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In This Week’s Podcast
For the week ending February 28, 2025, John Mandrola, MD, comments on the following topics: The debate over operating on asymptomatic patients with aortic stenosis, the move to composite endpoints in trials, instantaneous wave-free ratio (IFR) vs fractional flow reserve (FFR), and high-frequency low-tidal volume ventilation for AF ablation.
Aortic valve intervention for asymptomatic AS
Podcast EARLY TAVR Nov 8, 2024 – This Week in Cardiology Podcast
JAMA Cardiology published a widely circulated editorial this week from three leaders in the field of aortic stenosis therapy. Second author was Eugene Braunwald himself.
The title was “Aortic Valve Replacement for Asymptomatic Severe Aortic Stenosis—The Time Has Come”
From that you can gather that they are advocating for treating patients with asymptomatic aortic stenosis (AS). This would be a big change because for my entire career, we recommended aortic valve replacement (AVR) when patients with severe AS became symptomatic. The triad of symptoms of AS include angina, fainting, and heart failure symptoms like dyspnea on exertion.
The three key opinion leaders’ (KOL) argument cited three RCTs comparing either surgical AVR or transcatheter aortic valve replacement (TAVR) or either vs clinical surveillance.
Before I tell you why I disagree with their opinion on changing practice patterns, I want to set out how big of a deal this is, and how it will lead to a serious expansion of the number of TAVR procedures.
I found a paper on trends in AV interventions and there has been a massive shift from surgical aortic valve replacement (SAVR) to TAVR, especially in patients between ages 65 to 80. For instance, in this age group in the last year of the study, 2022, 14% of aortic valve interventions were SAVR and 86% were TAVR.
Now, if we shift to asymptomatic patients, there will be even more patients having TAVR. Notable, were that two of three KOL authors declared relationships with makers of TAVR valves.
One more thing, before I get into the critical appraisal of the three trials, is the difficulty in measuring AS.
My friend and former partner and echo expert Anthony Pearson emailed me about this challenge. He wrote:
Aortic valve area should be the measurement utilized to determine severity of AS. Gradients are too dependent on flow.
It has only been in the last 15 years or so that the arbitrary definition of severe AS increased from 0.75 cm2 to 1.0 cm2.
Using 0.75 cm2 as my criteria for AS, I have had no asymptomatic patients die prior to AVR.
With < 1.0 cm2 as the cutoff, a very large number of AS cases fall barely into the severe range. And, this is a measurement that requires meticulous attention to optimizing recording.
I have remeasured hundreds of such cases resulting in “moderate” AS and saving the patients from unnecessary premature AVR
Echo reading, Dr. Pearson concludes, requires meticulous attention to detail as well as a neutral mindset.
I concur with this. People have this impression that echo reading is like interpreting a lab value. It is not. It is a lot more subjective than people think.
Let’s do the critical appraisal. I covered the EARLY TAVR trial on the Nov. 8 TWIC podcast.
The trial compared clinical surveillance to early TAVR in 900 patients with asymptomatic AS. My main issue came in the choice of the primary endpoint, which was a composite of death, stroke, or “unplanned hospitalization for cardiac causes.”
The topline results reported a statistically significant 50% reduction in the primary endpoint with the early TAVR group. The sole driver of the primary endpoint was unplanned hospitalization, mostly for symptoms of AS. Death and stroke were not different.
The fatal flaw of this trial was that it was unblinded trial so patients in the surveillance arm knew that they had severe AS but were not treated, whereas the other group got “fixed.” It’s a classic problem with a phenomenon called faith healing and subtraction anxiety. I put very low weight on EARLY TAVR.
The key opinion leaders also cited two other trials in support of their call for early intervention.
The second trial was called the EVOLVED trial of 224 patients with asymptomatic AS and evidence of late gadolinium enhancement (LGE) in the left ventricle. This was a UK/Australian trial that compared clinical surveillance to early aortic valve intervention with either TAVR (25%) or SAVR (75%).
A primary outcome event of death or unplanned AS-related hospital admission occurred in 18% of the early group vs 23% of the clinical surveillance arm. That 21% relative risk reduction did not meet statistical significance. (HR 0.79, 95% CI, 0.44-1.43). Death rates were similar.
I did not misspeak. EVOLVED was a non-significant trial. The KOLs, however, called it underpowered and blamed the fact that the diagnosis to intervention time in the active arm was as long as 5 months.
The third trial cited in the opinion piece was called AVATAR, and it was a small trial of 157 asymptomatic patients randomized 1-1 to surgical AVR or CS.
AVATAR delivered positive results with a 54% relative risk reduction in death, MI, stroke or unplanned hospitalization for HF. While all-cause death was significantly lower in the SAVR arm, curiously cardiac death was the same.
AVATAR authors were cautious in their conclusions saying this was preliminary evidence for early surgery.
Comments
So, in sum, the key opinion leaders urged more aggression in operating on patients who complain of nothing but have abnormal shadows on ultrasound.
One trial is flawed because it is unblinded and driven by the bias-prone endpoint of unplanned hospitalization; another trial is non-significant for its primary endpoint, and a third is small and considered preliminary.
I don’t agree with them, and from my perch here in private practice, I see a great potential for overtreatment, especially using TAVR.
To those who I have not persuaded and think we should operate on asymptomatic patients, I will concede that there is a gray area worth considering in this area.
That is, a “seemingly” asymptomatic patient who has such slowly progressive AS, that he or she have adjusted their lifestyle to limit exertion so as avoid dyspnea or dizziness from low cardiac flow through the valve. These patients may be billed as asymptomatic, but they are not. Here, a careful history—and possible a low-level exercise test—may help tease out symptoms.
That said, patients who report normal functional capacity, and patients who report being happy, and all they have is an abnormal ultrasound, I think can be followed, or, as it is in this trial called, clinically surveilled.
Trial Endpoints
When I lecture on evidence-based medicine, one of the most common questions I get pertains to endpoints—that is, in the days of old, trials measured alive or dead. There was no adjudication, no bias, and the only decision a reader had to make was whether the difference in death was a) clinically significant, and b) due to the treatment effect and not statistical noise.
Newer trials, however, have become much harder to interpret because trialists have added composite endpoints of many different surrogate outcomes. Things like death due to cardiac causes, MI, stroke, angina, HHF, and urgent revascularization.
JAMA-IM has published a study from a group at Columbia University looking at outcomes of major trials in atherosclerotic disease. This was a descriptive study where they focused on the heterogeneity of original endpoints of trials.
Like many of these studies of studies, they selected trials from major journals—NEJM, Lancet, JAMA, EHJ, Circulation, and JACC—from the years 2019-2023, which is great because these are recent trials.
They looked only at the primary analyses of RCTs.
The analysis included 50 RCTs. Nearly all (49 of 50) used composite endpoints.
The most common composite endpoint was the 3-point major adverse cardiovascular events (MACE) of MI, stroke and CV death. But it was hardly a majority. Only 14 of 50 trials or 28% used this MACE endpoint.
The remaining 36 or 72% of trials included, and sit down for this, because it is the key finding—29 different endpoint combinations. That is crazy.
But perhaps even crazier was that the published and original primary endpoints were different in half the trials. In a third of trials, components of the original primary endpoint were edited after enrollment of patients. But not all of the trials reported these changes.
The most common rationale for changing endpoints was adding power—in other words, to accrue more events.
In 8 of 50 trials, or 16%, the initial clinicaltrials.gov entry reported an undefined original endpoint, for example, “cardiovascular disease or simply “MACE.”
The authors concluded that there is a bunch of heterogeneity of endpoints in recent atherosclerotic cardiovascular disease (ASCVD) RCTs.
This, they write, “may complicate” comparing results of different studies of interventions. I’d say.
They add, rightly I think, that modifying endpoints between the study initiation and publication compromise a trial’s scientific validity. Obviously, this is also true.
And, finally, they suggest that “regulators and journal editors should require that ASCVD RCTs use uniform end points (eg, 3-point MACE)
I could not agree more. The main teaching point from this well-thought-out investigation is that it chronicles sort of what we know: that composite endpoints vary a lot and can even change over the course of the trial.
The reason for this variability is partly a result of our field’s success. Take heart failure (HF) for instance. It’s going to be really hard to extend life any further than already has been achieved with the four classes of guideline-directed medical therapy (GDMT). Same with stable coronary artery disease (CAD) and a lot of cardiac conditions.
So, what do trialists do? They add more surrogate endpoints to the composite. That increases the event rate and adds power.
But…. But…. These are huge “buts.”
The users of this evidence (you and I) now have to fight through potential hype: that is, a trial with a composite endpoint that is positive, but it’s driven by one of the softer surrogate endpoints. This directly bears on the clinical significance of the finding.
A word on surrogate endpoints. These can be reasonable but increasingly, with technology, they can mean less than they did in the past. Take myocardial infarction (MI), for instance. Many composite endpoints include MI. And an MI can be a great thing to avoid. The problem with MI is that it’s getting easier and easier to diagnose it.
For instance, in 2021, David Brown, when he was at St Louis, led a huge meta-analysis of 144 CV trials that included more than a million patients randomized. They assessed the degree to which a nonfatal MI met the threshold for surrogacy—which required three things: a) biological plausibility, b) observational studies showing a constant association between the surrogate and the endpoint, and c) finding that reduction of the surrogate also reduces the ultimate endpoint of interest, like CV death or all-cause death.
Brown and his team found that—overall—nonfatal MI was not a surrogate for all-cause death, or CV death. This makes total sense, right, because 30 years ago, an MI was diagnosed with creatinine kinase (CK) elevations and ECG changes, and an MI was darn serious. And it still can be. But more recently, it’s much easier to make a diagnosis of MI with, say, a high-sensitivity troponin and some non-specific ST-T wave changes on an ECG.
Overall, the JAMA Internal Medicine analysis is sobering. Composite endpoints are all over the place and consist of quite dubious surrogate markers.
Which means, sadly, that many of our positive trials represent very small incremental gains. The onus on us is to be neutral skeptical but not cynical users of the evidence.
IFR vs FFR—a debate between RCTs and observational data
I did not know there was debate in interventional cardiology (IC) regarding the use of two techniques to assess functional stenoses of coronary lesions.
Of course, the old technique was a lot like echo reading: the IC would eyeball the angiogram and say it was 70% or 80% or 90%. Like judges who give harsher sentences before lunch, there was an utter lack of reproducibility.
Then came two techniques to assess coronary physiology. Fractional flow reserve (FFR) uses adenosine to create increased flow and the pressure gradient across the lesion is assessed during maximal vasodilatation. Anything below a ratio of 0.80 is considered significant—and don’t get me started on where 0.80 comes from.
Instantaneous wave-free ratio (IFR) on the other hand is adenosine-free and assessed during a diastole. It’s simpler and easier to do. But it too is a ratio.
It turns out two RCTs have compared the strategies for stable patients who were having angiography and considered for revascularization.
One was called DEFINE-FLAIR, which included 2500 patients and was originally published in the New England Journal of Medicine. At one year there was no difference in the primary outcome of death, MI, or unplanned revascularization.
However, at 5 years, there was now an 18% higher rate of the primary outcome in the IFR arm. The HR included 0.99-1.42 and the P value was 0.06.
The bigger issue came when looking at all-cause death and CV death, which was 56% and 2x higher in the IFR group. The weird thing was that MI and revascularization rates were not at all different. And, in patients who had their stent deferred because of the measure, there was no difference. All the increased risk in the IFR arm was in patients who had the percutaneous coronary intervention (PCI) done. That is strange.
The second trial comparing IFR and FFR was SWEDEHEART IFR. Here, 2000 patients were randomized and there was no significant difference at one year. Same primary endpoint of death, MI, revascularization.
At 5 years, the results were not significantly different for IFR vs FFR, though numerically there were more MACE events, and the rate of death was 9.4 vs 7.9 (HR, 1.20 ; 95% CI, 0.89 -1.62).
Both trials had similar follow-up and similar procedures and identical endpoints, so they lend themselves to a meta-analysis.
One was published in EHJ in 2023, first author is difficult to pronounce, Ashkan Eftekhari, found an 18% higher rate of MACE with HR 1.18 (95% CI, 1.04-1.34) and a 34% higher rate of all-cause death HR 1.34 (95% CI, 1.08-1.67) in the IFR arm, but, similar to both trials, there was no difference in MI or unplanned revascularization.
Early this week, JACC-IV published yet another study in this IFR vs FFR debate. It’s a large observational study. So, before I tell you about it, we have two RCTs, and one meta-analysis of about 4500 patients.
The observational study, first author Matthias Götberg, assessed 5-year outcomes of IFR vs FFR from the SWEDEHEART registry. This included about 43,000 patients who had either IFR or FFR.
Of course these were not randomized groups. So, the authors did 2:1 propensity score matching in about half the patients, leaving a group of 16k pts who had FFR and 8500 who had IFR.
They also did a secondary analysis wherein they compared the groups without matching.
They found no difference in MACE, death, CV death, MI or unplanned revascularization in the main propensity matched group.
Of note, the unadjusted risk for all-cause mortality in the unmatched cohort was increased with IFR (HR: 1.12; P = .003), even as the risk for MACE was reduced (HR: 0.93; P = .01). This the authors argue is likely because operators tend to do IFR on older, sicker patients.
Comments
Now we have a problem. We have RCT data which show a clear signal for worse outcomes with IFR. The death signal is significant but it’s hard to explain because the signal was not seen in the deferred PCI cohort of the DEFINE trial.
The overlap between IFR and FFR is fairly high, about 80%, but about 1 in 5 patients may get discordant results with the two techniques. Meaning one is positive and the other negative, which may lead to different approaches—PCI or no PCI.
The tension of course is that the real-world observational data show no differences. The problem of course is the same with all observational comparison: a doctor chose to do one or the other techniques. And while the authors did matching—a lot of matching—you can only match based on items on a spreadsheet. In the unadjusted analysis, death was higher. It went away with adjusting, but which is real?
Two editorialists, accompanying the observational study, put their chips down on there being no difference in techniques. They lean on the observational study, citing its size and its real-world origin and its strong attempts at adjustment. They also say the death signal in the meta-analysis is likely noise as the number of deaths were small, and there was no signal of other outcomes that could have led to death.
I find this a fascinating exercise in evidence-based medicine, because as an outside observer, it is really hard to say. I guess I lean toward there being no true harm signal with IFR. Another line of evidence I would cite, and I could be wrong, is that in all the studies, IFR led to more deferrals of PCI. And we know from FAME 1 that fewer stents led to better outcomes. We also know from every chronic CAD trial that revascularization did not improve outcomes over meds. So, to me, it is hard to implicate a measure that reduces PCI as harmful since PCI is neutral.
There are no planned RCTs of IFR and FFR, so this will have to be one of medicine’s mysteries. By all means, if you are an IC, and have an opinion different from mine, let me know.
High-frequency, low-tidal-volume ventilation
Speaking of non-random comparisons, a study in the journal Heart Rhythm compared two strategies of general anesthesia for the ablation of atrial fibrillation (AF).
I know, I know—this is a general cardiology podcast, who cares about such a specific question? I hear you. I highlight this study because it is a classic example of how not to study two treatment strategies.
Consider this more a question about ways of knowing rather than an AF ablation question.
Here is some background: In the pre-historic days of point-to-point radiofrequency (RF) ablation, we would make dots around the pulmonary veins (PVs) to electrically isolate the muscle bundles within the veins. Each dot was a few millimeter burn, if you will.
I say prehistoric, because most labs have gone to use multipole pulsed field ablation (PFA) catheters which ablate large swaths of atrial muscle—rather than a single point lesion.
One of the challenges of point-to-point RF ablation was that each lesion had to be perfect, because if it was not perfectly transmural, surviving myocardium would lead to PV reconnection and recurrence of AF days to weeks to months later.
One of the proposed ways to get “perfect” point RF lesions was to minimize chest movement during respiration. In the very old days we struggled with this when using conscious sedation because patients would take huge breaths. Then we moved to general anesthesia where breaths were controlled.
But a group of maximalists proposed even better general anesthesia wherein ventilation was maintained with very low tidal volumes and high respiratory rate. This was once called jet ventilation. The name is not important: it is simply ventilation with very low chest movement. The idea being better quality RF lesions and better results for AF suppression.
This is a totally reasonable question. I truly hope that TWIC listeners would know how to answer it. Right? You would say tens of thousands of AF ablations happen every day. All we have to do is randomize a fraction of these to low-volume high frequency ventilation and the other to standard ventilation and measure outcomes. It’s like the easiest trial ever.
Well, that is not what a group of high-frequency, low-tidal-volume (HFLTV) proponents have done. Instead they took 210 patients who had ablation and looked back and compared results of those who had HFLTV vs SV.
The study patients were part of a registry called REAL-AF. All patients had first AF ablation and posterior wall isolation and had persistent AF.
They found that patients who had HFLT ablation had shorter procedure times and less AF in follow-up (82% vs 69%; hazard ratio 0.41; 95% CI, 0.21–0.82; P = .012), indicating a 43% relative risk reduction and a 13% absolute risk reduction in all-atrial arrhythmia recurrence.
The authors who are proponents of the strategy spent many words in the discussion explaining why the HFLTV approach is better.
They do mention in the last paragraph that this was a non-random comparison and there could be selection bias but conclude that the HFLTV ventilation was associated with better outcomes…period. No caveats. No mention that this is hypothesis-generating and should be confirmed in RCT.
So, my friends, my comments are that this is bad—on multiple levels. First, HFLTV requires more work—it’s a different kind of anesthesia. They found no adverse events in the study of 200 patients but a lot of anesthesia in the community is delivered by non-MDs of varying and often low experience.
Without randomization, we don’t know whether the better results are driven by the different anesthesia or just patient selection or even performance bias. The latter being that docs who have a patient on HFLT ventilation might take better care to ablate.
Another issue, they screened more than 500 patients and excluded 225 patients because they did not have one year follow-up. That means you also have a selection bias because these are different sort of patients who complete their 1-year follow-up.
Yet another problem—you have a massive reduction in AF. A 13% absolute risk reduction, but the P value is 0.012, which is not very low and speaks to the fragility of the result.
I also question the 82% AF-free result at one year for persistent AF. This is way higher than other studies of ablation of persistent AF. Again, this I don’t see as nefarious but rather just a selection bias.
Clinically, I don’t worry too much about adoption of special anesthesia techniques because most labs have moved to PFA and, sadly, PFA is so easy, like a brain-dead procedure—that ventilation doesn’t matter.
I highlight this study as an example on how not answer questions in medicine. AF ablation, like left atrial appendage closure (LAAC) procedures are done at such high volume, it would be very easy to simply randomize patients and we would learn so much.
Looking back at non-random groups and comparing outcomes is fraught. And to me more likely to be misleading. I wish more of my colleagues resisted the urge.
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