funding fondling

A number of years ago, I was working part-time in Trinity College Dublin.  I'd work mostly at/from home but for two days a week I would be On Site in the lab.  Those two days were pretty intense: participating in lab meetings, giving statistical advice, criticising drafts of thesis chapters, polishing grant applications, trying to find 20 minutes for lunch . . . and suddenly I'd be drooling on my own collar as I fell asleep in the bus home. My boss and I would try hard to attend the departmental seminar on Thursday lunchtime - turning up was what you did for the community.  It was also about the only time when you would have the chance to be surprised by something because the speakers were almost always From Foreign; in the sense that even a speaker from UCD or DCU (the other universities in town) was Foreign.  The students who ran the seminar series would supply sandwiches to encourage people to attend and I learned to be very parsimonious about accepting this free food lest I fall asleep in the middle of our visitor's talk.  But I tell ya that I fell asleep aNNyway many times because the talks were so deadly dull and presented in such a stultifying, powerpoint-propped, droning way.  Most of the senior people in the department sacrificed whatever commitment they might have to community to their desire to not waste an hour of their life over something that was not in, or even close to, their field of interest. The great thing about being a generalist is that so much more of the universe is at least potentially interesting.

One day, the boss was unavoidably elsewhere, so she missed the weekly seminar.  When she came back in the afternoon, one of the graduate students and I were crowing about the best, the most inspiring, the niftiest ("Gad Whistler, I wish I'd said that") talk we'd heard that year; perhaps the best that decade.  The presenter was Aled Edwards from the University of Toronto and he talked about a brilliant example of Harry Potter winner-take-all that is costing science dear.  The Toronto hypothesis was that, after spending $1billion on sequencing the human genome, we should have something to show for it - new genes revealed, new associations of disease with mutations in the DNA, new drug targets, new ways to seeing.  But it wasn't like that! Edwards & Co, analysed two generations worth of scientific literature to count up the number of published papers about specific genes of pharma-medico-biological interest. In particular they looked at druggable targets in three classes: kinases, ion-channels and nuclear receptors, before and after the delivery of the human genome sequence into the public domain by Bill Clinton and Tony Blair (thanks boys!).  That's a lot of data to trawl through, as more than 20 million papers have been published since PubMed indexing started in 1950.

What they found, for all three rather different sorts of protein, was that we are still squeezing the last drops of info out of the same proteins that we were studying before the human genome became available.  This despite a lot of objective data to show that there were lots of very interesting disease-associations and potential therapeutic targets in the "dark-matter" of the genomic universe. The scientific community is still doing same-old same-old on the tried-and-true. Some time ago, Nobelist Roger Kornberg claimed that scientists have a tendency to "fondle their problems" or to use an even less appetising metaphor, to pick at the scabs of their previous research rather than coming up for a breath of fresh air and trying a new avenue to investigate.

Here's one we did earlier with my Yr3 bioinformatics class.  It is a tally of the number of papers published about 4 of the 10 Toll-like receptors that we humans have to detect the hostiles in the environment so that we can mount an appropriate immune response:

TLR	PubMed papers	PubMed reviews
TLR4	10116	633
TLR5	882	44
TLR7	1689	145
TLR9	3070	274

WTF?  We have ten TLRs, they must each have a(n essential) purpose.  Is it conceivable that the job TLR4 does for us is ten times more important than that which TLR5 fulfills?  D'ye think that some attention to TLR5 might save lives?  Do you think you can make bigger waves because the TLR5 pond is so under-populated? Go to!

There are three good (i.e. bad) reasons for this scab-picking.
1) It is easier for editors and referees to accept papers that are firmly in the context of existing research - critiquing earlier work or building on previous studies or doing the same analysis in a different species or different human population or different cell line.
2) Research funding bodies are chronically risk-adverse - they don't do Blue Skies and minority interest ERRa is blue skies compared to over-analysed diminishing-returns Era.
3) Research depends upon kit, and there are chemical probes available for the Harry Potter proteins but it costs person-years and multi-dollars to develop new probes for the emerging proteins.  The regrettable upshot is that these proteins don't emerge because nobody will risk (investing in) investigating their functions and attributes.

I thought that analysis was brilliant. Like the failures in ethics, failures in statistical power and failures of reproducibility, fondling is systemic in science (blobolinks).  In the Nature commentary that sums up this research, Edwards offers some suggestions about how we might break free of these incestuous shackles of familiarity.  My Institution is too poor to afford an electronic subscription to Nature, so I can't read that on-line but you may be able to.  A longer version of the same material is defo in the public domain.  This sort of research is also quite empowering because it shows you that useful and informative research can be done without horsing through thousands of dollars worth of kit and consumables.