If you do a search in PubMed for the words “Cov-2 main protease screen inhibitors”, you get 295 hits. That’s as of this morning, of course – there will be more as time goes on. That represents a great deal of work done in a relatively short time (all of the citations, naturally, are from 2020 and 2021). But allow me to express what might be (for some) an annoying or unpopular opinion: that’s far, far too many papers.
Scrolling through the list will, I believe, illustrate some of the reasons I say this. To start with, there are a great many screens of approved drugs: a search for the words “Cov-2 main protease screen inhibitors repurposing” gives you 96 papers, and the similar search of “Cov-2 main protease screen inhibitors approved” gives you 94, which is surely an almost complete overlap. My hope at first was that many of these would turn out to be reviews or brief front-of-the-journal notices to full papers themselves, but that doesn’t seem to be the case. It’s just one study after another. So as designated Pain In the Rear, I have to ask if we needed over ninety different papers screening what in many cases is more or less the same set of compounds, over and over and over.
Now, some of the 96 papers make that list because they mention repurposing of approved drugs in passing, before turning to something else – generally natural products, from what I can see. My strong impression is that there are many groups who have previously described compounds from Root X or Fungus Y, and who then turned around and ran an in silico screen with these structures to see if they might dock into the main protease binding site. Very few of them actually report experimental data from a physical screen. A quick look showed that at least 79 of the 96 papers appear to be completely computational – virtual screening, docking, and so on. I have not done a similar analysis of the 295 papers mentioned above, but spot checking indicates a roughly similar proportion.
That shouldn’t be too surprising. Computational studies are a lot easier to get off the ground than a physical assay (that’s one of the appealing things about them). But that’s one of their main disadvantages as well, and I think the current state of the coronavirus protease literature illustrates that. Frankly, very few of these papers seem to me to be worth very much, and they’re worth even less with so many other broadly similar studies out there at the same time. And I don’t want to sound like I’m just picking on the in silico papers – many of the ones that did actual protease assays haven’t added too much to our knowledge, either, since (as mentioned) they often are screening pretty similar libraries. Knowing that some polyphenolic phytochemical is a high-micromolar binder to the main protease does not shorten this pandemic nor will it shorten future ones, and hearing about it several times doesn’t change that.
In sum, the majority of these papers seem to be opportunistic efforts that have jumped on the pandemic as a way to pad everyone’s list of publications. And no, I’m not surprised to see this – it’s just what one would have expected. But that doesn’t make it pleasant to watch. If you move out of the coronavirus main protease screening literature, there are untold masses of papers that might as well be titled “Stuff We’ve Already Done, Now With a Coronavirus Angle Glued Onto It So It Can Be Published Again”. No doubt some of these authors felt that they were making a real contribution, if we’re going allow intent as a mitigating factor, but I’m also sure that many others just saw a chance to publish some easy papers, and likely in better venues than usual while the editorial standards were temporarily lowered.
I should make clear that I of course don’t have any problem with people studying inhibitors of coronavirus proteases. But it should also be clear that any work like this is being stored up for the future. It was and is extremely unlikely to have any effect on the course of the current pandemic, given the amount of time it takes for small-molecule drug development. These are not vaccines, where the massive machinery of the immune system is waiting for you to set it off in the right way and where we already know a number of methods that can be put to the test in the clinic. Protease inhibitors for a new pathogen start at the bottom and have to work their way up, and it’s a long haul. Frankly, even after those years of work, the finely tuned inhibitor of the current viral protease that would come out of such efforts is extremely unlikely to be useful against future viruses. Every protease is different, and a really effective drug is going to have to take advantages of all those individual features of its target – which makes it correspondingly less likely to be repurposed. The successful antiviral protease inhibitors have been developed against pathogens that just hung there in the sky like baleful stars for years because they were hard to work up a vaccine against: HIV, hepatitis C.
Enough grumbling for one day. There’s a bright side to the way the scientific literature has worked during the pandemic – in addition to all the repetitious junk, there have been huge amounts of actual useful information that have been shared with a speed and thoroughness never seen before. That cheers me up a great deal and gives me hope that it makes us all the more ready for future emergencies. But that doesn’t mean that we should give the junk a pass. Wastes of time and effort are still wastes. On that topic, though, the situation with the number of clinical trials run during the pandemic is an even bigger disgrace, and that deserves a separate look. We really don’t want to to that again. . .