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DBL%20Hendrix%20small.png College chemistry, 1983

Derek Lowe The 2002 Model

Dbl%20new%20portrait%20B%26W.png After 10 years of blogging. . .

Derek Lowe, an Arkansan by birth, got his BA from Hendrix College and his PhD in organic chemistry from Duke before spending time in Germany on a Humboldt Fellowship on his post-doc. He's worked for several major pharmaceutical companies since 1989 on drug discovery projects against schizophrenia, Alzheimer's, diabetes, osteoporosis and other diseases. To contact Derek email him directly: derekb.lowe@gmail.com Twitter: Dereklowe

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« Want To Make an Amide? Have I Got Good News For You! | Main | Chemical Biology - The Future? »

September 22, 2010

Synthetic Chemistry: All Mined Out?

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Posted by Derek

In the wake of yesterday's revelation about the latest breakthrough in amide formation, one point that's come up is whether we getting into the era of diminishing returns in finding new synthetic methods.

My opinion? We may well - but we shouldn't have to be. It is true that we know how to do an awful lot of transformations. And I'd also subscribe to the view that we can, given no constraints of time, money, or heartbreak, synthesize basically any stable organic molecule that anyone can think up. In what we're pleased to call the real world, though, constraints of money and time (related by a similar equation to Einstein's mass-energy one) are always with us. (Heartbreak, well, that seems to be in constant supply).

So even though we can do so many things, everyone realizes that we need to be able to do them better. That applies even to amide formation. There are eleventy-dozen ways to form amides in the literature. But as some of the comments to yesterday's post show, sometimes you have to go pretty far down the list to get one that meets your needs. There is no set of conditions that is simultaneously easy, fast, cheap, nonracemizing, nontoxic, tolerant of all other functional groups, and generates a benign waste stream. Finding such a universal reaction is a fearsome goal, especially considering the number of alternatives that have already been tried.

This is why stoichiometric samarium metal is such a ridiculous idea. There are a lot of good ways to form amides. And there are a lot of lesser-known ways that might save you in tough situations. And there are lots of stupid, crappy ways. The world does not need another one of the latter. So what does it need?

Well, if you're going to stick with amide formation, you're going to have to find something closer to that ideal reaction, which won't be easy. Several other transformations are in that same category - lots of alternatives available, so something new had better be good. There are, though, plenty of other reactions that don't work so well, where improvements don't require you to approach so near perfection. A person's time might be better spent there than on trying to find the Perfect Amide Reaction, although the impact of finding the latter would probably be greater. Neither possibility excuses time spent on finding Another Lousy Amide Reaction.

And there are a lot of transformations that we can't do very well. Turn a phenol into an aromatic aldehyde in one step. Selectively epoxidize aromatic double bonds. Staple a secondary amine in where an aliphatic C-H used to be. Fluorinate at will. You can go beyond that to reactions that you can't even think up a mechanism: go around a benzene ring, switching out carbon for nitrogen. Pyridine, pyrimidine, pyrazine. . .I have no clue how to do that, or if it's even possible. Change a given oxazole into its corresponding thiazole. Turn a methoxy back into a methyl group. And so on - we sure can't do those, and the list goes on.

Hard stuff! But there are plenty of non-science-fictional possibilities out there, too. An eye to applications beyond pure synthetic chemistry helps. Look, for example, at Barry Sharpless and the copper-catalyzed triazole formation (click chemistry). That's a nice little transformation, and there are people who probably would have just made a nice little Org Lett paper out of it if they'd discovered it themselves. But it's such a versatile way to stitch things together that it's finding uses all over the place, and the end is not in sight. The world could most definitely use more chemistry that can take off in such fashion, and surely it's out there to be found.

I realize that we had this discussion just back in August, and earlier in the summer. But it keeps coming up. Seeing someone form amides with a pile of elemental samarium brings it right back to mind.

Comments (41) + TrackBacks (0) | Category: Chemical News | Who Discovers and Why


COMMENTS

1. John on September 22, 2010 9:21 AM writes...

I see the point you're making. The problem is that we are not really training our chemists to approach problems like this. Problems like this take creativity, we're too busy making them work 75 hours a week to give them time to be creative.
Heck it starts in elementary school, there was an article recently in newsweek about how creativity can be taught, but we spend our time trying to get children to do better on standardized tests.
Stop the labor theory of value as applied to science.
The other thing people need is a basic understanding of things other than just synthetic chemistry. As you pointed out a lot of people would have turned the Sharpless paper into an Org. Lett paper. It took his knowledge and understanding of the possible applications to see the possibilities of the reaction. How can students learn these things when the goal of their advisers is to get them to produce papers and they are chastised for trying to broaden their education.
Just my two cents, if we don't want crap, lets end the sweatshop nature of phd training and actually take some time to educate young scientists. Show them some value in creativity, and originality. When your system is essentially run under a labor theory of value all you're gonna get is labor, and just labor is what produces papers like what we're discussing.

Permalink to Comment

2. Anonymous on September 22, 2010 9:30 AM writes...

It's very simple.

Academic Research today goes like this:

What -> How -> Why.

Look what I discovered in the lab -> how do I turn this into a JACs -> why is this important (usually addressed when the paper is being written).

When it really should go:

Why should I be doing this -> How am I going to solve this problem -> what I am going to do to make it happen.

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3. anonymous on September 22, 2010 9:42 AM writes...

In my own experience, I realized that my PIs method for making the natural product was going to take gobs of material and 2 full years for an end game which may not work. On my own time, I developed and executed a new method to get to the core in 6 steps vs. 24. I even got a freakin' crystal structure to prove the stereochemsitry. However, since it was not the PIs chemistry, I was told it was of no use and not to pursue it further.

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4. Ed on September 22, 2010 9:55 AM writes...

John #1 - google Robinson and ted dot com. The videos hits make wonderful watching.

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5. CMCguy on September 22, 2010 10:48 AM writes...

My old PI used to warn the more procedures published for a particular transformation then this likely reflects problems with application of a procedure to specific case you actually want to do. Often this issue of what you apply all comes down to a matter of perspective. Academics are most interested in publishing and training so demonstration of an incrementally different reaction does accomplish that (and who knows sometimes they were attempting more dramatic and end up have to make lemonade). Med chemists typically want to make many derivatives thus seek widely general procedures so as long as chemistry gets to the target analogs quickly without being too onerous they will be happy. Process chemists may be able to focus on a single target compound but the goals are largely those in paragraph three and usually becomes a balancing act with struggle against reality.

As pointed out in the earlier post sometimes nature through enzymes can come closet at times to achieving these criteria however is rare to have biochemical system that works beyond a limited group of substrates. While there has been much effort in the area I am not convinced can yet effectively harness the ability of nature to integrate in productive syntheses.

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6. Keith Robison on September 22, 2010 10:50 AM writes...

Is there a public hit list of the most desired transformations? Or perhaps a virtual futures market in what transformations are likely to be published in a reputable journal in the next agreed upon timeframe?

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7. anon on September 22, 2010 11:01 AM writes...

I actually am becoming more and more convinved that the more hours you work, the stupider you are.

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8. RM on September 22, 2010 11:32 AM writes...

I think Derek touched on a subtle point I'd like to make explicit.

Deliberate(*) new reaction development should be driven by particular use case. You need to have a particular transformation in mind, and need to have reasons why the existing ways of performing it are sub-standard (don't work/poor yield/side products/no access to reagents/etc.). Then the new reactions need to be evaluated on those merits. Just coming up with a new technique for an old reaction with a shrug and a "someone might find it useful someday" probably doesn't get us far.

Incidentally, I think that natural product work lends itself easily to this. You have a defined compound that you can't really alter to make things easier, you have a bucketload of functional groups that you need to work around, and you're probably limited in material quantities, so yield is a consideration, and the d*mned thing is probably not soluble in the solvent you'd prefer to work with.

(*)I'm ignoring the serendipitous discoveries. The "we found this reaction mechanism when we investigated why a "side product" was obtained in 70% yield"-type situations.

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9. Daniel Levy on September 22, 2010 12:21 PM writes...

I completely agree with Derek's assertion that almost any stable organic molecule can be synthesized using existing chemical technologies. Many of the transformations mentioned (such as converting benzenes into pyridines, selective epoxidation of aryl groups, converting methoxy groups into methyl, etc.), while potentially useful, are actually only nice to have.

Because we are able to prepare most any organic structure, the problem is now reduced to how such compounds can be prepared. That is where creativity is manifested - certainly not in the realm of additional methods for preparing amides.

From a medicinal chemistry standpoint, while productivity could be enhanced with "nice to have" transformations, the overall goal is to obtain as many relevant structures as is necessary to assess the potential of a given series. When a promising compound is identified, process chemistry efforts are initiated to determine the most efficient method of preparation for that specific compound of interest.

From an academic standpoint, there is always room for new and novel contributions to organic chemistry. This applies not only to the total synthesis of natural products, the study of novel polymers and the design of new catalysts/reagents but also to the design of novel, efficient and generally applicable transformations. The click chemistry developed by Sharpless certainly falls within this category. I am not certain that this applies to samarium-mediated amidations.

A story I heard during my undergraduate days relates to a statement asserting that everything was already known about organic molecules. Shortly after that statement was made, ferrocene was discovered and the field of organometallic chemistry began to emerge. As long as we are creative, possibilities are endless.

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10. bbooooooya on September 22, 2010 12:27 PM writes...

Natural progression since Wohler in 1828. Reactions are there, just smaller and less groundbreaking.

Sure, Sharpless/Suzuki chemistries were cool, but what have you done for me lately? Combi chem? Solid Phase synthesis (ooops, 1960s there)?

Still useful, but more dotting i's and crossing t's than climbing Mt Everest.

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11. mikeymedchem on September 22, 2010 12:53 PM writes...

Perhaps a timely article in Angew Chemie published online yesterday:

Factors Determining the Selection of Organic Reactions by Medicinal Chemists and the Use of These Reactions in Arrays (Small Focused Libraries)

DOI: 10.1002/anie.201002238

Permalink to Comment

12. anchor on September 22, 2010 1:47 PM writes...

As long as we have this "publish or perish" mentality in the academic World, nothing is going to change. Time will come to pass and on another day, we will have the same discussion when we see another synthesis of "amides" with stoichiometric radium. It is the quality over the quantity. And, I have seen it all even in pharmaceutical industry

Permalink to Comment

13. Anonymous on September 22, 2010 2:50 PM writes...

How about about a reasonable protecting group for a secondary amide? (besides SEM, PMB)

Even better, how about a mild method to remove a methyl group from a tertiary amide. CYPs can do this well. Is there a synthetic method to compare?

Permalink to Comment

14. European Chemist on September 22, 2010 3:04 PM writes...

I think #2 got it right, albeit in a bit blunt manner.

Problem is, as a PI there is a lot you need before you can embark in the process of "finding out how to go around a benzene ring and substitute carbon with nitrogen", for example. You need
- A big group so that other people can be working on "safe" chemistry that will produce papers
- Secured funding that allows you to employ the 2-3 students working on such wild ideas that might never get anything out of it
- Motivational skills to keep people foccused on such tough projects after the 3rd year of 0% yields
- and last but least, the creativity to come up with something reasonable to tackle those problems! Most people are just picking what's more comfortable. You will definitely not see any new PI's tackling anything too risky because more than 2-3 years with no publications can mean your early "academic death".

As for the assertion that everything has been discovered, well, as pointed out before, it's just because we're cranking out a generation of chemists that has not been trained to think out of the box but rather to propose incremental advances.

And let's not forget that surely the most groundbreaking of discoveries very often come through serendipity. I still believe that's the way a more efficient olefination procedure than Wittig (something I would love to see discovered) will eventually be found.

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15. Thomas McEntee on September 22, 2010 3:09 PM writes...

Read "Biocatalytic Asymmetric Synthesis of Chiral Amines from Ketones Applied to Sitagliptin Manufacture" by Savile et al. (Science, 16 July 2010 329: 305-309; published online 17 June 201017 June 2010 [DOI: 10.1126/science.1188934] (in Reports).

Is this synthetic chemistry? Is there truly a line separating chemistry from _molecular_ biology? IMHO, those chemists who see such a line are self-limiting; those molecular biologists who see it are self-serving.

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16. tt on September 22, 2010 3:41 PM writes...

RE McEntree

That's a good example, contrary to CMCguy's comment, where an enzyme turned out to be a very broad, general catalyst (evolved from 0% activity) for converting ketones to amines. Enzymes are just really big "organocatalysts" that are much, much easier to make libraries of. Evolving an enzyme to do something nature never intended is no different then screening hundreds of ligands, metals, and conditions to optimize a hydrogenation (it's just a lot less work).

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17. Marcus on September 22, 2010 4:42 PM writes...

To illustrate some of the points already raised,
Buchwald's back to back asap org lett. papers could be exhibit A.

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18. CMCguy on September 22, 2010 6:08 PM writes...

#16 tt perhaps I am just out of touch with current utility in the area because what you describe speaks to harnessing from nature's toolbox for productive synthesis and the field must have evolved (literally it sounds like) to get around the substrate specificity issues I eluded to. Enzymes in Organic Chemistry went through a stage of strong interest in I think was the mid-late 80s/early 90s, with related exaggerated claims as a paradigm shift for being able to do everything desired in synthesis. My impression was one of the major draw backs that held it back was inability to apply a particular enzyme broadly enough and each new analog became an involved research study in itself to find then improve for the job (I also think per #15 some self limiting behavior existed). It's great if are now achieving practical applications in more general way as always believed nature did many fundamental chemistry operations so much better. A 15-20 year cycle between hype and substantive success also would be fairly typical.

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19. Thomas McEntee on September 22, 2010 6:41 PM writes...

The paper I suggested as a legal mind-expanding read comes out of the California company, Codexis. I had run across Codexis at various US and European pharma trade shows and was intrigued by their thesis that naturally-occurring enzymes can be modified to enable their use in mixed organic-aqueous solvents, at temperatures > 37 C, and at substrate loadings far higher than you commonly see in industrial biotechnology. The Science paper describes an elegant and sophisticated process that brought the same sense of wonder I had reading the papers of the giants in natural products synthesis as I was finishing my undergraduate chemistry studies in the mid-1960s.

Mind you, the work to model and carry out the necessary mutations (27 or so mutations) to this enzyme, including those necessary for activity in in its dimeric form looks like grunt work. What boggles my aging mind is the rapidity with which such work can be done today. If I were in my early 20s and looking for a path to base a career on, it's this type of work. I should not have suggested that I have anything less than the highest regard for molecular biologists...my point was that workers in both fields forget that traditional organic chemistry and molecular biology are just different regions on a continuum...but they're both about organic chemical bonds.

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20. Francium on September 22, 2010 8:19 PM writes...

I am still going to publish a series of papers on the use of francium carbonate as a base for a variety of organic transformations.

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21. #2 anom on September 22, 2010 8:39 PM writes...

Is it possible that creative people don’t choose to do chemistry anymore?
Did our education system steer them away? Maybe just awarding big scholarships on grades alone is not a good idea.

When I was in Grad school I used to set up 5 small reactions every other week just on some crazy transformation that was the thermodynamically possible. I would inject them on the GC/MS to see if anything interesting popped up.

How many people will try something that has a good chance of NOT working?

There are still so many practical problems identified 20-30 years ago that have yet to be solved. Please read “the way of synthesis” by Hudlicky for the full list.

The main problem is the gross bandwagon’ing that goes on in academics. Every time I read the literature I roll my eyes at the recycled garbage that is peddled out there as cutting edge research. Everyone has become very good at justifying mediocre research.

And thanks useless peer review system which is really done by overworked apathetic grad students.

The worst part is that no one has the balls to stand up and say, we are not doing useful and meaningful work; we are wasting time and money. The system is broken but no one wants to rock the boat. The people in charge certainly do not want it to change.

Anyone have the solution?

Permalink to Comment

22. Oliver on September 23, 2010 3:25 AM writes...

Mention of Sharpless' 'click chemistry' always leaves me a little disappointed:
"Look, for example, at Barry Sharpless and the copper-catalyzed triazole formation (click chemistry)."

These 3+2 cycloaddtions, including those with azides were looked at in detail 40-odd (50??) years ago by Huisgen, in particular. I've always thought it was a little disingenuous of Sharpless, in spite of his achievements, to take an old reaction,'re-brand' it and call it his own.

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23. Mat Todd on September 23, 2010 5:45 AM writes...

Interesting that people mention the wonderful Codexis paper. This was right next to another stunner in Science, the Baker design and evolution of a Diels-Alderase. 10.1126/science.1190239. In these papers bugs are doing the grunt work, not grad students.

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24. Will on September 23, 2010 7:46 AM writes...

re epoxidation of benzene

Harman (and probably others) have developed metal systems that complex aromatics in such a way they can participate in Diels Alder type reactions. Seems like the metal/ligand could be tuned in such a way to active two carbons to an epoxidizing agent. Maybe this has already been done?

To me, the next frontier in organic chemistry is not in methodology for NP/drugs, but rather converting biomass into hydrocarbons for fuels/plastics. A catalyst that could reduce hydroxyls and aldehydes into methylenes using water as the hydrogen source

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25. Chemjobber on September 23, 2010 7:57 AM writes...

Re #22:

I think it's important to note that Sharpless most certainly does not hide the fact that Huisgen is the originator of the Cu-catalyzed cycloaddition. In fact, if you ask any one of his students/postdocs, they will tell you that 'click chemistry' is a concept and that the Cu-catalyzed azide-alkyne Huisgen cycloaddition is only an example of that concept (pretty much in those words.)

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26. Scripps Florida on September 23, 2010 8:06 AM writes...

There's lots of new methodology being developed for new reactions that will hopefully drive medicinal chemistry, not the other way around - i.e. hey, let's do a bunch of Suzuki reactions and reductive aminations to get lead molecules!

NHC catalysis and H-bond (urea, thiourea) are just two "bio-inspired" ways that generate less-toxic waste streams and offer high reactivity and chance for stereocontrol, not to mention all the proline and imidazolidinone catalysis.

C-C bonds are now being forged with Fe, Re, Au, Ti, Si....hardly the players usually thought of (Pd, Ni, Ru)...[3,3] has inspired work in [2,3], [3+3], [4+3], etc....and C-H functionalization reactions are coming to lower temperatures and accessing more densely-packed aromatics in single-step operations.

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27. bad wolf on September 23, 2010 8:12 AM writes...

to follow up on #25Chemjobber, a 're-branding' can also be a good thing, as an obscure name reaction can be popularized to biochemists and chemical biologists to actually do something new and productive with the reaction. Sitting in a 40 year old textbook wasn't doing anyone any good!

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28. David on September 23, 2010 8:58 AM writes...

To follow up comment number one, it seems to me that we have placed ourselves under so much pressure to be productive in the lab. As a consequence, there is little space to innovate in industry (on top of this trend to reduce thinking time in academia). I wonder if part of the problem is the reduction in headcount across chemistry in Europe and the US, replacing us with different skills and experience elsewhere. I wonder where this leaves pharma companies in terms of their ratio of chemists: bioscientists: DMPK. In my research area, the ratio is probably in the region of 1.0:2.0:0.8. How does this compare to 10 years ago, 20 years ago? How does this compare to other companies?

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29. bbooooooya on September 23, 2010 9:02 AM writes...

"they will tell you that 'click chemistry' is a concept"

Indeed, a shockingly brilliant paradigm of 'doing reactions that work well'. Whoda thunk that opening an eopxie with an azide would work....

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30. RM on September 23, 2010 10:58 AM writes...

bbooooooya@26 - If "doing reactions that work well" is so obvious, why was (comparatively) no one using the Huisgen reaction in the first few decades of its life? Also "working well" isn't the entirety of click chemistry/chemoselective ligation, unless you're simplifying to the point of useless imprecision. Coupling an acid chloride and a primary amine could be said to "work well", but would in no way be considered click/chemoselective.

Where click chemistry and chemoselective ligation have taken off is primarily in the bio-related fields, where prior to the SOP was either "selectively protect more reactive groups, selectively protect the coupling point, selectively protect all other reactive groups, selectively *deprotect* the coupling point, perform the conjugation, then deprotect all other groups" or "f*ck it, just label the d*mned thing nonspecifically." Sure, there were selective methods, but in general they required certain solvents (which the bio-substrate probably wasn't soluble/stable in) or gave small yields (a non-starter when 1 mg is considered a large amount
of starting material), or had some other issue, so most people didn't even consider it.

It really wasn't until Sharpless started banging on about click chemistry that people seriously considered that there might be a better way to do things. *That's* the click chemistry/chemoselective ligation concept - that reactions which can be performed specifically in mild conditions *actually exist and can be used*. Why do you think a large number of people talk about the "click reaction"? It's because they hear about the reaction and think "*I* could do *that*!", where prior to that it would have been too much of an effort to even bother. (It doesn't hurt that it has a catchy name that they can remember after they get home from the conference, either.)

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31. bbooooooya on September 23, 2010 1:02 PM writes...

"was (comparatively) no one using the Huisgen reaction in the first few decades of its life?"

No clue. I'd assume for the same reason that people like to forget about then reinvent investing castles in the sky, from tulip bulbs to south sea trading companies to the -tron stocks to pets.com. I'm not saying the chemistry done wasn't neato. heck, I fully believe that the AE, AD, and AE are brilliant, it's just that click chem is nothing new and does not need a new name.

Combining good nucleophiles with good electrophiles, and then directing then with some Weinstein or Furst-Plattner chemistry really should be called just that, "doing old chemistry that happens to work really well"---proclaiming it "click chemistry" is disingenous and self-serving (though I do note that KBS very well references those who invented the actual reactions).

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32. bbooooooya on September 23, 2010 1:49 PM writes...

Out of curiousity, is anyone aware of a "click molecule" that has progreesed to a Phase 2 clinical study?

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33. partiail agonist on September 23, 2010 5:34 PM writes...

In his Angew. review in 2001, Sharpless defined click chemistry as a group of reactions that “...must be modular, wide in scope, give very high yields, generate only inoffensive byproducts that can be removed by nonchromatographic methods, and be stereospecific (but not necessarily enantioselective). The required process characteristics include simple reaction conditions (ideally, the process should be insensitive to oxygen and water), readily available starting materials and reagents, the use of no solvent or a solvent that is benign (such as water) or easily removed, and simple product isolation. Purification, if required, must be by nonchromatographic methods, such as crystallization or distillation, and the product must be stable under physiological conditions”

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34. JK on September 23, 2010 6:09 PM writes...

I'm not a chemist, but a bit surprised at people saying that the methods are there to make any stable organic molecule.

e.g.

1) a 15kDa polypeptide with non-natural side chains. Introduce half a dozen covalent cross links in the core of the folded structure.

e.g.

2) A big buckball with a few hundred carbons. Now introduce an internal carbon chain connecting two specified atoms. Maybe add another internal chain, and make them twist around each other exactly twice.

etc.

People can really make *anythin*?

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35. bbooooooya on September 23, 2010 6:23 PM writes...

"In his Angew. review in 2001, Sharpless defined click chemistry as a..."

Sounds to me like pre 1960s organic chemistry....

Permalink to Comment

36. Tyrosine on September 24, 2010 2:50 AM writes...

How about a catalytic Friedel–Crafts reaction? An absolute gold mine for industry... FC has my vote for simultaneously being one of the most industrially useful and dirty reactions. Stoichiometric AlCl3 or polyphosphoric acid... sheesh.

Permalink to Comment

37. Jordan on September 24, 2010 8:30 AM writes...

The problem with "click molecules" in drug candidates is that no-one wants to make or handle organic azides on scale. Same applies to some of the other interesting materials chemistry using this reaction.

So -- interesting chemistry, but ask me to make 1 kg of a benzyl azide and I will politely decline.

Permalink to Comment

38. CMCguy on September 24, 2010 10:26 AM writes...

Jordan there are a couple ways to look at this. If a drug candidate of sufficient interest or potential (market-wise mainly) comes along that has unfavorable structure/chemistry likelihood increases work will be done to development alternate less hazardous routes or appropriate technology applied to handle the dangerous operations. This is function of process R&D and are many successful examples of those in pharma/chemical industry.

The other way with costs pressures being what they are these days, not knowing what that will take to prompt actual process R&D investment, the option is to outsource the bad stuff to Chindia with someone willing to not "decline" such endeavors. As has been noted many times in discussions in the blog besides lower labor other parts of the world have less stringent safety and environmental concerns so if a need is there can probably contract any type of chemistry. Might have to pay a premium and would want several different locations in operation. I inherently question the ethics of this approach however again believe many examples, much quieter, exist.

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39. Stu Jordan on October 16, 2010 2:08 PM writes...

Reading all this makes me want to be a chemist. What is the future in biochemistry? If you were in your 20's and decided to earn your graduate degree...what area would you specialize in?

Stu

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Our Most Snorted-At Papers This Month. . .