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In This Week’s Podcast
For the week ending May 24, 2024, John Mandrola, MD, comments on the following news and features stories: Clues on which pts with subclinical atrial fibrillation (SCAF) to anticoagulate, direct oral anticoagulant (DOAC) antidote, another negative thrombolytic trial in stroke, JAMA sparks change in observational studies, and guidelines challenged in stroke care.
ARTESIA Substudy
The ARTESIA investigators presented a late breaking clinical trial at the Heart Rhythm Society (HRS) meeting looking at the relationship between CHADSVASC score and stroke risk and apixaban effect on stroke and systemic embolism.
Before I tell you about this substudy, let’s briefly review ARTESIA. The main trial randomly assigned patients with implanted cardiac devices who had short-duration AF to either apixaban or aspirin (ASA). The primary endpoint was stroke and systemic embolism.
The average age of the 4000 patients was 77 years and mean CHADSVASC was 3.9. Median duration of AF was short at 1.5 hours. Only 20% of patients had AF longer than 6 hours.
Stroke or systemic embolism occurred in 0.78% (apixaban) vs 1.24% (ASA) per patient-year. This difference of only 31 stroke events in a trial of more than 4000 patients yielded a statistically significant relative risk reduction of 37% (hazard ratio [HR], 0.63; 95% confidence interval [CI], 0.45- 0.88; P = .007).
The safety endpoint of major bleeding occurred in 4.3% patients in the apixaban arm vs 2.3% patients in the ASA arm. This difference of 39 excess major bleeding events yielded a relative risk increase of 80% (HR, 1.80; 95% CI, 1.26-2.57; P = .001).
At the European Heart Rhythm Association meeting in April, ARTESIA investigators presented a provocative subanalysis finding no relationship between duration of SCAF and apixaban effect over ASA. That was weird because you’d expect OAC benefit in longer duration episodes. One problem with sorting out signal in ARTESIA (and NOAH) was the extremely low event rates.
This analysis, which was simultaneously published in the Journal of the American College of Cardiology, assessed the difference in stroke/systemic embolism and major bleeding based on CHADSVASC.
They made three groups with about a third of patients in each. One group had CHADSVASC < 4, one group had CHADSVASC = 4, and the third had CHADSVASC > 4.
For the < 4 group there was no difference in stroke or bleeding in apixaban ban vs ASA (stroke rates both around 0.9% per patient-year).
For the = 4 group the rate of stroke with apixaban vs ASA was 0.54% vs 1.2% per patient-year. But this difference did not meet significance. Same with bleeding — no difference, with 1.2% apixaban vs 0.9% ASA.
For the > 4 CHADSVASC group, the rate of stroke with apixaban was statistically lower than with ASA, basically 1% vs 2.25% per patient-year, HR 0.44 (CI 0.25-0.77). Bleeding was 2.1% vs 1.5% per patient-year but this difference did not reach statistical significance.
The authors converted this to absolute risk reduction (ARR) and wrote: “In this group, over a period of 3.5 years, apixaban prevented four strokes/systemic embolism per 100 patients compared with ASA and caused 1.70 major bleeds.
They calculated an interaction P-value to assess whether these differences between low, moderate to high, or very high CHADSVASCs were statistically significant, and the P-value was 0.06; technically not significant but very close.
The authors were quite strong in their written and spoken conclusions. They believed SCAF in patients with CHADVASC scores > 4 warranted OAC.
They cited the 1.2% ARR in stroke and the lack of significance in the higher rate of bleeding in this group.
They also cited a previously published sub-analysis from ARTESIA in which patients who had a prior stroke also benefited from apixaban vs ASA.
That analysis, which was presented but not yet published, found that the risk of stroke/systemic embolism among ASA-assigned patients with a history of stroke or transient ischemic attack is 3.1% per year; suggesting that OAC should be recommended for these patients even if their CHADSVASC score is ≤ 4
Comments. The conclusion that we should use OAC in patients with SCAF when CHADSVASC is > 4 makes sense. But I worry about the strong conclusions from this subgroup analysis paper.
What if the patient has 1 hour of AF over months? Is that enough? Is that SCAF? SCAF comes in many different varieties.
Remember, trials are powered for their overall results. ARTESIA was positive for stroke reduction, but this very small absolute risk reduction was balanced by a similarly sized increase in bleeding.
So, I consider ARTESIA — especially when combined with similar results of NOAH — inconclusive. Two trials and we still don’t know what to do with these patients with SCAF.
Now, ARTESIA authors want us to be certain about higher risk patients. I agree, somewhat.
But I am not totally convinced. For instance, ARTESIA authors also cite a NOAH sub-analysis based on CHADVASC, but the NOAH subgroup did not find the same heterogenous treatment effect.
The other thing I wonder about is the degree of freedom of this analysis. They split the subgroup into three groups. What happens if we split it into two? Or four? We don’t know.
The event in the main trial was low, about 1.5% per patient-year. When you carve this up into three groups, power goes down and signal to noise goes up.
I still think we have uncertainty. Yes, as CHADSVASC goes up, stroke rates are higher. A benefit of apixaban is more likely. But I don’t think we can apply an algorithm that SCAF with CHADSVASC > 4 always means DOAC.
DOAC Reversal – ANNEXA-1 Trial
I like the story of anticoagulation reversal agents. It’s a good canvass for thinking and testing that which makes sense. You have to move past first-order thinking.
What makes sense is that if you have a patient on a DOAC who has an intracranial bleed — the most serious kind — it makes sense to reverse the anticoagulant.
Brain bleeding that continues can be devastating because of the intracranial pressure, so reverse the AC.
Yet, you can’t just magically reverse systemic anticoagulation without creating a procoagulant situation systemically.
And that is why you need proper trials.
ANNEXA-1 is such a trial. But. But. You have to be careful and read beyond the primary endpoint.
The trial: 263 patients who had intracranial bleeding were randomly assigned to receive the reversal drug andexanet and 267 received usual care. Usual care included prothrombin complex concentrate in about 85% of patients, though there are no randomized clinical trials (RCTs) showing that this is effective.
The authors chose a composite primary endpoint of three things: hemostatic efficacy as defined by expansion of the hematoma by 35% or less; an increase in the National Institutes of Health Stroke Scale (NIHSS; 0 to 42) by less than 7 points; and no receipt of rescue therapy (like surgical drainage).
Hard clinical endpoints were secondary (or safety) endpoints, and as you will see, the story of this trial resides there.
Results:
For the chosen surrogate endpoints, andexanet worked. The overall hemostatic efficacy was superior in the andexanet group (67% vs 53%).
The absolute risk increase (better rate of the primary endpoint) was 13 percentage points, and the P-value was 0.003.
The composite was driven mostly by better outcomes in the hematoma expansion arm. More in the andexanet group had less than 35% expansion (77% vs 65%).
For the other two components (NIHSS and no receipt of rescue), the rates were fairly similar in both arms.
Safety (or secondary endpoints): There were more thrombotic events in the andexanet arm vs usual care. It was 10.3% vs 5.6%. That’s nearly 2-fold more.
Ischemic stroke occurred in 6.5% receiving andexanet vs 1.5% receiving usual care (difference, 5.0 percentage points; 95% CI, 1.5 to 8.8). Myocardial infarction (MI) occurred in 4.2% vs 1.5%. There were no significant differences in overall death.
Similar numbers of patients in both arms (28% vs 31%) had acceptable neurologic functioning at one month.
Comments. This is a definitively negative trial. While there was a positive primary endpoint — less hematoma expansion — clinical endpoints looked far worse.
For every 100 patients treated, there were five more thrombotic events, including five more ischemic strokes and three more MIs.
And, at a month, there was no difference in death nor the number of patients who had achieved acceptable neurologic function.
What’s more, the projected cost of andexanet is $22,000 per dose.
In sum, I love this trial because it shows that even though a drug can have a favorable effect on one thing, or one surrogate marker (like, say premature ventricular contractions after an MI), it takes a lot more to make a person function better or live longer.
TEMPO-2 Trial – Thrombolytic Therapy in Acute Stroke
Speaking of complexity of drugs beyond their designated jobs, we should talk about another negative thrombolytic trial in acute ischemic stroke.
This was the TEMPO-2 trial of tenecteplase vs placebo in patients with mild stroke and intracranial occlusion or focal perfusion defect. Tenecteplase is similar to alteplase, but it has a longer half-life, it is more fibrin-specific, and results in less systemic depletion of circulating fibrinogen than alteplase.
The idea for patients with mild stroke is, as the authors write, that these patients are at “high risk for early neurological deterioration, which most often occurs within the first 24 h after presentation. What’s more, this subpopulation were excluded from most of the trials and are often not given lytic therapy.”
The average NIHSS score was only 2, so, quite mild stroke.
Nearly 900 patients were randomized.
The primary outcome of return to baseline functioning on pre-stroke modified Rankin scale at 90 days occurred in 75% of patients in the control arm and 72% in the tenecteplase group.
The risk ratio was 0.96 and the CI went from 0.88 to 1.04; P=0.29
The trial was stopped early for futility. So, it seems like it was a wash. In addition, tenecteplase recanalized arteries. For patients with large vessel occlusion, recanalization rates were 48% in the tenecteplase group and 13% (P=0.0005) for the control group.
But it really wasn’t a wash. Death occurred in 5% in the tenecteplase arm vs vs 1% of controls. That’s a HR of nearly 4 times.
Symptomatic intracranial hemorrhage (ICH) occurred in eight vs two patients in the tenecteplase vs control arm.
Seven deaths (one in the control group and six in the tenecteplase group) were related to a symptomatic ICH.
The authors write that the theory was that the presence of an intracranial occlusion would define a “minor stroke” population that would have worse outcomes and a benefit from reperfusion therapy.
But it did not work out. Not at all.
A note on the rate ratio and CI of the primary outcome. You don’t see these tight intervals that often. The rate ratio was 0.96 and CI went from 0.88 to 1.04. I never know what the stats professors will say is the threshold for saying a therapy doesn’t work, but there seems to be tight CIs.
But added to that was the higher death rate, in large part becaiuse of the higher rates of ICH, and I think we can say that lytic therapy ought to be avoided in patients with minor stroke symptoms.
And this was despite the fact that the drug did what it was supposed to do — it recanalized the artery, 4 times more often than control.
I realize that most listeners are not stroke neurologists, but I believe this is a notable study for its clear harm > benefit signal.
I also steadfastly remain doubtful about the entire lytic frame for acute stroke. I will link to my old essay on this topic.
I would love to see the original National Institute of Neurological Disorders and Stroke trial repeated. That trial had clear differences in baseline characteristics, which may have driven the positive results.
Observational Research
As I have spoken about so often on this podcast, the best way to understand causation is with RCTs.
Treatment A vs Treatment B are presumed to have equipoise. Experts disagree on which one is better.
Knowledge is gained by letting randomization choose and then looking forward to the results of a given endpoint.
If you let clinicians choose one or the other treatments, and then look back at results, you can be fooled because clinicians use lots of factors to decide treatment. Some of these factors are easily controlled for because they show up on a datasheet — things like age, blood pressure (BP), diabetes, smoking, etc. But many factors —the patient’s demeanor, their home situation, etc, play into these treatment decisions and these factors cannot be controlled for because they don’t show up on a datasheet.
And that’s one of the main problems with non-random comparisons, namely, unknown variables that drive results instead of the treatment or exposure.
Randomization is beautiful because it balances both known and unknown variables.
This is a long intro into a new, and quite provocative policy change at the Journal of the American Medical Association (JAMA).
Earlier this month, the editors of JAMA wrote a special communication in which they have changed their approach to observational research.
Like many journals, JAMA had strictly forbidden causal language in the reporting of observational studies. Descriptive verbs such as “associate with” were the ones that were favored.
Now, though, they will allow the truth to come out. When authors look back, or observe the effects of two non-random treatments they will be allowed to say what they are doing: and that is… to determine cause, not just correlation.
JAMA editors will ask authors to address six core questions of observational studies:
What is the causal question?
What quantity would, if known, answer the causal question?
What is the study design? (For example, in cohort studies comparing different treatment strategies, the choice of the start of follow-up (time zero) and the alignment of that time with the time at which eligibility is determined can affect the validity of the analyses).
What causal assumptions are being made;
How can the observed data be used to answer the causal question in principle and in practice?
Is a causal interpretation of the analyses tenable?
Ultimately the editors write that there will be two main elements of an observational study:
[First, investigators must be] explicit about the “if-then” (conditional) structure needed for their interpretation (eg, if certain assumptions hold, then a causal interpretation of the findings is tenable); and second, acknowledging that careful context-informed judgments are necessary to evaluate whether assumptions are plausible, and a causal interpretation is tenable.
The editors then write:
The framework does not imply that all, or even most, observational studies merit a causal interpretation. For some observational studies that start with causal goals, causal inference may prove impossible; in these cases, estimates retain only associational interpretations.
I’ve discussed this with academic colleagues, and many think it is a bad idea. They worry that it will lead to even more biased conclusions and potentially faulty conclusions.
These colleagues tell me how easy it is to do low-quality data-base type research.
But.
I may be totally wrong, but I think this is a decent idea. I am less pessimistic.
Here is my thinking.
While some observational research is designed to describe things, such as trends over time, prognosis, procedural complications, much if not most of it is comparative.
Nearly every non-random observational comparison study is actually doing causal research.
Authors tally effect sizes; they adjust; they do their best to sort out biases and simulate randomization, all in an effort to sort out causation, not just correlation.
But then when they find different effect sizes or harms, journals make them hide their true effort with language. They force the authors to write that it’s an association.
Yet everyone knows what the authors mean. And what their goals are. The goals are not to report associations. The goal is to say something about causation.
JAMA will now allow such language. But in doing so — I hope — they will also force more rigor into the methods of why and how this study shows causation.
I like this, because, in the past, every observational study was considered the same. Lines like…”this is not randomized, so we cannot exclude residual confounding.” That line doesn’t help, because it is a given. And it basically makes everyone happy. Those who want to find causation feel like the line relieves them. We said it, now look at our findings. To those who see no possibility of causal inference, people like me for instance, we can say, see they write that residual confounding is likely.
Now, maybe with this new policy change, we can read why the authors think their findings are more than mere correlations. It’s also possible the entire observational research enterprise gets a boost.
We shall see.
Active and Aggressive BP Control in Stroke
Speaking of decent observational research that may sort out a causal question, and challenge guidelines, let me enter the acute ischemic stroke space again.
Some patients with acute stroke have very high BP. Guidelines recommend IV drugs to reduce BP so that patients can get lytic therapy, because lytic therapy is contra-indicated in patients with high BPs.
It turns out that there is little data for this strategy of aggressive BP lowering. In fact, there are potential harms in the setting of stroke.
Dutch authors had the idea to test this question but used a quasi-randomized observational design.
The TRUTH study used a cluster design wherein 37 Dutch centers either adhered strictly to the active BP control strategy or did not.
Patients had BPs above 185/110 and were otherwise eligible for lytic therapy.
The primary outcome was functional status at 3 months.
Over about 7 years they recruited 850 patients from 27 centers that followed the active BP treatment arm.
The control arm had only 200 patients from 10 centers that followed a non-lowering strategy.In the active BP control arm, (94%) received thrombolytic therapy with a door to needle time of 35 min.
In the control arm, only 52% received thrombolytic therapy with a door to needle time of 47 minutes.
And the results:
The adjusted odds ratio (aOR) for a shift towards a worse 90-day functional outcome was 1.27 (95% CI 0·96 to 1·68) for active blood-pressure reduction compared with no active blood-pressure reduction.
So, no statistical difference and a strong trend toward worse in the active BP control arm.
ICH occurred in 5% vs 3% of the two groups. Obviously that was not statistically different.
The authors concluded that “Insufficient evidence was available to establish a difference between an active blood-pressure-lowering strategy — in which antihypertensive agents were administered to reduce blood pressure below 185/110 mm Hg — and a non-lowering strategy for the functional outcomes of patients with ischemic stroke, despite higher intravenous thrombolysis rates and shorter door-to-needle times among those in the active blood-pressure-lowering group.
“Randomized controlled trials are needed to inform the use of an active blood-pressure-lowering strategy.”
Comments. See, observational studies can be done to give signals of benefit or harm.
This is a strong design. The authors make excellent conclusions. In the end, they say there is still insufficient evidence to warrant aggressive BP control in acute stroke. (There was insufficient evidence before and now there is still no signal of benefit after this observational study). They call for RCTs.
And they note in the methods section that RCTs have not been done because doctors have not been willing to consider not aggressively controlling BP and/or giving less thrombolytic therapy. I love that this observational study was done to bust up the lack of equipoise and prove the necessity of an RCT.
The paper is in Lancet Neurology and Medscape has a nice news story on it.
Take a look.
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Cite this: May 24, 2024 This Week in Cardiology Podcast - Medscape - May 24, 2024.
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