About this Author
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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November 5, 2009
Posted by Derek
Resveratrol's a mighty interesting compound. It seems to extend lifespan in yeast and various lower organisms, and has a wide range of effects in mice. Famously, GlaxoSmithKline has expensively bought out Sirtris, a company whose entire research program started with resveratrol and similar compound that modulate the SIRT1 pathway.
But does it really do that? The picture just got even more complicated. A group at Amgen has published a paper saying that when you look closely, resveratrol doesn't directly affect SIRT1 at all. Interestingly, this conclusion has been reached before (by a group at the University of Washington), and both teams conclude that the problem is the fluorescent peptide substrate commonly used in sirtuin assays. With the fluorescent group attached, everything looks fine - but when you go to the extra trouble of reading things out without the fluorescent tag, you find that resveratrol doesn't seem to make SIRT1 do anything to what are supposed to be its natural substrates.
"The claim of resvertraol being a SIRT1 activator is likely to be an experimental artifact of the SIRT1 assay that employs the Fluor de Lys-SIRT1 peptide as a substrate. However, the beneficial metabolic effects of resveratrol have been clearly demonstrated in diabetic animal models. Our data do not support the notion that these metabolic effects are mediated by direct SIRT1 activation. Rather, they could be mediated by other mechanisms. . ."
They suggest activation of AMPK (an important regulatory kinase that's tied in with SIRT1) as one such mechanism, but admit that they have no idea how resveratrol might activate it. Does that process still require SIRT1 at all? Who knows? One thing I think I do know is that this has something to do with this Amgen paper from 2008 on new high-throughput assays for sirtuin enzymes.
One wonders what assay formats Sirtris has been using to evaluate their new compounds, and one also wonders what they make of all this now at GSK. Does one not? We can be sure, though, that there are plenty of important things that we don't know yet about sirtuins and the compounds that affect them. It's going to be quite a ride as we find them out, too.
Comments (26)
+ TrackBacks (0) | Category: Aging and Lifespan | Biological News | Drug Assays
September 10, 2009
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
August 11, 2009
Posted by Derek
I was looking over a paper in PNAS, where a group at Stanford describes finding several small molecules that inhibit Hedgehog signaling. That's a very interesting (and ferociously complex) area, and the more tools that are available to study it, the better.
But let me throw something out to those who have read (or will read) the paper. (Here's the PDF, which is open access). The researchers seem to have done a screen against about 125,000 compounds, and come up with four single-digit micromolar hits. Characterizing these against a list of downstream assays showed that each of these acts in a somewhat different manner on the Hedgehog pathway.
And that's fine - the original screen would have picked up a variety of mechanisms, and there certainly are a variety out there to be picked up. I can believe that a list of compounds would differentiate on closer inspection. What I keep looking for, though, is (first) a mention that these compounds were run through some sort of general screening panel for other enzyme and/or receptor activities. They did look for three different kinase activities that had been shown to interfere (and didn't see them), but I'd feel much better about using some new structures as probes if I'd run them through a big panel of secondary assays first.
Second, I've been looking for some indication that there might have been some structure-activity relationships observed. I assume that each of these compounds might well have been part of a series - so how did the related structures fare? Having a one-off compound doesn't negate the data, naturally, although it certainly does make it harder to build anything from the hit you've found. But SAR is another factor that I'd immediately look for after a screen, and it seems strange to me that I can't find any mention of it.
Have I missed these things, or are they just not there? If they aren't, is that a big deal, or not? Thoughts?
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+ TrackBacks (0) | Category: Biological News | Drug Assays
July 17, 2009
Posted by Derek
I seem to have been putting a lot of graphics up this week, so here's another one. This is borrowed from a recent Science paper on the future of natural-products based drug discovery. It's interesting both from that viewpoint, and because of the general approval numbers:
And there you have it. Outside of anomalies like 2005, we can say, I think, that the 1980s were a comparative Golden Age of Drug Approvals, that the 1990s held their own but did not reach the earlier heights, and that since 2000 the trend has been dire. If you want some numbers to confirm your intuitions, you can just refer back to this.
As far as natural products go, from what I can see, the percentage of drugs derived from them has remained roughly constant: about half. Looking at the current clinical trial environment, though, the authors see this as likely to decline, and wonder if this is justified or not. They blame two broad factors, one of them being the prevailing drug discovery culture:
The double-digit yearly sales growth that drug companies typically enjoyed until about 10 years ago has led to unrealistically high expectations by their shareholders and great pressure to produce "blockbuster drugs" with more than $1 billion in annual sales (3). In the blockbuster model, a few drugs make the bulk of the profit. For example, eight products accounted for 58% of Pfizer’s annual worldwide sales of $44 billion in 2007.
As an aside, I understand the problems with swinging for the fences all the time, but I don't see the Pfizer situation above as anything anomalous. That's a power-law distribution, and sales figures are exactly where you'd expect to see such a thing. A large drug company with its revenues evenly divided out among a group of compounds would be the exception, wouldn't it?
The other factor that they say has been holding things back is the difficulty of screening and working with many natural products, especially now that we've found many of the obvious candidates. A lot of hits from cultures and extracts are due to compounds that you already know about. The authors suggest that new screening approaches could get around this problem, as well as extending the hunt to organisms that don't respond well to traditional culture techniques.
None of these sound like they're going to fix things in the near term, but I don't think that the industry as a whole has any near-term fixes. But since the same techniques used to isolate and work with tricky natural product structures will be able to help out in other areas, too, I wish the people working on them luck.
Comments (10)
+ TrackBacks (0) | Category: Business and Markets | Drug Assays | Drug Development | Drug Industry History
July 15, 2009
Posted by Derek
I've been meaning to get around to a very interesting paper from the Shoichet group that came out a month or so ago in Nature Chemical Biology. Today's the day! It examines the content of screening libraries and compares them to what natural products generally look like, and they turn up some surprising things along the way. The main question they're trying to answer is: given the huge numbers of possible compounds, and the relatively tiny fraction of those we can screen, why does high-throughput screening even work at all?
The first data set they consider is the Generated Database (GDB), a calculated set of all the reasonable structures with 11 or fewer nonhydrogen atoms, which grew out of this work. Neglecting stereochemistry, that gives you between 26 and 27 million compounds. Once you're past the assumptions of the enumeration (which certainly seem defensible - no multiheteroatom single-bond chains, no gem-diols, no acid chlorides, etc.), then there are no human bias involved: that's the list.
The second list is everything from the Dictionary of Natural Products and all the metabolites and natural products from the Kyoto Encyclopedia of Genes and Genomes. That gives you 140,000+ compounds. And the final list is the ZINC database of over 9 million commercially available compounds, which (as they point out) is a pretty good proxy for a lot of screening collections as well.
One rather disturbing statistic comes out early when you start looking at overlaps between these data sets. For example, how many of the possible GDB structures are commercially available? The answer: 25,810 of them - in other words, you can only buy fewer than 0.01% of the possible compounds with 11 heavy atoms or below, making the "purchasable GDB" a paltry list indeed.
Now, what happens when you compare that list of natural products to these other data sets? Well, for one thing, the purchasable part of the GDB turns out to be much more similar to the natural product list than the full set. Everything in the GDB has at least 20% Tanimoto similarity to at least one compound in the natural products set, not that 20% means much of anything in that scoring system. But only 1% of the GDB has a 40% Tanimoto similarity, and less than 0.005% has an 80% Tanimoto similarity. That's a pretty steep dropoff!
But the "purchasable GDB" holds up much better. 10% of that list has 100% Tanimoto similarity (that is, 10% of the purchasable compounds are natural products themselves). The authors also compare individual commercial screening collections. If you're interested, ChemBridge and Asinex are the least natural-product-rich (about 5% of their collections), whereas IBS and Otava are the most (about 10%).
So one answer to "why does HTS ever work for anything" is that compound collections seem to be biased toward natural-product type structures, which we can reasonably assume have generally evolved to have some sort of biological activity. It would be most interesting to see the results of such an analysis run from inside several drug companies against their own compound collections. My guess is that the natural product similarities would be even higher than the "purchasable GDB" set's, because drug company collections have been deliberately stocked with structural series that have shown activity in one project or another.
That's certainly looking at things from a different perspective, because you can also hear a lot of talk about how our compound files are too ugly - too flat, too hydrophobic, not natural-product-like enough. These viewpoints aren't contradictory, though - if Shoichet is right, then improving those similarities would indeed lead to higher hit rates. Compared to everything else, we're already at the top of the similarity list, but in absolute terms there's still a lot of room for improvement.
So how would one go about changing this, assuming that one buys into this set of assumptions? The authors have searched through the various databases for ring structures, taking those as a good proxy for structural scaffolds. As it turns out 83% of the ring scaffolds among the natural products are unrepresented among the commercially available molecules - a result that I assume that Asinex, ChemBridge, Life Chemicals, Otava, Bionet and their ilk are noting with great interest. In fact, the authors go even further in pointing out opportunities, with a table of rings from this group that closely resemble known drug-like ring systems.
But wait a minute. . .when you look at those scaffolds, a number of them turn out to be rather, well, homely. I'd be worried about elimination to form a Michael acceptor in compound 19, for example. I'm not crazy about the N,S acetal in 21 or the overall stability of the acetals in 15, 17 and 31. The propiolactone in 23 is surely reactive, as is the quinone in 25, and I'd be very surprised if that's not what they owe their biological activities to. And so on.
All that said, there are still some structures in there that I'd be willing to check out, and there must be more of them in that 83%. No doubt a number of the rings that do sneak into the commercial list are not very well elaborated, either. I think that there is a real commercial opportunity here. A company could do quite well for itself by promoting its compound collection as being more natural-product similar than the competition, with tractable molecules, and a huge number of them unrepresented in any other catalog.
Now all you'd have to do is make these things. . .which would require hiring synthetic organic chemists, and plenty of them. These things aren't easy to make, or to work with. And as it so happens, there are quite a few good ones available these days. Anyone want to take this business model to heart?
Comments (12)
+ TrackBacks (0) | Category: Drug Assays | Drug Industry History | In Silico
June 29, 2009
Posted by Derek
Not long ago, I wrote about a Pfizer program for smaller companies to come screen their targets against Pfizer's compound bank. Now Eli Lilly has flipped that around. In an initiative to bring other people's compounds out of the stockrooms and off the shelves, they'll screen them for free.
These aren't single-target assays. The company has four phenotypic screens going (for Alzheimer's, diabetes, cancer, and osteoporosis) and will look for improvement by any mechanism that comes to hand. No chemical structure information is shown to Lilly (I assume that they just know the molecular weight so they can run a dilution series). If something looks interesting, the company and the owners of the chemical matter have 120 days to come to terms for any further development deal - if not, then all rights revert to the submitter, and they can publish the data from the screens.
Lilly's working out a universal material transfer agreement, in collaboration with a number of universities, so that the paperwork stays the same every time. That's a good move. The lawyering can be a real holdup - in my experience, every party in these agreements usually comes in with slightly different wording in their magic legal spells, requiring several rounds of reconciliation before everyone's ready to sign.
I think that this is a worthwhile idea, and that they'll get a lot of takers. There are plenty of compounds sitting around in academic labs gathering dust, so why not send 'em in? The worst that can happen is nothing, and the best is that the compound actually turns out to be worth something. But will anything come out of it? The closest program to this is surely the National Cancer Institute's long-standing (since 1990) NCI-60 screening program, which also runs at no cost to the submitters. Even so, a recent reference mentions that there are between 40,000 and 50,000 compound in the NCI database, which actually seems rather small, considering. (To be fair, the program is not being funded at the levels that it was during the early 1990s). The only marketed compound that I'm aware of that can be said to have come out of the NCI-60 screen is Velcade (bortezomib), known then as PS-341, which was sent in for screening by Proscript Pharmaceuticals in the mid-1990s. Many other interesting structures have turned up along the way, though, which for various reasons haven't made it all the way through.
It'll be quite interesting to see what sort of hit rate Lilly's phenotypic assays call up - I hope they tell us. I have a lot of sympathy for the mechanism-agnostic approach myself, and I'd like to see how closely my bias are aligned to reality.
Comments (18)
+ TrackBacks (0) | Category: Drug Assays | Drug Development
June 19, 2009
Posted by Derek
After yesterday's post on pathway patents, I figured that I should talk about high-throughput screening in academia. I realize that there are some serious endeavors going on, some of them staffed by ex-industry people. So I don't mean to come across as thinking that academic screening is useless, because it certainly isn't.
What is probably is useless for is enabling a hugely broad patent application like the one Ariad licensed. But the problem with screening for such cases isn't that the effort would come from academic researchers, because industry couldn't do it, either: Merck, Pfizer, GSK and Novartis working together probably couldn't have sufficiently enabled that Ariad patent; it's a monster.
It's true that the compound collections available to all but the very largest academic efforts don't compare in size to what's out there in the drug companies. My point yesterday was that since we can screen those big collections and still come up empty against unusual new targets (again and again), that smaller compound sets are probably at even more of a disadvantage. Chemical space is very, very large. The total number of tractable compounds ever made (so far) is still not a sufficiently large screening collection for some targets. That's been an unpleasant lesson to learn, but I think that it's the truth.
That said, I'm going to start sounding like the pointy-haired boss from Dilbert and say "Screen smarter, not harder". I think that fragment-based approaches are one example of this. Much smaller collections can yield real starting points if you look at the hits in terms of ligand efficiency and let them lead you into new chemical spaces. I think that this is a better use of time, in many cases, than the diversity-oriented synthesis approach, which (as I understand it) tries to fill in those new spaces first and screen second. I don't mind some of the DOS work, because some of it's interesting chemistry, and hey, new molecules are new molecules. But we could all make new molecules for the rest of our lives and still not color in much of the map. Screening collections should be made interesting and diverse, but you have to do a cost/benefit analysis of your approach to that.
I'm more than willing to be proven wrong about this, but I keep thinking that brute force is not going to be the answer to getting hits against the kinds of targets that we're having to think about these days - enzyme classes that haven't yielded anything yet, protein-protein interactions, protein-nucleic acid interactions, and other squirrely stuff. If the modelers can help with these things, then great (although as I understand it, they generally can have a rough time with the DNA and RNA targets). If the solution is to work up from fragments, cranking out the X-ray and NMR structural data as the molecules get larger, then that's fine, too. And if it means that chemists just need to turn around and generate fast targeted libraries around the few real hits that emerge, a more selective use of brute force, then I have no problem with that, either. We're going to need all the help we can get.
Comments (25)
+ TrackBacks (0) | Category: Academia (vs. Industry) | Drug Assays | Drug Development
May 19, 2009
Posted by Derek
I've heard that Pfizer is doing something unusual with its proprietary compound collection: they're offering to let other people screen it.
Now, that's quite a step. Most companies guard their compounds pretty closely, considering them to be key assets. But I'm told that Pfizer has been meeting with several other (mostly smaller) companies, offering their (entire?) compound library as a screening resource. As I understand it, you need to come to them with a reasonably formatted HTS assay, and there's a fee in the high hundreds of thousands to run the screen.
That doesn't seem like much of a moneymaker, to be honest. The whole thing appears to me to be a way for Pfizer to strike deals with a number of other companies, since the compounds that come out of the screen will (likely as not) be covered by Pfizer's own patents. I haven't heard of how the IP issues are to be worked out in these deals, but that's the first thing that occurs to me. Anyone have more details?
Comments (17)
+ TrackBacks (0) | Category: Drug Assays
April 29, 2009
Posted by Derek
What a mess! Science has a retraction of a 2005 paper, which is always a nasty enough business, but in this case, the authors can’t agree on whether it should be retracted or not. And no one seems to be able to agree on whether the original results were real, and (even if they weren’t) whether the technique the paper describes works anyway. Well.
The original paper (free full text), from two Korean research groups, described a drug target discovery technique with the acronym MAGIC (MAGnetism-based Interaction Capture). It’s a fairly straightforward idea in principle: coat a magnetic nanoparticle with a molecule whose target(s) you’re trying to identify. Now take cell lines whose proteins have had various fluorescent tags put on them, and get the nanoparticles into them. If you then apply a strong magnetic field to the cells, the magnetic particles will be pulled around, and they’ll drag along whichever proteins have associated with your bait molecule. Watch the process under a microscope, and see which fluorescent spots move in which cells.
Papers were published (in both Science and Nature Chemical Biology), patent applications were filed (well, not in that order!), startup money was raised for a company to be called CGK. . .and then troubles began. Word was that the technique wasn’t reproducible. One of the authors (Yong-Weon Yi) asked that his name be removed from the publications, which was rather problematic of him, considering that he was also an inventor on the patent application. Early last year, investigations by the Korean Advanced Institute of Science and Technology came to the disturbing conclusion that the papers “do not contain any scientific truth”, and the journals flagged them.
The Nature Chemical Biology paper was retracted last July, but the Science paper has been a real rugby scrum, as the journal details here. The editorial staff seems to have been unable to reach one of the authors (Neoncheol Jung), and they still don’t know where he is. That’s disconcerting, since he’s still listed as the founding CEO of CGK. A complex legal struggle has erupted between the company and the KAIST about who has commercial rights to the technology, which surely isn’t being helped along by the fact that everyone is disagreeing about whether it works at all, or ever has. Science says that they’ve received parts of the KAIST report, which states that the authors couldn’t produce any notebooks or original data to support any of the experiments in the paper. This is Most Ungood, of course, and on top of that, two of the authors also appear to have stated that the key experiments (where they moved the fluorescent proteins around) were not carried out as the paper says. Meanwhile, everyone involved is now suing everyone else back in Korea for fraud, for defamation, and who knows. The target date for all this to be resolved is somewhere around the crack of doom.
Emerging from the fiery crater, CGK came up with another (very closely related) technique, which they published late last year in JACS. (If nothing else, everyone involved is certainly getting their work into an impressive list of journals. If only the papers wouldn’t keep sliding right back out. . .) That one has stood up so far, but it’s only April. I presume that the editorial staff at JACS asked for all kinds of data in support, but (as this whole affair shows) you can’t necessarily assume that everyone’s doing the job they’re supposed to do.
The new paper, most interestingly, does not reference the previous work at all, which I suppose makes sense on one level. But if you just came across it de novo, you wouldn't realize that people (at the same company!) had already been (supposedly) working on magnetic particle assays in living cells. Looking over this one and comparing it to the original Science paper, one of the biggest differences seems to be how the magnetic particles are made to expose themselves to the cytoplasm. The earlier work mentioned coating the particles with a fusogenic protein (TAT-HA2) that was claimed to help with this process; that step is nowhere to be found in the JACS work. Otherwise, the process looks pretty much identical to me.
Let’s come up for air, then, and ask how well useful these ideas could be, stipulating (deep breath) that they work. Clearly, there’s some utility here. But I have to wonder how useful this protocol will be for general target fishing expeditions. Fluorescent labeling of proteins is indeed one of the wonders of the world (and was the subject of a recent a well-deserved Nobel prize). But not all proteins can be labeled without disturbing their function – and if you don’t know what the protein’s up to in the first place, you’re never sure if you’ve done something to perturb it when you add the glowing parts. There are also a lot of proteins, of course, to put it mildly, and if you don’t have any idea of where to start looking for targets, you still have a major amount of work to do. The cleanest use I can think of for these experiments is verifying (or ruling out) hypotheses for individual proteins.
But that's if it works. And at this point, who knows? I'll be very interested to follow this story, and to see if anyone else picks up this technique and gets it to work. Who's brave enough?
Comments (9)
+ TrackBacks (0) | Category: Biological News | Drug Assays | The Dark Side | The Scientific Literature
March 13, 2009
Posted by Derek
A few readers have told me that I’m being too hard on antibacterial drug discovery, at least on target-based efforts in the field. The other day I asked if anyone could name a single antibacterial drug on the market that had been developed from a target, rather than by screening or modification of existing drugs and natural products, and the consensus was that there’s nothing to point to yet.
The objections are that antibacterials are an old field, and that for many years these natural products (and variations thereof) were pretty much all that anyone needed. Even when target-based drug discovery got going in earnest (gathering momentum from the 1970s through the 1980s), the antibacterial field was in general thought to be pretty well taken care of, so correspondingly less effort was put into it. Even now, there’s still a lot of potential in modifying older compounds to evade resistance, which is not something that a lot of other drug discovery areas have the option of doing.
And I have to say, these points have something to them. It’s true that antibacterials are something of a world apart; this was the first field of modern pharmaceutical discovery, and the struggle against living, adapting organisms makes it different than most other therapeutic areas even today. The lack of target-driven successes is surely due in part to historical factors. (The relative success of the later-blooming antiviral therapeutic targets is evidence in favor of this, too).
That said, I think that it’s not generally realized how few target-based drugs there are in the field (approximately none), so I did want to highlight that. And it does seem to be the case that working up from targets in the area is a hard row to hoe. There’s a rather disturbing review from GlaxoSmithKline that makes that case:
"From the 70 HTS campaigns run between 1995–2001 (67 target based, 3 whole cell), only 5 leads were delivered, so that, on average, it took 14 HTS runs to discover one lead. Based on GSK screening metrics, the success rate from antibacterial HTS was four- to five-fold lower than for targets from other therapeutic areas at this time. To be sure, this was a disappointing and financially unsustainable outcome, especially in view of the length of time devoted to this experiment and considering that costs per HTS campaign were around US$1 million. Furthermore, multiple high-quality leads are needed given the attrition involved in the lead optimization and clinical development processes required to create a novel antibiotic.
GSK was not the only company that had difficulty finding antibacterial leads from HTS. A review of the literature between 1996 and 2004 shows that >125 antibacterial screens on 60 different antibacterial targets were run by 34 different companies25. That none of these screens resulted in credible development candidates is clear from the lack of novel mechanism molecules in the industrial antibacterial pipeline. We are only aware of two compounds targeting a novel antibacterial enzyme (PDF) that have actually progressed as far as Phase I clinical trials, and technically speaking PDF was identified as an antibacterial target well before the genome era."
So although the history is a mitigating factor, the field does seem to have its. . .special character. The GSK authors discuss some of the possible reasons for this, but those can be the topic of another post or two; they're worth it.
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+ TrackBacks (0) | Category: Drug Assays | Drug Industry History | Infectious Diseases
March 6, 2009
Posted by Derek
There are a huge number of techniques in the protein world that relay on tying down some binding partner onto some kind of solid support. When you’re talking about immobilizing proteins, that’s one thing – they’re large beasts, and presumably there’s some tether that can be bonded to them to string off to a solid bead or chip. It’s certainly not always easy, but generally can be done, often after some experimentation with the length of the linker, its composition, and the chemistry used to attach it.
But there are also plenty of ideas out there that call for doing the same sort of thing to small molecules. The first thing that comes to mind is affinity chromatography – take some small molecule that you know binds to a given protein or class of proteins well, attach it to some solid resin or the like, and then pour a bunch of mixed proteins over it. In theory, the binding partner will stick to its ligand as it finds it, everything else will wash off, and now you’ve got pure protein (or a pure group of related proteins) isolated and ready to be analyzed. Well, maybe after you find a way to get them off the solid support as well.
That illustrates one experimental consideration with these ideas. You want the association between the binding partners to be strong enough to be useful, but (in many cases) not so incredibly strong that it can never be broken up again. There are a lot of biomolecule purification methods that rely on just these sorts of interactions, but those often use some well-worked-out binding pair that you introduce into the proteins artificially. Doing it on native proteins, with small molecules that you just dreamed up, is quite another thing.
But that would be very useful indeed, if you could get it work reliably. There are techniques available like surface plasmon resonance, which can tell with great sensitivity if something is sticking close to a solid surface. At least one whole company (Graffinity) has been trying to make a living by (among other things) attaching screening libraries of small molecules to SPR chips, and flowing proteins of interest over them to look for structural lead ideas.
And Stuart Schreiber and his collaborators at the Broad Institute have been working on the immobilized-small-molecule idea as well, trying different methods of attaching compound libraries to various solid supports. They’re looking for molecules that disrupt some very tough (but very interesting) biological processes, and have reported some successes in protein-protein interactions, a notoriously tempting (and notoriously hard) area for small-molecule drug discovery.
The big problem that people tend to have with all these ideas – and I’m one of those people, in the end – is that it’s hard to see how you can rope small molecules to a solid support without changing their character. After all, we don’t have anything smaller than atoms to make the ropes out of. It’s one thing to do this to a protein – that’ll look like a tangle of yarn with a small length of it stretching out to the side. But on the small molecule scale, it’s a bit like putting a hamster on a collar and leash designed for a Doberman. Mr. Hamster is not going to be able to enjoy his former freedom of movement, and a blindfolded person might, on picking him up, have difficulty recognizing his essential hamsterhood.
There's also the problem of how you attach that leash and collar, even if you decide that you can put up with it once it's on. Making an array of peptides on a solid support is all well and good - peptides have convenient handles at both ends, and there are a lot of well-worked-out reactions to attach things to them. But small molecules come in all sorts of shapes, sizes, and combinations of functional groups (at least, they'd better if you're hoping to see some screening hits with them). Trying to attach such a heterogeneous lot of stuff through a defined chemical ligation is challenging, and I think that the challenge is too often met by making the compound set less diverse. And after seeing how much my molecules can be affected by adding just one methyl group in the right (or wrong) place, I’m not so sure that I understand the best way to attach them to beads.
So I’m going to keep reading the tethered-small-molecule-library literature, and keep an eye on its progress. But I worry that I’m just reading about the successes, and not hearing as much about the dead ends. (That’s how the rest of the literature tends to work, anyway). For those who want to catch up with this area, here's a Royal Society review from Angela Koehler and co-workers at the Broad that'll get you up to speed. It's a high-risk, high-reward research area, for sure, so I'll always have some sympathy for it.
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February 24, 2009
Posted by Derek
Medicinal chemists spend a lot of their time exploring and trying to make sense of structure-activity relationships (SARs). We vary our molecules in all kinds of ways, have the biologists run them through the assays, and then sit down to make sense of the results.
And then, like as not, we get up again after a few minutes, shaking our heads. Has anyone out there ever worked on a project where the entire SAR made sense? I’ve always considered it a triumph if even a reasonable majority of the compounds fit into an interpretable pattern. SAR development is a perfect example of things not quite working out the way that they do in textbooks.
The most common surprise when you get your results back, if that phrase “common surprise” makes any sense, is to find that you’ve pushed some trend a bit too far. Methyl was pretty good, ethyl was better, but anything larger drops dead. I don’t count that sort of thing – those are boundary conditions, for the most part, and one of the things you do in a med-chem program is establish the limits under which you can work. But there are still a number of cases where what you thought was a wall turns out to have a secret passage or two hidden in it. You can’t put any para-substituents on that ring, sure. . .unless you have a basic amine over on the other end of the molecule, and then you suddenly can.
I’d say that a lot of these get missed, because after a project’s been running a while, various SAR dogmas get propagated. There are features of the structure space that “everybody knows”, and that few people want to spend their time violating. But it’s worth devoting a small (but real) amount of effort to going back and checking some of these after the lead molecule has evolved a bit, since you can get surprised.
Some projects I’ve worked on have so many conditional clauses of this sort built into their SAR that you wonder whether there are any boundaries at all. This works, unless you have this, but if you have that over there it can be OK, although there is that other compound which didn’t. . .making sense of this stuff can just be impossible. The opposite situation, the fabled Perfectly Additive SAR, is something I’ve never encountered in person, although I’ve heard tales after the fact. That’s the closest we come to the textbooks, where you can mix and match groups and substituents any way you like, predicting as you go from the previous trends just how they’ll come out. I have to think that any time you can do this, that it has to be taking place in a fairly narrow structure space – surely we can always break any trend like this with a little imagination.
Another well-known bit of craziness is the Only Thing That Works There. You’ll have whole series of compounds that have to have a a methyl group at some position, or they’re all dead. Nothing smaller, nothing larger, nothing with a different electronic flavor: it’s methyl or death. (Or fluoro, or a thiazole, or what have you – I’ve probably seen this with methyl more than with other groups, but it can happen all over the place). A sharp SAR is certainly nothing to fear; it’s probably telling you that you really are making good close contacts with the protein target somewhere. But it can be unnerving, and sometimes there’s not a lot of room left on the ledge when you have more than one constraint like this.
Why does all this go on? Multiple binding modes, you have to think. Proteins are flexible beasts, and they've got lots of ways to react to ligands. And it's important never to forget that we can't predict their responses, at least not yet and not very well. And of course, in all this discussion, we've just been considering one target protein. When you think about the other things your molecule might be hitting in cells or in a whole animal, and that the SAR relationships for those off-target things are just as fluid and complicated as for your target, well. . .you can see why medicinal chemistry is not going away anytime soon. Or shouldn't, anyway.
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January 21, 2009
Posted by Derek
I was blithely throwing around the term “chemical space” in yesterday’s post. So, what am I talking about, and how much room is in there, anyway?
Let's narrow it down to organic compounds, to start with, or at least compounds that are mostly organic. A working definition, as far as people interested in biology and medicine go, might then be “the domain of chemical compounds compatible with living systems”. That excludes the red-hot reactive stuff and the unstable exploders, but leaves most everything else. Let’s also ignore macromolecules of various kinds and cut back to “drug-like” sizes – say, molecular weight 500 or less. That way we don’t have infinite numbers of polymers going off in all directions; that should help. And that leaves us with. . .?
A ridiculously large set of compounds, still. You can see how things get out of control pretty quickly if you just consider a building-block problem. Imagine breaking compounds down into simple units - an aryl ring, an ether, a tertiary amine, and so on. What sorts of numbers do you get when you start mixing and matching them? Well, there are an awful lot of possible building blocks. You could quickly fill out a hundred different examples of each of those three subunits, so there's one hundred to the third, or a million possible compounds without even exerting yourself very much.
This sort of thought experiment has been done several times. One estimate done by this fragment approach and considering only stable structures came in between 10 to the twentieth and ten to the twenty-fourth compounds that could potentially be prepared using known synthetic methods. (See here for another "how many compounds are possible?" paper, from a different angle - the group that did that work has followed it up recently, which will be the subject of another post sometime). Needless to say, that is considerably larger than the total number of organic compounds ever described in reality. There's not enough carbon, oxygen, and nitrogen on earth to prepare a vial of each of these, and where would you put the vials? The terrifying thing is that this is actually one of the lower estimates, and thus perhaps a very reasonable and conservative one. You can find ten-to-the-sixtieth estimates out there, which is a figure that cannot be dealt with by human efforts.
These sorts of numbers are why some people doubt the utility of just cranking out neat structures. But looked at from the other direction, the number of compounds we have available isn't nearly so impressive, so making new ones, especially long lists of new ones, makes a difference in what we actually have in hand. But is it a difference akin to buying a thousand lottery tickets rather than buying one?
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January 20, 2009
Posted by Derek
Ever hear of Diversity-Oriented Synthesis? It’s an odd bird. DOS tries to maximize the number of structures and scaffolds produced from a given synthetic scheme – to find the most efficient ways to populate the largest amount of chemical space. In a way, it’s the contrapositive of natural product synthesis, which focuses all its effort into producing one specific molecule at a time. I should add that DOS isn’t about producing mixtures; its goal is discrete compounds, but plenty of them, and all over the map. (Here's more background from David Spring at Cambridge).
The point of this is to increase the diversity of compounds libraries for biological screening. And that’s traditionally been the concern of the drug companies, but (as far as I can tell) there’s very little DOS going on inside the industry. All the publications in the field, at any rate, seem to come from academia. Companies certainly do care about the diversity of their screening libraries, but they don’t seem to be addressing the issue through the “maximum diversity in the fewest steps” philosophy.
There’s a recent paper in Ang. Chem. that will give you a good flavor of what’s going on in this area. A group led by Adam Nelson at Leeds has published an interesting approach that relies on olefin metathesis. An ingenious use of protecting groups and sequential metathesis reactions builds up a wide variety of structural backbones pretty quickly. (Another key feature is the use of fluorous tagging for purification, which will be the topic of another future post around here). Metathesis was certainly a good choice, since that gives you a chance to form a lot of carbon-carbon bonds in a lot of ways, all using basically the same reaction conditions. In just a few steps (around five or six) they ended up with about 80 quite different scaffolds.
Stuart Schreiber, an early advocate of DOS, wrote up a “News and Views” piece for Nature about this paper, and he makes the case this way:
” The resulting products differ from the compounds found in most small-molecule screening collections. Typically purchased from commercial vendors, the compounds in such collections frequently lack chirality and are structurally simple. This means that they can bind to only a small number of biological targets. The compounds in commercial libraries also tend to be structurally similar — their 'diversity' is limited to variations in appendages attached to a small number of common skeletons. This undesirable combination of properties means that, although enormous numbers of compounds (often more than a million) are frequently tested in screenings, at great expense, in the case of undruggable targets relatively few biologically active 'hits' are found. In principle, a smaller library of compounds that contains a more diverse range of molecular shapes, such as those made by Morton et al., would provide both more hits for less money, and hits for the more challenging biological targets.”
I see where Schreiber is coming from, but there are some details being overlooked here. One big point is that smaller compounds actually tend to hit more targets, just not with as much absolute potency: that's the whole idea behind fragment-based drug design. Larger, more complex molecules tend to be more selective, but when they happen to fit, they can fit very well indeed. You need a huge pile of them to have a chance of finding one of those, though. (I think that a happy medium would be a DOS approach to not-very-large compounds, but that doesn't give you that much room to maneuver).
Another point is that the key thing about the collections you can buy is that they often depend on just a few bond-forming reactions. You get an awful lot of amides, ureas, and sulfonamides, since by gosh, those sure can be cranked out. To me, that’s the first thing that makes the Leeds compounds stand out: none of these classic library-making transformations was exploited. Unfortunately, the other things that make the Leeds compounds stand out aren’t necessarily good. For one thing, there are no basic nitrogens in any of the structures. The paper lists a big class of azacycles, but in every case, the nitrogens are capped with nosyl groups, which completely wipe out their character. And while it’s true that you can get biological activity without nitrogen, you’ll get a lot more with it. A useful extension of the chemistry would be to use some sort of (update: more easily) removable group on the nitrogens, so that each scaffold could be unmasked at the end – that would give you the basic nitrogens back, and you could then make a few amides and the like off of them for good measure.
The compound set is also heavy on alkenes, which isn't surprising, given the metathesis chemistry. There's nothing wrong with those per se, but it would be worth taking all the scaffolds through a hydrogenation reaction to saturate the bonds, giving you another compound set. Alternatively, if you want to be a real buckaroo, take them through a Simmon-Smith reaction and turn them into cyclopropanes - that could be messy, but cyclopropanes are very much under-represented in compound libraries, compared to how many of them could potentially exist. A bigger problem is that one of the linking groups the Leeds team uses is a silyl ketal. That’s not the most chemically attractive group in the world, nor the most stable, and as a medicinal chemist I would have avoided it.
That brings up another point about well, the point of these libraries. Schreiber makes the pitch that if we're going to do chemical biology on the tougher interaction targets (protein-protein, protein-nucleic acid, and so on), then we're going to need all the chemical diversity we can get. That's hard to dispute! But a lot depends on whether these compounds are meant to be in vitro tools, or real leads for drug discovery. You can put up with silyl ketals (or worse) if the former, but not for the latter. (Many medicinal chemists would say that if you have some functional group that you're just going to have to remove, then don't put it in there in the first place).
And that's the gap between academia and industry on this approach, right there. The in vitro tools, used to discover pathways and interactions, are more the province of the university labs, and the drug leads are more the concern of industry. As it stands now, the drug company folks look at many of the DOS libraries and say "Hmm. . .sort of, but not quite". That's probably going to change, and if I had to guess, I'd say that one way into industrial practice might be through chemical vendors. There are a number of companies who make their livings by offering unique building block compounds to the drug industry - as DOS matures, these people may sense a commercial opportunity and move in.
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November 14, 2008
Posted by Derek
So, you’re making an enzyme inhibitor drug, some compound that’s going to go into the protein’s active site and gum up the works. You usually want these things to be potent, so you can be sure that you’ve knocked down the enzyme, so you can give people a tiny, convenient pill, and so you don’t have to make heaps of the compound to sell. How potent is potent? And how potent can you get?
Well, we’d like nanomolar. For the non-chemists in the crowd, that’s a concentration measure based on the molecular weight of the compound. If the molecular weight of the drug is 400, which is more typical than perhaps it should be, then 400 grams of the stuff is one mole. And 400 grams dissolved in a liter of solvent to make a liter of solution would then give you a one molar (1 M) solution. (The original version of this post didn't make that important distinction, which I'll chalk up to my not being completely awake on the train ride first thing in the morning. The final volume you get on taking large amounts of things up in a given amount of solvent can vary quite a bit, but concentration is based, naturally, on what you end up with. And it’s a pretty flippin’ unusual drug substance than can be dissolved in water to that concentration, let me tell you right up front). So, four grams in a liter would be 0.01 M, or 10 millimolar, and foru hundred milligrams per liter would be a 1 millimolar solution. A one micromolar solution would be 400 micrograms (0.0004 grams) per liter, and a one nanomolar solution would be 400 nanograms (400 billionths of a gram) per liter. And that’s the concentration that we’d like to get to show good enzyme inhibition. Pretty potent, eh?
But you can do better – if you want to, which is a real question. Taking it all the way, your drug can go in and attach itself to the active site of its target by a real chemical bond. Some of those bond-forming reactions are reversible, and some of them aren’t. Even the reversible ones are a lot tighter than your usual run of inhibitor.
You can often recognize them by their time-dependent inhibition. With a normal drug, it doesn’t take all that long for things to equilibrate. If you leave the compound on for ten, twenty, thirty minutes, it usually doesn’t make a huge difference in the binding constant, because it’s already done what it can do and reached the balance it’s going to reach. But a covalent inhibitor, that’ll appear to get more and more potent the longer it stays in there, since more and more of the binding sites are being wiped out. (One test for reversibility after seeing that behavior is to let the protein equilibrate with fresh blank buffer solution for a while, to see if its activity ever comes back). You can get into hair-splitting arguments if your compound binds so tightly that it might as well be covalent; at some point they're functionally equivalent.
There are several drugs that do this kind of thing, but they’re an interesting lot. You have the penicillins and their kin – that’s what that weirdo four-membered lactam ring is doing, spring-loaded for trouble once it gets into the enzyme. The exact same trick is used in Alli (orlistat), the pancreatic lipase inhibitor. And there are some oncology drugs that covalently attach to their targets (and, in some cases, to everything else they hit, too). But you’ll notice that there’s a bias toward compounds that hit bacterial enzymes (instead of circulating human ones), don’t get out of the gut, or are toxic and used as a last resort.
Those classes don’t cover all the covalent drugs, but there’s enough of that sort of thing to make people nervous. If your compound has some sort of red-hot functional group on it, like some of those nasty older cancer compounds, you’re surely going to mess up a lot of other proteins that you would rather have left alone. And what happens to the target protein after you’ve stapled your drug to it, anyway? One fear has been that it might present enough of a different appearance to set off an immune response, and you don’t want that, either.
But covalent inhibition is actually a part of normal biochemistry. If you had a compound with a not-so-lively group, one that only reacted with the protein when it got right into the right spot – well, that might be selective, and worth a look. The Cravatt lab at Scripps has been looking into what kinds of functional groups react with various proteins, and as we get a better handle on this sort of thing, covalency could make a comeback. Some people maintain that it never left!
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November 11, 2008
Posted by Derek
I wrote a while back about the problem of compounds sticking to labware. That sort of thing happens more often than you’d think, and it can really hose up your assay data in ways that will send you running around in circles. Now there’s a report in Science of something that’s arguably even worse. (Here's a good report on it from Bloomberg, one of the few to appear in the popular press).
The authors were getting odd results in an assay with monoamine oxidase B enzyme, and tracked it down to two compounds leaching out of the disposable plasticware (pipette tips, assay plates, Eppendorf vials, and so on). Oleamide is used as a “slip agent” to keep the plastic units from sticking to each other, but it’s also a MAO-B inhibitor. Another problem was an ammonium salt called DiHEMDA, which is put in as a general biocide – and it appears to be another MAO-B inhibitor.
Neither of them are incredibly potent, but if you’re doing careful kinetic experiments or the like, it’s certainly enough to throw things off. The authors found that just rinsing water through various plastic vessels was enough to turn the solution into an enzyme inhibitor. Adding organic solvents (10% DMSO, methanol) made the problem much worse; presumably these extract more contaminants.
And it’s not just this one enzyme. They also saw effects on a radioligand binding assay to the GABA-A receptor, and they point out that the biocides used are known to show substantial protein and DNA binding. These things could be throwing assay data around all over the place – and as we work in smaller and smaller volumes, with more complex protocols, the chances of running into trouble increase.
What to do about all this? Well, at a minimum, people should be sure to run blank controls for all their assays. That’s good practice, but sometimes it gets skipped over. This effect has probably been noted many times before as some sort of background noise in such controls, and many times you should be able to just subtract it out. But there are still many experiments where you can’t get away from the problem so easily, and it’s going to make your error bars wider no matter what you do about it. There are glass inserts for 96-well plates, and there are different plastics from different manufacturers. But working your way through all that is no fun at all.
As an aside, this sort of thing might still make it into the newspapers, since there have been a lot of concerns about bisphenol A and other plastic contaminants. In this case, I think the problem is far greater for lab assays than it is for human exposures. I’m not so worried about things like oleamide, since these are found in the body anyway, and can easily be metabolized. The biocides might be a different case, but I assume that we’re loaded with all kinds of substances, almost all of them endogenous, that are better inhibitors of enzymes like MAO-B. And at any rate, we’re exposed to all kinds of wild stuff at low levels, just from the natural components of our diet. Our livers are there to deal with just that sort of thing, but that said, it’s always worth checking to make sure that they’re up to the job.
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October 16, 2008
Posted by Derek
A key step in all drug discovery programs are the cellular and animal models. The cells are the first time that the compounds are exposed to a living system (with cellular membranes that keep things out). The animals, of course, are a very stringent test indeed, with the full inventory of absorption, metabolism, and excretion machinery, along with the possibility of side effects in systems that you might not have even considered.
So it’s a tricky business to make sure that these tests are being done in the most meaningful way possible. You can knock your project out of promising areas for development if your model systems are too tough – and it’s even easier to water them down in the interest of getting numbers that make everyone feel better. “As stringent as they need to be” is the rule, but it’s a hard one to handle in practice.
Take, for example, the antibacterial field. The first cell assays there are unusually meaningful, since they’re being done on the real live targets of the drugs. (That doesn’t do much to get you past the high barrier of animal testing, though, since you have to see if your compounds that kill bacteria in a dish will still do it in that much more demanding environment). But there are all sorts of strains of bacteria out there, and it’s up to you to choose the ones that will tell you the most about what your compounds can do.
One way that bacteria evade being killed off by our wonder drug candidates is by pumping the compounds right back out once they get in. There are quite a few of the efflux pumps, and wild-type bacteria (particularly the resistant strains) are well stocked with them. You can culture all sorts of mutants, though, with these various transport mechanisms ablated or wiped out completely. If your compound doesn’t work on the normal lines, but cuts a swath through some of these, you have good evidence that your problem is efflux pumping, not some intrinsic problem with your target mechanism.
The problem is, we often don’t have a very good idea of what to do about efflux pumping. These proteins recognize a huge variety of different structures, and there aren’t really many useful ways to predict what they’ll take up versus what they’ll leave alone. In many cases, you just have to throw all sorts of variations at them and hope for the best. (The same goes for the other situations where active transport can be a big factor, such as with cancer cells and the blood-brain barrier).
So, how do you set up your assays? You can run the crippled bacteria first, which will give you an idea of the intrinsic potencies of your compounds, minus the pumping difficulty. That may be the way to go but you’d better follow that up with some things closer to wild-type, or you’re going to end up kidding yourself. Having a compound that infallibly kills only those bacteria that can’t spit it out is probably not going to do you (or anyone else) much good, considering what the situation is like out in the real world.
The same principle holds for other assays, all the way up to rats. If you run a relative pushover model in oncology, you can put up a very impressive plot of how powerful your compounds are. But what does that do for you in the end? Or for cancer patients, whose malignant cells are much more wily and aggressive? The best course, I’d say, is to run the watered-down models if they can tell you something that will help you move things along. But get to the wild-types, the real thing, as soon as possible. Those latter models may tell you things that you don’t want to hear – but that doesn’t mean that you don’t need to hear them.
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September 4, 2008
Posted by Derek
X-ray crystallography is wonderful stuff – I think you’ll get chemists to generally agree on that. There’s no other technique that can provide such certainty about the structure of a compound – and for medicinal chemists, it has the invaluable ability to show you a snapshot of your drug candidate bound to its protein target. Of course, not all proteins can be crystallized, and not all of them can be crystallized with drug ligands in them. But an X-ray structure is usually considered the last word, when you can get one – and thanks to automation, computing power, and to brighter X-ray sources, we get more of them than ever.
But there are a surprising number of ways that X-ray data can mislead you. For an excellent treatment of these, complete with plenty of references to the recent literature, see an excellent paper coming out in Drug Discovery Today from researchers at Astra-Zeneca (Andy Davis and Stephen St.-Gallay) and Uppsala University (Gerard Kleywegt). These folks all know their computational and structural biology, and they’re willing to tell you how much they don’t know, either.
For starters, a small (but significant) number of protein structures derived from X-ray data are just plain wrong. Medicinal chemists should always look first at the resolution of an X-ray structure, since the tighter the data, the better the chance there is of things being as they seem. The authors make the important point that there’s some subjective judgment involved on the part of a crystallographer interpreting raw electron-density maps, and the poorer the resolution, the more judgment calls there are to be made:
Nevertheless, most chemists who undertake structure-based design treat a protein crystal structure reverently as if it was determined at very high resolution, regardless of the resolution at which the structure was actually determined (admittedly, crystallographers themselves are not immune to this practice either). Also, the fact that the crystallographer is bound to have made certain assumptions, to have had certain biases and perhaps even to have made mistakes is usually ignored. Assumptions, biases, ambiguities and mistakes may manifest themselves (even in high-resolution structures) at the level of individual atoms, of residues (e.g. sidechain conformations) and beyond.
Then there’s the problem of interpreting how your drug candidate interacts with the protein. The ability to get an X-ray structure doesn’t always correlate well with the binding potency of a given compound, so it’s not like you can necessarily count on a lot of clear signals about why the compound is binding. Hydrogen bonds may be perfectly obvious, or they can be rather hard to interpret. Binding through (or through displacement of) water molecules is extremely important, too, and that can be hard to get a handle on as well.
And not least, there’s the assumption that your structure is going to do you good once you’ve got it nailed down:
It is usually tacitly assumed that the conditions under which the complex was crystallised are relevant, that the observed protein conformation is relevant for interaction with the ligand (i.e. no flexibility in the active-site residues) and that the structure actually contributes insights that will lead to the design of better compounds. While these assumptions seem perfectly reasonable at first sight, they are not all necessarily true. . .
That’s a key point, because that’s the sort of error that can really lead you into trouble. After all, everything looks good, and you can start to think that you really understand the system, that is until none of your wonderful X-ray-based analogs work out they way you thought they would. The authors make the point that when your X-ray data and your structure-activity data seem to diverge, it’s often a sign that you don’t understand some key points about the thermodynamics of binding. (An X-ray is a static picture, and says nothing about what energetic tradeoffs were made along the way). Instead of an irritating disconnect or distraction, it should be looked at as a chance to find out what’s really going on. . .
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July 16, 2008
Posted by Derek
At various points in my drug discovery career, I’ve worked on G-protein-coupled receptor (GPCR) targets. Most everyone in the drug industry has at some point – a significant fraction of the known drugs work through them, even though we have a heck of a time knowing what their structures are like.
For those outside the field, GPCRs are a ubiquitous mode of signaling between the interior of a cell and what’s going on outside it, which accounts for the hundreds of different types of the things. They’re all large proteins that sit in the cell membrane, looped around so that some of their surfaces are on the outside and some poke through to the inside. The outside folds have a defined binding site for some particular ligand - a small molecule or protein – and the inside surfaces interact with a variety of other signaling proteins, first among them being the G-proteins of the name. When a receptor’s ligand binds from the outside, that sets off some sort of big shape change. The protein’s coils slide and shift around in response, which changes its exposed surfaces and binding patterns on the inside face. Suddenly different proteins are bound and released there, which sets off the various chemical signaling cascades inside the cell.
The reason we like GPCRs is that many of them have binding sites for small molecules, like the neurotransmitters. Dopamine, serotonin, acetylcholine – these are molecules that medicinal chemists can really get their hands around. The receptors that bind whole other proteins as external ligands are definitely a tougher bunch to work with, but we’ve still found many small molecules that will interact with some of them.
Naturally, there are at least two modes of signaling a GPCR can engage in: on and off. A ligand that comes in and sets off the intracellular signaling is called an agonist, and one that binds but doesn’t set off those signals is called an antagonist. Antagonist molecules will also gum up the works and block agonists from doing their things. We have an easier time making those, naturally, since there are dozens of ways to mess up a process compared to the ways there are of running it correctly!
Now, when I was first working in the GPCR field almost twenty years ago, it was reasonably straightforward. You had your agonists and you had your antagonists – well, OK, there were those irritating partial agonists, true. Those things set off the desired cellular signal, but never at the levels that a full agonist would, for some reason. And there were a lot of odd behaviors that no one quite knew how to explain, but we tried to not let those bother us.
These days, it’s become clear that GPCRs are not so simple. There appear to be some, for example, whose default setting is “on”, with no agonist needed. People are still arguing about how many receptors do this in the wild, but there seems little doubt that it does go on. These constituitively active receptors can be turned off, though, by the binding of some ligands, which are known as inverse agonists, and there are others, good old antagonists, that can block the action of the inverse agonists. Figuring out which receptors do this sort of thing - and which drugs - is a full time job for a lot of people.
It’s also been appreciated in recent years that GPCRs don’t just float around by themselves on the cell surface. Many of them interact with other nearby receptors, binding side-by-side with them, and their activities can vary depending on the environment they’re in. The search is on for compounds that will recognize receptor dimers over the good ol’ monomeric forms, and the search is also on for figuring out what those will do once we have them. To add to the fun, these various dimers can be with other receptors of their own kind (homodimers) or with totally different ones, some from different families entirely (heterodimers). This area of research is definitely heating up.
And recently, I came across a paper which looked at how a standard GPCR can respond differently to an agonist depending on where it's located in the membrane. We're starting to understand how heterogeneous the lipids in that membrane are, and that receptors can move from one domain to another depending on what's binding to them (either on their outside or inside faces). The techniques to study this kind of thing are not trivial, to put it mildly, and we're only just getting started on figuring out what's going on out there in the real world in real time. Doubtless many bizarre surprises await.
So, once again, the "nothing is simple" rule prevails. This kind of thing is why I can't completely succumb to the gloom that sometimes spreads over the industry. There's just so much that we don't know, and so much to work on, and so many people that need what we're trying to discover, that I can't believe that the whole enterprise is in as much trouble as (sometimes) it seems. . .
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July 11, 2008
Posted by Derek
Here's an interesting idea: Merck, Lilly, and Pfizer are bankrolling a startup company to look for new technologies for drug development. Enlight Biosciences will focus on the biggest bottlenecks and risk points in the process, including new imaging techniques for preclinical and clinical evaluation of drug candidates, predictive toxicology and pharmacokinetics, clinical biomarkers, new models of disease, delivery methods for protein- and nucleic acid-based therapies, and so on.
It's safe to say that if any real advances are made in any of these, the venture will have to be classed as a success. These are hard problems, and it's not like there's been no financial incentive to solve any of them. (On the contrary - billions of dollars are out there waiting for anyone who can truly do a better job at these things). I wish these people a lot of luck, and I'm glad to see them doing what they're doing, but I do wish that there were more details available on how they plan to go about things. The opening press release leaves a lot of things unspoken, no doubt by design. (For instance, where are the labs going to be? What's the hoped-for balance of industry types to academics? How many people do they plan to have working on these things, and how will the companies involved plan to share the resulting technologies?)
Enlight is a creation of Puretech Ventures, a Boston VC firm that's been targeting early-stage ideas in these areas. Getting buy-in from the three companies above will definitely help, but their commitment isn't too clear at present. For now, it looks like they're getting to take a fresh look at some areas of great interest, without necessarily having to spend a lot of their own money. The press release says that Enlight will "direct up to $39 million" toward the areas listed on their web site, but those problems will eat thirty-nine million dollars without even reaching for the salt. Further funding is no doubt in the works, with the Merck/Pfizer/Lilly names as a guarantee of seriousness, and if any of these projects pan out, the money will arrive with alacrity.
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June 3, 2008
Posted by Derek
We recently encountered a problem that’s (unfortunately) a rather common one. An enzyme assay turned up an interesting hit compound, with some characteristics that we were hoping to see for leads against our target. A re-test showed that yes, the activity appeared to be real, which was interesting, since this hit was a welcome surprise from a class of compounds that we weren’t expecting much from.
It was a comparatively old compound in the files, and all we could find out was that it had been purchased rather than made in house. Looking around, it seemed that there were very few literature references to things of this type, and only one commercial source: the Sigma-Aldrich Library of Rare chemicals, known as SALOR. That, though, was a potential warning flag.
Those compounds come from an effort started by Aldrich’s Alfred Bader many years ago, who started trolling around various academic labs looking for unusual compounds that no one wanted to keep around any more. Over time the company has accumulated a horde of oddities that are often found nowhere else, but there are several catches. For one, these things are usually available only in small quantities, tens of milligrams for the most part. That’s plenty for the screening files, but you’re not going to make a bunch of analogs starting from what comes out of a SALOR vial. Another catch is that the compounds are sold, very explicitly, as is: the university sources tell Aldrich what’s on the label, so that’s what they sell you and caveat emptor all the way, dude.
So often as not, you get what we got, a nice-looking white powder which, on closer analysis, turned out to only have a vague relationship to the structure on its label. We knew that we were in trouble as soon as the first NMR came out: way too much stuff in one region, nowhere near enough in some others. Mass spec confirmed that this thing weighed more than twice as much as what it was supposed to. We’ve since pretty much nailed down what the stuff really is, and our interest in it has decreased as each of the veils has been removed from the real structure.
We’re correcting the data in our own screening files, of course. And yes, we’re going to tell the folks at Aldrich to change their label, too, assuming they have any of this stuff left. At least the next person will know what they’re getting. For once. But there are more of these things waiting out there – in every large compound collection, in every catalog, in every collection of data are mistakes. Watch for them.
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May 20, 2008
Posted by Derek
For those who were wondering, my copper reactions the other day worked out just fine. They started out a beautiful blue (copper iodide and an amino acid in straight DMSO – if that’s not blue it’s maybe going to be green, and if it’s not either one you’ve done something wrong). Of course, the color doesn’t stay. The copper ends up as part of a purple-brown sludge that has to be filtered out of the mix, which is the main downside of those Ullman reactions, no matter how people try to scrub them up for polite company.
And DMSO is the other downside, because you have to wash that stuff out with a lot of water. That’s one of the lab solvents that everyone has heard of, even if they slept through high school chemistry. But it’s not one that we use for reactions very much, because it’s something of a pain. It dissolves most everything, which is a good quality, but along with that one comes the ability to contaminate most everything. If your product is pretty greasy and nonpolar, you can partition the reaction between water and some more organic solvent (ether’s what I used this time), and wash it around a lot. But if your product is really polar, you could be in for a long afternoon.
That mighty solvation is something you need to look out for if you spill the stuff on yourself, of course. DMSO is famous for skin penetration (no, I have no idea if it does anything for arthritis). And while many of my compounds are not very physiologically active, I’d rather not dose myself with them to check those numbers. At the extreme end of the scale, a solution of cyanide in DMSO is potentially very dangerous stuff indeed. I’ve done cyanide reactions like that, many times, but always while paying attention to the task at hand.
Where DMSO really gets used is in the compound repository. That dissolves-everything property is handy when you have a few hundred thousand compounds to handle. The standard method for some years has been to keep compounds in the freezer in some defined concentration in DMSO – the solvent freezes easily, down around where water does (Not so! Actually, I've seen in freeze in a chilly lab a couple of times, now that I'm reminded of that in the comments to this post. Pure DMSO solidifies around 17 to 19 C, which is about 64 F C - a bit lower with those screening compounds dissolved in it, though).
But there are problems. For one thing, DMSO isn’t inert. That’s another reason it doesn’t get as much use as a lab solvent; there are many reaction conditions during which it wouldn’t be able to resist joining the party. You can oxidize things by leaving them in DMSO open to air, which isn’t what you want to do to the compound screening collection, so the folks there do as much handling under nitrogen as they can. Compounds sitting carelessly in DMSO tend to turn yellow, which is on the way to red, which is on the way to brown, and there are no pure brown wonder drugs.
Another difficulty is that love for water. Open DMSO containers will pull water in right out of the air, and a few careless freeze/thaw cycles with a screening plate will not only blow your carefully worked out concentrations, it may well also start crashing your compounds out of solution. The less polar ones will start decided that pure DMSO is one thing, but 50/50 DMSO/water is quite another. So not only do you want to work under nitrogen, if you can, but dry nitrogen, and you want to make sure that those plates are sealed up well while they’re in the freezer. (As an alternative, you can go ahead and put water in from the start, taking the consequences). All of these concerns begin to wear down the advantages of DMSO as a universal solvent, but not quite enough to keep people from using it.
And what about the compounds that don’t dissolve in the stuff? Well, it’s a pretty safe bet that a small molecule that can’t go into DMSO is going to have a mighty hard time becoming a drug, and it’s a very unattractive lead to start from, too. That’s the sort of molecule that would tend to just go right through the digestive tract without even noticing that there are things trying to get it into solution. And as for something given i.v., well, if you can’t get it to go into straight DMSO, what are the chances you’re going to get it into some kind of saline injection solution? Or the chances that it won’t crash out in the vein for an instant embolism? No, the zone of non-DMSO-soluble small organics is not a good place to hunt. We’ll leave proteins out of it, but if anyone knows of a small molecule drug that can’t go into DMSO, I’d like to hear about it. Taxol, maybe?
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April 3, 2008
Posted by Derek
I was having a discussion the other day about which therapeutic areas have the best predictive assays. That is, what diseases can you be reasonably sure of treating before your drug candidate gets into (costly) human trials? As we went on, things settled out roughly like this:
Cardiovascular (circulatory): not so bad. We’ve got a reasonably good handle on the mechanisms of high blood pressure, and the assays for it are pretty predictive, compared to a lot of other fields. (Of course, that’s also now one of the most well-served therapeutic areas in all of medicine). There are some harder problems, like primary pulmonary hypertension, but you could still go into humans with a bit more confidence than usual if you had something that looked good in animals.
Cardiovascular (lipids): deceptive. There aren’t any animals that handle lipids quite the way that humans do, but we’ve learned a lot about how to interpolate animal results. That plus the various transgenic models gives you a reasonable read. The problem is, we don’t really understand human lipidology and its relation to disease as well as we should (or as well as a lot of people think we do), so there are larger long-term problems hanging over everything. But yeah, you can get a new drug with a new mechanism to market. Like Vytorin.
CNS: appalling. That goes for the whole lot – anxiety, depression, Alzheimer’s, schizophrenia, you name it. The animal models are largely voodoo, and the mechanisms for the underlying diseases are usually opaque. The peripheral nervous system isn’t much better, as anyone who’s worked in pain medication will tell you ruefully. And all this is particularly disturbing, because the clinical trials here are so awful that you’d really appreciate some good preclinical pharmacology: patient variability is extreme, the placebo effect can eat you alive, and both the diseases and their treatments tend to progress very, very slowly. Oh, it’s just a nonstop festival of fun over in this slot. Correspondingly, the opportunities are huge.
Anti-infectives: good, by comparison. It’s not like you can’t have clinical failures in this area, but for the most part, if you can stop viruses or kill bugs in a dish, you can do it in an animal, or in a person. The questions are always whether you can do it to the right extent, and just how long it’ll be before you start seeing resistance. With antibacterials that can be, say, "before the end of your clinical trials". There aren’t as many targets here as everyone would like, and none of them is going to be a gigantic blockbuster, but if you find one you can attack it with more confidence than usual.
Diabetes: pretty good, up to a point. There are a number of well-studied animal models here, and if your drug’s mechanism fits their quirks and limitations, then you should be in fairly good shape. Not by coincidence, this is also a pretty well-served area, by current standards. If you’re trying something off the beaten path, though, a route that STZ or db/db rats won’t pick up well, then things get harder. Look out, though, because this disease area starts to intersect with lipids, which (it bears saying again) We Don't Understand Too Well.
Obesity: deceptive in the extreme. There are an endless number of ways to get rats to lose weight. Hardly any of them, though, turn out to be relevant to humans or relevant to something humans would consider paying for. (Relentless vertigo would work to throw the animals off their feed, for example, but would probably be a loser in the marketplace. Although come to think of it, there is Alli, so you never know). And the problem here is always that there are so many overlapping backup redundant pathways for feeding behavior, so the chances for any one compound doing something dramatic are, well, slim. The expectations that a lot of people have for a weight-loss therapy are so high (thanks partly to years of heavily advertised herbal scams and bizarre devices), but the reality is so constrained.
Oncology: horrible, just horrible. No one trusts the main animal models in this area (rat xenografts of tumor lines) as anything more than rough, crude filters on the way to clinical trials. And no one should. Always remember: Iressa, the erstwhile AstraZeneca wonder drug from a few years back, continues to kick over all kinds of xenograft models. It looks great! It doesn’t work in humans! And it's not alone, either. So people take all kinds of stuff into the clinic against cancer, because what else can you do? That leads to a terrifying overall failure rate, and has also led to, if you can believe it, a real shortage of cancer patients for trials in many indications.
OK, those are some that I know about from personal experience. I’d be glad to hear from folks in other areas, like allergy/inflammation, about how their stuff rates. And there are a lot of smaller indications I haven’t mentioned, many of them under the broad heading of immunology (lupus, MS, etc.) whose disease models range from “difficult to run and/or interpret” on the high side all the way down to “furry little random number generators”.
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+ TrackBacks (0) | Category: Animal Testing | Cancer | Cardiovascular Disease | Diabetes and Obesity | Drug Assays | Drug Development | Infectious Diseases | The Central Nervous System
March 27, 2008
Posted by Derek
There’s an excellent paper in the most recent issue of Chemistry and Biology that illustrates some of what fragment-based drug discovery is all about. The authors (the van Aalten group at Dundee) are looking at a known inhibitor of the enzyme chitinase, a natural product called argifin. It’s an odd-looking thing – five amino acids bonded together into a ring, with one of them (an arginine) further functionalized with a urea into a sort of side-chain tail. It’s about a 27 nM inhibitor of the enzyme.
(For the non-chemists, that number is a binding affinity, a measure of what concentration of the compound is needed to shut down the enzyme. The lower, the better, other things being equal. Most drugs are down in the nanomolar range – below that are the ulta-potent picomolar and femtomolar ranges, where few compounds venture. And above that, once you get up to 1000 nanomolar, is micromolar, and then 1000 micromolar is one millimolar. By traditional med-chem standards, single-digit nanomolar = good, double-digit nanomolar = not bad, triple-digit nanomolar or low micromolar = starting point to make something better, high micromolar = ignore, and millimolar = can do better with stuff off the bottom of your shoe.
What the authors did was break this argifin beast up, piece by piece, measuring what that did to the chitinase affinity. And each time they were able to get an X-ray structure of the truncated versions, which turned out to be a key part of the story. Taking one amino acid out of the ring (and thus breaking it open) lowered the binding by about 200-fold – but you wouldn’t have guessed that from the X-ray structure. It looks to be fitting into the enzyme in almost exactly the same way as the parent.
And that brings up a good point about X-ray crystal structures. You can’t really tell how well something binds by looking at one. For one thing, it can be hard to see how favorable the various visible interactions might actually be. And for another, you don’t get any information at all about what the compound had to pay, energetically, to get there.
In the broken argifin case, a lot of the affinity loss can probably be put down to entropy: the molecule now has a lot more freedom of movement, which has to be overcome in order to bind in the right spot. The cyclic natural product, on the other hand, was already pretty much there. This fits in with the classic med-chem trick of tying back side chains and cyclizing structures. Often you’ll kill activity completely by doing that (because you narrowed down on the wrong shape for the final molecule), but when you hit, you hit big.
The structure was chopped down further. Losing another amino acid only hurt the activity a bit more, and losing still another one gave a dipeptide that was still only about three times less potent than the first cut-down compound. Slicing that down to a monopeptide, basically just a well-decorated arginine, sent the activity down another sixfold or so – but by now we’re up to about 80 micromolar, which most medicinal chemists would regard as the amount of activity you could get by testing the lint in your pocket.
But they went further, making just the little dimethylguanylurea that’s hanging off the far end. That thing is around 500 micromolar, a level of potency that would normally get you laughed at. But wait. . .they have the X-ray structures all along the way, and what becomes clear is that this guanylurea piece is binding to the same site on the protein, in the same manner, all the way down. So if you’re wondering if you can get an X-ray structure of some 500 micromolar dust bunny, the answer is that you sure can, if it has a defined binding site.
And the value of these various derivatives almost completely inverts if you look at them from a binding efficiency standpoint. (One common way to measure that is to take the minus log of the binding constant and divide by the molecular weight in kilodaltons). That’s a “bang for the buck” index, a test of how much affinity you’re getting for the weight of your molecule. As it turns out, argifin – 27 nanomolar though it be – isn’t that efficient a binder, because it weighs a hefty 676. The binding efficiency index comes out to just under 12, which is nothing to get revved up about. The truncated analogs, for the most part, aren’t much better, ranging from 9 to 15.
But that guanylurea piece is another story. It doesn’t bind very tightly, but it bats way above its scrawny size, with a BEI of nearly 28. That’s much more impressive. If the whole argifin molecule bound that efficiently, it would be down in the ten-to-the-minus nineteenth range, and I don’t even know the name of that order of magnitude. If you wanted to make a more reasonably sized molecule, and you should, a compound of MW 400 would be about ten femtomolar with a binding efficiency like that. There’s plenty of room to do better than argifin.
So the thing to do, clearly, is to start from the guanylurea and build out, checking the binding efficiency along the way to make sure that you’re getting the most out of your additions. And that is exactly the point of fragment-based drug discovery. You can do it this way, cutting down a larger molecule to find what parts of it are worth the most, or you can screen to find small fragments which, though not very potent in the absolute sense, bind very efficiently. Either way, you take that small, efficient piece as your anchor and work from there. And either way, some sort of structural read on your compounds (X-ray or NMR) is very useful. That’ll give you confidence that your important binding piece really is acting the same way as you go forward, and give you some clues about where to build out in the next round of analogs.
This particular story may be about as good an illustration as one could possibly find - here's hoping that there are more that can work out this way. Congratulations to van Aalten and his co-workers at Dundee and Bath for one of the best papers I've read in quite a while.
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February 14, 2008
Posted by Derek
I’ve been reading an interesting paper from JACS with the catchy title of “Optimization of Activity-Based Probes for Proteomic Profiling of Histone Deacetylase Complexes”. This is work from Benjamin Cravatt's lab at Scripps, and it says something about me, I suppose, that I found that title of such interest that I immediately printed off a copy to study more closely. Now I’ll see if I can interest anyone who wasn’t already intruiged! First off, some discussion of protein tagging, so if you’re into that stuff already, you may want to skip ahead.
So, let’s say you have a molecule that has some interesting biological effect, but you’re not sure how it works. You have suspicions that it’s binding to some protein and altering its effects (always a good guess), but which protein? Protein folks love fluorescent assays, so if you could hang some fluorescent molecule off one end of yours, perhaps you could start the hunt: expose your cells to the tagged molecule, break them open, look for the proteins that glow. There are complications, though. You’d have to staple the fluorescent part on in a way that didn’t totally mess up that biological activity you care about, which isn’t always easy (or even possible). The fact that most of the good fluorescent tags are rather large and ugly doesn’t help. But there’s more trouble: even if you manage to do that, what’s to keep your molecule from drifting right back off of the protein while you’re cleaning things up for a look at the system? Odds are it will, unless it has a really amazing binding constant, and that’s not the way to bet.
One way around that problem is sticking yet another appendage on to the molecule, a so-called photoaffinity label. These groups turn into highly reactive species on exposure to particular wavelengths of light, ready to form a bond with the first thing they see. If your molecule is carrying one when it’s bound to your mystery protein, shining light on the system will likely cause a permanent bond to form between the two. Then you can do all your purifications and separations, and look at your leisure for which proteins fluoresce.
This is “activity-based protein profiling”, and it’s a hot field. There are a lot of different photoaffinity labels, and a lot of ways to attach them, and likewise with the fluorescent groups. The big problem, as mentioned above, is that it’s very hard to get both of those on your molecule of interest and still keep its biological activity – that’s an awful lot of tinsel to carry around. One slick solution is to use a small placeholder for the big fluorescent part. This, ideally, would be some little group that will hide out innocently during the whole protein-binding and photoaffinity-labeling steps, then react with a suitably decorated fluorescent partner once everything’s in place. This assembles your glowing tag after the fact.
A favorite way to do that step is through an azide-acetylene cycloaddition reaction, the favorite of Barry Sharpless’s “click” reactions. Acetylenes are small and relatively unreactive, and at the end of the process, after you’ve lysed the cells and released all their proteins, you can flood your system with azide-substituted fluorescent reagent. The two groups react irreversibly under mild catalytic conditions to make a triazole ring linker, which is a nearly ideal solution that’s getting a lot of use these days (more on this another day).
So, now to this paper. What this group did was label a known compound (from Ron Breslow's group at Columbia) that targets histone deacetylase (HDAC) enzymes, SAHA, now on the market as Vorinostat. There are a lot of different subtypes of HDAC, and they do a lot of important but obscure things that haven’t been worked out yet. It’s a good field to discover protein function in.
When they modified SAHA in just the way described above, with an acetylene and a photoaffinity group, it maintained its activity on the known enzymes, so things looked good. They then exposed it to cell lysate, the whole protein soup, and found that while it did label HDAC enzymes, it seemed to label a lot of other things in the background. That kind of nonspecific activity can kill an assay, but they tried the label out on living cells anyway, just to see what would happen.
Very much to their surprise, that experiment led to much cleaner and more specific labeling of HDACs. The living system was much nicer than the surrogate, which (believe me) is not how things generally go. Some HDACs were labeled much more than others, though, and my first thought on reading that was “Well, yeah, sure, your molecule is a more potent binder to some of them”.
But that wasn’t the case, either. When they profiled their probe molecule’s activity versus a panel of HDAC enzymes, they did indeed find different levels of binding – but those didn’t match up with which ones were labeled more in the cells. (One explanation might be that the photoaffinity label found some of the proteins easier to react with than others, perhaps due to what was nearby in each case when the reactive species formed).
Their next step was to make a series of modified SAHA scaffolds and rig them up with the whole probe apparatus. Exposing these to cell lysate showed that many of them performed fine, labeling HDAC subtypes as they should, and with different selectivities than the original. But when they put these into cells, none of them worked as well as the plain SAHA probe – again, rather to their surprise. (A lot of work went into making and profiling those variations, so I suspect that this wasn’t exactly the result the team had hoped for - my sympathies to Cravatt and especially to his co-author Cleo Salisbury). The paper sums the situation up dryly: "These results demonstrate that in vitro labeling is not necessarily predictive of in situ labeling for activity-based protein profiling probes".
And that matches up perfectly with my own prejudices, so it must be right. I've come to think, over the years, that the way to go is to run your ideas against the most complex system you think that they can stand up to - in fact, maybe one step beyond that, because you may have underestimated them. A strict reductionist might have stopped after the cell lysate experiments in this case - clearly, this probe was too nonspecific, no need to waste time on the real system, eh? But the real system, the living cell, is real in complex ways that we don't understand well at all, and that makes this inference invalid.
The same goes for medicinal chemistry and drug development. If you say "in vitro", I say "whole cells". If you've got it working in cells, I'll call for mice. Then I'll see your mice and raise you some dogs. Get your compounds as close to reality as you can before you pass judgment on them.
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January 29, 2008
Posted by Derek
I've had some questions about animal models and testing, so I thought I'd go over the general picture. As far as I can tell, my experience has been pretty representative.
There are plenty of animal models used in my line of work, but some of them you see more than others. Mice and rats are, of course, the front line. I’ve always been glad to have a reliable mouse model, personally, because that means the smallest amount of compound is used to get an in vivo readout. Rats burn up more hard-won material. That's not just because they're uglier, since we don’t dose based on per cent ugly, but rather because they're much larger and heavier. The worst were some elderly rodents I came across years ago that were being groomed for a possible Alzheimer’s assay – you don’t see many old rats in the normal course of things, but I can tell you that they do not age gracefully. They were big, they were mean, and they were, well, as ratty as an animal can get. (They were useless for Alzheimer's, too, which must have been their final revenge).
You can’t get away from the rats, though, because they’re the usual species for toxicity testing. So if your pharmacokinetics are bad in the rat, you’re looking at trouble later on – the whole point of tox screens is to run the compound at much higher than usual blood levels, which in the worst cases you may not be able to reach. Every toxicologist I’ve known has groaned, though, when asked if there isn’t some other species that can be used – just this time! – for tox evaluation. They’d much rather not do that, since they have such a baseline of data for the rat, and I can’t blame them. Toxicology is an inexact enough science already.
It’s been a while since I’ve personally seen the rodents at all, though, not that I miss them. The trend over the years has been for animal facilities to become more and more separated from the other parts of a research site – separate electronic access, etc. That’s partly for security, because of people like this, and partly because the fewer disturbances among the critters, the better the data. One bozo flipping on the wrong set of lights at the wrong time can ruin a huge amount of effort. The people authorized to work in the animal labs have enough on their hands keeping order – I recall a run of assay data that had an asterisk put next to it when it was realized that a male mouse had somehow been introduced into an all-female area. This proved disruptive, as you’d imagine, although he seemed to weather it OK.
Beyond the mouse and rat, things branch out. That’s often where the mechanistic models stop, though – there aren’t as many disease models in the larger animals, although I know that some cardiovascular disease studies are (or have been) run in pigs, the smallest pigs that could be found. And I was once in on an osteoporosis compound that went into macaque monkeys for efficacy. More commonly, the larger animals are used for pharmacokinetics: blood levels, distribution, half-life, etc. The next step for most compounds after the rat is blood levels in dogs – that’s if there’s a next step at all, because the huge majority of compounds don’t get anywhere near a dog.
That’s a big step in terms of the seriousness of the model, because we don’t use dogs lightly. If you’re getting dog PK, you have a compound that you’re seriously considering could be a drug. Similarly, when a compound is finally picked to go on toward human trials, it first goes through a more thorough rat tox screen (several weeks), then goes into two-week dog tox, which is probably the most severe test most drug candidates face. The old (and cold-hearted) saying is that “drugs kill dogs and dogs kill drugs”. I’ve only rarely seen the former happen (twice, I think, in 19 years), but I’ve seen the second half of that saying come true over and over. Dogs are quite sensitive – their cardiovascular systems, especially – and if you have trouble there, you’re very likely done. There’s always monkey data – but monkey blood levels are precious, and a monkey tox screen is extremely rare these days. I’ve never seen one, at any rate. And if you have trouble in the dog, how do you justify going into monkeys at all? No, if you get through dog tox, you're probably going into man, and if you don't, you almost certainly aren't.
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January 22, 2008
Posted by Derek
There’s been a big trend the last few years in the industry to try to build our molecules up from much smaller pieces than usual. “Fragment-based” drug discovery is the subject of many conferences and review articles these days, and I’d guess that most decent-sized companies have some sort of fragment effort going on. (Recent reviews on the topic, for those who want them).
Many different approaches come under that heading, though. Generally, the theme is to screen a collection of small molecules, half the size or less of what you’d consider a reasonable molecular weight for a final compound, and look for something that binds. At those sizes, you’re not going to find the high affinities that you usually look for, though. We usually want our clinical candidates to be down in the single-digit nanomolar range for binding constants, and our screening hits to be as far under one micromolar as we can get. In the fragment world, though, from what I can see, people regard micromolar compounds as pretty hot stuff, and are just glad not to be up in the millimolar range. (For people outside the field, it’s worth noting that a nanomolar compound binds about a million times better than a millimolar one).
Not all the traditional methods of screening molecules will pick up weak binders like that. (Some assays are actually designed not to read out at those levels, but to only tell you about the really hot compounds). For the others, you’d think you could just run things like you usually do, just by loading up on the test compounds, but that’s problematic. For one thing, you’ll start to chew up a lot of compound supplies at that rate. Another problem is that not everything stays in solution for the assay when you try to run things at that concentration. And if you try to compensate by using more DMSO or whatever to dissolve your compounds, you can kill your protein targets with the stuff when it goes in. Proteins are happy in water (well, not pure distilled water, but water with lots of buffer and salts and junk like the inside of a cell has). They can take some DMSO, but it’ll eventually make even the sturdiest of them unhappy at some point. (More literature on fragment screening).
And once you’ve got your weak-binding low-molecular weight stuff, what then? First, you have to overcome the feeling, natural among experienced chemists, that you’re working on stuff you should be throwing away. Traditional medicinal chemistry – analog this part, add to that part, keep plugging away – may not be the appropriate thing to do for these leads. There are just too many possibilities – you could easily spend years wandering around. So many companies depend on structural information about the protein target and the fragments themselves to tell them where these little guys are binding and where the best places to build from might be. That can come from NMR studies or X-ray crystal determinations, most commonly.
Another hope, for some time now, has been that if you could discover two fragments that bound to different sites, but not that far from each other, that you could then stitch them together to make a far better compound. (See here for more on this idea). That’s been very hard to realize in practice, though. Finding suitable pairs of compounds is not easy, for starters. And getting them linked, as far as I can see, can be a real nightmare. A lot of the linking groups you can try will alter the binding of the fragments themselves – so instead of going from two weak compounds to one strong one, you go from two weak ones to something that’s worse than ever. Rather than linking two things up, a lot of fragment work seems to involve building out from a single piece.
But that brings up another problem, exemplified by this paper. These folks took a known beta-lactamase inhibitor, a fine nanomolar compound, and broke it up into plausible-looking fragments, to see if it could have been discovered that way. But what they found, each time they checked the individual pieces, was that each of them bound in a completely different way than it did when it was part of the finished molecule. The binding mode was emergent, not additive, and it seems clear that most (all?) of the current fragment approaches would have been unable to arrive at the final structure. The authors admit that this may be a special case, but there’s no reason to assume that it’s all that special.
So fragment approaches, although they seem to be working out in some cases, are probably always going to miss things. But hey, we miss plenty of things with the traditional methods, too. Overall, I’m for trying out all kinds of odd things, because we need all the help we can get. Good luck to the fragment folks.
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December 11, 2007
Posted by Derek
Man, do we ever have a lot of assays in this business. Almost every drug development project has a long list of them, arranged in what we call a screening cascade. You check to make sure that your new molecule hits your protein target, then you try it on one or more living cell lines. There are assays to check its potency against related targets (some of which you may want, most of which you don’t), and assays to measure the properties of the compound itself, like how well it dissolves. Then it’s on to blood levels in animals, and finally to a disease model in some species or another.
Not all these assays are of equal importance, naturally. And not all of them do what they’re supposed to do for you. Some processes are so poorly understood that we’re willing to try all sorts of stuff to get a read on them. I would put the Caco-2 assay firmly in that category.
Caco ("cake-o")-2 cells are a human colon cancer cell line. When you grow them in a monolayer, they still remember to form an “inside” and an “outside” – the two sides of the layer act differently, and they pump compounds across from one side to the other. This sort of active transport is very widespread in living systems, and it’s very important in drug absorption and distribution, and from a practical standpoint we don’t know much about it at all. Membranes like the gut wall or the lining of the brain’s blood vessels do this sort of thing all the time, and pump out things they don’t like. Cancer cells and bacteria do it to compounds they judge to be noxious, which covers a lot of the things we try to use to kill them. Knowing how to avoid this kind of thing would be worth billions of dollars, and would give us a lot more effective drugs.
The Caco-2 cell assay is an attempt to model some of this process in a dish, so you don’t have to find out about it in a mouse (or a human). You put a test amount of your compound on one side of the layer of cells, and see how much of it gets through to the other side – then you try it in reverse, to see how much of that flow was active transport and how much was just passive leak-through diffusion. The ratio between those two amounts is supposed to give you a read on how much of a substrate your compound is for these efflux pumps, particularly a widespread one called P-glycoprotein.
I have seen examples in the literature where this assay appears to have given useful data. Unfortunately, as far as I can remember, I cannot recall ever having participated in such a project. Every time I’ve worked with Caco-2 data, it’s been a spread of numbers that didn’t correlate well with gut absorption, didn’t correlate well with brain levels, and didn’t help to prioritize anything. That may be unfair – after all, I’ve had people tell me that ‘s worked out for them – but I think that even in those cases people had to run quite a few compounds through before they believed that the assay was really telling them something. The published data on these things can turn out to be a small, shiny heap on the summit of a vast pile of compost - the unimpressive or uninterpretable attempts that never show up in any journal, anywhere.
You can think of several reasons for these difficulties, and there are surely more that none of us have thought of yet. These are colon cells, not cells from the small intestine (where the great majority of absorption takes place) or from the blood-brain barrier. They're from a carcinoma line, not a normal population (which is why they're still happily living in dishes). But that means that they’re far removed from their origins, to boot. (It’s well known that many cell lines lose some of their characteristics and abilities as you culture them. They’re not getting the stimuli they were in their native environment, and they shed functions and pathways as they’re no longer being called for). There’s also the problem that they’re human cells, but they’re often used to correlate with data from rodent models. Our major features overlap pretty well (most mouse poisons are human poisons, for example), but the fine details can be difficult to line up.
But people still run the Caco-2 assay. I think that now it’s mostly done in the hope, mostly forlorn, that this time it’ll turn out to model something crucial to this particular drug series. A representative list of compounds that have already been through the pharmacokinetic studies is tried, and the results are graphed against the blood levels. And, for the most part, the plots look like soup thrown against a wall – again. The quest to explain these things continues. . .
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October 11, 2007
Posted by Derek
Now we open the sedate, learned pages of Nature Methods, a fine journal that specializes in new techniques in molecular and chemical biology. In the August issue, the correspondence section features. . .well, a testy response to a paper that appeared last year in Nature Methods.
“Experimental challenge to a ‘rigorous’ BRET analysis of GPCR oligimerization” is the title. If you don’t know the acronyms, never mind – journals like this have acronyms like leopards have spots. The people doing the complaining, Ali Salahpour and Bernard Masri of Duke, are taking issue with a paper from Oxford by John James, Simon Davis, and co-workers. The original paper described a bioluminescence energy transfer (BRET) method to see if G-protein coupled receptors (GPCRs) were associating with each other on cell surfaces. (GPCRs are hugely important signaling systems and drug targets – think serotonin, dopamine, opiates, adrenaline – and it’s become clear in recent years that they can possibly hook up in various unsuspected combinations on the surfaces of cells in vivo).
Salahpour and Masri take strong exception to the Oxford paper’s self-characterization:
“Although the development of new approaches for BRET analysis is commendable, part of the authors’ methodological approach falls short of being ‘rigorous’. . .Some of the pitfalls of their type-1 and type-2 experiments have already been discussed elsewhere (footnote to another complaint about the same work, which also appeared earlier this year in the same journal - DBL). Here we focus on the type-2 experiments and report experimental data to refute some of the results and conclusions presented by James et al.”
That’s about an 8 out of 10 on the scale of nasty scientific language, translating as “You mean well but are lamentably incompetent.” The only way to ratchet things up further is to accuse someone of bad faith or fraud. I won’t go into the technical details of Salahpour and Masri’s complaints; they have to do with the mechanism of BRET, the effect on it of how much GPCR protein is expressed in the cells being studied, and the way James et al. interpreted their results versus standards. The language of these complaints, though, is openly exasperated, full of wording like “unfortunately”, “It seems unlikely”, “we can assume, at best” “(does) not permit rigorous conclusions to be drawn”, “might be erroneous”, “inappropriate and a misinterpretation”, “This could explain why”, “careful examination also (raises) some concerns”, and so on. After the bandilleros and picadors have done their work in the preceding paragraphs, the communication finishes up with another flash of the sword:
In summary, we agree with James and colleagues that type-2 experiments are useful and informative. . .Unfortunately, the experimental design proposed in James et al. to perform type-2 experiments seems incorrect and cannot be interpreted. . .”
James and Davis don’t take this with a smile, naturally. The journal gave them a space to reply to the criticisms, as is standard practice, and as they did for the earlier criticism. (At least the editors know that people are reading the papers they accept. . .) They take on many of the Salahpour/Masri points, claiming that their refutations were done under completely inappropriate conditions, among other things. And they finish up with a flourish, too:
"As we have emphasized, we were not the first to attempt quantitative analysis of BRET data. Previously, however, resonance energy transfer theory was misinterpreted (for example, ref. 4) or applied incorrectly (for example, ref. 5). (Note - reference 4 is to a paper by the first people to question their paper earlier this year, and reference 5 is to the work of Salahpour himself, a nice touch - DBL). The only truly novel aspect of our experiments is that we verified our particular implementation of the theory by analyzing a set of very well-characterized. . .control proteins. (Note - "as opposed to you people" - DBL). . . .In this context, the technical concerns of Salahpour and Masri do not seem relevant."
It's probably safe to say that the air has not yet been cleared. I'm not enough of a BRET hand to say who's right here, but it looks like we're all going to have some more chances to make up our minds (and to appreciate the invective along the way).
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August 20, 2007
Posted by Derek
As I've mentioned before, advances in molecular biology have continued to make all sorts of brute-force approachs possible - things that would have been laughed at (or, more likely, not even proposed at all) a few years ago.
Another recent example of this is a paper earlier this year in Nature from the group of Michael White at UT-Southwestern. The authors selected a lung cancer cell line that's know to be very sensitive to Taxol (paclitaxel), and looked for possible targets that might increase the drug's effectiveness. (It's a good compound to pick for a study like this, since it's simultaneously quite effective and quite toxic).
So, how do you go fishing for such combinations? These days, you set up 21,127 experimental wells, each one contained some cells and some silencing RNA molecules targeting, one at a time, 21,127 different human genes. And you look to see if knocking down expression of any of those genes increased the potency of a normally ineffective dose of the drug. (There were four different siRNAs per gene, actually, and each one was run in triplicate with and without Taxol, leading to a Whole Lotta 96-well plates. I'm glad I'm not paying for all the pipet tips, I can tell you that for sure.)
As you'd imagine, working up the data from this kind of thing takes as long, or longer, than setting one up. After comparing everything to the control wells and to each other several different ways, they ended up with 87 candidate genes whose knockdown seems to make the drug more effective. Gratifyingly, many of these make one kind of sense or another - there are several genes, for example, that are known to be involved in spindle formation, which is the target of paclitaxel itself.
Even more interestingly, not all the hits were obvioius. Another group of genes code for parts of the proteasome. That part of the cell is targeted by Millennium's Velcade (bortezomib), and it's recently been reported that the combination of Velcade and paclitaxel is more effective than expected. And there's another combination that seemingly hasn't been tried at all: the experiment suggests that inhibitors of vacuolar ATP-ase should synergize with Taxol, and (as it happens) a compound called salicylihalamide A has been looked at for just that target. They tried this experimental combination out on the cells, and it seems to work well - so, in humans?
As a commentary in the New England Journal of Medicine on this work dryly put it, "This hypothesis should be tested." And so it should. I've always had doubts about how far one can extrapolate cell data in cancer studies, but this kind of thing will tell us for sure. If something hits from this work, more such studies will come pouring out - they're getting easier to do all the time, you know. . .
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July 10, 2007
Posted by Derek
There's a problem in the drug industry that people have recognized for some years, but we're not that much closer to dealing with it than we were then. We keep coming up with these technologies and techniques which seem as if they might be able to help us with some of our nastiest problems - I'm talking about genomics in all its guises, and metabolic profiling, and naturally the various high-throughput screening platforms, and others. But whether these are helping or not (and opinions sure do vary), one thing that they all have in common is that they generate enormous heaps of data.
We're not the only field to wish that the speed of collating and understanding all these results would start to catch up with the speed with which they're being generated. But some days I feel as if the two curves don't even have the same exponent in their equations. High-throughput screening data are fairly manageable, as these things go, and it's a good thing. When you can rip through a million compounds screening a new target, generating multiple-point binding curves along the way, you have a good-sized brick of numbers. But you're looking for just the ones with tight binding and reasonable curves, which is a relatively simple operation, and by the time you're done there may only be a couple of dozen compounds worth looking at. (More often than you'd think, there may be none at all).
But genomics/metabolomics/buzzwordomics platforms are tougher. In these cases, we don't actually know what we're looking for much of the time. I mean, we don't understand what the huge majority of the genes on a gene-chip assay really do, not in any useful detail, anyway. So the results of a given assay aren't the horserace leader board of a binding assay; they're more like a huge, complicated fingerprint or an abstract painting. We can say that yes, this compound seems to be different from that one, which is certainly different from this one over here but maybe similar to these on the left - but sometimes that's about all we can say.
Of course, the story isn't supposed to stop there, and everyone's hoping it won't. The idea is that we'll learn to interpret these things as we see more and more compounds and their ultimate effects. Correlations, trends, and useful conclusions are out there (surely?) and if we persevere we'll uncover them. The problem is, finding these things looks like requiring the generation of still more endless terabytes of data. It takes nerve to go on, but we seem to have no other choice.
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April 26, 2007
Posted by Derek
When I wrote about lousy animal models of disease a few days ago, there was a general principle at the back of my mind. (There generally is - my wife, over the years, has become accustomed to the sudden dolly-back panorama shots that appear unannounced in my conversation). It was: that a bad model system is much, much worse than no model system at all.
I've been convinced of that for a long time. When you have no model for what you're doing, you're forced to realize that you have no clear idea of what's going on. That's uncomfortable, to be sure, but you at least realize the situation. But when you have a poor model, the temptation to believe in it, at least partially, is hard to resist. Even if it's giving you the right answers at a rate worse than chance, you can still take (irrational) comfort in knowing that at least you're not flying blind - even as you do worse than the people who are.
There are many reasons to hold on to an underperforming model. Sometimes pride is the problem. I've seen groups that stuck with assays just because they'd invented them, even though the method was slowly wasting everyone's time. Never underestimate cluelessness, either. People will use worthless techniques for quite a while if they're not in the habit of checking to see if they're any good. But the biggest reason that useless procedures hang around, I'm convinced, is fear.
Fear, that is, of being left out in the middle of the field with no models, no insights, and no path forward at all. It's a bad feeling, rather scary, and rather difficult to explain to upper management if you're a project leader. Better, then, to hold on to the assays and models you have, to defend them even if you're not sure you trust them. With any luck, the project will end (although probably not happily) before the facts have to be faced. As Belloc advised children in other situations: "Always keep ahold of Nurse / For fear of finding something worse."
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March 12, 2007
Posted by Derek
I wanted to link tonight to the "Milkshake Manifesto" over at OrgPrep Daily. It's a set of rules for med-chem, and looking them over, I agree with them pretty much across the board. There's a general theme in them of getting as close to the real system as you can, which is a theme I've sounded many times.
That applies to things like "Rule of Five" approximations and docking scores - useful, perhaps if you're sorting through a huge pile of compounds that you have to prioritize, not so useful if you've already got animal data.
He also takes a shot at Caco-2 cells and other such approximations to figure out membrane and tissue penetration. I've never yet seen an in vitro assay for permeability that I would trust - it's just too complicated, and it may never yield to a reductionist approach.
I'm a big fan of reductionism, don't get me wrong, but it's not the tool for every job. Living systems are especially tricky to pare down, and you can simplify yourself right out of any useful data if you're not very careful. The closer to the real world, the better off you are. It isn't easy, and it isn't cheap, but nothing good ever came easy or cheap, did it?
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February 5, 2007
Posted by Derek
Here's an interesting press release on a potential new class of anticancer drugs. It has a nice hook ("Lab mistake leads to cancer finding!"), and the work itself isn't bad at all. It's an neat biochemical result, which might eventually lead to something. You have to know a bit about drug discovery and development to spot the problem, though - and not that many people do, which provides the ecological niche for this whole blog, frankly.
The discovery (from the University of Rochester) has to do with PPAR-gamma compounds, an area of research I've spent some time in. I didn't spend enough time there to understand it, mind you - no one has spent enough time to do that yet, no matter how long they've been at it. I wrote about some of the complexities here in 2004, and things have not become any more intelligible since then. The PPARs are nuclear receptors, affecting gene transcription when small molecules bind to them. There are, however, zillions of different binding modes in these things and they affect a list of genes that stretches right out the door. Some get upregulated, some down, and these vary according to patterns that we're only beginning to understand.
The Rochester group found that a particular class of compounds, the PPAR-gamma antagonists, had an unexpected toxic effect on some tumor cell lines. Their tubulin system was disrupted - that's a structural protein which is very important during cell division, and is the target for other known oncology drugs (like Taxol). The PPAR ligands seem to be messing with tubulin through a different route than anyone's seen before, though, and that definitely makes it worth following up on.
But the tone of the press release is too optimistic. (I should turn that line into some sort of macro, since I could use it twenty times a day). It mentions "high-dose" PPAR antagonist therapy as a possible cancer treatment, but take a look at the concentrations used: 10 to 100 micromolar. Even for cells in a dish, that's really hammering things down. And there's hardly any chance that you could attain these levels in a real-world situation, dosing a whole animal (or human). As blood levels go, those are huge.
But how about using more potent compounds? Of the three that are mentioned in the paper, BADGE is pretty dead, but the other two are actually quite potent. Tellingly, nothing happened at all with any of them up to 1 micromolar. These things will mess with other PPAR-gamma driven processes at much lower concentrations, so you have to wonder what's really going on here. And keep in mind that other PPAR compounds whose mode of action is roughly the opposite of these have been suggested as potential anticancer agents, too - this sort of thing happens all the time with nuclear receptors, and reflects their head-grabbing complexity.
This is still worth figuring out; don't get me wrong. There might be a new mechanism here that could lead to something, eventually, although it looks to be a tough problem. But that's the part of this work that's interesting - the level of activity seen here isn't. If I had a dollar for every compound that affects tumor cells at 50 micromolar, I wouldn't need to be sending my CV out these days.
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January 10, 2007
Posted by Derek
After yesterday's post, several people brought up the issue of inverted screening cascades. What happens when your compound works better in the mice than it did in the cells? Worse, what if it would have worked in the mice, but you never put it in there because it was so weak in the cell assays?
These kinds of questions are worth worrying about, because we almost never get a chance to answer them. For obvious reasons, the vast majority of compounds that make it into animal models are ones that looked good in the earlier steps. You'd have to think that the hit rate in vivo would be much lower for the dud compounds, but you'd have to be pretty arrogant to think that it would be zero, too.
As I recall (and I was just down the hall when it happened), the discovery of Schering-Plough's cholesterol absorption inhibitor came out of a compound that made it into an animal model and worked well, even though it turned out later to be a loser at the project's original target. (I believe that the in vitro assay was down that week for some reason, but one of my former colleagues will probably set me straight if I'm wrong about that). This sort of thing is food for thought, all right, extreme example though it might be. Even if your compounds don't suddenly hit a new target, there's still room for plenty of surprises in pharmacokinetics and the like.
But it would be unethical just to shove everything into animals, tempting though it is sometimes. And it would cost an insane amount, too - let's not forget that. But I do advocate getting as close to the real disease as quickly as possible. You can really waste time and effort by over-optimizing in vitro, all the time convincing yourself that you're doing the right thing.
Then there's the ultimate question in this line: how many compounds are there that don't work well in the animal models, but would be good in humans? I've wondered about this for many years, and I'm going to go on wondering, because data points are mighty scarce. Human biomarkers might eventually lead to some companies crossing their fingers and going into man with a compound that they expect to outdo the animal models. But it's going to take a lot of nerve. (And here's another complication - those upside surprises that might show up in the animals? How many of those are going to translate to humans, do you think? Not all of them, clearly. . .)
I have no doubt that there are many potentially useful drugs that are abandoned early. False negatives are probably on the shelves all around us. I don't see that as a strong argument against animal use (what, after all, is the alternative?), but it sure isn't a big argument for it, either. It's just, for now, the way things are.
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+ TrackBacks (0) | Category: Clinical Trials | Drug Assays | Drug Development
Posted by Derek
I've noticed a few stories making the rounds recently about possible new cancer therapies. Johns Hopkins has press-released the work of a group there on, and several news outlets have picked up on a British study on the effect of vanilloid agonists (such as the hot-pepper compound capsaicin) on cancer cells.
And all this is fine, until the word "cure" starts being tossed around. It always is. The number of times you see it, though, is inversely proportional to how reliable your favorite news source is. I wish the Nottingham and JHU people all the best in their research, and I hope that their projects lead to something good. But they have a long way to go, which you might not realize from the "Johns Hopkins Patents Cancer Cure" and "Hot Peppers Can Cure Cancer" headlines.
You see, these studies are all on cell cultures. I've worked on several cancer research programs, and I'm sure that other readers who've done the same can back me up here: unless you've seen cancer drug discovery work at close range, you may have no idea of just how many compounds work against cancer cells in a dish. It isn't that hard. I have absolutely no idea of how many thousands of compounds I could dig up from our files that will just totally wipe out a lot of the common cancer cell lines - in culture, that is.
We don't even bother looking at a compound unless it goes through cultured cell lines like a flaming sword. Problem is, a good number of those compounds will go through normal cells in the same fashion, which isn't exactly what the oncology market is looking for. And of the ones that are left, the ones that aren't hideous toxins - well, a lot of those hit the skids when they go into a live mouse model. Drug candidates that rip through the cell assays but fizzle in the mouse are very easy to come by. Anyone who does oncology drug discovery can furnish you with piles of them, and you're welcome to the darn things.
Now comes the really ugly part. We've ditched the nonselective cell killers, and we've shaken out the compounds that can't cut it in a live animal. How many of these actually work in human beings? Nowhere near as many as we'd like, that's for sure. AstraZeneca's drug Iressa is always useful to keep in mind. That one was going to be a huge hit, back when it was in development. But in real patients, well. . .for the vast majority of them, it just doesn't do much at all. There are a few responders (some of whom we can screen for), but otherwise, you'd have to call the compound a massive failure in the real world. Oh, but you should see it kick through the cell assays, and watch what it'll do for the mice.
Our assays just aren't that predicitive. It's a big problem, and everyone in the field knows it, but so far (despite crazy expenditures of time, money, and brainpower), no one's been able to improve things much. Anyone who does cancer work knows not to celebrate until the human trials data come back, and you'd better be careful even then. So the next time you read about some amazing thing happening to cells in a dish, well - wish the researchers luck. And go back to what you were doing before. There's time.
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October 22, 2006
Posted by Derek
"You like those scatterplots, don't you?", someone said to me the other day. And I can't deny it. On most projects that my lab has been assigned to, at some point I end up messing around with all the project data, plotting one thing against another and looking for correlations.
Often what I find is negative. Plotting liver microsome stability (a measure, in theory, of one of the major pathways for drug metabolism) against compound blood levels in animal dosing has rarely, in my perhaps unrepresentative experience, shown much of a correlation. In vivo blood levels are just too complicated, and influenced by too many other things. But I'm often surprised by how many people assume that there's a correlation - because, to a first approximation, it sort of makes sense that there might be - without actually having run the numbers.
That's a theme that keeps recurring: a fair amount of what people think they know about their project isn't true. I think it's because we keep reaching for simple explanations and rules of thumb, in hopes that we can get some sort of grip on the data. We give these too much weight, though, especially if we don't examine them every so often to see if they're still holding up (or if they ever did in the first place).
Another factor is good ol' fear. It's unnerving to face up to the fact that you don't know why your compounds are behaving the way that they are, and that you don't know what to do about it. It's no fun to plot your primary assay data against your secondary data and see a dropped-paintcan scatter instead of a correlation, because that kind of thing can set your whole project back months (or kill it altogether). One of the biggest problems in an information-driven field is that not everyone wants to know.
One time when I was giving the numbers a complete run-through, I noticed one of the plots actually seemed to have a fairly good shape to it. Y-axis was potency (plotted as -log), and there it was, actually increasing - broadly, messily, but undeniably - with the X-axis, which was. . .corporate compound number, the one assigned to each new compound as it was sent in for the assay. Oh, well. It showed that we were making progress, anyway. And at least nobody suggested that we attempt to give the compounds numbers from years in the future, in order to make them instant surefire winners. I've heard sillier suggestions.
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August 30, 2006
Posted by Derek
If you want to make your friends in the cell culture lab jump, just walk up behind them and shout "mycoplasma!" (What's that? You say you have no friends in the cell culture lab? Hmm. . .)
Mycoplasma is a scary word because they're scary little organisms. They're bacteria, just barely, running much smaller than usual and without any sort of cell wall. They also have the tiniest genomes you're likely to ever see - being parasitic allows them to get away with a pretty limited instruction set. They can cause diseases in humans and other animals (excellent review here), but they just love to hang out with your cultured cell lines, too.
From their (admittedly rather limited) perspective, what's not to like? Constant temperature, lots of food, and plenty of well-taken-care-of cells to mooch off of. Problem is, once they get in there, they alter the behavior of the cells they've infected, and you can't trust the results of your assays with them any more. Every cell culture lab tests for these things, and every one of them still has the occasional outbreak. It's the price of doing business. If the cells aren't precious, they're tossed - if they are, there are some antibiotics that will generally kill the little creatures off, but you still have to watch things closely for a while. (If you don't want to test them yourself, you can send samples to these guys, and they'll do it for you).
There have been periodic mycoplasma spasms in many research areas, as various groups have found that their results are suspect due to contamination. Since the little beasts pass right through filters that will strain out normal bacteria, and can't even be reliably seen under normal microscopy conditions in many cell cultures, a little paranoia is justified. Have you checked your cells recently?
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June 21, 2006
Posted by Derek
Here's a question for my readers in the research community: what assay have you dealt that turned out to be the biggest waste of time and effort? I can think of several strong nominees, but I'll lead off with one from quite a while ago.
This one happened in an antiviral group, and I believe that they were targeting a viral protease. Several chemists started cranking away on the lead compound, turning out analogs for the primary assay. But there was no decent SAR trend to latch on to. Things would look (briefly) sensible, then fall apart again, and there was only a scatter when you tried to correlate things with the secondary assay.
After some three or four months, the reason for all this became clear (it doesn't always, I have to note). Turns out, as it was told to me, that a biologist on the project had everything tested against the wrong enzyme. Who knows what it was, but it sure wasn't the protease of interest. What's more, he had apparently realized early on that it wasn't the right stuff, and was frantically working in the background trying to get the right stuff running. It never worked out. He ended up generated week after week of meaningless data, hoping that the project would go away. Instead, as it turned out, he went away (and not by choice).
So that's my entry. No doubt horrors will quickly emerge to beat it.
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June 18, 2006
Posted by Derek
Well, my last post on biological systems and their ingredients really touched a nerve (see here for an example). I guess I should, um, clarify my position before the leaky bottles of beta-mecaptoethanol start arriving by FedEx.
I already knew the reasons for several of the components I spoke about - EDTA, for example. And I realize that there's a reason for everything that's in there. But what throws me as a chemist is that some of these recipes seem to be handed on "just because they work" Does a particular enzyme prep need EDTA in it or not? Many times, no one checks, because it probably won't harm things and it's better to be on the safe side, so in it goes. It may be hard for a biologist to understand how odd that feels to a synthetic organic chemist, but I can tell you for sure that it does.
One of the commentors to the last post brought up an important point: biologists optimize for the function of a system. And that often means having a lot of buffers, chelators, cofactors, adjuvants, reducing agents, and chaperones floating around in there with your protein of interest, to keep it thinking that it's still in some kind of cellular environment, thus putting it in the mood to do what it's supposed to be doing. There's no point in trying to see how minimal you can make the system if it's working the way you want it to already.
But we chemists are minimalists. We optimize for the function of a system, too, but in our case, purity is usually a good first variable to tune up. The cleaner everything is in our reactions, the better it generally works. That means pure, distilled solvents, with no water in them. It means an inert gas atmosphere, so there's no reactive oxygen around. And it means that your starting materials and reagents should be as clean as you can practically get them, because when there's two percent of this or five percent of that in the flask, things often start to go wrong in unpredictable ways. When a reaction wipes out on us, the first thing we check is whether everything was clean enough.
So you can imagine how biology looks to an organic chemist, whose ideal reaction is a clear solution in a clear glass flask, with one pure solvent and two pure reactants cleanly converting to only one product. Biological systems, to us, look like trying to do science by adding squirts of barbecue sauce to bowls of beef stew. Of course, as the biologists know, the stuff in those bowls was derived from stew (and worse), and was born to the stuff. It won't work unless things achieve a certain level of stewiness, and the surest way to kill it would be to turn an organic chemist loose on it to clean it all up.
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June 15, 2006
Posted by Derek
You know, I mean no offense to all my pharmacologist friends and readers, but. . .do y'all really know why all those things are in your buffers and solutions? I've been wrestling with this the last few days, trying to straighten out my "vial thirty-three" problem, and it's been interesting.
There's some reducing agent in there, naturally. Can't have those thiols turning into disulfides and balling up the protein, I understand - but does something bad happen if it's not in there? Generally, no one finds out, because, hey, why mess with it? And there's some EDTA, and some salt, and their function is? Well, as far as I can tell, they're also in there because they've sort of always been. Same goes for the squirt of detergent (Brij-35 or some such), and the tiny bit of bovine serum albumin, of all things. It's just part of the old-fashioned recipe from Grandma's Protein Kitchen.
Now, organic chemistry has a little of this, true, but it hasn't reached quite the Ancient Runestone levels of enzymology. We like to use tetrahydrofuran (THF) for a lot of organometallic reactions, for example, but at least we know that that's because THF is a good co-ordinator to metal cations. At least we don't have six other trace constituents in there that we always use whether we need 'em or not. Another example is how we tend to stick to good ol' ethyl acetate and hexane to run TLC plates, rather than look into other solvent combinations that might do a better job - probably because there are just too many of them to investigate, and EtOAc/hexane works well enough.
And that, I think, is the problem that the biologists face. Biochemical systems are tricky. They have way too many variables, which means that their degrees of freedom have to be reduced just to get anything to work. So all sorts of recipes and rules of thumb are handed down. Not all of them are optimal, but they're mostly decent and will allow you to get on with the project without wasting too much time. Especially in the early part of a project, an immediate 70% effectiveness is worth a lot more than a 98% that would take you a month of work to tweak up to.
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August 18, 2005
Posted by Derek
One of the odd things about science is that you spend a good amount of time trying to prove that you don't know what you're talking about. At least, if you're doing it right, you should.
Take the first part of a drug discovery project, for instance. Most of them have a "primary assay", which is usually done against a purified protein in vitro, under fairly artificial conditions. Compounds that meet some standard of activity against that target then move on to the secondary assay, which is supposed to be aimed at the same process, but now it's done in living cells. That's a much tougher test. (It's a big leap from pure proteins to cells, about the same size as the leap from cells to whole animals.)
The hope is that the two assays will correlate with each other, but it's never a perfect fit. Generally, what you see is some of the active compounds dropping out for no apparent reason in the cell assay. If your target is in the cytoplasm, then there's always the possibility that these compounds don't penetrate into the cell as well as the others. Or they make it in, but are pumped right back out before they can get anything accomplished. Or perhaps they find some other (even tighter) binding site once they're inside, on some protein unrelated to the readout of your assay. There are always plenty of ways to explain these misfires.
And that's fine, as far as it goes. But if you don't double back and check these things out occasionally, you run the risk of fooling yourself. If your two assays don't correlate very well, it might be that cell penetration is lousing things up, sure - and it might also be that your assays aren't measuring the same thing. Or it could be that your target from the first assay isn't as important as you thought it was. These are the sorts of thing you really ought to be sure about.
So you need to keep yourself honest. Take some of your not-so-good compounds, the ones you'd normally discard after the first cut, and take them on to the cell assay regardless. They'd better not work! Test some of the compounds on a closely related cell line that doesn't have your target in it, if you've got some - is your target really the reason for the activity you're seeing?
Most of the time, you'll find that things are just fine. The inactive compounds really are inactive all the way through. But I've seen the exceptions occur, and more than once. You don't want to wait any longer than necessary to find out that your project is a dud. And worse yet, you really don't want someone else to find out for you. It leads to some of those awkward scenes we'd all rather avoid.
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August 1, 2005
Posted by Derek
As a drug discovery project moves along, we synthesize lots of new compounds, test them, and pick the best ones to make in large quantities. Simple, eh? Try your hand, then, at some of these questions, all of which have come up in the course of my career so far:
1. If you're running an experiment in vivo, and your control compound (from a competitor) is a highly active, hard-to-beat standard - how do you interpret your results when you know that this compound has made it to market and is no great shakes in human patients?
2. What do you do when you have to make a large batch of some compound for advanced pre-clinical work, and there's only one person in the whole department who can really get the crucial reaction to work? Do you tell people that you have a good large-scale route, or not?
3. How about a bit earlier in the game - how do you deal with it when you have a high-yielding, clean route to a key intermediate that lots of your people are using, but it uses a reaction that you know, for a fact, that the scale-up group won't touch later on?
4. How do you handle things when your primary biological assay keeps acting up - by factors of five to ten? Do you normalize the numbers to a standard each time and hope for the best, or do you start to doubt the usefulness of the whole assay?
5. For bonus points, how do you tell which numbers you've been getting are closer to the truth - the ones that say your compounds are really active, or the ones that say that they stink?
6. How do you interpret things when the in vivo assay tells you that your compounds have wonderfully long durations of action, but the blood levels tell you that they completely disappeared from circulation long before?
7. What does it mean when your best compound is intolerant of even slight structural changes? Do you just run with it (after all, you only need one compound, right?) Or do you hammer away trying to find something that can be safely modified in order to have a back-up?
Are there right answers? Well, presumably. I know what answers I'd give to some of these, but I make no guarantees that they're the right ones. . .
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June 19, 2005
Posted by Derek
I had a question a while back about how often researchers are fooling themselves when they think they've found a new signaling pathway or a new disease target. That one's pretty easy to answer, to a rough approximation: the less work you do, the better the chance that you're fooling yourself.
But it can take years before you know if you were right, so there's really not enough data to give a more quantitative answer. Take a notorious example, beta-amyloid in Alzheimer's disease. That's been noted as a sign of the disease every since Alois Alzheimer described it nearly one hundred years ago. Huge mountains of data have piled up since then about the disease and what might be causing it, but we're still not one hundred per cent sure if amyloid plaques in your brain give you Alzheimer's or if Alzheimer's gives you amyloid plaques in your brain. Most of the money is on the former, but it's not quite a sealed case yet.
The same uncertainty hovers around everywhere. Let's say you study a particular form of cancer, and you find that there's a particular kinase that's always found in greater than normal amounts in the tumor cells as compared to normal ones. Is that a new target for therapy? The answer is a firm, resounding, "maybe!"
Perhaps it's the real deal, but there are other enzymes that will step right in to do your kinase's job if you inhibit it - in that case, you'd better be prepared to take those on, too, or get ready to pack it in. Perhaps it's part of the real problem, but it's just a sideshow. If it's not the key or limiting step in any given pathway, inhibiting it won't do anyone much good. Or maybe it's there to phosphorylate the realculprit, in which case you should put some resources on tracking that thing down, too - it could be a better handle on the disease. But on the other hand, maybe your kinse is only acting downstream of that real culprit, phosphorylating something else entirely, which is an extreme example of the sideshow possibility mentioned above. Or it may be that this kinase is upregulated because it's part of a mechanism that's trying (unsuccessfully) to get the cancer cell to shut down. You probably wouldn't want to inhibit that!
Unraveling all this is not a job for the impatient, or for the light of wallet either, for that matter. So many of these pathways have turned out to be more complicated than anyone had ever imagined, that it's gotten to the point that people are questioning the whole reductionist-molecular-biology approach to drug targets. Eight or ten years ago, I would have considered that a radical or even crazy position. These days, I kind of want to sign up. . .
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May 27, 2005
Posted by Derek
I've started my Memorial Day weekend early (thus the mid-morning posting time.)
One of the comments to the previous post mentions the "let's make these compounds because we can" attitude, and points out that this was the fallacy underlying the combichem boom (and bust.) True enough - I should have clarified my point by saying that the compounds I was recommending were much more targeted. They're related to a structural series that we know we're interested in, but we haven't made tested anything from this particular group yet.
And, truth be told, I don't mind the blue-sky let's-make-some-compounds approach, as long as it's done in moderation. Throwing some interesting structures into the screening files is never a waste of time, although there are often more pressing things to do.
I don't approve of sending in things that are poor candidates for starting off an optimization project, though. If something with a molecular weight of 1300 hits in your assay, there's often not much you can do about it. That's at least twice a reasonable molecular weight, and large compounds like that often can't be cut down to size. Their binding modes are complex, interesting, and almost impossible to deal with in any practical manner, unfortunately. Getting a handle on things like this is a longstanding problem in drug discovery, so unless you feel like solving it, you shouldn't add to it.
Similarly, anyone who sends in reactive compounds like acid chlorides deserves a whack over the head. Those things, assuming they don't fall apart in storage, will tear up most assays they're run in, and it's not like they're ever going to be drugs. Same goes for things like organotelluriums and other out-there elements. I have a fairly liberal attitude (silicon-carbon bonds are OK with me), but there's a limit. If you think someone's going to be happy when your nickel complex hits in their enzyme assay, you are not in touch with consensus reality.
The problem with the combichem boom wasn't always the underlying compounds, although some of them were stinkers (and most of them sure could have been cleaner.) I think the real trouble was how oversold the whole thing became. If you weren't buying or cranking out huge libraries, you were missing the gold rush. Vast untapped veins of drug leads were out there in those hills! Without the hype, things wouldn't have looked so bad. But hey, without the hype, most of those libraries wouldn't have been made. . .
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March 2, 2005
Posted by Derek
I spoke yesterday about going through lists of chemical structures, looking for ones that we might want to keep in our screening libraries and, simultaneously, for the ones that we never want to see again. There's a paper from last year in the Journal of Medicinal Chemistry (47, 4891) that's an embarrassing reminder of just how hard it is to do that consistently.
It's from an effort led by Michael Lajiness at what was then Pharmacia/Upjohn (and is now Pfizer, which might account for the lead author now being at Eli Lilly, if you can follow all that.) They had about 22,000 compounds to sort through to see if they wanted to purchase them for the screening files, so they broke them out into 11 lists of 2000 compounds each. Thirteen medicinal chemists volunteered (or were volunteered, unless I miss my guess) to go over these lists. Eight members of the team reviewed two separate lists, and one wild man reviewed three.
The authors of the paper took a look at the list of rejected compounds from each reviewer, correctly (in my view) believing that this list is more significant than the list of what was accepted. After all, an ugly structure that makes it through may well never hit in an assay, and if it does it'll go through many more layers of scrutiny. A structure that's rejected, though, disappears from the company's screening universe forever. False negatives could have bigger consequences than false positives.
So, when more than one chemist went over the same list of 2000 compounds, how similar were their reject lists? Not very! On the average, two medicinal chemists would agree to reject the same compounds only about 23% of the time. (I knew that the overlap wasn't going to be perfect, but that's a lot worse than I was expecting.)
To continue the punishment, the lists had each been, without the knowledge of the reviewers, seeded with the same set of 250 compounds, all of which had been rejected by a previous review. The chemist-to-chemist rejection overlap in this smaller set of potential losers was still only 28%. Not as much of an improvement as you'd hope for. . .
And now the whipped topping and chocolate sprinkles: recall that many of the reviewers did more than one list. That means that they got to see that same group of 250 compounds more than once, in the context of different lists. How did the same people do when they saw the exact same compounds? They only rejected them about 50% of the time, it pains me to report.
It looks as if potential drug leads follow the same rule as Tolstoy's comment in Anna Karenina: Good compounds are all alike, while bad compounds are each bad in their own way. It seems that the Pharmacia reviewers didn't reject many good structures, but they let varying (and inconsistent) numbers of bad ones through (with no particular correlation to their industrial experience, I should add.) The possible reasons advance for this variation include personal bias, inattention (and I wouldn't minimize that factor, not in a list of 2000 compounds), and a general human inability to sort through large complex data sets.
And right at the end, the authors allude to a bigger problem: If this is how consistently our med-chem intuition works, how well does it serve us during drug development? In a research project, there are plenty of decisions to be made about what compounds to make, what structural series to emphasize and which ones to set aside. Just how bad at this are we, really? I'm afraid to find out.
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March 1, 2005
Posted by Derek
How do we accumulate our piles of test compounds over here in the drug industry? Well, mostly, we make them ourselves. But we also buy collections of compounds. Some of them are from other companies that have gone under, and some of them are from outfits that do nothing but produce libraries of (putatively) interesting compounds. (You can buy some that they've already shared with other companies for a discount, or you can have a new one made up for you for a higher price.) That was a much hotter business ten years ago than it is now, but it's still going.
And we buy compounds from university labs. That's a little-known way (outside of chemistry, at any rate) that professors and their research groups earn some extra spending money. (Naturally enough, this practice also leads to some elbow-throwing between the research groups and the universities involved when each of them want a piece of the profits.) We generally pay a set price per compound, but you wouldn't want to buy every single thing that academia offers. Some of the stuff is quite interesting and useful, but many of the structures will become drug leads only when swine take to the skies.
I've helped evaluate lists of potential purchases before, and they're a mixed bag indeed. Once I looked over a collection from Leo Paquette's group at Ohio State. Now, he and his group did a lot of nice chemistry over the years, and there were a lot of useful compounds on the list. But there were also plenty of intermediates from his famous synthesis of dodecahedrane. Those represented a tremendous amount of effort from his students and post-docs, and were part of the history of organic synthesis.
And I didn't want us to buy them. For one thing, they didn't look much like drugs to me. "But what if they hit in our assays?" said one of my colleagues, trying to make the case that we should buy some. "That's what I'm worried about," I said. What indeed? If one of those structures turned out to be a wildly potent ligand for some protein target, what exactly were we going to be able to do about it? Follow the twenty-nine step synthesis to make more of it? No, in this case, I thought we were better off with nothing than with something we could never use. We passed.
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January 18, 2005
Posted by Derek
I've mentioned before that one of our big problems in the drug industry seems to be finding compounds that work in man. I know, that sounds pretty obvious, but the statement improves when you consider the reasons why compounds fail. Recent studies have suggested that these days, fewer compounds are failing through some of the traditional pathways, like unexpectedly poor blood levels or severe toxicity.
In the current era, we seem to be getting more compounds that make it to man with reasonable pharmacokinetics (absorption from the gut, distribution and blood levels, etc.) and reasonably clean toxicity profiles. Not all of them, by any means - there are still surprises - but the stuff that makes it into the clinic these days is of a higher standard than it was twenty years ago. But that leaves the biggest single reason for clinical failure now as lack of efficacy against the disease.
That failure is the sum of several others. We're attacking some diseases that are harder to understand (Alzheimer's, for example), and we're doing so with some kind of mechanistic reason behind most of the compounds. Which is fine, as long as your understanding of the disease is good enough to be pretty sure that the mechanism is as important as you think it is. But the floor is deep with the sweepings of mechanistically compelling ideas that didn't work out at all in the clinic - dopamine D3 ligands for schizophrenia, leptin (and galanin, and neutropeptide Y) for obesity, renin inhibitors for hypertension. I'm tempted to add "highly targeted angiogenesis inhibitors for cancer" to the list. The old-fashioned way of finding a compound that works, and no matter how, probably led to fewer efficacy breakdowns (for all that method's other problems.)
Another basic problem is that our methods of evaluating efficacy, short of just giving the compound to a sick person and watching them for a while, aren't very reliable. If I had to pick the therapeutic area that's most in need of a revamp, I'd have to say cancer. The animal models there are numerous, rich in data, and will tell you things that you want to hear. It's just that they don't seem to do a very good job telling you about what's going to work in man. I will point out that Iressa, for one, works just fine in many of the putatively relevant models.
The journal Nature Reviews: Drug Discovery (which is probably the best single journal to read for someone trying to understand pharma research) published a provocative article a couple of years ago on this subject. The author (the now late) David Horrobin, compared some parts of modern drug discovery to Hesse's Glass Bead Game: complex, interesting, internally consistent and of no relevance to the world outside. They got a lot of mail. Now the journal has promised a series of papers over the next few months on animal models and their relevance to human disease, and I'm looking forward to them. We need to hit the reset button on some of our favorites.
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May 24, 2004
Posted by Derek
Before getting started, I'd like to recommend the discussion going on in the Comments section of the "All the Myriad Ways" post below. If you find the topic of gene patents at all interesting, it's worth keeping up with. Me, I'm just watching for now, feeling like Teresa Nielsen Hayden as the discussion takes off on its own. (I show up in her comments section every so often myself, although I largely stay out of the political discussions because I think they'd throw things at me.)
On to the main topic tonight. There's an article in the latest Nature Reviews: Drug Discovery called "Prospects for Productivity" from Bruce Booth and Rodney Zimmel at McKinsey Consulting. They're talking about the now-familiar drug drought that seems to have affected everyone the last few years. It's real enough, although they make the point (which I've brought up myself, in a column for Contract Pharmamagazine) that people have been complaining about a drug shortage for decades.
Booth and Zimmel do a good job of running down the usual suspects. In their order, they have:
1. Lack of payoff from genomics. This one, they say, has "clearly driven part of the productivity decline." I can second that, because I (and friends of mine around the industry) have seen it at work right in front of them. There was a panic that made everyone start working on genome-derived targets, long before we knew enough to accomplish anything. In most cases, we still don't.
2. Poor chemical libraries. This is an earlier problem, but one whose effects are still working their way through the portfolio. The combinatorial chemistry craze (the craze before genomics, if you're keeping score at home) caused a lot of people to make a lot of compounds that had no chance of ever becoming drugs. Why? Because they could make them! And someone else might make them first! We're smarter now, theoretically. B & Z don't go into the details, but this one hit some companies harder than others, depending on how early and how hard they fell for combichem evangelism. Some careers never really recovered.
3. Tougher regulation. B & Z discount this, for the most part, as whining from the drug companies (not their exact wording!) They're probably right, although they correctly note that seemingly minor changes at the FDA have ended up costing huge amounts of money and time on our end. But this still isn't the major thing hurting us, not that it isn't still fun to complain about.
4. Tougher internal scrutiny. This is a real one, too, although it's hard to quantify. We've gotten more cautious over the years, as we've tried to keep from taking drugs deep into clinical trials before finding out that they have some ruinous problem. The early-stage filters and hurdles we've put in probably work a little too well, though. Unnervingly, there are any number of drugs on the market now that never would have made it through the current regimes. The verdict all depends on how many loser projects we're avoiding at the same time, a number that's pretty much unknowable. Ah, what an industry.
5. Unfulfilled technological hopes. This overlaps with some of their other categories (such as all that genomics money we're never going to see again). But Booth and Zimmel draw special attention to the problem of the industry spending huge amounts on better and better in vitro technology (as in the previous point), only to find that it still doesn't translate well to animal models, much less clinical practice. Presumably, we're eventually going to figure out what we're doing, but we're probably going to hose away still more cash while we're doing it, too.
6. Too big to innovate? Readers will recognize this as a particular favorite of mine, what with my happy attitude toward huge mergers. Proponents of such would do well do digest this quote: "Whether size itself is good or bad for R&D remains to be seen, (Heresy! Says the board at Pfizer! - DBL) but the simple fact is that a greater proportion of innovation is occurring outside the industry leaders." Their estimates show a meaningful decline just over the past seven years or so, which is rather alarming for the big guys.
Not a bad roundup. The article has a lot of other useful stuff in it, too; I highly recommend it. They have a few ideas for getting out of our current fix, which I'll try to get to in a future post. None of them strike me as particularly resonant rallying calls ("Improve investment discipline"), but that doesn't mean that they're wrong, either.
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April 22, 2004
Posted by Derek
I mentioned the other day that not everything in that Stuart Schreiber interview sounded sane to me, (although more of it does than I'd expected). The interviewer, Joanna Owens, asks him to expand on a statement he made about ten years ago: famously (in some circles, at any rate) Schreiber said that he wanted to - and thought that eventually he could - produce a small-molecule partner for every human gene.
A worthy goal, to be sure, but a honking big one, too. To his credit, though, Schreiber isn't making light of it:
". . .that challenge understates what we really want to do, which is to use small molecules to modulate the individual function(s) of multifunctional proteins, activating or inactivating individual functions as necessary. This is one of the differences between small molecules, for example, and the knockout of knowckdown technologies, where you inactivate everything to do with the protein of interest."
Note how things have appropriately expanded. There are a lot more proteins than there are genes (a lot more, given the surprisingly lowball figure for the total size of the human genome), and the number of protein activities is several times larger than that. He's absolutely right that this figure is the real bottom line. But here comes that Muhammed Ali side of his personality:
"Small molecules allow you to gain control rapidly, and can be delivered simply but, most importantly, we've shown that we can discover molecules that only modulate one of several functions of a single protein. . .(the scientific community has) identified 5000 out of the required 500,000 small molecules, which is similar to where the Human Genome Project was in year two of its 12-year journey. That might be a useful calibration - optimistically, we're ten years away."
Midway through that paragraph is where I start pulling back on a set of imaginary reins. Whoa up, there, Schreibster! Let's take the assumptions in order:
Small molecules allow you to gain control rapidly. . . Compared to transcription-level technology, this is largely correct. But the effects of small-molecule treatment often take a while to make themselves known, for a variety of reasons that we don't fully understand. The problem's particularly acute in larger systems - look at how long it takes for many CNS drugs to have any meaningful clinical effect. And these complex systems have other weird aspects, which make the phrase "gain control" seem a bit too confident. U-shaped dose-response relationships are common. Look at what you find in toxicology, where you see threshold effects and even hormesis, with large and small doses of the same substance showing opposite effects.
. . .and can be delivered simply. . . Well, when they can be delivered at all, I guess. But there more of them that come bouncing back at us than we'd like. In every drug research program I've been involved with, there are plenty of reasonable-looking compounds that hit the molecular target hard, but then don't perform in the cellular assay. You can come up with a lot of hand-waving rationales: perhaps the main series of compounds is riding in on some sort of active transport and these outliers can't, or they're getting actively pumped back out of the cell, or they hit some other sinkhole binding site that the others escape, and so on. Figuring out what's going on is an entire research project in itself, and rarely undertaken. Every time someone tells me that drug delivery is simple, I can feel my hair begin to frizz.
. . .we've shown that we can discover molecules that only modulate one of several functions of a single protein. . . True enough, and a very interesting accomplishment. But the generality of it is, to put the matter gently, unproven. It would not surprise me at all if there turn out to be many proteins whose functions can't be independently inhibited. The act of binding a small molecule to alter one of the functions would cause the other ones to change. And a bigger problem will be distinguishing these effects from the consequences of actually taking out that first function cleanly: how will you know when you've altered the system?
. . .which is similar to where the Human Genome Project was in year two. . . True, but that and forty dollars will get you an Aldrich Chemical can opener. The comparison isn't just optimistic - it's crazy. The problems that the genome sequencers faced were engineering problems - difficult, tricky, infuriating ones, but with solutions that were absolutely within the realm of possibility. Faster machines were made, with more computing power, and new techniques were applied to make use of them.
But as I've been saying, I'm not sure that the Maximum Inhibitor Library that Schreiber's talking about is even possible at all. Don't get me wrong - I hope that it is. We'll learn so much biochemistry that our heads will hurt. But its feasibility is very much open to question, to many questions, and we won't even begin to know the answers until we've put in a lot more work.
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March 17, 2004
Posted by Derek
I sent off a manuscript to a chemical journal not long ago. There's an initial flurry of e-mail activity when you do that - we've received your manuscript, we've sent your manuscript out to reviewers - and then a more or less prolonged period of silence. The next thing you hear is whether the paper's been accepted or not, along with the referee comments.
Mine were the usual mix of helpful suggestions and things that make you roll your eyes. One of the latter was a comment that immediately pegged the reviewer as someone from academia. They noticed that the data from our primary assay, against a human enzyme, didn't always match up well with the secondary assay, which was against a rodent cell line, and wanted some more explanation for why some groups of compounds weren't active.
To which I could only reply "You and me both!" That's a constant problem in medicinal chemistry. A majority of projects are set up in that format, with a cell-free assay as the first filter, then cells expressing the target as the next hurdle. And it's just about inevitable that there will be whole groups of compounds that work fine in the first assay, but just wipe out in the second one.
Why should that be? As far as we know, there are two general ways that compounds can get into cells: passive transport and active transport. The passive route is just diffusion across the cell membrane: "Wonder drug? You're soaking in it!" It's affected by broad trends in molecular size, polarity, and so on. The second route is when your compound hitches a ride on some transport protein.
There are hundreds of these things involved in opening up channels into and out of the cell. Some of the famous ones move ions (calcium, potassium and the like), which makes sense. Those are small and electrically charged, so they're not going to just wander across the membrane on their own, and the cellular machinery depends on keeping such membrane potentials tightly controlled. Then there are transporters for large proteins, which are too huge to diffuse by themselves, and for essential classes of small molecules like fatty acids.
No one's sure how many of these things exist. Just in the last few years, there's been a whole new class discovered, the aquaporins, which (as the name implies) move water itself across the cell membrane. You wouldn't think that you'd need an active transport system for that (at least a lot of people didn't think so) but the things turn out to be ubiquitous. If there's a transporter for water, there can be one for anything.
The efflux pumps I spoke of the other day in antibiotic resistance are active transport proteins, too, naturally. Those complicate things by taking compounds that diffuse perfectly nicely into cells and making them look like they're bouncing off a layer of armor plate instead. You'll also get that effect when your standard project compounds ride in on some transport system, then you make some small structural change which causes your drug to lose its train ticket.
It's a lot of work to figure out what's going on, and often you can't get a handle on it, anyway. Many of these transport systems don't have specific inhibitors, so it's not like you can switch them off one by one to see which one is the problem. If you have a good way to monitor your compound on a cellular level (like a fluorescent probe), you can actually see the things going in and being pumped back out sometimes, or you can see if the transport system can be saturated as you load up on drug. But there's no way you can do this for hundreds of drug candidates on every project.
So, it's just one of those things. I'm on a project right now that has the same thing going on. We make tiny changes to our molecules, and the cell activity suddenly gets a hundred times better, or a thousand times worse. But are these trends going to translate to the cells inside a real animal? And if they do, will they be relevant to the active transport systems in humans? Bite your tongue.
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| Category: Drug Assays | The Scientific Literature
February 25, 2004
Posted by Derek
Credit where it's due! Yesterday I mentioned the original chemist who started the ezetimibe story, but I should note that the drug itself was synthesized by another former colleague of mine, Stuart Rosenblum. He and a host of others developed a huge series of analogs, which built in more acitivity and greater in vivo stability. Just the way drug development is supposed to work, actually.
This drug is also used as an example in a very interesting front-page Wall Street Journal article yesterday. It's a public version of a debate that's been going on inside the industry for a few years now: has the huge increase in compound screening (and compound synthesis) done any good? The article does a pretty good job discussing the issue, although it does mix the two technologies together a bit. It's a very interesting topic, which I'll return to here soon.
And while you're at it, the same issue of the newspaper has (in the Money and Investing section) a nice piece on how drug companies tend to bury news of clinical failures. Different companies handle this differently, of course, but with some of them you really have to watch closely. The article makes the same point I did a while ago - investing in this industry is more of a gamble than most people think. Don't just buy one company's stock if you're looking at biotech and pharma - there's no way you can really know what's going on. Spread your risk.
These articles confirm the Journal's status as the best newspaper when it comes to covering the drug business. The New York Times tries, and sometimes has good work in it, but isn't in the same class. As for magazines, I'd say that Forbes does very well, as does their online site with its copious coverage from Matthew Herper.
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+ TrackBacks (0) | Category: Cardiovascular Disease | Drug Assays | Drug Industry History
February 24, 2004
Posted by Derek
There's a paper in the latest issue of Science from a team at Schering-Plough that may have tracked down how the company's cholesterol absorption inhibitor (Zetia, ezetimibe) works. That news really takes me back.
It's been years now, so it won't do any harm to mention that I used to work there. I had a ringside seat for the early years of that project, because it all happened right around the corner from my old lab. Ezetimibe was discovered fortuitously when one of my colleagues synthesized and sent in the original structures of the class for a project targeting a cholesterol handling enzyme known as ACAT. I believe that the in vitro assay was down that week, so the compounds went into the open slots for mouse testing, where they worked better than anything they'd seen. But when the protein assay came back on line, it was discovered that the compounds had no affinity for ACAT at all. Food for thought, that was.
The chemist involved was named Duane Burnett, and a search for "Burnett DA" in Pubmed will send you to most of the chemistry literature on the subject (along with this review). He had indeed hit on some features of a cholesterol binding site (which was his aim, based on blackboard-level structure modeling - no computers involved.) The compounds seemed to hit an unknown target in the small intestine that helped transport dietary cholesterol. The search for the protein involved began in about 1993, and seems to have concluded successfully in 2002-2003, years later than anyone thought it would take.
In the mid-1990s, all the classic methods for tracking down an unknown binding site were tried. The lead structure was biotinylated, modified with radiolabels, photoaffinity tags, and fluorescent groups (along with various combinations of these.) None of these methods identified the target.
They finally tracked down the protein by brute force genomics, using a cDNA library prepared from rat intestinal lining, coupled with sequence searching for the features you'd expect in a transmembrane protein with a steroid binding site. The evidence seems clear that the protein they've found is a key for ezetimibe's actions, but - most oddly - it still doesn't seem to bind to the protein. That would certainly explain the failure of all those modified compounds to pull out the target, but it does make you wonder what's going on. (Is there another real target? But if so, why wasn't that identified through the modified compounds? And so on.)
It took a lot of nerve to go on with that project, and I have to salute the people who kept it going. As with many other successful projects, there were several points along the way where it seemed like the whole effort was going to fail. As it turns out, ezetimibe is one of the main (few?) bright spots in Schering-Plough's portfolio. Merck, their eventual partner for the drug, values it pretty highly, too. I'm glad I got the chance to see it happen.
Credit where it's due! I should note that ezetimibe itself was synthesized by another former colleague of mine, Stuart Rosenblum. He and a host of others developed a huge series of analogs, which built in more acitivity and greater in vivo stability. Just the way drug development is supposed to work, actually.
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February 18, 2004
Posted by Derek
Everyone in the industry would like to do something about the failure rate of drugs in clinical trials. It would be far better to have not spent the time and money on these candidates, and the regret just increases as you move further down the process. A Phase I failure is painful; a Phase III failure can affect the future of the whole company.
So why do these drugs fall out? Hugo Kubinyi, in last August's Nature Revews Drug Discovery suggests that it's not for the reasons that we think. As he notes, there are two widely cited studies that have suggested that a good 40% of clinical failures are due to poor pharmacokinetics. That area is also known in the trade as ADME, for Absorption, Distribution, Metabolism, and Excretion, for the four things that happen to a drug once it's dosed. And we have an awful time predicting all four of them.
Of the four, we have the best handle on metabolism. In the preclinical phase, we expose compounds to preparations from human liver cells, and that gives a useful guide to what's going to happen to them in man. We also expose advanced compounds to human liver tissue itself, which isn't exactly a standard item of commerce, but serves as a more exacting test. Most of the time, these (along with animal studies) keep us from too many surprises about how a compound is going to be broken down. But the other three categories are very close to being black boxes. Dosing in dogs is considered the best model for oral dosing in humans for these, but there are still surprises all the time.
That 40% figure has inspired a lot of hand-wringing, and a lot of expenditure. But Kubinyi says that it's probably wrong. Going back over the data sets, he says that the sample set is skewed by the inclusion of an inappapropriately large group of anti-infective compounds with poor properties. If you adjust to a real-world proportion, you get an ADME failure rate of only 7%.
Now, when this paper came out, I think that there was consternation all over the drug industry. (There sure was among some of my co-workers.) The ADME problem has been common knowledge for years now, it was disturbing to think that it wasn't even there. So disturbing, it seems, that many people have just decided to ignore Kubinyi's contention and carry on as if nothing had happened. There have been big investments in ways to model and predict these properties, and I think that many of these programs have a momentum of their own, which might not be slowed down by mere facts.
The natural question is what Kubinyi thinks might be our real problem. In his adjusted data set, 46% of all failures result from lack of efficacy in Phase II. He admits that some of these (in either approach to the data) might still reflect bad pharmacokinetics, but still maintains that poor PK has made a much smaller contribution than everyone believes. Here's his drug development failure breakdown, which makes his point:
46% drop out from lack of efficacy
17% from animal toxicity (beyond the usual preclinical tox)
16% from adverse events in humans
7% from bad ADME properties
7% from commercial decisions
7% from other miscellaneous reasons
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+ TrackBacks (0) | Category: Drug Assays | Drug Development | Pharmacokinetics | Toxicology
January 8, 2004
Posted by Derek
A fellow researcher, working over at The Competition, sent along a couple of good questions. He's a biologist, and was reading the posts here earlier this week about compound repositories. He writes:
"I would like to pose to you a question I have tried for years to get chemists to address: why has no one yet come up with a better "universal" solvent than DMSO for dissolving compounds for routine screening in assays? As you point out, DMSO has numerous liabilities for this purpose (perhaps more on the biological side), and yet we all continue to use it routinely, because there doesn't seem to be a better alternative. In the various screening labs in which I have been involved for the past dozen or so years, we have tested a number of possible alternative solvents on an ad hoc basis, none of which seemed any better. Surely modern organic chemistry can do better?"
All I can offer my colleague is this: modern organic chemistry may not be quite as powerful as you've been led to believe. Perhaps the problem is that you've been listening to too many of us modern organic chemists. We do tend to go on.
He's right that DMSO has its down side, and there are some that I didn't even mention. For one, DMSO and air make for a decent oxidizing system, enough to cause trouble in electron-rich molecules. Things will start to change color on you in a DMSO solution that's been left open. And it does have its biological problems. Too much DMSO in an assay system will cause the proteins involved to change their conformations, probably inactivating them. At the very least, your data start to go haywire.
Is there anything we mighty chemists can do about this? Well. . .actually. . .no, probably not a whole lot. The problem is, anything that has "universal solvent" properties is going to have "universal denaturant" properties when it comes to large biomolecules. Proteins, carbohydrates, and nucleic acids are made to hang around with water. Anything that isn't water is going to cause trouble, sooner or later.
Coming up with a solvent that acts just like water, but isn't, may well be impossible. Water's just too weird. Its boiling point and viscosity are way off the estimates you'd get from looking at related things like ammonia and hydrogen sulfide, due to its extraordinary hydrogen-bonding powers. And it's those bonds that do the trick with biomolecules. It's sui generis - there's no other molecule that small that can do hydrogen bonds that strongly, at those angles, in two directions at once.
DMSO gets by because it's also small (although not as small as water.) It's the smallest sulfoxide possible, so it has the most character. The key is that the sulfur and oxygen atoms in the sulfoxide bond have a lot of charge on them - the oxygen's nearly a minus charge; the sulfur's nearly a plus. That dipole lets it really line up with any polar groups a molecule might have, and its two methyl groups give it a chance to dissolve some hydrocarbons that water won't accept. (Larger sulfoxide analogs just add greasiness, and are less powerful solvents. That's the wrong direction, and you can't go any further the other way.)
And all the other attempts at DMSO substitutes tend to follow that same path, things that are polar because of their high dipole moments. Some of the also-rans are N-methylpyrrolidone (NMP), DMPU, and the toxic HMPA. None of them are as good as DMSO, and they all suffer from its disadvantages. There may well be some funky structures out there that haven't been given a fair hearing, but I sure can't think of many right now. I'm afraid that we're just going to have to live with DMSO, and respect water's magical powers for what they are.
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January 5, 2003
Posted by Derek
We spend a lot of time in drug discovery thinking about ratios. As we accumulate data about our compounds, we start ranking them by how selective they are - "This one's 10x versus the other receptor subtype and that one's 50x," you'll hear someone say, or "We've got to get compounds at least 100-fold over that other enzyme or side effects are going to kill us." Generally you have several secondary assays that the compounds have to jump through along the way, and the ratios are what everyone looks at.
And when compounds start to get dosed in animals, you try to look for cutoffs that can tell you which compounds are worth trying in longer assays. Maybe they only work, for example, when the ratio of peak blood concentration, Cmax (or time-averaged total exposure, AUC) to the binding potency is 100x or more. (Other things being equal, that means you could get the desired effect with a really potent compound that doesn't get into the system all that well, or a weaker compound that hangs around a long time.)
So, how good are these numbers? There's the problem - not as good as we tend to think. Even experienced medicinal chemists can get caught over-interpreting data when it's expressed in ratio form. The problem is, on a graph we all expect to see error bars (and we get pretty antsy if they aren't there - it means someone didn't run the experiment enough times, or they're sloppy about making their graphs, or they're trying to pull a fast one.) And for single data points from an assay, we try to remember the variability - looking at the various runs that went into the number you see is always recommended.
But when things get expressed as ratios, all that disappears. We throw around "40-fold" as if it's different from "20-fold," and it takes a conscious effort to remember that it almost certainly isn't. The variability of biological assays would completely curl the hair of a physicist or physical chemist - at times it curls ours in med-chem, and we're supposed to be used to it. Plus or minus 100% is considered a nice, tight assay for many systems - really, it is. They get worse as the system gets more realistic, too - cloned proteins are usually tighter than isolated ones, which are invariably tighter than cell assays, which are certainly tighter than tissue preps, and anything's less variable than some of the animal assays. If you have one of the jumpier ones in the denominator of your ratio, well, prepare to get all sorts of crazy results.
This is why no one, and I mean no one of any competence at all, really trusts "N of 1" data, especially if it's saying something interesting or unusual. If you haven't run the assay again, you're often better off not telling anyone about your numbers until you have. I have seen many people fall flat on their faces because they couldn't resist trumpeting some startling result that later turned out to be junk. It's tough, because we live for startling results. But we die by error bars, and they rule the drug discovery world in the end.
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October 15, 2002
Posted by Derek
I mentioned in passing that getting cells to express a new gene's protein is voodoo. That's pretty close to the technical term of the art for it. Gene therapy is the high-profile application of the technique, but it's the bread and butter of molecular biology. I can tell you that a lot of drug company research would come to a lurching halt without cloned proteins.
One of my "Laws of the Lab" (more of those are on the way) is "When there are twenty ways in the literature to do something, that means that there is no good way to do it." This applies, in truckloads, to protein expression. When you consider the number of different cell lines you could try and the number of vectors you can use to get your DNA into them, you're already faced with plenty of choices.
Then you have the various things you can add to the main DNA sequence to try to get things to work, once they're in the cell. A good deal of protein-expression time is spent trying out different promoters, sequences that flank the one you're interested in that serve to lure the transcription machinery over to it. "Pick me! I'm important! You need lots of me, and you need it now! And get it right, will you?" is the sort of message these sequences are intended to send. After all, it does no good to insert DNA that doesn't get read at a useful level.
You generally want as much protein production as you can get (although it's possible overdo it, in which case you might start getting insoluble clumps as the stuff piles up inside the cells.) There are all sorts of systems to use that will give you a sign of whether or not your protein is actually being expressed, many of them quite ingenious. A common theme is to put in a marker gene along with your own, and many times that's a gene that confers an unusual resistance to some antibiotic. You transfect in your DNA, grow the cells, and hit them with the chemical agent - anything that survives has a good chance of having taken up and expressed the DNA you gave it (although you'd better check it by another route to make sure you aren't getting fooled.)
The big question, though, once you're sure that the stuff is being made, is whether it's coming out in a form that you can purify, and whether it's actually working the way it's supposed to. Those two questions are often tangled up in a knot - if your protein isn't clean, maybe that's why it isn't working. (Unfortunately, there are many times when your protein looks clean and still does the equivalent of floating belly-up to the top of the tank. Keeps everyone on their toes.)
There are plenty of separation techniques to fish your proteins out of cells. Most of them involve first breaking the cell walls and separating out the larger chunks like the nuclei (which you usually don't want,) the empty cell membrane (which you might, if you know your target protein lives there) and the cytoplasmic contents. Centrifugation is the standard way to do all this. There's a fair amount of gunk in the cytoplasm that you can "spin down," too (like the endoplasmic reticulum - to a cell biologist, "ER" isn't primarily the name of a TV show.)
Once you finish that, you're left with a mixture of thousands of different protein, carbohydrate, and lipid components. This is when you'll be glad that you overexpressed your target, because you'll need all the help you can get to make it stand out from the rest of the stew. Sometimes expression levels are high enough where you can do some minimal cleanup and use the stuff as is.
If that's not the case, a popular trick called "His-tagging" might be the answer. You set things up so that the proteins ends up with a run of histidine amino acids at one end (which you hope is far from the action that you care about.) All those imidazole side chains in a row will coordinate with metals, so you can pass the crude brew over a metal-containing column, wash all the non-histidine-rich stuff out, and then change to a stronger solvent to wash off your desired stuff. It's usually a safe bet that you won't have many natural proteins in there with a dozen histidines in a row - if there are such beasts, I'd like to know what the heck they do.
Another wild card is all the processing that proteins undergo in the cell - folding (sometimes with the assistance of other chaperone proteins,) phosphorylation, glycosidation and so on. As I understand it, if you run into trouble at this stage, you're pretty well sunk. Sometimes you can rescue things a bit by harvesting the protein at a different stage in the life cycle of the cells, but it's usually time to look for another cell type to start over with. This can happen especially if you go too far afield, phylogenetically. Bacteria, for example, are notorious for producing hopelessly hosed versions of some human proteins - although if you can engineer them just the right way, they can be tremendous producers. And (unlike tissue cultures) they're equipped to live on their own and take care of themselves. Yeast fall into that category, too - robust in their way, studied out the wazoo, but not always reliable for getting active protein.
Insect cells, though, are pretty good. A particular strain called SF-9 from the armyworm moth is widely used, in combination with a baculovirus vector, which has the advantage of not being infectious in humans. It doesn't always work, especially with proteins whose glycosylation pattern is critical, but it's one of the first things to try.
Mammalian (or even human) cells are a better bet to produce active protein, but they're often trickier to work with. A favorite line are the beloved CHO (Chinese Hamster Ovary) cells, which are often used when the expressed protein needs to be part of a living cell system for the assay. There are other common lines derived from mice and macaque monkeys. Moving to us, there are standard cell lines from human kidney or liver, and then there are the famous HeLa cells, one of many from human tumor sources. You don't see these types used as much for large-scale transfection/overexpression, though, because they necessarily give huge levels of protein, and any vector that can infect them can infect you, too.
So, getting things to work just the way you want them to involves manipulating a lot of variables, not all of which are well understood. Not to mention the ones about which we don't understand squat. Still, these experiments are a regular feature of any molecular biologist's life, and in a drug company we expect a pretty good success rate at eventually getting the proteins we want. It just depends on how much time and effort you want to throw at the problem - and what problem doesn't at least partially depend on that?
(For those who want more, here's a useful guide from one of the big commercial players in the area. It goes into details that I've skipped over, like various funky ways to get your DNA into the cells, and some fine points of how to grow them and keep them happy.)
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