You don’t often get to see the sort of fistfight that’s detailed in the latest issue of Organic Process Research and Development. Patents whose procedures are hard to reproduce are familiar to every industrial chemist, unfortunately, but coming across one that seems completely mistaken in its most important details is rare. And this is the first time I’ve seen one of these dragged out into the open literature for a give-and-take with the original authors about whether they’re delusional or not. (The editors of the journal seem to be in new territory themselves on this one).
I should add here that the great majority of patent preps I’ve followed have worked pretty much as described, and I don’t think that my success rate in reproducing them is any worse than procedures from the chemical journals. Some journals more than others, of course, (another topic!) but OPRD is known to be very, very reproducible indeed. As it should be: it’s a journal for process chemists, whose livelihood is refining chemical routes until they’re scalable, economical, and (very importantly) until they work exactly the same way every time they’re run.
So here’s the situation. In 2007, the journal published a paper by a group from Dr. Reddy’s Laboratories, a large Indian company that does both generic drugs and has their own drug discovery operation. (There are, I should note, some academic co-authors who seem to have completely disappeared during this current food fight). The paper covered a synthesis of S-citalopram, and it caught the attention of the process chemists at Lundbeck, in Denmark. And well it might – citalopram (Celexa and other brand names), an antidepressant, was discovered there in the late 1980s, and has been generic since 2003.
The original paper (Eliati et al.) described a new alkylation reaction route to produce a key intermediate and a resolution of it (and of citalopram) into pure enantiomers by forming chiral salts. So far, so good – these sorts of things are the heart of process chemistry, and entirely appropriate for a paper in OPRD. But only if they work.
The Lundbeck group (Dancer and de Diego), had tried that exact resolution of citalopram many times themselves, though, without success, so they were rather taken aback to see it published as working just fine. They detail their attempts to reproduce the Eliati procedure, and demonstrate in great detail that it indeed does not work as written. I won’t go into their experimental work, which is very extensive and painstaking, but nothing the Lundbeck team could do resulted in anything better than a 55:45 mixture, which is a rather poor substitute for a pure compound. Midway through their paper, they start putting the word “resolution” in quotation marks when discussing the Eliati procedure, and the arm’s-length-and-holding-the-nose attitude is very successfully conveyed. The phrases “enormous disparity”, “effectively impossible”, “extremely unlikely”, and “not feasible in any meaningful, practical sense” all make appearances.
They also were surprised at the alkylation reaction reported in the Eliati paper, which is the only one of its kind reported in the literature – well, other than a patent by the same team from Dr. Reddy’s, that is. The weird thing about it is that it uses 3-chloropropylamine, apparently as the isolated free base. My chemistry audience will now be raising their eyebrows, because this is not a compound that you’d expect to be very happy as anything but a salt. It should, in fact, start reacting with itself quite vigorously, with plenty of HCl being given off in the process. But the Eliati procedure doesn’t have enough base to allow for anything else, and they use (supposedly) 12 grams of the stuff in 2.5 mL of DMSO. Since no paper or patent has ever reported isolation of this free base, it’s a rather odd compound to drop into your manuscript without explanation.
Another example of the same reaction in the Eliati paper is even weirder. Not only do they use this never-before-seen chloropropylamine, but this time they do the reaction in acetone, at 60 to 65 degrees C, by first adding 7.5 grams of potassium t-butoxide to 40 mL of the acetone. Now that prep should get the attention of the organic chemists in the audience, because that sounds like an excellent way to make a bunch of hot polymerized gunk. For one thing, acetone boils at 56, so how you get it to 65 is a real stumper. And adding a strong base to it is a surefire way to deprotonate it and start the famous aldol condensation (and every other base-catalyzed ketone reaction you can think of, for that matter). The Lundbeck group tried it, out of sheer curiosity, and got:
”. . . a vigorous/violent reaction. . .with the formation of a quantity of a white solid. (It had) an odor of higher ketones/alkenes, and analysis by NMR indicated that it was a complex mixture of products, with peaks consistent with condensation products of acetone.
A solid majority of the chemists reading that sentence, you can bet, finished reading that and added a “No shit” to the end. This is the sort of thing a sophomore undergraduate should be able to spot, and my guess is that whoever reviewed the Eliati paper for OPRD has had some interesting correspondence with the journal. The resolution is one thing – that’s impossible to spot if you haven’t worked with that exact reaction. But this alkylation step is ridiculous.
The journal gave Eliati and co-workers a chance to respond to all this, and followed that with a last word from Dancer and de Diego at Lundbeck. These things are all published back to back; it's like watching a boxing match. The Dr. Reddy’s group runs up the white flag immediately on the chiral salt resolution, actually, agreeing that their published procedure doesn’t work. But they claim that a modified version of the procedure does work, and that they “inadvertently missed incorporating a few words in the text” of the article which would have made this clear. The Lundbeck group isn’t buying this for a minute. They point out that the manuscript would have been had to have been substantially reworked to make it into this different procedure, for one thing. And even worse, the details of it as reported by Eliati are internally inconsistent, with the masses and ratios not even adding up. And finally, they report their own attempts to reproduce the new procedure, and find that it, too, is basically impossible.
And as for the alkylation, Eliati et al. claim that if you work quickly, you can use the chloropropylamine free base as they described. They also present a table showing how long it lasts under different conditions and in different solvents, and claim to have done the best variation of the reaction on a six-kilo scale. The acetone reaction, they admit, wasn’t as clean, but they didn’t spend much time talking about that because their “aim was to isolate the desired product instead of the aldol product.” Dancer and de Diego aren’t very happy with that either, continuing to insist that the acetone procedure is “completely unworkable”. As for the chloropropylamine, they welcome the clarifications in the second Eliati paper, but point out that said details contradict themselves at one point, and at any rate, none of them are to be found in the corresponding Dr. Reddy’s patent application, which continues to talk about using only the free base, and (on top of everything else) in a way that makes no sense.
The final Lundbeck reply has a telling line in the acknowledgements, which is, in its way, even more pointed than anything else in their paper: “One of us (R.J.D.) thanks Sir John Cornforth for inspiration derived from a series of his articles in a similar case some years ago.” That’s the famous “Some Comments on a Paper by Samir Chatterjee” affair, Tetrahedron Letters 1980 709 and 1982, 2213. Cornforth completely demolished some heterocyclic chemistry work by the unfortunate Chatterjee, pointing out by several lines of evidence that the whole thing had to have been faked. Name-dropping this example is about as direct a statement of your opinion as the scientific literature will allow. . .