Sunday, March 3, 2013

Blog Syn #003A - Secret Ingredient

(Disclaimer: The following experiments do not constitute rigorous peer review, but rather illustrate typical yields obtained and observations gleaned by trained synthetic chemists attempting to reproduce literature procedures. We've taken efforts to stay close to the original procedure, using similar glassware, equipment, and reagents wherever possible. Images have been cropped and scaled to fit in the allotted space, but have not been digitally altered otherwise.)

It's been a wild month since our post concerning IBX-promoted benzylic oxidation. This piece provoked energetic discussion, evidenced by >200 comments (and counting!) between Blog Syn, two Pipeline posts, and Rich Apodaca's insightful discussion at Depth First

Before we wrap up this topic, we at Blog Syn first wish to thank Prof. Phil Baran, Dr. Tamsyn Montagnon, and Dr. Yong-Li Zhong (the original authors) for engaging us honestly and professionally, and helping uncover some of the hidden factors that make this reaction work.

I think we now know the most important one: water.

After reading Tamsyn and Phil's submissions to #003, we were puzzled: what was so different about our reaction conditions? Everyone was following the same procedure  [Santagostino, J. Org. Chem199964(12), 4537] to make their IBX...right?

Well, not really. No one's published the actual NMR spectrum for IBX in quite some time. Neither this paper, nor Kirsch OL 2006, nor JOC 1999[1], nor Tet. Lett. 1994 (which the JOC refers back to) do much more than provide a list of peaks. This next image shows the NMR spectra provided by Phil, Tamsyn, and by an anonymous commenter online at Blog Syn. Note the rather large water peak at 3.4 ppm (possibly from some pre-opened d6-DMSO?)

Next, I made some fresh IBX strictly following the JOC 1999 paper, which includes two acetone washes to dry the IBX. The small bump at 8.4 ppm, which we had believed to be an impurity, might actually be the OH proton of non-solvated IBX. Note that, as I titrate in additional H2O  the bump disappears, the aromatics shift and coalesce, and the 'signature' water peak grows in at 3.4 ppm! 
After discussion with the Blog Syn crew and the authors, we propose "hydrated IBX" may be the active species for the oxidation:


Co-author Yong-Li suggested some 18O-labeled experiments to determine water's role in the reaction. Sadly, we're not equipped for this type of chemistry, but if any readers are, please feel free to report your findings!

Rxn, 20 h, w/H2O
Now the fun part: "hydrated IBX" performs the oxidation! 

Here's a (straight-baseline) TLC; runs "A" and "B" have varying [H2O] in the solvent, which does seem to accelerate the reaction (right). Prof. Nicolaou had remarked on this trend in the Details of ACIEE 2002, 993 (see p. 996) noting that enone dehydrogenation yields decreased when solvent was pre-dried over 4A sieves.

Using "wet" DMSO and fluorobenzene (5:1), and heating to 95 deg C in a foil-coated, fully-submerged screwtop vial, I'm now able to convert 2-methylnaphthalene to naphthaldehyde in 52% yield (brsm). My colleagues have also observed increased conversion of toluene and 4-bromotoluene, but neither go to completion by the published time points.

So, what should we recommend? It seems clear that several critical details are missing from the original Supporting Info. How much have we deviated from the initial conditions?

Based on the information above, and the results in our hands over multiple runs, we will change our recommendation to Reproducible with optimization

We look forward to future communication with all authors involved, and hope that this interchange inspires chemists to have another look at IBX-promoted oxidation reactions...just add water!

[1] We should point out that JOC 1999 does include KF titration values, but the low water % detected does not rule out sufficient hydration of some IBX. Note also that the elemental analysis values deviate enough to include trace water.


  1. Nice work! This kind of problem solving is what I enjoy most in chemistry.


    Should be a useful resource for anyone having trouble with these conditions in future. Like an online post-doc...

  3. Well, now you're in trouble. That's important enough that it should be a peer-reviewed publication (esp. with some mechanistic data).

    Who's going to be first author? And more importantly, can SeeArrOh submit the dog as his bio picture?

    1. I look forward to ongoing mechanistic studies. Woof!

    2. By the way, do peer-review journals explicitly prohibit anonymous submissions?

    3. A very good question, Alex. Maybe I'll ask around...

  4. Cool. Not surprising, in retrospect, when you think about the structure of the Dess-Martin periodinane.

    1. Our thoughts exactly. Plus, assuming it's fully neutral, it *should* have improved solubility. It also helps to explain several of the other side products in the reaction, such as oxygenation para to phenols.

  5. Although I am not competent enough on the field to fully appreciate the work done I can identify a great work and communication for the benefit of science. Please continue your work. It is very much appreciated.

  6. Although I am typically a lurker, this discussion reminded me of a paper from Stu Schreiber (JOC 1994, 59, 7549) on the acceleration of the Dess-Martin oxidation by water. I have been using this procedure for years and it never lets me down; DMP oxidations in minutes! I make my own DMP and take good care of it, and by applying their procedures, I never have problems. According to Stu, perhaps you should be acknowledging Dess and Martin themselves in your manuscript?!? BTW: keep up the good work, this is important stuff.

    1. Thanks for your comment. We are indeed aware of Schreiber's JOC 1994 paper. In fact, I've often mused about the first line of his Experimental: "Reactions were performed during dry Cambridge winter months...30% relative humidity."

      However, as pertains to IBX, I've never seen our proposed "hydrate" structure (3 OH bound to I) in the synthetic literature (SciFinder, Reaxys, Google). If you are aware of such a study, please let us know!

    2. So I do not know of a study myself, but I think the logic fits that your proposal is reasonable. Isn't DMP just the acetylated version of IBX that renders it soluble in a more broad range of organic solvents? I guess I never felt like these oxidants were that different. We are talking about the same oxidation states regardless.

    3. Comparison of reagent reactivity based on oxidation state alone is a slippery slope. An organometallic chemist might tell you that reduction potential (mV), associative / dissociative mechanisms, solvation, open coordination sites, ligand sphere, pKa, and a whole host of other variables differentiate any one reagent from another.

      For example: Pd(OAc)2 and Pd(OPiv)2 are in the same oxidation states and have similar counterions. However, their participation in C-H activation chemistry is markedly different.

    4. Agreed on the organometallic end of life, but I have yet to see someone reconcile the reactivity of IBX based on a mechanism (SET, etc.) unique to that species vs. DMP.

  7. This reminds me of old Sharpless protocol for catalytic selenium dioxide terpene allylic methyl group oxidation, with tBuOOH 4-5 eqivs, 5mol% of SeO2 and few% of salicylic acid as a co-catalyst. I have been playing with the reaction conditions about 15 years ago and found out that 1) salicylic acid gets eventually chewed up and the reaction slows down from then on 2) about 2 mol% of water helped the reaction go faster (over 5;2 ratio the reaction was actually inhibited with water). My boss suggested that SeO2 needed to be depolymerized into monomeric species but more water will deactivate the electrophile. I then tried unsubstituted tetrazole in place of salicylic acid as a oxidation-resistant co-catalyst and it worked even better and water had no accelerating affect on this system. (We never got around to publish this little study)
    So perhaps you could try few mol% of tetrazole or 5-methyltetrazole as a supernucleophilic co-catalyst for IBX oxidation run in anhydrous DMSO. Unsubst tetrazole is hard to buy these days but you could ask nucleotide chemists, they usually have some around.

  8. I know IBX has a lousy solubility in everything apart from DMSO, but what's it like in DMF? I've got an ampoule of DMF-d7 (-61 °C m. pt) and a scheduled low temperature NMR session next week if someone wants to FedEx me a sample... You might be able to see the dynamic behavior freeze out and should see two species.

    1. IBX is soluble in DMF up to 25-30 mg/ml = ~0.1 M: Mendeleev Communications, 2008, 18(6), 309-311.

  9. amazing work guys (and girls?) love the blog looking forward to the next reaction :)

  10. I hate to be an epic downer, but people need to ask themselves why members of a blog had to invest time figuring out why they could NOT reproduce a reaction found in the literature. I'm not blaming the bloggers at all. I'm blaming the authors of the paper.

    I mean look at us. We are celebrating the fact that we got a little more than HALF of the reported yield described in the JACS paper. Even Phil couldn't get the reported 90%. I would give Phil et al a pass if the yield was 5 or 10% below the reported one, but we're talking a 25-38% difference. That is HUGE and we're calling that optimized!

    Granted, this isn't as egregious as that "Oxidation of Benzhydrol to Benzophenone with NaH" paper, but omissions like these result in the loss of hundreds of work-hours. During my PhD, I had attempted to perform the ketone to enone oxidation with IBX/MPO, and I got absolutely no reaction. Ever since then, I read any Nicolaou paper with extreme caution and skepticism.

    I commend the bloggers for examining this reaction. Too bad we won't see any corrigendum to the JACS paper (and for the whole Nicolaou IBX publication series) anytime soon.

    1. Hi Anon2:46 - Want to discuss this with me directly? Shoot an email over to

    2. It's because they exaggerated the yields in the paper. They lied. Just like all these frauds who put >98% yield after column chromatography. But the incentive to lie is pretty easy. Better yield, better ee, better DR = better paper. If you run a reaction get a 60% yield, why not put 80%? No one will ever know, no one will ever be able to prove you lied, and it makes you look like a better chemist! The shameless self promotion of PI's, the obsession with impact factor, and quantity over quality is killing science.

      In a perfect world, the reviewers of such work, should:

      1. Not know the names of the authors on a paper
      2. Repeat parts of the experiment to determine the quality of science

      If lets say Phil gets 90% yield on a reaction, and four other chemists who try the reaction get 30-70%. Sure, Phil may be a better a chemist, but if something can be reproduced by the average chemist, it isn't very useful is it.

    3. While yield inflation and "best yield" reporting are certainly problematic, and apparently quite widespread, this level of criticism is highly unfair.

      1) The grad students on the original projects probably did the reactions dozens or even hundreds of times. Any chemist knows if you do the same chemistry even 10 times, by the last reaction your yield will be much better. This applies to PB's chosen grad student as well as the blog posters.

      2) In response to: "If lets say Phil gets 90% yield on a reaction, and four other chemists who try the reaction get 30-70%. Sure, Phil may be a better a chemist, but if something can be reproduced by the average chemist, it isn't very useful is it."

      This is utterly and completely false. Many "difficult" procedures are useful and worthwhile. A few that come to mind (of different difficulty, for different reasons) are Rieke magnesium preparations, ATRP, direct (hetero)arylation, or some of the more esoteric DIBAL reductions. It's nice to know just how difficult, but sometimes (usually?) the authors are the best at it, and therefore not the best judges of the so called difficulty for an "average chemist" - whatever that is.

      The problem here is not the reaction, or the chemists, or even the paper. Perhaps the SI could have been better, but it also seems clear the original authors did not fully understand the reaction (and still don't) so many reactions. But, they understood it better than everyone else, and got it to work, and are still helping to iron out the details...years later. It's hard to ask for too much else.

      Also, thanks to the Blog Syn crew for all of this. It is a valuable service to the chemical community.


    4. @SeeArrOh Thanks for the offer, but I would like to remain, well, anonymous.

      Anon1:24's message may have been rather blunt, but he's not completely incorrect. I'm less inclined to believe that this problem is systemic. Not knowing the author of a paper I'm refereeing would be great because I could simply filibuster the paper and take the work....jk. Number 2 is a better idea and Organic Syntheses has been doing that very thing for decades now. However, dissemination of research would slow down to a crawl.

      @Troggy It's completely fine if the authors don't completely understand the reaction, but if it leads to unreliable yields, then they should examine it before publishing.

      Ah the good old days of chemistry. I absolutely LOVE repeating procedures described between the late 1800s to about 1989, especially in German publications like Liebigs Annalen, Chem Ber., and old school Angewandte, because I always got the yield they reported, down to the milligram for both the main product and any side product(s).

  11. Given the sheer number of groups that have used IBX and IBX/mpo for enone synthesis I think you should question your own technique there. There are at least 50 independent groups that have used it.

    1. Do you see any enone? ArMe to ArCHO is a very different transformation, one with which people struggled in the case of IBX... Not to question your judgement, I think you should at least read the post before writing a snotty comment

    2. He was referring to a commenter above that mentioned they could not make an enone from a ketone with IBX/mpo... Maybe you should heed your own advice and read comments before making a snarky reply.

  12. Milkshake I was responding to the above anonymous post regarding enone synthesis - not the whole blog syn entry.

  13. Nice one. Is the hydrate less explosive?

  14. I'm sure that you guys have a flood of chemists wanting to tackle the next big reaction. If not, please let me know how I can help.

  15. I think this is a great idea and want to thank you guys for doing something that you really shouldn't have to do. It would be one thing if you just said "the reaction didn't work" and left it at that, but you guys are actually shedding light on the nuances of the reaction and what is needed to make it work.

    That said, I agree with PSB that there should be a private discussion with the author before anything goes public. I understand that a discussion shouldn't be necessary, that everything necessary for the reaction to work should already be in the SI, but I think it respectful to give the author a shot at making things right BEFORE the failed reaction goes public.

    This has the added benefit of accelerating discovery of the issues hindering the reaction. If Phil hadn't had it run successfully in his lab with data on the reagents supplied, it probably would have taken much longer to figure out water was the issue.

  16. If you have time to spare - it would be incredibly useful to have those NMR spectra uploaded in slightly larger resolution.

    1. Hey, Anon: Email me at seearroh_AT_gmail, and I can send you any enhanced copies you'd like.

  17. This effort is really great, we def need a bigger spotlight on reproducibility in synthesis. Yesterday as a member of GWIS (in the US), I got to meet 5 amazing Indian women scientists as part of an International Visitor Leadership program sponsored by the State Department. They shared a funding opportunity in India that may be of interest conceptually.

    Essentially it's a grant program through CSIR (Indian version of NIH as I understand it) where anyone can submit a proposal, generally highly creative with high risk of failure. This is targeted for people who may be in remote areas or for some reason has had to step away from research. If selected, they will receive funding to carry out the research in the nearest R&D research center/university that has a collaboration with CSIR.

    So the bigger picture of what I'm getting at is the suggestion that an agency with sufficient funds (govt or even ACS) with a vested interest in reproducing work could fund individuals (part-time?) to carry out these reactions at participating labs with existing infrastructure.

    And yes, it is a bit pie in the sky, but no harm in thinking big..

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