Friday, January 27, 2017
This is a post to share my thoughts about the randomized, controlled trial of haloperidol, risperidone, or placebo for delirium in 'palliative care' patients, published recently in JAMA Internal Medicine.
Big hat tip to my fellows - Drs Amanda Hinrichs, Elena Wahmhoff, and Alison Feldman, whose discussion of the paper at a recent fellows' rounds helped me think through the study, as well as the AAHPM Connect communities bulletin board's discussions (BTW, have really appreciated these bulletin boards the last couple years and am grateful to AAHPM for pulling it off so well!). Geripal, as per usual, has a great post about the paper too.
The study has been discussed a lot the last couple weeks, and with some alarm (let's face it, us HPM folks tend to use antipsychotics a lot, and tend to have a positive view of them - 'see' the good they can do in many of our patients). Its headline findings are that haloperidol and risperidone (H/R from now on) worsened delirium in 'palliative care patients,' and were associated with higher mortality, compared to placebo.
First I'll review the paper, and share my thoughts about it. As always, more questions than answers. Warning, this will be very journal clubby (meaning it's going to as much be about interpreting research in general as it is about the paper itself). But then it veers into dangerous speculation, so it has that going for it.
The TL;DR is that I think this is a really well-done investigation, despite some gripes I have with how it's presented. I think the headline findings that low-dose H/R worsens delirium is valid. The mortality findings are also concerning, but don't prove causality, although one notes these data join multiple other studies showing an association between antipsychotics and death in delirium. And I don't know what we should do, apart from stopping using H/R in the manner they are used it in this trial.
Summary of the Paper
This was a multi-site (all Australian), double-blind (most importantly, the people doing the delirium assessments and clinicians caring for the patients were blinded to allocation, as were most others), randomized, intention-to-treat, placebo-controlled trial of dose-titrated haloperidol, risperidone, or placebo for the symptoms of delirium. All patients had 'advanced, progressive disease that was no longer curable who required inpatient care by a specialist palliative care team,' and had delirium diagnosed and measured by various scales. Patients with a clinician-anticipated survival of 7 days or fewer were excluded. The NuDESC scale was used in the primary outcome - it's a nursing delirium assessment tool (link to a pdf of it here). The study was registered, including all the secondary outcomes they reported.
Patients received low doses of the drugs, 0.5 mg of the active drug (or matching placebo) x1, then q12h prn. Doses could be increased by 0.25 mg on day 1 and 0.5 mg thereafter to a maxium of 4 mg daily. Patients over 65 years had half those doses. Subcutaneous midazolam, 2.5 mg q2h prn, was available as rescue, and use of rescue midazolam was an important secondary outcome (I believe there's no injectable lorazepam in much of the world outside of the US, and you often see midazolam used in situations where most in the US would use lorazepam). (I know you all hate lorezapam, and would never use it for delirium, but you know what I mean.)
The main study period was 72 hours, and the primary outcome was the NuDESC score on day 3. Importantly, NuDESC is one of those innumerable scales for which we don't have any clear 'minimum clinically significant difference.' They used items 2-4 of the NuDESC (each item is a 0-2 scale measuring presence & severity of illusions/hallucinations, 'inappropriate behavior,' and 'inappropriate communication.'). Essentially they were using a 6 point modified NuDESC score as their primary outcome. Because no one really knows what is clinically relevant on the NuDESC (ie, does a difference of 1 point mean anything clinically meaningful or not?), the investigators did some consensus work, and concluded that 1 point was clinically meaningful. While this isn't how we wished the world work, it's a reasonable thing to do, certainly so much better than not even bothering to think of what a clinically meaningful difference could be, and something David Currow (the senior author) has done in prior studies (eg the sham O2 for dyspnea study). On its face, looking at the NuDESC items 2-4, a one point difference seems reasonable to me, ie, I'd agree that the patient's condition was improved meaningfully. They used all this for their power calulations, and they recruited more than enough patients per their power estimates.
They randomized 249 patients - about 80 for each of the 3 arms. ~35% female, mean age ~75, ~90% had cancer, mean delirium score ~2.5 (out of 6 on their modified NuDESC), median KPS 40-50.
Despite the headline findings that delirium was worse in the H/R groups, their actual primary outcome, strictly interpreted, was that there was no clinically meaningful difference in delirium between the H/R groups and placebo. Patients receiving H/R had Patients receiving H/R had less than 0.5 points difference (for the worse) on the modified NuDESC score compared to placebo. Remember, this is a difference that, we are told, is not clinically meaningful. These differences however met statistical significance (p<0.002)
Admittedly Petty Gripe #1
This is my gripe #1 with the study (I only have 2) - they do all these things right, then basically fail to meet their primary outcome (stated unartfully, that there would be a 1 point or greater difference on their modified NuDESC), and instead report a statistically significant but apparently clinically meaningless finding as their main outcome. For instance, in the abstract, they say delirium scores were significantly higher in the H/R groups than placebo; they do not clarify that strictly speaking delirium was statistically worse but not clinically worse in the H/R group, as measured by their primary outcome measurement.
I should note that I'm being perhaps a petty, moralistic stickler here, because I do think their study actually did show that H/R actually clinically did worsen delirium, however it was not via their primary outcome measurements (it was via their secondary outcomes which are perfectly valid and fine and pre-specified - see below). Why I'm being a petty stickler is that I thought The Entire Universe had agreed that presenting statistically significant findings without qualification of their clinical relevance was Bull Shit, and we should all collectively stop doing it, and it disappoints me how they presented this.
That is, if all we had were the primary outcome results, if the paper stopped right here, all of us would be, like, *shrug*.
Back to the Paper Itself
But the study didn't end there, and here's where things get interesting. They measured delirium a different way (the Memorial Delirium Assessment Scalegoogle photos), and it was statistically worse in the risperidone group (not placebo), by like 1 point, and again we have no idea how to interpret the clinical relevance of that, so it probably is best to ignore it (I am).
But rates of midazolam rescue were also measured. 13-17% of the placebo patients needed midazolam rescue per day, vs 30-35% of the H/R patients (P values here <0.02; the number-needed-to-harm here is 6-7). It's a weird thing, I'm reading the paper for the first time, shaking my head, trying to understand what any of it means and wondering why I care, then I get to final paragraph of the results section, which presents this midazolam data, and I was like, 'Whoa, the H/R patients really did do worse.' They were so much more agitated as a group that the clinicians caring for them used a benzo at double the rate of the placebo patients. That, my friends, seems like a clinically meaningful difference that I can wrap my head around.
I want to pause here and mention the tremendous frustration it is a palliative clinician to try to interpret research findings that are based on indices/scales. I'm not suggesting there's any 'solution' to this, but it's something I think we all need to keep at the back of our minds as we interpret our research. Sometimes, you just gotta vent.
Because much of our research is based on scales and indices, it's often tough to understand what it means, and how much we should care. Eg, quality of life scales, symptom scales, etc etc. In contrast, survival and mortality; the NNT to prevent a stroke; months to dialysis; rates of hospitalization, length of stay on hospice - all these are straight-forward outcomes, and most of us can at least get some gut-calibration to what they mean without any further context. But what exactly does the statistically significant difference in QOL on the FACT-L scale of 6.5 points mean in the famous Temel lung cancer study? I honestly don't know - it's probably clinically meaningful, but I don't have any good way to judge that in contrast to an outcome like, eg, the percent of patients who met clinical criteria for depression. Notably, we should be as perplexed and skeptical of index-based outcomes that we like (Temel!) as we are of ones that upset us (This Study!).
Importantly, this is not a complaint that these studies are poorly designed or executed (the Temel study wasn't - it was really well done; nor is this study - I *wish* most clinical research was done as well as the H/R study!). Instead, it's more the epistemological conundrum we simple-minded clinicians face trying to interpret these investigations: should we care?
Which is why I'm grateful when there is a non-index based, clinically-relevant outcome included in this study, that my poor brain can understand - eg, the midazolam use. Which is why I think the fundamental conclusion of this study that H/R (as used/dosed in the trial) worsened delirium symptoms is legit: it was worse on the impenetrable indices but also the clinicans caring for these patients resorted to midazolam at double the rate. Important finding, and one I am grateful for.
As a final note on this point, I'll observe that there are some indices that have been around long-enough and have sufficient research base underlying them that we have a strong sense of what is clinically meaningful - as one example in our palliative world the ESAS folks have done a lot of work on this - but as a whole a lot of these indices remain very opaque.
Back to the Paper, and the Spectre of Death
However, there is also a non-index based, clinically-relevant outcome of the study that my poor brain had trouble understanding: the mortality findings. This is my other minor gripe with the study - it took me several re-reads and Encyclopedia Brown-level deduction skills to ferret-out what the mortality data actually represents. (I believe them, it's just that they're confusing.)
34 patients died during the study period. Each group had about 80 people in it: 9 in the placebo group, 9 in the H group, and 16 in the R group died. It's not initially obvious they mean in the 3 day active study period or the 12 month follow up observation period that's mentioned in the clinical trial registry (the registry says they will look at mortality over 12 months). Putting two-and-two together, I think these 34 patients died during the 3 day active study period. They present a Kaplan Meier survival curve which shows most patients died within a couple months, so these 34 have to represent those who died just in the 3 days of active intervention.
However, also confusingly, they report R patients were 29% more likely to die than placebo patients (this is a hazard ratio), and H patients were 73% more likely to die than placebo. Median survival for all placebo group patients was 26 days vs 17/16 days for the R/H arms, respectively.
Given the N were essentially the same (about 80 patients per arm) how is it that 16 died in the R group; 9 died in the H group; 9 in the placebo, but yet they report R patients were 29% more likely to die vs placebo, H group 73% more likely to die than placebo. This does not make sense to me, how that could add up, and how the paper is written it's just bewildering. The more I looked at it, the more apparent it became that the 9-9-16 data were for days 1-3, the other data (hazard ratios) were for the entire observation period which they said would go out to 12 months, although the KM curve gives data out to 1500 days, but whatever. This is the sort of stuff the editors & peer reviewers should have made sure was a little clearer.
Despite the confusion in how the data are presented, the median survival data are pretty clear, and I accept that the H/R patients died faster than the placebo ones, any way you look at it.
Phew, So Much For Summarizing The Paper, But What Does It Mean?
1) This is really important, well-done research, and I read it and think to myself 'Gosh I wish we had research this well designed and executed for all our clinical questions.' We need more of this. Easy for me to say, I know, I'm not an investigator, but goddamit I'd take a study like this anyday over a retrospective look at anything.
2) Fundamentally, I think their basic conclusions are sound, and well supported by their data: R/H - used how they used it - worsened delirium, it's fair to say modestly, and was associated with a higher rate of death. I don't see any way around accepting this; we should all accept this. (I want to be wrong, and please leave in the comments why you think I am.) Remember that this data is emerging in the context of a lot of research the last 15 years (in other contexts) suggesting a link between antipsychotic exposure and death. Clinical impressions and time-honored beliefs aside, we have just about zero high quality, well-designed research supporting our use of antipsychotics for delirium, especially in patients in the final months of life. In fact, it's totally amazing to me they could show an increased rate of mortality in the H/R patients, because it was so high in the entire cohort. These were sick, sick people most of whom died very quickly; showing more/faster death in the midst of that is pretty impressive, and honestly very damning of H/R in this context, if one accepts that longevity is a defacto 'good' outcome (see below).
3) Did the H/R accelerate the patients' deaths? Maybe - probably - however they also as a group had double the rate of midazolam exposure, right, so it could have been the midazolam in part, or 'just' the 'worse delirium' (presumably some complex effect of the more severe delirium).
4) The generalizability of this remains an open question.
A) The Aussies do some good palliative research, but there's always this sorta question mark for us State-side as to who these patients are. We clearly see patients like this, but because we don't have a palliative unit infrastructure/model of care like they have in Australia, it's not totally clear whom amongst our patients this applies to.
B) I've seen some comments on this about how 'Phew this doesn't apply to terminal delirium because they excluded people expected to die within 7 days.' I'm not so convinced of that. Over 10% of patients died just in the 3 days of the active study alone. Most patients died within the month. Also, 'terminal delirium' is not an actual, real, diagnosis/distinct physiologic phenomenon. It's just a clinical short-hand for a patient who is delirious for whom we judge the underlying cause of the delirium is unfixable (because the cause of the delirium is the same as the cause of their imminent death) or unfixable in the time they have left to live. Ie, I'm not so sure one can easily draw a clear line between delirium in cancer patients with less than a month to live and 'terminal delirium.'
C) However I think the real generalizabilty question here is about the dose of H/R, and whether we can apply this to antipsychotics in general (eg olanzapine, quetiapine, chlorpromazine). Strictly speaking we cannot apply it to other antipsychotics, and so we shouldn't. I think we should all be prepared and ready in our heart of hearts to accept this is a class-effect, while remaining strictly agnostic about that. The dose question though is a big one. These were small doses of H/R (less than 1 mg for patients over 65, less than 2 mg for others on average). They are doses I use sometimes, but still pretty darn small, and honestly my practice in that situation would be to give the patient more of the antipsychotic (all things being equal) than a benzo. Instead here they did tiny little dose increases plus gave benzos. I don't begrudge them that study design, but leaves me pondering the generalizability.
D) In that spirit, I do think we can maintain equipoise about whether higher doses of H/R are more effective for reducing the symptoms of delirium than placebo - this remains untested. It seems entirely improbable though that higher doses wouldn't also have the same (if not more) risk of death, even if more effective for reducing delirium symptoms.
In summary, think we should stop using these meds, routinely, at these doses, for delirium, in our late-stage patients.
We Should Focus More on the Lack of Efficacy, Than the Mortality Findings
What if the study showed that H/R were really effective to reduce the signs of delirium, but that also they doubled the 30 day mortality? Would that be ok? The answer is that of course it would be ok, some of the time (eg, for informed patients in which that would be compatible with care goals/values). For most of our patients with end-stage illness, in their final 1-2 months, life prolongation alone is not the primary goal. Sometimes it's not a goal at all, although I'd hazard that most of my patients are perfectly happy with whatever time they can get, if it's 'good time' (symptoms well controlled, meaningful interactions with loved ones).
Typically, patients who are accepting that time is short, symptom control and loving interactions are the top goal and they would not sacrifice that just for more time, right? Given that, if someone had significant, distressing delirium, it can be totally fine to give them something to reduce the distress, even if they live a week or two less. They or their decision makers should be informed of the risk of hastened death, and decisions should be made together whether that's acceptable. This scenario is of course the textbook scenario for the 'principle of double effect' (eg, 'morphine is ok at the end of life to relieve suffering even if it hastens things' - I know most of you hate that example because it stigmatizes opioids at EOL and probably isn't all that applicable anyway - I don't like the example - but you know what I mean and it's in all the textbooks).
I bring this up because I think it's important in HPM hat we are really careful and thoughtful with how we react to mortality outcomes of palliative-ish interventions (both when they seem great like the Temel trial) and "bad" like this one. Right? Because we all kinda exist because of the idea that some of the time, longevity is not what's most important in life and in medicine, and that's ok.
One day I'll put on my grumpy socks again, and write about what I think is the scandalous misapplication of scant data to promote the idea that 'hospice and palliative care' prolong life (honestly guys, the data ain't there). We should all be satisfied with reducing suffering and improving quality of life, friends, it's what we do and we do it well.
It barely matters of course here, because H/R didn't even help the delirium, so there you go.
And Now For What We Should Do, Although Honestly I Don't Really Know, and the Reckless Speculation
Part of the discussion I've seen has been along the lines of "Well what do we do now?" Great question, and one that I of course have no real answer to.
In general, outside of our late-stage patients, until there's a demonstrated safe and effective drug, obviously most of the effort should continue to be on prevention and behavioral and environmental interventions. With drugs only being used rarely, and judiciously, for safety (basically as a chemical restraint) reasons. Maybe ramelteon will pan out (probably not, but that would be nice).
That's all nice and good, but doesn't really apply to our late-stage patients: they will get delirious, we can't prevent it (ok we could probably prevent some of it by stopping opioids, but that would mean many more people dying in agony) and they sometimes don't have time for us to treat/remove the underlying cause. We have to do something, right? Of course, but perhaps, until we have drug interventions which are proven effective, and safe, maybe that something is behavioral, environmental, and social (calm environment, presence of familiar loved nes, quiet nights, bright days, etc), alongside a hefty dose of family education and support on how to keep the patient safe, and how to assess the patient for distress in the midst of the delirium, what to be more worried about, etc. And reserve drug-therapy for cases to keep the patient physically safe, or for patients who are really agitated and distressed despite environmental, behavioral, social interventions (I keep thinking of patients I've had with pathologic fractures who are agitated, forgetful and keep on trying to sit up and get out of bed every 5 minutes, each time causing themselves agonizing pain - I've met many of these patients and boy it's a tough, tough situation). What that 'cut off' is when the agitation is 'distressing enough for drugs' - I don't know.
Which brings us back to benzos, and a spot of speculation I've had about them for delirium. I think the problem with them is that they've been used at too-low a dose, and with the wrong goal in mind. Absolutely I accept that benzos can and often do worsen delirium. They are a terrible 'treatment for' delirium. However, at the right dose, they are great sedatives, right? That's what they do.
I think the problem is that people have used them at lower, anxiolytic doses (eg, 0.5, 1 mg lorazepam) to try to 'calm down' agitated and restless patients and instead end up just disinhibiting them, worsening the agitation. However, give someone enough (usually over 2 mg at a time, sometimes more), with the specific goal of sedating them (not 'improving the delirium'), and benzodiazepines are perfectly effective (at sedating someone). Ie, part of this is being really clear about what the actual goals of therapy are. While we'd all like to take away our patients' delirium lickety split, sometimes for safety, or because they are imminently dying and are really distressed and agitated and confused, simply sedating them is the right thing to do. Not often, but sometimes.
Again, this is mere speculation based on personal clinical experience on my part, and I'm curious as to others' thoughts about it - low vs high dose benzodiazepines and the goal of deliberately sedating people.
But the point of this is that the H/R paper makes me wonder whether antipsychotics are a similar case, and their routine use at low doses for delirium should be ended.
Drew Rosielle, MD is a palliative care physician at University of Minnesota Health in Minnesota. He founded Pallimed in 2005. For more Pallimed posts by Drew click here.