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Maoecrystal V: You Poor People

The virtues and shortcomings of total synthesis are both on display in this new paper from the Baran group at Scripps, “Total Synthesis of Maoecrystal V”. Actually, they’re on display in not only that paper, but in it and in the four previous total syntheses of the molecule, but we’ll get to that.

Maoecrystal is definitely an appealing molecule for academic synthesis, in that it’s a collection of tightly bunched ring systems and dense functionality. It was also reported to show very good activity in cancer cell lines, which for decades now has been enough to get things underway. The existing routes to it (reported starting in 2010) all go through a Diels-Alder reaction, as the new paper shows, but Baran and co-workers decided to try to follow something more like the proposed biosynthesis. This led to an eleven-step synthesis (discussion here from one of the co-authors) where the known routes are between 18 and 35 steps, although there are some telescoped two-for-one-pot transformations in there, so if you’re picky you can argue about that figure. (I regard those no-workup transformations as a desirable feature, no matter how you count them, and any process chemist will tell you the same).

An interesting feature of the synthesis is that many of the intermediates have small-molecule X-ray structures. That’s a good idea, since the ring systems involved are not trivial to establish by NMR and other methods. Nothing will show that your 2.2.2 bicyclic system now has third and fourth rings attached to it in the right configurations like good solid X-ray data, though. The other reason that they were able to get so many structures has to be that this synthesis actually produced 80mg of the synthetic natural product, which by the standards of the field is like scooping flour out of a fifty-pound sack.

When you look at the synthesis in detail, though, you see the price of that good a route. Some of these steps took a horrific amount of optimization. Let’s just use the first step as an example in detail:

The synthesis of 1 commenced (Scheme 1) with a highly enantioselective conjugate addition of an allyl silane to cyclohexenone to deliver 7 in 80% isolated yield (99% ee). Among the many ligands explored, the TADDOL-derived phosphine-phosphite L1 designed by Schmalz was singularly successful. The use of CuI·0.75DMS was also critical to minimize dimerization of the Grignard reagent. A profound solvent effect was also observed with a mixture of PhMe/MeTHF being essential to obtain consistently high yield and enantioselectivity on 20 g scale.

Right. You don’t even have to be an organic chemist to notice that none of these conditions would have been the first things that the group tried, or the fourth, or the ninth. And note that since it’s the first step in the synthesis, you’re going to be trying these things out pretty quickly on 20-gram scales, since showing that a new combination works on 50 milligrams will be of limited interest. The next step, an oxidative alpha-acetoxy formation, also needed a lot of beating on according to the paper, and for the next step (a Sakurai reaction) it’s noted that over 50 Lewis acids were screened. And that takes us up to the hard parts of the synthesis – no, that’s exactly the case, because all the ring-forming stuff is yet to come. One of those steps includes a description that we’re going to be hearing about for years to come:

Roughly 1000 experiments were conducted changing every conceivable variable from the base used to deprotonate, the solvent employed, additives, and the electrophile. Emerging from this exhaustive study was the remarkable finding that the addition of LaCl3·2LiCl to the extended sodium enolate of 3, followed by quenching with freshly prepared formaldehyde gas led to the desired adduct 11 in 84% yield as a 2:1 diastereomeric mixture favoring 11 (3 g scale).

Exhaustive is right. That’s a ferocious amount of work, chewing through piles of advanced intermediates which are in themselves no fun to prepare. Process chemists in industry have run synthetic variations on this scale (or approaching it) when the situation warrants, but the key to successful industrial work is to avoid putting yourself into such situations at all. The molecules in those cases are less complex, so there are generally more robust routes that can be found without having to go this far. In natural products synthesis, though, you have little choice: every single step is like juggling blown-glass sculptures on a tightrope.

The next step, a stereoselective reduction, needed only about a hundred variations to be optimized, and again the conditions settle down onto a wildly picky protocol that has never been used before in the literature: zinc triflate, which has to go in first, followed by lithium borohydride. “Zinc borohydride”, you think, but you’re wrong: that reagent itself does squat when you try it as such. And so on. Skipping forward a bit, the last step of the synthesis is particularly audacious, with what are formally about seven reactions all happening in the same flask in sequence. And there you have maoecrystal V!

But what do you have once you have it? That’s the kicker at the end of the paper. With a really useful amount of the compound in hand at last, and all the spectral data (including X-ray) to show that they really did have the exact compound, the group had it run across a large panel of cancer cell lines. And it showed no activity whatsoever. Well, now. This means, almost certainly, that the original reports of activity are incorrect: something was active in their samples, most likely, but it wasn’t maoecrystal V. Either that, or the assay was totally blown.

Now, that (from one viewpoint) this is a great advantage of total synthesis: here we have the definitive compound and producing has provided definitive information. It’s tempting to say, though, that this information could have been acquired earlier had the original work been done with more care. That’s partly unfair, though, because the original authors presumably believed that the compound was clean enough to evaluate and the assays were working and were presumably competent enough to make those calls. I’m sure that the original data (60 nM on HeLa cells!) will be revisited in light of these new findings. And this certainly isn’t the first time that a natural product, reported as biologically active, has been come up short on resynthesis.

On that other hand, though. . .maoecrystal V has been synthesized by four different research teams before this one, and we’re only now finding out that it’s not active? Here’s the Thomson group at Northwestern in 2014 (discussion here), and here are the Davies (Emory) and Zakarian (UCSB) groups in 2014, here’s the Danishevsky synthesis (with one co-author, Feng Peng!) in 2012, and here’s the first synthesis (the Yang group in Beijing) from 2010 (discussion here), with another one in 2015. In every case, there appears not to have been enough of the final product produced to actually try repeating any cell assays. If one of the points of total synthesis is to produce bioactive compounds, then something has gone awry here if the bioactivity never gets a look in over all these years and after all this work.

Make no mistake, the Baran route is an excellent piece of organic synthesis. The paper states, though, that “The primary goal of this study was to demonstrate that the notorious difficulties surrounding the exotic architecture of 1 could be solved by total synthesis in a practical way.” Fair enough, but I strongly suspect that this structure would not have set off the amount of interest it did in the synthesis community without that cancer-cell bioassay data attached to it. Those difficulties only became notorious because so many people have worked on this molecule, and its (putative) biological activity had plenty to do with that. There’s also room to raise an eyebrow at that word “practical”. It’s true that this route has delivered more maoecrystal V than anything else in the world, and has thus produced truly practical amounts of the compound. That’s a good thing. But as a look at the synthesis itself shows, it took a brutal amount of effort to get things to this state: it seems a bit odd to refer to a practical synthesis that had a single step (out of many hard ones) that needed a thousand tries to figure out the right conditions. It ends up practical, but if every chemotherapy drug had to be synthesized in this fashion, we’d be in a hell of a mess, not least because very few research groups in the world are capable of doing organic synthesis at this level at all.

There’s also the traditional (stated) goal of total synthesis of providing analogs of such natural products that can’t be obtained otherwise. That certainly does happen sometimes, but not as often as it should. None of the existing syntheses of maoecrystal V, as far as I can see, have provided any. This latest one, which can indeed deliver the original compound in quantity, illustrates the problem. A synthesis like this is (obviously) an extremely finely tuned machine. Throw in an extra methyl group somewhere, pretty much anywhere, and that machine will start spraying oil and throwing piston rods into the ceiling. Get ready for another thousand optimization runs if you change much of anything, is my bet, and that goes for pretty much any bespoke synthesis of this kind. If you want to make analogs, you have design the synthesis from the start to make analogs, and not every sort of molecule is going to be amenable to that. This one certainly isn’t – it’s not a modular synthesis where you make Part A over here and Part B over here and bring them together. It’s all in one place, with the spotlights on every single step, and I don’t see how you’re going to get around that.

So I congratulate the Baran group on a terrific piece of organic synthesis. And I offer my condolences to the Baran group for a terrific piece of organic synthesis. How do we keep those both from being appropriate at the same time?

66 comments on “Maoecrystal V: You Poor People”

  1. not a chemist says:

    Not an academic & not a chemist but this seems like a waste of $$ & many students/postdocs talents that could be put to better use.
    Question- are the chemistries that were used in the synthesis likely to be broadly applicable?

    1. UndergradChemist says:

      Maybe. Probably not.

    2. RM says:

      One thing I like about the Baran group’s work is their tenancy to play around with optimizing reaction conditions, to try for the one-pot mutistep reaction, and to seek out novel reaction schemes.

      In the balance of probabilities, having a new synthetic scheme for Maoecrystal V probably isn’t going to help anyone with anything. (Though if people manage to isolate a contaminant from the standard reaction schemes which is causing the positive assays, that might be something.) Even these particular chemistries may or may not have broader use. However, you shouldn’t underestimate the institutional knowledge which comes along with pursuing such a project.

      Thinking that the point of a synthesis project is *only* to make the compounds is short-sighted. There’s a whole bunch of “meta-knowledge” that gets generated in such projects – knowledge about how best to set up and run such future synthesis projects, regardless of the target. It’s a little sad that reviewers (and authors) tend to focus only on the actual compounds when looking at papers, and that meta-knowledge either gets just a passing mention, or is ignored completely in the write-up.

      So yes, if this was just a brute force, apply-standard-reactions turn-crank project, the value might be minimal. But if you try new things, you tend to learn new things.

    3. DCStone says:

      To quote one of my favourite sayings, “No experiment is ever a complete failure; it can always serve as a negative example of something.”

      I wouldn’t say it was a waste of money since, as Derek pointed out, there was prior evidence suggesting that this could be a really important cancer treatment.

      As far as the students’ time, this was not a waste either. Remember, they’re there to develop the practical expertise, research experience, and intellectual abilities to tackle – and solve – previously intractable problems. This project, while undoubtedly filled with moments of extreme frustration for the students, provided plenty of exactly that kind of training.

      Some of the techniques and odd conditions found and reported will also undoubtedly reappear elsewhere, now that they’ve been described.

      Remember, if it was easy, it wouldn’t be research!

    4. Smigglewilly says:

      For a student / postdoc one of the goals of a research project is to publish it. Since a publication resulted, it wasn’t a waste of their time. As an academic, the goal is to learn something new, if they learned something new, it wasn’t a waste of money.

  2. anon says:

    Wow, I’m not a synthetic chemist but to me the figures in this paper seem especially nicely done.

    If you knew ahead of time that the pure compound was inactive you might question funding this synthesis, but reliable negative results DO have value, even if they are disappointing.

  3. Chrispy says:

    It is intellectually unsatisfying to just try conditions randomly until you find something that works. A study done like this underscores how clueless we really are. It reminds me of Tesla’s famous frustration with Edison, who worked this way.

    Said Tesla of that time: “If Edison had a needle to find in a haystack, he would proceed at once with the diligence of the bee to examine straw after straw until he found the object of his search. I was a sorry witness of such doings, knowing that a little theory and calculation would have saved him ninety percent of his labor.”

    Now in this case, I suspect that if there was any theory or calculation to be applied that Baran’s group applied it. We have so little idea what we’re doing that there is no other way than just trying things. It does make me wonder what the point is with a molecule like this, though.

  4. Marcin says:

    I think the inactivity might have to do with the time from synthesis to the assay as well as the pH inside the cell vs inside the cell. I do think the enolization/isomerization with the formation of the H-bond with other keto might be the culprit.

    1. turminder says:

      If that were the case it would also happen with the natural product tested before.
      I do think the knowledge gained with this awful amount of work will be useful for some, specially for those who learned while working in this project.
      However, the key here is that when natural products or other chemicals are tried against cancer cell lines, the composition must be clear. Many groups are sloppy with characterization.
      What I do think is that this work (a lot of work, yes, in a good old american institution) should not be published in JACS. It is the 4rth synthesis of the product.

      1. David says:

        Why does it matter whether it’s the first, fourth, or four hundredth synthesis? Surely the important thing is the novelty and interest value of the chemistry, and the importance of the biological results, not whether or not someone’s made the same molecule before?

        1. bad wolf says:

          Why does it matter whether it’s the first, fourth, or four hundredth synthesis? Surely the important thing is the novelty and interest value of the chemistry”

          Lack of self-awareness detected.

          1. zero says:

            It wasn’t the four-hundredth identical synthesis, it was a new, more efficient and more productive synthesis using different strategies than the others. Importantly, it yielded enough product to proceed with testing the original hypothesis of activity against cancer cells when none of the other attempts had done so.

            Your position is a bit like saying solar panels are not worthy of academic notice, since we already have so many ways of generating electricity.

          2. bad wolf says:

            I don’t have a problem with Baran’s work but David’s statement is already reductio ad absurdum. Or maybe the field of organic synthesis should be limited to “novel” approaches to quinine, reserpine and strychnine?

            Your suggestion would be better posed as “what if we continued to refine the vacuum tube and ignored the diode”.

  5. VTJ says:

    I’m curious, Derek…if you had to hire a recent graduate to work with you, would you lean towards one of the two authors on this paper or towards one of Baran’s other students that has worked on more practical projects (assume all else is equal and ignore things like personality, etc. for a moment)? As a synthetic chemist (so I’m a bit biased), I don’t think there is much value to sheer stubbornness but I am inclined to believe that a total synthesis student who does his/her PhD right will be forced to think more deeply and much more broadly than many methodology students, who have the option of backing away from challenging substrates. That is not to say that you can’t learn the same problem-solving skills as a methods chemist (or that you automatically learn them as a total synthesis person) but…well, even with your justified criticism for many aspects of total synthesis, don’t you think that the synthesis student would be generally be better prepared for challenging projects in a future career?

    1. Mustard says:

      “…I am inclined to believe that a total synthesis student who does his/her PhD right will be forced to think more deeply and much more broadly than many methodology students, who have the option of backing away from challenging substrates.”

      That’s not very kind to methodology students: that’d be like saying that methodology students have to think more deeply about why their reactions aren’t working compared to synthesis students, who have the option of re-routing to use other reactions.

    2. Cm says:

      VTJ your comments almost offend me and reflect a common bias that I thought faded where doing total synthesis is supposedly better training than a methodology project which, I suggest having done both, is mostly foolishness. Heck most total syn PhDs often spent most of the time continuously bringing up more materials to do late steps, unless they had undergrads or younger lab colleagues who got stuck with that labor. Not very deep or broad mind utilization and for methods not sure many PI would tolerate those who back away from difficult substrates. Stubbornness, at least in form of persistence, is a highly valuable for a person in drug R&D since will hit many walls that trust can overcome.

    3. Devil's Advocate says:

      I am inclined to believe that a methodology student who does his/her PhD right will be forced to think more deeply and much more broadly than many total synthesis students, who have the option of backing away from challenging reactions.

  6. Marcin says:

    enolization on top of the prozaic ester hydrolysis

  7. Hap says:

    I think a modular synthesis would have required even more (intellectually) back-breaking labor to have achieved – it takes a lot of work to make something fire and forget, and if you’re going to put in that work, you’d have to have a good idea that it would be useful.

    There is probably room for generalization, but considering that even the pieces of chemistry that are really general require lots of tinkering to get specific reproducible results (*cough*peptide synthesis*cough*), asking for lots of quick, reproducible syntheses seems nowhere within our grasp yet. Baran’s group is at least trying to live up to what they said; the fact that it’s hard and ugly and not generalizable might be the nature of the beast. Or of my lack of imagination.

  8. Anonymouse says:

    This paper taught me something else beyond the science. A larger number of articles than I thought (such as this one) bypass the “Just Accepted” portion of the JACS website and go directly to the ASAPs. So I suppose I have missed quite a few things by going directly to the “Just Accepted” page each day. This one had been pre-advertised on Baran Twitter so I didn’t miss it.

    1. CH says:

      I think you can check whether you want to be in Just Accepted or not.

  9. Axel says:

    Ei-ichi Negishi used to say, the goal in synthesis is to have either the first synthesis, or the last.

    I suspect that Baran’s synthesis of Maoecrystal V will be the last (I sure as heck hope so), but in this case, that’s not such an admirable outcome.

    1. CH says:

      Ricky Bobby’s dad had the same philosophy. You’re either first or last (last not being good here).

  10. anon says:

    I guess the take away lesson here is that any reaction can be made to work if there is a professor capable of getting a graduate student to try a thousand different reaction conditions.

    I’m willing to bet that if anyone wants to use this reaction as a model for their own work, they too will end up having to screen a thousand different conditions to find the one that works.

    1. Used to be a chemist says:

      Are you therefore suggesting that Baran’s sole talent is his ability to convince/coerce grad students into testing a thousand reaction conditions? Perhaps an overstatement on my part, but I think that there is further talent/creativity at play here and that the overall strategy is brilliant. In exchange for the commitment to exhaustively optimize each step, the student is exposed to a high level of intellectualization of the problem which, coupled with some empiricism at the experimental level, produces what may well qualify for the Negishi success of the last synthesis. For me, this looks like a success and a phenomenal training experience for the student(s). But perhaps that’s just me…

      1. Anon says:

        “Are you therefore suggesting that Baran’s sole talent is his ability to convince/coerce grad students into testing a thousand reaction conditions?”

        No, not at all. Sorry if I implied that. Just saying that in this case testing a thousand reaction conditions may not have been useful beyond the specific case it was done for.

        1. CH says:

          It is clearly not his sole talent… but it is one of them. That is undeniable in this instance.

        2. Screen the Substrate Library says:

          This is the case for almost all methods papers recently, especially those using photocatalysis. Students screen hundreds of conditions to get the yield up for a test substrate and then screen tens, if not hundreds, of substrates to find those that perform well enough to get the paper into JACS. Sure, this method is narrow and herculean in its development, but at least it doesn’t claim to be a “general solution” like those dishonest methods.

          1. Brain quenching says:

            More like final solution

        3. CH says:

          It is not his sole talent…but it is one of them. As can be seen in this paper.

        4. KevinH says:

          Playing a bit of devil’s advocate, I might suggest that the ability to parallelize and test hundreds or thousands of conditions for an optimization could be a bit of valuable training and knowledge in and of itself.

          Even if this particular synthesis of this particular compound is never done again, being aware of (and able to apply) the various considerations involved in designing such an optimization process (and as important, knowing when the application of such brute force is worthwhile) could be a skill that a trainee will – eventually – be glad to have.

          As an aside, my neighbours are a lab that does a fair bit of x-ray crystallography (of ‘difficult’, often membrane-associated proteins), and a part of that work is screening hundreds or thousands of conditions to identify reagent mixtures that will produce nice crystals. I know that robotics and automation have made a huge difference to their work–letting the robot crunch through a stack of 96-well plates overnight is a vastly different experience from a month of soul-crushing, RSI-inducing, sanity-sapping pipetting.

          So, does that sort of mechanical assistance feature much in today’s organic synthesis lab? Or does screening a thousand reaction conditions mean a thousand glass tubes and ten thousand hand pipetting operations?

  11. Curious Wavefunction says:

    Maoecrystal was also a compound used to benchmark the computational techniques that spelt doom for the infamous hexacyclinol.

  12. Anon says:

    I hope they synthesized all their own reagents and solvents from scratch (pure elements), otherwise it’s cheating. Seriously, what % of the chemical bonds in the final product were made during synthesis and not already part of the reagents?

  13. anon says:

    Are the results presented for LMTX at ICAD2016 today in Toronto enough to be called a cure for Alzheimer’s disease?

    1. Anon2 says:

      Underpowered sub-group analysis (pre-specified, at least!). The effect size wasn’t stated in the press release and, in any case, may decrease in a powered study.

    2. Biotechie says:


  14. anon (the real one) says:

    Thank you cousin Anon2.

    Yes, I am always worried with a positive subgroup especially when the size of the subgroup is likely quite small (and unstated in this instance). The result did replicate in both phase 3 AD studies and there is another phase 3 result in FTD that has now been postponed fo ryet more analysis. The nearly 7 point difference in ADCS-ADL and the very small p values does at least seem encouraging. Too bad there isn’t a stock ticker we could follow to see what the money is saying about this!

  15. Albert says:

    Wow, 1000 trials for a single reaction? I’m a process chemist and sometimes we do a lot of trials, but I think in my lab a record so far is about 250. Maybe double that if several labs are working on the same reaction or if there is extensive robotic screening.

  16. anon (the real one) says:

    The million (trillion?) dollar question here is why would taking approved Alzheimer’s drugs reduce the treatment effect of LMTX? taurx prespecified this subgroup because they saw hints this were true in the phase 2 trial.

    How does taking FDA approved Alzheimer’s drugs make your response to LMTX worse than taking LMTX as a monotherapy (assuming LMTX is effective)?

    1. HFM says:

      Assuming it’s a repeatable effect – quite an assumption, alas – I imagine that LTMX must be hitting the same target as previous drugs (never mind what they say it does). If you’ve already been there, done that, and collected your minor improvements in outcome, adding LTMX would then give no further benefit.

  17. anon (the real one) says:

    Phase 2, Page 2 Methods :Subjects. AD medications were excluded from the phase 2 trial.
    It reported strongly favorable results. For some reason the phase 3 trial allowed approved AD treatment. Those receiving these approved treatments did not show a benefit from LMTX.

  18. Barry says:

    Process chemistry is closer to natural product synthesis than is drug discovery/med. chem., albeit with added constraints on reagents and solvents. Med. Chem. in the 21st century puts a premium on a late common intermediate that can be elaborated into a whole class of compounds to be screened, rather than a unique target. The fantasy of the 1980s that we would design a novel drug in-silico to bind/modulate a known biological target remains just that.

  19. Peter S. Shenkin says:

    Well, nobody’s ever going to accuse that molecule of being too 2-dimensional!

    I did a (very little) bit of organic synthesis as an undergrad – just enough to realize that at times you had to try what felt like an Edisonian approach of “if these reaction conditions and solvent don’t work, try these other ones”. I always felt frustrated by the fact that, although there was some rational thinking about why X didn’t work and why Y should be the next thing to try, there was rarely an attempt to figure out whether our reasoning had been sound, even if Y in fact worked.

    Is this still the case? If we had a log of, say, the 1000 ring-forming experiments, or the 100 attempts at stereoselective reduction, (what the conditions were, what was observed at each stage, and what we were thinking when we planned the n+1st attempt), would we learn anything of general utility?

  20. Dr CNS says:

    makes me wonder… how many other reports of activity of natural products are actually not so…

  21. Curt F. says:

    The last sentence of the abstract is Reevaluation of the biological activity calls into question the initial exuberance surrounding this natural product.

    I think that’s an good example of excellent and non-Woodwardian writing. The whole paper generally falls in that category.

  22. Mark Thorson says:

    This would have been a good story for a 2-part feature on PBS’s Nova show. Get inside the meetings in which they were deciding the main approaches, evaluating the pros and cons, assigning pieces of the problem to various researchers. And there must have been specialized meetings, like where the solvent guys get together to decide what solvent mixtures to try first. Then, there would be the enormous amount of sweat working to fill every cell of the spreadsheet. And then the climax when the stuff doesn’t work! I’d watch that!

    1. UndergradChemist says:

      The “solvent guys”? It was one guy. Doing everything. With some help from a postdoc. No teams of researchers making a rational decision on what solvent should work best, just mixing and matching ad nauseum until the reaction works.

      1. Peter S. Shenkin says:

        “No teams of researchers making a rational decision on what solvent should work best, just mixing and matching ad nauseum until the reaction works.”

        That was kinda my question, UndergradChemist. “Edisonian.” And is it safe to assume that there was no attempt to figure out *why* B worked when A hadn’t?

        I keep thinking that there must be *some* way to get useful general insight out of the list of successes and failures.

  23. Anon Dude says:

    How can Baran compare the total step count with previous syntheses when he’s making his chow with the definition of a step?

    “Dude you only lift 45 kg. Pffft I lift A HUNDRED pounds.”

    1. Anon Dudette says:

      If you have read other work on Maoecrystal V, you would notice that other people do exactly same thing. Except they actually do silica plug filtrations and still count it as a single step. If anything, Baran’s definition of step is much more accurate and correct.

  24. Anon says:

    “it seems a bit odd to refer to a practical synthesis that had a single step (out of many hard ones) that needed a thousand tries to figure out the right conditions.”

    I don’t see it this way. Your commentary is on the optimization of the synthesis, not the synthesis itself.

  25. Phil (not Baran) says:

    ” In every case, there appears not to have been enough of the final product produced to actually try repeating any cell assays. If one of the points of total synthesis is to produce bioactive compounds, then something has gone awry here if the bioactivity never gets a look in over all these years and after all this work.”

    With reported nM activity that most certainly isn’t correct if you have produced enough to declare your synthesis successful. No, I suspect the negative result isn’t actually a surprise to some of those groups, but just harder to publish.

  26. anon says:

    1000 experiments? People can get 2 Ph.D.’s with that many experiments. Any idea how long did it take for the student to finish this whole project? I would also like to know how he really feels with this brute force approach.

    1. Phil says:

      Um, I completed over 1000 experiments by the end of my second year and had no results worth publishing. To be clear, this is not bragging. If you know someone who completed a Ph. D. in organic chemistry by running only 500 experiments (what is that <2 per day for one year??), I would like to meet this person.

  27. DevilsAdvocate says:

    While I have to say I’m not a huge fan of the somewhat boastful description of the 1000 trials needed to find the “singularly” successful reaction conditions, how is this that different from the tenacity needed in any other scientific endeavor? Do we fault the medicinal chemists who make hundreds, and often thousands, of analogs to find the singular compound that is deemed worthy of entering clinical trials? Do we mock crystallographers who test hundreds of arbitrary conditions to obtain a structure of a GPCR which may only incrementally advance understanding in this field? In all of these, along with the scientific tenacity to continue, I think the knowledge of when to recognize that efforts are best spent elsewhere is a key attribute; however, since the molecule was completed, the Baran team can’t be faulted here.

    The argument can certainly be made that the latter endeavors are potentially more broadly useful, but it at this stage it’s impossible to comment on the broad applicability of the conditions discovered; no doubt the Baran group or someone else will investigate these in short order. And at the end of the day, we are talking about the efforts of a couple of students during a few years of their education/training. As such students proceed into potential industrial careers such as medicinal or process chemistry, where no doubt 20+ years of work will have much greater implications than 5 years of graduate work, would one prefer to hire someone who’s training involved in depth optimization of a broad range of transformations, or the student who did similar types of often arbitrary optimization, only on 3-4 incremental variations of the same C-H functionalization?

    1. Anon says:

      I don’t think they were boasting about those 1000 experiments, nor did they intend to undermine achievement and hard work of other fields. I believe they just wanted to highlight that it was indeed a difficult transformation and the exotic choice of LaCl3 lewis acid came from experimental observations, that unfortunately took some time.

      I met one of the authors at a conference, the guy was very humble, even too hard on himself. According to him, the reaction had a pretty elaborate set up and the main problem was not the chemical reactivity but engineering of the set up. They spent a lot of time trying to figure out how to scale this reaction up in a reliable way.

  28. LiqC says:

    I had its synthesis proposed for Baran’s tot syn class. One of the key steps was some Lewis acid catalyzed magic, using TiCl4 and unicorn poop. One of the comments from the TA (now Prof. Ian Seiple) was that it might be hard to source unicorn poop for scale up.

    1. skylab says:

      just go to the right stable….

  29. Paco says:

    I think people should be a little less surprised at the irreproducibility of the bioactivity. Back in 2004 I noticed something strange in the original paper. The “great” selectivity reported in the paper was based on a 0.02 ug/mL IC50 for the HeLa cell line versus 1.5E4 to 2.6E5 ug/mL for the other cell lines tested. Given the MW of the molecule in question, the highest of these concentrations is equivalent to 0.7 MOLAR! Now look again at the supporting information and realize that they only isolated 5 mg of the material — a portion of which was diverted to characterization including crystallization and x-ray diffration. Assuming they had 3 mg left to devote to biological testing, and that their assay used 100-fold stock solutions, then they would have had to prepare their stock solution using less than 1 uL of DMSO (assuming no higher concentrations were tested in the assay). This is absurd.

    In 2005 I contacted the authors about this and they replied claiming that there were typos in the manuscript. Those high concentrations should have a negative exponent they said (i.e. 2.6E-5 ug/mL). So sorry! This was also absurd, as the new figures would suggest that these compounds had IC50s around 50 picoMolar. This is an impressive potency, but only slightly more believable that their initial claims — and it would also mean that the “remarkable” selectivity noted in the original report (which fueled all subsequent research) was a misinterpretation of the data.

    So in conclusion, the authors of the paper (as well as anyone who was investigating this compound and actually read the paper) knew that the “interesting” bioactivity was likely nonsense. To my knowledge no correction was ever reported in Org Lett. As a scientific community we dedicated 11 years of synthetic time & $$ to making this useless molecule over and over. With the foreknowledge that the reported bioacivity was nonsensical, could we not have found a better use for those 11 years? The experienced synthetic chemist in me (i.e. cynical curmudgeon) thinks the answer is “no.”

  30. Li Zhi says:

    It just seems to me that either these guys were unbelievably lucky or impressively persistent. Apparently guys with ADHD go into synthetic organic. I was wondering: If their paper ONLY detailed the exact reaction conditions/steps they used, and didn’t discuss the others, would it have been published? It’s great that we’re publishing more negative results. Of course, that plenitude will just bring the day when A.I. can do our jobs better than us closer…

    1. bad wolf says:

      “From autism to automation: the story of organic chemistry” = Future documentary title, 2026.

  31. Yong says:

    Anyone, please tell me what are the definitions of one step and one pot? I saw Baran group count steps like this just recently. I guess if we could do the same “magic” on the syntheses published before, we might be able to make it even shorter. No offence. Nice syntheses though. Only the best chemist can make it without Diels-Alder Rx.

  32. Grouch says:

    Step count pretty simple – see above comments.

    Whatever can be done in the same pot without any work up, filtration, or plugs etc is one step. Sequential additions of reagents are one step (like a swern oxidation). This is not easy to accomplish and you there is no funny business here. Baran’s last several papers have clearly defined what a step is in the SI. Read it.

  33. Justin Peucon says:

    Given that this huge synthetic work eventually resulted in a JACS with 3 co-authors, I hope that the students involved in the project were awarded with *substantial* scholarships.

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