Jeff Houlahan writes: > That said, science is many things - 'a predictive > enterprise, not some form of mindless after-the-fact exercise in number > crunching.' - fits under the umbrella but I don't think captures the whole > enterprise. Sequencing the human genome was, in my opinion, a version of > mindless number crunching (although perhaps somebody can put that effort in a > hypothesis testing context that I haven't thought of). I think most people > would be hard pressed to say it wasn't science. In fact, there is an > emerging field of statistics (data mining) that seems to be useful in > developing scientific hypotheses and is all about the 'mindless after-the- > fact exercise in number crunching'. My feeling is that data can provide > hypotheses or test them. When it does the first, it is a very useful part of > science but it is not predictive and it does not test hypotheses (null, > competing or otherwise). When it does the latter it falls ito the category > that Feynman was describing.
> I think the reason we often get these trivial tests of hypotheses is because > there is this sense that science is only about testing hypotheses - therefore > to do science I must test a hypothesis...whether there is a meaningful one or > not. In my opinion, science can also just be about looking for patterns that > we can use to suggest hypotheses. These kinds of discussions can quickly become pretentious, but I don't want this one to become so. There is a deep joy associated with doing science, and you're right of course, science isn't purely about prediction. It also has an exploratory component to it as well, where you go over the mountain just to see what you can see. Nonetheless, prediction is still our only measure of how well we understand the world around us, and no one has ever said that making these predictions was supposed to be easy. If it were, none of us would be getting the large salaries we're being paid. Nonetheless, your last sentence strikes a deep resonant chord with me. No one agrees more than I do that to do science we must seek out patterns. Robert H. MacArthur's first line in his 1972 book, "Geographical Ecology," is: "To do science is to search for repeated patterns, not simply to accumulate facts, and to do the science of geographical ecology is to search for patterns of plant and animal life that can be put on a map." But seeking out these patterns is only the beginning. The Latin word "scientia" is generally translated as "knowledge," but I much prefer to translate it as "understanding," it's alternate meaning, and there is a difference between the two. Understanding is by far the higher state of grace. There is only one science, regardless of what subdiscipline you engage in, and your statement that perceived patterns in the data can be used to suggest hypotheses has been said a hundred times before. It was certainly said most clearly by the astronomer Alan Sandage in the first few paragraphs of his 1975 book, "Galaxies and the Universe." Indeed, he precisely recapitulates your last sentence in his first paragraph: "The first step in the development of most sciences is a classification of the objects under study. Its purpose is to look for patterns from which hypotheses that connect things and events can be formulated by a method proposed and used by Bacon (1620). If the classification is useful, the hypotheses lead to predictions which, if verified, help to form the theoretical foundations of a subject." But he goes on to quite rightly say that doing just this is insufficient to doing science. In the end, we want to understand causation and mechanism. We want to understand the rules -- the physics -- that governs the system under study. We haven't done our job until we do achieve this understanding. Sandage continues: "Simple description, although not sufficient as a final system, is often an important first step... But as a classification develops, a next step is often to group the objects of a set into classes according to some continuously varying parameter. If the parameter proves to be physically important, then the classification itself becomes fundamental, and often leads quite directly to the theoretical concepts." Ecology has had this large psychological penduluum that has swung through its core over the last several decades. I first became involved in ecological research during the time of "systems ecology," in the late 1960's and early 1970's, a time of Lotka, Volterra, MacArthur, Slobokin and Hutchinson, and I was greatly entranced by the idea that there are rules that govern the interaction of life on this planet. But I was also impressed at the time that the psychological attitude then seemed to recapitulate that of The Golden Age of Reason, a time when Newton's laws of motion were first being introduced into Europe, where for the first time the world began to make sense, to the point that poetry was written about the effect: Nature and nature's laws lay hid in Night. God said, "Let Newton be!" and all was light. But the Golden Age of Reason was also a time of philosophical excess and overextrapolation. It was believed by many that the future was now predictable, if only you could measure the mass and momenta of every desk, chair, horse and carriage, and attempts were made to do just that. What was not clearly understood was the nature of random processes and how they fundamentally disturb the most explicit of equations, particularly on the small scale. This same grand extrapolation was true of the overreactions that resulted in programs such as the International Biome Program, in the decade following the development of the theory of systems ecology, which attempted to measure the mass and momenta of bush, insect, horse and carriage in the various biomes of North America. The unfortunate result was the same in both instances, a grand disappointment in the value of theory, to the point that when the graduate students who conducted the field work could no longer be denied their degrees and were allowed to become the next generation of biology faculty, opinion swung so violently that it became common to say that ecology has no laws and that biological populations represent nothing much more than random walks through time, space, genetics and demographics. Neither view is correct of course. The problem in ecological research is one of scale. If sufficiently large enough swathes of area and time are considered, fundamental patterns that are hidden by local noise are made transparently clear at the larger scale. And there remains great value in the *idea* of fundamental and realized niches, even if they can't easily be measured. Although the word "law" has fallen out of favor and is not even used in physics any longer, to be a "law" only means that a principle must be universally applicable, and we have a number of laws well in hand now for ecology and evolution. Our test will occur when we first explore newly discovered life-bearing planets where independent geneses of life have occurred. While we cannot reliably say anything now about the biochemistries that we will find there, we can I believe truly quite accurately describe the informational physics that must govern that life, Darwinian natural selection being the most pre-eminent of those laws. But we can name others as well: the species-area curve, the carrying capacities of environments, the evolution of internal information error-repair mechanisms, and the value of the evolution of sex. If these patterns aren't repeated on every alien world we encounter, we will be vastly surprised, and it will mean that we haven't properly done our work here. But my guess is that we won't be surprised, and that we will find these same patterns of life that we've discovered here reflected in those alien ecologies as well. However, saying all of this is a long ways from my initial posting, where I wanted to emphasize David Anderson's original point. We only advance our understanding when we work to segregrate the "truth" (in small letters) from an array of *plausible hypotheses*, not the trivial, obviously untrue "null hypotheses" that have become common in ecological research nowadays. We learn nothing of mechanism or process when we do the latter. Wirt Atmar
