, but for some reason they designed the trial specifically so it couldn’t address that question. (They were still collecting data, but you can no longer really blame it on the study intervention, because clinicians could do whatever they wanted at that point.) The 4 hour cut off also probably biases the patient population, if clinicians were aware that they would be allowed to intubate everyone they enrolled in 4 hours anyway. 

Even the primary outcome in this trial doesn’t make much sense to me. Yes, death is an important outcome (and there were none). However, making ICU length of stay your primary outcome basically guarantees the results we saw. Of course ICU use is less if you don’t intubate patients. I didn’t need an RCT to study that question. Using that as a primary outcome biases this trial needlessly from the start.

What we needed to see here were real patient oriented outcomes. What was the overall aspiration risk in both groups? That is an important question, and it could go either way. (We temporarily increase the aspiration risk a lot while intubating, but there is a much longer opportunity to aspirate if we do not.) Hypoxia is listed as 1.8% with restricted intubation and 3.7% with control, but they list these as a subset of “adverse events from intubation”, so maybe this wasn’t all hypoxia? If it was, I want to know the details. A sat of 89% is very different from a sat of 40% and a crash intubation. Those are the real outcomes of interest, and simply aren’t reported. 

Some of the numbers don’t make sense to me either. They say “first pass failure” was 1/113 in the restricted intubation group, but seeing as only 19 patients were intubated in that group, I have no idea what they are talking about. 

There was cross-over between the groups. Only 58% of the intubation group was intubated while 16% of the no-intubation group was intubated. (Those aren’t the actual interventions, but the point is that this isn’t a trial comparing intubation to no intubation.) Therefore, whatever your opinion on the outcomes of this trial, it is clear that clinical judgment is still required based on these numbers. (Although there is nothing in this data that proves that the patients who were intubated needed to be intubated.)

The lack of blinding, although probably inescapable, is also problematic. The outcomes that drive the conclusions (ICU and hospital length of stay) are not objective. In fact, they are highly subjective. As I already said, they are expected outcomes from the choice to intubate. However, they say nothing about whether the decision to admit (or not) to the ICU was a good one. Perhaps we are over-using ICU resources by intubating patients who don’t need it. However, it is equally possible that in the restrictive group, all of these patients should have been admitted to an ICU for close monitoring, and the fact they weren’t was just a bad decision based on the unblinded nature of this trial. 

I normally only bring it up if I spot problems, but I will give this trial credit for the fact that their manuscript is perfectly consistent with not just the final registry on clinicaltrials.gov, but also the very first pre-trial registry. 

Understanding the stats

I don’t usually delve too much into the stats, but this was the first time that I had heard of the Finkelstein-Schoenfeld method, or a “hierarchical composite outcome”, and so I think it is worth a quick explanation. (Redfors 2020) Basically, they rank the outcomes based on importance (death is more important than ICU length of stay), and then pair patients up virtually and compare them. If one patient pair has a winner and loser for the most important outcome (ie, death in this trial) they are removed from the rest of the analysis. If there is a tie for the first analysis, then they compare those patients again for the second outcome, and so on. 

I think this is a clever way to deal with composite outcomes, where the primary concern is that the various components of the composite have different values. There are two main problems though. First, you need to ensure the components of the composite make sense, and I don’t think looking at ICU length of stay in a study of intubation makes any sense. Second, I think this approach may still be confusing when results are presented. What is the benefit of making the outcome a composite if you are just going to compare them separately? I think having ranked primary outcomes could make sense. That would allow you to make more specific claims. “Intubation has no effect on mortality, but does increase ICU length of stay.” However, if you are going to do that, not only do you need to pre-register these outcomes, but you also need to statistically adjust for making multiple comparisons, which is something that they don’t do here. 

Bottom line

This unblinded trial shows that more liberal intubation results in more ICU usage. It does not show any difference in patient oriented outcomes, and has numerous sources of significant bias.

That being said, I think the conclusion is clearly correct, because of course you shouldn’t be intubating drunk patients. It sounds like the practice is different around the world, but these patients would never be intubated anywhere I have worked or trained. 

Other FOAMed

REBEL EM: The NICO Trial: NIV in Comatose Patients with Acute Poisoning

St. Emlyn’s: Intubation for the low GCS tox patient

Evidence based medicine is easy

The EBM bibliography

Evidence based medicine resources

EBM deep dives

References

Freund Y, Viglino D, Cachanado M, Cassard C, Montassier E, Douay B, Guenezan J, Le Borgne P, Yordanov Y, Severin A, Roussel M, Daniel M, Marteau A, Peschanski N, Teissandier D, Macrez R, Morere J, Chouihed T, Roux D, Adnet F, Bloom B, Chauvin A, Simon T. Effect of Noninvasive Airway Management of Comatose Patients With Acute Poisoning: A Randomized Clinical Trial. JAMA. 2023 Dec 19;330(23):2267-2274. doi: 10.1001/jama.2023.24391. PMID: 38019968

Redfors B, Gregson J, Crowley A, McAndrew T, Ben-Yehuda O, Stone GW, Pocock SJ. The win ratio approach for composite endpoints: practical guidance based on previous experience. Eur Heart J. 2020 Dec 7;41(46):4391-4399. doi: 10.1093/eurheartj/ehaa665. PMID: 32901285