Crick's tips on biological research

 

CRICK'S TIPS ON BIOLOGICAL RESEARCH

 

David W. Brown

 

ABSTRACT

 

      Francis Crick is perhaps the greatest theoretical biologist of the twentieth century. A common error limits the appreciation of the possible greatness of the Crick-Mitchison theory. A century or two might pass before the world sees another theoretical biologist as great as Francis Crick. Leonardo da Vinci observed that the good student excels the teacher. Thus a good biologist should study Dr. Crick's Sunday Morning Service in Crick's book ‘The Astonishing Hypothesis’. A righteous researcher should reverence The Gossip Test, The Baffling Hypothesis, Rocking the Boat, The alpha Helix, How to Live with a Golden Helix, Theory in Molecular Biology, Triplets, Conclusions, and Epilogue in Crick's book ‘What Mad Pursuit’. Seven synopses summarize Crick's advice. The value of theses tips might extend beyond theoretical biology into medical diagnosis and general problem solving.

 

INTRODUCTION

 

     I suggested(1) that Crick and Mitchison's note(2) on the function of REM sleep might be the greatest paper ever written in the field of psychiatric medicine. The point is that if, during REM sleep, undesirable modes of interactions in neural networks are not removed properly, then a variety of psychiatric symptoms might result. The Crick-Mitchison theory might give a framework for understanding some aspects of schizophrenia, mania, depression, Parkinson's disease, and Tourette's syndrome. From such a foundation of understanding, better theoretical models of psychiatric illness might result.

     In a review(3) of their original paper, Crick and Mitchison admitted that they blundered in suggesting the slogan 'We dream in order to forget.' They(2) never intended the slogan as more than a half truth to be used as a mnemonic. They really should have made a more complex slogan such as 'We dream in order to adjust our brains to accommodate the changes involved in learning and juvenile brain growth.' Their slogan has two bad results. Some people seize upon the half truth and proclaim it as a whole truth representative of the Crick-Mitchison theory. Worse still, a few people seize upon the half truth and extrapolate from it to arrive at their own theories which are modifications, oversimplifications, or distortions of the Crick-Mitchison theory, and then these new theories are tacitly presented as the Crick-Mitchison theory. Thus Crick and Mitchison have an important tip for us: 'Your words can and will be used against you.'

 

     In addition to Crick and Mitchison's original paper (2) and subsequent review(3), I studied Crick's book ‘What Mad Pursuit’ and encountered numerous suggestions that scientific researchers might find useful. I am not the only one impressed by Crick's suggestions on doing scientific research. In a review(4) of Crick's book ‘What Mad Pursuit’, Nobel Physics Laureate Philip W. Anderson stated: ‘The basic goal of physics is not mathematical elegance or even the achievement of tenure, but learning the truth about the world around us.’ Crick's words are as good a guide to that end as I have seen. Crick's tips on research may help biologists, medical doctors, physical scientists, and anyone else who deals with science.

 

WHAT ARE CRICK'S TIPS?

 

     Crick's tips are not quite a working philosophy of doing science but instead a scattering of helpful hints. Mentioning one chapter from one book(5) and nine chapters from another book(6), I present a mixture of paraphrase, quotation, extrapolation, oversimplification, and commentary. My stream of consciousness replaces Crick's coherence.

 

From ‘The Astonishing Hypothesis’

DR. CRICK'S SUNDAY MORNING SERVICE:

 

     Experiment is great and theory is trifling. New experiments suggest new ideas and refute old ideas. Philosophers talk about a problem in order to clarify the problem. However, philosophers make no real progress in solving the problem because they discuss the outward manifestations and ignore the scientific instruments needed to penetrate the inward fundamentals. The language of the philosophers is inevitably the wrong idiom, because experiments dictate the words needed to describe the facts. Scientific experiments determine scientific theories which replace vague impressions and traditional myths.

 

     Consciousness is, in the twentieth century, a fundamental mystery but science has solved many mysteries. The aim of science is to explain all aspects of nature. If consciousness and all other real things belong to nature, then what are the claims of religion? What is religion without divine powers in a supernatural realm? Does the hypothesis of the supernatural realm lead to anything productive? 'Dream as we may, reality knocks relentlessly at the door.'

 

     People are relentlessly curious. Curiosity, when combined with science, leads to truth.

 

From ‘What Mad Pursuit’

THE GOSSIP TEST:

     Science requires the utmost dedication. Profound curiosity is what motivates the best scientists.

 

     What you are curious about is what you gossip about. Whether you are the best of scientists or the worst of scientists, let gossip be your guide.

 

THE BAFFLING PROBLEM:

     Natural selection is 'powerful, versatile, and very important.' Natural selection acts at the molecular level and the level of organisms and populations.

 

     Molecular biology has nicely answered the fundamental questions which arose from the ideas of Darwin and Mendel. However, in science the younger generation finds it hard to grasp that many obvious facts are solutions to problems that baffled the older generation.

 

     For most problems near the frontiers of research, assumptions can be dangerously misleading. 'In research the front line is almost always in a fog.'

 

ROCKING THE BOAT:

     Bragg made bold, simplifying assumptions, looked at a wide range of data, and matched his model to experimental facts with criticism that was harsh but not overly harsh. Crick tried to make his model include too many little details and got stuck.    

 

If you want to criticize someone else's work, you should preface your criticism with any possible praise of the work. Criticize firmly but nicely. You should be polite and diplomatic at all times.

 

     You love your dog because your dog is happy to see you and never criticizes you. People buy love with dog food. People reject criticism.

 

     Scientists who work on 'hopeless' subjects are incorrigible optimists. An unrealistic goal acts as a force of natural selection that removes everybody except those who cheerfully delude themselves. The great pot of gold at the end of the rainbow seems to justify ever larger ladders to the sky.

 

THE alpha HELIX:

     Watson stated that a good model never accounts for all the facts, because some of the facts are misleading irrelevancies which are inherently unpredictable and some of the alleged facts are actually falsehoods. A theory which accounts for all the facts is too good to be true.

 

     Standard chemistry seems good enough to explain contemporary molecular biology. Esoteric quantum effects have, so far, played a minor role in the study of molecular biology.

 

     Biological systems are based on molecular biology. If you don't understand a biological system at the molecular level, then your understanding is sketchy, wrong, or fraudulent.

 

HOW TO LIVE WITH A GOLDEN HELIX:

     Because Watson and Crick were intensely curious about the structure of DNA, they found what they were looking for. Curiosity made them make history.

 

     Watson and Crick could work intensely on DNA and then take a break. This on and off work helped them avoid very long runs through blind alleys.

 

     Watson and Crick evolved informal but effective methods of collaboration. Their back and forth teamwork gave them a crucial advantage over their competitors. First, one partner would suggest a new idea; then the other partner would, with candor but without hostility, try to refute the idea. Watson and Crick repeated thesis, antithesis, and synthesis over many cycles; these cycles evolved into a solved problem.      

 

Usually, scientists make many steps in the wrong direction. Mistaken ideas can be detours. Experimental facts illuminate the proper path. Mistaken ideas can be stumbling blocks along the proper path. Your partner can see the stumbling blocks that you can't see because your own errors tend to be invisible to you.

 

     Think of persistence, partnership, strategy, and curiosity. Persistence means that you don't give up too soon. Partnership means that you can avoid getting trapped in a blind alley. Strategy means that you select the right problem. Curiosity means that you can sustain your interest.

 

THEORY IN MOLECULAR BIOLOGY

     Because of evolution, biological mechanisms are too arbitrary and too complicated to yield to theory. Thus the theoretical biologist may have better luck in telling the experimentalist what not to look for. An attempt at positive predictions might be the theoretical biologist's equivalent of the British general's Charge of the Light Brigade.

 

     You shouldn't believe too strongly in your own theory. Negative arguments that rule out possible approaches are particularly dangerous. The road not travelled might be the road to your desired destination.

 

     It's easy to cobble together some oversimplified assumptions and elaborate mathematics that roughly fit some data, but such theory is unlikely to be worthy of attention. There are more facts than are dreamt of in your theory.

 

     It might take a lot of time and effort to make a theory more precise so that it goes from somewhat plausible to somewhat probable to highly probable to virtually certain. However, a theory that deserves respect should be supported by unexpected evidence. A model that predicts no more than the already known evidence is little better than yesterday's newspaper.

 

TRIPLETS:

     Nobody will be much interested in your idea, so you will probably have to test it yourself. Get help from the best available experts.

 

     Talking about experiments and their results is a poor substitute for knowing exactly what the experiments consist of. The way to know is to do. 'There is nothing like actively doing experiments to make one realize all the ins and outs of a technique.' Doing the experiments fixes the details in your mind. The armchair scientist loses touch with reality.

 

     Doing an experiment is far less boring than reading about it. Most scientific papers are badly written, and their 'experimental methods' sections make cookbooks seem like suspense thrillers.

 

CONCLUSIONS

 

     Physics has powerful, deep laws based on mathematics, symmetry, and conservation. Biology has 'laws' that are generalizations with significant exceptions.

 

     Evolution provides the biologist with hints that might be useful or might be misleading. Historical facts are harder to decide than contemporary facts. Evolution confounds the physicist who looks for the simplest model because the natural history of biological phenomena consists of simple steps that proceed from other simple steps according to the unknown problems faced by unknown numbers of unknown organisms.

 

     Theorists become too fond of their own ideas. Theorists cherish their own brain children with a protective parent's love, but few children grow up to be Newton or Einstein. Your dearly beloved theory may predict a few things correctly and yet be completely false. I can easily believe that your theory is wrong but I find it almost impossible to believe that my theory is wrong.

 

     A good model for a biological mechanism doesn't just vaguely resemble the truth. A good model goes down to the level of molecular cell biology and pins things down. Theoretical biologists need to worry when their models ignore too many worries.

 

     Only the experimental evidence can lead to the truth. However, experimental facts can be misleading or they can be false 'facts.' The theorist needs 'a deep and critical knowledge of many different types of evidence.' Only with hindsight can the theorist know 'what type of evidence is likely to give the game away.'

 

     If your theory makes a dubious prediction or fails to make a likely prediction, then don't tinker with your theory but instead seek some crucial test that gets at the essence of your theory. If current experimental methods aren't good enough to make the crucial test, then seek new experimental methods.

 

     Most theories are failures. The theorist who wants to be a success must produce false theory after false theory and expeditiously abandon these false theories in order to reach the true theory.

 

     The main purpose of a scientific theory is to suggest new experiments. 'A good theory makes not only predictions, but surprising predictions that then turn out to be true. (If its predictions appear obvious to experimentalists, why would they need a theory?)'

 

EPILOGUE

 

     Science marched rapidly to answer the basic questions of molecular biology. Crick boldly abandoned his domain of expertise and eventually moved on to the study of visual consciousness.

 

     The functionalists in contemporary psychology and linguistics unaccountably ignore molecular biology. 'It is not usually advantageous to have one hand tied behind one's back when tackling a very difficult job.'

 

     'If you want to understand function, study structure.' Molecular biology's pioneers succeeded by approaching their problems at all levels. 'Hybrid subjects are often astonishingly fertile, whereas if a scientific discipline remains too pure it usually wilts.'

 

     To understand a complicated system, study the system's higher levels, but characterize the system by the system's lower levels that uniquely determine the way the system works. If a higher animal is too complicated, a lower animal might yield useful information.

 

     Decide upon your main long-term interest. Then choose a particular target and figure out how to hit the target.

 

     Sometimes, the basic problems that seem the most difficult are the easiest. Fortune may favor the bold who attempt the summit, because there are fewer paths up a mountain than across a meadow. The fewer the paths, the fewer ways there are to get lost.

 

     If you want to produce a biological theory that compares with Einstein's theory of general relativity, then you are not likely to succeed if your theory concerns 'a complicated combination of rather simple tricks evolved by natural selection.' In the absence of molecular biology, theoretical fads dominate psychology. Psychologists sometimes seem more interested in getting grant money than in testing their models. 'Nobody likes to ask if a model is really correct since, if they did, most work would come to a halt.'

 

     To unscramble a complicated system, you need three main approaches. First, take the system apart and find out what the basic building blocks are and how they work. Second, find out exactly where each part of the system is located within the system and how the parts interact with each other. Third, synthesize the study of the system's structure and behavior; delicately alter the system's various parts and observe the effects on the behavior of the system and its components; make such observations on behavior at all levels of the system.

 

     The 'soft' science of psychology will soon yield to the 'hard' science of molecular psychology.

 

SUBJECTIVE SUMMARY

 

     Perhaps, I substitute my own tips for Crick's tips to a great extent. The reader should study Crick's ideas in their original form. I summarize my impressions under seven headings: Curiosity, Strategy, Data, Methods, Evolution, Persistence, and Partnership.

 

1. Curiosity.

     Above all, work on what interests you. Focus on your main interest.

 

2. Strategy.

     Define the main problem by a reasonable number of tentative questions. Try to find a decisive test for your ideas. Develop a strategy for answering the main questions. Be prepared to revise the questions or the strategy for answering them. Consider the possibility that your goal is unrealistic or overly ambitious in terms of current science and technology. Keep in mind that your favorite original ideas might be partially or completely wrong.

 

3. Data.

     Keep in mind all the empirical data. Remember that some experiments are wrong and that you will inevitably try to ignore the experiments that make you look wrong; the two groups of experiments are not generally identical. Talk to the experimentalists working in your field of interest.

 

4. Methods.

     Keep in mind the current state of the art of experimental methods. Resolve the main problem into subsidiary problems that can be solved in a limited time with existing methods. If existing methods are inadequate, then develop a strategy for developing new methods. Only those who do an experimental method truly understand it; the Chinese proverb is: I hear and I forget; I see and I remember; I do and I understand.

 

5. Evolution.

     Keep in mind that Darwinian evolution governs biological phenomena. Your notions of simplicity and economy may not fit into the evolutionary history of how things came to be the way they are.

 

6. Persistence.

     Keep pursuing the main problem. Always continue to return to the main problem. Avoid getting sidetracked. Create leisure time for yourself in order to consider your best course of action. Follow strategy to determine tactics. Follow tactics to determine techniques. Keep the main things in their proper perspective. Consider ways to avoid or delegate minor tasks or distractions. Don't get so busy that you don't have time to think.

 

7. Partnership.

     Often when you are stuck on a problem, someone else can suggest a way to solve or avoid the problem. Work with one other person who can objectively criticize your ideas.

 

                    REFERENCES

 

1. Brown DW. Crick and Mitchison's theory of REM sleep and neural networks. Med Hypotheses 1993; 40: 329-331.

 

2. Crick F, Mitchison G. The function of dream sleep. Nature 1983; 304: 111-114.

 

3. Crick F, Mitchison G. REM sleep and neural nets. J Mind Behav 1986; 7: 229-249.

 

4. Anderson PW. Some thoughtful words (not mine) on research strategy for theorists. Physics Today 1990; 43; February: 9.

 

5. Crick F. The Astonishing Hypothesis: The Scientific Search for the Soul. New York: Scribners, 1994.

 

6. Crick F. What Mad Pursuit: A Personal View of Scientific Discovery. New York: Basic Books, 1988.