A reader sent along this paper that's come out recently in JACS, from a Michigan/South Korea/UCSB team of researchers. It's directed towards a possible therapeutic agent for Alzheimer's disease. They're attempting to build a molecule that binds beta-amyloid, coordinates metals, and has antioxidant properties all at the same time.
An uncharitable view would be that they have also taken aim at the year 1995, which is about when all three of these ideas were also being worked on for AD. But it's not like the field has cleared up too many of these questions since then, so perhaps that gets a pass, although it should be noted (but isn't in the paper) that no one has ever been able to find any significant effect on Alzheimer's from treatment with either antioxidants or metal chelators. The debate on whether anyone has been able to see anything significant with agents targeting amyloid is still going on (and how).
I bring that up partly for mechanistic plausibility, and partly because of the all-in-one aspect of the molecule that the paper is studying. Any such drug candidate has to justify its existence versus a mixture of therapies given simultaneously, especially since the odds are that it will not be as efficacious against all (or even any) of its subtargets compared to a cocktail of more specific agents. With Alzheimer's, it's tempting to say that well, we're hitting all three of these mechanisms at once, so that has to be a good thing. But are all three of them equally important? The fraction of your compound that's binding amyloid is presumably not available to serve as an antioxidant. The ones that have chelated metals are not available to bind amyloid, and so on.
Most of the paper details experiments to show that the ligand does indeed bind amyloid, both in the soluble form and as fibrils. But there's room to argue there, too. Some in the field think that altering the distribution between those populations could be important (I'm agnostic on this point, as I am about amyloid in general). If you're binding to all of them, though, what happens? There's information on the compound's effect on amyloid oligomerization, but the connection between that and Alzheimer's pathology is also up for argument. These questions, already complicated, are made harder to think about by the absence of any quantitative binding data in the paper - at least, if it's there, I'm not seeing it yet. There are mass spec, LC, and NMR experiments, but no binding constants.
There's also little or no SAR. You'd almost get the impression that this was the first and only compound made and tested, because there's nothing in the main body of the paper about any analogs, other than a comparison to a single quinolinemethanol. Even without binding data, some qualitative comparisons might have been made to see how the amyloid binding responded to changes in the structure, as well as how it balanced with the metal-binding and antioxidant properties.
There's some cell-assay data, viability in the presence of amyloid (with and without metals), and it looks like under A-beta-42 conditions the cells are about 70% viable without the compound, and around 90% with it. (It also looks like the cell viability is only in the lower 80% range just when the compound alone is added; I don't know what the background viability numbers are, because that control doesn't seem to be in there). They also tried the same neuroblastoma line with the Swedish-mutation APP in it (a huge risk factor for an early-onset form of human Alzheimer's), but I can't see much difference in the compound's effects.
But as with any CNS proposal, the big question is "Does the compound get into the brain?" The authors, to their credit, do have some data here, but it's puzzlingly incomplete. They show plasma and brain levels after oral gavage (10 mpk) in CD1 mice, but only at one time point, five minutes. That seems mighty early for an oral dose, at least to me, and you really, really want to see a curve here rather than one early time point. For what it's worth, plasma levels were around 6 ng/g and brain levels were around 14 ng/g at that point, but since this was just done by brain homogenate, it's unclear if the compound really gets in or not. No other tissues were examined.
There also don't seem to be any data on what else this compound might do. If you're seriously proposing it as a possible therapy for Alzheimer's, or as a starting point for one, it would be worthwhile to collect some numbers in selectivity screens. Alternatively, if you're not proposing this as a starting point for Alzheimer's therapy, then why do all this work in the first place (and why write it up for JACS)? This is another one of those cases where I'm honestly baffled by what I'm reading. My industrial perspective sees a single compound given a very labor-intensive in vitro workup on a hazy therapeutic rationale, with no analogs, no selectivity data, and no PK other than one time point, and I just shrug my shoulders with a puzzled look on my face. Why do it?
Well, universities aren't drug companies. And the groups involved are, presumably, not focused on making the next big Alzheimer's breakthrough. But what are they focused on? Training students? That's a really worthwhile goal, but I have to wonder if some way could have been found to train them that would have been a bit more congruent with the real world. Picking three rationales, thinking up a single compound to try to combine them, and then spending all your effort on it as if it's a real lead isn't (to my mind) a good fit. I realize that resources are limited, and that this same level of effort just couldn't have been applied to a whole series of compounds the way it would in an industrial setting (not that we'd have done it). But if you're going to do this stuff, a less-intense look at the amyloid-aggregating and cellular effects of a wider series of compounds could have been more valuable than a lot of information about just one.
I feel bad every time I write like this about academic drug-discovery papers, but I can't help it. From my perspective, there's a lot of confusion out there about what drug discovery really entails, and about the relative value of doing a little of it, or doing it in an odd way.