As part of this, in the mid-1700s the development of better telescopes led to huge advances in understanding the stars and their motion. Among the pioneers of this work were William Herschel and his wife Caroline. They discovered Uranus as the then most-distant planet known, and galaxies, and began to reveal to us for the first time how immense the universe is.
However, other questions also arose, or so one would think. But when Herschel said to the Astronomer Royal "I want to know what the stars made of," the latter replied, somewhat annoyed, "What we're interested in, is mapping."
|Replica of the telescope the Herschels used to discover Uranus; Wikipedia|
Once, about 15 years ago, I was on a site visit to evaluate and make a funding decision on whether to award the requested grant. The investigator was describing how the trait, call it Disease X, would be investigated with the latest GWAS tools. This was that one required greater sample sizes than had been available before to be able to identify spots in the genome that might be potential causes of X, as the investigator proposed to do.
There had already been smaller studies that had rather convincingly identified about 5 or so genes that seemed to lead to high risk of the disease. The mechanism and reason that these genes might be causal were, however, not at all clear nor could anything be done about the problem for persons carrying the seemingly causal variation in these genes. By analogy to Herschel's question to the Astronomer Royal (What were these genes made of?), when I asked why the investigator was proposing to search for even weaker signals than the ones already known, rather than working on understanding how the latter worked, the investigator replied: "Because mapping is what I do."
In the 15 years since then, lots of mapping has been done in this spirit, and a modest number of additional genes or possible-genes have been found, but no real progress has been made in the treatment or prevention of X, nor has there been much increased understanding of the mechanisms of the previously known genes, nor any gene-based therapy.
This reveals the attitude of so many in science today. "What I do is collect [specify some form of] Big Data!" 'Big Data' has become a fashionable term that, when dropped, may suggest gravitas or insight. But we aren't doing astronomy and while we certainly are highly ignorant about much of the nature of genomes, when it comes to funding the study of disease, for purposes of public health, this is a lame excuse for business as usual. What we need are more instances of what is (also fashionably) called proof of principle: proof that knowing about risk-conferring genetic variants leads to doing something about it. That's very tough, and we have precious few instances of such principle in genetics, but we do have enough to suggest, to us, that we should not be funding further gene-gazing expeditions, into the astronomical realm of genomic complexity and the astronomical costs of the studies. We should be focusing and intensifying the efforts to know how to do something to alleviate the problems caused by the genes, and there are many, that we know about, or the problems that seem to be truly 'genetic'.
We are not supposed to be just star gazing with public health funds; society expects and is promised benefits (whereas only NASA expects benefits, in the form of more funding, for star-gazing; for the rest of us, it's basically no different from watching science fiction on television).
Science requires data, and we never have enough. There are areas where modern style beetle collecting is still very much worth doing, because our knowledge is sufficiently rudimentary. But there are areas in which we've done enough of that, and the challenge is to concentrate resources on mechanism and intervention. In many instances, that really has nothing to do with technology, but has everything to do with lifestyle, because we have clear enough understanding to know that the diseases are largely the result of environmental exposure (too many calories, smoking, and so on). Funding for public health should go there, in those important instances.
From a genome point of view there are certainly areas where primary data-collection is still crucial. To take one example, it has been clear for decades that we don't yet have nearly a clear enough idea of how mutations arise in cells during development and subsequent life, nor how those mutations lead to disease and its distribution by age and sex, including interacting with environmental components and each other. But identifying mutations and their patterns in our billions of cells, as they arise by age, and how they affect cells is a major technological challenge, far harder than collecting larger case-control studies for traits we've already studied that way before.