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DBL%20Hendrix%20small.png College chemistry, 1983

Derek Lowe The 2002 Model

Dbl%20new%20portrait%20B%26W.png After 10 years of blogging. . .

Derek Lowe, an Arkansan by birth, got his BA from Hendrix College and his PhD in organic chemistry from Duke before spending time in Germany on a Humboldt Fellowship on his post-doc. He's worked for several major pharmaceutical companies since 1989 on drug discovery projects against schizophrenia, Alzheimer's, diabetes, osteoporosis and other diseases. To contact Derek email him directly: derekb.lowe@gmail.com Twitter: Dereklowe

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September 10, 2009

To What End?

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Posted by Derek

I was looking through my RSS feed of journal articles this morning, and came across this new one in J. Med. Chem.. Now, there's nothing particularly unusual about this work. The authors are exploring a particular subtype of serotonin receptor (5-HT6), using some chemotypes that have been looked at in serotinergic ligands before. They switch the indole to an indene, put in a sulfonamide, change the aminoethyl side chain to a guanidine, and. . .wait a minute.

Guanidine? I thought that the whole point of making a 5-HT6 ligand was to get it into the brain, and guanidines don't have the best reputation for allowing you to do that. (They're not the easiest thing in the world to even get decent oral absorption from, either, come to think of it). So I looked through the paper to see if there were any in vivo numbers, and as far as I can see, there aren't.

Now, that's not necessarily the fault of the paper's authors. They're from an academic med-chem lab in Barcelona, and animal dosing (and animal PK measurements) aren't necessarily easy to get unless you have a dedicated team that does such things. But, still. The industrial medicinal chemist in me looks at these structures, finds them unlikely to ever reach their intended site of action, can find no evidence in the paper's references that anyone else has ever gotten such a guanidine hydrazone into the brain, either, and starts to have if-a-tree-falls-in-the-forest thoughts.

Now, it's true that we learn some more about the receptor itself by finding new ligands for it, and such compounds can be used for in vitro experiments. But it's not like there aren't other 5-HT6 antagonists out there, in several different chemical classes, and that's just from the first page of a PubMed search. Many of these compounds do, in fact, penetrate the brain, because they were developed by industrial groups for whom in vitro experiments are most definitely not an end in themselves.

I don't mean to single out the Barcelona group here. Their work isn't bad, and it looks perfectly reasonable to me. It's just that my years in industry have made me always ask what a particular paper tells me that I didn't know, and what use might some day be made of the results. Readers here will know that I have a weakness for out-there ideas and technologies, so it's not like I have to see an immediate practical application for everything. But I would like to see the hope of one. And for this work, and for a lot of medicinal chemistry that comes out of academic labs, I just don't see it.

Update: it's been pointed out in the comments that there's a value in academic work that doesn't have to be addressed in industry, that is, training the students who do it. That's absolutely right. But at the same time, couldn't people be trained just as well by working on systems that are a bit less dead on arrival?

And no, I'm not trying to make that case that academic labs should make drugs. If they want to try, then come on down. If they don't, that's fine, too - there's a lot of important research to be done in the world that has no immediate practical application. But this sort of paper that I've written about today seems to miss both of these boats simultaneously: it isn't likely to produce a drug, and it doesn't seem to be addressing any other pressing needs that I can see, either.

And yes, I could say the same about my own PhD work. "The world doesn't need another synthesis of a macrolide antibiotic", I told people at the time. "But I do". Does it have to be like that?

Comments (28) + TrackBacks (0) | Category: Academia (vs. Industry) | Drug Assays | Drug Development | The Central Nervous System | The Scientific Literature


COMMENTS

1. Aspirin on September 10, 2009 8:41 AM writes...

Are there transporters that would get a guanidine past the BBB?

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2. JPB on September 10, 2009 9:15 AM writes...

Well, here's a question: Can we point to any good examples (or locations) of medicinal chemistry from an academic lab? I'm sure the answer is yes ...

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3. Petros on September 10, 2009 9:23 AM writes...

Temozolomide is a recent example from an academic lab. Malcolm Stevens group in Birmingham, UK. And that is now a blockbuster (for S-P)

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4. partial agonist on September 10, 2009 9:42 AM writes...

I'm not sure that the academics vs. industry angle is all that relevant. A good academic group or a good industrial group would have considered potential for exposure to the target tissues. A good reviewer would have MADE them do so.

I see blurbs from minor pharma that also leave some gaping holes in logic. Often I feel that they followed up unwisely on a certain screening hit far enough to publish something and have different structure types that are a whole lot better.

It should be up to the journal reviewers to make the authors explore potential deficiencies, so it is as much a statement on the reviewing process as on the research, academic or not.

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5. Sili on September 10, 2009 10:44 AM writes...

Might it be that that particular group specialises in something else and just happens to have a great reaction for sticking guanidines to stuff?

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6. startup on September 10, 2009 11:06 AM writes...

As you must know the real value of academic research is not the results it produces, but what the students learn in the process.

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7. Anonymous on September 10, 2009 11:20 AM writes...

Emtricitabine

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8. Lucifer on September 10, 2009 11:49 AM writes...

Derek,

So tell me, why does pharma spend so much time on me-too drugs and chiral isomers of existing drugs. Since you guys know how to make a therapeutically innovative drug, why not make a couple (even one is not bad).

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9. Hap on September 10, 2009 11:54 AM writes...

But isn't part of (drug)research he process of learning to ask the right questions? If you make something that can't possibly work in a living thing, and don't bother to explain why your molecule's limitations are not relevant or applicable to its activity, what is the point of your article exactly? Someone's students are going to get kicked hard (if they are expecting to know drug research) when they get hit with unpleasant answers to questions they didn't even ask.

Of course, the journal reviewers and editors (again) ought to have known to ask those questions, because it's their job to ask them and not to let up without reasonable answers. On the other hand, if people can publish articles without even a cursory look to see that the articles are printed properly (like, in the appropriate character set), then perhaps asking editors or reviewers to look at the actual chemistry is a bit much.

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10. partial agonist on September 10, 2009 12:30 PM writes...

Lucifer,

Lipitor was a "me-too" drug, 5th or 6th in line. Was it useful?

Who spends any time at all on single isomers of existing drugs except for a tiny fringe company named (for now) Sepracor? Nevermind that even this is not a particularly fruitful strategy anymore, though it once was. Those patent loopholes no longer exist.

As far as making "a couple"... research never stops with the clinical candidate. Just about every drug that made it had many "backups" that probably were better than it was but they lost in the horse race, i.e. the first compound to the clinic did well enough, so managment didn't want to wait a year or two or three for the better one to catch up.

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11. skeptical on September 10, 2009 12:54 PM writes...

Esteve (co-author of the paper) is a spanish small pharma company that collaborates closely with this academic group. Surprisingly enough, they agreed to develop and patent this kind of compounds. Why guanidines? Lack of med chem experience, knowledge of the chemistry of those compounds in the academic group,... Who knows, but everything has to be published in small groups like this one, regardless of the quality of the outcome.

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12. MePenn on September 10, 2009 1:32 PM writes...

Derek,

I think this whole "let's rip on academic work" trend as of late is a little dangerous. You used to be very much a centralist in realizing that both academic and industrial labs play they part.

Here's where I have a problem with going after this particular work. People in academia are so set on "in this past, this was shown not to work," when clearly some of the best finding in sciences have come from unexpected findings. If this is the case, we're going to end up doing the same thing and converge on this boring medium where no creativity is rewarded.

While it's really important to have prior knowledge of the system you are working with, we've learned over and over that some times you have to let go of that knowledge temporarily. This is especially true when dealing with compounds that target the CNS.

These are my two cents. I know people will disagree. I'm not condoning science without a hypothesis. All I'm saying is, when you're talking about a black box like the CNS it is important to keep your mind open to compounds that do not fall into a preconceived notion of prime drug candidates.

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13. Derek Lowe on September 10, 2009 1:42 PM writes...

MePenn, I don't mind science without a hypothesis, either, but that doesn't seem to have been what this was. The paper is actually a fairly cautious step beyond what had already been reported for serotinergic ligands, combining two or three structural features that had been explored in separate series.

As far as I can tell, the authors were in no way trying to say "Hey, we're going to try something new, and let the chips fall where they may". It looks more like "Other people have put guanidines on their 5-HT ligands, never mind that none of those seem to have any animal data associated with them. We've already done an indene-for-indole switch in another series, so we're going to do it here, too".

And that might be OK, if they went on to say "We realize that guanidines don't have a very good track record in brain penetration. So we're going to check that first thing, of course". But they didn't. Nor did they say "We realize that guanidines don't have a very good track record in brain penetration. But we don't care, because these are in vitro tool compounds". Perhaps that's because the world does not, as far as I can see, need more in vitro tool ligands for this receptor subtype - not until someone can show me how the known ones differ, if they do, and how these new ones are yet different from all the rest.

I guess I should address all this in a follow-up post, from the looks of it. . .

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14. Karen on September 10, 2009 3:01 PM writes...

There's also the value in academic research of learning how reactions work, and which reactions work for which groups. You never know how that reaction might be applied in the future. As an industrial chemist, I've found a lot of papers through SciFinder and Beilstein searches that seemed complately impractical in a medchem sense, but something in those papers applied nicely to the work that I was doing. And I'm amazed to see how the "impractical" work I did as a student ends up being applied - once or twice a year I check to see who has referenced my paper, and it's surprising to see what turns up.

Medchem work in industry wouldn't be possible if we couldn't build on work that was done in academia - even if that work seems useless in the short term.

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15. dithii on September 10, 2009 6:57 PM writes...

Not every HT receptor is located in the brain. Maybe they're hoping to target gut receptors without neurological side effects from drugs that go to the brain.

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16. Jose on September 10, 2009 9:43 PM writes...

I think Derek's point in highlighting the academic/industrial divide is the simple fact that "academic medchem" doesn't really have any need to exist. It is not the best way to train students, and beyond that? It should be renamed "dilettante drug discovery" or something. 99% of academic groups have no-where near the collected knowledge (tox, adme, animal husbandry etc etc) necessary to even begin the process in a credible fashion; hell, 90% of biotechs don't either. The structures in the overwhelming majority of academic medchem papers are so horrific it is just painful- they simply are too far removed from biological reality. The slant of going against conventional wisdom has its place, but DD is absurdly difficult without the added surprises this tack will certainly add.

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17. Lucifer on September 10, 2009 9:52 PM writes...

Jose,

and aren't pharma labs discovering innovative drugs everyday... fix your own house before criticizing others, and pharma certainly does not lack the monetary resources to fix it.

But organisations filled with greedy, short-sighted and conservative charlatans can only do so much..

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18. Jose on September 10, 2009 11:52 PM writes...

Lucifer- this is exactly my point. If pharma and big biotech are struggling so mightily with truly massive resources (funding, personnel, experience) it is just absurd to posit that academic groups can do it better. (with the noted exceptions like Dennis Liotta). DD is a staggeringly resource heavy enterprise.

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19. David on September 11, 2009 1:32 AM writes...

Does anyone know why the Aetiology blog has suddenly gone silent. The blog seemed to stop in June.

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20. DCRogers on September 11, 2009 1:45 AM writes...

Maybe this compound was published because is was not a good drug candidate, and the real candidates kept private?

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21. BigSky on September 11, 2009 6:28 PM writes...

As an academic re-entrant from biotech and Pharma I can see valid points in several of the posts above. I'm realizing that the skill level amoung grad students, postdocs and career-long faculty is amazing low and very peculiar. However, Pharma didn't do much better when I was there. Marketing driven mandates on research outcomes pretty much choked innovation and the skill set that led to advancement (and a seat at the table for decisions) was not a shared set with scientific and analytic experience or thought.

It's the systems we've got but we should all fight hard against the wider adoption of silly/stupid regardless of where we encounter it.

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22. Cassius on September 11, 2009 11:48 PM writes...

A comment and a question:

There has to be SOME semi-stable hydrolyzable group one can put on a guanidine to get at least slight BBB penetration. And if the drug is potent enough, maybe you only need to get a low percentage of the prodrug to cross.

If academic med chem is so poor, why do I never hear anyone from big pharma pointing us academics in the right direction? It's always "your work is crap, give up". I just started at an academic med chem facility, and I want to do it right, but still serve the academics (mainly biologists) that need my help. Give me some direction that does not include "make these 4000 compounds and then evaluate your program".

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23. Jack on September 12, 2009 10:56 AM writes...

Guanidine?

Derek's comments on guanidine are valid. Remember over a decade ago, every issue of JMC had an article on Factor Xa inhibitors with the guanidine group? None of them were really bioavailable. Here is a thought, guanidines' lack of bioavailability stems from its basicity. What if we oxidize it to N-oxide to remove its basicity? Just a thought.

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24. milkshake on September 12, 2009 3:02 PM writes...

#23 previous commenter: most of these (Xa, VIIa inhibitors) were actually amidines - they all share the same problem.

Hydroxyamidine pro-drugs are known, they occasionally work but the conversion to active drug is pretty capricious. Generally, if you are introducing amidine into your molecule you need to drastically simplify and remove most other polar groups, if you hope for oral absorption. There are no generally-useful ways to pro-drug the amidine group, AFAIK.

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25. SynChem on September 12, 2009 3:35 PM writes...

Derek,

I could not disagree any more with your statement "The world doesn't need another synthesis of a macrolide antibiotic". Whether there is none or a million published syntheses of a NP is completely irrelevant. The sky is still the limit when it comes to the potential of improving just about any NP synthesis. Number of steps, overall yield, selectivity issues, you name it. Just look at the progress made in the past 20 years or so. Total synthesis is the ideal platform for inventing new methods and strategies that actually solve real problems.


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26. Ed on September 14, 2009 8:03 AM writes...

Cassius, some "academic" med chem is good - but mostly it is done in large, dedicated institutes and centres where there is sufficient critical mass and expertise to do what us Pharma types might consider as "real" med chem/drug discovery.

If you work in a smaller college, maybe look into doing similar stuff to what Terrence Burke has been doing on SH2 domains - a lot of protein-protein interaction type stuff (that pharma typically doesn't want to touch because the probability of success is very low). Or look at doing "old" things in new ways (such as Merck allosteric AKT inhibitors). Follow med chem principles - a big problem is the oversized nature of protein-protein interaction inihibitors - for example is it possible to design hybrid molecules to target active transport mechanisms to overcome poor permeability whilst retaining activity at a primary target?

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27. Cassius on September 14, 2009 9:20 PM writes...

Ed, thanks for the tips! I understand the argument for lack of expertise in academia. I came straight out of my postdoc and worked in biotech for a little over a year before starting at this med chem facility and I am essentially the director.... so case in point. But I'm finding that many research groups on campus have been looking for someone like me. And I want to become a solid medicinal chemist.

I like your example of protein-protein interactions. Indeed some of our current projects are targeting these interactions. Although I basically take what comes my way and do not have control over much other than the chemistry, it is good to hear what may actually succeed in academia. Your question about whether "tagging" an active compound with a moiety that targets a transport protein is certainly a good one.

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28. MadChem on November 3, 2009 11:38 PM writes...

It is pretty hard to get academia to do serious medchem research because 1) PhD students and postdocs don't hang around for long and 2) good funding is hard to come by. And because of the publish-or-perish mentality, we're kind of force to publish half-decent work. I'm guilty of this myself. But I do hope there is a level of tolerance for this sort of work anyway because you just might get something useful out of it in the long run.

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