The Nobel Prize conundrum

I rarely jump on the blogging hype of noting the new Nobel Prize winners every year. Exceptions are cases when I have a different slant on it, e.g., when a Prize goes to someone in my neighborhood or if the winners have published in PLoS ONE and PLoS Pathogens (lots of loud cheering back at the office).

But usually I stay silent. Mainly because I am conflicted about the prizes in science in general, and Nobel in particular.

On one hand, one week every year, science is everywhere - in newspapers, on the radio, on TV, all over the internet. And that is good because it is a push strategy (unwilling consumers getting bombarded with information they did not specifically seek, but find interesting once exposed to) as opposed to the usual pull strategy (when already interested people actively seek information). The journalists usually have a tough job - the Nobels are often awarded for findings that are way beyond 6th grade level and explaining the science which requires quite a lot of background is not easy. Good science journalists prepare very well for the Nobels, though, and usually get the reporting done well. The general population gets to go beyond the basics and learn what's new and exciting at the present moment. And Nobel winners are celebrities of sorts and people love celebrities. So this is a plus.

But the minuses are many as well.

First, sometimes a prize goes for a technique, not a fundamental discovery. This year's prize in Chemistry is a case in point - discovery and cloning of the green fluorescent protein (GFP) from the jellyfish, Aequorea victoria. The 1993 prize for Chemistry was similar - it went to Kary Mullis and Michael Smith "for contributions to the developments of methods within DNA-based chemistry", aka for the polymerase chain reaction (Mullis) and site-directed mutagenesis (Smith) - hmmm, both of these were biology prizes awarded for Chemistry: a pattern?

Like Larry, I think this is a bad idea. First, it reinforces the confusion that many people have - not being able to distinguish between science and technology. Second, I feel that a Nobel should go to discoveries that importantly affect the way we think about nature, rewrite the textbooks and perhaps have big implications for medicine (in the case of the Prize for Medicine). Technique in itself does not do this - it allows thousands of people to chip at nature's secrets, experiment by experiment, one detail at the time, and perhaps collectively over time bring about fundemantal changes in our thinking about the way the world works. But the prize does not go to those thousands who actually discovered something new, it goes to people who provided the technical tools.

Second, it reinforces the popular notion that science is competitive and that scientists do research in order to gain fame and fortune - you all know the stereotype of the crazy anti-social scientist show spends decades in the basement laboratory dreaming of a Nobel Prize. Where is the usual reason people go into science - natural curiosity?

Third, it messes up with the new incoming scientists - it gives them a skewed idea of what science is all about. So, they do whatever it takes to get into a highfallutin' school where they can join one of the enormous, faceless, gene-jockey labs with 25 postdocs where all the PI does is write grant proposals, the atmosphere is dog-eat-dog and one is tempted to doctor the data and do other unethical stuff. In that lab, the student is given a little detail to work on, while fostering the dreams of discovering a cure for cancer and getting a Nobel. There is an enormous pressure to produce lots of data quickly and to publish them in GlamourMagz.

What those students are not told is to go check the list of Nobel laureates and see what they got the prizes for. It was not one of the thousands of people working on C.elegans now, it went to the person who was the first to work on C.elegans. It was not one of the thousands of people working on zebrafish now, it went to the person who was the first to work on zebrafish. Likewise, it will not go to one of the thousands of people working on p53, or estrogen receptor, or using transgenic mice, or DNA-arrays, or whatever is the bandwagon now. All of that work needs to be done, but it is not revolutionary (at least not for a Nobel). It is "normal science", incremental placing of pieces into the puzzle. Nothing wrong with that, but don't get your hopes too high.

This brings me back to this year's prize for the Green Fluorescent Protein. You have probably heard the story of Dr.Prasher, the guy who did not win the Nobel although he was the first to clone the GFP gene. He is now a shuttle driver for a garage (interestingly, Kary Mullis, the other guy who got a Nobel for a technique, is also now out of science: a surfer, womanizer and HIV denialist). Why? He could not get funding for the continuation of his work. When did this happen? In the late 1990s, at the time when the science funding started to go down.

So, if this is so revolutionary, why didn't he get funding? The official notes on his grant proposals are probably official-sounding and diplomatic, but I can imagine what was going on through the reviewer's head while reading Prasher's proposal - something along the lines of "What on Earth is this jellyfish, Aequorea victoria? Why would anyone care about such an animal (is it an animal anyway, or what is it?)? Why not do something useful, in humans or mice, or at least in fruitflies? Why waste time and taxpayer money on this Discovery Channel crap?"

Being one of the thousands on a bandwagon is bad. Especially in the time of poor funding. But working on a non-bandwagon question, using non-molecular techniques, in a non-model animal is worse, much worse. At the time of the peak in funding, it was sometimes possible to get funding from NIH, but even then it was not easy for such research. Most biologists, though usually not covered by the media much, do that kind of stuff - just go to the SICB conference one year and see for yourself. Luckily, the research itself is usually not very expensive and a lab can "go on fumes" if needed for a year or so as long as it can keep its animals and rooms. There is alternative way of funding: instead of one large NIH grant, many of these labs have many small grants from NSF, NASA, US Army (or Airforce, or Navy), USDA, private foundations, etc. But at the time of low overall funding, even these sources dry up.

Some years ago, I listened to a very interesting talk by Knut Schmidt-Nielsen. The talk was in an unusual format and initially took some people aback. Instead of starting with a big question, gradually zooming in to the methods and results, then at the end zooming out again to the Big Picture, Knut started with an anecdote. Then, he told another anecdote. Then another. After an hour, we finally 'got it' - there was an undelying thread in all of these anecdotes. Each highlighted a piece of strange research by a strange person in a strange organism, marred by lack of funding and appreciation (and sometimes outright derision), yet in the end resulting in a ground-breaking discovery that shook our way of understanding the world, or provided a potent research tool (yes, GFP was one of the examples, tetrodotoxin was another). The take-home message was: do what you are passionate about, look at non-model organisms, let your curiosity take over, do not focus on application, tough out the lean financial times, and who knows, you may deserve a Nobel one day. For doing what you like, not what others told you is "hot".

Look at that list of Nobel laurates in Physiology and Medicine again. Each one of them was a pioneer, doing something weird that nobody else thought made any sense at the time. They persisted and followed their hunches and finally overcome the resistance of their peers. And many thousands of others who did not win a prize, still retired happy with their career - they did something useful and had fun all along.

Not all of that research even required a lot of money, expensive equipment and large numbers of postdocs. Watson and Crick tinkered with pieces of metal and made a model. My favourite Nobel is the 1973 one: von Frisch used a fine paintbrush to mark the bees and a few dishes with sugar water; Lorenz walked around the yard followed by a flock of ducklings; Tinbergen had some fish in a tank, painted red dots on seagulls' beaks, and moved some pine-cones around. And each one of them made revolutionary discoveries about the way the brain works. It is better to have a problem to solve and use one's creativity to solve it in the simplest, cheapest, most decisive way, than to search for a question that you can address with the technique you are good at.

Often those simple, cheap, creative techniques provide more trustowrthy data. I know from my own work - I ran some gels and that's an art, not science. I do not believe my own data (people around me in the lab did). What I got are hunches, perhaps something that statistics may say is relevant, but I dare you to try to repeat the experiment and get the same results! On the other hand, when I came up with a creative experimental protocol - all I needed to do is count eggs every day - the result I got was an all-or-none uber-conclusive response that does not need no steenkin' statistics and simply over-rules a few decades of published literature (I really need to publish that stuff). Not all questions require, or could appropriately be addressed by running expensive molecular experiments. Each question is at a particular level of organization and requires the experiment to be done at that level, perhaps higher, not lower (as one can infer the behavior of parts from the behavior of the whole, but not vice versa).

There are many questions at the levels of molecules and cells that are worth asking, but that is not all there is in biology - and that is something that students need to be told. And some people will be really good at designing such experiments and answering important questions. But there are other levels in biology and other approaches, and some people will be better suited for those. And for saving money by designing and building one's own equipment (my PI always told me if my PhD studies did not get me anywhere, I could always find a job using the skills learned in the lab - as an electrician or carpenter). At least in those other fields, the competitiveness is toned down a notch - no need to ask for millions of dollars every few years, no need to get into a GlamourSchool and publish in GlamorMagz - you can do it anywhere and publish wherever you want. Who can scoop you if you are studying deer in a particular forest? You have a couple of years of data in advance. You see if a competitor comes in - and you offer collaboration instead.

So, it's up to one's interests, talents and temperament. I was strongly advised (at the time when a PhD looked likely and such) to do a postdoc in a heavily molecular lab in order to get molecular techniques under my belt because that is "a necessity for getting a job". So I tried - I went and spent a few weeks in such a lab (they even cleared up some space in the freezer for my samples) and decided that it was not for me. The PI was really nice, but part of that super-competitive atmosphere I detest. The lab consisted of 25 people who seemed really nice - on those rare moments when one could actually talk to them. Most of the time - and that is about 13 hours per day, 7 days a week - they were hunched over their benches, quiet, pale like Eloi. The specter of the Japanese hell-bent on scooping was hanging over everyone's head. A saw postdoc, a really good, creative, smart guy with several excellent papers to his name, being told, on a Friday afternoon, to re-do his experiments and show the data first thing on Monday morning! WTF!? One thing I most appreciated in my old lab was time - I did my stuff when I wanted to. I did twice as much as asked because I was excited. Those who wasted their time left the lab after a year or less, but I persisted on my own. And nobody ever told me when to get the data or when to do my work. I did a lot of it at nights and over weekends because I am too social - would rather chat with people and attend seminars than work if others are around - but that was my own choice. Nobody tells me what to do.

Back to the topic. In non-bandwagon, non-molecular, non-medical biology, there is no need to rush, or to be secretive about one's work, or to fudge the data, or not to do Open Notebook Science. No patents or big prizes or big money are at stake. But you have a nice, pleasant career in science suitable to those who are not of the A-type temperament. You have time for family and hobbies. And you enjoy the collegiality and collaborations and the growth in your own respect and authority over the years. That kind of stuff can sometimes even be done by amateurs. Nothing wrong with that.

So, the Nobel Prizes are used, in a way, to lead the students along the wrong paths - to jump on bandwagons. But being on a bandwagon, as history shows, does not result in winning a Nobel - quite the opposite. It is the weirdos, or people who moved from one discipline from another (thus avoiding thinking inside the box of the discipline) - the mavericks - who tend to hit on something really important, sometimes by intent, sometimes by serendipity.

So, go on and study what you are truly excited about in some emerging model system, or something weird like the platypus, or sea cucumbers, or ferns, or Venus flytraps, or silverslippers - who knows where that can end (more likely on science blogs or Discovery Channel where cool animals doing cool things are appreciated, than in Stockholm), but even if it does not, you'll have fun all the way.