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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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« The Dark Side | The Scientific Literature | Things I Won't Work With »

July 11, 2014

My Imaginary Friends Would Be Glad to Serve as Referees

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Posted by Derek

Here's the biggest fake-peer-review operation I've heard of yet. Retraction Watch, which does not seem to be in any danger of running out of material, reports that a researcher in Taiwan decided to not leave the review process at the Journal of Vibration and Control up to chance. He set up scores of fake identities in their online submission database, with as many as 130 fabricated e-mail addresses, and guess who got to review his manuscripts?

The journal has retracted sixty papers going back to 2010, and I'd like to know if that's the record. I haven't heard of anything better - well, worse, you know what I mean. The professor involved has been removed from his position in Taiwan, as well he might, and the editor of the journal has resigned. As well he might, too - that editor is not implicated in the publication scam, as far as I can tell, but what exactly were his editorial duties? Dozens of papers come pouring in every year from some obscure university in Taiwan, all of them with overlapping lead or co-authors, and you don't even so much as look up from your desk? Hardly a month goes by without another bulletin from the wildly productive engineers at Pingtung U, sometimes four or five of the damn things at once, and you think you're doing your job? And nobody else who reads this journal - assuming anyone ever does - wonders what's going on, either?

If the professor involved was really getting something out of this (tenure, promotion, grant money, what have you), then the people who awarded those to him were idiots, too. In fact, that's how I'd sum up the whole affair: a fool, faking papers for a bunch of incompetents, and rewarded for it by idiots. What a crew. You really cannot underestimate the low end of the scientific publishing industry, nor its customers.

Comments (14) + TrackBacks (0) | Category: The Scientific Literature

July 7, 2014

That Retracted Stressed Stem Cell Work

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Posted by Derek

This article from David Cyranoski at Nature News is an excellent behind-the-scenes look at all the problems with the "STAP" stem-cell work, now retracted and apparently without any foundation at all. There were indeed problems with all of it from the start, and one of the key questions is whether these things could have been caught:

The committee was more vexed by instances of manipulated and duplicated images in the STAP papers. Obokata had spliced together gel lanes from different experiments to appear as one. And she had used an image of cells in a teratoma — a tumorous growth that includes multiple types of tissue — that had also appeared in her PhD dissertation. The captions indicated that the image was being used to represent different types of cell in each case. The committee judged that in both instances, although she might not have intended to mislead, she should have been “aware of the danger” and therefore found her guilty of misconduct. Obokata claimed that they were mistakes and has denied wrongdoing. . .

. . .Philip Campbell, editor-in-chief of Nature, says: “We have concluded that we and the referees could not have detected the problems that fatally undermined the papers.” But scientists and publishers say that catching even the less egregious mistakes raises alarm bells that, on further investigation, can lead to more serious problems being discovered.

Many say that the tests should be carried out on all papers. Christopher says that it takes about one-third of her working week to check all accepted manuscripts for the four journals published by EMBO Press. At Nature and the Nature research journals, papers are subjected to random spot-checking of images during the production process. Alice Henchley, a spokeswoman for Nature, says that the journal does not check the images in all papers because of limitations in resources, and that the STAP papers were not checked. But she adds that as one outcome of this episode, editors “have decided to increase the number of checks that we undertake on Nature’s papers. The exact number or proportion of papers that will be checked is still being decided.”

A complication is that some of the common image manipulations (splicing gel lanes, for example) are done in honest attempts to present the data more clearly, or just to save space in a figure. My guess is that admitting this up front, along with submitting copies of the original figures to the editors (and for inclusion in the Supplementary Material?) would help to clear that up. The article raises another good point - that editors are actually worried about confronting every example of image manipulation that they see, for fear of raising the competence of the average image manipulator. There's an evolutionary-arms-race aspect to all this that can't be ignored.

In the end, one gets the impression that Nature's editorial staff (a separate organization from the News people) very much regret ever having accepted the work, as well they might. Opinion seems divided about whether they could have caught the problems with the papers themselves - this was one of those cases where a number of reputable co-authors, at reputable institutions, all screwed up simultaneously when it came to cross-checking and verification. What remains is a portrait of how eager people can be to send in groundbreaking results for publication, and how eager editors can be to publish it. Neither of those are going to change any time soon, are they?

Update: from the comments, see also this timeline of events for a look at the whole story.

Comments (14) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

July 1, 2014

Scientific Journals: Who Pays What?

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Posted by Derek

If you've ever wondered about those deals where the large scientific publishers offer bundled discounts to libraries, wonder no more. There's a paper in PNAS whose authors used Freedom of Information Act requests to track down what various university libraries really paid for these deals, and it reveals that everyone paid something different.

Here's a comment in Nature on the study, which they can do with a straight face, since the Nature Publishing Group wasn't included in the study (although the authors seem to think, in retrospect, that they should have done so). These deals are always secret - the publishers make it a requirement not to disclose the terms. And that, as you might easily expect, benefits the publishers, since the library systems don't have a good way of finding out what the market price might be. The PNAS study reveals some odd discrepancies, with some universities getting noticeably better (and worse) deals than others. Wisconsin and Texas bargained hard, it appears, while BYU and Georgia could have done better for themselves.

As the article details, publishers used site licenses to take care of arbitrage opportunities, and the "Big Deal" bundles were used as incentives for the library systems and as tools for the publishers to figure out how much each customer might be willing to pay (using the print-based subscription data as a starting point). As you might have guessed, Elsevier comes out at the top of the pricing list when you just look at the dollar figures. On a cost-per-citation basis, though, they don't look so bad - in fact, they're the most cost-effective of the big publishers by that metric. (Sage and Taylor & Francis both look pretty bad in that table). For reference, the ACS bundle looks pretty decent, and it turns out that nearly 60% of the libraries that deal with the ACS choose the whole package (a high percentage compared to many other publishers). Interestingly, it turns out that some very wealthy schools (Harvard, MIT, Caltech) still don't take the full Elsevier bundle.

And the bundles are, naturally, a mixed bag. It's their whole purpose to be a mixed bag:

It would cost about $3.1 million at 2009 á la carte prices to buy all of the journals in Elsevier’s bundle, the “Freedom Collection.” The average research 1 university paid roughly $1.2 million, or 40% of the summed title-by- title prices, for access to the Freedom Collection. However, this bundle price is by no means equivalent to a 60% discount from journal-by-journal pricing. The Freedom Collection includes about 2,200 journals, many of which are expensive but rarely cited. The least cost-effective 1,100 journals contained in this collection supply fewer than 5% of the citations, but their prices add to more than 25% of the total of á la carte prices. A library that spent $1.2 million on Elsevier journals at listed catalog prices, selecting journals for cost-effectiveness, could obtain access to journals providing 79% of the citations to journals found in the Freedom Collection. Thus, for the average research 1 institution, the citation-scaled discount obtained from the Freedom Collection is about 21%.

Elsevier, though, drops its prices for smaller universities more quickly than many other publishers, and for Master's-level schools it's actually a better deal than many of the nonprofit publishers. We wouldn't know this, though, if these authors hadn't dug up all the info from FOIA requests, and I guess that's the take-home here: scientific publishing is a very opaque, inefficient market. And the publishers like it that way.

Comments (6) + TrackBacks (0) | Category: The Scientific Literature

June 27, 2014

Varieties of Scientific Deception

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Posted by Derek

Some may remember a paper from 2011 on the "reverse click" reaction, an interesting one where triazoles were pulled apart with mechanical force. This was an interesting system, because we really know surprisingly little, down on the molecular level, about what happens when bonds are physically stressed in this way. What do molecular orbitals look like when you grab both ends of the molecule and tug hard? Which bonds break first, and why? Do you get the reverse of the forward reaction, or do different mechanisms kick in (free radical intermediates, etc.)? (Note that the principle of microscopic reversibility doesn't necessarily apply when the conditions change like this).

Unfortunately, there seems to be trouble associated with this example. Science has an editorial "expression of concern" on the paper now, and it appears that much of it is not, in fact, reproducible (see this report in C&E News).

The paper was from the Bielawski lab at UT-Austin, and Bielawski is reported as saying that a former group member has confessed to manipulating data. But he also says that the conclusions of the paper are unchanged, which is interesting. My guess is that the "unclick" does happen, then, but nowhere as smoothly as reported. Someone may have sweetened things to make it all look better. At any rate, a correction is coming soon in Science, so we should get more information at that point.

This reminds me of the scheme I use to rate political and economic corruption. Stage I is paying someone off to do something they wouldn't normally do (or aren't authorized to do) for you. This happens everywhere, to some extent. Stage II is when you're bribing them just to do the job they're supposed to be doing in the first place. Many countries suffer from institutional cases of this, and it's supremely annoying, and a terrible drag on the economy. And Stage III, the worst, is when you're paying them not to harm you - a protection racket with the force of law behind it. Cynics may adduce examples from the US, but I'm thinking about countries (Russia, among others) where the problem is far worse.

Similar levels apply to fakery in the scientific literature. Here's how I break it down:

Stage I is what we may have in this case: actual conclusions and effects are made to look cleaner and better than reality. Zapping solvent peaks in the NMR is a perfect small-scale example of this - for organic chemists, solvent peaks are sometimes the training wheels of fakery. The problem is, once you're used to altering data, at what point do you find it convenient to stop? It's far better not to take that first step into matters-of-degree territory.

Stage II is unfortunately common as well, and there's a nice slippery path from Stage I that can land you here. This is when you're convinced that your results are correct, but you're having such a hard time getting things to work that you decide to "fake it until you make it". That's a stupendously bad idea, of course, because a lot of great results were never real in the first place, which leaves you hung out to dry, and even the ones that can be finally filled in don't have to do so in the way that you were faking them to happen. So now a real result is tainted by deception, which will call the whole thing into doubt when the inconsistencies become clear. And faked results are faked results, even if they're done in what you might think is a good cause. Many big cases of scientific fraud have started off this way, with someone just trying to fill in that one little gap, just for now.

Stage III, the bottom, is when something is faked from beginning to end. There was no question of it even working in the first place - it never did. Someone's just trying to get a paper, or a degree, or tenure, or fame, or something, and they're taking the shortcut. I think that there are two main classes of fakery in this category. In one group (IIIa?), you have people whipping up bogus results in low-profile cases where no one may notice for years, if ever, because no one cares. And you have IIIb, the famous high-profile cases (see Jan-Hendrik Schön, among too many others) where impressive, splashy, look-at-that stuff turns out to have been totally faked as well. Those cases are a study in human psychology. If you report a big result in superconductors, stem cells, cancer therapy or any other field where a lot of smart, competent people are paying very close attention, you will be found out at some point. How can you not be? We're in Bernie Madoff territory here, where someone comes into work every day of every week knowing that their whole reputation is a spray-painted scrim of deception that could have a hole punched through it any minute. How people can possibly live this way I don't really know, but people do. The self-confidence displayed by this sort of personality is a wonder of nature, in its way. IIIa cases are initiated by the desperate, stupid, and/or venal. IIIb cases, though, are brought on by people born to their task.

Update: as pointed out by several good comments, there are plenty of not-quite-fraud sins that neighbor these. Those are worth a separate post, partly because they're even more common than straight-up fraud.

Comments (53) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

June 6, 2014

The Robustness Test: Why Don't We Just Require It?

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Posted by Derek

There's a follow-up paper to that one on the robustness of new synthetic methods that I blogged about here. This one's in Nature Protocols, so it's a detailed look at just how you'd go about their procedure for shaking down a new reaction.

The reaction they've chosen is a rhodium-catalyzed indole formation (phenylhydrazine plus substituted alkyne), which is a good test bed for the real world (heterocycles, metal-catalyzed mechanism). The authors suggest a matrix of additives and reaction conditions, analyzed by GC, as in their original paper, to profile what can be tolerated and what can't. It's good to have the detailed reference out there, and I hope it gives referees and journal editors something to point at.

But will they? I can imagine a world where new reactions all have a "standard additives" grid somewhere in the paper, showing how the yields change. You could even color-code them (the old stoplight slide scheme, red/yellow/green, would be fine), and then we'd all have a way to compare synthetic methods immediately. Aldrich and others could sell the pre-assembled kit of the standard compounds to use. This would also point out reactions where more useful work could be done, since it would be immediately obvious that the new Whatsit Cyclization fails in the presence of tertiary amines, etc. Too often now you have to work that our for yourself, usually by seeing what the authors left out.

So why don't we all do this? It's more work, that's for sure, but not an incredible amount more work. If the major synthetic chemistry journals starting asking for it, that would be that. It would also make the publication landscape even more clear, because the titels that don't ask for an extra few days to be spent on the reaction conditions would be hard-pressed to make a case that they weren't just venues for hackwork (or for people with something to hide). I'd rather read about reactions with a clear statement of what they'll work on and what they won't - wouldn't you?

Comments (13) + TrackBacks (0) | Category: Chemical News | The Scientific Literature

June 2, 2014

No More Acid Stem Cells

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Posted by Derek

In case you hadn't seen it, the "acid-washed stem cells" business has gone as far into the dumper as it can possibly go. It now appears that the whole thing was a fraud, from start to finish - if that's not the case, I'll be quite surprised, anyway. The most senior author of the (now retracted) second paper, Teruhiko Wakayama, has said that he doesn't believe its results:

The trigger, he told Bioscience, was his discovery—which he reported to Riken a few weeks ago--that two key photos in the second paper were wrong. Obokata, lead author on both papers, had in April been found by Riken guilty of misconduct on the first paper: the falsification of a gel electrophoresis image proving her starting cells were mature cells, and the fabrication of images proving resulting STAP stem cells could form the three major tissue types of the body.

But Riken had not yet announced serious problems with the second paper.

Last week, however, there was a flurry of activity in the Japanese press, as papers reported that two photos—supposed to show placenta made from STAP cells, next to placenta made from embryonic stem (ES) cells—were actually photos of the same mouse placenta.

As with so many cases before this one, we now move on (as one of Doris Lessing's characters once put it) to having interesting thoughts about the psychology of lying. How and why someone does this sort of thing is, I'm relieved to say, apparently beyond me. The only way I can remotely see it is if these results were something that a person thought were really correct, but just needed a bit more work, which would be filled in in time to salvage everything. But how many times have people thought that? And how does it always seem to work out? I'm back to being baffled. The stem cell field has attracted its share of mentally unstable people, and more.

Comments (12) + TrackBacks (0) | Category: Biological News | The Dark Side | The Scientific Literature

May 28, 2014

The Science Chemogenomics Paper is Revised

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Posted by Derek

The Science paper on chemogenomic signatures that I went on about at great length has been revised. Figure 2, which drove me and every other chemist who saw it up the wall, has been completely reworked:

To improve clarity, the authors revised Fig. 2 by (i) illustrating the substitution sites of fragments; (ii) labeling fragments numerically for reference to supplementary materials containing details about their derivation; and (iii) representing the dominant tautomers of signature compounds. The authors also discovered an error in their fragment generation software that, when corrected, resulted in slightly fewer enriched fragments being identified. In the revised Fig. 2, they removed redundant substructures and, where applicable, illustrated larger substructures containing the enriched fragment common among signature compounds.

Looking it over in the revised version, it is indeed much improved. The chemical structures now look like chemical structures, and some of the more offensive "pharmacophores" (like tetrahydrofuran) have now disappeared. Several figures and tables have been added to the supplementary material to highlight where these fragments are in the active compounds (Figure S25, an especially large addition), and to cross-index things more thoroughly.

So the most teeth-gritting parts of the paper have been reworked, and that's a good thing. I definitely appreciate the work that the authors have put into making the work more accurate and interpretable, although these things really should have been caught earlier in the process.

Looking over the new Figure S25, though, you can still see what I think are the underlying problems with the entire study. That's the one where "Fragments that are significantly enriched in specific sets of signature compounds (FDR ≤ 0.1 and signature compounds fraction ≥ 0.2) are highlighted in blue within the relevant signature compounds. . .". It's a good idea to put something like that in there, but the annotations are a bit odd. For example, the compounds flagged as "6_cell wall" have their common pyridines highlighted, even though there's a common heterocyclic core that that all but one those pyridines are attached to (it only varies by alkyl substitutents). That single outlier compound seems to be the reason that the whole heterocycle isn't colored in - but there are plenty of other monosubstituted pyridines on the list that have completely different signatures, so it's not like "monosubstituted pyridine" carries much weight. Meanwhile, the next set ("7_cell wall") has more of the exact same series of heterocycles, but in this case, it's just the core heterocycle that's shaded in. That seems to be because one of them is a 2-substituted isomer, while the others are all 3-substituted, so the software just ignores them in favor of coloring in the central ring.

The same thing happens with "8_ubiquinone biosynthesis and proteosome". What gets shaded in is an adamantane ring, even though every single one of the compounds is also a Schiff base imine (which is a lot more likely to be doing something than the adamantane). But that functional group gets no recognition from the software, because some of the aryl substitution patterns are different. One could just as easily have colored in the imine, though, which is what happens with the next category ("9_ubiquinone biosynthesis and proteosome"), where many of the same compounds show up again.

I won't go into more detail; the whole thing is like this. Just one more example: "12_iron homeostasis" features more monosubstituted pyridines being highlighted as the active fragment. But look at the list: there's are 3-aminopyridine pieces, 4-aminomethylpyridines, 3-carboxylpyridines, all of them substituted with all kinds of stuff. The only common thread, according to the annotation software, is "pyridine", but those are, believe me, all sorts of different pyridines. (And as the above example shows, it's not like pyridines form some sort of unique category in this data set, anyway).

So although the most eye-rolling features of this work have been cleaned up, the underlying medicinal chemistry is still pretty bizarre, at least to anyone who knows any medicinal chemistry. I hate to be this way, but I still don't see anyone getting an awful lot of use out of this.

Comments (6) + TrackBacks (0) | Category: Biological News | Chemical Biology | Chemical News | The Scientific Literature

May 14, 2014

A Unique Correction

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Posted by Derek

A reader sent this correction notice along this morning, and I agree: I've never seen anything quite like it. Here's how it goes (emphasis added):

According to the recent reconsideration and re-evaluation of every author’s contribution of this work, all of authors have reached the final conclusion that we should rearrange the order of the authors and remove Dr. Usui from the author list as observed below.

(List of authors follows)

All of authors have already approved this correction. Dr. Usui, our supervisor, also authorized and approved it.

There's surely a story here, but I'm sure that I don't quite know what it is, either!

Comments (31) + TrackBacks (0) | Category: The Scientific Literature

April 22, 2014

J. Appl. Drivel or Gibberish Lett.? Choices, Choices.

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Posted by Derek

People keep hoaxing the predatory "scholarly" publishers out there, and the publishers keep falling for whatever drivel is slung at them. Here's the latest example from a reporter at the Ottawa Citizen, Tom Spears. He molded a pile of steaming gibberish into the rough shape of a manuscript, and that was more than enough:

I have just written the world’s worst science research paper: More than incompetent, it’s a mess of plagiarism and meaningless garble. . .

. . .I copied and pasted one phrase [in the title] from a geology paper online, and the rest from a medical one, on hematology.

I wrote the whole paper that way, copying and pasting from soil, then blood, then soil again, and so on. There are a couple of graphs from a paper about Mars. They had squiggly lines and looked cool, so I threw them in.

Footnotes came largely from a paper on wine chemistry. The finished product is completely meaningless.

The university where I claim to work doesn’t exist. Nor do the Nepean Desert or my co-author. Software that catches plagiarism identified 67 per cent of my paper as stolen (and that’s missing some). And geology and blood work don’t mix, even with my invention of seismic platelets.

And you guessed it - the acceptances came rolling in, and pretty damned quickly, too. Peer-reviewed, refereed, and edited within 24 hours - where are you going to find an honest journal with service like that? 16 of the 18 bottom-feeding "journals" accepted it, and one of the rejections suggested that it just needed a bit of tweaking to be accepted. And one of the publishers has asked Spears to serve on an editorial advisory board, so he's clearly got what it takes.

Of course, as yesterday's post shows, even a peer-reviewed journal with a recognizable name can publish gibberish. But I assume that Drug Discovery Today and Elsevier didn't charge the author $1000 to do it. On the other hand, they might have taken more than 18 hours to review the manuscript. Or not.

Comments (14) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature | The Scientific Literature

J. Appl. Drivel or Gibberish Lett.? Choices, Choices.

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Posted by Derek

People keep hoaxing the predatory "scholarly" publishers out there, and the publishers keep falling for whatever drivel is slung at them. Here's the latest example from a reporter at the Ottawa Citizen, Tom Spears. He molded a pile of steaming gibberish into the rough shape of a manuscript, and that was more than enough:

I have just written the world’s worst science research paper: More than incompetent, it’s a mess of plagiarism and meaningless garble. . .

. . .I copied and pasted one phrase [in the title] from a geology paper online, and the rest from a medical one, on hematology.

I wrote the whole paper that way, copying and pasting from soil, then blood, then soil again, and so on. There are a couple of graphs from a paper about Mars. They had squiggly lines and looked cool, so I threw them in.

Footnotes came largely from a paper on wine chemistry. The finished product is completely meaningless.

The university where I claim to work doesn’t exist. Nor do the Nepean Desert or my co-author. Software that catches plagiarism identified 67 per cent of my paper as stolen (and that’s missing some). And geology and blood work don’t mix, even with my invention of seismic platelets.

And you guessed it - the acceptances came rolling in, and pretty damned quickly, too. Peer-reviewed, refereed, and edited within 24 hours - where are you going to find an honest journal with service like that? 16 of the 18 bottom-feeding "journals" accepted it, and one of the rejections suggested that it just needed a bit of tweaking to be accepted. And one of the publishers has asked Spears to serve on an editorial advisory board, so he's clearly got what it takes.

Of course, as yesterday's post shows, even a peer-reviewed journal with a recognizable name can publish gibberish. But I assume that Drug Discovery Today and Elsevier didn't charge the author $1000 to do it. On the other hand, they might have taken more than 18 hours to review the manuscript. Or not.

Comments (14) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature | The Scientific Literature

April 21, 2014

Molecular Printing of Drug Molecules. Say What?

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Posted by Derek

Update: the author of this paper has appeared in the comments here (and elsewhere) saying that he's withdrawing the paper. These are apparently reviewer's comments on it, although I have no way of verifying that. Many of them don't sound like the comments I might have expected. There's more here as well.

Here we have one of the oddest papers to appear in Drug Discovery Today, which is saying something. The journal has always ranged wider than some of the others in this space, but this is the furthest afield I've seen to date. The title is "DrugPrinter: print any drug instantly", and I don't think I can do better than letting the abstract speak for itself:

In drug discovery, de novo potent leads need to be synthesized for bioassay experiments in a very short time. Here, a protocol using DrugPrinter to print out any compound in just one step is proposed. The de novo compound could be designed by cloud computing big data. The computing systems could then search the optimal synthesis condition for each bond–bond interaction from databases. The compound would then be fabricated by many tiny reactors in one step. This type of fast, precise, without byproduct, reagent-sparing, environmentally friendly, small-volume, large-variety, nanofabrication technique will totally subvert the current view on the manufactured object and lead to a huge revolution in pharmaceutical companies in the very near future.

Now, you may well read that and ask yourself "What is this DrugPrinter, and how can I get one?" But note how it's all written in the conditional - lots of woulds and coulds, which should more properly be mights and maybes. Or maybe nots. The whole thing is a fantasy of atomic-level nanotechnology, which I, too, hope may be possible at some point. But to read about the DrugPrinter, you'd think that someone's ready to start prototyping. But no one is, believe me. This paper "tells" you all the "steps" that you would need to "print" a molecule, but it leaves out all the details and all the hard parts:

Thus, if DrugPrinter can one day become a reality it will be a huge step forward in drug discovery. The operator needs only to sit down in front of a computer and draw the structure of compound, which is then inputted into the computer, and the system will automatically search by cloud computing for suitable reaction conditions between bond and bond. . .

That actually captures the tone of this paper pretty well - it exists on a slightly different plane of reality, and what it's doing in Drug Discovery Today is a real mystery, because there's not much "Today" in it, for one thing. But there's something else about it, too - try this part out and see what you think:

Thus, this novel protocol only needs one step instead of the five-to-ten steps of the current synthesis process. In actual fact, it is even better than click chemistry, with lower costs and with better precision of synthesis. A world-leading group led by Lee Cronin has made advances with the technology named ‘Chemputer’. However, it is different to our concept. We specifically address the detail of how to pick up each atom and react. We also disagree that it is possible for anyone to simply download the software (app) from the internet and use it to print one's own drug. It is not feasible and should be illegal in the future.

Some of this, naturally, can be explained by non-native English usage, although the editorial staff at DDT really should have cleaned that up a bit. But there's an underlying strain of grandiose oddness about the whole manuscript. It makes for an interesting reading experience, for sure.

The paper proposes a molding process to fit the shape of the desired target molecule, which is not prima facie a crazy idea at all (templated synthesis). But remember, we're down on the atomic scale here. The only thing to build the mold out of is more atoms, at the same scale as the material filling the mold, and that's a lot harder than any macroscale molding process that you can make analogies to. The MIP (molecularly imprinted polymer) idea is the closest real-world attempt at this sort of thing, but it's been around for quite a while now without providing a quick route into molecular assembly. There is no quick route into molecular assembly, and you’re certainly not going to get one from stuff like this:

Benzene has six carbon atoms joined in a ring, with one hydrogen atom attached to each carbon atom. It can be divided into six reactors for three atoms: C, H and C (Fig. 3). After inputting the chemical structure of benzene, the system will search for the best synthesis condition for each bond. The best optimal condition will be elucidated by computer and controlled by a machine with optical tweezers to pick up the reactant and the atoms of carbon and hydrogen. The carbon atom will be picked up by optical tweezers in the right position in these tiny reactors (just like a color laser printer). DrugPrinter technology will work just like a color laser printer but instead of a four-color (red, yellow, blue and black) printer toner cartridge there will be various atoms.

Right. The computer will search for the best reaction conditions for building up benzene by individual carbon atoms? There are no best conditions for that. You can make benzene from acetylene, if you’re so minded, but you need metal catalysts (Reppe chemistry). And how are these “conditions” to work inside some sort of benzene-shaped mold? How are the intermediates (propene? butadiene?) to be held in there while another carbon atom comes in? Making benzene in this manner would be Nobel-level stuff, and this paper’s just getting warmed up:

. . .The chamber for the storage of elements is divided into three parts based on the character of each atom according to the periodic table of elements. Roughly, there are three categories: nonmetals, metals and transition metals. Of course, most drugs are organic compounds, thus it is reasonable to expect that carbon (C), hydrogen (H) and oxygen (O) will be the major consumables (just as the black toner cartridge always runs out before the other three colors in a printer). . .

I don’t know what the author’s background is, but honestly, you get the impression that it doesn’t include much organic chemistry. The whole paper is written about a world where you take individual atoms from these reservoirs and fly them down small channels “with lasers or plasma” to be caught by optical tweezers and put into the right position. Apparently, things are just going to snap together like so many molecular model pieces once that happens. Reaction mechanisms, thermodynamics, reactivity and selectivity make no appearance at all that I can see. What does make an appearance is stuff like this:

Big data is applied suddenly in any field. For DrugPrinter, we allow the user to upload their desired compound by a webserver. A cloud computing system and fast dealing and optimal of the chemical reaction must be searched immediately. All the bond–bond reactions will be collected in an intelligent system by cloud computing. Because we built a world-first intelligent cloud computing drug screening system called iScreen (http://iscreen.cmu.edu.tw/) and an integrated webserver (http://ismart.cmu.edu.tw/) including the world’s largest traditional Chinese medicine (TCM) database (http://tcm.cmu.edu.tw/), this has enabled our technology. . .

I’m not trying to be unkind here, but some of this reads rather like the spam comments that pile up on this blog and others. “The buzzword will be made by high-tech buzzword by use of buzzword systems”. None of this is real, and as speculation it’s not too exciting, either. Eric Drexler is far more interesting reading – you can certainly find many things to argue about with him (as Richard Smalley famously did), but he’s thought about these problems in a useful way, as have many others. Drexler’s name, by the way, appears nowhere in this current paper, although the whole thing reads like a smudged tenth-generation photocopy of his work from the 1980s.

And that brings up an editorial question: who reviewed this? How did the staff at Drug Discovery Today find this worth publishing in its current form? I have no problem with them running papers about speculative nanotech chemical synthesis, I should add. I like that stuff; I like reading about it. But I don’t like reading hand-waving hoo-hah illustrated with videos of traditional egg-cake molding machines (I kid you not). As published, I found this paper to be an irritating, head-shaking, eye-rolling waste of time, and I would gladly have said so in a referee report. I see that Chemjobber is baffled as well. Who wouldn’t be?

Comments (46) | Category: Chemical News | The Scientific Literature

April 16, 2014

Professor Fukuyama's Solvent Peaks

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Posted by Derek

See Arr Oh expresses some doubts about all the NMR spectral corrections we've been seeing lately. He's specifically referring to Bethany Halford's interview piece, and he has this to say after reading it:

If your group focuses on "clean up your spectra" more than "purify your compounds better," that's a communications issue. If a professor with a large group sees nothing but perfect spectra all day, two thoughts should crop up:

1. "I must have the smartest, most efficient students in the world," or...
2. "Something's fishy here."

Perfect-looking data should always be a cause for concern in any experiment. My guess is that Prof. Fukuyama was closer to Option One, though, possibly in the variant of "My group has such high standards!" But high standards or not, a series of perfect, flat, NMR spectra with no solvent and no impurities is rather hard to achieve in total synthesis, considering the quantities that are being used. Load up the tube with 50mg of material and you can make a lot of stuff look good, but you don't have fifty mgs at step thirty-four, do you? I remember putting everything I had into one NMR tube (or worse, one polarimeter tube) in my own total synthesis days, and I carried the thing down to the machine like it was a bag of gold.

But there's no doubt that in a big group, there will be people who try to slip things past the boss. I've seen it myself; I'm sure that a lot of you have. And if you're giving the boss exactly what the boss wants to see - perfection - then it's going to be a lot easier. These spectral problems look like a collaborative effort to me - expectations from above, willingness from below. And there are a lot of other groups that have done (and, I feel sure, still do) the same thing. Zapping the solvent peaks in the NMR is the least of it, in some cases.

Update: added a direct link to the Fukuyama/Yokoshima interview.

Comments (19) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

April 14, 2014

More on the Science Chemogenomic Signatures Paper

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Posted by Derek

phenol%20equil.png
This will be a long one. I'm going to take another look at the Science paper that stirred up so much comment here on Friday. In that post, my first objection (but certainly not my only one) was the chemical structures shown in the paper's Figure 2. A number of them are basically impossible, and I just could not imagine how this got through any sort of refereeing process. There is, for example, a cyclohexadien-one structure, shown at left, and that one just doesn't exist as such - it's phenol, and those equilibrium arrows, though very imbalanced, are still not drawn to scale.
subst%20align.png
Well, that problem is solved by those structures being intended as fragments, substructures of other molecules. But I'm still positive that no organic chemist was involved in putting that figure together, or in reviewing it, because the reason that I was confused (and many other chemists were as well) is that no one who knows organic chemistry draws substructures like this. What you want to do is put dashed bonds in there, or R groups, as shown. That does two things: it shows that you're talking about a whole class of compounds, not just the structure shown, and it also shows where things are substituted. Now, on that cyclohexadienone, there's not much doubt where it's substituted, once you realize that someone actually intended it to be a fragment. It can't exist unless that carbon is tied up, either with two R groups (as shown), or with an exo-alkene, in which case you have a class of compounds called quinone methides. We'll return to those in a bit, but first, another word about substructures and R groups.
THF%20R%20group.png
Figure 2 also has many structures in it where the fragment structure, as drawn, is a perfectly reasonable molecule (unlike the example above). Tetrahydrofuran and imidazole appear, and there's certainly nothing wrong with either of those. But if you're going to refer to those as common fragments, leading to common effects, you have to specify where they're substituted, because that can make a world of difference. If you still want to say that they can be substituted at different points, then you can draw a THF, for example, with a "floating" R group as shown at left. That's OK, and anyone who knows organic chemistry will understand what you mean by it. If you just draw THF, though, then an organic chemist will understand that to mean just plain old THF, and thus the misunderstanding.

If the problems with this paper ended at the level of structure drawing, which many people will no doubt see as just a minor aesthetic point, then I'd be apologizing right now. Update: although it is irritating. On Twitter, I just saw that someone spotted "dihydrophyranone" on this figure, which someone figured was close enough to "dihydropyranone", I guess, and anyway, it's just chemistry. But they don't. It struck me when I first saw this work that sloppiness in organic chemistry might be symptomatic of deeper trouble, and I think that's the case. The problems just keep on coming. Let's start with those THF and imidazole rings. They're in Figure 2 because they're supposed to be substructures that lead to some consistent pathway activity in the paper's huge (and impressive) yeast screening effort. But what we're talking about is a pharmacophore, to use a term from medicinal chemistry, and just "imidazole" by itself is too small a structure, from a library of 3200 compounds, to be a likely pharmacophore. Particularly when you're not even specifying where it's substituted and how. There are all kinds of imidazole out there, and they do all kinds of things.
four%20imidazoles.png
So just how many imidazoles are in the library, and how many caused this particular signature? I think I've found them all. Shown at left are the four imidazoles (and there are only four) that exhibit the activity shown in Figure 2 (ergosterol depletion / effects on membrane). Note that all four of them are known antifungals - which makes sense, given that the compounds were chosen for the their ability to inhibit the growth of yeast, and topical antifungals will indeed do that for you. And that phenotype is exactly what you'd expect from miconazole, et al., because that's their known mechanism of action: they mess up the synthesis of ergosterol, which is an essential part of the fungal cell membrane. It would be quite worrisome if these compounds didn't show up under that heading. (Note that miconazole is on the list twice).
other%20imidazoles.png
But note that there are nine other imidazoles that don't have that same response signature at all - and I didn't even count the benzimidazoles, and there are many, although from that structure in Figure 2, who's to say that they shouldn't be included? What I'm saying here is that imidazole by itself is not enough. A majority of the imidazoles in this screen actually don't get binned this way. You shouldn't look at a compound's structure, see that it has an imidazole, and then decide by looking at Figure 2 that it's therefore probably going to deplete ergosterol and lead to membrane effects. (Keep in mind that those membrane effects probably aren't going to show up in mammalian cells, anyway, since we don't use ergosterol that way).

There are other imidazole-containing antifungals on the list that are not marked down for "ergosterol depletion / effects on membrane". Ketonconazole is SGTC_217 and 1066, and one of those runs gets this designation, while the other one gets signature 118. Both bifonazole and sertaconazole also inhibit the production of ergosterol - although, to be fair, bifonazole does it by a different mechanism. It gets annotated as Response Signature 19, one of the minor ones, while sertaconazole gets marked down for "plasma membrane distress". That's OK, though, because it's known to have a direct effect on fungal membranes separate from its ergosterol-depleting one, so it's believable that it ends up in a different category. But there are plenty of other antifungals on this list, some containing imidazoles and some containing triazoles, whose mechanism of action is also known to be ergosterol depletion. Fluconazole, for example, is SGTC_227, 1787 and 1788, and that's how it works. But its signature is listed as "Iron homeostasis" once and "azole and statin" twice. Itraconzole is SGTC_1076, and it's also annotated as Response Signature 19. Voriconazole is SGTC_1084, and it's down as "azole and statin". Climbazole is SGTC_2777, and it's marked as "iron homeostasis" as well. This scattering of known drugs between different categories is possibly and indicator of this screen's ability to differentiate them, or possibly an indicator of its inherent limitations.

Now we get to another big problem, the imidazolium at the bottom of Figure 2. It is, as I said on Friday, completely nuts to assign a protonated imidazole to a different category than a nonprotonated one. Note that several of the imidazole-containing compounds mentioned above are already protonated salts - they, in fact, fit the imidazolium structure drawn, rather than the imidazole one that they're assigned to. This mistake alone makes Figure 2 very problematic indeed. If the paper was, in fact, talking about protonated imidazoles (which, again, is what the authors have drawn) it would be enough to immediately call into question the whole thing, because a protonated imidazole is the same as a regular imidazole when you put it into a buffered system. In fact, if you go through the list, you find that what they're actually talking about are N-alkylimidazoliums, so the structure at the bottom of FIgure 2 is wrong, and misleading. There are two compounds on the list with this signature, in case you were wondering, but the annotation may well be accurate, because some long-chain alkylimidazolium compounds (such as ionic liquid components) are already known to cause mitochondrial depolarization.

But there are several other alkylimidazolium compounds in the set (which is a bit odd, since they're not exactly drug-like). And they're not assigned to the mitochondrial distress phenotype, as Figure 2 would have you think. SGTC_1247, 179, 193, 1991, 327, and 547 all have this moeity, and they scatter between several other categories. Once again, a majority of compounds with the Figure 2 substructure don't actually map to the phenotype shown (while plenty of other structural types do). What use, exactly, is Figure 2 supposed to be?

Let's turn to some other structures in it. The impossible/implausible ones, as mentioned above, turn out to be that way because they're supposed to have substituents on them. But look around - adamantane is on there. To put it as kindly as possible, adamantane itself is not much of a pharmacophore, having nothing going for it but an odd size and shape for grease. Tetrahydrofuran (THF) is on there, too, and similar objections apply. When attempts have been made to rank the sorts of functional groups that are likely to interact with protein binding sites, ethers always come out poorly. THF by itself is not some sort of key structural unit; highlighting it as one here is, for a medicinal chemist, distinctly weird.

What's also weird is when I search for THF-containing compounds that show this activity signature, I can't find much. The only things with a THF ring in them seem to be SGTC_2563 (the complex natural product tomatine) and SGTC_3239, and neither one of them is marked with the signature shown. There are some imbedded THF rings as in the other structural fragments shown (the succinimide-derived Diels-Alder ones), but no other THFs - and as mentioned, it's truly unlikely that the ether is the key thing about these compounds, anyway. If anyone finds another THF compound annotated for tubulin folding, I'll correct this post immediately, but for now, I can't seem to track one down, even though Table S4 says that there are 65 of them. Again, what exactly is Figure 2 supposed to be telling anyone?

Now we come to some even larger concerns. The supplementary material for the paper says that 95% of the compounds on the list are "drug-like" and were filtered by the commercial suppliers to eliminate reactive compounds. They do caution that different people have different cutoffs for this sort of thing, and boy, do they ever. There are many, many compounds in this collection that I would not have bothered putting into a cell assay, for fear of hitting too many things and generating uninterpretable data. Quinone methides are a good example - as mentioned before, they're in this set. Rhodanines and similar scaffolds are well represented, and are well known to hit all over the place. Some of these things are tested at hundreds of micromolar.

I recognize that one aim of a study like this is to stress the cells by any means necessary and see what happens, but even with that in mind, I think fewer nasty compounds could have been used, and might have given cleaner data. The curves seen in the supplementary data are often, well, ugly. See the comments section from the Friday post on that, but I would be wary of interpreting many of them myself.
insolubles.png
There's another problem with these compounds, which might very well have also led to the nastiness of the assay curves. As mentioned on Friday, how can anyone expect many of these compounds to actually be soluble at the levels shown? I've shown a selection of them here; I could go on. I just don't see any way that these compounds can be realistically assayed at these levels. Visual inspection of the wells would surely show cloudy gunk all over the place. Again, how are such assays to be interpreted?

And one final point, although it's a big one. Compound purity. Anyone who's ever ordered three thousand compounds from commercial and public collections will know, will be absolutely certain that they will not all be what they say on the label. There will be many colors and consistencies, and LC/MS checks will show many peaks for some of these. There's no way around it; that's how it is when you buy compounds. I can find no evidence in the paper or its supplementary files that any compound purity assays were undertaken at any point. This is not just bad procedure; this is something that would have caused me to reject the paper all by itself had I refereed it. This is yet another sign that no one who's used to dealing with medicinal chemistry worked on this project. No one with any experience would just bung in three thousand compounds like this and report the results as if they're all real. The hits in an assay like this, by the way, are likely to be enriched in crap, making this more of an issue than ever.

Damn it, I hate to be so hard on so many people who did so much work. But wasn't there a chemist anywhere in the room at any point?

Comments (39) + TrackBacks (0) | Category: Biological News | Chemical Biology | Chemical News | The Scientific Literature

April 11, 2014

Biology Maybe Right, Chemistry Ridiculously Wrong

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Posted by Derek

Note: critique of this paper continues here, in another post.

A reader sent along a puzzled note about this paper that's out in Science. It's from a large multicenter team (at least nine departments across the US, Canada, and Europe), and it's an ambitious effort to profile 3250 small molecules in a broad chemogenomics screen in yeast. This set was selected from an earlier 50,000 compounds, since these realiably inhibited the growth of wild-type yeast. They're looking for what they call "chemogenomic fitness signatures", which are derived from screening first against 1100 heterozygous yeast strains, one gene deletion per, representing the yeast essential genome. Then there's a second round of screening against 4800 homozygous deletions strain of non-essential genes, to look for related pathways, compensation, and so on.

All in all, they identified 317 compounds that appear to perturb 121 genes, and many of these annotations are new. Overall, the responses tended to cluster in related groups, and the paper goes into detail about these signatures (and about the outliers, which are naturally interested for their own reasons). Broad pathway effects like mitrochondrial stress show up pretty clearly, for example. And unfortunately, that's all I'm going to say for now about the biology, because we need to talk about the chemistry in this paper. It isn't good.

enamine.png
phenol.pngAs my correspondent (a chemist himself) mentions, a close look at Figure 2 of the paper raises some real questions. Take a look at that cyclohexadiene enamine - can that really be drawn correctly, or isn't it just N-phenylbenzylamine? The problem is, that compound (drawn correctly) shows up elsewhere in Figure 2, hitting a completely different pathway. These two tautomers are not going to have different biological effects, partly because the first one would exist for about two molecular vibrations before it converted to the second. But how could both of them appear on the same figure?

And look at what they're calling "cyclohexa-2,4-dien-1-one". No such compound exists as such in the real world - we call it phenol, and we draw it as an aromatic ring with an OH coming from it. Thiazolidinedione is listed as "thiazolidine-2,4-quinone". Both of these would lead to red "X" marks on an undergraduate exam paper. It is clear that no chemist, not even someone who's been through second-year organic class, was involved in this work (or at the very least, involved in the preparation of Figure 2). Why not? Who reviewed this, anyway?

There are some unusual features from a med-chem standpoint as well. Is THF really targeting tubulin folding? Does adamantane really target ubiquinone biosynthesis? Fine, these are the cellular effects that they noted, I guess. But the weirdest thing on Figure 2's annotations is that imidazole is shown as having one profile, while protonated imidazole is shown as a completely different one. How is this possible? How could anyone who knows any chemistry look at that and not raise an eyebrow? Isn't this assay run in some sort of buffered medium? Don't yeast cells have any buffering capacity of their own? Salts of basic amine drugs are dosed all the time, and they are not considered - ever - as having totally different cellular effects. What a world it would be if that were true! Seeing this sort of thing makes a person wonder about the rest of the paper.

Nitro.pngMore subtle problems emerge when you go to the supplementary material and take a look at the list of compounds. It's a pretty mixed bag. The concentrations used for the assays vary widely - rapamycin gets run at 1 micromolar, while ketoconazole is nearly 1 millimolar. (Can you even run that compound at that concentration? Or that compound at left at 967 micromolar? Is it really soluble in the yeast wells at such levels? There are plenty more that you can wonder about in the same way.

And I went searching for my old friends, the rhodanines, and there they were. Unfortunately, compound SGTC_2454 is 5-benzylidenerhodanine, whose activity is listed as "A dopamine receptor inhibitor" (!). But compound SGTC_1883 is also 5-benzylidenerhodanine, the same compound, run at similar concentration, but this time unannotated. The 5-thienylidenerhodanine is SGTC_30, but that one's listed as a phosphatase inhibitor. Neither of these attributions seem likely to me. There are other duplicates, but many of them are no doubt intentional (run by different parts of the team).

I hate to say this, but just a morning's look at this paper leaves me with little doubt that there are still more strange things buried in the chemistry side of this paper. But since I work for a living (dang it), I'm going to leave it right here, because what I've already noted is more than troubling enough. These mistakes are serious, and call the conclusions of the paper into question: if you can annotate imidazole and its protonated form into two different categories, or annotate two different tautomers (one of which doesn't really exist) into two different categories, what else is wrong, and how much are these annotations worth? And this isn't even the first time that Science has let something like this through. Back in 2010, they published a paper on the "Reactome" that had chemists around the world groaning. How many times does this lesson need to be learned, anyway?

Update: this situation brings up a number of larger issues, such as the divide between chemists and biologists (especially in academia?) and the place of organic chemistry in such high-profile publications (and the place of organic chemists as reviewers of it). I'll defer these to another post, but believe me, they're on my mind.

Update 2 Jake Yeston, deputy editor at Science, tells me that they're looking into this situation. More as I hear it.

Update 3: OK, if Figure 2 is just fragments, structural pieces that were common to compounds that had these signatures, then (1) these are still not acceptable structures, even as fragments, and (2), many of these don't make sense from a medicinal chemistry standpoint. It's bizarre to claim a tetrahydrofuran ring (for example) as the key driver for a class of compounds; the chance that this group is making an actual, persistent interaction with some protein site (or family of sites) is remote indeed. The imidazole/protonated imidazole pair is a good example of this: why on Earth would you pick these two groups to illustrate some chemical tendency? Again, this looks like the work of people who don't really have much chemical knowledge.

0560-0053.pngA closer look at the compounds themselves does not inspire any more confidence. There's one of them from Table S3, which showed a very large difference in IC50 across different yeast strains. It was tested at 400 micromolar. That, folks, was sold to the authors of this paper by ChemDiv, as part of a "drug-like compound" library. Try pulling some SMILES strings from that table yourself and see what you think about their drug likeness.

Comments (130) + TrackBacks (0) | Category: Chemical Biology | Chemical News | The Scientific Literature

April 3, 2014

More Fukuyama Corrections

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Posted by Derek

The Fukuyama group has another series of corrections out, this time in JACS. Here's one, and the other follow right behind it in the ASAP queue. This adds to the string of them in Organic Letters. It's more whiteout stuff - vanishing solvent peaks and impurities. These presumably don't affect the conclusions of the paper, but they don't make a person any more confident, either. One hopes that these high-profile cases will shake people up. . .

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March 28, 2014

More on the UT-Austin Retraction Case

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Posted by Derek

I mentioned an unusual retraction from Organic Letters here last year, and here's some follow-up to the story:

Nearly six years after Suvi Orr received a Ph.D. in chemistry from the University of Texas, the university told her it has decided to do something that institutions of higher learning almost never do: revoke
the degree. Orr, in turn, has sued UT in an effort to hold onto the doctorate that launched her career in the pharmaceutical industry.

Her lawsuit in state district court in Travis County contends that revocation is unwarranted and that the university violated her rights by not letting her defend herself before the dissertation committee that condemned her research long after she graduated. In addition, she says, the committee relied heavily on her former professor, who, she claims, was motivated to “cast the blame elsewhere.”

What a mess. More details as things develop. . .

Comments (17) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

March 21, 2014

Dosing by Body Surface Area

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Posted by Derek

We were talking about allometry around here the other day, which prompts me to mention this paper. It used the reports of resveratrol dosing in animals, crudely extrapolated to humans, to argue that the body surface area normalization (BSA) method was a superior technique for dose estimation across species.

Over the years, though, the BSA method has taken some flak in the literature. It's most widely used in oncology, especially with cytotoxics, but there have been calls to move away from the practice, calling it a relic with little scientific foundation. (The rise of a very obese patient population has also led to controversy about whether body weight or surface area is a more appropriate dose-estimation method in those situations). At the same time, it's proven useful in some other situations, so it can't be completely ignored.

But it seems that the FASEB paper referenced in the first paragraph, which has been cited hundreds of times since 2008, may be overstating its conclusions. For example, it says that "BSA normalization of doses must be used to determine safe starting doses of new drugs because initial studies conducted in humans, by definition, lack formal allometric comparison of the pharmacokinetics of absorption, distribution, and elimination parameters", and cites its reference 13 for support. But when you go to that reference, you find that paper's authors concluding with things like this:

The customary use of BSA in dose calculations may contribute to the omission of these factors, give a false sense of accuracy and introduce error. It is questionable whether all current cancer treatment strategies are near optimal, or even ethical. BSA should be used for allometric scaling purposes in phase I clinical trials, as the scaling of toxicity data from animals is important for selecting starting doses in man, but the gradual discontinuation of BSA-based dosing of cytotoxic drugs in clinical practice is seemingly justified.

Citing a paper for support that flatly disagrees with your conclusions gets some points for bravado, but otherwise seems a bit odd. And there are others - that reference that I linked to in the second paragraph above, under "taken some flak", is cited in the FASEB paper as its reference 17, as something to do with choosing between various BSA equations. And it does address that, to be sure, but in the context of wondering whether the whole BSA technique has any clinical validity at all.

This is currently being argued out over at PubPeer, and it should be interesting to see what comes of it. I'll be glad to hear from pharmacokinetics and clinical research folks to see what they make of the whole situation.

Comments (17) + TrackBacks (0) | Category: Pharmacokinetics | The Scientific Literature

March 20, 2014

Years Worth of the Stuff

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Posted by Derek

bAP15.pngThis time last year I mentioned a particularly disturbing-looking compound, sold commercially as a so-called "selective inhibitor" of two deubiquitinase enzymes. Now, I have a fairly open mind about chemical structures, but that thing is horrible, and if it's really selective for just those two proteins, then I'm off to truck-driving school just like Mom always wanted.

Here's an enlightening look through the literature at this whole class of compound, which has appeared again and again. The trail seems to go back to this 2001 paper in Biochemistry. By 2003, you see similar motifs showing up as putative anticancer agents in cell assays, and in 2006 the scaffold above makes its appearance in all its terrible glory.

The problem is, as Jonathan Baell points out in that HTSpains.com post, that this series has apparently never really had a proper look at its SAR, or at its selectivity. It wanders through a series of publications full of on-again off-again cellular readouts, with a few tenuous conclusions drawn about its structure - and those are discarded or forgotten by the time the next paper comes around. As Baell puts it:

The dispiriting thing is that with or without critical analysis, this compound is almost certainly likely to end up with vendors as a “useful tool”, as they all do. Further, there will be dozens if not hundreds of papers out there where entirely analogous critical analyses of paper trails are possible.

The bottom line: people still don’t realize how easy it is to get a biological readout. The more subversive a compound, the more likely this is. True tools and most interesting compounds usually require a lot more medicinal chemistry and are often left behind or remain undiscovered.

Amen to that. There is way too much of this sort of thing in the med-chem literature already. I'm a big proponent of phenotypic screening, but setting up a good one is harder than setting up a good HTS, and working up the data from one is much harder than working up the data from an in vitro assay. The crazier or more reactive your "hit" seems to be, the more suspicious you should be.

The usual reply to that objection is "Tool compound!" But the standards for a tool compound, one used to investigate new biology and cellular pathways, are higher than usual. How are you going to unravel a biochemical puzzle if you're hitting nine different things, eight of which you're totally unaware of? Or skewing your assay readouts by some other effect entirely? This sort of thing happens all the time.

I can't help but think about such things when I read about a project like this one, where IBM's Watson software is going to be used to look at sequences from glioblastoma patients. That's going to be tough, but I think it's worth a look, and the Watson program seems to be just the correlation-searcher for the job. But the first thing they did was feed in piles of biochemical pathway data from the literature, and the problem is, a not insignificant proportion of that data is wrong. Statements like these are worrisome:

Over time, Watson will develop its own sense of what sources it looks at are consistently reliable. . .if the team decides to, it can start adding the full text of articles and branch out to other information sources. Between the known pathways and the scientific literature, however, IBM seems to think that Watson has a good grip on what typically goes on inside cells.

Maybe Watson can tell the rest of us, then. Because I don't know of anyone actually doing cell biology who feels that way, not if they're being honest with themselves. I wish the New York Genome Center and IBM luck in this, and I still think it's a worthwhile thing to at least try. But my guess is that it's going to be a humbling experience. Even if all the literature were correct in every detail, I think it would be one. And the literature is not correct in every detail. It has compounds like that one at the top of the entry in it, and people seem to think that they can draw conclusions from them.

Comments (18) + TrackBacks (0) | Category: Biological News | Cancer | Chemical Biology | Drug Assays | The Scientific Literature

March 19, 2014

More Things Synthetic Chemists Hate

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Posted by Derek

I enjoyed this post over at Synthetic Remarks on "Five things synthetic chemists hate". And I agree; I hate all of 'em, too. Allow me to add a few to the list:

1. The Mysterious Starting Material. How many times have you looked through an experimental section only to see a synthesis start cold, from a non-commercial compound whose preparation isn't given, or even referenced? One that doesn't seem to have any foundation anywhere else in the literature, either? I think that this is a bit more common in the older literature, but it shouldn't be happening anywhere.

2. It Works on Benzaldehyde; What More Do You Want? What about those new method papers that include a wide, diverse array of examples showing how versatile the new reaction is - but when you look at the list, you realize that it's full of things like cyclohexanone, benzaldehyde. . .and then 4-methylcyclohexanone, p-fluorobenzaldehyde, and so on? Turns out that the reaction lands flat on its nose, stretched out on the sand if there's a basic amine within five hundred yards. But you have to find that out for yourself. It ain't in the text.

3. The Paper Chase. In these days of humungous supplementary info files, what excuse is there to write a paper where all the reactions use one particular reagent - and then send people back to your previous paper to learn how to make it? Sure, reference yourself. But don't march everyone back to a whole other experimental. Are authors getting some sort of nickel-a-page-view deal from the publishers now that I haven't heard about?

4. If I Don't See It, It Isn't There. When I review papers, one of the things I end up dinging people about, more than anything else, is the reluctance to cite relevant literature. In some cases, it's carelessness, but in others, well. . .everyone's seen papers that basically rework someone else's reaction without ever citing the original. And in these days of modern times, as the Firesign Theatre guys used to say, what excuse is there?

5. Subtle Is the Lord. Once in a while, you find an experimental writeup that makes you wrinkle your brow and wonder if someone's pulling your leg. The reaction gets run at -29 degrees C, for 10.46 hours, whereupon it's brought up to -9 and quenched with pH 7.94 buffer solution. That kind of thing. If you're going to put that Proustian level of detail in there, you'd better have a reason (Proust did). No one just stumbles into conditions like that - what happened when you ran your reaction like a normal human, instead of like Vladimir Nabokov on Adderall?

Comments (38) + TrackBacks (0) | Category: Chemical News | The Scientific Literature

March 17, 2014

What If Total Syntheses Had Only 25 Steps to Work In?

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Posted by Derek

Via the Baran lab's Twitter feed, here's a provocative article on whether total organic synthesis has a place in the modern world or not.

One may wonder why this situation has passed undisputed for such a long time. Currently however, wide parts of the chemical community look upon total synthesis as a waste of time, resources and talents. Behind the scene, it may even be argued that the obsession to synthesize almost any natural product irrespective of its complexity and practical importance has blocked the development of other more relevant fields. Therefore, it is high time to consider a reorientation of the entire discipline

That's a bit of a straw man in that paragraph, and I have to note it, even though I do feel odd sticking up for total synthesis (about which I've been pretty caustic myself, for many years now.). I don't think that there's been an "obsession to synthesize almost any natural product", although it's true that many new synthetic methods have used some natural product or another as demonstration pieces. But the author, Johann Mulzer, came out of the Corey group in the old days, and has spent his career doing total synthesis, so he's speaking from experience here.

He goes on to argue that the field does have a place, but that it had better shape up. Short syntheses have to take priority over "first syntheses", because (let's face it), just about anything can be made if you're willing to throw enough time, money, and postdocs at it. The paper is full of examples from Mulzer's own career (and others'), and if you read it carefully, you'll see some unfavorable contrasts drawn to some Nicolaou syntheses. He finishes up:

In conclusion, this article tries to show how various strategies may be used to streamline and to shorten otherwise long synthetic routes to complex target molecules. The reader may get the impression that it pays very well to think intensively about cascade reactions, intramolecular cycloadditions, suitable starting materials and so on, instead of plunging into a brute-force and therefore mostly inefficient sequence. After all, there is an iron maxim: if a target cannot be reached within, say, 25 steps, it is better to drop it. For what you will get is a heroic synthesis, at best, but never an efficient one.

A 25-step limit would chop an awful lot out of the synthetic literature, wouldn't it? But it's not fair to apply that retrospectively. What if we apply it from here on out, though? What would the total synthetic landscape look like then?

Comments (46) + TrackBacks (0) | Category: Chemical News | The Scientific Literature

March 14, 2014

Going After Poor Published Research

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Posted by Derek

This should be interesting - John Ioannidis, scourge of poorly reproducible published results, is founding an institute at Stanford. The Economist has more:

They will create a “journal watch” to monitor scientific publishers’ work and to shame laggards into better behaviour. And they will spread the message to policymakers, governments and other interested parties, in an effort to stop them making decisions on the basis of flaky studies. All this in the name of the centre’s nerdishly valiant mission statement: “Identifying and minimising persistent threats to medical-research quality.”

It will be most interesting to see what comes of this. Better quality research is in everyone's best interest, to put it mildly, and I hope that this leads to some.

Comments (13) + TrackBacks (0) | Category: The Scientific Literature

March 6, 2014

We Are Pleased To Publish Your Senseless Ravings

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Posted by Derek

There's been some (justified) hand-wringing in scientific publishing circles over the revelation that at least 120 abstracts and papers out there in the literature are complete nonsense generated by SciGen. (A few previous SciGen adventures can be found here and here) Some news reports have made it seem like these were regular full papers, but they're actually published conference proceedings which (frankly) are sort of the ugly stepchild of the science journal world to begin with. They're supposed to be reviewed, and they certainly should have been reviewed enough for someone to catch on to the fact that they were devoid of meaning, but if you're going to fill the pages of a reputable publisher with Aphasio-matic ramblings, that's the way to do it.

And these were reputable publishers, Springer and the IEEE. Springer has announced that they're removing all this stuff from their databases, since the normal retraction procedure doesn't exactly seem necessary. They're also trying to figure out what loophole let this happen in the first place, and they've contacted Cyril Labbé, the French researcher who wrote the SciGen-detecting software, for advice. The IEEE, for its part, has had this problem before, has had it for years, has been warned about it, but still seems to be ready and willing to publish gibberish. I don't know if Springer has had bad experiences with SciGen material, but the IEEE journals sure have, and it's apparently done no good at all. Live and don't learn. The organization has apparently removed the papers, but has made (as far as I can tell) no public statement whatsoever about the whole incident.

So who went to all this trouble, anyway? That Scholarly Kitchen link above has some speculations:

An additional (and even more disturbing) problem with the proceedings papers most recently discovered is emerging as the investigation continues: at least one of the authors contacted had no idea that he had been named as a coauthor. This suggests that the submissions were more than spoofs — spoofing can easily be accomplished by using fake names as well as fake content. The use of real scientists’ names suggests that at least some of these papers represent intentional scholarly fraud, probably with the intention of adding bulk to scholars’ résumés.

This takes us back to the open-access versus traditional publisher wars. When this sort of thing happens to OA journals, the response from some of the other publishers, overtly at times, is "Well, yeah, sure, that's what you get when you don't go with the name brand". And there's certainly a lot of weird crap that shows up - take a look at this thing, from the open access journal Cancer Research and Management, and see if you can make head or tail of it. Clozapine might have helped it a bit, but maybe not:

Our findings suggest that we are dealing with true reverse biologic system information in an activated collective cancer stem cell memory, in which physics participates in the elaboration of geometric complexes and chiral biomolecules that serve to build bodies with embryoid print as it develops during gestation.

That's a little more coherent than what SciGen will give you, but not so coherent as to, you know, make any sense. And if by any chance you were OK with that extract, the rest of the abstract mentions comets and the Large Hadron Collider, so take that. It lacks only gyres (don't we all?) But what this latest incident tells us is that this paper would have waltzed right in at plenty of other publishers, open-access or not. The authors should be aiming higher, y'know?

Comments (19) + TrackBacks (0) | Category: The Scientific Literature

March 3, 2014

Sydney Brenner on the State of Science

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Posted by Derek

Via Retraction Watch, here's an outspoken interview with Sydney Brenner, who's never been the sort of person to keep his opinions bottled up inside him. Here, for example, are his views on graduate school in the US:

Today the Americans have developed a new culture in science based on the slavery of graduate students. Now graduate students of American institutions are afraid. He just performs. He’s got to perform. The post-doc is an indentured labourer. We now have labs that don’t work in the same way as the early labs where people were independent, where they could have their own ideas and could pursue them.

The most important thing today is for young people to take responsibility, to actually know how to formulate an idea and how to work on it. Not to buy into the so-called apprenticeship. I think you can only foster that by having sort of deviant studies. That is, you go on and do something really different. Then I think you will be able to foster it.

But today there is no way to do this without money. That’s the difficulty. In order to do science you have to have it supported. The supporters now, the bureaucrats of science, do not wish to take any risks. So in order to get it supported, they want to know from the start that it will work. This means you have to have preliminary information, which means that you are bound to follow the straight and narrow.

I can't argue with that. In academia these days, it seems to me that the main way that something really unusual or orthogonal gets done is by people doing something else with their grant money than they told people they'd do. Which has always been the case to some extent, but I get the impression it's more so than ever. The article also quotes from Brenner's appreciation of the late Fred Sanger, where he made a similar point:

A Fred Sanger would not survive today’s world of science. With continuous reporting and appraisals, some committee would note that he published little of import between insulin in 1952 and his first paper on RNA sequencing in 1967 with another long gap until DNA sequencing in 1977. He would be labelled as unproductive, and his modest personal support would be denied. We no longer have a culture that allows individuals to embark on long-term—and what would be considered today extremely risky—projects.

Here are Brenner's mild, temperate views on the peer-review system and its intersection with academic publishing:

. . .I don’t believe in peer review because I think it’s very distorted and as I’ve said, it’s simply a regression to the mean.

I think peer review is hindering science. In fact, I think it has become a completely corrupt system. It’s corrupt in many ways, in that scientists and academics have handed over to the editors of these journals the ability to make judgment on science and scientists. There are universities in America, and I’ve heard from many committees, that we won’t consider people’s publications in low impact factor journals.

Now I mean, people are trying to do something, but I think it’s not publish or perish, it’s publish in the okay places [or perish]. And this has assembled a most ridiculous group of people. I wrote a column for many years in the nineties, in a journal called Current Biology. In one article, “Hard Cases”, I campaigned against this [culture] because I think it is not only bad, it’s corrupt. In other words it puts the judgment in the hands of people who really have no reason to exercise judgment at all. And that’s all been done in the aid of commerce, because they are now giant organisations making money out of it.

I don't find a lot to disagree with there, either. The big scientific publishers have some good people working for them, but the entire cause is more and more suspect. THere's a huge moral hazard involved, which we don't seem to be avoiding very well at all.

Comments (35) + TrackBacks (0) | Category: General Scientific News | The Scientific Literature

February 26, 2014

Changes in Papers

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Posted by Derek

Here's a look at some of the changes in JACS papers over the decades. Several trends are clear - there are more authors now, and single-author papers have almost vanished. Reference lists are much longer (which surely reflects both the sie of the literature and the relative ease of bibliography compared to the bound-volume/index card days). Have a look at the charts - François-Xavier Coudert, the blog's author, says that he'll be putting up some more later on, and I look forward to seeing what comes up.

Comments (5) + TrackBacks (0) | Category: The Scientific Literature

February 20, 2014

The NIH Takes a Look At How the Money's Spent

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Posted by Derek

The NIH is starting to wonder what bang-for-the-buck it gets for its grant money. That's a tricky question at best - some research takes a while to make an impact, and the way that discoveries can interact is hard to predict. And how do you measure impact, by the way? These are all worthy questions, but here's apparently the way things are being approached:

Michael Lauer's job at the National Institutes of Health (NIH) is to fund the best cardiology research and to disseminate the results rapidly to other scientists, physicians, and the public. But NIH's peer-review system, which relies on an army of unpaid volunteer scientists to prioritize grant proposals, may be making it harder to achieve that goal. Two recent studies by Lauer, who heads the Division of Cardiovascular Sciences at NIH's National Heart, Lung, and Blood Institute (NHLBI) in Bethesda, Maryland, raise some disturbing questions about a system used to distribute billions of dollars of federal funds each year.

(MiahcalLauer recently analyzed the citation record of papers generated by nearly 1500 grants awarded by NHLBI to individual investigators between 2001 and 2008. He was shocked by the results, which appeared online last month in Circulation Research: The funded projects with the poorest priority scores from reviewers garnered just as many citations and publications as those with the best scores. That was the case even though low-scoring researchers had been given less money than their top-rated peers.

I understand that citations and publications are measurable, while most other ways to gauge importance aren't. But that doesn't mean that they're any good, and I worry that the system is biased enough already towards making these the coin of the realm. This sort of thing worries me, too:

Still, (Richard) Nakamura is always looking for fresh ways to assess the performance of study sections. At the December meeting of the CSR advisory council, for example, he and Tabak described one recent attempt that examined citation rates of publications generated from research funded by each panel. Those panels with rates higher than the norm—represented by the impact factor of the leading journal in that field—were labeled "hot," while panels with low scores were labeled "cold."

"If it's true that hotter science is that which beats the journals' impact factors, then you could distribute more money to the hot committees than the cold committees," Nakamura explains. "But that's only if you believe that. Major corporations have tried to predict what type of science will yield strong results—and we're all still waiting for IBM to create a machine that can do research with the highest payoff," he adds with tongue in cheek.

"I still believe that scientists ultimately beat metrics or machines. But there are serious challenges to that position. And the question is how to do the research that will show one approach is better than another."

I'm glad that he doesn't seem to be taking this approach completely seriously, but others may. If only impact factors and citation rates were real things that advanced human knowledge, instead of games played by publishers and authors!

Comments (34) + TrackBacks (0) | Category: The Scientific Literature | Who Discovers and Why

February 19, 2014

Robo-Combing the Chemistry Literature For Mistakes

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Posted by Derek

This is a very timely post indeed from Peter Murray-Rust. He's describing a system that his group has developed (ChemVisitor) to dig through the chemical literature looking for incorrect structures (and much more).

He shows examples from an open-access paper, in which one of the structures is in fact misdrawn. But how would Elsevier, Nature, the ACS, Wiley or the other big publishers take to having these things highlighted every day of the week. Not well:

So try it for yourself. Which compound is wrong? (*I* don’t know yet) How would you find out? Maybe you would go to Chemical Abstracts (ACS). Last time I looked it cost 6USD to look up a compound. That’s 50 dollars, just to check whether the literature is right. And you would be forbidden from publishing what you found there (ACS sent the lawyers to Wikipedia for publishing CAS registry numbers). What about Elsevier’s Reaxys? Almost certainly as bad.


But isn’t there an Open collection of molecules? Pubchem in the NIH? Yes, and ACS lobbied on Capitol Hill to have it shut down as it was “socialised science instead of the private sector”. They nearly won. (Henry Rzepa and I ran a campaign to highlight the issue). So yes, we can use Pubchem and we have and that’s how Andy’s software discovered the mistake.

This was the first diagram we analysed. Does that mean that every paper in the literature contains mistakes?

Almost certainly yes.

But they have been peer-reviewed.

Yes – and we wrote software (OSCAR) 10 years ago that could do the machine reviewing. And it showed mistakes in virtually every paper.

So we plan to do this for every new paper. It’s technically possible. But if we do it what will happen?

If I sign the Elsevier content-mining click-through (I won’t) then I agree not to disadvantage Elsevier’s products. And pointing out publicly that they are full of errors might just do that. And if I don’t?…

This comment on Ycombinator is from someone who's seen some of the Murray-Rost group's software in action, and is very interesting indeed:

They can take an ancient paper with very low quality diagrams of complex chemical structures, parse the image into an open markup language and reconstruct the chemical formula and the correct image. Chemical symbols are just one of many plugins for their core software which interprets unstructured, information rich data like raster diagrams. They also have plugins for phylogenetic trees, plots, species names, gene names and reagents. You can develop plugins easily for whatever you want, and they're recruiting open source contributors (see https://solvers.io/projects/QADhJNcCkcKXfiCQ6, https://solvers.io/projects/4K3cvLEoHQqhhzBan).

As a side effect of how their software works, it can detect tiny suggestive imperfections in images that reveal scientific fraud. I was shown a demo where a trace from a mass spec (like this http://en.wikipedia.org/wiki/File:ObwiedniaPeptydu.gif) was analysed. As well as reading the data from the plot, it revealed a peak that had been covered up with a square - the author had deliberately obscured a peak in their data that was inconvenient. Scientific fraud. It's terrifying that they find this in most chemistry papers they analyse.

Peter's group can analyse thousands or hundreds of thousands of papers an hour, automatically detecting errors and fraud. . .

Unless I'm very much mistaken, we'll be hearing a lot more about this. It touches on the quality of the literature, the quality of the people writing the papers, and the business model(s) of the people publishing it all. And these are very, very relevant topics that are are getting more important all the time. . .

Comments (31) + TrackBacks (0) | Category: The Scientific Literature

February 18, 2014

Thoughts on Overpublishing

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Posted by Derek

My recent memorial notice for Alan Katritzky brought an interesting comment, by someone who did the math that I didn't. His total publication count actually seems to be 2215 papers published since 1953. That comes to one paper every ten days over sixty-one years. I have trouble even imagining that. This is a vast amount of work, both the chemistry and the writing, and it's a monument that very, very few people will leave behind them.

Should anyone, though? I mean no disrespect to Katritzky's memory by asking this question, let me note quickly. But I wrote about this here a few years ago, the idea that a person can, in fact, publish too many papers. My example then was H. C. Brown - I'm not sure how many papers he co-authored, but the figure is a large one and brings on similar thoughts.

There have been many scientists on the other end of the scale, going back to Isaac Newton, who had to be badgered into letting everyone know that he'd revolutionized physics. Lars Onsager is a good example from the physics/chemistry borderlands - there are stories told about the work he had stored away in his filing cabinets, a terrifying stockpile that most other people would have found very much to their credit to have published. This approach is clearly not the way to go, either - people don't have a chance to build on your work when they don't know about it, and others may spend a good amount of effort duplicating things when you could (and should) have saved them the effort.

But publishing thousands of papers doesn't seem like a good alternative, to be honest. People will have trouble sorting out the good parts, and they can't all be good parts. Time will settle that question, you might think, but time could bungle that job. Time has dropped the ball before.

Update: See Arr Oh did a very interesting list last year of the organic chemists who publish the most. Katritzky did indeed lead the field.

Comments (44) + TrackBacks (0) | Category: The Scientific Literature

Not Again - Stem Cell Results in Trouble?

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Posted by Derek

Oh, @#$!. That was my first comment when I saw this story. That extraordinary recent work on creating stem cells by subjected normal cells to acid stress is being investigated:

The RIKEN centre in Kobe announced on Friday that it is looking into alleged irregularities in the work of biologist Haruko Obokata, who works at the institution. She shot to fame last month as the lead author on two papers published in Nature that demonstrated a simple way to reprogram mature mice cells into an embryonic state by simply applying stress, such as exposure to acid or physical pressure on cell membranes. The RIKEN investigation follows allegations on blog sites about the use of duplicated images in Obokata’s papers, and numerous failed attempts to replicate her results.

PubPeer gets the credit for bringing some of the problems into the light. There are some real problems with figures in the two papers, as well as earlier ones from the same authors. These might be explicable as cimple mistakes, which is what the authors seem to be claiming, if it weren't for the fact that no one seems to be able to get the stem-cell results to reproduce. There are mitigating factors there, too - different cell lines, perhaps the lack of a truly detailed protocol from the original paper. But a paper should have enough details in it to be reproduced, shouldn't it?

Someone on Twitter was trying to tell me the other day that the whole reproducibility issue was being blown out of proportion. I don't think so. The one thing we seem to be able to reproduce is trouble.

Update: a list of the weirdest things (so far) about this whole business.

Comments (25) + TrackBacks (0) | Category: Biological News | The Scientific Literature

February 17, 2014

The Org Lett Spectral Hammer Falls Again

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Posted by Derek

I see that as of this moment, the five articles at the top of the Organic Letters ASAP feed are all corrections from the Nakada group. It looks to be the same situation as the Fukuyama corrections: NMR editing. The corrections (visible for free because you can see the first page) all mention that the conclusions of the papers are not altered, nor are the yields of products. So Amos Smith really is serious about his data-cleaning crusade, and I can see where he's coming from. Falsus in unum, falsus in omnibus. The only place to draw the line is right back at the start.

Comments (31) + TrackBacks (0) | Category: The Scientific Literature

February 14, 2014

"It Is Not Hard to Peddle Incoherent Math to Biologists"

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Posted by Derek

Here's a nasty fight going on in molecular biology/bioinformatics. Lior Pachter of Berkeley describes some severe objections he has to published work from the lab of Manolis Kellis at MIT. (His two previous posts on these issues are here and here). I'm going to use a phrase that Pachter hears too often and say that I don't have the math to address those two earlier posts. But the latest one wraps things up in a form that everyone can understand. After describing what does look like a severe error in one of the Manolis group's conference presentations, which Pachter included in a review of the work, he says that:

. . .(they) spun the bad news they had received as “resulting from combinatorial connectivity patterns prevalent in larger network structures.” They then added that “…this combinatorial clustering effect brings into question the current definition of network motif” and proposed that “additional statistics…might well be suited to identify larger meaningful networks.” This is a lot like someone claiming to discover a bacteria whose DNA is arsenic-based and upon being told by others that the “discovery” is incorrect – in fact, that very bacteria seeks out phosphorous – responding that this is “really helpful” and that it “raises lots of new interesting open questions” about how arsenate gets into cells. Chutzpah. When you discover your work is flawed, the correct response is to retract it.

I don’t think people read papers very carefully. . .

He goes on to say:

I have to admit that after the Grochow-Kellis paper I was a bit skeptical of Kellis’ work. Not because of the paper itself (everyone makes mistakes), but because of the way he responded to my review. So a year and a half ago, when Manolis Kellis published a paper in an area I care about and am involved in, I may have had a negative prior. The paper was Luke Ward and Manolis Kellis “Evidence for Abundant and Purifying Selection in Humans for Recently Acquired Regulatory Functions”, Science 337 (2012) . Having been involved with the ENCODE pilot, where I contributed to the multiple alignment sub-project, I was curious what comparative genomics insights the full-scale $130 million dollar project revealed. The press releases accompanying the Ward-Kellis paper (e.g. The Nature of Man, The Economist) were suggesting that Ward and Kellis had figured out what makes a human a human; my curiosity was understandably piqued.

But a closer look at the paper, Pachter says, especially a dig into the supplementary material (always a recommended move) shows that the conclusions of the paper were based on what he terms "blatant statistically invalid cherry picking". See, I told you this was a fight. He also accuses Kellis of several other totally unacceptable actions in his published work, the sorts of things that cannot be brushed off as differences in interpretations or methods. He's talking fraud. And he has a larger point about how something like this might persist in the computational biology field (emphasis added):

Manolis Kellis’ behavior is part of a systemic problem in computational biology. The cross-fertilization of ideas between mathematics, statistics, computer science and biology is both an opportunity and a danger. It is not hard to peddle incoherent math to biologists, many of whom are literally math phobic. For example, a number of responses I’ve received to the Feizi et al. blog post have started with comments such as

“I don’t have the expertise to judge the math, …”

Similarly, it isn’t hard to fool mathematicians into believing biological fables. Many mathematicians throughout the country were recently convinced by Jonathan Rothberg to donate samples of their DNA so that they might find out “what makes them a genius”. Such mathematicians, and their colleagues in computer science and statistics, take at face value statements such as “we have figured out what makes a human human”. In the midst of such confusion, it is easy for an enterprising “computational person” to take advantage of the situation, and Kellis has.

You can peddle incoherent math to medicinal chemists, too, if you feel the urge. We don't use much of it day-to-day, although we've internalized more than we tend to realize. But if someone really wants to sell me on some bogus graph theory or topology, they'll almost certainly be able to manage it. I'd at least give them the benefit of the doubt, because I don't have the expertise to call them on it. Were I so minded, I could probably sell them some pretty shaky organic chemistry and pharmacokinetics.

But I am not so minded. Science is large, and we have to be able to trust each other. I could sit down and get myself up to speed on topology (say), if I had to, but the effort required would probably be better spent doing something else. (I'm not ruling out doing math recreationally, just for work). None of us can simultaneously be experts across all our specialities. So if this really is a case of publishing junk because, hey, who'll catch on, right, then it really needs to be dealt with.

If Pachter is off base, though, then he's in for a rough ride of his own. Looking over his posts, my money's on him and not Kellis, but we'll all have a chance to find out. After this very public calling out, there's no other outcome.

Comments (32) + TrackBacks (0) | Category: Biological News | In Silico | The Dark Side | The Scientific Literature

February 12, 2014

Genius, Sheer Genius

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Posted by Derek

So we have bogus scientific journals out there, and we have people who will sell you results so you can make just-add-water papers for the real journals. And we have impact factors, the overuse of which leads to still more bogosity in every part of scientific publishing. So. . .why not sell fake impact factors? That way, you can harvest publication fees from credulous impact-seeking bozos. My Iranian wife tells me that there's a saying in Farsi that translates as "A thief robs a thief, and God smiles".

Comments (11) + TrackBacks (0) | Category: The Scientific Literature

February 11, 2014

Pesticide Toxicity?

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Posted by Derek

There's been a report on the toxicity of various pesticides in the literature suggesting that they're far more toxic to human cells than had been thought. My eyebrows went up a bit when I heard this, because these sorts of assays had been done many times before. Then I realized that this was another paper from the Séralini group, and unfortunately, that alone is enough to account for the variance.

Update: commentors to this post have noted that the cell culture conditions used in the paper are rather unusual. Specifically, they're serum-free during the testing period, which puts the cells under stress to begin with. There's also the general problem, which others have brought up, about what it means to dispense these things directly onto cell cultures in diluted DMSO, since that's rather far from how they're going to be presented in the real world. Cell assays get run like that in the drug industry, to be sure, but you've got to be very careful drawing toxicological or other whole-animal conclusions from them. And we already have whole-animal studies on these formulations, don't we? I mean, juiced broccoli straight from the organic farmer's market might well have similar effects under these conditions.

Here's a story from Science with more background. Seralini is the guy who made headlines a couple of years ago with another report that genetically modified corn caused tumors in rodents, but that one was so poorly run and poorly controlled that its conclusions (which have not been seen in any other study) cannot be taken seriously. That's Séralini's problem right there: from all appearances, he's a passionate advocate for his positions, and he appears to be ready to go with whatever results line up with his beliefs. This is human nature, for sure, but science is about trying to work past those parts of human nature. The key is to keep the curious, inquisitive side, and correct for the confirmation bias I-know-I'm-right side. At this point, even if Séralini were to discover something real (and really worth taking seriously), it would have a hard time gaining acceptance, because his previous papers have been so unreliably over-the-top.

I'm not the only person who thinks that. An editor of the journal this latest Seralini paper appeared in has actually resigned because it got published:

When Ralf Reski read the latest paper from controversial French biologist Gilles-Eric Séralini, he quickly decided he wanted nothing to do with it. Séralini’s report in BioMed Research International describes how pesticides kill cultured human cells, with the hair-raising conclusion that pesticides may be vastly more toxic than assumed by regulatory authorities. Some scientists are criticizing the findings as neither surprising nor significant—but they have touched off a firestorm, with environmental groups calling for changes in how pesticides are regulated. That was too much for Reski. Within hours of reading the paper last week, the plant scientist at the University of Freiburg in Germany resigned as an editor of the journal and asked for his name to be removed from its website. "I do not want to be connected to a journal that provides [Séralini] a forum for such kind of agitation," he wrote in his resignation e-mail to the publisher, Hindawi Publishing Corporation.

Should pesticide toxicity be a subject of investigation? Absolutely. Should people be alert to assays that have not been run that should be investigated? Definitely. Are there things that we don't know about pesticide exposure that we should? I would certainly think so. But Séralini's history makes him (scientifically) one of the least effective people to be working on these questions. As a headline-grabber, though, he's pretty efficient. Which I suspect is the real point. If you're sure you're right, any weapon you can pick up is a good one.

Comments (17) + TrackBacks (0) | Category: The Scientific Literature | Toxicology

February 10, 2014

Today We Have Naming of Parts

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Posted by Derek

I can strongly recommend this article by Carmen Drahl in C&E News on the way that we chemists pick fights over nomenclature. She has examples of several kinds of disagreement (competing terms for the same thing, terms that overlap but are still different, competing ways to measure something in different ways, and terms that are fuzzy enough that some want to eliminate them entirely).

As several of the interviewees note, these arguments are not (always) petty, and certainly not always irrational. Humans are good at reification - turning something into a "thing". Name a concept well, and it sort of shimmers into existence, giving people a way to refer to it as if it were a solid object in the world of experience. This has good and bad aspects. It's crucial to the ability to have any sort of intellectual discussion and progress, since we have to be able to speak of ideas and other entities that are not actual physical objects. But a badly fitting name can do real harm, obscuring the most valuable or useful parts of an idea and diverting thoughts about it unproductively.

My own favorite example is the use of "agonist" and "antagonist" to describe the actions of nuclear receptor ligands. This (to my way of thinking) is not only useless, but does real harm to the thinking of anyone who approaches nuclear receptors having first learned about GPCRs. Maybe the word "receptor" never should have been used for these things in the first place, although realizing that would have required supernatural powers of precognition.

There are any number of examples outside chemistry, of course. One of my own irritants is when someone says that something has been "taken to the next level". You would probably not survive watching a sports channel if that phrase were part of a drinking game. But it presupposes that some activity comes in measurable chunks, and that everyone agrees on what order they come in. I'm reminded of the old blenders with their dials clicking between a dozen arbitrary "levels", labeled with tags like "whip", "chop", and "liquify". Meaningless. It's an attempt to quantify - to reify - what should have been a smooth rheostat knob with lines around it.

OK, I'll stop before I bring up Wittgenstein. OK, too late. But he was on to something when he told people to be careful about the way language is used, and to watch out when you get out onto the "frictionless ice" of talking about constructions of thought. His final admonition in his Tractacus Logico-Philosophicus, that if we cannot speak about something that we have to pass over it in silence, has been widely quoted and widely unheeded, since we're all sure that we can, of course, speak about what we're speaking about. Can't we?

For today's post title, see here

Comments (20) + TrackBacks (0) | Category: Chemical News | The Scientific Literature

A Timeline from Cell

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Posted by Derek

Here's a very interesting feature from Cell - an interactive timeline on the journal's 40th anniversary, highlighting some of the key papers it's published over the years. This installment takes us up into the early 1980s. When you see the 1979 paper that brings the news that tyrosine groups on proteins actually get phosphorylated post-translation, the 1982 discovery of Ras as involved in human cancer cells, or another 1982 paper showing that telomeres have these weird repeating units on them, you realize how young the sciences molecular and cell biology really are.

Comments (3) + TrackBacks (0) | Category: Biological News | The Scientific Literature

February 4, 2014

Put Down That White-Out; Drop That Photoshop Cursor

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Posted by Derek

I've had some e-mails about this today: an impressive series of six corrections in Organic Letters (scroll down here). I guess Amos Smith was serious about his editorial last year on manipulation of spectra. All of these corrections are for NMR cleanup of just that variety (disappearing solvent and impurity peaks, along with restated reaction yields). We'll see if it can encourager les autres.

Update: See Arr Oh asks if the Fukuyama lab jumped, or were they pushed?

Comments (44) + TrackBacks (0) | Category: The Scientific Literature

January 24, 2014

Are There Good Writers In This Business?

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Posted by Derek

Here's a question sent in by a reader that I actually have trouble answering: who would you say are the best writers of scientific papers in our field? I'm not necessarily talking about the results in those papers, as much as clear presentation and layout, written in a way that gets the point of the paper across without having to decode the thing.

It's tough, because writing a journal publication means operating under a variety of constraints. One of the biggest of those is word count (or page length). The fierce compression that this can bring on makes unpacking some papers a sentence-by-sentence excavation job, but it's not that the authors would write it like that if they weren't forced to. The opposite situation would be a disaster, too, though - there are, I'm sure, plenty of people who would just ramble on and on given unlimited page space to work with. Pascal's apology for writing such a long letter ("There was not enough time to write a shorter one") is germane. Rare is the first draft that can't be tightened up substantially, scientific publication or not.

But many journal articles are tightened up so hard that they twang when you try to read them. Maintaining clarity and flow under these conditions isn't easy, and I'd be interested to hear about people who manage to stand out enough to be noticed. And since this is a blog, and this is the internet, feel free to bring up examples from the other end of the scale - people whose papers are inevitably a chore. Nominees?

(My impression, by the way, is that well-written papers are more likely to be found in the older literature. I'm not sure if that's just selection bias, since we get to choose over a wider range of time and subject matter that way, or if journal editors were a bit looser about what they would allow back then. The original Watson and Crick DNA paper, for example, would surely never be written up that way today).

Update: here's a Curious Wavefunction post on this from a couple of years ago, with some of his own nominations.

Comments (43) + TrackBacks (0) | Category: The Scientific Literature

January 21, 2014

Throwing Out the Files

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Posted by Derek

Since I'm in the process of moving my office, I've been taking time to do something that's needed to be done for quite a while: cleaning out my files. Somewhere around 2007 or so, I made the switchover to keeping PDFs as my primary filing system, with paper copies when needed. There was a transitional period, which I ended up splicing together by checking through my recent printed copies and backfilling those into my digital archive, but after that, it was all digital. (For the record, I'm still using Zotero for that purpose, although there are several equally valid alternatives, both commercial and freeware).

But I still had a pretty massive filing cabinet full of stuff, and I let that remain undisturbed, even though I knew some of it was surely junk. Only when I started digging into it did I realize just how much of it was little more than that. I'd estimate that I've thrown at least 80% of my files into the recycling bin, an act that would have made me uneasy only a few years ago, and horrified me in, say, 2004. It was easier than I thought, though.

That's because the folders easily fell into several broad categories. In the medical/biological sections of the cabinet, there were "Topics I'm Unlikely to Revisit - And When I Do, It Won't Be With These References". Those went right into the recycling bin. And there were "Topics I May Well Revisit, But When I Do, It Won't Be With These References". Those, after a glance through their contents, went into the bin as well. These were folders on (for example) disease areas that I've worked on in the past, and might conceivably work on again, but a folder full of ten-year-old biomedical articles is not that useful compared to the space it takes up and the trouble it takes to move it. And if that sounds borderline to you, how about the ones that hadn't been updated since the late 1990s? Junk. Nothing in the literature goes out of date faster than a state-of-current-disease-research article.

Moving to the chemistry folders, I was quickly surprised at how many of those I was throwing away as well. The great majority of the printed papers I kept were chemistry ones, but the great majority of what I started out with went into the recycling bin anyway. Digging through them was, in many cases, a reminder of what keeping up with the literature used to be like, back in the day. It was a time when if you found a useful-looking paper, you copied it out and put it in your files, because there was no telling when or if you'd be able to find it again. If you were one of the supremely organized ones, you drew a key reaction or two on an index card and filed that according to some system of your own devising - that's before my time, but I saw people doing that back when I was a grad student. The same sort of pack-ratting persisted well into the 1990s, though, but eroded in the face of better access to Chemical Abstracts (and the rise of competing databases). Finding that reaction, or others like it, or even better references than the ones you knew about, became less and less of a big deal.

So in my files, over in the section for "Synthesis of Amines", there was a folder on the opening of epoxides by amines. And in it were several papers I'd copied in the late 1980s. And some printed-out hits from SciFinder searches in about 1993. And a couple of reactions that I'd seen at conferences, and a paper from 1997 showing how you could change the site of ring opening, sometimes, with some systems. Into the bin it went, despite the feeling (not an inaccurate one) that I was throwing away work that I'd put into assembling all that. But if I find myself wanting to run such a reaction, I can probably set something up that'll work fairly well, and if it doesn't, I can probably find a review article (or two) where someone else has assembled the previous literature.

One of the biggest problems with my chemistry files, I realized, was the difficulty of searching them. I'd gotten used to the world of SciFinder and Reaxsys and Google and PubMed, where information can be called up any way you like. File folders, though, do not speak of their contents. Unless you have the main points of that content committed to memory, you have to open them up and flip through them, hoping for something relevant to pop up. I can well remember doing that in the early 1990s with some of these very folders ("Hmm, let's see what methods I have for such-and-such"), but that style of searching disappeared many years ago. You can now see what methods everyone has, and quickly find out what's been added to the pile since the last time you looked. Younger researchers who've grown up in that world may find it odd that I'm pointing out that water is wet, but my earliest file-cabinet folders were started in another time. File folders are based on tagging (and in its purest form, a physical label), and I agree with people who say that the ability to search is more important and useful than the ability to tag.

So, what did I keep? Folders on specialized topics that I recalled were very difficult to assemble, in a few cases. Papers that I know that I've referred to several times over the years. Papers that refer directly to things that I'm currently working on. Some stuff that's so old that it falls under the category of memorabilia. And finally, papers on more current topics that I want to make sure that I also have in digital form, but didn't have time to check just now. But that three-inch-thick collection of nuclear receptor papers from 2000-2002? The papers on iron dienyl reagents that I copied off during a look at that chemistry in 1991, and never had a need to refer to after about ten days? A folder of reductive amination conditions from the late 1980s? Into the big blue bin with all of it.

Comments (23) + TrackBacks (0) | Category: Life in the Drug Labs | The Scientific Literature

January 20, 2014

A Long Fight Over Allegations of Fraud

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Posted by Derek

Here's a long article from the Raleigh News and Observer (part one and part two) on the Eaton/Feldheim/Franzen dispute in nanoparticles, which some readers may already be familiar with (I haven't covered it on the blog myself). The articles are clearly driven by Franzen's continued belief that research fraud has been committed, and the paper makes the most of it.

The original 2004 publication in Science claimed that RNA solutions could influence the crystal form of palladium nanoparticles, which opened up the possibility of applying the tools of molecular biology to catalysts and other inorganic chemistry applications. Two more papers in JACS extended this to platinum and looked at in vitro evolutionary experiments. But even by 2005, Franzen's lab (who had been asked to join the collaboration between Eaton and Feldheim, who were now at Colorado and a startup company) was generating disturbing data: the original hexagonal crystals (a very strange and interesting form for palladium) weren't pure palladium at all - on an elemental basis, they were mostly carbon. (Later work showed that they were unstable crystals of (roughly) Pd(dba)3, with solvated THF. And they were produced just as well in the negative control experiments, with no RNA added at all.

N. C. State investigated the matter, and the committee agreed that the results were spurious. But they found Feldheim guilty of sloppy work, rather than fraud, saying he should have checked things out more thoroughly. Franzen continued to feel as if justice hadn't been done, though:

In fall 2009, he spent $1,334 of his own money to hire Mike Tadych, a Raleigh lawyer who specializes in public records law and who has represented The News & Observer. In 2010, the university relented and allowed Franzen into the room where the investigation records were locked away.

Franzen found the lab notebooks, which track experiments and results. As he turned the pages, he recognized that Gugliotti kept a thorough and well-organized record.

“I found an open-and-shut case of research fraud,” Franzen said.

The aqueous solution mentioned in the Science article? The experiments routinely used 50 percent solvent. The experiments only produced the hexagonal crystals when there was a high level of solvent, typically 50 percent or more. It was the solvent creating the hexagonal crystals, not the RNA.

On Page 43 of notebook 3, Franzen found what he called a “smoking gun.”

(Graduate student Lina) Gugliotti had pasted four images of hexagonal crystals, ragged around the edges. The particles were degrading at room temperature. The same degradation was present in other samples, she noted.

The Science paper claimed the RNA-templated crystals were formed in aqueous solution with 5% THF and were stable. NC State apparently offered to revoke Gugliotti's doctorate (and another from the group), but the article says that the chemistry faculty objected, saying that the professors involved should be penalized, not the students. The university isn't commenting, saying that an investigation by the NSF is still ongoing, but Franzen points out that it's been going on for five years now, a delay that has probably set a record. He's published several papers characterizing the palladium "nanocrystals", though, including this recent one with one of Eaton and Feldheim's former collaborators and co-authors. And there the matter stands.

It's interesting that Franzen pursued this all the way to the newspaper (known when I Iived in North Carolina by its traditional nickname of the Nuisance and Disturber). He's clearly upset at having joined what looked like an important and fruitful avenue of research, only to find out - rather quickly - that it was based on sloppy, poorly-characterized results. And I think what really has him furious is that the originators of the idea (Feldheim and Eaton) have tried, all these years, to carry on as if nothing was wrong.

I think, though, that Franzen is having his revenge whether he realizes it or not. It's coming up on ten years now since the original RNA nanocrystal paper. If this work were going to lead somewhere, you'd think that it would have led somewhere by now. But it doesn't seem to be. The whole point of the molecular-biology-meets-materials-science aspect of this idea was that it would allow a wide variety of new materials to be made quickly, and from the looks of things, that just hasn't happened. I'll bet that if you went back and looked up the 2005 grant application for the Keck foundation that Eaton, Feldheim (and at the time, Franzen) wrote up, it would read like an alternate-history science fiction story by now.

Comments (14) + TrackBacks (0) | Category: Chemical News | Press Coverage | The Dark Side | The Scientific Literature

January 16, 2014

Should Drug Industry Research All Get Rejected For Publication?

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Posted by Derek

If you work in the drug industry, and for some reason you feel that your blood pressure isn't quite high enough today, a look at this debate at the British Medical Journal should fix that up for you. "Should journals stop publishing research funded by the drug industry?" is the title - there, doesn't that constrict your blood vessels already?

Taking the "Yes, they should" side are Richard Smith (former editor of the journal, now with a British organization called "Patients Know Best", and Peter C. Gøtzsche of the Nordic Cochrane Center. Here's their opening statement, and Gøtzsche's recent opinion piece in the same journal is a good harbinger, as it turns out:

The BMJ and its sibling journals have stopped publishing research funded by the tobacco industry for two main reasons: the research is corrupted and the companies publish their research to advance their commercial aims, oblivious of the harm they do. But these arguments apply even more strongly to research funded by the drug industry, and we suggest there is a better way to communicate the results of trials that would be safer for patients.

Prescribed drugs are the third leading cause of death, partly because of flaws in the evidence published in journals. We have long known that clinical trials funded by the drug industry are much more likely than publicly funded trials to produce results favourable to the company. The reason is obvious. The difference between an honest and a less than honest data analysis can be worth billions of euros, and the fraudulent trials of some cyclo-oxygenase-2 inhibitors for arthritis and selective serotonin reuptake inhibitors for depression are good examples

They're absolutely right about the financial motivations, and a first-rate moral hazard it is, too. But the comparison with the tobacco companies is a real pencil-snapper (as they no doubt intended it to be). They go on about prescription drugs being the "third largest cause of death", about "drug industry crimes", and so on. To be fair, and first let me brush these pencil fragments off my desk, the pharmaceutical companies have laid themselves wide open to these sorts of attacks, painting huge fluorescent bulls-eye targets on themselves again and again. But still.

This piece casually mentions that "olanzapine (Zyprexa), has probably caused 200 000 deaths", footnoting a book by one of the two authors. I seem to have missed that. Many antipsychotic drugs are associated with QT prolongation, which can lead to fatal heart arrythmias, but the worst of them have long been taken out of use. The FDA is investigating two deaths following injection of long-acting olanzapine, not two hundred thousand. Olanzapine has plenty of side effects, though, including weight gain (which can exacerbate Type II diabetes), and it has a warning label in the US about giving it to elderly patients under any conditions. But two hundred thousand deaths? I can't find any support for any such figure; it appears in Gøtzsche's book and apparently nowhere else, so citing it in this article as if it were a well-established fact is a nice move.

Taking the "No" side is Trish Groves of the BMJ itself. She rejects the analogy with the tobacco industry - as she should, because it's offensive and ridiculous. She goes on to detail the problems with industry-reported results and what the journal is doing about them. As opposed to the "Yes" side, it's a pretty reasonable piece. One of the things she mentions is that investigator-led trials have their own sources of bias. Very few people organizing an effort the size of a useful clinical trial will be disinterested in its results, unfortunately.

How much can we trust the evidence base for drugs in current use? It’s hard to tell, given the woeful legacy of widespread non-registration, non-publication, and selective reporting of clinical trials. Much of this reporting bias also applies to investigator led trials, and the many steps now being taken to mandate prospective trial registration, ensure reporting of all results, and access patient level data on interventions’ benefits and harms, as called for by the AllTrials campaign, must apply to them as much as to industry led trials. Moreover, new rules on transparency need to be applied retrospectively: laudable plans to provide access to data on new drugs aren’t enough.

That’s why the BMJ is keen to publish papers from the RIAT (Restoring Invisible and Abandoned Trials) initiative, through which academics who find previously unreported trials can write them up and publish them if the original investigators decline to do so. We also welcome “negative” trials that find no evidence of benefit, as long as their research questions are important and their methods robust, and we’re particularly interested in publishing trials of comparative effectiveness. Both these types of study can be much more useful to clinical practice than the placebo controlled trials that regulators demand. . .

It should be no great task to guess which side of this debate I favor - after all, I'm one of those evil drug company scientists who mow down the customers by the hundreds of thousands. I do wish that Groves' response had strayed a bit from the topic at hand and addressed those accusations of mass murder (that's what they are). I realize that it must be hard to tell a former editor to tone things down and go back for a rewrite. But still.

Comments (47) + TrackBacks (0) | Category: Clinical Trials | The Scientific Literature | Why Everyone Loves Us

January 7, 2014

How Much Is Wrong?

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Posted by Derek

Here's another take, from Jeff Leek at Simply Statistics, on the "How much published research is false?" topic. This one is (deliberately) trying to cut down on the alarm bells and flashing red lights.

Note that the author is a statistician, and the the arguments made are from that perspective. For example, the Amgen paper on problems with reproducibility of drug target papers is quickly dismissed with the phrase "This is not a scientific paper" (because it has no data), and the locus classicus of the false-research-results topic, the Ioannidis paper in PLoS Medicine, is seen off with the comment that "The paper contains no real data, it is purely based on conjecture and simulation."

I'll agree that we don't need to start assuming that everything is junk, as far as the eye can see. But I'm not as sanguine as Leek is, I think. Semi-anecdotal reports like the Amgen paper, the Bayer/Schering paper, and even scuttlebutt from Bruce Booth and the like are not statistically vetted scientific reports, true. But the way that they're all pointing in the same direction is suggestive. And it's worth keeping in mind that all of these parties have an interest in the answer being the opposite of what they're finding - we'd all like for the literature reports of great new targets and breakthroughs to be true.

The one report where Leek is glad about the mathematical underpinnings is the Many Labs project. But there's something about that that bothers me. The Many Labs people were trying to replicate results in experimental psychology, and while there's probably some relevance to the replications problems in biology and chemistry, there are big differences, too. I worry that everything is getting lumped together as Science, and if this part of Science is holding up, then those worries that people in other parts of Science have are probably ill-founded (after all, they don't have any real numbers, right?)

Comments (11) + TrackBacks (0) | Category: The Scientific Literature

January 2, 2014

It Just So Happens That I Have A Conference Right Here

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Posted by Derek

Here's a good addition to the "bogus conferences" file. The folks at Retraction Watch have the story of Navin Kabra, an Indian engineer who's blowing the whistle on a racket peculiar to that country.

There are apparently many universities in India that have a requirement that everyone attaining a certain degree has to have their work accepted at an "international conference". So. . .a number of "international conference" organizers have stepped up to fill that market niche, with hefty registration fees and talk of rigorous peer review and high standards. They do nothing of the kind, of course. People pay their cash, pay their own way to the conference, and get to present to a scattered audience of other people who've done the same thing. No one else shows up - why would anyone?

So Kabra sent them a manuscript full of gibberish and stretches of dialog from "My Cousin Vinny", and (you guessed it), the thing passed the brutal review process as soon as the cash appeared. After revealing his hoax, the paper seems to have been taken down from the conference web site, but up until then, it was available for interested scholars, or people interested in Joe Pesci and/or Marisa Tomei. As long as the universities pretend that everyone coming through their programs has done work that's fit to present, there will be people there who will pretend to hold conferences for them. The real losers are the students, many of whom apparently think that these are real meetings. How do you recognize the real thing if all you've ever been exposed to are the scams?

Comments (7) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

December 16, 2013

Top Chemical Publications of 2013

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Posted by Derek

From Organic Solution, here's a list of the top chemical papers of 2013. If I were to make my own list, some of the papers on this one would certainly overlap. Other people will have different ones, though, and I'd be glad to link to them as well - I'll update this post with any suggestions that come in for other selections.

Comments (8) + TrackBacks (0) | Category: The Scientific Literature

December 11, 2013

Down With the Luxury Journals?

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Posted by Derek

Nobel laureate Randy Schekman has stirred up a lot of controversy with his public declaration that he will send no more manuscripts to Nature, Science, Cell and such "luxury journals".

. . .The prevailing structures of personal reputation and career advancement mean the biggest rewards often follow the flashiest work, not the best. Those of us who follow these incentives are being entirely rational – I have followed them myself – but we do not always best serve our profession's interests, let alone those of humanity and society.

We all know what distorting incentives have done to finance and banking. The incentives my colleagues face are not huge bonuses, but the professional rewards that accompany publication in prestigious journals – chiefly Nature, Cell and Science.

These luxury journals are supposed to be the epitome of quality, publishing only the best research. Because funding and appointment panels often use place of publication as a proxy for quality of science, appearing in these titles often leads to grants and professorships. But the big journals' reputations are only partly warranted. While they publish many outstanding papers, they do not publish only outstanding papers. Neither are they the only publishers of outstanding research.

These journals aggressively curate their brands, in ways more conducive to selling subscriptions than to stimulating the most important research. Like fashion designers who create limited-edition handbags or suits, they know scarcity stokes demand, so they artificially restrict the number of papers they accept. The exclusive brands are then marketed with a gimmick called "impact factor". . .

The editorial staffs at these journals have been quick to point out that this is not necessarily a disinterested move, since Schekman is editor of eLife, a high-end open access journal. And no doubt some colleagues thought to themselves that it's much easier to abjure publication in the big journals after you've won your Nobel prize.

But there's a flip side to both those arguments. Scheckman is indeed editor of eLife, but that also means that he's willing to put his time and effort where his mouth is when he says that the current top-tier journals are a problem. And he's also willing to use his Nobelist profile in the service of that idea - many of the people complaining about how Scheckman is already famous would have produced no headlines at all had they announced that they would no longer publish in Nature. I seem to have taken that vow myself, at least so far in my career, without even realizing it.

Here's the response from Phillip Campbell at Nature Publishing Group. He says that he doesn't think it's helpful to mix the idea of open access with selectivity in publication, since open access is more of a business model. I see his point - there are selective open-access journals (like eLife), and there are nonselective ones, all the way down to the outright frauds. The same applies to the traditional journals, although the opportunities for fraud are not as lucrative. Campbell also decries the emphasis on impact factors, although the same objections can be made as with Scheckman, that it's easy for the editor of a high-impact-factor journal to play them down.

But impact factors really are pernicious. There will always be more- and less-presigious places to publish your research - any attempt to legislate otherwise is on a par with the creation of the New Soviet Man. But the advent of the impact factor gives everyone a lazy way to make the worst of it. It's especially tempting for people who don't even understand what someone else's research means, or might mean, but who have to judge them anyway. Why bother with the technical details? You have everything you need, to three idiotic decimal places, right there.

That actually sums up what I think about impact factors, although I've never put it quite so succinctly before: they're a moral hazard.

Update: more from Retraction Watch on the subject.

Comments (20) + TrackBacks (0) | Category: The Scientific Literature

December 6, 2013

Shop Up Some Gels For the Paper

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Posted by Derek

There have been many accusations over the years of people duplicating and fudging gels in biology papers. The Science-Fraud.org site made quite an impression with some of these, and there are others. But as in so many other fields, manual labor is giving way to software and automation.

Nature News has the story of an Italian company that has come up with an automated way of searching images in scientific papers for duplication. The first scalp has already been claimed, but how bad is the problem?

Now midway through the analysis, he estimates that around one-quarter of the thousands of papers featuring gels that he has analysed so far potentially breached widely accepted guidelines on reproducing gel images. And around 10% seem to include very obvious breaches, such as cutting and pasting of gel bands. Some journals were more affected than others, he says. Those with a high impact factor tended to be slightly less affected. He plans to publish his results.

I'll be happy to see the paper, and glad to see this sort of technique applied more broadly. I wonder if it can be adapted to published NMR spectra?

Comments (21) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

December 3, 2013

What You Can Publish After a Shamectomy

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Posted by Derek

The sleazy scientific publishing racket continues to plumb new depths in its well-provisioned submarine. Now comes word of "Stringer Open" - nope, not Springer Open, that one's a real publisher of real journals. This outfit is Stringer, which is a bit like finding a list of journals published by the American Comical Society. The ScholarlyOA blog noticed that the same person appears on multiple editorial boards across their various journals. When contacted, she turned out to be a secretary who's never heard of "Stringer". Class all the way. The journals themselves will be populated by the work of dupes and/or con artists - maybe some of those Chinese papers-for-rent can be stuffed in there to make a real lasagna of larceny out of the whole effort.

Comments (12) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

December 2, 2013

Authorship For Sale. Papers For Sale. Everything For Sale.

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Posted by Derek

Academic publishing fraud in China has come up here before, but Science has an in-depth look at the problem. And a big problem it is:

"There are some authors who don't have much use for their papers after they're published, and they can be transferred to you," a sales agent for a company called Wanfang Huizhi told a Science reporter posing as a scientist. Wanfang Huizhi, the agent explained, acts as an intermediary between researchers with forthcoming papers in good journals and scientists needing to snag publications. The company would sell the title of co–first author on the cancer paper for 90,000 yuan ($14,800). Adding two names—co–first author and co–corresponding author—would run $26,300, with a deposit due upon acceptance and the rest on publication. A purported sales document from Wanfang Huizhi obtained by Science touts the convenience of this kind of arrangement: "You only need to pay attention to your academic research. The heavy labor can be left to us. Our service can help you make progress in your academic path!"

For anyone who cares about science and research, this is revolting. If you care a lot more about climbing that slippery ladder up to a lucrative position, though, it might be just the thing, right? There are all sorts of people ready to help you realize your dreams, too:

The options include not just paying for an author's slot on a paper written by other scientists but also self-plagiarizing by translating a paper already published in Chinese and resubmitting it in English; hiring a ghostwriter to compose a paper from faked or independently gathered data; or simply buying a paper from an online catalog of manuscripts—often with a guarantee of publication.

Offering these services are brokers who hawk titles and SCI paper abstracts from their perches in China; individuals such as a Chinese graduate student who keeps a blog listing unpublished papers for sale; fly-by-night operations that advertise online; and established companies like Wanfang Huizhi that also offer an array of above-board services, such as arranging conferences and producing tailor-made coins and commemorative stamps. Agencies boast at conferences that they can write papers for scientists who lack data. They cold-call journal editors. They troll for customers in chat programs. . .

The journal contacted 27 agencies in China, with reporters posing as graduate students or other scientists, and asked about paying to get on a list of authors or paying to have a paper written up from scratch. 22 of them were ready to help with either or both. Many of these were to be placed in Chinese-language journals, but for a higher fee you could get into more international titles as well. Because of Chinese institutional insistence on high-impact-factor journal publications, people who can deliver that kind of publication can charge as much as a young professor's salary. (Since some institutions turn around and pay a bonus for such publications, though, it can still be feasible).

Some agencies claim they not only prepare and submit papers for a client: They furnish the data as well. "IT'S UNBELIEVABLE: YOU CAN PUBLISH SCI PAPERS WITHOUT DOING EXPERIMENTS," boasts a flashing banner on Sciedit's website.

One timesaver: a ready stock of abstracts at hand for clients who need to get published fast. Jiecheng Editing and Translation entices clients on its website with titles of papers that only lack authors. An agency representative told an undercover Science reporter that the company buys data from a national laboratory in Hunan province.

The article goes on to show that there are many Chinese scientists that are trying to do something about all this. I hope that they succeed, but it's going to take a lot of work to realign the incentives. Unless this happens, though, the Chinese-language scientific literature risks finding itself devolving into a bad joke, and papers from Chinese institutions risk having to go through extra levels of scrutiny when submitted abroad.

Comments (29) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

November 19, 2013

More on the Open Access Sting Article

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Posted by Derek

I wrote here about the recent article by John Bohannon in Science, where he submitted a clearly substandard article to a long list of open-access publishers. (The results reflected poorly on many of them). Now here's a follow-up interview with Bohannon at The Scholarly Kitchen, where he addresses many of the critiques of the piece. Well worth a read if this issue interests you.

Q: What has been the response of editors and publishers? Have any journals ceased publication? Have any editors/editorial board members resigned in protest? Do any of them blame you, personally, for the outcomes? Have any threats (legal or otherwise) been made towards you or Science Magazine as a result of the exposé?

A couple of weeks before the story was published, I contacted editors and publishers specifically named in the story. Their responses are printed in the article, ranging from falling on their own sword and accepting responsibility to blaming the publishers and claiming they were not involved with the journal. But since the story was published, editors and publishers have largely fallen silent.

One exception is an editor based in the Middle East who says that the sting has cost him his job. It pains me to hear that. But then again, he clearly wasn’t doing his job.

As far as I can tell, it has been business as usual for the 157 publishers that got stung. I know of only one fully confirmed closure of a journal (as reported in Retraction Watch). There have been statements by publishers that they intend to close a journal, but I’ll believe it when I see it.

Of course, closing a single journal is nothing but a pinprick for many of the publishers that accepted the fake paper. Most publish dozens–some, hundreds–of titles.

I was bracing myself for lawsuits and PR blitzes from the publishers and editors that got stung. Ironically, the attacks came instead from advocates of the open access movement.

Comments (24) + TrackBacks (0) | Category: The Scientific Literature

November 12, 2013

It Doesn't Repeat? Who's Interested?

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Posted by Derek

Nature Biotechnology is making it known that they're open to publishing studies with negative results. The occasion is their publication of this paper, which is an attempt to replicate the results of this work, published last year in Cell Research. The original paper, from Chen-Yu Zhang of Nanjing University, reported that micro-RNAs (miRNAs) from ingested plants could be taken up into the circulation of rodents, and (more specifically) that miRNA168a from rice could actually go on to modulate gene expression in the animals themselves. This was a very interesting (and controversial) result, with a lot of implications for human nutrition and for the use of transgenic crops, and it got a lot of press at the time.

But other researchers in the field were not buying these results, and this new paper (from miRagen Therapeutics and Monsanto) reports that they cannot replicated the Nanjing work at all. Here's their rationale for doing the repeat:

The naturally occurring RNA interference (RNAi) response has been extensively reported after feeding double-stranded RNA (dsRNA) in some invertebrates, such as the model organism Caenorhabditis elegans and some agricultural pests (e.g., corn rootworm and cotton bollworm). Yet, despite responsiveness to ingested dsRNA, a recent survey revealed substantial variation in sensitivity to dsRNA in other Caenorhabditis nematodes and other invertebrate species. In addition, despite major efforts in academic and pharmaceutical laboratories to activate the RNA silencing pathway in response to ingested RNA, the phenomenon had not been reported in mammals until a recent publication by Zhang et al. in Cell Research. This report described the uptake of plant-derived microRNAs (miRNA) into the serum, liver and a few other tissues in mice following consumption of rice, as well as apparent gene regulatory activity in the liver. The observation provided a potentially groundbreaking new possibility that RNA-based therapies could be delivered to mammals through oral administration and at the same time opened a discussion on the evolutionary impact of environmental dietary nucleic acid effects across broad phylogenies. A recently reported survey of a large number of animal small RNA datasets from public sources has not revealed evidence for any major plant-derived miRNA accumulation in animal samples. Given the number of questions evoked by these analyses, the limited success with oral RNA delivery for pharmaceutical development, the history of safe consumption for dietary small RNAs and lack of evidence for uptake of plant-derived dietary small RNAs, we felt further evaluation of miRNA uptake and the potential for cross-kingdom gene regulation in animals was warranted to assess the prevalence, impact and robustness of the phenomenon.

They believe that the expression changes that the original team noted in their rodents were due to the dietary changes, not to the presence of rice miRNAs, which they say that they cannot detect. Now, at this point, I'm going to exit the particulars of this debate. I can imagine that there will be a lot of hand-waving and finger-pointing, not least because these latest results come partly from Monsanto. You have only to mention that company's name to an anti-GMO activist, in my experience, to induce a shouting fit, and it's a real puzzle why saying "DeKalb" or "Pioneer Hi-Bred" doesn't do the same. But it's Monsanto who take the heat. Still, here we have a scientific challenge, which can presumably be answered by scientific means: does rice miRNA get into the circulation and have an effect, or not?

What I wanted to highlight, though, is another question that might have occurred to anyone reading the above. Why isn't this new paper in Cell Research, if they published the original one? Well, the authors apparently tried them, only to find their work rejected because (as they were told) "it is a bit hard to publish a paper of which the results are largely negative". That is a silly response, verging on the stupid. The essence of science is reproducibility, and if some potentially important result can't be replicated, then people need to know about it. The original paper had very big implications, and so does this one.

Note that although Cell Research is published out of Shanghai, it's part of the Nature group of journals. If two titles under the same publisher can't work something like this out, what hope is there for the rest of the literature? Congratulations to Nature Biotechnology, though, for being willing to publish, and for explicitly stating that they are open to replication studies of important work. Someone should be.

Comments (20) + TrackBacks (0) | Category: Biological News | The Scientific Literature

November 11, 2013

The Past Twenty Years of Drug Development, Via the Literature

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Posted by Derek

Here's a new paper in PlOSOne on drug development over the past 20 years. The authors are using a large database of patents and open literature publications, and trying to draw connections between those two, and between individual drug targets and the number of compounds that have been disclosed against them. Their explanation of patents and publications is a good one:

. . .We have been unable to find any formal description of the information flow between these two document types but it can be briefly described as follows. Drug discovery project teams typically apply for patents to claim and protect the chemical space around their lead series from which clinical development candidates may be chosen. This sets the minimum time between the generation of data and its disclosure to 18 months. In practice, this is usually extended, not only by the time necessary for collating the data and drafting the application but also where strategic choices may be made to file later in the development cycle to maximise the patent term. It is also common to file separate applications for each distinct chemical series the team is progressing.

While some drug discovery operations may eschew non-patent disclosure entirely, it is nevertheless common practice (and has business advantages) for project teams to submit papers to journals that include some of the same structures and data from their patents. While the criteria for inventorship are different than for authorship, there are typically team members in-common between the two types of attribution. Journal publications may or may not identify the lead compound by linking the structure to a code name, depending on how far this may have progressed as a clinical candidate.

The time lag can vary between submitting manuscripts immediately after filing, waiting until the application has published, deferring publication until a project has been discontinued, or the code name may never be publically resolvable to a structure. A recent comparison showed that 6% of compound structures exemplified in patents were also published in journal articles. While the patterns described above will be typical for pharmaceutical and biotechnology companies, the situation in the academic sector differs in a number of respects. Universities and research institutions are publishing increasing numbers of patents for bioactive compounds but their embargo times for publication and/or upload of screening results to open repositories, such as PubChem BioAssay, are generally shorter.

There are also a couple of important factors to keep in mind during the rest of the analysis. The authors point out that their database includes a substantial number of "compounds" which are not small, drug-like molecules (these are antibodies, proteins, large natural products, and so on). (In total, from 1991 to 2010 they have about one million compounds from journal articles and nearly three million from patents). And on the "target" side of the database, there are a significant number of counterscreens included which are not drug targets as such, so it might be better to call the whole thing a compound-to-protein mapping exercise. That said, what did they find?
compounds%20targets%20year%20chart.png
Here's the chart of compounds/target, by year. The peak and decline around 2005 is quite noticeable, and is corroborated by a search through the PCT patent database, which shows a plateau in pharmaceutical patents around this time (which has continued until now, by the way).

Looking at the target side of things, with those warnings above kept in mind, shows a different picture. The journal-publication side of things really has shown an increase over the last ten years, with an apparent inflection point in the early 2000s. What happened? I'd be very surprised if the answer didn't turn out to be genomics. If you want to see the most proximal effect of the human genomics frenzy from around that time, there you have it in the way that curve bends around 2001. Year-on-year, though (see the full paper for that chart), the targets mentioned in journal publications seem to have peaked in 2008 or so, and have either plateaued or actually started to come back down since then. Update: Fixed the second chart, which had been a duplicate of the first).
targets%20source%20year.png
The authors go on to track a number of individual targets by their mentions in patents and journals, and you can certainly see a lot of rise-and-fall stories over the last 20 years. Those actual years should not be over-interpreted, though, because of the delays (mentioned above) in patenting, and the even longer delays, in some cases, for journal publication from inside pharma organizations.

So what's going on with the apparent decline in output? The authors have some ideas, as do (I'm sure) readers of this site. Some of those ideas probably overlap pretty well:

While consideration of all possible causative factors is outside the scope of this work it could be speculated that the dominant causal effect on global output is mergers and acquisition activity (M&A) among pharmaceutical companies. The consequences of this include target portfolio consolidations and the combining of screening collections. This also reduces the number of large units competing in the production of medicinal chemistry IP. A second related factor is less scientists engaged in generating output. Support for the former is provided by the deduction that NME output is directly related to the number of companies and for the latter, a report that US pharmaceutical companies are estimated to have lost 300,000 jobs since 2000. There are other plausible contributory factors where finding corroborative data is difficult but nonetheless deserve comment. Firstly, patent filing and maintenance costs will have risen at approximately the same rate as compound numbers. Therefore part of the decrease could simply be due to companies, quasi-synchronously, reducing their applications to control costs. While this happened for novel sequence filings over the period of 1995–2000, we are neither aware any of data source against which this hypothesis could be explicitly tested for chemical patenting nor any reports that might support it. Similarly, it is difficult to test the hypothesis of resource switching from “R” to “D” as a response to declining NCE approvals. Our data certainly infer the shrinking of “R” but there are no obvious metrics delineating a concomitant expansion of “D”. A third possible factor, a shift in the small-molecule:biologicals ratio in favour of the latter is supported by declared development portfolio changes in recent years but, here again, proving a causative coupling is difficult.

Causality is a real problem in big retrospectives like this. The authors, as you see, are appropriately cautious. (They also mention, as a good example, that a decline in compounds aimed at a particular target can be a signal of both success and of failure). But I'm glad that they've made the effort here. It looks like they're now analyzing the characteristics of the reported compounds with time and by target, and I look forward to seeing the results of that work.

Update: here's a lead author of the paper with more in a blog post.

Comments (22) + TrackBacks (0) | Category: Drug Development | Drug Industry History | Patents and IP | The Scientific Literature

October 22, 2013

ACSNano on Problematic Papers

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Posted by Derek

The editorial board at ACSNano has come out with a statement on how they'd like problematic papers to be handled. This, the article most pointedly does not say, is surely a response to the controversy over a recent (ridiculously Photoshopped) paper that appeared in the journal. That one didn't make anyone look good, and I can see why the editors felt that they had to make an effort.

The piece is superficially reasonable. They're asking that if someone sees a paper with questionable content, that they should contact the journal first, which I think is good practice in any case. But then we have this:

In the end, a decision will be made, ranging from notification that no cause was found to support the accusations made, corrections to a published article, retraction of the article, and/or to notifying the authors’ institutions of such actions. At ACS Nano, we take scientific fraud seriously and, as needed, retract articles and place sanctions on authors for set numbers of years, including bans on further submissions. The difference between this formalized accusation investigation and reports in blogs or on Twitter is that, during the investigation, the authors of the article under dispute have a fair chance to explain, and the decisions are made by known experts in the field. After we have made our decision, all are welcome to comment on it in any blog, even if they have different opinions; this is their privilege. We strongly suggest that such comments be made without the cloak of anonymity, using real names and affiliations, so that direct and open discussion of the work can be understood by others.

While we appreciate readers being critical and thus helping to weed out incorrect or fraudulent manuscripts, we still should not consider each publication from a competitor as being potentially wrong. A climate of mistrust will not help anyone and will only hamper honest scientists, which are the great majority of our community. Researchers make their reputations by publishing excellent data, not by being whistleblowers with mixed records of accuracy. It is easy to criticize the work of others, but it is substantially harder to achieve something by oneself. In other words, be critical, but never forget to be fair. One can be competitive, but still friends with colleagues, who naturally are also in some ways competitors. We are all humans, and we should never forget the human touches in our work.

So no one is supposed to comment until the editors have made a decision, no matter how long that might take? Desirable or not, I don't see that happening. Look, a scientific paper, once published out on the flippin' internet, is open to comment from whoever wishes to read it. That's what it's there for, to be made use of as its readers find appropriate. I tend to think that a more wide-open discussion of the merits of articles (or their lack of same) is actually good for the field. It should spur people on to write better papers, and put a bit more fear into those who might be tempted to fake things up.

I realize that people are afraid of libel, of character assassination, and so on. But arguing over the details of scientific publications does not lend itself to those activities very easily, although it's certainly true that there are plenty of folks out there who would not above that sort of thing if they thought they could get away with it. But these misdeeds are rather transparent, for the most part, and can just end up making the accusers themselves look foolish. They get the same kind of scrutiny as everyone else. (And besides, don't the sorts of people who really get into that stuff have a significant overlap with the sorts who would fake their papers?) I don't see this as mistrust - I see it as science. If your results are firm, they should be able to stand up to some shaking. If they can't, well, everyone should know about it. If you accuse someone mistakenly, well, you yourself should be ready to take the consequences of that, too. On the other hand, assuming (as the ACSNano piece seems to assume) that anyone with complaints about a paper must be a disgruntled competitor seems be a rather mistrustful way to look at things, too.

That second paragaph above, with its "play nice" advice, should be read while glancing at the "nanorod" photos from that recent paper. Try to reconcile the high-minded tone with what you see, and see if you have any better luck than I did.

Comments (62) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

October 17, 2013

The Reproducibility Initiative is Open

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Posted by Derek

Looks like the Reproducibility Initiative might be getting off the ground. This press release from the Center for Open Science says that they have a $1.3 million grant to start validating high-profile results in the oncology research literature. This will be done through the Science Exchange site, with results freely available to all comers.

I'm happy to see something like this coming together, but I don't know how far that money's going to go. The press release talks about 50 key papers that they'd like to reproduce, and I don't see how 1.3 million dollars will be enough to get through that list. (Is there a list of the papers anywhere? I can't find it). Some of the key tests will be relatively quick and cheap, but not all of them. But I agree with the COS that one of the important things here is to get this idea out into the real world, to get people used to it, and to establish it as useful. If they pick their targets carefully, the money should allow that to happen.

Comments (9) + TrackBacks (0) | Category: Cancer | The Scientific Literature

October 16, 2013

Holding Back Experimental Details, With Reason

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Posted by Derek

There's a lot of worry these days about the reproducibility of scientific papers (a topic that's come up here many times). And there's reason to believe that the sharing of data, protocols, and materials is not going so well, either.

. . . authors seem less willing to share these additional details about their study protocols than they have been in the past, according to a survey of 389 authors who published studies in the Annals of Internal Medicine. The findings, presented on 9 September at the International Congress on Peer Review and Biomedical Publication in Chicago, found that over the five years studied the percentage saying they would be willing to do so has dropped from almost 80% to only 60%.

A lack of incentives for sharing might be partly to blame. “There's no recognition, no promotion and no profit for scientists who share more information,” says Steven Goodman, a clinical research expert at Stanford University School of Medicine in California, who was part of the team that evaluated the survey results.

But there are two new papers out that deliberately does not share all the details, and it's not hard to see why. This NPR report has the background, but the abstract from the first paper will be enough for anyone in the field:

Clostridium botulinum strain IBCA10-7060, isolated from a patient with infant botulism, produced botulinum neurotoxin type B (BoNT/B) and another BoNT that, by use of the standard mouse bioassay, could not be neutralized by any of the Centers for Disease Control and Prevention–provided monovalent polyclonal botulinum antitoxins raised against BoNT types A–G.

That's not good. Until an antitoxin is available, the sequence of this new neurotoxin will not be published, although the fact of its existence is certainly worth knowing. The Journal of Infectious Diseases has two editorial articles on the issues that this work raises:

(The) identification of a novel, eighth botulinum neurotoxin (BoNT) from a patient with botulism expands our understanding of Clostridium botulinum and BoNT diversity, C. botulinum evolution, and the pathogenesis of botulism, but it also reveals a significant public health vulnerability. This new toxin, BoNT/H, cannot be neutralized by any of the currently available antibotulinum antisera, which means that we have no effective treatment for this form of botulism. Until anti-BoNT/H antitoxin can be created, shown to be effective, and deployed, both the strain itself and the sequence of this toxin (with which recombinant protein can be easily made) pose serious risks to public health because of the unusually severe, widespread harm that could result from misuse of either [3]. Thus, the dilemma faced by these authors, and by society, revolves around the question, should all of the information from this and similar studies be fully disseminated, motivated by the desire to realize all possible benefits from the discovery, or should dissemination of some or all of the information be restricted, with the goal of diminishing the probability of misuse?

I think they've made the right call here. (Last year's disputes about publishing work on a new strain of influenza are in just the same category.) Those studying botulin toxins need to know about this discovery, but given the molecular biology tools available to people, publishing the sequence (or making samples of the organism available) would be asking for potentially major trouble. This, unfortunately, seems to me to be an accurate reading of the world that we find ourselves in. There is a point where the value of having the knowledge out there is outweighed by the danger of. . .having the knowledge out there. This is going to be a case-by-case thing, but we should all be ready for some things to land on this side of the line.

Comments (14) + TrackBacks (0) | Category: Infectious Diseases | The Dark Side | The Scientific Literature

October 4, 2013

An Open Access Trash Heap

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Posted by Derek

Science magazine and writer John Bohannon have done us all a favor. There's a long article out in the latest issue that details how he wrote up a terrible, ridiculous scientific manuscript, attached a made-up name to it under the aegis of a nonexistent institution, and sent this farrago off to over three hundred open-access journals. The result?

On 4 July, good news arrived in the inbox of Ocorrafoo Cobange, a biologist at the Wassee Institute of Medicine in Asmara. It was the official letter of acceptance for a paper he had submitted 2 months earlier to the Journal of Natural Pharmaceuticals, describing the anticancer properties of a chemical that Cobange had extracted from a lichen.

In fact, it should have been promptly rejected. Any reviewer with more than a high-school knowledge of chemistry and the ability to understand a basic data plot should have spotted the paper's short-comings immediately. Its experiments are so hopelessly flawed that the results are meaningless.

I know because I wrote the paper. Ocorrafoo Cobange does not exist, nor does the Wassee Institute of Medicine. Over the past 10 months, I have submitted 304 versions of the wonder drug paper to open-access journals. More than half of the journals accepted the paper, failing to notice its fatal flaws. Beyond that headline result, the data from this sting operation reveal the contours of an emerging Wild West in academic publishing.

Well, sure, you're saying. Given the sorts of lowlife publishers out there, of course they took it, as long as the check cleared. But it's even worse than it appears:

Acceptance was the norm, not the exception. The paper was accepted by journals hosted by industry titans Sage and Elsevier. The paper was accepted by journals published by prestigious academic institutions such as Kobe University in Japan. It was accepted by scholarly society journals. It was even accepted by journals for which the paper's topic was utterly inappropriate, such as the Journal of Experimental & Clinical Assisted Reproduction.

Here's all the documentation, and it documents a sorry state indeed. You'll note from the world map in that link that India glows like a fireplace in this business. Nigeria has a prominence that it does not attain in the legitimate science publishing world, and there are exotic destinations like Oman and the Seychelles to be had as well. The editors of these "journals" tend to be people you've never heard of from universities that you didn't even know existed. And the editorial boards and lists of reviewers have plenty of those folks, mixed in with people who reviewed one paper before they didn't know better, and with people who didn't realize that their names were on the mastheads at all.

Bohannon didn't actually submit the exact same manuscript to all 304. He generated mix-and-match versions using an underlying template, giving him variations of the same crap and taking great care that the resulting papers should be obviously flawed:

he papers describe a simple test of whether cancer cells grow more slowly in a test tube when treated with increasing concentrations of a molecule. In a second experiment, the cells were also treated with increasing doses of radiation to simulate cancer radiotherapy. The data are the same across papers, and so are the conclusions: The molecule is a powerful inhibitor of cancer cell growth, and it increases the sensitivity of cancer cells to radiotherapy.

There are numerous red flags in the papers, with the most obvious in the first data plot. The graph's caption claims that it shows a "dose-dependent" effect on cell growth—the paper's linchpin result—but the data clearly show the opposite. The molecule is tested across a staggering five orders of magnitude of concentrations, all the way down to picomolar levels. And yet, the effect on the cells is modest and identical at every concentration.

One glance at the paper's Materials & Methods section reveals the obvious explanation for this outlandish result. The molecule was dissolved in a buffer containing an unusually large amount of ethanol. The control group of cells should have been treated with the same buffer, but they were not. Thus, the molecule's observed "effect" on cell growth is nothing more than the well-known cytotoxic effect of alcohol.

The second experiment is more outrageous. The control cells were not exposed to any radiation at all. So the observed "interactive effect" is nothing more than the standard inhibition of cell growth by radiation. Indeed, it would be impossible to conclude anything from this experiment.

I like this - the paper looks superficially presentable, but if you actually read it, then it's worthless. And yes, I realize that I've described a reasonable fraction of the ones that actually get published, but this is a more egregious example. I hope. The protocol was that Bohannon submitted the paper, and if it was rejected outright, that was that. If any reply came back addressing the paper's flaws in any way, he had a version ready to send back with more stuff in it, but without fixing any of the underlying problems. And if the paper was accepted, at any point in the process, he sent the journal a note that they'd discovered a serious flaw in their work and had to withdraw the manuscript.

157 journals accepted the paper, and 98 rejected it. He'd submitted it to a further 49 journals from his original list, but at least 29 of those appeared to be out of the business entirely, and the other 20 still had the paper "under review". So of those 255 decisions, 149 of them looked as if they'd occurred with little or no review. For a rejection, that's not so bad - this is a perfect example of manuscript that should not even be sent out for review. But the acceptances, well. . .

The other 106 editorial decisions made with some review are problematic, too. 70% of these were acceptances. Even in the few cases (36 times out of 304) where the paper was actually reviewed, and the reviewers realized that something was wrong with it (as they should have), the paper was accepted by 16 journals anyway.

The Elsevier journal that took this heap of junk was Drug Invention Today, in case you're wondering. I've never heard of it, and now I know why. The Sage journal was the Journal of International Medical Research, so you can strike that one off your list, too, assuming that the name wasn't enough all by itself. Another big open-access publisher, Hindawi (they advertise on the back cover of Chemistry World in the UK) rejected the paper from two of its journals, much to their relief. Jeffrey Beall's list of predatory publishers came as as pretty accurate, as well it might.

The problems with all this are obvious. These people are ripping off their authors for whatever publication fees they can scam, and some of these authors are not in a position to afford the treatment they're getting. No doubt some subset of the people who send manuscripts to these places are cynically padding their publication lists. The "editors" of these things get to reap a little unearned prestige for their "efforts" as well, so the whole enterprise just adds to the number of self-inflated jackasses with padded reputations, and the world is infested with too many of those people already. But I'm sure that there's another subset of authors who don't realize that they're submitting their results into a compost pile, and being asked to pay for the privilege. The first group are contemptible; the second group is sad. None of it's good.

Comments (57) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

October 3, 2013

RSS Readers: An Update

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Posted by Derek

The topic of RSS feeds for keeping up with the scientific literature has come up around here several times, especially since the demise of Google Reader. I've been trying several of these out, and wanted to report back. The Old Reader looked promising, but they seem to have had trouble dealing with the influx of users, leading to a notice a couple of months back that they were basically closing the service off to new users. This now seems to have been walked back: if others have found that they've settled things down, it's still definitely worth a look. I tried Feedly for a while, but couldn't stand the way that it dealt with graphical abstracts, and it seemed to hang on me a bit too often. So now I'm evaluating NewsBlur, and so far, it's working well, and doing what I want it to do. Keep in mind that I'm not a big social-share-this-story guy when it comes to RSS - in fact, since I use it for work, I really can't be. I just need a way to deal with the continual geyser of scientific publication.

Comments (46) + TrackBacks (0) | Category: The Scientific Literature

October 2, 2013

Results From the JACS Challenge

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Posted by Derek

The first results are in for the "JACS Challenge" that I mentioned here the other day. It looks like people's picks did correlate with later citation counts, overall, but with some curious exceptions. Some things that looked as if they would have been referred to a lot weren't, such as a paper on solventless polymerization. And a paper on transition-metal catalyzed boron-nitrogen bond formation was only picked by two respondents, but has amassed 258 citations since it was published. For the most part, though, people tended to judge the past pretty well (here's the PDF with all the statistics, if you're interested).

Comments (5) + TrackBacks (0) | Category: The Scientific Literature

September 30, 2013

They'll Fake the Journal if You'll Fake the Papers

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Posted by Derek

The Economist has a disturbing article on the extent of academic publishing fraud in China. It's disturbing that it goes on so much, and should be disturbing that it's in The Economist:

DISGUISED as employees of a gas company, a team of policemen burst into a flat in Beijing on September 1st. Two suspects inside panicked and tossed a plastic bag full of money out of a 15th-floor window. Red hundred-yuan notes worth as much as $50,000 fluttered to the pavement below.

Money raining down on pedestrians was not as bizarre, however, as the racket behind it. China is known for its pirated DVDs and fake designer gear, but these criminals were producing something more intellectual: fake scholarly articles which they sold to academics, and counterfeit versions of existing medical journals in which they sold publication slots.

As China tries to take its seat at the top table of global academia, the criminal underworld has seized on a feature in its research system: the fact that research grants and promotions are awarded on the basis of the number of articles published, not on the quality of the original research. . .

If there's one thing that economists are sure of, it's that you get what you subsidize (even if you might not have realized up front just what it was you were paying for). And if the Chinese establishment has decided that long publications lists are necessary, then long publication lists they shall have. The same thing happens in a drug research department when management is so foolish as to reward people for sheer number of compounds submitted - you get a deluge of amides, sulfonamides, and methyl-ethyl-butyl-futile coupling reactions. One half of the stockroom gets mixed with the other half, in the presence of HATU and/or palladiu, and voila, productivity on a shingle.

At least those are real componds. Apparently, many of the papers being generated under the Chinese onslaught are not just repetitious, bite-sized chunklets of stretched-out lab results, but flat-out fantasies:

The pirated medical-journal racket broken up in Beijing shows that there is a well-developed market for publication beyond the authentic SCI journals. The cost of placing an article in one of the counterfeit journals was up to $650, police said. Purchasing a fake article cost up to $250. Police said the racket had earned several million yuan ($500,000 or more) since 2009. Customers were typically medical researchers angling for promotion.

And this makes you wonder how many of the people doing the evaluating also knew, or suspected, that these journals were fakes, but had reasons of their own to pretend otherwise. Something needs to be done about all this, clearly, but that's not going to be possible without a lot of disruption. The longer it goes on, though, the worse that disruption might be. . .

Comments (21) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

September 26, 2013

An Unknown Author With Someone Else's Work. Why?

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Posted by Derek

Here's a bizarre one: someone apparently faked up a bunch of author names and contact information, and published results (in Biochemical and Biophysical Research Communications) that they're heard Bruce Spiegelman of Harvard talk about. The motive? Well. . .the only thing that makes sense is sheer vituperativeness, and even that doesn't make much. Here's the story - see if you can make sense of it!

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September 23, 2013

What's An Important Paper? Take the JACS Challenge!

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Posted by Derek

Here's a darn good question: how good are we at telling (when they're published) what scientific papers are important? We were talking around here the other day about famous work that had been rejected, and this is the less dramatic aspect of the same phenomenon.

At ScienceGeist, they're putting this to an empirical test. Given a ten-year-old issue of the Journal of the American Chemical Society, could a person predict which papers in it have had the most impact? Well, here's the issue, and here's the survey to take after you've looked it over. Please don't cheat by looking up citation counts or the like - approach this one cold and use your mighty scientific intuition. I'll be putting my own answers in later this morning. I look forward to seeing the results!

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September 17, 2013

Thoughts on the Scientific Publishing Model, And Its Inverse

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Posted by Derek

I mentioned the idea of an Elsevier boycott here last year. Here's someone who's thought about another course of action: if you can't beat 'em, join 'em - up to a point:

How about this for a solution:

1. We start a (say) monthly journal.

2. Set up a simple, lucrative payment for accepted articles. As a first stab, how about $10,000 paid personally to the researchers responsible. Similarly, each reviewer receives $2,000 for each article reviewed.

I imagine this would be enough to attract some serious submissions. So serious, in fact, that universities and libraries would be obliged to subscribe (at drastically reduced prices). Oh yeah, and you can only submit articles if you or your institution is a subscriber.

So every month hundreds of thousands of dollars would be distributed to scientists, and there would be a monthly prize pool for excellent research. And I bet the journal would be a cracking read (or as cracking as stiff scientific prose ever is, anyway).

But why not take it a step further.

3. Assuming, of course, you executed that first step and attracted some worthwhile research, you could simply distribute all of the profits. So if you attracted 5% of the market… say 50% penetration at half price, you would be able to distribute 250m a year (I know, I know).

I imagine a star researcher would prefer to get paid $200k rather than submit to Nature. And as the quality of the new journal improved, it could even end up becoming more prestigious.

The first problem I have with this, and it's a big one, is that if you're giving "drastically reduced" subscription prices to libraries and universities, where are all the profits coming from that you're using to pay the authors? I believe that squeezing institutional subscribers is, in fact, the business model for many of the scientific publishers. A second difficulty (there are others, too) is that our current system already encourages people to divide publications up into smaller units and get a longer list of papers to their name. If there's sill more incentive to publish (cash rewards!), I can imagine this problem only getting worse.

The general rule in nonscientific publishing, that "money flows towards the author", is based on a market that pays for the finished products voluntarily, and has the option of not reaching into its collective pocket at all. Publishers are also free to pick and choose among the many, many manuscript opportunities they're offered, trying to find those that they think will provide a return on their own investments of time and money.

Scientific publishing is a different undertaking, with a mixed set of motivations. We're publishing our results to show what we've accomplished, and to add to the storehouse of human knowledge (as opposed, say, to adding to the storehouse of human romance novels or slow-cooker chicken recipe compendia). We're also publishing to make ourselves look better, to our current employers and to potential future ones, not that such publications are a very efficient way to do that, but still. And the readers are keeping up with the published matter partly out of a desire to learn about what we have to say, and partly out of professional necessity.

Here's the thing: if it were not for the expense necessary to produce the journals, there would be no market involved at all. In the early days of science, results were distributed by personal correspondence, and journals are, in a way, just collections of such letters. Some of them, you'll notice, refer to that function by having "Letters" in their names. No one was paid to write those letters to their colleagues, and no one paid to receive them. The only expenses were the writing materials, the time it took for composition, and postage - just as the expenses now are the time and effort for composition (on the author's part) and the time and effort for editing, reviewing, and publishing (on the journal's part). These expenses have, in theory, been going down as fewer journals are published on pressed tree sheets and hauled around by mail trucks, but they cannot go to zero as long as there is editing involved, as well as commentary on the papers themselves and publicity for them, not to mention things like server maintenance, etc.

All the fights about the cost of scientific journals are fought on that narrow strip of ground. How much does it cost to do these things, and is it truly worth what people pay for them? Otherwise, we might all just as well upload everything into a central electronic archive, with a nominal fee to keep the hardware running. We'd then be back to sending letters around to let everyone else know when we've put in something that we think is hot stuff, or setting up web sites to get the news out. And some of those might become useful enough to start charging a subscription fee, and then. . .

Comments (16) + TrackBacks (0) | Category: The Scientific Literature

September 10, 2013

Great Papers That Have Been Rejected

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Posted by Derek

A discussion in the lab brought up this topic: there have been, so everyone hears, famous papers in the sciences that were rejected by the first journals that they were submitted to. I believe, for example, that Dan Schectman faced a lot of opposition to getting his first quasicrystal work published (and he certainly got a lot, notably from Linus Pauling, after it came out). To pick one, the original Krebs cycle paper was turned down by Nature, which a later editor called the journal's biggest single mistake. Here are some famous examples from computer science and related mathematics (update: in a parody/spoof paper!) and here's a discussion from an economist on this topic in his own field - I believe that the original Black-Scholes option pricing model paper was turned down as well.

If anyone has more examples to add from chemistry, I'd be glad to highlight them. I have some more thoughts on the subject that I'll expand into another post later on. . .

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September 9, 2013

What To Do About Chemistry Papers That Don't Work?

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I wanted to follow up on a point raised in the comments to this morning's post. Reader DJ writes that:

Our lab recently tried to repeat a procedure from a TL methodology paper on the amination of amines to make protected hydrazines. We noticed that the entire paper is wrong since the authors did not analyze the product NMRs carefully, and incorrectly assumed that they were forming the desired hydrazines, rather than the rearranged alkoxyamines. It's a systemic error throughout the paper that renders the entire premise and methodology essentially useless. So our quandry is this: (1) This is clearly not a case of fraud, but just bad science. (2) Our discovery is not all that interesting on its own, since the unusual reaction pathway has little practical value, and (3) the original report is from a TL paper that probably not many people will read in the first place. Still, I am tempted to do SOMETHING to correct the public record, but what? Maybe contact the original authors (somewhere in India)? Try to write a 'rebuttal style' paper in the same journal? Any suggestions?

That's a really good question. And I have a personal interest in it - no, I didn't write the hydrazine paper. I've recently tried to use a method in a paper from Chemical Communications that I cannot get to work. I gave it several tries, messing around with fresh reagents and so on, but I get nothing. In my case, I've written to the authors, and received no reply whatsoever. So, like DJ, I'm wondering what to do next. Writing to the authors is the first step that I recommend that he take, but he might well end up in the same situation I am.

So what next? Neither of these rise to a Blog-Syn level, I think, because just having half a dozen more people confirm that "Yeah, this stuff doesn't work" doesn't seem like a good use of people's time. (I think that Blog Syn efforts are better for reactions that work, but not as well as they're supposed to, because of some variables that aren't well worked out in the original papers). I'm not particularly interested in running a "Name and Shame" site for organic chemistry papers that can't be reproduced (and anyone who does will, I think, find themselves with a lot more work and many more headaches than they'd imagined). But what is there to do?

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Exposing Faked Scientific Papers

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Posted by Derek

Chemistry World has a good article on the problem of shaky data in journal article, and the intersecting problem of what to do about it in the chemistry blogging world. Paul Bracher's ChemBark is, naturally, a big focus of the piece, since he's been highlighting some particularly egregious examples in the last couple of months (which I've linked to from here).

The phrase "witch hunt" has been thrown around by some observers, but I don't think that's fair or appropriate. In great contrast to the number of witches around (and their effectiveness), faked information in published scientific articles is very much a real thing, and can have real consequences. Time spent looking for it and exposing it is not time wasted, not when it's at its current levels. But who should be doing the looking and the exposing?

The standard answer is "Why, journal editors and reviewers, who shouldn't be letting this stuff past in the first place". Quite true. But in many cases, they are letting it past, so what should be done once it's published? A quiet, gentlemanly note to the editorial staff? Or a big blazing row in a public forum, such as a widely-read blog? Even though I don't start many of these myself, I come down more on the side of the latter. There are problems with that stance, of course - you have to be pretty sure that there's something wrong before you go making a big deal out of it, for one thing. Hurting someone else's reputation for no reason would be a bad thing, as would damaging your own credibility by making baseless accusations.

But in some of these recent cases, there's been little doubt about the problem. Take that nanorod paper: the most common result when I showed to to people was "Oh, come on." (And the most common result when I showed the famous "Just make up an elemental" paper to people was "Oh, (expletive)", with several common words all filling in appropriately). So if there's clearly trouble with a published paper, why is it such a good thing to make a big public spectacle out of it?

Deterrence. I really think that there will be less of this if people think that there's a reasonable chance that fake science will be exposed widely and embarrassingly. Covering up half your NMR spectrum with a box of digital white-out is fraud and people committing fraud have given up their opportunity to be treated with respect. And don't forget, the whole deterrence argument applies to editors and reviewers, too. I can guarantee that many chemists looked at these recent examples and wondered if they would have let these papers go through the review process, through carelessness or lack of time, and resolved to do better the next time. I certainly did.

That said, I do not intend to make this blog the full-time scourge of the chemical literature by patrolling the literature myself. If I see something suspicious, I'll speak up about it, and if other chemistry blogs (or readers) pick up on something, I'm very glad to hear about it or link to it. But finding these examples is a perfect example of something that I think is best left to the crowd. The person best equipped to discover a fraudulent paper is the person who is interested in its subject and would like to build on its results - in other words, the person who would be most harmed by it. And if someone fakes a paper, but no one ever reads it or refers to it, well, that's the author's own reward, and I hope that they enjoy it.

Comments (24) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

August 30, 2013

Welcome to the Author's Brain. The "Fasten Seatbelts" Sign Is Illuminated

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Posted by Derek

Well, it's the Friday before a long holiday weekend here in the US, so I don't know if this is the day for long, detailed posts. I do have some oddities in the queue, though, so this is probably a good day to clear them out.

For starters, here's one in the tradition of the (in)famous Andrulis "gyre" paper. Another open-access publisher (SAGE) has an unusual item in their journal Qualitative Inquiry. (Some title, by the way - you could guess for days about what might appear under that category). The paper's title gets things off to a fine start: "Welcome to My Brain". And the abstract? Glad you asked:

This is about developing recursive, intrinsic, self-reflexive as de-and/or resubjective always evolving living research designs. It is about learning and memory cognition and experiment poetic/creative pedagogical science establishing a view of students ultimately me as subjects of will (not) gaining from disorder and noise: Antifragile and antifragility and pedagogy as movements in/through place/space. Further, it is about postconceptual hyperbolic word creation thus a view of using language for thinking not primarily for communication. It is brain research with a twist and becoming, ultimately valuation of knowledges processes: Becoming with data again and again and self-writing theory. I use knitting the Möbius strip and other art/math hyperbolic knitted and crocheted objects to illustrate nonbinary . . . perhaps. Generally; this is about asking how-questions more than what-questions.

Right. That's word-for-word, by the way, even though it reads as if parts of speech have been excised. Now, I do not, sadly, have access to journals with the kind of reach that Qualitative Inquiry displays, so I have not attempted to read the whole text. But the abstract sounds either like a very elaborate (and unenlightening) word game, or the product of a disturbed mind. The Neurobonkers blog, though, has some more, and it definitely points toward the latter:

This article is therefore about developing recursive intrinsic self-reflexive as de- and/or resubjective always evolving living research designs. Inquiry perhaps full stop—me: An auto-brain—biography and/or a brain theo­rizing itself; me theorizing my brain. It is thus about theo­rizing bodily here brain and transcorporeal materialities, in ways that neither push us back into any traps of biological determinism or cultural essentialism, nor make us leave bodily matter and biologies behind.

Apprarently, most of the manuscript is taken up with those "This is about. . ." constructions, which doesn't make for easy reading, either. At various points, a being/character called "John" makes appearances, as do recurring references to knitting and to Möbius strips. Brace yourselves:

Knitting John, John knitting. Knitting John Möbius. Möbius knitting John. Giant Möbius Strips have been used as conveyor belts (to make them last longer, since “each side” gets the same amount of wear) and as continuous-loop recording tapes (to double the playing time). In the 1960’s Möbius Strips were used in the design of versatile electronic resistors. Freestyle skiers have named one of their acrobatic stunts the Möbius Flip. The wear and tear of my efforts. My stunts, enthusiasm knitting. My brain and doubling and John.

OK, that's deranged. And how could anyone at SAGE have possibly reviewed it? This is the same question that came up with the MDPI journals and the Andrulis paper - five minutes with this stuff and you feel like calling up the author and telling them to adjust their dosages (or perhaps like adjusting yours). This sort of thing is interesting in a roadside-accident sort of way, but it also calls open-access publishing into disrepute. Maybe it's time for not only a list of predatory publishers, but a list of nonpredatory ones that freely admit garbage.

Comments (43) + TrackBacks (0) | Category: The Scientific Literature

August 27, 2013

Not Sent Out For Review

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Posted by Derek

Blogger Pete over at Fragment-Based Drug Discovery has a tale to tell about trying to get a paper published. He sent in a manuscript on alkane/water partition coefficients to the Journal of Chemical Information and Modeling, only to get back the "not sent out for review" response. That's the worst, the "We're not even going to consider this one" letter. And the odd thing is that, as he rightly put it, this does sound like a JCIM sort of paper, but the editor's response was that it was inappropriate for the journal, and that they had "limited interest" in QSAR/QSPR studies.

So off the paper went to the Journal of Computer-Aided Molecular Design. But as it was going to press, what should appear in JCIM but a paper on. . .alkane/water partition coefficients. There follows some speculation on how and why this happened, and if further details show up, I'll report on them.

But the whole "not sent out for review" category is worth thinking about. I'd guess that most papers that fall into that category truly deserve to be there - junk, junk that's written impossibly and impenetrably poorly, things that should have been sent to a completely different journal. These are the scientific equivalent of Theresa Nielsen Hayden's famous Slushkiller post, about the things that show up unsolicited at a publisher's office. If you're editing a science fiction magazine, you might be surprised to get lyric poetry submissions in another language, or biographical memoirs about growing up in Nebraska - but you'd only be surprised, apparently, if you'd never edited a science fiction magazine before (or any other kind).

But a journal editor can consign all sorts of papers to the outer darkness. At some titles, just getting a manuscript sent out to the referees is an accomplishment, because the usual response is "Stop wasting our time" (albeit not in those exact words, not usually). An author isn't going to be surprised in those cases, but getting that treatment at a less selective journal is more problematic.

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August 15, 2013

Big Pharma And Its Research Publications

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Posted by Derek

A longtime reader sent along this article from the journal Technological Forecasting and Social Change, which I'll freely admit never having spent much time with before. It's from a team of European researchers, and it's titled "Big Pharma, little science? A bibliometric perspective on Big Pharma's R&D decline".

What they've done is examine the publication record for fifteen of the largest drug companies from 1995 to 2009. They start off by going into the reasons why this approach has to be done carefully, since publications from industrial labs are produced (and not produced) for a variety of different reasons. But in the end:

Given all these limitations, we conclude that the analysis of publications does not in itself reflect the dynamics of Big Pharma's R&D. However, at the high level of aggregation we conduct this study (based on about 10,000 publications per year in total, with around 150 to 1500 publications per firm annually) it does raise interesting questions on R&D trends and firm strategies which then can be discussed in light of complementary quantitative evidence such as the trends revealed in studies using a variety of other metrics such as patents and, as well as statements made by firms in statutory filing and reports to investors.

So what did they find? In the 350 most-represented journals, publications from the big companies made up about 4% of the total content over those years (which comes out to over 10,000 papers). But this number has been dropping slightly, but steadily over the period. There are now about 9% few publications from Big Pharma than there were at the beginning of the period. But this effect might largely be explained by mergers and acquisitions over the same period - in every case, the new firm seems to publish fewer papers than the old ones did as a whole.

And here are the subject categories where those papers get published. The green nodes are topics such as pharmacology and molecular biology, and the blue ones are organic chemistry, medicinal chemistry, etc. These account for the bulk of the papers, along with clinical medicine.
Pharma%20global%20map%20of%20science.png
The number of authors per publication has been steadily increasing (in fact, even faster than the other baseline for the journals as a whole), and the organizations-per-paper has been creeping up as well, also slightly faster than the baseline. The authors interpret this as an increase in collaboration in general, and note that it's even more pronounced in areas where Big Pharma's publication rate has grown from a small starting point, which (plausibly) they assign to bringing in outside expertise.

One striking result the paper picks up on is that the European labs have been in decline from a publication standpoint, but this seems to be mostly due to the UK, Switzerland, and France. Germany has held up better. Anyone who's been watching the industry since 1995 can assign names to the companies who have moved and closed certain research sites, which surely accounts for much of this effect. The influence of the US-based labs is clear:

Although in most of this analysis we adopt a Europe versus USA comparative perspective, a more careful analysis of the data reveals that European pharmaceutical companies are still remarkably national (or bi-national as a results of mergers in the case of AstraZeneca and Sanofi-Aventis). Outside their home countries, European firms have more publications from US-based labs than all their non-domestic European labs (i.e. Europe excluding the ‘home country’ of the firm). Such is the extent of the national base for collaborations that when co-authorships are mapped into organisational networks there are striking similarities to the natural geographic distribution of countries. . .with Big Pharma playing a notable role spanning the bibliometric equivalent of the ‘Atlantic’.

Here's one of the main conclusions from the trends the authors have picked up:

The move away from Open Science (sharing of knowledge through scientific conferences and publications) is compatible and consistent with the increasing importance of Open Innovation (increased sharing of knowledge — but not necessarily in the public domain). More specifically, Big Pharma is not merely retreating from publication activities but in doing so it is likely to substitute more general dissemination of research findings in publications for more exclusive direct sharing of knowledge with collaboration partners. Hence, the reduction in publication activities – next to R&D cuts and lab closures – is indicative of a shift in Big Pharma's knowledge sharing and dissemination strategies.

Putting this view in a broader historical perspective, one can interpret the retreat of Big Pharma from Open Science, as the recognition that science (unlike specific technological capabilities) was never a core competence of pharmaceutical firms and that publication activity required a lot of effort, often without generating the sort of value expected by shareholders. When there are alternative ways to share knowledge with partners, e.g. via Open Innovation agreements, these may be attractive. Indeed an associated benefit of this process may be that Big Pharma can shield itself from scrutiny in the public domain by shifting and distributing risk exposure to public research organisations and small biotech firms.

Whether the retreat from R&D and the focus on system integration are a desirable development depends on the belief in the capacities of Big Pharma to coordinate and integrate these activities for the public good. At this stage, one can only speculate. . .

Comments (14) + TrackBacks (0) | Category: Academia (vs. Industry) | Drug Industry History | The Scientific Literature

August 14, 2013

Nanorods? Or Photoshop?

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Posted by Derek

If you haven't seen this, which goes into some very odd images from a paper in the ACS journal Nano Letters, then have a look. One's first impression is that this is a ridiculously crude Photoshop job, but an investigation appears to be underway to see if that's the case. . .

Update: the paper has now been withdrawn. The chemistry blogs get results!

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August 8, 2013

Make Up the Elemental Analysis: An Update

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Posted by Derek

Chemistry Blog has more on the incident picked up first at ChemBark and noted here yesterday. This rapidly-becoming-famous case has the Supporting Information file of a paper published at Organometallics seemingly instructing a co-author to "make up" an elemental analysis to put in the manuscript.

Now the editor of the journal (John Gladysz of Texas A&M) has responded to Chemistry Blog as follows:

Wednesday 07 August
Dear Friends of Organometallics,

Chemical Abstracts alerted us to the statement you mention,which was overlooked during the peer review process, on Monday 05 August. At that time, the manuscript was pulled from the print publication queue. The author has explained to us that the statement pertains to a compound that was ”downgraded” from something being isolated to a proposed intermediate. Hence, we have left the ASAP manuscript on the web for now. We are requiring that the author submit originals of the microanalysis data before putting the manuscript back in the print publication queue. Many readers have commented that the statement reflects poorly on the moral or ethical character of the author, but the broad “retribution” that some would seek is not our purview. As Editors, our “powers” are limited to appropriate precautionary measures involving future submissions by such authors to Organometallics, the details of which would be confidential (ACS Ethical Guidelines, http://pubs.acs.org/page/policy/ethics/index.html). Our decision to keep the supporting information on the web, at least for the time being, is one of transparency and honesty toward the chemical community. Other stakeholders can contemplate a fuller range of responses. Some unedited opinions from the community are available in the comments section of a blog posting: http://blog.chembark.com/2013/08/06/a-disturbing-note-in-a-recent-si-file/#comments

If you have any criticisms of the actions described above, please do not hesitate to share them with me. Thanks much for being a reader of Organometallics, and best wishes. . .

This is the first report of the corresponding author, Reto Dorta, responding about this issue (several other people have tried to contact him, with no apparent success). So much for the theory, advanced by several people in the comments section at ChemBark, that "make up" was being used in the British-English sense of "prepare". Gladysz's letter gets across his feelings about the matter pretty clearly, I'd say.

Comments (31) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

August 7, 2013

New Frontiers in Analytical Chemistry

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Posted by Derek

A reader sends this new literature citation along, from Organometallics. He directed my attention to the Supplementary Information file, page 12. And what do we find there?

. . .Solvent was then removed to leave a yellow residue in the vial, the remaining clear, yellow solution was concentrated to a volume of about 1ml, and diethyl ether was added in a dropwise manner to the stirred solution to precipitate a yellow solid. The vial was centrifuged so the supernatant solvent could be decanted off by Pasteur pipette. The yellow solid was washed twice more with ether and the dried completely under high vacuum to give 99mg (93% yield) of product.

Emma, please insert NMR data here! where are they? and for this compound, just make up an elemental analysis...

And don't forget to proofread the manuscript, either, while you're at it. Oops.

Update: I see that Chembark is on this one, and has gone as far as contacting the corresponding author, whose day has gotten quite a bit longer. . .

Comments (28) + TrackBacks (0) | Category: Analytical Chemistry | The Scientific Literature

July 16, 2013

Touching Up the Spectra

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Posted by Derek

Organic chemists have been taking NMR spectra for quite a while now. Routine use came on in the 1960s, and higher-field instruments went from exotic big-ticket items in the 1970s to ordinary equipment in the 1980s. But NMR can tell you more about your sample than you wanted to know (good analytical techniques are annoying that way). So what to do when you have those little peaks showing up where no peaks should be?

The correct answer is "Live with 'em or clean up your sample", but wouldn't it be so much easier and faster to just clean up the spectrum? After all, that's all that most people are ever going to see - right? This little line of thought has occurred to countless chemists over the years. Back In The Day, the technology needed to remove solvent peaks, evidence of isomers, and other pesky impurities was little more than a bottle of white-out and a pen (to redraw the lovely flat baseline once the extra peaks were daubed away). Making a photocopy of the altered spectrum gave you publication-ready purity in one easy step.

NMR spectra are probably the most-doctored of the bunch, but LC/MS and HPLC traces are very capable of showing you peaks you didn't want to see, either. These days there are all sorts of digital means to accomplish this deception, although I've no doubt that the white-out bottle is still deployed. In case anyone had any doubt about that, last month Amos Smith, well-known synthetic organic chemist and editor of Organic Letters, had this to say in a special editorial comment in the journal:

Recently, with the addition of a Data Analyst to our staff, Organic Letters has begun checking the submitted Supporting Information more closely. As a result of this increased scrutiny, we have discovered several instances where reported spectra had been edited to remove evidence of impurities.

Such acts of data manipulation are unacceptable. Even if the experimental yields and conclusions of a study are not affected, ANY manipulation of research data casts doubts on the overall integrity and validity of the work reported.

That it does. He went on to serve notice on authors that the journal will be checking, and will be enforcing and penalizing. And you can tell that Smith and the Org Lett staff have followed up on some of these already, because they've already had a chance to hear the default excuse:

In some of the cases that we have investigated further, the Corresponding Author asserted that a student had edited the spectra without the Corresponding Author’s knowledge. This is not an acceptable excuse! The Corresponding Author (who is typically also the research supervisor of the work performed) is ultimately responsible for warranting the integrity of the content of the submitted manuscript. . .

As the editorial goes on the say, and quite rightly, if a student did indeed alter the spectrum before showing it to the boss, it's very likely because the boss was running a group whose unspoken rule was that only perfection was acceptable. And that's an invitation to fraud, large and small. I'm glad to see statements like Smith's - the only ways to keep down this sort of data manipulation are to make the rewards for it small, increase the chances of it being found out, and make the consequences for it real.

As for those, the editorial speaks only of "significant penalties". But I have some ideas for those that might help people think twice about the data clean-up process. How about a special correction in the journal, showing the altered spectra, with red circles around the parts that had been flattened out? And a copy of the same to the relevant granting agencies and department heads? That might help get the message out, you think?

As an aside, I wanted to mention that I have seen someone stand right up and take responsibility for extra peaks in an NMR. Sort of. I saw a person once presenting what was supposed to be the final product's spectrum, only there were several other singlet peaks scattered around. "What are those?" came the inevitable question. "Water" was the answer. "Umm. . .how many water peaks, exactly?" "Oh, this one is water in solution. And this one is water complexed with the compound. And this one is water adsorbed to the inside of the NMR tube. And this one is water adsorbed to the outside of the. . ." It took a little while for order to be restored at that point. . .

Comments (38) + TrackBacks (0) | Category: Analytical Chemistry | The Dark Side | The Scientific Literature

July 9, 2013

Non-Reproducible Science: A Survey

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Posted by Derek

The topic of scientific reproducibility has come up around here before, as it deserves to. The literature is not always reliable, and it's unreliable for a lot of different reasons. Here's a new paper in PLOS ONE surveying academic scientists for their own experiences:

To examine a microcosm of the academic experience with data reproducibility, we surveyed the faculty and trainees at MD Anderson Cancer Center using an anonymous computerized questionnaire; we sought to ascertain the frequency and potential causes of non-reproducible data. We found that ~50% of respondents had experienced at least one episode of the inability to reproduce published data; many who pursued this issue with the original authors were never able to identify the reason for the lack of reproducibility; some were even met with a less than “collegial” interaction.

Yeah, I'll bet they were. It turns out that about half the authors who had been contacted about problems with a published paper responded "negatively or indifferently", according to the survey respondents. As to how these things make it into the literature in the first place, I don't think that anyone will be surprised by this part:

Our survey also provides insight regarding the pressure to publish in order to maintain a current position or to promote ones scientific career. Almost one third of all trainees felt pressure to prove a mentor's hypothesis even when data did not support it. This is an unfortunate dilemma, as not proving a hypothesis could be misinterpreted by the mentor as not knowing how to perform scientific experiments. Furthermore, many of these trainees are visiting scientists from outside the US who rely on their trainee positions to maintain visa status that affect themselves and their families in our country.

And some of these visiting scientists, it should be noted, come from backgrounds in authority-centered and/or shame-based cultures, where going to the boss with the news that his or her big idea didn't work is not a very appealing option. It's not for anyone, naturally, but it's especially hard if you feel that you're contradicting the head of the lab and bringing shame on yourself in the process.

As for what to do about all this, the various calls for more details in papers and better reviewing are hard to complain about. But while I think that those would help, I don't see them completely solving the problem. This is a problem of human nature; as long as science is done by humans, we're going to have sloppy work all the way up to outright cheating. What we need to do is find ways to make it harder to cheat, and less rewarding - that will at least slow it down a bit.

There will always be car thieves, too, but we don't have to make it easy for them, either. Some of our publishing practices, though, are the equivalent of habitually walking away with the doors unlocked and the keys in the ignition. Rewarding academic scientists (at all levels) so directly for the number of their publications is one of the big ones. Letting big exciting results through without good statistical foundations is another.

In this vein, a reader sends along the news that the Reproducibility Initiative is now offering grants for attempts to check big results in the literature. That's the way to get it done, and I'm glad to see some money forthcoming. This effort is concentrating on experimental psychology, which is appropriate, given that the field has had some recent scandals (follow-up here) and is now in a big dispute over the reproducibility of even its honestly-meant data. They need all the help they can get over there - but I'll be glad to see some of this done over here in the biomedical field, too.

Comments (16) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

July 8, 2013

19 Years to a Retraction. Bonus Midnight Camera Footage Included.

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Posted by Derek

This Retraction Watch post details the longest correction/retraction saga I've heard of yet. A 1994 paper in Nature has finally been pulled back, after years and years of wrangling. And by "wrangling" I mean multiple attempted repeats, blinded samples, fraught exchanges over scientific ethics with one of the most high-profile professors in the Czech Republic and hidden camera footage from the lab freezer. Yep, it got to that point - midnight break-ins to alter the stored samples. Read the post for more; it's really something.

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June 24, 2013

How Robust Is That New Reaction, Anyway?

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Posted by Derek

Here's a paper in Nature Chemistry that addresses something that isn't explicitly targeted as often as it should be: the robustness of new reactions. The authors, I think, are right on target with this:

We believe a major hurdle to the application of a new chemical methodology to real synthetic problems is a lack of information regarding its application beyond the idealized conditions of the seminal report. Two major considerations in this respect are the functional group tolerance of a reaction and the stability of specific chemical motifs under reaction conditions. . .

Taking into account the limitations of the current methods, we propose that a lack of understanding regarding the application of a given reaction to non-idealized synthetic problems can result in a reluctance to apply new methodology. Confidence in the utility of a new reaction develops over time—often over a number of years—as the reaction is gradually applied within total syntheses, follow-up methodological papers are published, or personal experience is developed. Unfortunately, even when this information has evolved, it is often widely dispersed, fragmented and difficult to locate. To address this problem, both the tolerance of a reaction to chemical functionality and of the chemical functionality to the reaction conditions must be established when appropriate, and reported in an easily accessible manner, preferably alongside the new methodology.

This is as opposed to the current standard of one or two short tables of different substrates, and then a quick application to some natural product framework. Even those papers, I have to say, are better than some of the stuff in the literature, but we still could be doing better. This paper proposes an additional test: running the reaction in the presence of various added compounds, and reporting the % product that forms under these conditions, the % starting material remaining, and the % additive remaining as well. (The authors suggest using a simple, robust method like GC to get these numbers, which is good advice). This technique will give an idea of the tolerance of the reagents and catalysts to other functional groups, without incorporating them into new substrates, and can tell you if the reaction is just slowed down, or if something about the additive stops everything dead.

Applying this setup to a classic Buchwald amination reaction shows that free aliphatic and aromatic alcohols and amines kill the reaction. Esters and ketones are moderately tolerated. Extraneous heterocycles can slow things down, but not in all cases. But alkynes, nitriles, and amides come through fine: the product forms, and the additives aren't degraded.

I like this idea, and I hope it catches on. But I think that the only way it will is if editors and reviewers start asking for it. Otherwise, it'll be put in the "More work" category, which is easy for authors to ignore. If something like this became the standard, though, all of us synthetic chemists would be better off.

Comments (18) + TrackBacks (0) | Category: Chemical News | The Scientific Literature

June 20, 2013

The Perfect Papers For Each Journal

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Posted by Derek

For the Journal of the American Chemical Society:
"Nanoscale Stuff That We Can Imagine Could Have Gone to Science or Nature, But It Went There First So It Ends Up Here"

"Another Row of Glowing Sample Vials"

For Chemical Communications:
"Wild, Out-There Amalgam of Three or Four Trendy Topics All at Once, All in Two Manuscript Pages, From a Chinese Lab You've Never Heard of"

"A Completely New Assay Technique That Looks Like It Should Need A Twelve-Page Paper, Here In Two Because We're First and Don't Forget It"

For Angewandte Chemie:
"An Actually Useful and Interesting Paper (We Reviewed This One, We Promise), Brought to You With a Wincing, Toe-Curling Pun in the Abstract"

"The First Plutonium-Plutonium Quintuple Bond. Who's Going to Say It Isn't?"

For the Journal of Organic Chemistry:
"Remember Us? Here's an Actual Full Paper About Some Reaction, With Experimental Details and Everything. Where Else Can You Find That, Eh?"

"A Total Synthesis That Would Have Been in JACS Back When, You Whippersnappers"

For Tetrahedron Letters
"Remember Us? Here's a Four-Page Paper About Some Reaction With No Experimental Whatsoever. Where Else Can You Find. . .Oh, Right. Never Mind."

"The Four Thousand And Forty-Seventh Way to Prepare Nitriles From Oximes"

For Organic Letters:
"A Four-Page Paper With No Experimental (Supplementary Info If You're Lucky), But One You Actually Might Want to Read"

"A New Metal-Catalyzed Coupling, Featuring a Catalyst You Can't Buy and Don't Want to Make"

For the Journal of Medicinal Chemistry:
"Big Pharma Here, With a Gigantic Flaming Viking Funeral for a Project That Chewed Up Eight Years, And Here's All We Have to Show For It?"

"Small Academic Lab Here, With A Series of Rhodanines and Polyphenols That Are Seriously Hot Leads for At Least Ten Diseases"

For Science:
"Don't See Much Synthetic Chemistry Over Here, Do You? That's How You Know This is Hot Stuff!"

"People Only Read One or Two Papers Out of Any Issue of This Journal, and This Isn't One of Them, is It?"

For Synthesis:
"As Long as There are Five-Membered Heterocyclic Systems, and German Labs to Make Every Possible Derivative of Them, We Will Survive"

For SynLett
"The Number of Four-Page Organic Chemistry Manuscripts Is Larger Than You Can Comprehend. Obviously."

For ACS Chemical Biology, ChemBioChem, Nature Chemical Biology, Chemistry and Biology, et very much al.:
"Look, We Have NMR Spectra and Cell Culture Conditions in the Same Article, and It Isn't Med-Chem, So Where Else Do We Publish? Right."

Update: I've left out some journals haven't I?

For Bioorganic and Medicinal Chemistry Letters:
"We Wanted to Publish This in J. Med. Chem., But It's Been So Long That We Lost Half the Analytical Data, So Here You Are"

"A Quick Resume-Building Paper, Part XVI, But Man, You Sure Need a Lot From This Journal to Build a Resume These Days"

For Bioorganic and Medicinal Chemistry:
"No One in History Has Ever Read This Journal Without Being Sent Here by a Literature Search, So It Doesn't Matter What Title We Give This. Cauliflower Bicycle Zip-Zang."

For Chemistry: A European Journal:
"German Flexibility, Italian Thoroughness, and the French Work Ethic Have Combined to Bring You This Research, Funded by a List of Euro-Acronyms That Takes Up Half a Page"

Comments (78) + TrackBacks (0) | Category: The Scientific Literature

June 13, 2013

Watching DNA Polymerase Do Its Thing

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Posted by Derek

Single-molecule techniques are really the way to go if you're trying to understand many types of biomolecules. But they're really difficult to realize in practice (a complaint that should be kept in context, given that many of these experiments would have sounded like science fiction not all that long ago). Here's an example of just that sort of thing: watching DNA polymerase actually, well, polymerizing DNA, one base at a time.

The authors, a mixed chemistry/physics team at UC Irvine, managed to attach the business end (the Klenow fragment) of DNA Polymerase I to a carbon nanotube (a mutated Cys residue and a maleimide on the nanotube did the trick). This give you the chance to use the carbon nanotube as a field effect transistor, with changes in the conformation of the attached protein changing the observed current. It's stuff like this, I should add, that brings home to me the fact that it really is 2013, the relative scarcity of flying cars notwithstanding.

The authors had previously used this method to study attached lysozyme molecules (PDF, free author reprint access). That second link is a good example of the sort of careful brush-clearing work that has to be done with a new system like this: how much does altering that single amino acid change the structure and function of the enzyme you're studying? How do you pick which one to mutate? Does being up against the side of a carbon nanotube change things, and how much? It's potentially a real advantage that this technique doesn't require a big fluorescent label stuck to anything, but you have to make sure that attaching your test molecule to a carbon nanotube isn't even worse.
KF%20graphic.jpg
It turns out, reasonably enough, that picking the site of attachment is very important. You want something that'll respond conformationally to the actions of the enzyme, moving charged residues around close to the nanotube, but (at the same time) it can't be so crucial and wide-ranging that the activity of the system gets killed off by having these things so close, either. In the DNA polymerase study, the enzyme was about 33% less active than wild type.

And the authors do see current variations that correlate with what should be opening and closing of the enzyme as it adds nucleotides to the growing chain. Comparing the length of the generated DNA with the FET current, it appears that the enzyme incorporates a new base at least 99.8% of the time it tries to, and the mean time for this to happen is about 0.3 milliseconds. Interestingly, A-T pair formation takes a consistently longer time than C-G does, with the rate-limiting step occurring during the open conformation of the enzyme in each case.

I look forward to more applications of this idea. There's a lot about enzymes that we don't know, and these sorts of experiments are the only way we're going to find out. At present, this technique looks to be a lot of work, but you can see it firming up before your eyes. It would be quite interesting to pick an enzyme that has several classes of inhibitor and watch what happens on this scale.

It's too bad that Arthur Kornberg, the discoverer of DNA Pol I, didn't quite live to see such an interrogation of the enzyme; he would have enjoyed it very much, I think. As an aside, that last link, with its quotes from the reviewers of the original manuscript, will cheer up anyone who's recently had what they thought was a good paper rejected by some journal. Kornberg's two papers only barely made it into JBC, but one year after a referee said "It is very doubtful that the authors are entitled to speak of the enzymatic synthesis of DNA", Kornberg was awarded the Nobel for just that.

Comments (5) + TrackBacks (0) | Category: Analytical Chemistry | Biological News | The Scientific Literature

June 11, 2013

The Overselling of Ionic Liquids

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Posted by Derek

Ionic liquids (molten salts at relatively low temperatures) have been a big feature of the chemical literature for the last ten or fifteen years - enough of a feature to have attracted a few disparaging comments here, from me and from readers. There's a good article out now that talks about the early days of the field and how it grew, and it has some food for thought in it.

The initial reports in the field didn't get much attention (as is often the case). What seems to have made things take off was the possibility of replacing organic solvents with reusable, non-volatile, and (relatively) non-toxic alternatives. "Green chemistry" was (and to an extent still is) a magnet for funding, and it was the combination of this with ionic liquid (IL) work that made the field. But not all of this was helpful:

The link with green chemistry during the development of the IL field, propelled both fields forward, but at times the link was detrimental to both fields when overgeneralizations eroded confidence. ILs were originally considered as green since many of these liquid salts possess a negligible vapor pressure and might replace the use of volatile organic solvents known to result in airborne chemical contamination. The reported water stability and non-volatility led to the misconception that these salts were inherently safe and environmentally friendly. This was exacerbated by the many unsubstantiated claims that ILs were ‘green’ in introductions meant to provide the motivation for the study, even if the study itself had nothing to do with green chemistry. While it is true that the replacement of a volatile organic compound (VOC) might be preferred, proper knowledge of the chemistry of the ions must also be taken into account before classifying anything as green. Nonetheless, the statement “Ionic Liquids are green” was widely published (and can still be found in papers published today). Given the number and nature of the possible ions comprising ILs, these statements are similar to “Water is green, therefore all solvents are green.”

There were many misunderstandings at the chemical level as well:

However, just as the myriad of molecular solvents (or any compounds) can have dramatic differences in chemical, physical, and biological properties based on their chemical identity, so too can ILs. With the potential for 10^18 ion combinations, a single crystal structure of one compound is not a good representation of the chemistry of the entire class of salts which melt below 100 °C and would be analogous to considering carbon tetrachloride as a model system for all known molecular solvents.

The realization that hexafluorophosphate counterions can indeed generate HF under the right conditions helped bring a dose of reality back to the field, although (as the authors point out), not without a clueless backlash that decided, for a while, that all ionic liquids were therefore intrinsically toxic and corrosive. The impression one gets is that the field has settled down, and that its practitioners are more closely limited to people who know what they are talking about, rather than having quite so many who are doing it because it's hot and publishable. And that's a good thing.

Comments (12) + TrackBacks (0) | Category: Chemical News | The Scientific Literature

More on the GSK Shanghai Scandal

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Posted by Derek

The accusations of data fabrication at GlaxoSmithKline's China research site are quite real. That's what we get from the latest developments in the case, as reported by BioCentury, Pharmalot, and the news section at Nature Medicine. Jingwu Zang, lead author on the disputed paper and former head of the Shanghai research site, has been dismissed from the company. Other employees are on administrative leave while an investigation proceeds, and GSK has said it has begun the process of retracting the paper itself.

As for what's wrong with the paper in question, BioCentury Extra has this:

GSK said data in a paper published in January 2010 in Nature Medicine on the role of interleukin-7 (IL-7) in autoimmune disease characterized data as the results of experiments conducted with blood cells of multiple sclerosis (MS) patients "when, in fact, the data reported were either the results of experiments conducted at R&D China with normal (healthy donor) samples or cannot be documented at all, suggesting that they well may have been fabricated."

Pharmalot and others also report that GSK is asking all the authors of the paper to sign documents to agree that it be retracted, which is standard procedure at the Nature Publishing Group. If there's disagreement among them, the situation gets trickier, but we'll see what happens.

The biggest questions are unanswered, though, and we're not likely to hear about them except in rumors and leaks. How, for one thing, did this happen in the first place? On whose initiative were results faked? Who was supposed to check up on these results, and was there anything that could have been done to catch this problem earlier? Even more worrying - and you can bet that plenty of people inside GSK are thinking this, too - how many more things have been faked as well? You'd hope that this was an isolated incident, but if someone is willing to whip up a batch of lies like this, they might well be willing to do much more besides.

The involvement of the head of the entire operation (Jingwu Zang) is particularly troubling. Sometimes, in such cases, it turns out that the person at the top just had their name on the paper, but didn't really participate much or even know what was going on. But he's the only person so far in this mess who's been outright fired, which suggests that something larger has happened. We're not going to hear much about it, but you can bet there are some rather worried and upset people digging through this inside GlaxoSmithKline. There had better be.

Comments (30) + TrackBacks (0) | Category: The Dark Side | The Scientific Literature

June 7, 2013

Mutato Nomine De Te Fabula Narratur

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Posted by Derek

Reader may remember the sudden demise of science-fraud.org, under threats of legal action. Its author, Paul Brookes, had a steady stream of material pointing out what very much seemed to be altered and duplicated figures in many scientific publications.

Now comes word that the Brazilian researcher (Rai Curi) whose legal threats led to that shutdown has corrected yet another one of his publications. That Retraction Watch link has the details, but I wanted to highlight the corrections involved:

After the publication of this manuscript we observed mistakes in Figures 3A, 4A, and 6A. The representative images related to pAkt (Figure 3A), mTOR total (Figure 4A), and MuRF-1 total (Figure 6A) have been revised. Please note the original raw blots are now provided with the revised Figures as part of this Correction.
In Figure 3A, pAkt panel, the C and CS bands had been duplicated.
In Figure 4A, the bands were re-arranged compared to the original blot.
In Figure 6A, the band for group D was incorrect.

The remaining Figures, results and conclusions are the same as originally reported in the article. The authors apologize for these errors and refer readers to the corrected Figures 3A, 4A, and 6A provided in this Correction.

So I'm certainly glad that Prof. Curi went after a web site that looks for rearranged blots and altered gels. We wouldn't want any of that around. Would we, now.

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