The other day, I had some uncomplimentary things to say about a recent J. Med. Chem. paper on fragment-based dihydrofolate reductase inhibitors. Well, I know that I don't say these things into a vacuum, by any means, but in this case the lead author has written me about the work, and a reviewer of the paper has showed up in the comments. So perhaps this is a topic worth revisiting?
First, I'll give Prof. Joelle Pelletier of U. Montreal the floor to make the case for the defense. Links added are mine, for background; I take responsibility for those, and I hope they're helpful.
I was informed of your recent blog entitled ‘How do these things get published’. I am corresponding author of that paper. I would like to bring to your attention a crucial point that was incorrectly presented in your analysis: the target enzyme is not that which you think it is, i.e.: it is not a DHFR that is part of ‘a class of enzymes that's been worked on for decades’.
Indeed, it would make no sense to report weak and heavy inhibitors against ‘regular’ DHFRs (known as ‘type I DHFRs’), considering the number of efficient DHFR inhibitors we already know. But this target has no sequence or structural homology with type I DHFRs. It is a completely different protein that offers an alternate path to production of tetrahydrofolate (see top of second page of the article). It has apparently evolved recently, as a bacterial response to trimethoprim being introduced into the environment since the ‘60’s. Because that protein is evolutionarily unrelated to regular DHFRs, it doesn’t bind trimethoprim and is thus intrinsically trimethoprim resistant; it isn’t inhibited by other inhibitors of regular DHFRs either. There have been no efforts to date to inhibit this drug resistance enzyme, despite its increasing prevalence in clinical and veterinary settings, and in food and wastewater (see first page of article). As a result, we know nothing about how to prevent it from providing drug resistance. Our paper is thus the first foray into inhibiting this new target – one which presents both the beauty and the difficulty of complex symmetry.
Regular (type I) DHFRs are monomeric enzymes with an extended active-site cleft. They are chromosomally-encoded in all living cells where they are essential for cellular proliferation. Our target, type II R67 DHFR, is carried on a plasmid, allowing rapid dissemination between bacterial species. It is an unusual homotetrameric, doughnut-style enzyme with the particularity of having a single active site in the doughnut hole. That’s unusual because multimeric enzymes typically have the same number of active sites as they do monomers. The result is that the active site tunnel, shown in Figure 4 a, has 222 symmetry. Thus, the front and back entrances to the active site tunnel are identical. And that’s why designing long symmetrical molecules makes sense: they have the potential of threading through the tunnel, where the symmetry of the inhibitor would match the symmetry of the target. If they don’t string through but fold up into a ‘U”, it still makes sense: the top and bottom of the tunnel are also alike, again allowing a match-up of symmetry. Please note that this symmetry does create a bit of a crystallographer’s nightmare at the center of the tunnel where the axes of symmetry meet; again, it is an unusual system.
You have referred to our ‘small, poorly documented library of fragment compounds’. As for the poor documentation, the point is that we have very little prior information on the ligands of this new target, other than its substrates. We cast as wide a net as we could within a loosely defined chemical class, using the chemicals we have access to. Unfortunately, I don’t have access to a full fragment library, but am open to collaboration.
As a result of extending the fragments, the ligand efficiency does take a beating… so would it have been better not to mention it? No, that would have been dishonest. In addition, it is not a crucial point at this very early stage in discovery: this is a new target, and it IS important to obtain information on tighter binding, even if it comes at the cost of heavier molecules. In no way do we pretend that these molecules are ripe for application; we have presented the first set of crude inhibitors to ‘provide inspiration for the design of the next generation of inhibitors’ (last sentence of the paper).
Your blog is widely read and highly respected. In this case, it appears that your analysis was inaccurate due to a case of mistaken identity. I did appreciate your calm and rational tone, and hope that you will agree that there is redeeming value to the poor ligand efficiency, because of the inherent novelty of this discovery effort. I am appealing to you to reconsider the blog’s content in light of the above information, and respectfully request that you consider revising it.
Well, as for DHFRs, I'm guilty as charged. The bacterial ones really are way off the mammalian ones - it appears that dihydro/tetrahydrofolate metabolism is a problem that's been solved a number of different ways and (as is often the case) the bacteria show all kinds of diversity compared to the rest of the living world. And there really aren't any good D67 DHFR inhibitors out there, not selective ones, anyway, so a molecule of that type would definitely be a very worthwhile tool (as well as a potential antibiotic lead).
But that brings us to the fragments, the chemical matter in the paper. I'm going to stand my my characterization of the fragment library. 100 members is indeed small, and claiming lack of access to a "full fragment collection" doesn't quite cover it. Because of the amount of chemical space that can be covered at these molecular weights, a 200-member library can be significantly more useful than a 100-member one, and so on. (Almost anything is more useful than a 100-member library). There aren't more compounds of fragment size on the shelves at the University of Montreal?
More of a case could be made for libraries this small if they covered chemical space well. Unfortunately, looking over the list of compounds tested (which is indeed in the Supplementary Material), it's not, at first glance, a very good collection. Not at all. There are some serious problems, and in a collection this small, mistakes are magnified. I have to point out, to start with, that compounds #59 and #81 are duplicates, as are compounds #3 and #40, and compounds #7 and #14. (There may be others; I haven't made a complete check).
The collection is heavily biased towards carboxylic acids (which is a problem for several reasons, see below). Nearly half the compounds have a COOH group by my quick count, and it's not a good idea to have any binding motif so heavily represented. I realize that you intentionally biased your screening set, but then, an almost featureless hydrophobic compound like #46 has no business in there. Another problem is that some of the compounds are so small that they're unlikely to be tractable fragment hits - I note succinimide (#102) and propyleneurea (#28) as examples, but there are others. At the other end of the scale, compounds such as the Fmoc derivative #25 are too large (MW 373), and that's not the only offender in the group (nor the only Fmoc derivative). The body of the manuscript mentions the molecular weights of the collections as being from 150 to 250, but there are too many outliers. This isn't a large enough collection for this kind of noise to be in it.
There are a number of reactive compounds in the list, too, and while covalent inhibitors are a very interesting field, this was not mentioned as a focus of your efforts or as a component of the screening set. And even among these, compounds such as carbonyldiimidazole (#26), the isocyanate #82, and disuccinimidylcarbonate (#36) are really pushing it, as far as reactivity and hydrolytic stability. The imine #110 is also very small and likely to have hydrolytic stability problems. Finally, the fragment #101 is HEPES, which is rather odd, since HEPES is the buffer for the enzyme assays. Again, there isn't room for these kinds of mistakes. It's hard for me to imagine that anyone who's ever done fragment screening reviewed this manuscript.
The approach to following up these compounds also still appears inadequate to me. As Dan Erlanson pointed out in a comment to the Practical Fragments post, small carboxylic acids like the ones highlighted are not always legitimate hits. They can, as he says, form aggregates, depending on the assay conditions, and the most straightforward way of testing that is often the addition of a small amount of detergent, if the assay can stand it. The behavior of such compounds is also very pH-dependent, as I've had a chance to see myself on a fragment effort, so you need to make sure that you're as close to physiological conditions as you can get. I actually have seen some of your compounds show up as hits in fragment screening efforts, and they've been sometimes real, sometimes not.
But even if we stipulate that these compounds are actually hits, they need more work than they've been given. The best practice, in most cases when a fragment hit is discovered and confirmed, is to take as many closely related single-atom changes into the assay as possible. Scan a methyl group around the structure, scan a fluoro, make the N-for-C switches - at these molecular weights, these changes can make a big difference, and you may well find an even more ligand-efficient structure to work from.
Now, as for the SAR development that actually was done: I understand the point about the symmetry of the enzyme, and I can see why this led to the idea of making symmetrical dimer-type compounds. But, as you know, this isn't always a good idea. Doing so via flexible alkyl or alkyl ether chains is not a good idea, though, since such compounds will surely pay an entropic penalty in binding.
And here's one of the main things that struck both me and Teddy Z in his post: if the larger compounds were truly taking advantage of the symmetry, their ligand efficiency shouldn't go down. But in this case it does, and steeply. The size of the symmetical inhibitors (and their hydrophobic regions, such as the featureless linking chains, make it unsurprising that this effort found some micromolar activity. Lots of things will no doubt show micromolar activity in such chemical space. The paper notes that it's surprising that the fragment 4c showed no activity when its structural motif was used to build some of the more potent large compounds, but the most likely hypothesis is that this is because the binding modes have nothing to do with each other.
To be fair, compounds 8 and 9 are referred to as "poorly optimized", which is certainly true. But the paper goes on to say that they are starting points to develop potent and selective inhibitors, which they're not. The fragments are starting points, if they're really binding. The large compounds are dead ends. That's why Teddy Z and I have reacted as strongly as we have, because the path this paper takes is (to our eyes) an example of how not to do fragment-based drug discovery.
But still, I have to say that I'm very glad to hear a direct reply to my criticism of this paper. I hope that this exchange has been useful, and that it might be of use for others who read it.