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Chemical Biology

New Chemistry, And Its Limits

Here’s an article in Nature Chemistry on organic synthesis and drug discovery, from a distinguished group of drug-industry chemists. The authors are going over a number of areas where medicinal chemistry could make use of more advanced synthetic techniques, and they’re good ones.

For example, “From an industry perspective, the most common challenge for any new synthetic method is its level of tolerance to the polar functional groups and nitrogen heteroatoms found in biologically active molecules.” Yes indeed. That’s what I look at when I see a neat new transformation in the literature – what did it work on? Basic amines OK? Tertiary or secondary? Secondary amides tolerated? Carboxylic acids? Free OH groups? I’m disappointed sometimes when I find that a reaction can’t tolerate these, but I’m glad that the papers involved at least went to the trouble of finding the limits to their chemistry. Far worse than that is a paper that tiptoes around the issues of chemical compatibility, leaving you to find out for yourself – if you’re so inclined, and often one is not.

Another area identified is late-stage functionalization, C-H bond activation, etc. Those reactions are always welcome, for sure. Chemical diversity is one of the names of the game that we play, and anything that allows us to get more of it quickly and reliably is good news. Blending with the above, the more complex and functionalized the molecules that can be used as substrates for such chemistry, the better. We’ll take fluorination, hydroxylation, amination, addition of methoxy, trifluoromethyl, what have you. It’s great to be able to predict where the functionalization will happen, of course, but there’s value in things that just sort of go in and mess with structures, too: new molecules! After all, that’s what the liver enzymes do to our drugs; we’re used to it.

The paper also calls for new ways to synthesize and functionalize small heterocyclic rings, new metal-catalyzed coupling reactions (and new C-C bond-forming reactions in general), more biomolecule-compatible reactions, and more. It also goes briefly into machine-assisted synthesis and software-assisted retrosynthesis, but the bulk of the paper is on synthetic methods, and I can only cheer on their suggestions. These are all potential areas for academic-industrial collaboration to generate new chemistry, because everyone benefits from success in these areas (indeed, some of this collaboration goes on already for just these reasons).

So I enjoyed this paper very much, but it starts off with a claim that’s worth arguing about: “organic synthesis is still a rate-limiting factor in drug-discovery projects“. Is that true?

It depends on where you’re standing. All the synthetic limitations described above are real, and they keep us from being able to make a lot of molecules that we’d otherwise be cranking out. But (and this is a big point) it’s rarely the case that we medicinal chemists identify a tricky new structure that absolutely has to be made. That sounds odd, but it comes down to our predictive powers, which aren’t so great. We don’t generally draw some wild compound up on the hood sash and say “That’s the one, folks: find a way to make it or die trying”. We never know which is the one, so in the absence of knowing, we make the things that we can make in the ways that we can make them, and honestly, much of the time, we can manage to come up with something.

In a more general sense, though, things like the ability to make more polar compounds reliably and quickly would probably lead to better and more structurally diverse drug candidates and screening compounds, not to mention better starting points for projects in general. We just don’t know which ones. The main examples of specific compounds I can think of are metabolites or potential metabolites, where the liver has made some new polar compound out of an existing drug candidate, and we need to make the new compound(s) for testing. Those can be tough, and sometimes the only way is to grind out small quantities by exposing the drug to liver tissue itself (!)

As for times we can’t come up with something, I would like to believe that far more diverse and interesting sets of compounds, millions of them, would allow for real hits to be found against target classes that we currently have trouble attacking. But that remains to be proven, if it ever can be. Chemical space is so large that you can always say “Well, your compound set still wasn’t big enough – the good ones are still out there”, and there’s no way to say that’s wrong.

Overall, the real killers in drug discovery stem from – to put it mildly – our incomplete understanding of biology. It’s Phase II and Phase III failures that hammer us, and those happen because we don’t understand our desirable (and undesirable) mechanisms of action enough, leading to failures in efficacy and safety. Even worse, they come after a big pile of money has been spent. Compared to these problems, generating chemical matter is not as big a concern. We already generate enough chemical matter to send all sorts of stuff into the clinic, where 80 to 90% of it dies for other reasons entirely.

Organic chemistry is, of course, crucial to making small-molecule drugs, and you’d think that would be enough. But as a chemist, I wish that organic synthesis were more relevant to these deep problems. But in the big picture, it isn’t quite so. Chemical biology, as a field, is an attempt to make that happen, but How to Make will never be able to answer questions of What to Make and Why.


32 comments on “New Chemistry, And Its Limits”

  1. milkshake says:

    Chemistry and especially new robust user friendly chemistry is pretty important but it is not the rate limiting step in drug discovery – China, India and Russia have plenty chemists and yet they are far from being drug discovery powerhouses. The limiting factor is actually academia-driven discovery biology. Tremendous resources are wasted when medicinal chemists go after dubious targets. I participated in several such hopeless projects: cMet (where our least selective series got rescued by repurposing them for ALK – the glorious Crizotinib resulted), p38 and JNK.

    1. yf says:

      I agree that discovery biology is the bottle-neck here. It can not be scaled up; it is not a process that can be managed by MBAs. However, new biology is essential for the growth of top-line. MBAs can manage the bottom-line. Unfortunately, a lot of people in industry are process-orientiated and people in academia are too knowledge based. We lack people who can utilize science from academia to make products to fit into the process of industry.

  2. Jake says:

    Derek — they don’t mention them by name, but I believe the direct aziridination of an alkene is something medicinal chemists might like to do, but I have no idea if the reaction is used in industry. I’m working on a variation of it in my lab. What would you want to see as far as an advancement there?

  3. CMCguy says:

    Derek you are correct on why at the core its lack of biology comprehension bogging down drug discovery progress however the perception that its the medchemist/molecule generation at rate determining is based on the long hyped supposed dominance of the role and people involved synthetic efforts have themselves promoted (in both claimed criticality and organizational oversight positions). At one time several decades ago syn chem may have played a greater part in the overall course of drug development, and still should be able to make contributions, but trust the arrogance can be replaced with collaboration to work with the multitude of other functional areas to tackle the biological problems where even may turn out never completely understand can at least devise means to positive impact the patients afflicted with errant biochemical events.

  4. Peter Kenny says:

    This is a useful article that highlights some relevant directions in which synthetic chemistry is headed but I don’t see these developments transforming drug discovery. Perhaps, if they were AI-enabled with bright, shiny machine learning algorithms running on cell phones, drug discovery would be disrupted but, as you point out, validating targets in Phase II/III is not sustainable in the long term. Biology is indeed difficult and one reason for this is that is not generally possible to measure unbound intracellular concentration of compounds in real time.

    1. tlp says:

      re: Biology is indeed difficult and one reason for this is that is not generally possible to measure unbound intracellular concentration of compounds in real time.

      This is quite a lax definition of biology 😉

      1. Peter Kenny says:

        I agree. We use chemical probes to understand biology and there is much discussion about the need for selectivity and affinity. However, there is little or no discussion about intracellular concentration (which drives binding).

  5. Magrinhopalido says:

    For pre-clinical progress, the longer the cycle time, the more slowly we learn how to move forward. I believe it is, more or less, that simple.

    Determining ADME, in vivo toxicity, efficacy in animal models of disease are all more rate-limiting because the cycle time is 2-6 weeks. In vitro testing of new compounds is routinely done twice a week so chemists can optimize for potency relatively quickly.

  6. Barry says:

    If the chemistry existed, we might like to modify a candidate–once it had sufficient potency/selectivity–by replacing each of the C-H bonds with a C-F bond, in the quest for better tissue penetration and/or reduced clearance. In practice, this often requires going back to begin with a different starting material, and we need a good reason to invest the time. Direct C-H activation on a complex substrate remains aspirational.

  7. CAprof says:

    Organic synthesis is very rarely rate-limiting. It’s not the making of the molecules that is the problem. It’s knowing which molecule(s) to make! We’re still puttering around in the “screening will save us” phase of the business where hopes are pinned on fancier machines and bigger libraries. As others have said here, problem #1 is the biology (Knowing where to intervene) and problem #2 is the target (Knowing how to intervene).

  8. KazooChemist says:

    Very interesting topic. I clicked on the link to check the author list and actually got to see the entire article. I decided to finish Derek’s post and then go back to the article at my leisure. It is now behind a $59.00 paywall. I have no clue as to how the entire article came up the first time around.

    1. Peter Kenny says:

      Try the link that I’ve used as the URL for this comment

      1. KazooChemist says:

        Thanks for trying. The first page looks fine. The remaining pages are very low resolution and are impossible to read. I tried capturing as an image and opening in a viewer, but that didn’t work either.

  9. DIscoStu says:

    Although the authors have some good points at the beginning of the article, the rest seems like a list of reactions highlighted in C&EN rather than a realistic assessment of what is really useful medicinal chemists. For example, I doubt that allylic amination chemistry is something needed everyday by medicinal chemists. It would be great to hear from more chemists “in the trenches” about the new methods that are working for them, and what new reactions would really change the way they work day to day.

  10. cynical1 says:

    If organic chemistry is a rate-limiting factor in drug discovery, then why has the entire industry down-sized, outsourced and off-shored organic chemists in drug discovery?

    1. Chris Phoenix says:

      On general principles: If it’s rate-limiting and can be parallelized, it’s probably expensive. If it’s expensive, then both downsizing and offshoring can look attractive.

  11. Anonymous says:

    Management always promised more than we (synthesis) could deliver and that always got us in trouble. Biology and Comp Chem would design molecules they wanted us to make but would have been difficult or impossible to make. “We need a methyl over here someplace.” Or freshman orgo: ortho and para, easy; meta, not so much. They wanted meta NOW; I said we might be able to deliver a single example in a few months, if new schemes worked. I would frequently say, “We make what we can make.” And much of what we made was useless. Which leads me to another related point …

    How many have heard, “Don’t worry. The biology is easy enough to learn. Synthesis is the hard part.” AND “Don’t worry. The chemistry is easy enough to learn. The biology is the hard part.” For us chemists, the core biology of a med chem target starts out, basically, simple but it is also a moving target that changes very quickly (if you are lucky enough to get clear results from screening or literature). For biologists, they don’t really need to know synthesis or orgo at the PhD level. A good undergrad textbook has most of the important stuff for them (such as, you can ask us for the meta-X of this advanced candidate but it will take us several months to go back and make it some other way).

    It would be great if chemists were allotted more time to solve more general problems (reactivity, selectivity, new reactions, general Pharma problems, etc.) but I have not been in an environment where that was appreciated. It has usually been “just make more.”

    1. Design Monkey says:

      Ah, yeah, meta substitution.

      Main idea beyond belinostat was exactly sidestepping the then already existing scores of simple HDAC inhibitor patents, which were en masse based on easy ortho-para substituted scaffolds. Belinostat was meta and won his own place under the̶ s̶u̶n̶ FDA.

    2. Matt R says:

      Biologists need to understand that molecules don’t just fall out the sky into their hands. The lack of chemistry knowledge among some biologists is shocking.

  12. Devils' advocate says:

    Let me play a devil’s advocate here. Organic chemistry provides probes to enable understanding of Biology, as we all agree. The better tools that we can generate more quickly, better capable and better positioned are we to probe the Biology or to intervene the targets, I suppose. Haven’t we once turned to fancy machines and larger library generations in the name of “combinatorial chemistry and Highthroughput Screening”. (combinatorial approach failed due to just flat molecules that populated the libraries, as we all know….hadn’t been the case then why did the whole field embrace it for nearly two decades and still continue to hunt the needle in the hay stock!). So, the author’s premise still holds ground that we still need better synthesis tools and advancements and organic synthesis is one of the rate liming steps, if not the rate limiting step ( I am not a P chemist, and probably it violates the laws of kinetics to have more than one rate limiting step). Imagine if we can stitch millions of analogues of a potent natural products such as erythromycin, wouldn’t we have better success/hit rate towards anti-bacterial screening ( I agree that there could be potential pit falls at a later point in the path of drug discovery, however, it would at least enable better hit/success rate than the flat molecule that we currently can make/buy…thus enhancing the rate of drug discovery)

    It is too soon to declare that ‘organic chemistry’ is matured science and we do not need to fund any synthesis proposals ( I agree with the sentiments that the scale was probably tilted by some selfish leaders in the field. However, thanks to nearly 40-50 years of toiling by all those synthetic chemists across the world, specifically from China, Germany, Japan, India, USSR and US and Derek and others are at least in a position to say that synthesis is no longer a bottle neck. However, there is lot more that needs to be done in organic synthesis/chemistry to declare that we no longer need any more tools to make compounds…R&D needs to be continued until even a biologist can make what ever he/she needs to study the research problem at hand. It hasn’t been reduced to a mere tool yet though all of us would like it to be. The fact that people toil for 5-6 years to produce 1 or 2 mg of the complex 3-dimensional natural products attest to the fact that it is not every body’s cup of tea, just yet. Until we can produce millions of complex non-flat drug like molecules , we will all be trying to probe the biology with wrong or insufficient flat tools/probes and we will be failing in Phase II and Phase III levels. I do not mean to undermine the importance of good and sound biology ( other advancements that are interrelated in the process of drug discovery), just saying that every field is equally important in the quest for better drugs. Just my two cents.

    1. regularguy says:

      One point I think you’re making I like a lot – the biological target validation step that is the real bottleneck would be improved by being able to more quickly finding suitable probes to interrogate things. That is, biological validation is the bottleneck, but chemistry can help here too. I totally agree.
      Not sure I agree that our ability to find probes, or to populate “quality” screening decks for example, is really that limited by existing synthetic methods though. Some DOS libraries featured fairly sophisticated reactions & made some high complexity molecules, but those weren’t in any kind of sweet spot either, as much as Schreiber has tried to argue they were.

  13. Blunderbuss says:

    Surprised to see DeVry University got a Nature paper.

  14. anon1 says:

    If you have a good target, good assays, and a good chemical starting point, the med chem and synthesis nearly always goes smoothly. Hard to call it the rate-limiting step!

  15. @HartungIngo says:

    I fully agree with the assessment that synthesis is rarely the limiting factor in medicinal chemistry. Just one comment: You mentioned that accessing metabolites is sometimes really difficult and the final option is incubating with liver cells. Biocatalysis has seen significant progress over the last two decades and there are many standard processes to use recombinant CYP or UGT enzyme preparations for mg-to-g scale synthesis of metabolites (or whole cell fermentations). We as synthetic organic chemistry need to accept that such methods should be used as the most efficient way to get those metabolites and not only the last resort option. It’s a bit like photochemistry or electrochemistry: We need to incorporate these different technologies into our synthetic repertoire and not stick to our most preferred limited set of classical round-bottom flask synthetic organic procedures. In that regard we as medicinal chemists are sometimes too conservative in making use of new methodologies (resulting from timeline pressure etc.).

    1. Useless Overhead says:

      Are there CROs one can use to try making metabjolites as you propose above, with recombinant enzymes? Because all we know here is, cook the parent in hepatocytes and purify the soup, just as Derek’s original post mentions…

      1. tt says:

        Plenty of CROs do just this type of metabolite synthesis with P450s, BM3s, or fungi. I won’t plug any particular CRO, but this is now easy to do.

  16. Not a chemist says:

    What I’ve observed from the outside over the years: any idiot can make a protein inhibitor, making a drug takes talent.

  17. putchemistsbacktoworknow says:

    Well….don’t U think that if you could make more of the difficult compounds, faster and cheaper, that you would get a better understanding of SAR from the beginning of the whole process?

  18. KN says:

    “From an industry perspective, the most common challenge for any new synthetic method is its level of tolerance to the polar functional groups and nitrogen heteroatoms found in biologically active molecules.”
    Oh, yes. Since I’ve started working on DNA-encoded libraries, 80% or more of my synthetic knowledge and experience became irrelevant.

  19. A curious chemist says:

    I’ve got a (possibly naieve) general question for the audience. As one of the directions mentioned in this paper, how much of a need is there for revisiting classical complexity generating reactions and updating them such that they fulfill process chemistry requirements? My experience with medicinal chemistry and natural products has not seen one heck of a lot of overlap. For instance (and I’d love to see a proper example if anyone can think of it), oftentimes the natural bioactive compounds contain one or two complex polycyclic core scaffolds and a couple side chains. To prepare such molecules often takes a long linear multistep classical synthesis sequence with multiple chormatography steps and horrible material throughput (those 2 mg at the end to be proud of). Medchem analogues often replaces the polycyclic cores (especially if they aren’t signficant to binding activity) with a series of small cyclic and heterocyclic molecules directly linked through well known means, improving material throughput and enabling preparation on scale without chromatography. Spatially it fits in the same places. All the heteroatoms are correctly positioned. But now it breaks down differently.
    Can anyone think of a good example where the medchem compound is effective but fails for toxicity reasons so they go back and replace the simplified linker with a more complex nature-mimicking core and the toxicity issues go away? Is that a potentially useful strategy or is it a fools errand? Is that a worthwhile synthetic space for anyone to be in? Or does attempting scaleup of medium complexity transformations generate so many issues that its not even worth it for medicinal chemists to make it, even if it goes well bench small scale?
    Thanks for taking the time to answer.

  20. An Old Chemist says:

    I guess that the pharmaceutical industry should increase funding (on a war scale) to academic synthetic chemists to invent more reactions that can directly be used to modify final molecules (C-H conversion to C-F). Currently a lot of synthetic chemistry is being done overseas also (India, China, Russia), and such a funding to them by the US companies (chemicals shipped quickly) will help tremendously.

  21. David Edwards says:

    Meanwhile, admittedly somewhat off topic but possibly relevant here, there’s another new paper in Nature Chemistry illustrating the sort of fun and games that’s ensuing in med chem research, courtesy of this little gem, which I suspect Derek may want to devote a post to in future …

    Rhinoviruses (RVs) are the pathogens most often responsible for the common cold, and are a frequent cause of exacerbations in asthma, chronic obstructive pulmonary disease and cystic fibrosis. Here we report the discovery of IMP-1088, a picomolar dual inhibitor of the human N-myristoyltransferases NMT1 and NMT2, and use it to demonstrate that pharmacological inhibition of host cell N-myristoylation rapidly and completely prevents rhinoviral replication without inducing cytotoxicity. The identification of cooperative binding between weak-binding fragments led to rapid inhibitor optimisation through fragment reconstruction, structure-guided fragment linking and conformational control over linker geometry. We show that inhibition of the co-translational myristoylation of a specific virus-encoded protein (VPO) by IMP-1088 potentially blocks a key step in viral capsid assembly, to deliver a low nanomolar antiviral activity against multiple RV strains, poliovirus and foot-and-mouth disease virus, and protection of cells against virus-induced killing, highlighting the potential of host myristoylation as drug target in picornaviral infections.

    Now that’s a piece of research I’d have loved to be the proverbial fly on the wall for, especially if it delivers post Phase III.

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