Take on a Big Problem? A ton of money or a tub of water?

Two Nobel laureates were interviewed recently on the BBC Radio 4 program, The Life Scientific, and they said some relevant and interesting things.  The program is new series, interviews with some of the most influential scientists alive.

Paul Nurse, who won his prize for work on the genetics of cell division, was interviewed in October.  His prize was earned essentially because cell division is in many ways a similar process in all forms of life.  In light of evolution this could be said not to be a surprise: the same process might be expected to involve the same mechanism.  On the other hand, there is a lot of parallel evolution and given the complexity of many controlling mechanisms, one gene might substitute for another for the process.  But, at least in terms of some of the controlling genes, evolution somehow maintained the same mechanism over more than a billion years.

The other scientist of particular interest, interviewed in November, was John Sulston.  He innovated methods for mapping (locating) the genes on the genomes (chromosomes) of an important experimental model, the tiny flatworm called C. elegans, and then led the race to sequence the entire human genome.  A main part of this work was done at the Sanger Centre, near Cambridge, England, where I was fortunate enough to spend a sabbatical in 2005.  In his modest self-description, Sulston said that his job was just to identify the entire genome, and let people more clever than he have that information to do the work to find out what different parts of the genome do.

C. elegans; Weiss and Buchanan, The Mermaid's Tale, 2009

This moved the field from 'genetics' that dealt with single genes and classical hypothesis-driven science (where you have a specific, restricted idea, and then design experiments to test it), to 'genomics' or what is called hypothesis-free science: sequence everything in every individual you study, and search for unsuspected pattern to emerge that can then be specifically tested.  The latter is more like Victorian plant and beetle specimen collection, that we so often love to criticize as useless, not even 'science', really.

There are two aspects of this that are relevant to the current drive to understand life, largely from the genome perspective. First, Nurse said one should start out a science career by picking a really Big Problem.  Even if you work on a narrow scale, do it to solve a major problem about life--he started out with yeast, before turning to human cells and generalizing how cell division work.

Sulston got a similar prize but by taking a diametrically opposite view: his job was to collect the beetles and let everyone have a crack at the data to see what they could find.  Genomics has been driven by the technology that makes it possible. But it is in some ways the opposite--or even the antithesis--of Nurse's idea.  It is doing a really big study on a really small problem.

GWAS (genome wide association studies) to understand, say, the genomic basis of diabetes may not seem like a small problem.  If the genomic approach works, and it leads to major reductions in diabetes morbidity or mortality, it would be a big success.  But the problem itself is very local and particular, and there is no intent that solving it would apply to a bigger problem.  One can criticize the blind following of this Big Science approach, and it richly deserves the criticism for the manifest, numerous reasons we often point out.

But is this also a big problem hiding under a big budget for a small question?  It is often argued so.  In defense of ever-larger studies of biobanks, GWAS, and the like (or, in regard to evolutionary genetics, of ever more whole genome sequencing from ever more species, applying ever more detailed and exotic statistical tests for evidence of natural selection), defenders often argue that yes, it's expensive, and yes it may be decades before it bears fruit, and yes, GWAS may not identify major causal genes, BUT these studies will reveal biological mechanisms or pathways that will have much broader applicability.

There is no answer to this.  We are clearly, however, training a generation of technocratic scientists who think big budget and big technology either first, or immediately after whatever question they are asking.  And the questions are nowadays mainly applied ones: what causes diabetes or stomach cancer, for example, or what cause skull shape variation.  However the studies are routinely justified for what they will reveal more generally.  We often, if not routinely, point to chance discoveries in the history of science, and say that's what we're aiming for.

Of course, the vast majority of science is routine, if not hum-drum and with little likelihood of any impact other than to feed the investigator and his or her lab group.  It is vainglory of a high magnitude to promise serendipitous Eureka! moments as justification for dipping so deeply into the public treasure for each of our studies.

On the other hand, it is certainly true that Eureka! discovery moments do arise.  So is this an acceptable justification for investment in, say, big-scale genomic approaches?  This is for you to decide.

But what we're doing clearly is proposing the kinds of studies to answer the kinds of questions that require big data and expensive, extensive, and often very complex instrumentation and statistical methods to address.  Inevitably and systematically, perhaps, some issues are being closed to us while others are being opened.   One can argue that the narrower your training or focus the less likely you'll have one of the major moments, but in any field in any era it has always been only the very rare, lucky person who has had one.  Also, without the investment, they certainly can't happen.

Or are these correct arguments in support of the way we do things today?  In the past, it was individuals slogging doggedly after a problem (Galileo, Newton, Darwin, Einstein, others) rather than big factory operations (which, to be fair, didn't really exist until fairly recently), that delivered Eureka! discoveries.  Will the lone, persistent, investigator have the next transformative insight?

Nurse had substantial though we think not enormous funding.  Sulston and the Human Genome project garnered enormous funding for their work.  Both got Nobel prizes for their work.  On the other hand, Darwin just worked in his backyard after a low-cost sailing trip round the world, Mendel in his modest garden out back of a monastery, Galileo with a cheap telescope and under house arrest.

And the real Eureka! moment?  That just required Archimedes to take a bath.

2020 visions, or 20-20 hindsight?

For an article in Nature this week ("2020 Visions"), a number of "leading researchers and policy-makers" were asked to comment on what their field is going to look like in ten years. "We invited them to identify the key questions their disciplines face, the major roadblocks and the pressing next steps."

Well, Nature is a commercial operation, not as unlike, say, People Magazine, as it may wish to be viewed as, and it often looks like it, too. As it does here, since only incremental science can even generally be predicted (for example, that the price of whole-genome DNA sequencing will drop dramatically, and that as a consequence we'll all be hungering to do it in almost any kind of study, whether justified or not). So, this article is essentially free advertising for the respondents. The futuristic bravado is limited, as in a way it must be. But let's suspend our disbelief and see if we can go with their premise for a minute.

The respondents include a university president, an astronomer, a chemist, a paleontologist, a computer scientist, someone from the NIH, a geneticist and so on. We aren't qualified to comment on the specifics of Google's director of research's vision of the future, but we can say, in general, that this is an odd exercise, as prognostication generally turns out to be a wish-list in disguise (right, we can't even go with the premise for a whole minute!). So, prognosticators on the future of personalized medicine, say, are advocating for their own view of the future. Or rather, of the present. One interviewee comments about how rare genetic variation will be found to have much more predictive power for disease than common variants--exactly what one might expect given the failure of 'common' variants to solve all the world's problems, and the next level of ramped-up DNA-variation-based promises that have been growing in recent years, not coincidentally nor disinterestedly along with the technologies being sold for ever-cheaper whole-genome sequences. This is essentially rationalizing for more of the same, since although there may be new findings for disorders with clearly known causal genes, generally rare variants will be very difficult to assign causal effect to (for example, suppose it's only seen in one patient?). So rare variants will not be very useful in public health terms, yet public health funds are going to be demanded for this work. We have to assume that the leading experts in the areas we know a lot less about are doing the same kind of nest-feathering.

Of course, any scientists can each be expected to be excited about, and to want to promote, their own field of interest. If we didn't think it important, it would be depressing to go to work every day. And these days, as things are structured, science is expensive and has become a kind of competitive commercial Get-Grants enterprise. But journalism, even science journalism, should bear the responsibility of calling things by their true names, and asking seriously about vested interests and so on.

But, the Nature piece is provocative in the following sense. A deeply embedded belief (truth?) one hears over and over again about science is that major discoveries over the centuries have been accidental. They can't be planned or predicted. Geniuses must be given free rein to think, tinker, experiment, and their eureka moments will follow.

If this is really true, how likely is it still to happen in today's vested-interest, continuity-driven funding-based arena? Big-money science today is goal-oriented--with the goals often dictated by the patron (NIH, the military, etc.)--and those goals are generally very specific and incremental, with every step carefully planned even years ahead of time. Knowledge is gained, for sure, but it was gained by Victorian beetle collectors, too, which didn't go very far. On the way, unexpected things are certainly to be found, but even they usually are within the incremental rather than conceptually door-opening.

Given the way science is funded these days, that's the way it has to be. So, there's less and less room for real luck and serendipity, as the 'visions' of the 2020 visionaries show in a round-about sort of way. Does this mean no progress will be made? Of course not, but it is a different kind of science.

Personally, we think that centralization of high-cost technology (like high-throughput DNA sequencing), and distribution of more, but smaller though longer-term grants to more different investigators, especially junior investigators, with less detail required in grant proposals, and with promotion and tenure and overhead disconnected from individual grantees' would increase the 'ecological' diversity of science and raise the probability of major new discoveries. Less intense pressure to hustle, more time to think, but there should be eventual accountability and project-termination criteria, too--unlike much of the Big Science that is being constructed, with guarantees of continuity in mind.

Nothing ensures any particular level of dramatic discovery, but as scientists we should want the odds to be as high as possible. Institutionalized enterprize may not be the best way to make that happen.