The effect of hyperbaric oxygen therapy on myocardial function in post-COVID-19 syndrome patients: a randomized controlled trial, 2023, Leitman et al.

Israeli research

We've seen other papers from members of this team. There have been issues with undeclared conflicts of interest.

Hyperbaric oxygen therapy improves neurocognitive functions & symptoms of post-COVID condition: randomized controlled trial, 2022, Zilberman-Itskovich
This paper was on the same study - with the 2022 one focused on cognitive symptoms and this latest one focused on cardiac issues.

Recovery of Repressed Memories in Fibromyalgia Patients Treated With Hyperbaric Oxygen, 2018, Lev-Wiesel et al

 

There was some loss of data along the way - creating opportunities for biasing outcomes, so we need to trust that the authors acted properly. This is more difficult to do when no competing interests are declared (as is the case with this paper) when we know that some authors do in fact have significant competing interests.

For example, Efrati Shai, the senior author here, is a shareholder in Aviv Scientific and an employee of the Sagol Centre, with those organisations together rolling out a global network of hyperbaric clinics (as I noted in a comment on the 2022 paper):

 

I think there were quite a lot of parameters potentially up for evaluation. Only one was found in the straight comparison of the treatment versus sham groups - GLS. I'm not sure how significant the reported mean change at baseline really is.

Another paper looked at 16 papers on GLS, covering 2,396 patients. It concluded that the mean was 20.7 and that normal should be regarded as over 18%, borderline 16 to 18% and abnormal function below 16%. So, in that case, the GLS figures in this HBOT study at baseline were normal, as they were after treatment.

Given that the GLS is the single difference, the actual changes are pretty minor. To reiterate:
HBOT - 19.1 +-1.8% to 20.4 +-2.1
sham - 19.5 +-2.1% to 20.0 +-2.1
And the mixed model analysis was not significant - I think that means that we can't conclude that the treatment made any difference to GLS.

They did a post hoc analysis, by selecting a subset of participants - which is fair enough, but again creates a whole range of opportunities to bias the outcomes. So, Figure 2 actually looks a bit convincing, in terms of the HBOT moving GLS towards that 20% mean, but we have to remember this is not in fact the primary outcome, but instead is data with post hoc selection.

 

From the discussion:

I think this probably overstates things. From that paper I quoted above, a GLS of less than -20% is not necessarily a dysfunction, subtle or otherwise.

Also from the discussion:

That's interesting.
Ref 33 is Ramadan, M. S., Bertolino, L., Zampino, R., Durante-Mangoni, E. & Monaldi Hospital Cardiovascular Infection Study G. Cardiac sequelae after coronavirus disease 2019 recovery: a systematic review. Clin. Microbiol. Infect. 27(9), 1250–1261 (2021).
We haven't looked at that paper yet. I note it's a review paper, so it will be citing another paper when it talks about that specific finding.

 

I won't make a separate thread for that paper, as it doesn't relate specifically to Long Covid. It just evaluates cardiac parameters in people who had had Covid-19.

Here's the link: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC8220864/

Figure 2 of the Ramadan paper summarises reports from various papers. I found references to three papers mentioning GLS:
Brito - 0% of the sample was hospitalised. 11% had a reduced GLS
Li - 100% of the sample had been hospitalised. 70% had a reduced GLS
Wang - 100% of the sample had been hospitalised. 30% had a reduced right ventricle peak GLS.
Figure 2 suggests that only 2% of people who had had COVID-19 had reduced GLS in the 0 to 3 month post-infection period. I didn't see where theRamadan et al authors got that figure from.

We'd have to look at those specific papers to see if anything was said about the likely pre-infection heart condition of the samples, and what exactly constituted a reduced GLS. Regardless, just on the information in the Ramadan paper, I think we can say that it's rather misleading to say, as this 2023 Leitman paper did, that "reduced GLS was reported in 30% of post-COVID patients 3-6 months from infection". I think that's, at best, only a reasonable conclusion for hospitalised patients, and we don't really know if that was a result of the infection or a pre-disposing factor for a serious infection.

The Ramadan paper doesn't provide any evidence that reduced GLS is relevant to people with persisting symptoms after a Covid-19 infection.