Repost - Slow Science II

Get ready for Slow Science III. I like the idea of having them all in a row. So here's the second essay in the series on Slow Science!

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Earlier this week, I had an encounter with a collaborator of mine who is an established researcher at a well-known university. After I recounted my tale of experimental woe he said to me, "You should pursue this it sounds like a really interesting problem and could turn out to be very cool." My answer, "I would but I don't really have the time. My supervisor Dr.Add'EmUp has to apply for a grant soon and he would really like to have this experiment finished and the paper submitted." He nodded, acknowledging the situation and said, "Yes of course. Of primary importance is getting that paper done."

This anecdote is my way of saying, that as academic scientists we make choices on a daily basis to pursue what is expedient at the cost of what may turn out to be interesting, all because of the lack of time. This rushed time frame creates an environment that does not support slow science. And it made me think back to my first post on Slow Science Gets The Shaft: Part 1. And the supposed follow-up that I said I would write and never did. Well folks, here it is. Part 2. Albeit, terribly, terribly slow (bad pun intended) to arrive. It’s a novel – so get yourself a cup of java and a healthy gluten free muffin and sit ‘er down.

In February the Lenski lab celebrated the 50,000 generation mark of their long term E.coli experiment. This experiment was started in Feb 1988 with a single genotype or clone (not a single microbial cell). From this single clone, 12 replicate populations were grown in 12 separate liquid environments (12 flasks with Davis Media broth supplemented with glucose and citrate). The lines are identical, except for a neutral marker that distinguishes six of the lines from the other six. Once in the flask, the populations are grown at 37°C for 24 hrs. After 24h, a subset of the population from each of the 12 flasks are transferred to a new flask with fresh media and the whole growth process is started anew. Furthermore every 75-500 generations (depends on which paper you read), samples are frozen down. These then provide a fossil record with which to ask what were the changes and how many occurred over time, etc. In 24h bacteria, divide approximately 6.67x, which means that Lenski and his students/postdocs have been doing this for every day for 7496.25 days or 20 years.

Lenski is a fantastic evolutionary biologist and a visionary. His experimental designs are awesome. He’s TheMan. If you look at the list of former students and postdocs that have come out of his lab, it reads like a Hollywood’s who’s who in evolutionary biology. I realize the term visionary might seem a little extreme to many, but it’s not. The reason is because Lenski had the foresight to recognize that what’s interesting and unpredictable is found, not in the short term, but often emerges from a long-term pattern. Although many organisms can undergo adaptive change in a relatively few generations and strong selection creates observable differences among populations within a species, it is only through the long-term changes that we can really understand what processes were relevant. As Conway Morris has said, “The possible evolutionary routes are many, but the destinations limited.” As a young academic, Lenski had to invest time and money to follow his curiousity about science, in a way that today’s young tenure track academics, limited by the drive to get tenure and funding, can’t do.

Did it pay off? Yes, of course. Work from these populations demonstrate parallel phenotypic evolution, changes in morphology relative to the ancestor, the evolution of increased DNA supercoiling with parallel changes in gene expression profiles, and the evolution of mutator phenotypes. But there are two major findings that came out only after the experiment was run for 20 years. First last fall, this paper came out in Nature. It showed that the rate of adaptation, as measured by the number of beneficial mutations accrued over time, exhibits a clock-like regularity. This clock-like behaviour is often expected from neutral evolution but not necessarily from adaptive change. Lenskiites were not the first to show this surprising result, Wichman and colleagues (2005), demonstrated a similar result with a bacteriophage growing in a chemostat for 13,000 generations. Whether macroevolution is nothing more than an aggregate of many small events, as Sean Carroll (2007) suggests is only explainable by experiments that quantify those events over the long term.

The second very cool result was that a key innovation happened in one of the replicate populations. Typically, under oxygen rich conditions, E.coli eats and metabolizes glucose (its carbon source), with no ability to use citrate as an energy source. Well guess what? In one of the replicate populations, a citrate-using genotype finally evolved at generation 31,500. That a key innovation evolved so late in the experiment, is telling about the importance of doing long-term studies.



In 2002, Peter Grant and Rosemary Grant published a 30-year study that showed how the direction and magnitude of selection fluctuates wildly over the long term. Environmental change and infrequent hybridization led to a phenotypic trajectory in the Galapagos finches that was not predictable in the short term. Both Lenskis work and the Grants study, however pale in comparison to the Park Grass experiment started by John B. Lawes and Joseph H. Gilbert in 1856 at Rothamsted, Hertfordshire, England. This experiment is the longest running ecological experiment in the world and over 170 publications have come out of it. Although it was started to test how different fertilizers would improve yield, it has since inspired new ecological theory (resource ratio hypotheses), demonstrated long term population dynamics related to life history not detectable over a shorter time period, and provided examples of local adaptation, reproductive isolation and drift. More importantly what this experiment and the two other long-term studies show is that these types of experiments grow in value with time. Although conceived to investigate one scientific question, they can be used to answer a multitude of interesting and often unexplored areas.

The benefits of long term studies like this one seem obvious and yet it is no surprise that they are rare. In fact, in the book The Clock of the Long Now, Stewart Brand laments that science today “is more often driven at a commercial or even fashion velocity than at the deliberate pace of governance or the even slower pace of nature. “ He offers seven reasons for why more scientists are not performing this kind of research.

1. Long term studies aren’t about proving or disproving hypotheses.
2. They don’t generate quick papers, the coin of science
3. They bear no relation to scientific fashion, where the excitement is
4. Not subject to money making patent or copyright.
5. They die when the primary researcher dies.
6. Extremely difficult to maintain funding
7. Archives are expensive and a hassle to service and keep accessible.

There are many short term studies that don’t use hypothesis driven research. We only need to look to the new discipline of bioinformatics to see examples of research that look for patterns in DNA sequence and expression data. Furthermore, I disagree with his last point. In such a computer advanced and internet driven society, the database and archival capacity of computers is enormous and the internet makes accessibility less of a problem. I think, that what explains why we don't see many long term experiments, is largely due to the structure and incentive model of granting agencies and academic institutions, specifically in North America.

Long-term experiments or studies require a scientist who is patient, thorough, and slow. The superstars in my field are anything but slow. Instead, as Brand states they tend to “track noisy signals too closely and confuse themselves by making changes before the effects of previous actions are clear.” In other words, publish one paper and then six months later publish another renouncing the results of the first. Why? Because that is how the game is played. The current game rewards prolific at the expense of being profound.

(Although I've heard the common refrain from faculty that some members of a search committee do look for quality, I wonder how many of them have actually read any of the papers from the job candidates. And if that assessment of quality is based on the journal's impact factor or the faculty member's own assessment of the candidate's science? It seems to me that there is a clear unwritten understanding that not every paper that gets into those high impact journals is actually profound and quality science. Here again the time factor creates an atmosphere of rush.)

Prolific is what gets you the chance at a t-t job, grants and ultimately the sweetest of all carrots - tenure. The system in the US (maybe less so in Canada) doesn’t support patient, thorough, slow, and profound science. Here in the US, despite being hired by colleagues, a good scientist can find themselves fired by these same people in 3-5 years when they go up for tenure. Fired or given terminal contracts simply because they didn't have the requisite number of publications or a lack of external funding. But really, how many are actually lucky enough to get funding when success rates at NIH and NSF are 7-12%. In Canada, this doesn’t happen. Once hired as an assistant professor, it’s rare that you don’t get tenure. The screening process for tenure is in the hiring, as my PhD supervisor once told me.

An environment that uses a carrot (tenure) and stick (terminal contract) incentive model narrows people’s focus and destroys creativity. If you don’t believe me, listen to the facts put forward by Daniel Pink, in his TED talk (it's worth 17 minutes of your time) on the science of motivation. Why would you spend time doing science that you think is worthwhile when it doesn’t get you the carrot. Instead, the choice is obvious, you do science that you know will work, ie get you the publications, the grants, all in the drive for tenure. This carrot and stick model leaves no room for innovation and creativity. In fact, TheDude, a tenured professor at a prestigious university told me, “Academia is broken. It's out of control. Getting tenure is the part that makes it broken.” He advises his students to do whatever it takes to get tenure and then “You can start doing the science you really think is worthwhile.” But I wonder what does that say about the science you do up until that point? And really by the time you do get tenure, if all your training is focused on routine, obvious, mechanical science, will you be practiced in innovative thinking such that you will even know which questions to ask?

A second effect that this “if you do this then you will get this or else” atmosphere does is it creates and attracts a particular type of scientist to academia and selects against another. One academic I know, has said that he doesn’t participate in a project unless he sees a publication in it for himself. Cutthroat, yes. But, at least honest. I can think of several colleagues of mine who are so much smarter than the known superstars in my field, both in terms of the quality of science and the level of innovation in their science. But they won’t make it. Why? Because they don’t want to publish just anything for the sake of publishing. And, they would argue, isn’t there enough shit to wade through already? Instead they want the work to matter. They would much rather have solid, well thought out, and fully explored ideas in 3 papers than 10 papers that either test the obvious, review a topic that has already been reviewed, or just do acceptable science. Again words from TheDude, “The problem is the number of papers that anyone individual produces is out of control. If I were the king I would eliminate half the journals especially N and S and limit people to publishing only two papers a year.”

My feeling is that somewhere between the two extremes is probably the right place. Half baked ideas are okay to publish as long as the author acknowledges the limitations and the caveats associated with their incompleteness. And we definitely need innovation and profound, thoughtful scientists. After all, diversity is the stuff of evolution. And progress is only achieved when there is diversity. So the real question is can academia in its current state support both types of scientists (fast and slow) and both types of studies (short and long term)? My belief is that it cannot in its current form. What will be the effect in the long term on the quality of academic science?

“We see nothing of these slow changes in progress, until the hand of time has marked the long lapse of ages.” Darwin (1859).

I guess we shall just have to wait to see the outcome of this long-term experiment.




Interested in reading some of the papers I cited? See below:

Barrick, J. E., D. S. Yu, S. H. Yoon, H. Jeong, T. K. Oh, D. Schneider, R. E. Lenski, and J. F. Kim. 2009. Genome evolution and adaptation in a long-term experiment with Escherichia coli. Nature 461:1243-1247.

Blount et al. (2008) Historical contingency and the evolution of a key innovation in an experimental population of Escheria coli. PNAS 105:7899-7906.

Brand, S. (1999) The Clock of the Long Now: time and responsibilities.

Carroll et al. (2007) Evolution on ecological time-scales. Functional Ecology 21: 387-393.

Grant, P.R. and Grant, R. (2002) Unpredictable evolution in a 30-year study of Darwin’s finches. Science 296: 707-711.

Conway Morris, S (2003) Life's Solution. Cambridge Uni Press, Cambridge, UK.

Silvertown et al. (2006) The Park Grass Experiment 1856-2006: its contribution to ecology. Journal of Ecology 94: 801-814.

Wichman, H.A., J. Millstein, and J.J. Bull. (2005) Adaptive molecular evolution for 13,000 phage generations: a possible arms race. Genetics 170:19-31.