Page 1


How do you do Life Science?

Hans G Boman Essäist

How do you do Life Science? The essay is only published in English! Intoduction

Some forty years ago when molecular biology was new and hot, there was an inflow of ideas from physics. This cascade was sometimes quite forceful and it was not always welcome in old universities, still committed to a Linnaean thinking. This meant that life science was either botany or zoology sometimes with museums and an element of stamp collection. In many places departments of microbiology and genetics served as islands for the new way of asking scientific questions. Several scientists have written about what you may call a missionary attempt for how to do science. Myself, I remember the excitement caused by J.R. Platt’s paper ”Strong Inference” (1) vividly discussed for many years. Why was my present paper written? - Because I wanted to capture some moments of doing science and in a compressed form transmit my views to others. When I left Uppsala in 1958 for a post doctoral stay at the Rockefeller Institute, I had decided that I should leave method oriented research and make a shift to problem solving. My thesis on ion exchange chromatography of proteins taught me that the next best method was almost wasted time and effort. During my two postdoc years at the Rockefeller Institute for Medical Research in New York (now a University) I learned much about the conduct of science from talks with different ”Members” (no professors at that time) especially Friz Lipmann, but also from Rollin Hotchkiss and Gobind Khorana (then a visiting Guest). After my appointment as professor and chairman of a new department at the new

University of Umeå, I felt a strong need to persuade others about how to do science. My long term ambition was to build an American type of department in Northern Sweden, in a provincial hospital converted to a new medical school. Some scientists I had met in the US thought Umeå was a most exotic place to visit. Thus, I could early get a number of good scientists to come up and talk at our regular seminars. Also I gave a course in ”How do you do science?” and parts of the content of the present paper dates back to this teaching. In the 60-ties, starting a new university in a very remote place was a large scale political experiment. We should turn out physicians who wanted to stay in The North and predictions indicated a significant increase in jobs for the whole area. Thus for a couple of years, I interacted with politicians on several levels. My first paper on the methods of science was written in Swedish (2), because I wanted to have reprints both to give to graduate students and to handle over to politicians after discussions about what we were trying to do. Why do I now want to publish a paper with ideas from the 40 years ago? - Because I feel we are at a paradigm shift caused by the masses of DNA sequences available. Of course it is fine that we now have the complete genome of man and mice, Drosophila, yeast and the Elegant nematode not to speak of some 40 or more bacterial genomes. The problem is that in each genome there are 20-40% of the genes for which no known function can be ”extrapolated”. Thus we are facing in a gigantic scale a new way of doing science with new techniques and a tool called ”proteonomics”. This means that a large amount of scientific man power for economic and

political reason will have to leave the study of functions and searching for the molecules involved. Instead this is turned upside down: We have now lots and lots of molecules in search of functions. As I see it, the time of thinking like Platt (1) may be lost - not only the wisdom but also some of creative fun. At about the same time as Platt article came, Peter Medawar was writing on The Art of Science, (3) first; published in 1967. - How are discoveries done and can you learn anything from the past? - A volume dedicated to Max Delbrück in 1969 contained several interesting recollection from members of The Phage Group (4). In 1988 Georg Klein asked me for a contribution to a book about creativity that he was going to edit. By mistake I wrote in English, but my English draft could be published separately (5). Besides these references, I want to mention Beveridge excellent book ”The Art of Scientific Investigations”. It is the single reference I would recommend to all graduate students (and other interested). It was first printed in 1953, but there are many editions and my latest copy (6) was purchased in 1997 in Tucson, Arizona. W.I.B. Beveridge, was a British professor of pathology working on infections. The book is written for scientists in general, particularly young ones. It is a good reading, a practical book dealing with many things from experimentation to intuition and from imagination to writing papers and dealing with different personalities in science.

Three ways to study the science of science

Before going any further I must tell that there are at least three very different ways to study how science is done and/or best should be done. First there is a sociological approach, appreciated in social sciences, but not very much among natural scientists. The sociologists assume that

there is no difference what so ever between science and other human endeavors. Thus, scientist like all other people are working and acting for ”carrots”, that is rewards in the form of better jobs, more payment, more power, increased prestige and ultimately for prizes. Scientists themselves cannot be objective, their comments on their own work is therefore by necessity at best naive, at worst outright dishonest. Since the individuals cannot be trusted, statistics is the best way to describe the work of scientists. Thus, for a number of individuals they count the number of papers, judge the quality from citation index and/or honors like prizes, count the number of committees where people are members, look for promotions and so forth. Since people always are the same and behave in the same way this type of work should adequately describe the scientific process. Some members of the sociological school have also recently been digging into the history of science and one victim of such a ”reevaluation” was Louis Pasteur. However, even if sociology hardly can be the right way to describe science or its history, social motives are obviously of importance and they are natural in certain situations. This will be further discussed later on. Secondly, there is a philosophical approach called ”philosophy of science”. During much of the last century, Karl Popper was the leading spokesman of this approach. His main thesis was that in science you can never prove a hypothesis, only disprove it by showing that it contradicts experimental facts (or logic). Popper believed in deduction, but objected to the use of induction or intuition in science. The philosophers of Science never had any first hand experience of experimental work and this clearly was a significant handicap. Peter Medawar’s book ”Intuition and the Induction in Scientific Thought” (7) is an analysis of the philosophy of science in general and in particular a very

critical discussion of Karl Popper ideas. In this new century the core of Poppers ideas may look like ”The Emperors New Cloths” in thinking. In the middle of the last century, Thomas Kuhn was another well known philosopher of science who emphasized that science progressed in epoch, paradigms as he called them. However, he believed in a total breakdown of the old thinking when a new paradigm was borned and this idea was not generally accepted. Also Kuhn became quite isolated from his contemporary scientists and the term paradigm maybe what today remains of his thinking. George Klein has made a fine remarked about non-scientists writing on the conduct of science: He said it is possible for a person born deaf to write a book about music, describe how to build a fugue, a string quartet or a symphony and how to conduct an oratory, but in the end something will be missing. Thirdly, there are the descriptions and the analysis that scientists themselves have written down, an introspective way of describing science. Even if science can be done in surprisingly many different ways, there is a large consensus about the scientific method that most scientists would agree on. What counts at the end is if the scientific community at large will accept conclusions from new work. In order for science to proceed, it has to build on previous investigators, but there are really no needs for ”proves” in the way Popper stated. To give an historic example: no scientist would think of falsifying the penicillin structure. They would argue that the three-dimensional structure done by X-ray crystallography beyond any doubts shows that the penicillin structure is correct. As the structure was first deduced from chemical analysis and degradations an uncertainty remained about the symmetry of the molecule.

At the end there is always a need to convince other scientists, a task that can take quite some time (remember Mendel’s work had to be rediscovered after 40 years). The more unexpected the results are, the more independent data are required in order to convince. At early stages alternative interpretations are usually the rule, then the investigator must try to construct experiments that would discriminate between the alternatives. Finally, one may be able to say that the experiments are consistent with one claim and others may feel that data are reasonably good and convincing. However, Pascal was slightly pessimistic and remarked that old erroneous opinions do not disappear before their spokesmen dye.

My three assumptions

My present writing is based on three assumptions. The first is that each scientist may benefit from more or less regular analysis of his own motivations. At an early state in a scientific carrier it helps if you understand both the motivations of yourself as well as your potential super wiser. Later the situation may be reversed the more senior person will better understand his junior collaborators if both are clear of their respective motivations. The second assumption is that all research is always decision-making. You can always do something else than you are doing. If you think of one experiment, then there is always another experiment that you can think of. You have to decide which experiment will give you the best answer to the questions that you (or somebody else) have put up in front of you. Rational decision-making is based on motives, reasons and judgements. Thus, I will try to focus on arguments which are personal or general, but I leave out emotions as private. An important delimitation: there could be very good private reasons for doing one thing, but that is not the topic I want to discuss. Also, there are of cour-

se always practical limitations in terms of funds or time, but still there are almost always decisions. The third is the question about the way you like to define ”science” There are many suggestions depending on the purpose and the goal of the work. For this paper science is defined as the integration of facts into new knowledge. The facts themselves can be present before, or be collected as part of a research project. The importance lies in the two terms ”integration” and ”new knowledge”. The integration is an intellectual, a mental achievement which transforms facts into ”understanding”. It cannot be trivial and may sometimes require the optimal performance of the brains involved. The knowledge must be new, that is not known to anybody before. In practice this means not being published or registered in a data base. The elucidation of the DNA structure is a famous example of an integration. Watson and Crick had access to two carnal set of facts from other scientists. First they had ”Chargaff’s rules” that for each DNA ”An equals T and C equals G” and secondly they had Rosalind Franklin’s X-ray pictures. From these points of departure their work and the model building provided an integration of data to a new fundamental understanding. Not everybody will agree with the use of these three assumptions. To collect data without an understanding may be a legitimate and respectable occupation. The people involved often feel a pleasure just like stamp collection gives enjoyment. There may be moments of chance both in collecting data or stamps. At meetings you can share data just as you can exchanges stamps and all involved are happy in a congenial atmosphere even if an understanding seems remote. This is nothing to look down on rather it seems to reoccur as mega number of DNA sequences, unknown genes in completed genomes, se-

quences in search of functions. There is also a need to see the difference between soft facts and hard facts. Statistics and correlations are soft facts even if no other facts can be collected. There are people who think that soft facts and a lot of mathematics become hard facts, but that is not the case (pointed out to me long ago by Melvin Cohn). The famous atomic physicist Earl Rutherford once remarked that ”if you need statistics to explain your experiment, then you have done the wrong experiment”. An example of hard facts is the identification of proteins based on both complete (or reasonably long) amino acid sequences and convincing mass analyses. An identification of a protein based only on a Western blot analysis will have to be supported by several other independent data before becoming convincing as hard fact.

Motivations and Long Term Decisions

Motivations for research may not differ in principle from motivations for selecting a given professions in general. Of course there is the influence of parents, family and the society, socio-economic and cultural aspects as well as strictly private reasons. What may in some cases be different for scientists is the intensity by which the goals are pursued. Disregard weaker reasons, it may be possible to claim that devoted scientists may consider three main types of motivations as summarized in the Table 1.

TABLE I: Reasons to select a field of research - personal motivations Moral reasons (A1) - working to improve the quality of life

People driven by social motivations (A3) are those who work for the rewards of society, those who strive for promotions, prestige, power and prizes. As remarked earlier social motivations are naturally common. For scientists as for othA REASONS EXAMPLES OF GOALS ers motivations are mixed and they 1 Moral To decrease suffering and to improve human life shift during certain 2 Amoral Curiosity - of use to science, only periods of life. Most 3 Social To get a job, to make a fortune, to hunt for a prize people will have to make compromiMoral reasons (A1) mean situations in ses, that is at the same time to consider which somebody works on a problem re- several different motives. When one goal lated to a human disease or a third world is reached the next does not have to be of problem because he or she in the end a similar nature. This does not change the hopes to reduce suffering or improve the notion that everybody could benefit from quality of life. You can find this type of ra- an analyze of his/her own situation, sotionale among certain scientists in clinical metimes also of other people’s situations. medicine, in environmental sciences and There are many examples and a few dein cancer research. Those inclined to con- scriptions and the discovery of bacteriopsider moral reasons may also hold the hages given below is just one. My writing opinion that there are unmoral fields they is largely taken from Gunther Stent’s exwould not touch. It may apply to different cellent little book ”Molecular Biology of types of defence research, but it could Bacterial Viruses”. Another example is also extend to studies of the origin of life. given by James Watson in The Double Helix which shows how the mirage of a Amoral reasons (A2) stands for basic cu- great prize could coexist with curiosity as riosity and creator’s joy, and it should not a driving force. This book is also available be mixed up with ”unmoral reasons”, as as a paper bag edition with comments by specified above. Amoral means free from Stent. a moral dimension, that is people who are motivated only by the internal rewards of How to decide? - Six test queries the work. In an extreme form you find this For the selection of a scientific problem type of motivation in the mathematician the personal motivations can of course who proposed a toast for ”pure mathe- be applied again. However, assuming that matics” and added B QUESTIONS TO PUT TO WHAT TO LOOK FOR AHEAD OF START ”may it be of no YOURSELF use to anybody”. 1 Can I solve this problem? Methods, competence, help etc. Besides the purest 2 Input of work - So what? Is work input related to work impact? of motives there Trivial or fundamental? are in mathematics 3 Consequences at the end? and also in experiCan time improve or waste my work? mental sciences 4 Effects of time on work? Look around and count competitors aesthetic elements 5 Do I select a band-wagon? that are extremely Do I like to climb a ”new” mountain? pleasant to realize. 6 Do I select a challenge?

quality aspects, ”strong inference” will enter the judgement, it is possible to formulate certain queries which are interscientific. Table II - shows certain interscientific queries. TABLE II: Test queries for a specific problem professional judgments. The first three in Table II are all related to how you focus on a problem, the density of the question. The forth about time is something you must remember, but you can hardly do much about it before it is too late. The last two are sort of personality tests, sometimes useful to know about. The ”So what” question will apply to almost anything. However, the queries in Table II are meant as a set that should not be split up. It is an over-all judgment intended as an investigators guide. They may apply both to long term decisions (years) and short term decisions (weeks and months). Before any start, already at the planning state the fundamental judgement must be: Is this a problem that I can solve with my imagination, my financial means and my working capacity (B1 in Table II)? A question can easily be formulated that is premature, that is the means required are not available to anyone or just not to me. Medawar has analysed ”the art of the soluble” very clearly in a book with that name (3), which he in turn has borrowed from Arthur Koestler. Medawar’s goal is that a scientist should undertake the most difficult problem that he personally is able to solve. - If you take on too easy a problem, then you waste your talent. - If you start on a problem that is too difficult, you will waste both your own time and somebody else’s money! - The art of the soluble is to take on the most difficult problem that you can solve with the facilities you have, or expect to get, during the work.

At the beginning of an investigation or even before a single experiment it is critical to try and imagine what the result would be, what conclusions (new understanding) you will get from that experiment (B2). You should in advance be able to see your future results; you should see the plotted curves. - Then you should ask yourself: ”is this worth the efforts or will you (or somebody else) just say ”so what?”. And watch out, it is possible to do very nice experiments, but still not being able to conclude anything you did not know before. Piotr Kapitza was a famous Russian physicist who graduated in Leningrad 1919. He managed to move to England for a PhD and he soon joined the Rutherford’s school in Cambridge. He became the world expert on very strong magnetic fields and during his life he wrote a number of interesting essays about science in general and about his contemporary scientists (8). Once Einstein looked Kapitza up and wanted Kapitza to measure the speed of light in a strong magnetic field. In this way Kapitza could verify Einstein theory of relativity. However, to measure the speed of light, it’s not an easy thing and Kapitza refused. He believed that the speed of light was correctly predicted and he did not think that the experimental efforts were justified. The outcome was more or less predictable and Kapitza did not want to do waste his time in this way. Einstein tried every argument even that ”God would be pleased”, but Kapitza was unimpressed. A few years later the speed of light was recorded in a much simpler way. Thus, Kapitza was right in doing something else. Query B3 asks about the scientific density of the problem when it is solved. - Are you dealing with a fundamental or a peripheral question? At the start there may not be general answer. However, sooner or later you (or somebody else) may see the difference. It matters very much on the

job market, for promotions and for getting grants. In most human endeavors a feeling for quality and originality is valued, but even more so in science. Only rarely are doctoral theses fundamental science, that are not expected and can be possible only in very few situations. However, a talented graduate student may find out if he/she, or the ”super wiser”, is working on a peripheral or more fundamental question. Again, imaging what follows when the problem is solved. - Does it give a dramatic increase in understanding, then it is perhaps an important question. Many people who are working for their degrees are part of teams, and a few of these teams may be of world class and then the results and outcome could be fundamental. A dramatic increase in understanding is valuable as such. In addition it can give spin offs in the form of new drugs. If so, patents will be needed and potential conflicts of interest can follow (to be discussed later). Question B4 asks if time will affect the outcome of your work. Time is always limited and it goes by quite quickly. The time factor has changed the working situation for many a scientist. Of course if you work in a competitive field, where you know that there are several other groups which are trying to solve the same problem, then you must always watch time. It is important that fundamental results are verified and conclusions confirmed, but it is much nicer to be the first person who shows it. Thus, the time factor can easily affect the judgements of questions B1-B3. What was fundamental at the beginning could become trivial at the end. Especially, if somebody else has done it before and in a simpler way. Benzer’s and Nirenberg’s work, in the 50’s and the 60’s illustrate how time can affect a long term planning. Seymour Benzer is a physicist who early turned to biology

and started to work with the bacteriophage genetics. He selected phage T2, a relatively small virus and he realized that if he could map all possible mutations in a gene, he might be able to solve the genetic code. At that time the code looked to most people like an unsoluble problem far from ripe. But Benzer did a very clever selection of the gene to study and during the work he was the first to realize new genetic concepts (like the cistron) and he did important findings like mutational hotspots. However, when he had obtained something like 2/3 of all possible mutations something totally unexpected happened. It was the outcome of Nirenberg’s control (to be described further on under the heading ”To spot a discovery”). A race was started with Nirenberg, Khorana and Ochoa who rapidly worked out the entire genetic code with biochemistry. All the triplets and the redundancy was found within a very short time. Benzer was overtaken by a short-cut which was totally unexpected even for Nirenberg. As you may learn from reading Benzer’s own adventures (in ref. 4), he decided that it was time to quit. He started with neurobiology of the fruit fly Drosophila and he is still continuing these investigations combining genetics and cell biology. Some years ago he was awarded the Crafoord Prize in Biology for his ground breaking research on behavior, especially the influence of light and the finding of circadian clocks. Scientific band wagons do get going now and then (B5). What it means is that somebody else has been able to make a good judgement on queries B1-B4. When this becomes obvious to many people, there are always some who like to jump on the band wagon. Looking at science as whole, a band wagon leads to that things are really carefully checked which is good. However, it is the contrary to originality and of course it is suboptimal use of

grant money. But many people enjoy competition and in our culture we are always surrounded by competitive events, all our media are full of it. Even strange sports like women skiing combined with fast gun shooting can become front-page news. Of course some people cannot stand competition, they just get too nervous. Query B6 asks if you would like to do something that most people believe cannot be done? - I spent the summer of 1959 working in the laboratory of Gobind Khorana in Vancouver, B. C. At that time Khorana’s group were synthesizing di- and trinucleotides, a quite difficult thing without any solid phase chemistry. The ultimate long term goal grew and ended about 20 years later with the synthesis of a complete and functional gene for a transfer RNA molecule. In summer of 59 there was a TV commercial with musical hit song ”they say it couldn’t be done”. Thus every time a new synthesis was made, somebody was whistling or singing this slogan ”they say it couldn’t be done”. There is a kind of pleasure in doing something that other people think is difficult or impossible, it is a challenge. Literary speaking scientists may only rarely be mountain climbers although I have met one, Gilbert Adair in Cambridge, England. However, there may be something in the psychology of a challenge which is related to mountain climbing. A climber does not regard every mountain to be worth his effort. It should be a mountain that is difficult enough, perhaps a mountain that nobody else has climbed before. Literary this time is gone. People are now cleaning the slopes of Mount Everest from the trash left by earlier expeditions. This happens also in science. In the concept of mountain climbing there is also a statement about the driving force of some scientists. Again, what is the sense in doing something that anyhow will be done relatively soon by somebody else? I have felt certain sympathy for this state-

ment and it may be related to our ambitions. You can afford to ask this question when your social motivations are fulfilled. However, if you are not alone there is also an issue of responsibility, once well stated by Sol Spiegelman (who pioneered DNARNA hybridization). After a seminar he replied that ”this was the question about how many graduate students you wanted to sacrifice on a problem”. As the scientific society is constructed, there are only very few situations when you can undertake a real challenge, because either you risk your own future or you risk somebody else’s future. If you do it, you have to have a certain confidence that it is worth the risks and the suffering.

Creativity in general

What is creativity and why os it inetersting? - Creativity is a problem-solving capacity of the mind, the ability of the brain to produce novel and unexpected answers, answers reaching at one extreme from a repartee in an ordinary dialog to the other, the solution of an artistic or scientific problem of a high complexity. Creativity is rewarding in a number of ways. First of all, most societies are interested in problem solving and there are strong external rewards both in private and public sectors. In addition there are also strong intrinsic rewards: Mastering a profession that requires a complex technology, organizational skill and moments of creativity can produce high satisfaction. The very moments of creativity are also rewarding because they generate a very strong feeling of physical pleasure. Creativity at a low level could be a stimulating conversation that contains moments of unexpected surprises just as it is boring to know in advance what somebody is going to say. The very rare moments of the highest levels of creativity require long periods of mental preparation, and they generate not only an extreme pleasure, but also an extreme fatigue - the mind has

been operating at the very limit of its capacity. At all levels of creativity there is use of the subconscious part of the mind. A lot has been written about creativity in science and I have already referred to my reading of Medawar (3,7) and Kapitza (8). My favourite list also includes the English mathematician Littlewood (10) and collections of autobiographic writings, like the volumes dedicated to the geneticist Max Delbrück (4) and the biochemist Severo Ochoa (9). Here some outstanding scientists about the background and the circumstances at the times when they made their discoveries. Readings of similar type is also included in certain volumes of Annual Reviews but tend to differ a little in interest and originality. Creativity can show up anywhere in human life. Humour is a most enjoyable form of creativity as shown in writings from Hasek to Mark Twain or Orwell, in movies by Chaplin or in Carné’s ”The Perfect Crime” or in cartoons from Doré to Thurber. There is of course a special form of verbal creativity best seen in Joyce’s Ulysses and Finnegan’s Wake. There is an everyday form of creativity of cooking and there is sometimes also a creativity in crooking as shown in the ingenuity needed by hackers to create data viruses or break safety codes. I do not think that there is a special type of creativity exercised for instance in the life sciences. I rather think that there are strong similarities in the working processes in large areas of the natural sciences and the creative elements are probably the same in science and in art. Look how many time times the word ”art” is used in titles of the references. There are two things which have to be linked to creativity, necessary in order to produce results of lasting quality. The first is a strong motivation, that is the rationale, the reasons by which one explains one’s own driving force or passion for the work.

There are the three classes of motivations already discussed in Table I. However, there is not only a reason and a direction; there is also an intensity factor. Some people consider science to be a hobby; they may think that all problems are more or less equally interesting and that the life of a scientist should be relaxed. The opposite extreme does also exist - people who work because of a neurotic drive, people who cannot take a real vacation because after a day or two they are always uneasy or even miserable when they are unable to work. For some of these people and for others science is a deadly serious business that is linked to an ambition to do a first-rate job. Thus, there are Captain Ahab’s hunting white whales and golden apples not only in literature but also in science. Some people are extremely creative, they produce good ideas all the time, but they may be failures in science, because they lack self-discipline. Creativity can produce dozens and dozens of ideas, you cannot work these out at the same time. If you cannot choose between your own creative ideas, then you are lost. You must have self-discipline enough to be able to say ”This is what I will do, I’m going to discard my five other ideas as being less good or important.” Creative must be joined with self-discipline in order to work. The masters of Science realize the right moment when the scientific development and the available techniques render a difficult problem solvable (Medawar’s thinking again). Natural science is very much of an international enterprise and this means that you are more or less competing with the best minds of your contemporaries. Consequently, you cannot be honest and humble at the same time. You may not have to tell it to everybody around, but you have to believe in yourself. In one way or another you must trust yourself to

have a fair chance to solve the problem you have selected. In practice this means either that you should be able to solve! it before somebody else does it, or that nobody else has been clever enough to spot this problem at the right time.

The controlled use of creativity

As stated creativity must always be combined with a rigorous self discipline. Experiments are done in order to understand the laws and the rules of nature. For most of the time this means hard working along lines that are logically deduced from previous sets of experiments. A working hypothesis may already be present and the experiments are designed to disprove or support it. This is the craft part of science and it does not need to have very much to do with creativity. In this way it is often possible to clarify quite many problems, and consequently a good deal of science can be done and is done without much use of creativity. However, now and then the experimental data obtained do not make sense that is they do not conform to the logical thinking of your planning. There are two possible explanations: (a) Something is wrong with the experiments, or (b) something is wrong with the logic. This may sound awfully simple, still it is not that easy to realize when it happens to you. It is easy to conclude that one has arrived at an unsuccessful experiment, but the difficulty is to have enough confidence in one’s experiments. To put it the way I used to each graduate students: There are no unsuccessful experiments; there are either sloppy experiments or experiments that did not turn out the way you thought”. The latter is the case when creativity has to enter, although Delbrück once talked about doing experiments according to the ”the principle of controlled sloppiness”. The situation of being stuck in science is an interesting and stimulating one. To

handle such a plight requires a combination of craft and creativity. The first thing to do is to go back a number of steps in order to find out exactly when and where logic disappeared. For those who have a tendency to cut corners more work is usually needed. In any case when the critical point has been identified a new and better working hypothesis has to be found. If one wants to be really strict, one should produce not only one but two hypotheses formulated in such a way that they mutually exclude one another. The reason for this is that experiments can never really prove a hypothesis; they can only disprove it (this reasoning touches the philosophy of science discussed in the introduction). In the everyday life of experimental biologists the dual hypothesis way of working is rarely followed. It is often difficult enough to formulate a first hypothesis that is consistent with earlier data, and one usually ends up with a number of independent experiments that are all consistent with one hypothesis. In many ways this is an oversimplification of what actually happens. First of all experiments can almost always be refined, errors can be reduced, parameters considered trivial can be found to be important and so forth. The search for explanations and new hypotheses may go hand in hand with new exploratory experiments and require long periods of what Littlewood called vague thinking. This phase of an investigation can finally end in three different ways. First, the investigator may find the problem too difficult to solve; then he has to give it up and turn to another line of work. Secondly, he may find a trivial explanation and be able to return to his previous concepts of working. Thirdly, in rare cases he may realize that he has arrived at the beginning of a discovery. Several times I have returned to Medawar’s ”The art of the soluble” as the ultimate way of doing science. - The question is, how do

you do in normal science? - You may still have to define a problem in such a way that you know that you can get answers to it with the tools available. However, you may have to be less demanding and more modest about queries B1-3. The methods available change with time. Suddenly, you can buy an expensive kit that would let you do the crucial experiment in just two days while before it took weeks or months. Another alternative often liked and used is to collaborate. There may well be somebody else who could help you with crucial experiments.

The art part

One must respect intuition in science. Littlewood has called this the ”art of vague thinking” (10), something like the creative moments in art. A painting or a sculpture is taking shape during the work and the same can apply to a piece of science. And there may also be the same pleasure in the work. At this stage, the application of logic may even be counter productive. There is also an element of art in the planning and a perfect experiment has a specific beauty, an esthetic element. Some scientists can use their ingenuity to design experiments in such an elegant way that a maximum of information is obtained from a minimum of work. Other scientists master the art of semi-rational planning always leaving a limited part for their intuition. This is what Linus Pauling once called ”the stochastic method” - you guess and you guess right. Meselson and Stahl did a classical experiment which showed the semi conservative replication of bacterial DNA. They used heavy isotopes during in vivo synthesis and took samples at different times. When they analysed the DNA with gradient density centrifugations, they could separate the new and the old double helices of DNA and show an intermediate with one heavy and one light chain. That was a new

technique, an elegant art in solving a classical problem. Most people enjoy esthetic elements, both when they do certain experiments and when they read about them in journals. There is a special art in designing reproducible experiments which at the same time move you forward. I would call it a partial overlap, so that you reproduce the main point of the previous experiment, but at the same time you add something new that was not shown in the previous one. In this way you may construct a whole paper by a series of overlapping experiments where you add one point after another. If you can avoid it, never reproduce an experiment in exactly the same way as you did before. Only if you run into serious problems and cannot reproduce anything, you have to go back and try again. But probably there must be a mistake, contaminated chemicals, wrong notes or something else. In general to proceed by overlapping experiments will take well care of both progress and reproducibility. What can you expect from nature? That is again something you can learn both from reading and from observations of nature at work. It has nothing to do with logic, logic may even ruin it. Nature is relatively predictable and talented people are very good in guessing exactly what nature does. Crick ones stated that ”you have to hear when nature shouts at you”. It is more or less the same thing as Pauling’s ”stochastic method”. An increasing part of today’s science aim at the understanding of causality chains with many interconnected links and branches. The beginning and the end of each chain should be cardinal information, still many scientist are very fond of receptors in the middle of a chain even when they do not know what is at the very end. This is certainly the case in immunology, maybe also in gene control. Sometimes it is label-

led as ”signal transduction”. Also this type of problem solving can be aided by a feeling for how nature works and a useful way of reasoning is the teleological argument: If one thing is there, then it must have a function. Otherwise it would not be there, it would have been lost during evolution. This argument will have to be used with an understanding of evolution and applied to forms of life that are not so domesticated that an evolutionary perspective has lost its justification. Erasmus Darwin was the grandfather of Charles Darwin. He was a natural scientist who long before his grandson had ideas about the evolution of life. However, compared to Charles he was probably more intuitive, more imaginative and less organized. Littlewood quotes Erasmus Darwin as recommending: ”Every so often you should do a damn foolish experiment”. Himself, he played the trombone for his tulips (10). Another way is when running a 10-20 test tube experiments, to insert a few extra tubes for gambling or ”long shots” which meet the suggestion of Erasmus Darwin. It can give your experiment an extra emotional thrill and you may also find something, but you have to think ahead. Long after Erasmus Darwin there was also a useful statement: ”Don’t waste clean thinking on dirty enzymes”. It was attributed to Arthur Kornberg and he has used it but he claims that he learned it from somebody else. Anyhow it is important to identify the weakest link(s) in your chain of scientific arguments to see the difference between soft and hard facts. To spot a discovery How to discover something you do not know to exist? - Probably there are two or three main ways to answer this question. The first one is to be able to understand an unexpected and unplanned finding as when Becquerel found an unexposed film

to be darkened by radioactivity from a thorium in a test tube stored beneath the film. Something slightly different is to realize that you have got a totally unexpected experimental result, for instance from a control. This was the case when Marshall Nirenberg found out that polyU was the messenger RNA for polyphenylalanine. He was interested in protein synthesis in vitro, he was using TMV RNA as the messenger and as control he wanted an absolutely inert RNA that could not code for anything. Somebody nearby at the NIH had polyU - an artificial man-made RNA. He used it with a mixture of labelled amino acids suitable for making the TMV core protein which also contained labelled phenylalanine enough to give the rather insoluble polyphenylalanine. He got much more incorporation in the control than with the viral RNA. He realized that this could be the very first unfolding of the genetic code and he concludes that three uracils coded for phenylalanine. Another way is to start on something that might exist, but has not appealed or appeared soluble to fellow scientists. This may be ”The Art of the Soluble”. When a new area of work is opened up, it happens that there is a band-wagon phenomenon, lots of scientist start on more or less the same problem. Nirenberg started such a band-wagon and very soon protein and RNA synthesis became highly competitive. It may be difficult to spot a discovery at the moment of publication. Almost every year one to three papers will be published which in 10-20 years will be the foundation for Nobel Prizes. Can you spot these papers when they are published? It is not as easy as it sounds. You may even make a discovery yourself without seeing what at that moment is not so obvious.

To talk about science

The ability to make oral presentations is important for scientists at all levels. Previously, it was common in Europe that a scientist applying for a professorship submitted all his publication. And the experts consulted were expected to read every paper. Not so any more. Now the applicant has to list his/her 10 best papers and to give a seminar about his/her ongoing work. A department chairman or his search committee will have time only to glance at selected best papers. Then someone will choose to use the telephone to check references and schedule an interview after the seminar. Oral presentations can be learned and they can be improved. One way is to rehearsal. The academic traditions in some European countries often lack this habit. At all good schools in the US people (also professors) rehearsal. Another way offered by many teaching departments is video tape of a short speech. Politician and company directors use this method all the time as it is offered by special consultants. You can then see what other people see, how you perform. It is rather helpful when given time to repeat and to improve. In science you must communicate, you must be able to convince your fellow scientists that you have done something important. Quite many journals have special forms that they want referees to answer. A common question is if the paper is dull reading. You must avoid to be dull both in oral presentation and in written papers. An entertaining article about ”The Art of Talking about Science” is by Lawrence Bragg (11). He suggest as a criterion for a good speech that the next day the listener wants to tell his wife about the main points (or if she is not interested, a friend on the subway train). A bad talk is when the listener the next day does not remember the main points.

Conflicts of interests

A lot has been written about this topic and it is important to face such problems in advance. There are ethic guidelines and examples in a very useful leaflet entitled ”On being a scientist” (12). The writing was done by a committee of members of American Academies and it is commonly used in the US. The booklet is not a list of rules, it is a collection of examples of conflicts of interest. It is left to the reader to find out how to solve the conflicts outlined. It is a practical warning on complications which can occur in a research group. As an example, there may be an internal competition within a group because the leader wants to be promoted. He could then be tempted to overemphasize his own contributions and perhaps be inclined to reduce the role played by a junior co-worker. Patent questions is a special issue that goes hand in hand with the growing biotechnology industry. Some universities and large research institutes have adapted their own rules and every new scientist has to sign an agreement on these rules before starting to work. If no general rules are valid, try early after a finding to sign an agreement on how to divide the credits and patent rights. Then there is something called personal chemistry, not all personalities in science enjoy each other.

The pitfalls of science

The human eye For many day-animals including humans, vision is the most indispensable of the senses. It is hard to imagine that among our ancestors a blind individual would have survived. In some cultures blinding was also early used as the next sever punishment, both among Gods and their apologetics. If you compare the resolving power of the eyes of a hawk (or many other birds) to that of human, the top flighter is much superior. Thus, it is an irony that visual impression of forms and structures has been the scientific tool most used in the past.

Clearly, the use of the brain for sorting and organizing visual information has compensate humans for their rather poor ability to collect and distinguish different visual impressions. The eye has evolved in order to find food and perhaps mating partners. Naturally other senses are also involved, I am only suggesting that vision is the most indispensable. However, for scientific problems like evolution and development it is certainly misleading to to think that what you see as shapes and forms are more relevant than the chemistry of life. Thus, vision is the most seducing of the tools of natural science. Humans are evolutionary inclined to believe what they see and often reluctant to accept what they cannot see with a naked eye (or a magnification device). Just look at an issue of Nature or Science and record the number of advertisement which offer scientists help to visualize their findings. Since during the evolution of Homo sapience a reasonably good vision had a strong survival value, visual information has a tendency to capture also scientist, especially biologist. Not so among physicists and chemists who early had to learn abstract thinking in order to investigate invisible things like electricity, magnetism or the composition of the earth’s atmosphere. In these branches of science numbers were used early, while biologist like Linnaeus and Darwin used only visual forms and shapes as data and for conclusions. In genetic crosses Mendel combined numbers and simple visual characteristics. However, neither Darwin nor Mendel knew about the existence of microbes and this is something often forgotten even among todays scientists (because you don’t see them or you don’t think about them). In 1999 the full genom of the nematode C. elegance was published in Science. The editors had judged what was most important and arranged for comments on neurobiology (a lot) and evolution (much less), but they totally disregarded bacteria which is the food of the

nematode. Bacteria are at least 2 billion years older than C. elegans and there never was an evolution of nematodes, there was only the coevolution of a vast number of bacteria and some worm ancestors. Of course microscope provides structures and colors which gave us the knowledge of the eukaryotic cell and as well as a way to group bacteria by the Gram staining. Later electron microscopy provided an increase in resolution to the extent that one sometimes had arguments about what one was looking at. Still when Archaea were discovered, they looked pretty much like ordinary bacteria and in retrospective it may be hard to imagine the heated arguments that were exchanged even when an evolutionary clock - the small unit of the ribosome - indicated that Archaea differed significantly from ordinary bacteria. It was the size and the vision which were superficially similar, so similar that it was emotionally unacceptable to many scientists that they in fact were looking at organisms from another kingdom. And of course in the bottom there were again electrophoresis and PCR of the 16S RNA but the differences recorded concerned molecules and could be described by numbers and sequences. As stated in the beginning, a scientist must always convince fellow scientists (editors and journal readers) about the validity of his experiments. Still to me it is quite surprising to what extent life science still relies on pictures rather than on numbers. And the method that outnumbers all other is electrophoresis (sometimes renamed as Southern, Northern or Western blot analysis), still an homage to Arne Tiselius who invented the method and analysed the results first by recording refractive index of moving boundaries of proteins and then simplified it to electrophoretic mobility in paper strips afterwards stained by brom phenolblue.


It is hard to state which is most important in life science, logic or vision, both can be extremely useful and also misused to the extreme. One must realized that everything that can be deduced by logic from present knowledge is in a way trivial. There is no way to use logic to discover the unpredictable. In the beginning, in the explanatory phase of an investigation intuition and imagination are the chief tools that may lead from one set of experiments to the next. It is often claimed that women are better than men when it comes to these talents. If at this stage things seems unlogic, it may in fact signalize that something novel is being discovered. What helps is a sort of common sense, a feeling of what to expect from nature. Still it must be repeated that with pure logic (and no creativity) it is possible to make many important contributions to different fields of science.

The scientific freedom

As a concept, this is more or less the unicorn of science. Of course everybody is free to think whatever he likes, but if he wants to show it experimentally then grant money is required and if he wants to print what he is thinking there is normally an editor to pass. It is often argued that university employment should involve a large, if not unlimited degree of freedom to do science. This is sometimes the case and many grant giving institutions pride themselves by allowing their research money to be used with a large degree of freedom. However, in the end the freedom is often linked to a quality judgment, those who first-rate science will have freedom to continue, while those who are less successful quickly may lose both their freedom and their grants. On top of this comes ethical and moral judgement from the society and from the scientific community itself. For animal work, more and more journals now require an ethical permit before they even like to review a piece of work. Pressure groups like animal rightists often join with antiintellec-

tuals with the aim of curbing many type of biological experiments. Wether created or not, nature is in some way sacred. There was a time when recombinant DNA work required working permissions and at present we have in Europe a strong public resistance to gene-modified plants, while in the US and Canada this issue does not cause too much concern.


All through the history of humankind, there always were many people who felt that almost everything was known and that science would soon come to an end. Even good scientists can get the notion that The Golden Age has come and there will be no more excitements to expect. Naturally certain branches of science like human anatomy reach an end, no more bones will be found in the human body. This just illustrates how foolish it is to have narrow academic disciplines. I do not think disciplines as such exists, they are only human steering mechanism used by politicians to allocate money or by universities for describing curricula for students and to avoid gross misuse of professorships. What we can spot in nature are just problems and they can be investigated by all suitable tools. It does not matter if they belong to what we in daily languish call chemistry, physics, ultra structure or something else (often referred to as disciplines). Many people still think that all micro-organisms are known, that they are deposited in the American Type Culture Collection or described in Bergey’s Manual for Determinative Bacteriology. That was never correct. As it looks today, approx 1% of the microbial flora is known, because the rest cannot be cultivated by the methods now in use. Linnaeus divided the living world in plants and animals. He believed that God had created everything and put Linnaeus in charge of just the organizing. When Pas-

teur and Kock founded microbiology, most microbes were considered as plants, only protozoa became animals. Only slowly the kingdoms of animals and plants became three because all microbes were named protists and added as a separate kingdom. Now we have got a new kingdom, the Archaea, and a discussion about what kingdoms really should mean. When the first sequence of an Archaea bacterium was published in Science in 1998 only 3538% of the genes were known or could be interpreted. Thus, the living world is much larger and much different from what we thought only 10 years ago. As stated in the introduction, in many biology departments during the 60-ties ”strong inference” was replacing ”stamp collection”. Now things have suddenly changed, the emperor has got new cloths. We have a completed human genome hailed by scientists, presidents and prime ministers as a scientific break through. A new epoch in life science has begun and we should expect enormous benefits in forms of both natural drugs and a cure of genetic diseases. Maybe we had a type of Kuhn’s shift in paradigm around 1970 and maybe we are facing another one in the beginning of this new century. As it looks today (and probably tomorrow) with Nature Insight (13) ”Functional Genomics” (whatever in may become in the future) is needed to organize the most enormous stamp collection ever made. To integrate these data into a biological understanding may take a very long time with only soft correlations. Hopefully, new types of technology will be born which will reduce the waiting time and improve understanding, perhaps facilitated by new disciplines like ”proteonomics”. Given this background one may ask: Which are the qualities needed to make a scientific discovery today and tomorrow? - It is obvious that sheer intelligence is useful and it is equally clear that there are some very

bright people in science who do not produce quite what might be expected from them. Other attributes needed are creativity, an independent mind, organizing capacity and originality, and the right mix of these qualities is critical. There are some highly creative people who cannot control their creativity and be organized enough to work through the long and perhaps boring periods of self-discipline needed for the verification of a brilliant idea. Originality is somewhat more difficult to pin down. In part it is a capacity to combine mentally very separated entities into a novel unit. Some people do this all the time and they may be mistaken for nuts. Of course there are also real nuts in life, and in the scientific community it may be quite difficult to judge the appearance of brightness and originality, the shapes and shadows of personalities. In the end the only thing that counts is the output, the productivity of first-rate science - that is how well the ghost in the machine works. Towards the end of a piece on how to do science it is finally relevant to ask: What is luck and why is it that scientists ever so often speak about luck? - It is an old problem, and more than a hundred years ago Pasteur pointed out that luck can only strike the prepared mind. It is not always easy to reconstruct one´s own creativity or to understand if one’s own mind was prepared at a given moment. Thus, people say that they just had luck and that was all it was. And real luck in a more trivial sense does certainly happen also to scientists. What it all boils down to is the fact that luck once or possibly twice can happen to anyone of a number of gifted scientists, but that repeated luck is real talent or even genius.

References 1.Boman, H.G., ”Varför forska: Motivation för individ och samhälle”, Läkartidningen,66: 2918-2928 (1969).

Hans G Boman, Professor emeritus. The 27th of May 2002.

2.Platt, J.R. ”Strong Inference”, Science 146: 347-353 (1964). 3.Medawar, P. ”The Art of the Soluble”, Methuen & Co LTD, London 1967 4.”Phage and the Origins of Molecular Biology” (Eds. J. Cairns et al.) Cold Spring Harbor Laboratory of Quantitative Biology, Long Island, N.Y., 1969. 5.Boman, H.G. ”The Art of Science. Craft and Creativity”, Perspect. in Biol. Med. (1989). 6.Beveridge, W.I.B.,”The Art of Scientific Investigations” Vintage Books, Random House, New York. 7.Medawar, P.”Induction and Intuition in Scientific Thought”, American Philosophical Society, Philadelphia 1969. 8.”Collected Papers of P. L. Kapitza”, Volume 3 (Ed. D. ter Haar) Pergamon Press, Oxford 1967. 9.”Reflections on Biochemistry” (Eds. A. Kornberg et al.) Pergamon Press, Oxford 1976. 10.Littlewood, J. E. ”The Mathematician´s Art of Work” in The Rockefeller University Review, Sept. Oct. 1967. 11.Bragg, L. ”The Art of Talking about Science”, Science 154: 1613-1616 (1966). 12.”On Being a Scientist. Responsible Conduct in Research”, National Academy Press, Washington, D.C. 1995. 13.”Functional Genomics”, Nature insight, Nature 405: 819-865 (2000).

Hans G Boman gets the Nordic Fernström Prize 2000

Hans G Boman, Essäist Hans G. Boman was born in Stockholm 1924. He became BSc in chemistry 1950 and received his PhD in 1958 at Uppsala University. His dissertation dealt with chromatography of phosphates. In 1958 he emigrated to USA and took up a position as a research associate in Fritz Lipmann’s laboratory at Rockefeller Institute for Medical Research, New York, where he was working on protein syntheses of bacteria. In 1963 he became associate professor of molecular biology at Uppsala University. He became Sweden’s first Professor in microbiology at Umeå University in 1966. In Umeå University he discovered that the main mechanisms behind the resistant of the bacteria was either a specific enzyme of the bacteria that degrades penicillin or mutations in the cell membrane that block the absorption of penicillin. From 1970, first in Umeå and later at Stockholm University, until his retirement in 1990, the focus of his research changed to new areas. He then studied the insects’ mecha-

nisms of defence to bacteria and later, in collaboration with Viktor Mutt, professor at Karolinska Institutet, antibacterial peptides in pigs and humans. The systems of defence that insects have were found to be more or less identical to those in all living organisms. As professor emeritus from 1997 at the Department of Microbiology, Tumor and Cell biology, MTC, at Karolinska Institutet, he succeeded to show in 2002 that patients with Kostmann’s disease lacked antibacterial peptides. His biography ”A life of a stubborn biologist as told by him” was also published in 2002. The Essay is only published in English. Eva Cederquist, the writer of Hans G Boman’s biography (translated by Barbara Klockare).

Profile for Barbara Klockare

How do you do Life Science?  

Hans G Boman about How do you do Life Science?

How do you do Life Science?  

Hans G Boman about How do you do Life Science?

Profile for ki200