About this Author
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: Twitter: Dereklowe

Chemistry and Drug Data: Drugbank
Chempedia Lab
Synthetic Pages
Organic Chemistry Portal
Not Voodoo

Chemistry and Pharma Blogs:
Org Prep Daily
The Haystack
A New Merck, Reviewed
Liberal Arts Chemistry
Electron Pusher
All Things Metathesis
C&E News Blogs
Chemiotics II
Chemical Space
Noel O'Blog
In Vivo Blog
Terra Sigilatta
BBSRC/Douglas Kell
Realizations in Biostatistics
ChemSpider Blog
Organic Chem - Education & Industry
Pharma Strategy Blog
No Name No Slogan
Practical Fragments
The Curious Wavefunction
Natural Product Man
Fragment Literature
Chemistry World Blog
Synthetic Nature
Chemistry Blog
Synthesizing Ideas
Eye on FDA
Chemical Forums
Symyx Blog
Sceptical Chymist
Lamentations on Chemistry
Computational Organic Chemistry
Mining Drugs
Henry Rzepa

Science Blogs and News:
Bad Science
The Loom
Uncertain Principles
Fierce Biotech
Blogs for Industry
Omics! Omics!
Young Female Scientist
Notional Slurry
Nobel Intent
SciTech Daily
Science Blog
Gene Expression (I)
Gene Expression (II)
Adventures in Ethics and Science
Transterrestrial Musings
Slashdot Science
Cosmic Variance
Biology News Net

Medical Blogs
DB's Medical Rants
Science-Based Medicine
Respectful Insolence
Diabetes Mine

Economics and Business
Marginal Revolution
The Volokh Conspiracy
Knowledge Problem

Politics / Current Events
Virginia Postrel
Belmont Club
Mickey Kaus

Belles Lettres
Uncouth Reflections
Arts and Letters Daily
In the Pipeline: Don't miss Derek Lowe's excellent commentary on drug discovery and the pharma industry in general at In the Pipeline

In the Pipeline

« Neat! Wish It Were True! | Main | The Big and the Little »

December 3, 2007

Exciting Nonsense Wins Another One

Email This Entry

Posted by Derek

The lessons of the recent pyridinium follies are old ones. We’re going to have to relearn them again and again – doomed, if like. That’s because as scientists we’re pulled toward two opposite sorts of error when it comes to new ideas, and because in science, everything comes down to new ideas. We’ll have these problems with us always.

The first error, for which the recent retracted papers are the latest posters on top of a thick, stapled, stack, is to become too infatuated by one’s own ideas. It’s a very easy emotion to yield to. To use an unexpectedly R-rated metaphor, it’s the intellectual equivalent of sexual excitement. Under either influence, potentially dangerous decisions and courses of action can begin to seem reasonable and natural, in contrast to how they might appear in less agitated states of mind. Objections, even quite real and forceful ones, are swept aside as being trivial, fit to deal with later after the important business at hand has been concluded.

The problem is, the best scientific ideas induce this state of mind, and in proportion to their scope. I’ve been hit by a few of these, at my own level, and it’s difficult enough. Think about what goes on up in the heights! Can you imagine what it must have been like for James Clerk Maxwell to tie all of electromagnetism up into a perfectly wrapped gift box with three bows on it? Or for Watson and Crick, looking at their DNA model when they were the only two who’d seen it? That intense joy of discovery, of being right, causes people to behave in strange ways. But it’s one of the driving engines of science and always will be.

By the standards of the great discoveries, these latest cases are trivial – as is most work by most scientists, and all of mine, I hasten to add. But the same principles apply. You look at these things and think “Why didn’t they look into known pyridinium chemistry more? Spend some extra time in the library? Some of those salts are surely crystalline – why didn’t they get an X-ray structure as soon as possible?” All perfectly good questions, from outside, and in retrospect. But any of us could end up brushing aside similarly good questions about our own work, and we shouldn’t forget it.

Now for the other error. The excitement of a new idea has a flip side: the depressed (and depressing) feeling that it must have been done before. Surely this can’t be as good as it seems, otherwise it would be known, right? Most new ideas die. Actually, punishingly near all the new ideas in science die, and most of them die quickly. This spectacle horrifies and numbs many scientists, especially if they have sensitive or fearful natures, and causes them to keep their heads down. No breakthrough, no cry.

If you stay in this mindset long enough, the problem takes care of itself: you’ll train yourself to no longer have many new ideas at all, and you need not face the prospect of watching what happens to them. Unusual, potentially interesting things may happen to your experiments, but you won’t be fooled: into the red waste can they’ll go, along with all the other stuff that didn’t give you what you wanted. Nobel prizes have been poured into red waste cans.

Transportation metaphors are safer than copulatory ones. Discovery, then, is a road with ditches on both sides of it, and the hard part is steering between them. Too much optimism and you go whooping off after junk – or worse, catching it and publishing it after writing your name all over it. Too much pessimism, though, and you never accomplish anything at all. I’ve got mud from both sides of the road on my lab coat – how about you?

Comments (12) + TrackBacks (0) | Category: The Scientific Literature | Who Discovers and Why


1. Rich Apodaca on December 3, 2007 12:08 PM writes...

"Nobel prizes have been poured into red waste cans." You've nailed it. This is the tension that makes the discovery of something truly new such a rare event.

Your scientific career stagnates when your need for respectability outweighs your need to pursue new ideas wherever they might lead.

Your scientific career implodes when your harshest critic is outside your own head.

It takes an unusual kind of person to face both realities and thrive.

Permalink to Comment

2. milkshake on December 3, 2007 1:37 PM writes...

All they could have done is to look in more deail on the isotopic envelope in the MS spectra. Theirs is rather bad, elementary way of screwing up. It should have raised the reviewers concerns.

By the way, I accidentaly run acros a more subtle problem in a JACS article - we were asked to "review" an article of our choice as an excersize in school and there was the exciting paper about BINAP-Rh catalyze asym conjugate addition of boronic acids to enones. Very solid work, with ees done on chiral HPLC/GC - until you look close to the way they determined the absolute stereochemistry of their products. They did so only for 2-cyclohexenone (by chiral derivatisation) and they simply assumed that all other substrates provided the same sense of induction. No worry that the transistion state could change for non-cyclic substrates.

I also saw a published paper in EJOC that was an exact re-discovery of a cyclization mentioned as a footnote in some J.Med. Chem paper 20 years earlier. The annoying part was that the authors apparently became aware of the probelm as they were preparing their manuscript and they managed to tiptoe about the embarassing truth without re-wording their intro about how original and tremendous their contribution was.

The referees don't get paid and often they are very busy. My boss gave me an article to review - he did not want to spend time on it himself - and I did not spend much time on it either and I missed important things (the paper was in the difficult category - unremarcable but not bad enough to reject, with lots of literature precedents to cover).
There has to be some way of making the review process less superficial

Permalink to Comment

3. Hap on December 3, 2007 2:42 PM writes...

MS: That is pretty standard, unfortunately, for asym. catalysis papers. If one is fortunate, they determined the absolute stereochemistry for more than one structure and only did reactions of analogous substrates so that you might have an idea what the reaction might actually get you.

I think the compromise between persistence in the face of unfounded criticism and ignorance of valid criticism is sometimes hard to achieve. People don't always play nice, and some of their criticisms may be ill-intentioned or poorly thought out. We are supposed to be rational about our own ideas, and to ask as many questions of ourselves as possible to protect ourselves from the criticism of those people. I don't remember who said that it is best to prick your own balloons (ideas) before someone else does, but that sentiment seems valid.

In case one isn't critical enough of one's research, the reviewers are present to assure that the obvious questions that one needs to answer for in one's work have been answered (so that the journal doesn't have to answer unpleasant questions after publication.) Data standards would also help (so that one's claims are backed up with an appropriate amount of data (and, no, NMR spectra for the final product and the penultimate intermediate do not count as sufficient data for a 37-step total synthesis).

Permalink to Comment

4. Anne on December 3, 2007 3:01 PM writes...


I'm a grad student (in astrophysics), just at the beginning (so my standards for discovery are low), and I recently made my first observations. The feeling of actually *seeing* something was astonishing. Nothing quite like it has ever been seen before. That giddy feeling lasted only a couple of days, but I am so far managing to channel the doubts into going over the data with a fine-toothed comb. I know I'm going to reach a point, soon, where I know everything that's in the data set we have, and I have a feeling that we just won't know for sure whether what we're seeing is real. Since this is a transient source, it's all too possible that we won't see it again, and we'll be left with a big “maybe”.

The story also reminds me of the story of Jocelyn Bell's discovery of the first pulsar: she saw some trash on her chart recorder tapes. She noticed it had an unusual character, and that it repeated at the same sidereal time every day, and she followed it up. But an earlier researcher saw the same phenomenon, gave his chart recorder a whack, and it went away, costing him a Nobel prize.

Permalink to Comment

5. Wavefunction on December 3, 2007 3:24 PM writes...

As the late Carl Sagan said, the key to science is to tread the tortuous road between open-mindedness and skepticism. It's hard.

We see what we want to see. All of us. In all walks of life. There's no escaping that.

Permalink to Comment

6. JSinger on December 3, 2007 5:13 PM writes...

Nobel prizes have been poured into red waste cans.

My favorite example -- do you know how many people used sense RNA as a "positive control" in their 1990's antisense experiments and didn't get the expected result, before Mello and Fire thought to wonder about it? Literally hundreds, if not thousands, of labs had seen RNAi in action and ignored it.

Quite a few grad students and postdocs were berated for their supposed incompetence, I can tell you.

Permalink to Comment

7. Great Molecular Crapshoot on December 3, 2007 5:21 PM writes...

In Pharma, it's not just optimism versus pessimism. There is the herd instinct which I suggest is the reason that so much flakey data analysis is not challenged with the vigour that it should be. Research managment love to believe that 'molecular descriptor of the month' is a reliable predictor of oral bioavailability because it gives their Leadership a pleasing quantitative edge (search The Crapshoot for 'physics envy' to find out more). The journals don't help by publishing analyses based on proprietary data sets using in house software that are impossible to verify.

At least the pyridine follies got picked up. With a lot of the QSAR/QSPR/pharmacophore/docking stuff, it is really difficult to figure out whether it's good or complete BS. There are ways however. One QSAR paper I bounced, was fitting experimental pIC50s to 0.02 units. Clearly overfit but the PLS model didn't think so. There were other problems but overfitting would probably have been sufficient to dispatch it on its own.

Permalink to Comment

8. milkshake on December 3, 2007 5:34 PM writes...

We had a guy who came from an academic group studying cannabinois, doing assays and medchem too. He said he could not trust any published data that came out of their group: their assays did not work, their biologist tended to manufacture the results the PI expected from him. Some group members were presenting stuff they never synthesized, many submited compounds were terrible mixtures often not containing even a trace of the correct compound and so on. This was apparently going on for years and the standards within the group were getting progressively worse. He run out - and of course he is not going to denounce this high-profile PI

Permalink to Comment

9. John Spevacek on December 4, 2007 8:38 AM writes...

Speaking of Crick and Watson, remember that Pauling published the DNA structure first - only it was wrong as he forgot about keto-enol rearrangements. That cost him a third Nobel Prize, but it still didn't make him gun shy.

Permalink to Comment

10. Wavefunction on December 4, 2007 12:10 PM writes...

Pauling forgot something even simpler; that phosphate groups wpn't be protonated at pH 7.
Watson has a great video at TED on the story. He calls Pauling's paper "crap". It's endearing.

Permalink to Comment

11. srp on December 4, 2007 6:55 PM writes...

The best fictional description I know of the scientific tension Derek describes is the novel Timescape (Greg Benford), although Intuition (Allegra Goodman) is also very good.

For a real-life description of this tension from the inside (where the final answer has not yet been conceded by all), check out Louis Frank's The Big Splash and then follow the ensuing developments at his website and around the Internet. To a layman, Frank is probably wrong (although I'd like him to be right), but he has not been wrong in stick to his guns--most of the criticism he faced was misinformed and prejudiced, and we are going to end up learning things about the upper atmosphere previously unsuspected.

Permalink to Comment

12. jalopy on December 4, 2007 11:33 PM writes...


Take a look at the Watson-Crick paper:

Pauling postulated a triplex, with no base pairing, with the anions at the center.

Permalink to Comment


Remember Me?


Email this entry to:

Your email address:

Message (optional):

The Last Post
The GSK Layoffs Continue, By Proxy
The Move is Nigh
Another Alzheimer's IPO
Cutbacks at C&E News
Sanofi Pays to Get Back Into Oncology
An Irresponsible Statement About Curing Cancer
Oliver Sacks on Turning Back to Chemistry