Jun 23, 2023 This Week in Cardiology Podcast

John M. Mandrola, MD


June 23, 2023

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 June 23, 2023, John Mandrola, MD, comments on the following news and features stories.


First an announcement. Next week, #TWICPodcast takes a Friday off to celebrate US independence from the British monarchy. The Mandrola family, ranging from age 2 to 86 years, will spend the weekend at the lake in rural Kentucky. If you think I am a beginner in statistics, you should see me try to park a boat in a dock.

Starting HF Meds During Hospitalization for HF

The Journal of the American College of Cardiology (JACC) has published an observational study that describes what is happening in certain hospitals regarding heart failure (HF) medications.

First off, this is a great use of observational data. Science tells us what we can do, trials tell us what we should do, and registries (and observational data) tell us what we are doing. Good. No non-random comparisons.

The goal of this analysis of about 50,000 patients from 160 hospitals who are signed up to be in the Get With The Guidelines Registry was to compare the actual vs maximal prescribing of evidence-based medical therapy for HF with reduced ejection fraction (HFrEF).


  • On admission, 15% of patients were receiving all indicated HF medications.

  • Overall, the mean number of recommended medications was 3.9 (maximal use based on database records). The actual number was 2.1 on admission, and then 3.0 at discharge.

  • Said another way, 1 in 6 patients were getting the full regimen of “evidence-based meds” at admission and this increased to 1 in 3 at discharge.

  • Another piece of good news was that over the time of the study, 2017-2020, there was a steady increase in medication initiation.

  • Also, initiation of all four classes of medications increased steadily.

On the downside, women were less likely to have “appropriate” medication initiation. And rural hospitals did worse than urban hospitals. The authors also note that patients with co-morbidities are less likely to receive full HF medications.

Comments: First, I like covering observational studies that don’t try to make comparisons. Good on JACC and the authors. But as I have said many times before, I worry about this rush to medicate patients with HF.

My worries relate not to any concerns about the evidence for HF therapy. (except of course sacubitril/valsartan) but rather the translation of this evidence to patients who are not in clinical trials.

Whenever possible and consistent with the patient’s goals I go full gas on the big four classes of HF medications. But we must remember basic principles,

  • First, most of the evidence for HF meds comes from stable outpatients. This is a lot different from trying to initiate meds in acutely ill older patients who are in the hospital. These patients are much more vulnerable to harm.

  • Many patients I see have HFrEF because of atrial fibrillation (AF) with a rapid rate. They do best with short-acting beta blockers and digoxin. Thus, in a spreadsheet, and in my quality measures I look to be a failing doctor.

  • For example, many patients have HF because of infection. These patients have soft blood pressure (BP) and renal insufficiency and docs are nervous about starting patients on full gas HF meds.

  • Many patients have co-morbid conditions. By definition, evidence-based meds may not apply here, because these sorts of patients were not common in trials.

  • The authors cite STRONG-HF, a trial that I have lauded, in support of rapid titration of HF meds. But few medical centers have even a fraction of the set-up and back up that was used in STRONG-HF.

While I agree that hospitalization for HF is an opportunity to improve care, I worry that the get-with-the-guidelines enthusiasm has a risk of turning doctors into prescribing robots. And that is a bad idea.

Finally, we need to always remember Goodhart’s law — once a measure becomes a target it loses its effectiveness as a measure.


Note: I normally shun brand names. Industry needs no marketing help. But in the case of the Impella, this would mean saying percutaneous micro-axial left ventricular assist device each time. So, I will make an exception here.

Four weeks ago, I covered a paper from JACC describing use of Impella 5 series for support during ventricular tachycardia (VT) ablation. This was a paper from Cleveland Clinic. It was a non-random comparison using a historical control. The bottom-line was that success rates were no different, but complication rates were much higher in the Impella-assisted VT ablations: 29% vs 2.4% in controls.

Then 2 weeks ago, I covered a story about Abiomed recalling nearly 500 of its Impella 5 series devices due to purge fluid leaks.

On both occasions I opined a bit about the lack of randomized controlled trial (RCT)-level data supporting use of this device, the wide variation in its use, the financial incentives for its use, the low-bar it reached in getting approval, and the worrisome signals from the observational data thus far.

Well, here we are again.

JAMA-Cardiology has published another observational study, this one with quite impressive methods. The study comes to a somewhat unusual conclusion.

  • The analyses come from the Beth Israel Boston group led by Dr. Robert Yeh. First author Zaid Almarzooq. I used the plural “analyses” here because, while this was one manuscript, they used four different ways to compare outcomes in patients who had Impella used for cardiogenic shock (CS).

  • The data source was Medicare fee for service claims for patients who had acute myocardial infarction (MI)-related cardiogenic shock (CS) from 2015-2019.

  • In this database, there are basically two groups: those with CS in whom a doctor decided to use the Impella, and those in whom a doctor decided not to use the device.

Of course, these types of studies are being done because the device was approved without passing muster in an RCT. I will return to that but for now let’s stay with the paper, because it is quite good.

In much the same way that Brian Nosek asked different groups of scientists to analyze one data set and the groups chose to analyze the data in different ways, Dr. Yeh and colleagues decided to look at this database in four different ways.

  • They first compared the Impella use vs nonuse strategy with a standard propensity matching analysis. Here they used an inverse prob of treatment weighting to try and account for baseline differences.

  • In the second way they looked at the data, they used an instrumental variable analysis to sort out the baseline differences. Instrumental variables that are relevant, exchangeable and have no effect on treatment are hard to find. One example of an instrument variable might be natural experiments. In this study, they used a hospital’s percentage use of Impella in all CS patients undergoing percutaneous coronary intervention (PCI) in the previous 2 years.

  • The third way they compared the two strategies was with a difference in difference approach. This means they looked at changes in outcomes at hospitals whose use of Impella grew rapidly over time vs outcomes from hospitals that did not increase Impella use over that same time. You’ve probably guessed here that this is clearly a population-type comparison and so basically this acts a sensitivity analysis for the two previous approaches.

  • Finally, they looked at the effectiveness of initiating Impella use within 2 days of PCI. This approach creates a time-zero standard, because including devices placed later induces an immortal time bias issue – meaning you have to be alive for those days to get the device.

I realize that this is a lot of methods stuff. My AF-ablation doctor translation is that these are four approaches to simulate the elegant and ultimate way of knowing things — that is, you randomize patients with CS and count outcome events.

Here are the results:

  • The analysis included 56,000 patients; mean age 73 years, mostly male.

  • About 17% got an Impella and 83% did not. Of those who did not get Impella, about one-third got an intra-aortic balloon pump.

  • Unadjusted, there was a massive 19% higher rate of death in the Impella arm; 56% vs 38%.

  • Of course, unadjusted comparisons don’t tell you anything because their baseline characteristics table shows that patients who received the Impella were much sicker.

  • That is the core problem they are trying to solve with those fancy four methodologies I told you about.

What happens with the variable adjusting techniques? Again, results here are absolute not relative differences.

  • For the basic propensity matching of variables, Impella use was associated with a 15% higher absolute risk of death vs nonuse. There were tight confidence intervals (CIs).

  • For the instrumental variable analysis, Impella use was associated with a 13% higher risk of death vs non-use. There were wider CIs.

  • For the difference in difference analysis looking at hospitals, Impella use did not have a higher risk of death but CIs were even wider.

  • For the grace period analysis looking at early Impella use, there was an 18% higher rate of death with Impella, with tight CIs.

Interpretation: On the surface, you could look at this and say three of the four techniques found strongly negative associations with Impella use. The one approach that found no association had the widest CI.

And the authors do get around to writing that not one of their analyses found benefit from Impella use. This is similar to many other observational studies that have reported worse outcomes with Impella

Here is the problem though: The authors tell us that Evidence from the data as well as background knowledge regarding drivers of treatment decisions and institutional differences suggested that key assumptions for all approaches likely were strongly violated.... Thus, we are not confident that any of the statistical estimates summarized above can be given a causal interpretation.

My translation is this: Look, we know that doctors decide to use Impella in sicker patients. No matter the matching techniques, retrospective looks at administrative data are susceptible to bias — sicker patients get Impella and that is why they do worse.

So they tried to use different approaches than basic matching, including an instrumental variable and difference in difference analysis among hospitals. These are novel techniques. Sadly, they also found significant violations of assumptions in the instrumental variable analysis — things like different hospital sizes, teaching status at a hospital, and variations in the treatment of minority patients. In addition, in the difference-in-difference analysis, wide CIs precluded reliable interpretation.

Now here are their conclusions: Our findings suggest that commonly used observational data sets cannot support a causal interpretation of the estimates produced by different analyses used for the evaluation of percutaneous mechanical support devices in cardiogenic shock. Randomized clinical trials will allow valid comparisons across candidate treatment strategies and help resolve ongoing controversies.

David Cohen and Manesh Patel wrote the editorial. It’s quite good. You should read it. They laud the authors for doing a far more rigorous than normal observational study.

  • They, too, conclude that some questions can’t be answered with observational data. It seems that almost every week, I am saying the same thing.

  • I am tempted here to say, Okay, wait a second. Bobby Yeh’s group is one of the best at this stuff. They did these incredible analyses and three of the four analytic methods suggest serious harm with Impella, as have other observational studies. Can’t we then consider that the weight of the evidence is towards harm?

  • But you know the answer to that temptation. No. Double no. Cohen and Patel and Yeh are correct. In my mind, it doesn’t matter if 30 observational studies found harm from Impella. Non-randomized comparisons are just inherently susceptible to the bias of sicker patients getting Impella.

  • The analogy is hormone replacement therapy for cardiovascular (CV) protection in women. There actually were more than 30 observational studies suggesting benefit. And guess what? The Women’s Health Initiative RCT showed that they were all biased.

What’s weird though is that the cardiology literature overflows with these sorts of analyses. It’s as if academic cardiologists are similar to masters’ bike racers. We train all winter, every winter, thinking come spring, we will ride like a pro. But we never do. It never changes. The fast guys always win. And in academic cardiology, the observational comparisons continue to be done. And no matter the analytic method, bias persists.

The main reason to read Cohen and Patel is the final two paragrpahs where they support their subtitle: “Putting the horse back in front of the cart.”

They argue for incentivizing the use of RCTs. This made me cheer, because it is the first policy I would enact if I was in charge.

  • Enhance the ability of payers to incentivize performance of clinical trials of approved devices through conditional coverage with evidence generation.

  • My only change would be that coverage with evidence generation would be before approval. You want us to pay you for this device, fine, enroll the patient in a trial.

  • If this was our policy, we would know if Impella helps or harms or does nothing. We would know if left atrial appendage closure helped or harmed. We would know the placebo-controlled effect of AF ablation.


I’ve never taken testosterone, though amateur bike racers who race for free socks, are now tested for testosterone as a performance enhancing drug.

Everyone I have ever talked to who took testosterone said it works. Studies done over decades find its clear androgenic effects. You get stronger. You feel younger. That is no small thing. And as men age, their testosterone levels drop, muscles sag, watts per kilo go down.

The $64,000 question is whether or not men who have low testosterone should take extra testosterone.

But in the same way we know that testosterone makes for bigger muscles, more sex drive, and more watts per kilo, we also know that it can increase hemoglobin (think viscosity) and increase BP.

You could feel stronger and be more apt to have a cardiac event.

Last Friday evening, the New England Journal of Medicine (NEJM) published the TRAVERSE study — a non-inferiority placebo-controlled RCT of testosterone in older men who had pre-existing or a high risk of heart disease.

  • To be enrolled, men had to have symptoms and signs of hypogonadism. This included two fasting testosterone levels of < 300 ng/dL.

  • More than 5200 patients were randomly assigned to testosterone gel or placebo. The dose was adjusted to maintain testosterone levels between 350 and 750 ng/dL.

  • The CV safety endpoint was the first occurrence of a three-component composite endpoint: CV death, MI, stroke. A secondary endpoint included these three plus coronary revascularization.

  • Non-inferiority required an upper-bound of less than 1.5 for the hazard ratio (HR) of the primary endpoint.

  • Mean follow-up was 33 months. Mean age of men 63 years; mean body mass index (BMI) was 35; median testosterone level was 227 ng/dL.

Results: 7% of the testosterone group had a primary outcome event vs 7.3% in the placebo arm. That’s an HR of 0.96.

But it’s a noninferiority study, so you have to check the 95% CI of the HR. Here the worst-case scenario or upper bound of the CI was 1.17, way less than the 1.5.

Said another way, the upper bound of the 95% CI included a 17% risk increase of CV events and that was less than the chosen noninferiority of 50 % worse. So noninferiority was met. This was done on the intention to treat analysis. There was a high discontinuation rate, but they performed robust sensitivity analyses to evaluate treated patients, and these upheld the noninferiority.

  • The secondary endpoint of CV death, MI, stroke, or revascularization were nearly identical.

  • No difference in prostate cancer occurrence and only minor increases in systolic BP,

  • However, in the testosterone group there were:

    • 14 more venous thromboembolism events (HR 1.46);

    • 12 more pulmonary embolisms (PE);

    • 47 more non-fatal arrhythmia;

    • 27 more AF events;

    • 20 more acute kidney injury (AKI) events.

One important factor: Figure 1 shows very strict control of testosterone levels during the trial.

Mean testosterone in the placebo group were about 225 ng/dL. Testosterone levels in the active arm were about 350 ng/dL but decreased over time. To me, this seems important.

Comments. I am not sure this answers the question of testosterone safety. These were 63-year-old men studied for 2 years. The upper bound included a 17% increase in major adverse cardiac events (MACE) in just this short time.

There were more PEs, more arrhythmias, and more AKI events in the testosterone group.

Plus, these patients were way overweight — mean BMI was 35. I know, don’t beat me up, BMI is not a perfect measure, a handful of them could have been bodybuilders, but mostly these were fat old dudes.

What if they lost fat? Here they might get a boost of testosterone with a decrease in MACE.

The AbbVie sponsored trial may have checked the regulatory boxes, but I am not convinced testosterone replacement for fat 63-year-old men with CV disease or high risk for CV disease is a place the medical profession should be going.

I feel the same way here as I do about ablating AF in patients who have not had attempts at risk factor modification. It’s unwise. Many people say Mandrola, you are foolish, people won’t or can’t lose weight and get fit. Just ablate them, give them testosterone etc.

I hear that. I am also a pragmatist, and I practice that way. But doctors still have a respected standing among many people. As doctors, we have a chance to help people with our words. Most will not heed the diet and exercise talk, but some do. And when I ask those who transformed their lives by exercising and eating better why they did it, they often say because my doctor told me I should.

Two decades on, I still stand by the notion that we should not give up on our chance to heal with words. I suspect some of you will disagree. Let me know. Teach me.


Did you know that colchicine has been used for hundreds of years? It’s so old that it was never approved by the US Food and Drug Administration (FDA) for a formal indication. That led to a regulatory mess around 2010 in which a single drug company decided to test colchicine formally in a trial, a very small and inexpensive trial, and it garnered formal approval of branded Colcrys for gout. That led to a 3-year term of marketing exclusivity, prohibition of generic sales, and a 50-fold increase in price.

Oral colchicine remains expensive today.

Biologically, colchicine has broad anti-inflammatory effects, and we all know that atherosclerotic disease is at least partially an inflammatory disease.

Recently FDA has approved lower-dose 0.5 mg daily of colchicine as the first anti-inflammatory drug demonstrated to reduce the risk of MI, stroke, coronary revascularization, and CV death in patients with either known heart disease or high risk for CV disease.

Two trials underpinned the approval. Both were published in NEJM.

  • COLCOT, in 2019, randomly assigned about 4700 patients who had had a recent MI to colchicine vs placebo.

  • These were 60-year-old mostly white men, who could not have left ventricular dysfunction.

  • 99% were on statins and dual antiplatelet therapy.

  • Over a median follow-up of just 22 months, a primary endpoint of CV death, resuscitated cardiac arrest, MI, stroke, or urgent coronary revascularization occurred in 5.5% in the colchicine group vs 7.1% of the placebo group. This 1.6% absolute risk reduction (ARR) corresponds to an HR of 0.77 (0.46-0.96); P = 0.02.

  • A positive trial. But CV death, sudden cardiac death, and MI did not differ much. The composite endpoint was driven mostly by lower rates of urgent revascularization and stroke. All-cause deaths were nearly identical.

  • Adverse events were mostly similar with slightly more diarrhea and nausea in the colchicine arm.

In 2020, LoDoCo2 randomly assigned about 5500 patients who had chronic coronary artery disease (CAD) to colchicine vs placebo. These were 66-year-old mostly white men from Australia or the Netherlands; 94% were on statins.

Notable was a run-in period in which 15% of patients did not undergo randomization, mostly for gastrointestinal reasons.

  • Over a median follow-up of just 28 months, a primary endpoint of CV death, MI, stroke, or coronary revascularization occurred in 6.8% (colchicine) vs 9.6% (placebo).

  • This 2.8% ARR corresponds to a HR of 0.69 (0..57-0..83); P < 0.001.

  • A positive trial, but CV death rates were low and not different.

  • MI was 1.2% less in colchicine arm.

  • Stroke incidence was low and not much different.

  • Again, lower revascularization rates were the main driver of the composite.

  • Death from any cause was non-statistically-significantly higher in the colchicine arm: 2.6% vs 2.2% in the placebo arm, driven by a 50% higher rate of non-CV-death.

Comments on low-dose colchicine. The drug looks to have a consistent effect. It’s a modest reducer of non-fatal cardiac events. Most positive is that it works in addition to good background therapy, and the rates of gout were substantially lower in LoDoCo2.

  • In patients with chronic CAD, who don’t mind taking extra pills to maximally reduce non-fatal events, low-dose colchicine is reasonable. In addition, the Kaplan Meier curves seemed to be separating over time, so maybe the effect would increase with time.

  • Scientifically, it piques your interest because it’s the first anti-inflammatory drug to market for CV disease. Canakinumab also reduced inflammation and CV events in the CANTOS trial but the reductions were modest and the company decided not to market the interleukin 1-beta inhibitor.

  • But I am not enthusiastic about colchicine. This is clearly an incremental advance.

  • These were young patients in their 60s and the trials were less than 3 years long. There were no signals of reductions of CV death or death.

  • In fact, the higher death rate in the colchicine arm in LoDoCo2 is concerning. Maybe the 50% higher rate of non-CV-death was noise, but the CI went from 0.99 to 2.31.

I hope colchicine does not displace statins. Both trials studied colchicine in patients with very high rates of statin use.

I also suspect the branded drug will be costly. Patients in ttheir late 60s who have established CAD, and likely other chronic conditions such as hypertension, diabetes, and maybe AF will have to take oodles of pills. Adding another pill for a 1% to 2% ARR of non-fatal events over 2.5 years seems hardly worth the trouble.


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