I mentioned phosphatase inhibitors while talking about okadaic acid the other day, and that brings me to a paper from the journal ChemBioChem (6, 1749) that I was recently reading. It's a collaboration from six German academic groups, led by one at the Max Planck Institute for Molecular Physiology in Dortmund. And there are some things about it that just don't seem to make much sense.
On the surface, everything's fine. They're investigating some cyclic peptide derviatives called stevastelins, which are microbial natural products known to show some phosphatase inhibitor activity. They produced some synthetic analogs of the natural products and ran them against several phosphatases of interest. They then turned around and did the same thing with some analogs of two more phosphatase-inhibiting natural products, roseophilin and prodigiosin. (For those of you who've done some bacteriology, that first compound is responsible for the red color of Serratia marcesens colonies).
Then the paper makes a sharp turn, as they move on to a 20,000 compound library that's been assembled by a German academic team. They screened this against their panel of phosphatase enzymes, and came up with 8 or 10 pyrrolobenzoic acid structures that showed some inhibitory activity. End of paper.
Well, the way I've presented this, it sounds like a fairly reasonable paper, if a bit of a hodgepodge. But it's the way everything's presented that makes me wonder. For example, their first group of stevastelin analogs is (for the most part) inactive against the five phosphatases they assayed. One of them hits the Cdc25a enzyme, one of them hits PTP1B, and one of them is active against MptpA, all of which are legitimate drug targets. But these compounds are all around 10 to 15 micromolar, which potency doesn't exactly make me leap up out of my chair.
But the authors refer to this as "pronounced selectivity for individual phosphatases". If you read the fine print, the "not active" values are compounds that were 30 micromolar and worse, so we could easily be looking at just two- or three-fold selectivity here. That is not my definition of "pronounced". Add that to the very weak potency, and you have results that I would toss if I saw them come out of a screening run. As a medicinal chemist, I'd start to get really interested at about a hundred times the potency of these compounds, and I'd be willing to bet that by that time the selectivity, if it's really there, would be long gone.
Their other natural product analogs are similar - one's as good as 3 micromolar against PTP1B, but others start to hit the 30 micromolar ceiling of the assay again. Even the active compound has a very unappealing chemical structure, which would only be developed by a desperate drug company indeed. (I particularly enjoy one of them that's reported against MptpA as "28.7 +/- 9.7" micromolar).
What's also irritating is the statement the authors make to justify all this: "We have previously forwarded the notion that biologically active natural products should be regarded as evolutionarily selected and biologically prevalidated starting points for inhibitor development." I'm glad they brought that up, since drug development from natural products has only been a popular technique for a century or so. The problem, as they're demonstrating here, is that if these compounds really are evolutionarily selected as phosphatase inhibitors, and the last hundred million years have only given you micromolar potency, then the odds of being able to push that lower by making half a dozen analogs are rather slim.
And that brings us to their screening efforts. Their compound library is "selected due to their diverse representation of reportedly bioactive scaffold elements". But 20,000 small molecules, however carefully selected, is not a very large collection. And when you get down to it, our compound collections in the drug industry are also supposed to represent a lot of reportedly bioactive scaffolds, and most of them are a couple of orders of magnitude larger.
The compounds from the screen are all micromolar. One of them looks a bit interesting, and possibly selective between the two kinases they ran it against. (What happened to the other enzymes by this point in the paper, I wonder?) I wouldn't want to try to develop these guys, but with the application of a lot of time, money, and effort, you might be able to get somewhere. Or you might wipe out within six months, which is how a lot of projects go, even the ones with better starting points than this, which is most of them.
Ah, but the authors are more optimistic than I am, because (I suspect) they haven't actually tried to do any drug development. "Further application of medicinal chemistry methodologies should allow for the development of more potent inhibitors for subsequent biological investigations in iterative cycles", they say. Oh, yes. Shouldn't it always?
Why am I going on at this length? Because I think that this paper illustrates a general problem: many academic labs do not understand what drug discovery entails, and (worse) they don't realize that they don't understand. The attitude shown here - presenting a few micromolar compounds as fine lead compounds and saying that med-chem should be able to sort things out - would actually be a good way to get fired at most companies. If this paper's data were somehow presented to me as a rationale for starting a project, I would create a distraction and dive for the door. No, there's still a long way to go.