Genetics' Next Frontier
In 1974, I published a paper entitled "The genetics of Caenorhabditis elegans ," also known as the nematode. Its first sentence read: "How genes might specify the complex structures found in higher organisms is a major unsolved problem of biology." This remains true today. How do genes build organs, bones, or skin and specify their function? Has our slowness in finding out been due to our difficulties in choosing the right organism to study?
Until the early 1960's, biology's great-unanswered question was far more modest: how does DNA determine the simplest of proteins? But then it became clear that all you have to do is get a gene and sequence it, get a protein and sequence it, and simply translate one into the other. In principle, we could learn what genes do just by reading their chemical language.
Of course we didn't have the right tools at the time. We did have primitive tools to sequence proteins, so we could figure out their chemistry. But we could not tackle the chemistry of genes. All we could do was follow the standard--and painfully slow--procedure established by Gregor Mendel, the 19 th Century founder of genetics. According to Mendel, a gene's presence in an organism is confirmed only when we find an alternative form of it, called an allele . For example, Mendel could not say that there was a gene for tallness in a plant species until he discovered dwarf mutants of the same species.
This approach defines genes according to an organism's observable characteristics. Fortunately, technological progress lets us define genes much faster than Mendel could. With the discovery of genetic recombination in viruses that penetrate rapidly reproducing bacteria, it became possible to measure variation in offspring much more minutely, and thus to dissect the fine structure of a gene.
So it was natural by this point for biologists to ask whether a similar approach would crack the genetics of more complex, multi-cellular organisms. The rule from the earlier research on bacteria was to obtain mutants and study them as deeply as possible. What was needed was an organism with a rapid growth rate, like bacteria. This would provide us with lots of genetic variation, enabling us to analyze the genes fully.
I was interested in the nervous system, and thought it important to study it in a way that it could be summarized in the form of a wiring diagram. The plan was not to trace genes directly to behavior, but to separate the problem into two questions: a developmental question ("how do genes build nervous systems?"), and a physiological question ("how do nervous systems or brains generate behavior?").
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The idea was to study mutants of C. elegans in the hope of finding mutants of genes that regulate behavior. But even in an organism as simple as C. elegans , our technological limits made it extremely difficult to pinpoint the function of genes. We started by studying muscle, simply because it gave us large amounts of proteins.
The invention in the mid-1970's of technology to clone and sequence DNA opened new vistas for research, and its use on humans and other mammals has been enormously successful in terms of scientific discovery. But the development of genetics has remained dependent on the ability to study model organisms like C. elegans and Drosophila (the fruit fly).
In fact, the great risk nowadays is that with so many genetic descriptions of organisms pouring out, we are drowning in a sea of data but are moving further away from understanding biological complexity. The basic functional units of all complex living organisms, it should be remembered, are cells , not genes. What we need now are cell maps and maps of how cells talk to each other.
Our first job is to say how many different cells there are in a complex organism. I think we can now say that for C. elegans . But for vertebrate organisms like ourselves, we are still very far away.
This brings us to the need to reflect on human beings--not just the human genome--as subjects for biological research. This struck me recently while I was attending a meeting on the mouse, which is a model for human beings. The meeting proposed that we create a genetically mixed pool of 30,000 mice. We would train people to go around examining these mice and diagnose high blood pressure, diabetes, greed, and so forth. Then we would study the genotypes of these mice--the particular variants of their genes.
The problem is that we are technologically incapable of mapping 30,000 genotypes. But it occurred to me that even if one could map 30,000 genotypes, why would one work on a mouse? After all, we already have many highly trained people to examine subjects, namely physicians. So, when technology permits (and I think it can and will), why don't we work directly on humans?
The right way to do this would be to work with a population where everybody is anonymous.
We can prove that we understand the genetic structure of a human disease by synthesizing the same disease in a mouse. But the very purpose of using model organisms is to confirm what we find in the real thing.