There are perfectly valid reasons to conduct large pragmatic trials of syndromic conditions, particularly where the biology isn’t fully understood at a mechanistic level.
I’ll talk with respect to sepsis (not ARDS) because that’s more directly in my domain of expertise academically speaking. Sepsis is a heterogenous syndrome. A very heterogeneous syndrome. A very very heterogeneous syndrome. But, we share the world with abundant micro-organisms who have co-evolved with us. Some have evolved to become “predators” as Lawrence puts it (I actually really like this and will be using in future teaching with attribution if that’s ok) while others are more out to try and co-exist, but can’t help but cause damage along the way (a lot of which is “friendly fire” from our own immune system anyway). Some pathways in this process and extremely well conserved. LPS for example. The mechanistic pathways of LPS are so well conserved that injecting sterile LPS will cause multi-organ failure and “sepsis” without even needing bacteria to be present. So there is a rationale for trying to study even a heterogeneous syndrome like sepsis as a single group. The question is, where do you draw the line in terms of experimental design, and where do you try to tackle any heterogeneity of treatment effect through analysis, accepting that the latter will inherently have lower power.
Current sepsis RCTs recruit patients that look like this: “All comers to the ICU with shock and proven or presumed infection”. It’s highly pragmatic, but if you were to find a signal, it would be incredibly broad in its generalisability. You can also do a big study fast. Great. Only this includes 30 year old men with pneumonia caused by pneumococcus, 90 year old women with a UTI and shock from e.coli and everything else in between. My view is that this is just too heterogenous a group, and my evidence for this has been the rather overt inability to discover effective treatments in this field over the past 20 years. We have tried immunomodulation of specific and well conserved pathways that tend to be activated by all bacteria (IL-x etc.) but generally this hasn’t worked. Probably because we either encounter patients too late and they would almost need to be used in a prophylactic context, or because the pathways are just more complicated than we presently understand and more lab/bench work is needed.
So could we go narrower? Sure. I think an optimal RCT in sepsis might look like this “All comers to the ICU with shock thought secondary to proven gram negative bacteria”. This is a little more refined. You can still do a large RCT and the results would still be broadly applicable. Patients in this group will still have a variety of different organ systems as their point of inoculation, but we are designing the study against a particular host-organism interaction (principally LPS in this case). There will still be heterogeneity. E. coli is not the same as Klebsiella pneumoniae as an example. They do cause clinically distinct presentations. However, there is still quite a lot of conservation in the host interaction. Even with this arrangement, I have concerns. Pseudomonas is quite a different animal with a lot of intrinsic resistance factors. What about organisms with inducible AmpC. The list could go on.
Should we go narrower still? I don’t think so, at least not for now. What would this look like? Recruit: “Male patients, over 65 years old, who are previously independent, with proven E coli infection from a urinary source, in shock, but not DIC, in the UK”… etc etc. Where do you draw the line? With any infectious ailment, the clinical manifestation is an interaction between the host (a highly complex organism in its own right) and the microorganism. The variability in human hosts is vast. This is not a lab with all male Wistar rats of the same weight and age. Further, by demanding such a strict entry criteria, it will be very challenging to recruit any patients. And by the time we recruit a single patient, they will probably be so late on in their clinical pathway, that our proposed treatment will have long since missed its chance to work. Could you do it with a massive global research network? Maybe, but the results will have such limited generalisability that I almost think it would be a worthless endeavour.
All this Petty/Bone chat misses the point. It isn’t a binary state between a “good” trial and a “bad” trial based on who we include in the trial. Everything sits on a continuum and we need to decide where is optimal. I fully accept that the current approach for lots of things is too pragmatic and too broad. But that doesn’t mean the solution is so straightforward as you suggest it is. It’s still incredibly difficult to know where to stop slicing.
There are also treatments where the host interaction is likely to be very well conserved and so it’s reasonable to do a large and inclusive trial. The mechanisms for how humans handle and respond to oxygen are effectively universal. ICU-ROX and Mega-ROX are good examples (who incidentally both have pre-defined “sepsis” subgroups, as they are expecting there to be some heterogeneity of treatment effect).
This isn’t some global scientific conspiracy. The thought that there could be such a thing when most people in a single department don’t even agree on a single trial interpretation does make me laugh a little! I’m a little wary when people tell me they’ve stumbled upon something that a global scientific community has missed, because honestly, we haven’t. I can’t tell you how many times my lab group has had the syndrome/heterogenity conversation in sepsis/ARDS/critical care etc… It’s incidentally also a theme of my PhD thesis (i.e. how we should best address it).
But maybe these ideas need publishing in the mainstream journals again if you are concerned that we aren’t talking about it enough? If there is appetite from a journal editor I’d happily write on the issue.