May 23 2025 This Week in Cardiology

Medscape

23-05-2025

Please note that the text below is not a full transcript and has not been copyedited. For more insight and commentary on these stories, subscribe to the This Week in Cardiology podcast , download the Medscape app or subscribe on Apple Podcasts, Spotify, or your preferred podcast provider. This podcast is intended for healthcare professionals only. In This Week's Podcast
For the week ending May 23, 2025, John Mandrola, MD, comments on the following topics: Listener feedback on sports 'disqualification,' big digoxin news, Brugada syndrome, another positive finerenone study, and unblinded transcatheter trials.
Paul Dorian, a senior Canadian academic EP who has written extensively in the area of sports cardiology, writes via email regarding my comments on the Mayo Clinic's 'return-to-play' genetic heart disease study that I covered last week.
Dorian first agrees with my comments and the ideas of the authors who report an extremely favorable prognosis of patients with gene-positive but phenotype-negative disease. Let me quote from his email, because it is so educational.
I take issue with the phrase 'disqualification.' As sports cardiologists, we never ever 'disqualify' any athlete from competing in a sport.
Disqualification should be entirely restricted to the team, organization, or governing sport entity for a particular sport. Disqualification is a legal and organizational concept. What physicians, especially sports cardiologists, can, and should do is inform the patient of the best estimate of the risk of sport, specifically tailored to the severity of illness, the predicted risk of adverse events, including sudden death, the specific genotype, and or phenotype, and the type of sport and frequency, intensity, and duration of activity. Using the now well accepted concept of shared decision-making, this is then up to the individual patient/athlete to decide whether they wish to participate in their desired sport or sports, and at what intensity and under what circumstances.
Although physicians are sometimes asked to 'clear' an athlete for competition or sometimes indicate that the athlete should be 'disqualified' this is always inappropriate and should never be done (unless the physician is representing the team or sporting organization as opposed to caring for the athlete).
This, of course, does not mean that physicians should refrain from giving clear advice, including recommending against certain activities, if they feel that the risk is high enough.
For context, the risk of dying per ascent of Everest is 1%. The risk of dying from hang gliding or parachute jumping is approximately 2 per 1000 participants. If we don't 'disqualify' our patients or friends from attempting Everest, or hang gliding, or parachute jumping, why would we 'disqualify' a patient with much less than 1% annual risk of death from participating in sport?
I want to thank Dr Dorian for writing and I am glad to learn from experts like yourself. Digoxin News
On May 19, the European Journal of Heart Failure published the baseline characteristics of the DIGIT-HF trial. This is a placebo-controlled RCT in patients with symptomatic heart failure with reduced ejection fraction (HFrEF) with EF < 30% and Class 3-4 HF symptoms that compares the safety and efficacy of digitoxin vs placebo—in addition to baseline geometric mean titer (GMT). The authors published the rationale paper in 2019. I will link to it.
The primary outcome will be death and heart failure hospitalizations (HHF). The motivation for this trial stemmed from the old DIG trial, one of my favorites to discuss. The DIG trial, circa 1997, randomized just under 7000 patients and found no difference in mortality, which was its primary endpoint.
At the time, the trial was—largely—considered a negative trial as this was the era of angiotensin-converting enzyme (ACE), and beta-blockers, and mineralocorticoid receptor antagonists (MRA). However, in today's terms, where almost all HF interventions fail to move mortality, and only decrease surrogate endpoints, such as HHF, the DIG trial could easily be recast as a winner. For four big reasons:
One is that Dig shredded HHF (by a statistically significant 28%), on par with SGLT2 inhibitors and angiotensin receptor–neprilysin inhibitors (ARNIs) in heart failure with preserved ejection fraction (HFpEF). Two is that Dig also reduced total hospitalizations—which, in my opinion, is the only hospitalization surrogate that patients care about. Three…subgroup analyses from the Dig trial found a heterogenous treatment effect where most of the dig benefit came from patients with more advanced HF and lower EFs. Four, trial procedures allowed for open-label use of dig in the event of worsening HF. This occurred 8% more often in the placebo arm.
Also notable about the DIG trial is it was highly pragmatic. There was no run-in period and no dig levels were mandated.
Some might ask whether the DIGIT-HF trial enrollment of only 1200 patients will have enough power. I think it's a serious concern, but it's also possible by only recruiting the sickest of the sick, there will likely be higher event rates. Although underpowered trials are terrible because it's unethical to experiment on people without hope of having enough power to sort signal from noise.
Then, right after I tweeted this out, ID doctor Todd Lee responded to me on Twitter that there another ongoing dig trial for patients with HF. In August of last year, the European Journal of Heart Failure published the rationale and design paper for the Dutch-led DECISION trial.
This is an RCT, double-blind, placebo-controlled trial looking at dig in patients with 'chronic' HF and LVEF < 50%. The primary endpoint is cardiovascular death and HF visits, including hospitalization and urgent visits. The sample size is 1000 patients, all of whom have been enrolled by Dec 23.
It's powered to find a 22% reduction in the composite endpoint.
I am glad there are two trials but worry about the power of these trials. Make no mistake, dig use requires care and knowledge of pharmacology, which is less common in the modern clinician. But I also strongly believe digoxin has been unfairly maligned by biased observational comparisons wherein sicker patients get dig and that is why there is an 'association' with worse outcomes.
I will cite a meta-analysis of all DIG studies, first author Oliver Ziff, in the BMJ , wherein the association with digoxin harm falls in parallel with the robustness of statistical methodology. And, in fact, there is no association of harm when only dig RCTs are combined.
Dig can be an extremely useful adjunct to help patients with HF.
I don't know about you, but we get a fair number of consults to evaluate patients who are unfortunate enough to get an ECG that the computer reads as possible Brugada syndrome. Some, perhaps most of these, can be simply put off as misdiagnosed, because incomplete right bundle branch block is a common normal variant.
But, for patients who likely have Brugada syndrome and are asymptomatic, it's a struggle because you know there is a tiny but asymmetrically terrible risk of sudden death.
Everyone agrees that implantable cardioverter defibrillator (ICDs) should be used for secondary prevention of a second cardiac arrest, but for primary prevention where nothing has happened in Brugada syndrome, the harms likely outweigh the benefits.
If only there was a risk prediction model. You know, like the totally accurate helpful CHA 2 DS 2 VASc score.
Well, a paper from the group of Dr. Rui da Providencia in London has subjected the many risk prediction models of Brugada syndrome to systematic review and risk of bias assessment. The first author is Daniel Gomes and it's in EuroPace .
The first thing to say about this paper is that there are at least 11 multi-parameter risk scores for predicting major arrhythmia events in patients with Brugada syndrome. I did not know there were that many risk scores.
The second main finding was that 100% of the models were assessed as an overall high risk of bias. Third…the pooled c-statistics for each model had a lot of heterogeneity and lower discriminative power than originally reported.
The authors' second paragraph of the discussion outline the challenge:
At present, almost two thirds of patients with Brugada syndrome are asymptomatic at the time of the diagnosis, and up to 0.2%–0.6% per year will eventually develop ventricular arrhythmia or sudden cardiac death as the initial presentation.
They then write that clinicians need to balance that tiny risk against a cumulative ICD complication rate of 4%–6% per year — many-fold higher.
Think about it: how do you predict an event with a less than 1% incidence. We can try, but I think it's best to be super humble, calm, and reassuring in the exam room.
It turns out that there is a good list of 'general preventive measures' to go over with patients with Brugada syndrome. These include aggressive treatment of fever, avoiding dehydration and drugs that may induce ST-segment elevation in right precordial leads (Class I anti-arrhythmics, some anesthetics, and psychotropic drugs). We can also have these patients avoid recreational substances such as cocaine, cannabis, and excessive alcohol intake. All of these things can exacerbate the type 1 pattern and trigger VF.
To be fair, I am no expert in assessment of models, as it's above my pay grade as a clinician, but I cover the paper for the same reason I covered the genetic heart disease paper last week: technology and testing have increased the number of asymptomatic people harboring Brugada syndrome and its incredibly low risk of a terrible event. The digital health revolution will bring more of these problems, not less.
I have seen aggressive marketing (Watchman, Cardio-Mems, Entresto) but finerenone may be the champion of marketing.
At the European Society of Cardiology HF meeting, and simultaneously publishing in the Journal of Cardiac Failure , the FINEARTS HF authors report the results of a substudy of a small subset (~1000) of the total 6000 in the trial.
I don't have to tell you the topline result because you already know them: the sky is blue and every finerenone study is positive.
First let's briefly review FINEARTS-HF: NEJM 2024. Finerenone vs placebo in 6000 patients with HFpEF. Mean age 72 years, almost half female and the mean left ventricular ejection fraction (LVEF) was 52%. The primary outcome was CVD or a worsening heart failure (HF) event which included HHF or urgent visit for HF.
The finerenone arm had a 16% lower rate of the composite endpoint, which was statistically significant. The absolute risk reduction was 2.8% but there was no difference in CVD. Lower rates of HF events drove the positive results. Total death was also not statistically different.
The core problem of course was that this finerenone trial, like all finerenone regulatory trials, were compared against placebo rather than the $4 per month spironolactone tablet.
Purists will say, John, there is no proof that spironolactone reduces outcomes in HFpEF. They would cite the negative TOPCAT trial, and this would be technically correct. But, when TopCat was analyzed without the outlier countries Russia and Georgia, it was clear that spironolactone also reduced outcomes in HFpEF. Of course it does. Any doc who treats HFpEF knows that spironolactone is a secret weapon.
If we had had robust regulatory authorities at FDA, they would have forced Bayer to design their regulatory trials against spironolactone. If I were at FDA, it is what I would have required. Or at least do a three-arm trial with finerenone, spironolactone, and placebo.
Anyway, the latest substudy took 1000 patients of the total 6000 who had been randomized during a HF hospitalization or shortly after. In FINEARTS, recall that the proportion of patients without a worsening ambulatory or hospitalized HF event within 3 months of randomization was prospectively capped at approximately 50% of total enrollment.
The purported idea was to capture a unique cohort at risk for readmissions and to examine the effectiveness of early initiation of finerenone on short term readmission endpoints.
And you guessed it, among these patients, 30-day readmissions for HF were 1.8% vs 3.6% in those randomized to placebo. Similar results were observed when examining 60- and 90-day HF readmissions
You can see the marketing potential. HF readmissions is an area of focus among the quality people. Because it can bear on reimbursement.
Now the proponents of finerenone can say, look, we have a drug that reduces HF readmissions.
Come on you all. First, this is a small subgroup of a trial with a mere 16% reduction in a composite primary endpoint of HF events, with no difference in hard outcomes like CVD or all-cause death. And a weak comparator arm.
What's more, what do you think happens if you randomize one group of patients sick enough to have a HF hospitalization to an extra diuretic vs no extra diuretic? You get fewer readmissions.
I have little doubt that MRA drugs are effective in all patients with HF, regardless of EF. The question is whether the non-steroidal and surely more costly finerenone is better than spironolactone or eplerenone.
I have opined often on this podcast about the use of subjective endpoints in transcatheter trials that are open-label. The problem is that one group gets an intervention, with its huge caring signal, and the other groups gets no procedure. Tablets only. Probably bland white tablets.
Close your eyes and picture the scene in a valve-clipping procedure from the patient's perspective. The patient meets at least two, perhaps three specialist doctors in the prep area. Then they go in the room — the procedure room — and they see massive booms, huge screens, multiple people. And even if you give them general anesthesia, the impression is one of …holy mackerel, I remember that room — this procedure has got to help me. The control arm gets nothing but also knows they could have been randomized to the procedure.
Huge problem. Well, I am delighted to tell you that Sanjay Kaul, surely one of the best evidence adjudicators in all of medicine, wrote a short editorial in the journal EuroIntervention where he persuasively argues that open-label trials are rarely adequate to support labeling claims based on patient-reported outcomes.
I want to thank Sanjay for his incredible generosity. He has taught me so much over the years. He is really excellent.
In the editorial, Kaul cited a great example, one I did not know about. Perhaps you did. He contrasted two trials of hemodynamic monitoring. One was the GUIDE-HF trial of invasive hemodynamic monitors in HF patients, which used blinded assessment of Quality of Life (QoL). Every patient got a CardioMEMS device and its use was blinded. GUIDE-HF found no difference in the KCCQ. But the MONITOR-HF trial, which was similar, was open label trial of hemodynamic monitoring and guess what happened: it showed an improvement of Kansas City Cardiomyopathy Questionnaire (KCCQ) in the patients who had the device.
The article is a Tour De Force argument in favor of using proper sham controls for devices. It's an important concept because the cardiology space iterates so fast. I was talking yesterday with a nurse who is my age and we were reminiscing about the old vs new devices.
One depressing feature of this story is that it would be super-easy to do blinded trials. For the tricuspid valve interventions, you simply sedate the patient and put a catheter in the femoral vein and you have a sham control procedure. Then we would know.
Whenever you think a placebo procedure is unethical or risky — we can't do that, Mandrola — I ask you to think about two things: first, think about the counterfactual where we may still be doing left internal mammary artery (LIMA) ligation or TMR, transmyocardial revascularization if not for sham-controlled trials showing that they weren't effective. And the second thing to think about is to go look at the angiograms in the Lancet supplement of ORBITA trial. Look at those angiograms. Half of these scary lesions were initially treated with nothing. That should reassure you that sham controls are possible.
Finally, perhaps the most depressing part of the unblinded transcatheter trials is that I know , and you know , that the investigators know that blinding is necessary.
Medical investigators are supposed to be scientists and clinicians. Scientists should not need regulators to push them to do proper trials. If they're scientists, they should just do proper trials. And as clinicians they use the placebo effect nearly every day in the office, so they know that proper sham controls are needed from the clinical perspective.
Yet they did not do it. I'm just sad about this whole thing.