This blog post was inspired by two recent events.
First, in response to a NY Times article about the "data deluge" affecting biologists, one of my Facebook friends said something like "stop whining about how hard it is to analyze the data and do some good experiments instead!" I vehemently disagreed with this simple statement -- but why??
Second, I used the 4th domain paper by Jonathan Eisen in my computational science class, and we discussed how one would reject or accept the 4th domain with more confidence. Somewhat to my surprise, my own conclusion was that I would ... sequence everything! Yep, just go out and sequence everything I could get my hands on in the tree of life, as well as a bunch of communities from ocean and soil. I was surprised to reach this conclusion (which we can debate on its own merits some other time) because my background is in real science, not "discovery science", and I'd been trained to believe that the discovery-based approach of shaking the trees to see what falls out was kind of unintellectual and unscientific.
Both of these events made me rethink my attitude towards discovery science. The first, because the guy that told us all to stop whining isn't dumb, but I also don't think he's entirely or even mostly right; and the second, because, together with the first, it made me challenge the conventional wisdom in molecular biology that hypothesis driven science is the Right Way.
The way many (most? all?) molecular biologists work is something like this: they develop a theory about some process (physiological or developmental or genomic or whatnot), develop a specific hypothesis or set of hypotheses, and then figure out how to test those hypotheses using controlled experiments. "Hypothesis: objects of near equal mass accelerate equally in a uniform gravitational field; test: drop two objects of equal mass; control for wind resistance." In developmental biology, the molecular field with which I'm most familiar, you might say "I think that the pax3/7 gene is necessary for neural crest specification in these cells at this time, so I'm going to knock it down and see what happens to neural crest." The key point is that you always need to reframe your theory in the form of a fairly specific hypothesis, and then figure out a way to test it. Training students to develop, frame, and test hypotheses is What We Do as professors. When you write grant proposals, you write about why you have developed a specific set of hypotheses (that is, you justify your hypotheses by appealing to prior work and preliminary results), claim that these hypotheses are important or interesting, and then argue vigorously that you are the right person to receive beaucoup bucks to test these hypotheses. Hypothesis-driven research is what we do!
This somewhat dogmatic picture obscures a number of inconvenient truths, however. First of all, many grant agencies (and reviewers) are risk averse, so they prefer to fund things that appear as certain as possible. This means you have to walk the line between crippling your hypotheses by predetermining them with your data, and coming up with an interesting and novel hypothesis -- if you've already tested your hypothesis and you're pretty sure it's right, then it's no longer that interesting to test! Second, no research plan survives contact with reality. So what you really do is sketch out a small extension to a near-certain hypothesis, get funded (admittedly this step is rather rare...), and then discover that your extension is incredibly simplistic and most likely wrong and a dead-end alley. So you end up working on something else completely. That is, you get the grant to work on X and end up working on Z -- not necessarily too far away from X, but not X, either. This leads to a third truth, which is that you get grants because you've been able to make a successful argument, not because anyone expects you to accomplish exactly what is in the grant. The only people that really take your grant proposal literally are the contracts & grants people at your university; the grant administrator and you both understand that this is research, and a real researcher is likely to end up someplace other than where you intended to go, at least in detail.
(I always like to cite Einstein at this point in a conversation: "If we knew what we were doing, it wouldn't be called research, would it?")
What happens when a student confronts this situation? Well, usually students have to write research proposals as part of their qualifying exams, and often students try to stick to those research proposals even when their experiments go awry. I've been part of a bunch of committees where the student will say "ok, so these were our original aims, and here's where I've gone away from them". They don't seem to understand that we don't care (or at least I don't): the real point of the qual is to make sure they know how to frame a hypothesis, and to ensure that they know what a testable hypothesis looks like, smells like, feels like, and tastes like. After that, your research will go where it goes, and that's as it should be. (Aside: my most frustrating (but still positive) moment as a committee member occurred when a student presented a hypothesis and talked about how she was going to test that hypothesis with method X, method Y, data analysis Z, etc. We asked her a bunch of questions and she seemed strangely confident and specific about the expected results. Upon further probing, it turned out that she'd already done the experiments and knew the answers, but thought that the qual needed to be about her hypotheses de novo, and shouldn't take into account actual data she'd generated. WTF??)
Unfortunately, we often stick students with projects where there is no honest way to frame a specific hypothesis. This is true of young labs, which may not have enough specific data to develop a good testable hypothesis for their system and are still casting about for a specific direction to take; and it's increasingly true of established labs that are using next-gen sequencing.
Cue next story: a student of mine was (and still is) part of a collaboration where we were doing bioinformatic analysis of genome-scale disease data. The other professor had funding and generated the data, which was basically sequencing RNA from an affected organ. There literally was no specific hypothesis other than "let's go see how this disease is affecting the spleen transcriptional response." This was then given to my student, who happily pounded away at the data for a few months (making many more trenchant observations about mRNAseq than about the disease, but nonetheless making progress). It came time for his committee meeting, and his committee insisted that he present a hypothesis. He cast about for a while, and finally come up with "there will be a differential transcriptional response to this disease in the spleen." This was nearly disastrous, of course, because it's simply not very specific! Sure, it's a hypothesis, and it's almost certainly true, but it's not specific enough to be useful. So my student nearly failed his committee meeting (note that I was a young(er) prof at this point, and hadn't seen this coming; my fault!) Why am I telling this story, though? Because my collaborator, who had generated the data in a hypothesis free manner, was a member of the committee, and was very disturbed by my student's lack of a hypothesis. Why? Because it was considered very important that our students be doing hypothesis driven science, even though neither he nor I had directed the project that way!
Before I continue on to draw a lesson from this, let me say: I'm not anti-hypothesis in any way. The student is, eventually, going to have to develop a hyp, or he isn't going to get his PhD; he knows that, and I know that. But we were still working on generating hypotheses from the data, and didn't have them ready at hand; developing the hypotheses was actually the first, very significant component of the project. Another point is that the committee was completely unprepared for this. And a third was that the guy who generated the data was so wedded to this hypothesis-driven approach that he basically ended up being hypocritical -- which I point out to him regularly :). (Another component that actually played a smaller part than I'd feared was the computational nature of the research: a certain subset of molecular biologists will vehemently deny that useful work can be done without a pipette man in hand. This either leads to ineffective one-handed typing in bioinformatics, or vociferous arguments among professors -- neither good for committee meetings.)
The lesson I want to draw from this anecdote is simple: hypothesis-driven science is dead!
No, no, not at all. More seriously, I think that as data generation becomes easier in some fields of biology, we should recognize that an extended period of hypothesis generation through discovery-driven approaches may be useful and necessary for many projects. Many biologists may not be any good at this, because they've been honed for decades to focus on moving as quickly as possible to a hypothesis based on a relatively small amount of hand-curated data; but in practice, hypotheses are now cheap (because data is plentiful) and I think we should focus on developing likely hypotheses and winnowing out the dumb 'uns computationally before we ever pick up a pipette man to test 'em. That is, expand the hypothesis-generation and analysis stages so that we're more likely to develop a comprehensive and interesting hypothesis.
About Models, and Model Systems
One of the limitations of the drive to proximal hypotheses is that you need to have tractable systems -- systems in which you can relatively quickly and easily test hypotheses. This leads to using models, and model systems. For example, Drosophila is a great model for genetics and development: it's been used for decades, and has led to at least one set of Nobel prizes for basic understanding of genetics. You can do lots and lots of things with it way more easily than you could imagine doing those same things in a mammalian system: mutagenize, resequence the genome from scratch, do all sorts of crosses in what appear to be a few weeks, etc. etc. But, whether you're interested in biomedical applications, or you're interested in population genetics, or whatnot, it's still just a model, and to build a connection to the broader set of science, you need to analogize the model in various ways. The bigger the field around the model system gets, the less the people feel the need to make the model explicit, and then the junior people forget about it. And so sometimes the model just doesn't apply. One of my favorite examples (just to pick on Drosophila and C. elegans, which are the two biggest invertebrate animal model systems) is from the early days of genomics. We sequenced mouse, and human, and Drosophila, and C. elegans, and saw that there were about 30% more types of genes and gene families in vertebrates. This led to a certain amount of breathless discussion about "the genes that made us vertebrates". Then we sequenced hydra (most emphatically not a vertebrate!), and discovered that it had almost all those gene families. Bang! It turned out that Drosophila and C. elegans were members of a monophyletic group, the Ecdysozoa, which had undergone extensive gene loss! So in some ways, Drosophila and C. elegans are really bad models for vertebrate genomics! They're from a relatively distant branch of the animals, they have small genomes partly because they were chosen for rapid breeding, and there are lots of things that are just different about them. They're still awesome, and they deserve a lot of study, but the history of genetic research on them really shows both the pluses and minuses of model systems: sometimes a model system that's great for one reason is horrible for another.
The same thing happens in ecology and population genetics, it seems to me. There's a lot of mathematical models that are simple and tractable and that let you "test hypotheses" about certain kinds of relationships, but then you have to determine how relevant those models are to reality. People would prefer not to spend that kind of time or effort -- because it's time and effort not spent generating and testing hypotheses. So the connection is made only for a few kinds of systems, which limits the vision of people doing research.
What about cancer?
I think another catalyst that made me think about all of this is the book The Emperor of Maladies, a Pulitzer-prize winning biography of cancer. There you see again and again how hypothesis driven approaches basically failed, while we slowly developed diagnostic tools and (frankly) guessed randomly about how to deal with cancer. Only recently have we started to gain an understanding of exactly what's going on at the genomic and genetic level, but it's still slow to make its way into therapeutic use; chemo -- killing the cancer slightly more quickly than the normal cells -- is still the main treatment, for chrissakes. Do you think we would do that if we had any other option?? Reading the book, the guy who developed the Pap smear (an excellent diagnostic for cervical cancer) did so on guinea pigs, because it was the only way he could detect estrus in guinea pigs -- by scraping the cervix. He spent 20 years trying to find a biomedical use for it! That's not hypothesis-driven science. Epidemiology has probably had a greater effect on cancer treatment than anything else, by tracking down the specific causes of various conditions like lung cancer, long before we were thinking about cellular mutations.
In my class the other day, the one where we talked about the 4th domain work, James Foster from U Idaho made the point that observation in biology used to be called "Natural History". One of the greatest successes of Natural History? Evolution, the greatest explanatory theory in biology, came directly from the synthesis of vast amounts of observation, with no experiment involved. It took decades for Darwin and others to put it together, and decades more for it to be validated in a hypothesis-driven framework (I'm thinking the finches, or the Lenski E. coli experiment, here; there are probably better places to cite that I don't know about).
When my Facebook friend & colleague talked about how we should stop bitching about data processing and start thinking about experiments, I'm pretty sure he meant that people should be better hypothesis-driven scientists. My instinctive reaction to that thesis is that he's not right (nor is he entirely wrong -- hypothesis-driven science is still necessary, just not sufficient!)
One of my current projects is working on a group of sea squirts, the Molgula, that underwent a dramatic morphological change in the larval form: many of the larvae lack tails. We want to know, how did this happen?
To address this question, we went out and generated about 600 million reads of mRNAseq from a variety of larval stages for a tailed sea squirt, a tailless sea squirt, and hybrid crosses between them. This has let us ask which genes are present, what their levels of expression are, and whether there is allele-specific expression of certain genes in one species over another (never mind, just trust me, it's important & interesting to know). In order to analyze this data - which amounts to about 80 GB of DNA, compressed -- we've had to invent a whole new series of data analysis and reduction tools. This is because the Molgula aren't well-studied model systems: they don't have genome sequences available, no large scale cDNA projects have been done on them, and the molecular tools for doing basic probes are still thin on the ground. It was far easier to spend \$20k on sequencing and get an answer in a matter of months -- even counting the development of the data analysis tools -- than it was to do anything else.
Are we going to now go out and take our high-throughput data and analyze it and conclude, voila, we know why the tails aren't forming? No, we're not that dumb! But we are developing several early hypotheses based on the data we have, and we're checking to see if they're plausible in the face of tissue-specific gene expression assays (WMISH). Then we'll go and do the hypothesis-driven perturbations to see: is the tail being specified and failing to extend? Or is it not being specified at all?
It's worth pointing out that virtually everything known about tail development in the sea squirts comes from one particular species, Ciona intestinalis, which is now a pretty established model system: genome, database, EST projects, a whole community. The Molgula, however, which look morphologically pretty similar, are about as far away from Ciona (evolutionarily speaking) as you can get and still be a sea squirt. Wouldn't it be fascinating to know how tails develop in them? Well, if we hadn't lucked into some excellent seed funding for the Molgula project and been able to generate and analyze the vast amounts of sequence, we wouldn't be on our way to looking at them -- this kind of study is seen as a fishing expedition, not worthy of being funded.
This is really the problem with hypothesis-driven approaches, and the priority we give them: they focus us on the questions that can be answered fairly quickly and easily, and not necessarily on the big questions. Sometimes it's possible to find a fundable route to those big questions; sometimes not. In the latter case, the questions go unaddressed.
The other big-ass data project I'll bring up is the Great Prairie Grand Challenge, in which the DOE JGI is sequencing literally terabases worth of DNA extracted from midwestern soil. The ultimate goal is to understand the microbial community composition and function.
Do we have any idea how to do that?
Well, the answer is, "not really". The field of metagenomics is still young, and it turns out to be technologically blocked. That is, the diversity of soil is so high that you need to sample it really deeply; but then the depth of sampling yields so much data, that you can't do anything clever with it computationally. This is one of the other focuses of my lab, and it's emphatically a long-term discovery-driven project. We have only a little idea of what we're looking for, and it's likely to be unrecognizable on the first four looks. We'll have to look and think deeply, AFTER solving the data analysis problems (which, again, I think we have. But it was really hard :).
One of my other favorite citations is that great Rumsfeld quote, about the known knowns, known unknowns, and unknown unknowns (in his case, with respect to invading Iraq -- oops). We know so little about biology that to restrict our gaze to the known knowns, or even to the known unknowns, is foolish.
Look again at this evolutionary tree of life, from Norm Pace's lab. We understand virtually nothing about the vast majority of those organisms. Sure, we can start to get at the commonalities of some aspects of protein composition, cellular organization, and genomics. But who knows what's out there? Certainly not me, and I suspect no one else. We have a long way to go.
To return to the original purpose of this rant, a lot of this "known unknown" and even more of this "unknown unknown" stuff involves looking at vast amounts of data and finding clever ways to grok the structure of the data, filter out stuff we think is uninteresting, and cherry pick the stuff that IS interesting. This is one of my focuses, and it is hard, specialized, time consuming, and wonderfully challenging. To hear other scientists say, dismissively, that we need to learn how to do proper experiments is a bit disheartening, and, even more problematically, rather short-sighted for the field.
Data -- especially the vast amounts of next-gen data starting to come from sequencers -- is usefully "hypothesis neutral". In Timo Hanny's defense of Chris Anderson's theory that "hypotheses are dead" in The 4th Paradigm, he pointed out that surely there is some point where "more" is different from "some". Being able to sensitively look at minor members of communities, or low-expressed genes and isoforms, will inevitably be informative; we shouldn't just discard it as "that useless discovery science stuff".
A key part of doing good hypothesis driven science is to come up with good hypotheses based on large-scale observations of biological systems. We should respect that initial stage of observing more than we seem to. My graduate advisor, Eric Davidson, told me the famous analogy about scientific practice being similar to a drunk, having dropped his keys in a dark alleyway, looking for them under the street light; while some people spend their career carrying flashlights into dark corners and doing a really detailed search, and others work on the flashlights, I think it's also going to fruitful to turn up the wattage on the street light so that all of those dark corners get illuminated. And we'll need sharp eyes to search all that newly lit territory. DNA sequencing is turning up the wattage; let's develop the methods to find the nifty stuff that we can now see.
Posted by Mick Watson on 2011-12-07 at 03:40.
I can add some comments on my frustrations about large NGS projects ;) First of all, when you're a well-funded group with very large budgets to spend on sequencning "everything", it's easy to forget that there are LOADS of people who would kill to have your problems - I know, I **used** to be one, and moved jobs specifically so I could be part of the digital deluge. So stop whingeing about the amount of data you have, you're lukcy to have it. Secondly, I VERY MUCH DOUBT that project leaders wrote in "the grant" that they would generate huge amounts of data that they would have serious difficulty managing, analysing and interpreting. If they did write that, and got funded, then I need to have a bit of what they eat for breakfast. No, what they probably wrote is that by sequencing all of this "stuff" that they'd find out loads of interesting information, develop some new methods along the way, and answer some fundamental biological questions. Great. So stop whingeing and go do what you said you'd do. And finally, discovery science or hypothesis-driven science, whichever you're doing, you definitely have to have SOME kind of idea of the questions you are trying to answer. I am hopelessly, cripplingly bored with "the 1000 genomes project", "the 10000 genomes project", "the million genomes project". Oh f*ck off will you?!!! I think the biggest and best outcome of the 1000 genomes project will be the bioinformatics developments that were developed and published, and that's a little bit great and a little bit sad. The impact of NGS on human health will not come from these massive, multi-centre, unfocused projects - they will come from the clinics, from smaller case-control studies, from patient studies in hospitals where we're already seeing NGS having an impact on how patients are treated. So why don't we fund more of the focused projects, and less of the massive, unfocused ones? The challenge of NGS is not even analysis; it's interpretation. And for that, I agree with Mike Eisen - go design some experiments.
Posted by Titus Brown on 2011-12-07 at 09:25.
That's quite the set of frustrations :). If funding priorities were at all aligned to solve your frustrations, I would be less frustrated myself -- that is, right now there's virtually no support for computational tool development, compared to the amount of money spent on generating data. As for the million whatever projects, sure; but many small labs are now doing their own "million" projects just without the funding or hype...
Posted by Matt on 2011-12-07 at 10:23.
I think you have hit upon an important issue-- the 1st step in developing hypotheses is understanding something about nature/biological processes/natural phenomenon.. Without this knowledge, we're stuck. Now, trying to get a natural history project funded-- well that is next to impossible.. Most of these large scale genome projects are really 'just' natural history-- natural history of the Homo genome, characterizing variation, noting interesting details or irregularities, etc.. These studies, done properly, would make Joseph Grinnell proud! In short, science needs a mix of both types of work, Hypothesis driven AND "Discovery Science"
Posted by marie on 2011-12-07 at 23:52.
You should take long flights more often - your rants are great! I particularly enjoyed this one because it allowed me to laugh at my own predicament of having to increase the scope of my project to accommodate a hypothesis-driven component (Aim 1) while really (secretly) wanting to do discovery science (Aim 2), along with proposing the development of improved computational methods to overcome obstacles to the other things I've proposed (Aim 3). It feels like overwhelming madness... can I cite your blog as a source to justify the virtues of discovery-based science? ha! And just to whine some more - I could just as easily spend all my time working on other people's pig-dog-bear-man projects because taking your course has apparently given me a magical knows-anything-at-all-about-the- buzz-word-of-the-day-NGS popularity. Or just maybe I actually learned something ;) Aside - could I presume that your "sequence everything" approach would also include "assemble everything" and "annotate everything"?
Posted by Titus Brown on 2011-12-08 at 09:36.
Hey Marie, I think the null hypothesis is that you've been blessed by the NGS magic wand :). And yes, good catch: sequence, then assemble, then annotate :).