Advice To A Young Scientist is a book by P. B. Medawar for folks keen on entering research. Medawar won the Nobel Prize for Medicine in 1960 for his research on why immune systems reject organ transplants. Medawar's writing is meticulous and a joy to read. Though the former half of the book deals with practical information for the newbie, the latter turns into a treatise on science and the scientific method. Not bad reading at all.
Excerpts from the book:
In this book I interpret "science" pretty broadly to refer to all exploratory activities of which the purpose is to come to a better understanding of the natural world. This exploratory activity is called "research," and research is my chief topic, although it is only a small fraction of the multitude of scientific or science-based activities, (which include scientific administration, scientific journalism which grows in importance with science itself), the teaching of science, the supervision and often the execution of many industrial procedures [...]
People who believe themselves cut out for a scientific life are sometimes dismayed and depressed by, in Sir Francis Bacon's words, "The subtilty of nature, the secret recesses of truth, the obscurity of things, the difficulty of experiment, the implication of causes and the infirmity of man's discerning power, being men no longer excited, either out of desire or hope, to penetrate farther."
A novice must stick it out until he discovers whether the rewards and compensations of a scientific life are for him commensurate with the disappointments and the toil; but if once a scientist experiences the exhilaration of discovery and the satisfaction of carrying through a really tricky experiment — once he has felt that deeper and more expansive feeling Freud has called the "oceanic feeling" that is the reward for any real advancement of the understanding — then he is hooked and no other kind of life will do.
[...] experimentation is a form of thinking as well as a practical expression of thought.
It can be said with complete confidence that any scientist of any age who wants to make important discoveries must study important problems.
After graduate students have taken their Ph.D.s, they must on no account continue with their Ph.D. work for the remainder of their lives, easy and tempting though it is to tie up loose ends and wander down attractive byways. Many successful scientists try their hands at a great many different things before they settle upon a main line of investigation [...]
The great incentive to learning a new skill or supporting discipline is an urgent need to use it. For this reason, very many scientists (I certainly among them) do not learn new skills or master new disciplines until the pressure is upon them to do so; thereupon they can be mastered pretty quickly. It is the lack of this pressure on those who are forever "equipping themselves" and who show an ominous tendency to become "night-class habitues" [...]
Too much book learning may crab and confine the imagination, and endless poring over the research of others is sometimes psychologically a research substitute, much as reading romantic fiction may be a substitute for real-life romance.
Following the lead of Bismarck and Cavour, who described the art of politics as "the art of the possible," I have described the art of research as "the art of the soluble." [...] What I meant of course was that the art of research is that of making a problem soluble by finding out ways of getting at it — soft underbellies and the like.
Scientists will certainly encounter and must work out some suitable means for rebutting the notion that, so far from trying to better the lot of mankind, the outcome of their work is to devalue much of what ordinary folk hold dear. Through science, you may hear, art has been replaced by artifice: portraiture by photography, live music by Muzak, good food by processed substitutes, and the old-fashioned crusty loaf by a chemically bleached or otherwise "improved," devitaminized, revitaminized, steam-baked, presliced parallelepiped in a polyethylene shroud.
I cannot give any scientist of any age better advice than this: the intensity of the conviction that a hypothesis is true has no bearing on whether it is true or not.
Problems to do with priority are especially acute in science because scientific ideas must eventually become public property, so that the only sense of ownership a scientist can ever enjoy is that of having been the first to have an idea — to have hit upon a solution or the solution before anyone else.
A scientist who is too cagey or suspicious to tell his colleagues anything will soon find that he himself learns nothing in return. G. F. Kettering, the well-known inventor (antiknock gasoline additives) and cofounder of General Motors, is said to have remarked that anyone who shuts his door keeps out more than he lets out. The agreed house rule of the little group of close colleagues I have always worked with has always been "Tell everyone everything you know"; and I don't know anyone who came to any harm by falling in with it.
Such a class distinction is particularly offensive because it is based upon a complete misconception of the original meaning of the word pure — the meaning that was thought to confer a loftier status upon pure than upon applied science. The word was originally used to distinguish a science of which the axioms or first principles were known not through observation or experiment — vulgar activities both — but through pure intuition, revelation, or a certain quality of self-evidence.
How often has it not been contemptuously said that "modern medicine cannot even cure the common cold"? What is offensive here is not the statement's falsity (it is true) but its implication: is it not pointless to pour billions of dollars into cancer research when modern medicine... and so on. What is wrong here is the almost universally held belief that clinically mild diseases have simple causes while grave diseases are deeply complex and are proportionately difficult to discern the causes of or to cure. There is no truth in either; a common cold, caused by one or more of a multiplicity of upper respiratory viruses and with an overlay of allergic reactivity, is an extremely complex ailment; so is eczema, most forms of which are baffling still. On the other hand, some very grave diseases such as phenylketonuria have relatively simple origins; some can be prevented, as phenylketonuria can be, or cured, as so many bacterial infections can be.
Harriet Zucker-man has shown in Scientific Elite, her study of American Nobel laureates, that in relation to the population "at risk," as actuaries say — at risk of making a contribution to science — the modal age at which laureates did the work that won them their prizes was early middle age.
[...] people with anything to say can usually say it briefly; only a speaker with nothing to say goes on and on as if he were laying down a smoke screen.
[...] an experiment is a contrived, as opposed to a natural, experience or happening — is the consequence of "trying things out" or even of merely messing about.
A young scientist has now a meter or so of bench space, let us say, a white coat, authority to use the library, and a problem that he has thought up himself or that a senior has asked him to look into. To begin with, anyway, it is almost certain to be a small problem — one of which the solution will facilitate the solution of something more important, and so on, until the long-term objective of the enterprise is in sight. Nonscientists cannot immediately see the connection between the lesser problem and the greater.
Thus the day-to-day business of science consists not in hunting for facts but in testing hypotheses — that is, ascertaining if they or their logical implications are statements about real life or, if inventions, to see whether or not they work.
A large part of the art of the soluble is the art of devising hypotheses that can be tested by practicable experiments.