How Not to Do Philosophy of Science:
A Guide for Makers and Consumers
John D. Norton
Department of History and Philosophy of Science
University of Pittsburgh
This page at www.pitt.edu/~jdnorton/Goodies
Good philosophy of science is done this way:
Formulate and state clearly a strong, interesting and novel thesis and argue cogently for it.
This recipe is easy to state as an abstract conception. We can point to many excellent examples of it. We each have our own favorites. I am a great fan of Carl ("Peter") Hempel and Wesley ("Wes") Salmon. They were masters of the craft. Their writing is lucid. Their logic is precise. They make it look easy. Consult any of their works and make emulating them your goal.
It is a real delight for me when I come upon a new, well-crafted example of good philosophy of science. Too often, however, I come across work that is quite well-intentioned, but falls short.
Over the years, I have come to see that there are several ways this can happen that are often repeated. I collect some of the ways here.
My purpose is to offer guidance to philosophers of science who may be uncertain about just what their business is. If you see enough flawed examples, your own conception of good work can become corrupted.
My goal also is to offer guidance to those who read and listen to philosophy of science. "Is this good work?" you may ask. It may sound erudite and polished, but if it falls into one of the problems below, whatever else it may be, it is not good work in philosophy of science.
In each case, it is easy to fall into the problem. New ideas in philosophy of science are hard to find. This truism is easily overlooked. Finished, polished work in philosophy of science has an effortlessness to it that masks the labor needed to formulate it.
We need all the help we can get to find novelty. We are surrounded by many strong, well worked out ideas already in the literature. It is all too easy to grasp onto them and repeat them. But that is not novel work.
There is no recipe that guarantees success. I can only give you an assurance that finding novel ideas is hard. They often start in distant, feeble glimpses. You might be puzzled not by what people are saying, but by what they are not saying. Today, you have a nagging but inchoate thought that won't go away. Tomorrow, it is the central of claim of your next paper.
Where can we find these glimpses? Any of the approaches below might provide them. The new idea may emerge when we delve into the history of a science or when we scrutinize a science's logical structure. These efforts and the others like are the preparation.
When our goal is novel philosophy of science, these preparations have only succeeded when they have led us to the novelty. Sometimes that just doesn't happen. Not all prospectors find gold. Then you may decide to keep looking. Perhaps digging just a little deeper will bring rewards. Or you might decide that it is time to move on and look elsewhere.
To do otherwise is to fall into the problems I will describe below.
When you first read philosophy of science, you are immersed in a flood of different ideas on many different topics, coming from many perspectives. It is easy to add to the flood. It is easy to add remarks and asides that add small drops to the torrent. If you collect enough of them, you might even have something of the length of a paper.
However a collection of thoughts and observations, no matter how well-informed, no matter how erudite, no matter how extensive, is not yet a good piece of philosophy of science.
Good philosophy of science provides a well-structured understanding of some area of science. The pieces connect and, in the case of the strongest analysis, the edifice stands as a whole. You cannot take out one piece without bringing it all down.
That good philosophy of science has this structure follows from that fact that, at its core, are strong, interesting and novel theses. Such theses are logically strong. That means that they have many consequences. Accommodating these consequences into a consistent system is the providing of the structure that good philosophy of science needs.
A scientific realist, for example, asserts that we should construe our best scientific theories literally. The realist is then committed to developing an account of why such literal construal is sustainable, given the repeated history of failure of what were once our best theories.
On the other side, a scientific antirealist refuses the realist's invitation to literal construal. The antirealist must then develop an account of how so many scientific theories enjoy impressive successes, if they are not capturing the truths of the world.
Each of these, realist and antirealist, will develop an account that supports and sustains their core thesis. It will automatically be structured around this defense.
Good philosophy of science requires a good knowledge of a science. That does not merely mean some abstract conception of what science is about. One needs to have a deeper understanding of at least one science. Otherwise one is merely speculating from a distance.
Getting that knowledge is an essential preparation. It is common for good philosophy of science to include expositions of a science of special interest. The expositions may well be admirable examples of the science popularizer's craft.
The trouble comes when it stops there. An exposition of some piece of science, no matter how erudite, is not philosophy of science.
The way to identify this mode of failure is to ask yourself "Just what was the philosophical thesis advanced?" and "Just what reasons were given for me to believe the thesis?" If you cannot answer quickly, there is trouble. If your answer is "..., but I learned a lot of cool science." then you have an instance of this problem.
Scientists sometimes think that the value to them of philosophy of science is that it will guide them to the next great theory. I like to think that this might be so. We subject the foundations of a science to critical scrutiny and it might well happen that this scrutiny, absorbed by a prepared mind, can lead to novel breakthroughs.
However creating new science is not our business. It is the business of the scientists. They have just the expertise needed and they have the background. They are steeped in the minutia of their fields. Our expertise is different. We trade in precision of thought and unforgiving critical analysis. That is not the best way to new ideas.
More than once I have talked with a scientist about some piece of speculation that I condemn, in high dudgeon and with some justice, as irretrievably muddled thinking. The response is not to deny the muddle, for it is undeniable. Rather it is: "Yes, but it has proven fertile in finding new science!"
That might well be a good response for someone whose goal is to find new science. It is a dangerous one for a philosopher whose goal is to understand with all clarity our present science.
If you want to make novel contributions to a science, you are better off working directly in that discipline. Whichever it is, it will be larger than the minuscule fragment of philosophy of science devoted to that area. There you can surround yourself by people and by work all devoted to the creation of the new science. Perhaps then you might just have a chance to create some new science.
A put down of philosophy of science is attributed apocryphally to the eminent physicist, Richard Feynman:
"The philosophy of science is as useful to scientists as ornithology is to birds."
May I offer this rebuttal?
"Ornithologists are not trying to be useful to birds."
It is rewarding when work in philosophy of science proves useful to scientists. This happens, I suspect, much more than they know. So many of the general notions scientists use in their work are actually the product of philosophical analysis.
However it is important for philosophy of science to set its own standard of success. That standard cannot be that someone working in another field, even if neighboring, approves of the product of our labor.
I believe in the value of history. My own work has a strong "HPS'ish" character. I am all but unable to resist delving back into the history of science as part of almost any of my philosophical projects. It can be essential to them.
If the thesis at issue depends on some claim about "What Einstein did," then it matters that I really do have a good grasp of what Einstein did. And there is a wonderful sharpness, depth and subtlety at the moment of creation. It is dulled in later accounts, for the urgency of the moment is lost.
However history of science by itself is not philosophy of science. The history can inspire or support a philosophical thesis. But, once again, it is preparatory. The historical scholarship must eventually lead up to a definite thesis in philosophy of science and a definite argument.
In recent years, there has been a flourishing of work in the history OF philosophy of science. These reservations apply equally to it. It can be enormously interesting to learn, even in great detail, the philosophical ideas of one of the greats of the past.
However reporting their thoughts is still just history. The next step has to be taken. Can we extract from their work a thesis that we advocate now? Can we extract a good argument that supports it?
While we ponder these questions, we should bear in mind that we are not the first to read the words of this or that great philosopher. They are acknowledged as greats because their contemporaries or later generations saw the value of their work, studied it, wrote about it and incorporated it into their thinking.
Might it be that the truly important in their work has already been extracted and incorporated into our modern tradition? Is this really the best path to new, interesting philosophy of science?
What compounds this last worry is that all philosophers are inhabitants of their own era. Things change. Sciences develop and often in surprising ways. It is hard enough for good philosophers to see farther than those of their time. It is harder still for their ideas to do this centuries later.
Whitehead wrote a memorable quote (that might look a little different if put in its context):
"The safest general characterization of the European philosophical tradition is that it consists of a series of footnotes to Plato."
This quote encourages us to be humble. It is a universally praised virtue and it is easy to make a show of conforming. However it gives us poor advice if we seek new philosophy. I am, in the end, less impressed by erudite footnotes to Plato. (See "Unstructured Wisdom" above.) I am more impressed by a well-structured piece of novel philosophy of science, where Plato is in the footnotes.
Good philosophy of science clarifies science by making the imprecise, precise. Sometimes, the source of an imprecision in science is a lack of mathematical precision. Here a focus on mathematics can be decisive. Replace muddled informal analysis with something mathematically precise and the confusions may just dissolve.
There's the problem--they may dissolve. But they will only dissolve if the problem is a lack of mathematical precision in the first place. If that was not the problem, then adding more mathematical precision will not help. Rather it is likely to hinder finding a good solution. For greater mathematical precision typically brings greater complications and these complications may just make it that much harder to see clearly what the real problem is.
When a project translates something less rigorous into something mathematically more rigorous, the question that must be asked is this "What philosophical problem has now been solved that could not be solved before?"
In the worst case, the mathematics brought in can have problems peculiar to it. Then, when we end up laboring over those problems, we kid ourselves that we are somehow clarifying the original problem.
Mathematical precision should not be an end it itself. It is like a vitamin. A little can be good if we happen to be deficient in just that vitamin. It does not follow that a lot is better; or that a dose of vitamins is always a tonic.
One of the greatest achievements of science is the discovery that one can organize a body of knowledge into axioms and their logical consequences. It can clarify greatly just what are the ideas and content of some branch of knowledge.
However I am quite wary of axiomatization done purely for its own sake. To formulate some body of knowledge axiomatically often requires simplification, so that a logically tractable system can be specified. There is now a real danger of oversimplification and that we overlook the danger since we are distracted by the logical demands of building a complex axiom system.
Once again, the question to be asked of any axiom system is "What philosophical problem has now been solved that could not have been solved before?" In the case of axiom systems, the good answer is most commonly that certain foundationally important inferences are now enabled, that were not enabled before; or some are blocked, that were formerly thought admissible.
An especially fraught form of this danger is when the axiomatization involves some symbolic formal system. Then we risk the dual dangers of axiomatization and excess mathematical precision. That we can restate matters in symbolic language is not, of itself, an advance.
Once again, an axiom system, especially a symbolic one, may have problems that are peculiar to the techniques used to axiomatize. When we grapple with those problems, we may kid ourselves that we are addressing problems pertinent to the original problem.
Precise terminology is essential for good philosophy of science. Without it, precise theses and arguments are unlikely, if not impossible. Since scientific systems can be complicated, it can be a major project to provide unambiguous naming of their parts and the philosophical conceptions we apply to them.
Thus a preparation for successful philosophical analysis often includes proposing a terminological taxonomy.
Once again, offering the taxonomy is only a preparation. Its value lies entirely in its enabling us to formulate theses and arguments that were, prior to it, out of our reach.
The danger is that we might simply be restating what we already knew well enough, but now in elevated language that gives the misleading impression of new learning.
Finding the right question can often be the hardest part of philosophical analysis. My experience has been that, sometimes, finding the right question comes at the end of the project. One struggles through all sorts of hunches and complications until one has achieved some clarity. One then presents the result as a question and its answer.
The key thing in all this is the answer. An elaborate narrative that ends up with a probing, suggestive question is, at best, preparation. If there is no answer, the analysis has not delivered a result. The analysis has been made public prematurely.
An oblique form of this problem comes in narratives that are elaborate displays of learning and erudition. One marvels at the depth of scholarship, the many sources cited, their obscurity and the rich detail in the footnotes. And it all seems to be deeply philosophical, since the narrative is liberally sprinkled with philosophical terms of art.
However, as the narrative unfolds, one question remains open: "Just what is the claim advanced?" Instead of finding a clear statement, we have suggestive questions and queries. We are invited to ponder and think, to reflect on what we may take for granted, to open our horizons and be ready contemplate the unimaginable.
At best these invitations are preparation for the analysis that should have been given.
Big ideas in philosophy of science are commonly interconnected. One starts with one and soon finds oneself entangled with another. So it is very easy to tackle one problem and find that its solution resides in the solution of another problem.
There is a danger with this reduction of one problem to another. It may happen that the new problem is more opaque and more intractable than the one with which we started. My rule of thumb is that this danger has been been realized when we are told that the present problem is solved by notions of:
explanation, understanding, simplicity
and you can likely add your own terms to the list. Getting clear on just what is going on in each of these has proven to be major and long-lived puzzles.
When one is tempted to reduce an easier problem to a harder one, you should recognize this as a danger sign. You have not solved the problem. You have just relocated it and in a way that takes you further from a solution.
Sometimes the relocation will take you back to where you started. We will understand A, we note, with a fuller understanding of B. If we stop at that, we may overlook a common second step: we will understand B better, when we have a fuller understanding of A. These circles are common in philosophy of science when we face an intractable problem.
Copyright, John D. Norton, November 12, 2016, December 9, 2017.