How do you know when a scientific problem is finished? Biologists have been cracking open the cell and studying its molecular insides for a very long time now. How much more is there to learn? Perhaps it seems obvious that we are still missing much: we can't cure cancer very well, for example. On the other hand, one could ask, what's really keeping us from curing cancer, a lack of basic understanding or insufficiently developed technology? Nowhere is this problem of defining a scientific endpoint more obvious than in the community of scientists who are focused on some of the most basic questions in cellular and molecular biology - the community of yeast biologists. Yeast biologists now have to figure out what human biologists will be asking in the decades to come: what does it mean to solve a cell? Are there any big questions left in molecular biology?
Yeast biologists have been ahead of the curve
Like the pioneering molecular biologists who used E. coli to crack the genetic code and work out many other of the most fundamental and universal cellular processes, yeast biologists have been focused on basic questions relevant to essentially all cells. E. coli took center stage in much of the Nobel-prize winning work of the 1950's and 60's. Single-celled baker's yeast hit the scene as a major model system a little later, really taking off in the 1970's when scientists used it to study problems such as how proteins are modified as they mature into their final forms, and what basic machinery is involved when cells divide. Studies teasing apart the control system regulating cell division resulted in a Nobel Prize, as well as a much deeper understanding of how our own cells (including cancerous ones) divide.
The community of yeast scientists has continued, for 30 years, to stay at the forefront of nearly every major development in molecular biology. The yeast genome was the first eukaryotic genome to be sequenced, and nearly every major genome-scale technology was first pioneered in yeast, including whole-genome DNA chips, systematic cloning of all genes in an organism, and genome-wide studies to discover which regulatory proteins bind which genes.
As a result of being ahead of the curve for so long, baker's yeast is one of the most well-characterized organisms on the planet. Scientists have some idea of what most of the 6000 yeast genes do, and many of the yeast metabolic, structural, information processing, and control systems have been worked out in great detail. Perhaps the best way to see this is to look at the Saccharomyces Genome Database, which contains essentially everything we know about the most well-studied eukaryotic cell. To see what kind of information is there, go to the database and type in the name of a gene in the search box. (If you happen to be that rare person who doesn't know the name of a yeast gene, try Cdc28.) For most genes, we know where in the genome they are located, which regulatory proteins turn the gene on, where the protein hangs out in the cell, what other proteins it interacts with, what biological process that protein is involved in, what happens to the cell when you delete the gene, and much, much more.
When have we asked enough questions?
In other words, we know a lot about most of the genes in yeast. And some day soon this database will be complete - we will have detailed information in the database for every gene in yeast. We will have completely mapped the molecular insides of this particular organism. On that day, we will face a critical question: is yeast solved? Have we learned all that we need to learn about this particular research model system? When should the community of yeast scientists call it quits?
This question is not just a problem for the small group of biologists who study yeast. It is a question all molecular biologists should be asking themselves. Once the yeast database is filled, do we just go on and fill the databases for the other model research systems - worms, flies, mice, and finally humans? Or let's think about it this way: when we declare yeast solved, we are setting the standard for everything that comes afterwards. Will we be satisfied when we understand human cells as well as we understand yeast cells? What will it mean for a human cell to be solved? (And will we be able to cure cancer then?)
I hope it's clear that this is more than just a question of where to put our limited scientific resources. This question is about the intellectual agenda of biology for the next century, and again, yeast biologists have a chance to be ahead of the curve and foreshadow the science of the future. Yeast biologists have the chance to prove that the future of biology will not be boring.
Boring? It's hard to imagine biology today being boring; most people think it's one of the hottest sciences around. But if you look at where yeast biology is today, or 5-6 years down the road, and take that as the gold standard of what it means for a cell to be solved, then all the rest of molecular biology is just filling in details. The pathbreaking biologists in the 1950's, 60's, and 70's made all of the important conceptual advances, figuring out the system of DNA, RNA, and proteins that make all life run. A few other later discoveries added to this picture: RNA can be an enzyme just like a protein, and now we know that RNA can also regulate genes. We have major conceptual outlines (and often more) for basic, universal processes such as sugar, fat, and protein metabolism, as well as information processing pathways. What this means is that very few basic, near-universal processes are left to be discovered. We aren't going to find many more new types of RNA molecules, important metabolic pathways, or signal transduction cascades. What's left is to fill in the details, for yeast and for humans - no more major conceptual advances remain.
Is that really true? Obviously I don't think so, or I wouldn't be writing this piece. But the danger of limiting ourselves to detail-filling is real. Scientists, especially younger ones who don't like the idea of boring career in the decades ahead, need to set the next major intellectual agenda for molecular biology. A major aspect of that agenda needs to involve turning molecular biology into a quantitative, predictive science.
We can sharpen our intuition here by thinking about cancer. When we've filled in all of the details of interest about a human cell (actually, it would be one human cell type, such as a fibroblast, out of the hundreds of cell types - there is a lot of detail-filling left to do for all cell types), can we rationally design new cancer drug? Given a particular type of cancer, with particular molecular characteristics, can we design a drug that will shut down just those cancer cells, and leave the rest of the body's cells unharmed? To do this, we need to be able to predict what will happen, to a cancer cell and a healthy cell, when you knock out a particular protein or biological process with a drug. We need a predictive model - something more than just verbal reasoning, because verbal reasoning quickly gets swamped by the cell's complexity.
A new style of science
The key problem is to take the information in the databases, all those details, and put them into quantitative models. This involves a different style of science from what has typically prevailed in molecular and cell biology. (This has been less of an issue in biochemistry and genetics, fields with more of a tradition of making mathematical models). Instead of asking questions like what is protein XYZ doing during a stress response, researchers should be asking, how do the interactions between protein XYZ and a half-dozen other proteins work together to produce the dynamic, quantitative behavior we observe when a cell decides to divide?
What does it take to do this kind of science? Two things, which have been sorely neglected in the training of most biologists. First, scientists have to be able to put together mathematical models and explore their dynamics. Engineers and physicists frequently get this kind of training in nonlinear dynamics, but few biologists do.
The second requirement is the ability to do difficult experiments involving measurements in single cells (as opposed to a large sample of billions of cells) over time. These kinds of experiments often require newer techniques and instruments, ones which many biologists aren't exposed to during their training - too often, grad students spend much of their time on more conventional techniques asking conventional questions. To identify the parts of the cell and what those parts do, traditional experimental methods focusing on billions of cells are very effective. But to get beyond those more conventional research questions, we need to make measurements on individual cells as we follow them over time.
The focus of a growing number of labs is on these more forward-looking questions, and not surprisingly, many of these labs are using the most well-studied cell they can get their hands on - yeast. If we can make conceptual advances in yeast, then there is hope for research on human cells as well.
A research group led by Fred Cross and Eric Siggia, at the Rockefeller University is using math and single-cell experiments to probe the dynamics of the commitment to cell division. When a cell decides to divide, it moves out of a 'resting' state into a replicating state. In these different states, different proteins are active, because in each state different tasks get accomplished. But how does a cell move from one state into another? And once it enters the replicating state, what keeps it from sliding back into the 'resting' state? Verbal reasoning isn't enough; it turns out that the irreversibility of this state transition can be explained in terms of positive feedback loops.
Another group, led by Roger Brent at the Molecular Sciences Institute in Berkeley, California, is studying another yeast decision process, the commitment to mate. Brent's group is making an effort to obtain detailed measurements on the information-processing pathway involved in yeast mating. This information processing pathway has to be robust to molecular noise; on the scale of a yeast cell, molecular fluctuations are a big deal, and pose a signal-to-noise ratio challenge for cells seeking information about the environment.
So is the future of biology boring? It obviously doesn't have to be, but the danger is real. Once the databases for various organisms fill up, scientists may start to jump ship and start filling in the details for the next organism in line. And without a doubt, there is a lot of this work to do: we really do want to understand a human cell the way we understand a yeast cell today. Yeast has 6,000 genes, which we have almost figured out; there is a lot more work to do to figure out what all 20,000 human genes do. The good news is that the technology is advancing at a spectacular rate, and projects that take advantage of this technology will ensure that figuring out human cells won't take the 40 years per 6000 genes that it took for yeast.
It is good news then that the yeast cell is far from really being solved. It's time for younger scientists to think about a new style of doing science, considering new types of research questions, and adopting the technology necessary to study those questions. If we succeed in yeast, it means that we won't some day fill up a human genome database and then ask, now what? We'll know what direction to take, how to build and test predictive models. We will be able to design cancer drugs that effectively kill cancer cells without damaging healthy ones. And we'll keep biology intellectually exciting for at least the next century.