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Drug Development

The Big Problems

I’ve had a lot of people ask me about yesterday’s protein folding news as it relates to drug discovery. And while I did a post on that last year, I thought it might be useful to briefly lay out the real problems with drug discovery, as I see them. Most folks in drug discovery will find the next few paragraphs to be pretty obvious stuff, but that’s because we’ve been living it. Readers can decide for themselves, though, where improved protein folding predictions fit in.

One of our biggest difficulties is choosing the wrong target. No, really. We have all sorts of compounds that make it into human trials and then don’t actually work, because it turns out that our hypothesis about the underlying disease was just wrong. It’s hard to overemphasize this: we don’t know enough about human biology to make sure, much of the time, that we have grasped the right end of the stick. A few simple questions will illustrate the problem: what causes Alzheimer’s? What’s the best way to interrupt septic shock? What’s the underlying cause of Parkinson’s disease? What’s the best target to work on to deal with chronic pain? What’s the actual biochemical cause of major depression? If you wanted to reverse fibrosis in a given tissue, how would you best go about that?

You can do that sort of thing for quite a while. Some of these questions have slightly more plausible answers than others, but believe me, all of them will involve substantial risk as you go into Phase II trials in humans. Just look at the landscape around many of them – all the previous trials that have wiped out. So I think it’s fair to say that being able to do a better job of picking the actual disease-relevant targets for our drugs would be a great improvement. Unfortunately, there does not appear to be a general solution to this problem, since it involves a more detailed understanding of each individual disease.

Better models (animal and otherwise) of such diseases and conditions would be great to have, but that’s a high bar. The arguing over animal models of Alzheimer’s has been going on for decades, since the underlying difficulty is that humans are the only animal that actually gets Alzheimer’s. You might think that pain signaling would be a conserved process and that animal models would tell you a lot, but I have lost count of the number of compounds that work in such models but do not work in human trials, so there’s clearly something missing there. Model development in general sometimes runs into a chicken-and-egg question, since you would need to know a lot more about the disease before you can work up a good model to mimic it.

Here’s another: we would love to have a better warning system for toxicity in human trials as well. Many promising drugs have dropped out of the clinic due to unexpected tox effects, for sure – some of these turn out to be mechanism-related and some of them are just compound-related (where the compound does something else that you don’t want), but there are many instances where we can’t even make that distinction yet. Animal models for toxicity are extremely valuable, but they don’t get you all the way. You are still taking a risk every time a new compound or new mechanism goes into human trials, and it would be very useful if we could lower that risk a bit. The general solution would be some sort of system that exactly mimics human biology but doesn’t consist of a bunch of human swallowing pills. This is a difficult goal to realize.

To my mind, these are some of the biggest problems in coming up with new therapies. As a medicinal chemist, one of the things that you come to realize is that med-chem itself is often at the mercy of these things. You can deliver a potent, selective, bioavailable compound aimed directly at your disease target, only to find out in the clinic that whoops! That target doesn’t work. I have been involved in a good number of these over the years, and so has everyone else. No amount of compound optimization will fix that issue; the problem is bigger than the compounds.

So when you hear about a new technique that’s announced as speeding up the development of new drugs, ask yourself if it’s going to bear on the issues above or not. Now, that doesn’t mean that advances of that sort are useless, far from it. New techniques to screen compounds, or to find leads from the screening data, or to optimize them more efficiently into clinical candidates, new formulations and assays and delivery methods and mechanisms, all of that is useful. But all of those are upstream of the problems of target selection and unexpected toxicity. Finding out more quickly and with less expense that you have chosen the wrong target is no bad thing – but an even better thing would be to not choose the wrong target.

30 comments on “The Big Problems”

  1. ATMosphere says:

    Thanks Derek, You have perfectly captured what has been bothering me about this news all day – I should be more excited but couldn’t shake the feeling of ‘and….’

  2. Molmechanic says:

    So, you ‘ve discovered a great compound that is bio-available, great drug properties, and has passed all the tox hurdles. Wonderful! But it doesn’t do what you want in the clinic, at least not against the disease you were aiming for. Surely, it’s gotta do something against some biochemical target. Is this an opportunity for drug repurposing? And if so, how is this actually done?

    1. Patrick says:

      Sure; all the big places keep big libraries of … everything they’ve made ever, or close to; and especially so for anything that’s been in humans (and didn’t hurt them, but you keep even that stuff around- maybe you can modify it).

      Then, when you’ve got a new target or disease or whatever, you do library screens against it.

      If you get so lucky as to have a tolerated-in-humans compound (that you own or can make a close analogue of) hit in one of these screens, well, that’s pretty exciting. (Then you have a zillion hours of checking stuff to see if this is real and a good idea etc etc, but still)

      That’s the basic idea from the chemistry end – failed compounds go in a library to test against new things.

    2. Derek Lowe says:

      One of the first things I worked on was a beautifully selective dopamine D1 antagonist (SCH39166). It failed in the clinic for schizophrenia, and it has failed every attempt to repurpose it to other indications ever since. You’d think that it would be good for something, but it’s been 30 years and no one’s found a use yet.

  3. Lane Simonian says:

    Rather than focusing on misfolded proteins themselves, a focus on the bigger question of what causes protein misfolding might lead to greater progress in disease treatments. The misfolded proteins may under certain circumstances contribute to disease progression, but if you interrupt what leads to the protein misfolding in the first place and “unfold” the protein, you not only address the misfolded protein problem but many other problems as well.

  4. Lane Simonian says:

    Just to put an exclamation point on my previous comment:

  5. metaphysician says:

    A somewhat related problem I ran across while discussing this breakthrough with friends: scale. Say you can perfectly predict the folding and behavior of any protein you choose. Which do you choose? I mean, twenty amino acids. Average protein length in a eukaryote is about 400. 20 ^ 400 possible configurations.

    There are only 10 ^ 80 or so particles in the observable universe. Ohhh.

    Which is to: can this system run in *reverse*, where you put in a particular geometry and get out a sequence of aa needed to generate such?

    1. Nat says:

      Protein design is indeed a natural application of structure prediction methods and many of the groups that have done well in CASP are doing far more impactful design work now. Here’s one example: I am far more interested in seeing what AlphaFold could do in this field than any short-term pharmaceutical applications.

  6. Frossty the Merckman says:

    But, Derek, doesn’t that mean that medicinal chemistry is basically useless? Medicinal chemistry isn’t solving any of the problem you mention, because you’re saying that the real problems are in biology. Or even if you’re not going so far as to say it’s entirely useless, that it’s essentially a low-value commodity? The management certainly agrees with you, which is why they keep laying off chemists.

    1. Derek Lowe says:

      Alternatively, med-chem is not the problem. . .

      1. Frossty the Merckman says:

        If that were true, how come it took so long to drug KRAS? How come we’ve still only drugged a few mutants? It’s as if medicinal chemists can succeed at anything – so long as someone else has drugged it before. And even then, if med-chem is not the problem, why does lead optimization take more than one iteration?

    2. Another Guy says:

      I believe Derek discussed in his previous posts that to date software that can design drugs tailored to fit into a specific binding site often come up, shall we say, lacking:

      We still need chemists.

      1. Frossty the Merckman says:

        I agree with you that the computational chemists are useless. Unfortunately, showing that computational chemists are not needed does not prove that medicinal chemists are needed. Derek and management agree that you don’t need medicinal chemists* either, because they’re not solving the real problems. What you need are the biologists and toxicologists. That’s the place to spend the money.

        * Specifically you don’t need expensive medicinal chemists in North America or the UK. Get the cheapest ones you can find somewhere else.

        1. CR says:

          Ah…there’s the rub. You are not going to solve those problems in biology and toxicology without chemistry/chemists.

        2. Chembio guy says:

          Chemical approaches provide some of the most effective and relevant means to interrogate target and pathway biology. That takes med chem. The point is there are very few golden targets that “if we only could develop a compound” would be disease home runs. Even Ras inhibitors will probably not provide durable monotherapy.

  7. luysii says:

    Another problem with drug design even when you know the structure very well is the following

    “Like other hallucinogens (LSD, mescaline, psilocin) NBOMe binds to the 2A variety of serotonin receptor (aka 5HT2A — at least 16 serotonin receptors are known) and acts like LSD as an agonist.

    Which brings me to Cell vol. 182 pp. 1574 – 1588 ’20 —, probably behind a paywall. Which has beautiful cryoEM structures of 5HT2A bound to LSD, NBOMe and methiothepin, an inverse agonist. To get pictures they had to stabilize the structure with a single chain variable fragment of an antibody (something that always makes me wonder how physiologic the structure obtained actually is).

    Why use NBOMe as an example of how hard drug discovery is? Well the binding site of LSD to 5HT2A is well known, and the paper has some beautiful pictures of LSD snuggled between the 7 transmembrane segments of 5HT2A. What is remarkable about NBOMe is that it lies in the binding site in a completely different orientation. Moreover NBOMe fits in a previously undescribed pocket between transmembrane segments #3 and #6 (TM3, TM6). Actually I think NBOMe actually produces the pocket.

  8. Yvar says:

    I believe that one of the biggest issues facing drug discovery today is the lumper vs splitter debate of what a disease actually is – related to but not the same as the problems that Derek nicely listed. Alzheimer’s is a perfectly good example – one of the biggest problems with treating Alzheimer’s is knowing when someone has it vs another type of dementia, and knowing whether all Alzheimer’s is the same. Cancer is my prototypical example – often describing cancer by tissue type is helpful, but certainly isn’t the only useful way to categorize it, and it is very clear that actual solid tumors in actual patients respond heterogeneously to every treatment I’m aware of, but they’re all classified together. I think personalized medicine is eventually the answer to this problem, while I completely acknowledge that trying to treat everyone’s condition as if it is unique has its own huge set of unsolved problems.

    1. BB says:

      This is exactly why so many companies like to work on rare diseases caused by known defects in well studied genes. The disease is well “split” for you and the target is often (but not always) apparent.

      Derek chooses to focus on complex diseases in his examples – noble challenges indeed. Many of those “diseases” are often syndromes, lots of different disorders lumped together as you say by symptomology etc. Doesn’t mean they don’t have single targets that might be effective, just that they’re a lot harder to find. I say, let human population genetics lead the way! (Or… Derek’s favorite, the old fashioned phenotypic screen) 🙂

  9. brotherjohn says:

    Hi Derek,

    there is a lot of work being done in more complex human tissue models. What do you make of the recent popularity of organoids? Do you see them as one way bring necessary complexity to in vitro screening approaches? Or are these just messy balls of random biology?

  10. sci says:

    I thought Verge and Recursion and the like were going to solve the first problem with AI??

  11. Nathan says:

    Hey Derek, would love to hear your take on ISRIB.

  12. MoMo says:

    Let the computational chemists alone! They deserve their chance to be great too. Just don’t let them in the synthesis labs- they’ll end up hurting themselves.

    1. Andy Callaghan says:

      @Derek , speaking of which it must surely be time time for another “Things i won’t work with”

  13. Barry says:

    A med. chem. department tries to balance its efforts between known targets and novel targets. Resources are always finite; having validation in hand that the enzyme/ion-channel/receptor…target you’re working to modulate is relevant to human disease is a big advantage. But there’s glory and profit in being the first to achieve a new approach to a disease. Readers here will have their own handicapping notes on which are promising.We’ve known e.g. since ’92 that over-expression of MDM2 promotes cancers in nude mice, but still have no validation that inhibiting its human homolog modulates cancer in Man. How many groups have blocked the function of Tie2 and found no therapeutic effect…

  14. Our view/approach is that there is no right or wrong target. I think the idea of target-based drug discovery is why we’re in the mess we’re in, with drug discovery lagging behind other fields technologically. Our approach is to look at ALL targets and off-target effects which there inevitably will be due to the small molecule nature of drugs and small peptides. By our calculations, each drug that is approved is predicted to strongly interact with at least ~200 proteins. Even if we’re only half right on the number (that may be the case), that’s still a lot of proteins that go into making a drug a drug (and we may just be wrong in which proteins, but the overall numbers may be even higher). A drug has to get efficacy right but also has to ADME-T right. There’s also other macromolecular interactions that are taking place.

    In drug discovery we have to confront the problem of interconnected network changes (the combined system of all drugs and metabolites, all molecules, and other interacting entities within a body, and the dynamic aspects are stronger here). Again, the problem now is lack of data and let’s say we had that equivalent amount and did solve the multibody problem, the dynamic aspects of drug behaviour would make it more difficult than protein structure prediction (not saying it can’t be done, but there’s a temporal effect to drug behaviour we have to consider).

    (Our approach BTW is the Computational Analysis of Novel Drug Opportunities (CANDO) platform for shotgun drug discovery, repurposing, and design. Recent publication can be found via Google – I’m not sure if this site censors URLs or not but I didn’t see my comment appear so I’m trying again.)

  15. Josef Maximilian Klein says:

    I find it totally irresponsible of governments to be lulled into allowing only animal tox studies to be sufficient for Market Authorization for Chemicals. Even more after reading this.

  16. Dominic Ryan says:

    Unfortunately success in drug discovery does not really tell you how to be successful on the next one. If it did the pharma industry would never fail. We are always looking for lessons. Some of those lessons help a lot, some not so much.
    That lack of applicability leads to all sorts of ‘management solutions’: The problem is really the poor [biology|tox|chemistry|compchem|astrology] and in any one project any of them might be the problem but not usually for lack of doing good science.
    It always comes down to balancing resources and what it takes to derive *instructive and actionable data*.
    Take the question of target-based discovery vs. phenotypic (and I include Ram Samudrala’s description in this). In target discovery you better have the right target, as said above. In phenotypic discovery the trade off is the information density from experiments. If your molecule is doing multiple things then what does it take to guide you to a better outcome? Often you need a more complex assay or even an in vivo assay. Say you have $100K to spend on a block of the project. Do you make 100 compounds and test with an in vitro assay with one target? Or, do you have to test in vivo and therefore use up 5x as much compound with much slower turnaround and only make 20 compounds. Now you are making fewer compounds for a more complex highly multi-factor readout. Ideally the more components to an important readout the more compounds you probe with.
    Even that depends on the stage of the project. If your whole game is hit discovery then the phenotypic approach could look compelling. But if you are charged with getting it to a development candidate the picture might not look the same.
    Consider another example in repurposing. An early comment on this page mentions even having an in-human tolerated compound. That is valuable data. But the next comment: “…or one you can make an analog of” is much less useful. That compound will still be a new entity and need the same safety package as any new entity. It might be a good project start, but it is not repurposing.
    Generating useful data is difficult and always a compromise. We have to make decisions about progression without getting all the data we would want. Given the scale of possible data to get that’s not surprising. Demonising one discipline or group says more about a lack of appreciation of the complexity than expertise about one area.

  17. BDBinc says:
    The CDC says it isn’t available.

    The CDC document is titled, “CDC 2019-Novel Coronavirus (2019-nCoV) Real-Time RT-PCR Diagnostic Panel.” It was originally published in February, 2020, and re-published in July.

    Buried deep in the document, on page 39, in a section titled, “Performance Characteristics,” we have this: “Since no quantified virus isolates of the 2019-nCoV [SARS-CoV-2] are currently available, assays [diagnostic tests] designed for detection of the 2019-nCoV RNA were tested with characterized stocks of in vitro transcribed full length RNA…”

    The key phrase there is: “Since no quantified virus isolates of the 2019-nCoV [virus] are currently available…”
    No new deadly virus, everyone’s been” exposed ” to corona( +Sars CoV 2002), antibodies do not prove you have immunity so whats going on here?

    1. Lane Simonian says:

      We live in a strange world where the denality of reality has become a cottage industry (or a global one thanks to social media). I blame a lot of this on Trump, but I cannot blame it all on him.

      I cannot believe that the people who perpetrate false realities have deluded themselves; only that they enjoy deluding others for fun, power, and profit.

  18. Lane Simonian says:

    Correction: denial of reality.

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