Wired by Experience: How Culture Shapes the Brain

by Santiago Ramón y Cajal

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General Education

We needn’t dwell on the fact that our novice must acquire a thorough knowledge of the science intended to be explored. It is essential that this knowledge come from descriptions in books and monographs, as well as from the direct study of nature itself. However, it is equally important that he acquire a general knowledge of all those branches of science that are directly or indirectly related to the one of choice because they contain guiding principles or general methods of attack. For example, the biologist does not limit his studies to anatomy and physiology, but also grasps the fundamentals of psychology, physics, and chemistry.

The reason for this general education is obvious. The discovery of a fact or the significance of a biological phenomenon usually rests on the application of principles derived from physics or chemistry. As Laplace has pointed out, to discover is to bring together two ideas that were previously unlinked. And it is important to note that this fruitful association typically occurs between data from one of the complex sciences (biology, sociology, chemistry, and so on) and a principle culled from a general science. In other words, the general or abstract sciences (according to the classification of Comte and of Bain) often explain the phenomena of the complex and concrete sciences, leading one to conclude that a well-established hierarchical classification of human knowledge constitutes a veritable genealogical tree.

Discovery is often a matter of simply fitting a piece of data to a law, or wrapping it in a broader theoretical framework, or, finally, classifying it. Thus, it may be concluded that to discover is to name something correctly, something that had been christened incorrectly or conditionally before. This leads to the conclusion that when science has been completed, each phenomenon will have its correct name, after its relationship to general laws has been firmly established. When viewed in this way, the well-known saying of Mach acquires real meaning: "A well-chosen word can save an enormous amount of thought," because to name is to classify, to establish ideal affiliations—analogous relationships—between little-known phenomena, and to identify the general idea or principle wherein they lie latent, like the tree within its seed.

More than anything, the study of philosophy offers good preparation and excellent mental gymnastics for the laboratory worker. Do not forget that many renowned investigators have come to science from the field of philosophy. It is needless to point out that the investigator will be concerned less with doctrine and philosophical creed—which unfortunately change every fifteen or twenty years—than with the criteria of truth and the standards of critical judgment. Ex What Newcomers to Biological Research Should Know 55 ercise of the latter allows one to acquire flexibility and wisdom, as one learns to question the apparent certainty of the best-established scientific systems. This is how one’s own imagination is properly bridled. The investigator’s motto will always be Cicero’s phrase: Dubitando ad veritatem pervenimus.

As far as the microscopic anatomy of plants and animals is concerned, most of the core data forming this science are derived from interactions between the chemical properties of certain reagents and the structural elements of cells and tissues. In bacteriology, neurology, and so on, we owe most of what we know today to the fortunate application of the staining agents developed by modern chemistry, and the same applies to general biology. Simply recall Loeb’s interesting work on artificial parthenogenesis, or the work of Harrison, Carrel, Lambert, and others on artificial cell cultures from animal tissues. Novel experiments such as these rely fundamentally on chemical and physical changes taking place in the cellular environment.

This intimate union of the sciences has been appreciated by many. It was especially clear to Letamendi, who defined scientific specialties as "the application of science as a whole to a particular branch of knowledge."

If a supreme intelligence knew all the mysterious explanations linking all phenomena in the universe, there would be one single science instead of many different sciences. The frontiers that appear to separate fields of learning, the formal scaffolding of our classification scheme, the artificial division of things to please our intellects—which can only view reality in stages and by facets—would disappear completely in the eyes of such an individual. Total science would appear as a giant tree, whose branches represent the individual sciences and whose trunk represents the principle or principles upon which they are founded. The specialist works like a caterpiller perched on a leaf, cherishing the illusion that his little world flutters isolated in space. Endowed with a philosophic sense, the generalist sees—however imperfectly—the stem that is common to many branches. But only the genius alluded to above would enjoy the good fortune and power to see the entire tree, science, unitary despite its many specializations.

 

The Need for Specialization

It is wise, however, not to emphasize the unifying principle just discussed. It is too easy to run aground on the shoal of encyclopedic learning, where minds incapable of orderliness—who are restless, undisciplined, and unable to concentrate attention on a single idea for any length of time—tend to stop. Rotating inclinations, as a highly original physicianwriter has called them, may create great writers, delightful conversationalists, and illustrious orators, but rarely scientific discoverers.

The well-known proverb, "Knowledge does not occupy space," is a grave mistake. Fortunately, this is of little practical consequence because even those who believe it must confess that learning many things at the very least takes time. Only an excessively flattering estimate of one’s talents can explain the encyclopedic mania. The intent to master a number of sciences is a chimerical aspiration. Just consider the indefatigable men of real genius who resign themselves to a profound knowledge of one branch of knowledge—and often to one concrete theme within a given science—only to harvest a small number of facts.

In short, do not get carried away by illusion. If a lifetime is needed to learn something about all of the human arts, it What Newcomers to Biological Research Should Know 57 is barely sufficient to master completely, down to the last detail, any one or two of them.

Modern encyclopedists such as Herbert Spencer, Mach, and Wundt are actually specialists in the philosophy of the sciences and arts, as were Leibnitz and Descartes in their own time. However, the latter were able to dominate larger territory, and make discoveries in two or three sciences, because less was known during their lifetimes.

Multifaceted investigators have disappeared, perhaps forever. It is important to realize that today, in physics as in mathematics, in chemistry as in biology, discoveries are made under the astute direction of specialists. However, they do not focus exclusively on a narrow topic; instead, they follow attentively the latest developments in related sciences, without losing sight of their specialty. In addition to being good policy, this division of work is an indispensable necessity. We are forced to adopt it because of the extraordinary amount of time required by the testing and mastery of new techniques reported almost daily, by the growing volume of the literature, and by the many scholars working simultaneously on virtually every topic.

It seems useful to conclude with a frequent comparison that is expressed in two maxims of everyday philosophy: "A long harvest, little corn," and "Knowledge occupies no space." The inquisitive mind is like a sword used in battle. If it has one sharp edge, we have a cutting weapon; with two edges it will still cut, though less efficiently; but if three or four edges are arranged simultaneously, the effectiveness of each diminishes progressively, until the sword is reduced to a dull bludgeon. Strictly speaking, a bayonet still cuts, although a great deal of energy is required, whereas a well-sharpened dagger is dangerous even in the hands of a child.

Like unmolded steel, our mind represents a potential sword. The forging and polishing of study transform it into the tempered and keen scalpel of science. Let us have a cutting edge on only one side, or on two at the most, if we want to conserve its analytical powers and penetrate to the heart of problems. Leave to the scatterbrained ency clopedists the privilege of transforming their minds into dull weapons.

 

Foreign Languages

Obviously, the investigator’s library should contain the important books and journals related to his specialty that are published in the most advanced countries. The German journals will be consulted regularly because it must be admitted that Germany alone produces more new data than all the other nations combined when it comes to biology.1

He who desires an end desires the means. Because aknowledge of the German language is essential to keep abreast of the latest scientific news, let us study it seriously, at least to the point of being able to translate it adequately. Abandon the superstitious terror that the complicated twists and turns of the Northern languages inspires in us Spaniards. A knowledge of German is so essential that today there is probably not a single Italian, English, French, Russian, or Swedish investigator who is unable to read monographs published in it. And because the German work comes from a nation that may be viewed as the center of scientific production, it has the priceless advantage of containing extensive and timely historical and bibliographic information.2

In order of importance, English and French follow German. We shall not discuss Italian because any Spaniard with an average education can translate it, even without the help of a dictionary. However, it is important to recall that in some areas of scientific work, Italy marches at the head of the procession.

At the present time scientific work is published in more than six languages. Although reverting to Latin or using Esperanto as a universal scientific language might appear useful, scholars have responded instead by using even more languages for presenting their scientific work in print. It must be admitted that from the standpoint of practicality, Volapük or Esperanto simply became one more language to be learned.3 This reality should have been predicted because it is inevitable in this day and age, with the essentially democratic and popularizing influences of modern knowledge, and the practical views of authors and editors whose moral and material interests impel them to spread among the general public the scientific victories that long ago were the exclusive property of the academies and a tiny group of lecture hall celebrities.

It is clearly not necessary, however, for the investigator to speak and write all of the European languages. It is enough for the Spaniard to translate the following four: French, English, Italian, and German. It is appropriate to call them the languages of learning, and virtually all scientific work is published in one of them. Naturally, Spanish does not figure among the languages of learning. Therefore, if our investigators want their research to be known and appreciated by the specialists, they have no choice but to write and speak one of these four European languages.4

 

How Monographs Should Be Read

When monographs on the specialty one has chosen to investigate are read, particular attention should be focused on two important things: research methods used by the author in his work, and problems that remain unsolved. What might be called popularizing books merit less attention and confidence, unless they are comprehensive reviews of the field of interest, or contain useful general concepts that may be applied in the laboratory. In general, it may be assumed that books reflect historical eras in science. Because they take so long to write and edit, especially when authors are determined to simplify the material so that the public can readily understand it, books are either not written about contemporary issues, or they are very lightly sketched. The same holds true for methodological details and paths of investigation.

Monographs by outstanding authors who have contributed most to a field should be submitted to thorough and critical study. Among other qualities, original talent has the great virtue of stimulating thought. A feature of every good book is that it allows the reader not only to extract the ideas deliberately presented by the author but also to formulate completely new ideas (different for each reader) that result from a conflict between our own fund of ideas and views expressed in the text. Clearly, the good treatise is an effective reagent for our cerebral energies, in addition to being an excellent source of scientific lore.

Human brains, like desert palms, pollinate themselves at a distance. However, for the union of two minds to occur and generate fruitful results through a book, the reader must become fully absorbed in what a master has written, must penetrate fully its meaning, and finally must develop an affection for the author. In science as in life, fruit always comes after the realization of love. So many beginners fall into the trap of considering old or even ancient discoveries as the fruit of their own labor simply because they relied on secondary sources instead of consulting original reports!

Our new and inexperienced man of science must flee from abstracts and syllabuses as if from the plague. The syllabus is good for teaching purposes, but is abominable for guiding the investigator. He who abstracts a book does so with his own purposes in mind. He often displays his own judgments and doctrines instead of the author’s. He takes from the latter what pleases him or what he understands and digests easily. And he makes important that which should be secondary, and vice versa. In the name of clarifying and popularizing someone else’s work, he who does the abridging ends up substituting his own personality for that of the author, whose intellectual character—which is so interesting and educational for the reader—remains in the shadows.

Thus, the investigator has a strict obligation to read an author’s original work if he wishes to avoid disagreeable surprises—unless the abstract is by the author himself. Here at least, we may find original and guiding ideas that can be used to real advantage in analytical work, despite their brevity.

At this point, an interesting question emerges: should beginners review the literature before starting experimental work? Permeated, if not saturated, by whatever has been written on the subject, mightn’t we run the risk of being influenced, and of losing the invaluable gift of independent judgment? Won’t our aspirations of finding something completely original be fatally injured by all the detailed information we have surrendered ourselves to, leaving the impression that there is nothing left to discover?

Each person must solve this problem in his own way. Nevertheless, there seems to be general agreement that no inquiry should be started without having all the relevant literature at hand. This approach avoids the painful disillusionment that comes with finding that we have squandered our time rediscovering something already known, thus neglecting the profound study of genuinely unknown aspects of a problem.

In my view, the wisest course is to complete a thorough review of the literature routinely before launching an analytical project. But when this is not feasible due to insuperable difficulties (which unfortunately occur in Spain, where the universities lack recent foreign books, and the academies do not have the resources to subscribe to the most important scientific journals), we should not desert the laboratory because one or another monograph is unavailable. If we work hard and long with the best methods available, we shall find something that has escaped the attention of previous workers. Not having been influenced by them, we shall have traveled different routes and considered the subject from different points of view. In any event, it is worth a thousand times more to risk duplicating discoveries than to give up all attempts at experimental investigation. This is true because when a beginner’s results turn out to be similar to those published a short time earlier, he should not be discouraged—instead, he should gain confidence in his own worth, and gather encouragement for future undertakings. In the end he will produce original scientific work, providing his financial resources match his good intentions.

 

The Absolute Necessity of Seeking Inspiration in Nature

We may learn a great deal from books, but we learn much more from the contemplation of nature—the reason and occasion for all books. The direct examination of phenomena has an indescribably disturbing and leavening effect on our mental inertia—a certain exciting and revitalizing quality altogether absent, or barely perceptible, in even the most faithful copies and descriptions of reality.

All of us have probably observed that when we attempt to verify a fact presented by a writer, unexpected results invariably emerge, suggesting ideas and plans of action not aroused by the mere act of reading. In our view, this is due to an inability of the human word to paint exactly and faithfully. In any branch of knowledge one may wish to mention, reality presents a surface of highly varied and complex sensations. Symbolic expression always arises through abstraction and simplification, and can only reflect a small part of reality.

No matter how objective and simple it may appear, all description relies on personal interpretation—the author’s own point of view. It is well-known that man projects his personality onto everything, and that when he believes he is photographing the outside world he is often observing and depicting himself.

From another perspective, observation provides the empirical data used to form our conclusions, and also arouses certain emotions for which there are simply no substitutes— enthusiasm, surprise, and pleasure, which are compelling forces behind constructive imagination. Emotion kindles the spark that ignites cerebral machinery, whose glow is required for the shaping of intuition and reasonable hypotheses.

As an example of the direct thought-provoking effects that nature has on the observer, it seems appropriate to relate the impressions I felt on observing the phenomenon of the circulation of the blood for the first time.

I was in my junior year of medical studies and had learned about the details of this phenomenon from various books, although my interest had not been aroused particularly, and I had given it little thought. However, one of my friends, Mr. Borao (a physiology assistant), was kind enough to demonstrate the circulation in the frog’s mesentery to me.During the sublime spectacle, I felt as though I were witnessing a revelation. Enraptured and tremendously moved on seeing the red and white blood cells move about like pebbles caught up in the force of a torrent; on seeing how the elastic properties of red corpuscles allowed them suddenly to regain their shape like a spring after laboriously passing through the finest capillaries; on observing that the slightest obstruction in the stream converted potential spaces between endothelial cells into actual spaces providing the opportunity for minor hemorrhage and edema; and finally, on noticing how the cardiac beat weakened by curare slowly propelled the obstructing red corpuscles, it seemed as though a veil had been lifted from my soul, and my beliefs in I know not what mysterious forces I had attributed the phenomena of life receded and vanished. In my enthusiasm I exclaimed the following, not knowing that many others, including Descartes especially, had done so centuries before: "Life seems to be pure mechanism. Living bodies are hydraulic machines that are so perfect they can repair the damage caused by the force of the torrent moving them, and even produce other similar hydraulic machines through the mechanism of reproduction." I am absolutely convinced that the vivid impression caused by this direct observation of life’s internal machinery was one of the deciding factors in my inclination to biological research.5

 

Mastery of Technique

Once a topic has been chosen for study, and the investigator has examined all of the literature relevant to the problem of interest, it is time to confirm the latest published data with the most appropriate analytical methods available. Very often during this attempt at proof, questionable points, untenable hypotheses, and gaps in observation will be recognized; and now and then the young investigator may glimpse the road he will be privileged to travel along in search of knowledge about the problem.

Mastery of technique is so important that without fear of contradiction it may be stated that great discoveries are in the hands of the finest and most knowledgeable experts on one or more of the analytical methods. Through intense application, the masters have learned all of the secrets that the technique may have to offer.

In support of this contention, I would simply ask you to recall that of the hundreds of histologists, embryologists, and anatomists working in Europe and America, the most important scientific conquests have been won by only a dozen men who became known for their invention or improvement of a research method, or for their having absolutely mastered one or more of them.

The latest research techniques can be given preference, but first priority must go to the most difficult because they are the least exploited. Time wasted on experiments that don’t work does not matter. If the method has very high resolution, the desired results will have real importance, and will repay our eagerness and zeal quite handsomely. Moreover, difficult techniques provide us the inestimable advantage of proceeding almost alone, finding very few imitators and competitors along the way.

 

In Search of Original Data

We now come to a difficult problem: the great frustration of the beginner who knows from the history of scientific research that once the first discovery is made, others related to it will certainly follow.

A new discovery is often the fruit of patient and stubborn observation—the result of having spent more time, been more consistent, and used better methods than our predecessors. As we have already pointed out, scrupulous and repeated consideration of the same data eventually yields a supersensitive, refined, analytical perception of whatever is relevant to the chosen problem. How often we find entirely new things in preparations, where our unsuspecting pupils saw nothing! This is due to the quick judgment that results from experience. And how many things probably escaped our attention when we were still inexperienced in microscopic technique and each preparation appeared like a sphinx defying understanding!

In addition to how remarkably our differentiating powers increase through repeated experimentation and observation, the resolute study of a problem almost always suggests improvements in methodology, after one determines the conditions that produced some unfortunate result and thus the factors that yield maximum technical efficiency.

Diligence is often rewarded with discovery. It is simply a matter of applying a recent technique to a problem that has lain dormant for some time. These tactics have generated tremendous and easy progress in bacteriology and in comparative anatomy and histology.

Because the great pioneers of science typically have created new methods, it would be ideal if rules for their discovery could be formulated. Unfortunately, almost all of the analytical methods in biology have been found as a result of chance.

It is true to say that, in general, methods are useful applications to one branch of knowledge of principles belonging to another. However, the applications are often developed by trial and error, or at most are inspired by vague analogies.

As we have already noted, in areas such as bacteriology, histology, and histochemistry, methods are based on the selective effects of dying agents or of reagents created by modern chemistry. However, there was no rationale—unless the intention was to produce a useful result by chance—for Gerlach to stain nuclei with carmine; for Max Schultze to use osmic acid on nervous tissue; for Hannover to fix tissues with chromic acid and dichromates; for Koch, Ehrlich, and others to stain bacteria with the aniline dyes; and so on.

If we knew the entire chemical composition of living cells, results due to the application of a particular staining reagent could be deduced simply from biochemical principles. However, because we are so far from this position, those aspiring to discover new biological methods are forced to submit live tissues to the same blind tests resorted to by chemists for centuries in the hope of now and then finding some unforseen combination of reactions or mixtures of elements.

Thus, it is necessary to trust at least partly in chance, which can be encouraged by repeated series of trials that must be guided by intuition and as deep and accurate a knowledge as possible of the latest reagents and techniques emerging from chemistry and industry.

This brings me to the point of discussing the role of chance in the realm of scientific investigation. There is no doubt that accident is a major component of empirical work, and we must not overlook the fact that science owes brilliant achievements to it. However, as Duclaux has graphically pointed out, chance smiles not on those who want it, but rather on those who deserve it. It is important to recognize that only the great observers benefit from chance because only they know how to pursue it with the necessary strength and perseverance. And when an unexpected revelation appears, only they are in a position to realize its great importance and scope.

In science as in the lottery, luck favors he who wagers the most—that is, by another analogy, the one who is tilling constantly the ground in his garden. If Pasteur discovered bacterial vaccines by accident, he was assisted by genius. He envisioned all of the benefits that might be derived from a casual observation, the reduced virulence of a bacterial culture exposed to air (probably reduced by the action of oxygen).

The history of science is full of similar tales. Scheele happened upon chlorine while trying to isolate manganese; Claude Bernard planned experiments to characterize the destructive agent in sugar but instead discovered the glycogenic function of the liver; and so on. To end this section, we shall consider two recent examples of almost miraculous good luck in the stupendous discoveries of Roentgen, Becquerel, and the Curies.

It is well known that the discovery of x-rays by Professor Roentgen was the result of simple chance. In his Würzburg laboratory, this learned man repeated the experiments of Lenard on the unique properties of cathode rays. The emitted radiation was projected in the usual way onto a screen made fluorescent with barium platinocyanide. Roentgen was interested in determining how long the fluorescence lasted, and one day it occurred to him to darken the laboratory by covering the Crookes tube (the well-known apparatus that generates cathode rays) with a cardboard box. When the transformer was turned on, Roentgen looked at the screen and to his amazement saw that it was brightly illuminated anyway. He then substituted a piece of wood, and then a book, and he observed that part of the radiation—the new rays—went through these opaque objects readily. Finally, in a moment of feverish impatience, he accidentally placed his hand between the Crookes tube and the fluoroscopic screen. Overcome with intense emotion—perhaps even terror—he observed an astonishing spectacle: on the surface of the fluorescent screen, the bones of his hand were faithfully depicted in black, as if there were no surrounding tissues. The wonderful x-rays had been discovered, and with them fluoroscopy. X-ray photography and the many valuable surgical and industrial applications known to all soon followed.

The second story is just as elegant, and involves the accidental discovery of radioactivity, which we owe to the renowned French physicist, Henri Becquerel.

The unappreciated Poincaré had already asked whether it might not turn out in the long run that x-ray production is a property of all fluorescent elements. Wanting to confirm this suggestion, and well prepared for this line of investigation, M. Becquerel planned to examine uranium sulfate, a typical fluorescent compound. But the cloudy days of February came and went, and the sun failed to appear. Hoping the celestial monarch might dissipate the thick Parisian mists, the physicist prepared his experiment with a great deal of anticipation. He placed various crystals of uranium sulfate on a sensitized plate that was wrapped in black paper, and he also placed a copper cross on the plate. Impatience devoured and goaded him until one day it occurred to him by chance to remove the plate from its protective wrapping and develop it. To his great surprise, and contrary to his expectations (the uranium salts had remained in the dark), a vivid pattern was observed on the plate: The crystals of uranium salts were represented in black and the metallic cross was represented in white. Without intending to, he had discovered the emission of radioactivity by matter, one of the most wonderful conquests of modern science.

But the most extraordinary and outstanding part of this story is that M. Becquerel was able to make such a great discovery (winning him a Nobel prize) on the basis of a false hypothesis—that there is an etiologic relationship between the emission of x-rays and fluorescence. By sheer coincidence, of all known fluorescent elements, uranium is the only one that is radioactive! The effect was obviously theatrical, as if prepared by an ironic genius determined to prod science along in spite of how inaccurate its concepts may be.

It is obvious that while many scholars have discovered things they were not actively looking for, they nevertheless searched with admirable tenacity and were worthy of their success. With rare insight they succeeded in finding unexpectedly the great developments that lie hidden within the timid and fragmentary revelations of the great unknown. In the long run, fortunate accidents almost always have a way of rewarding perseverance.

To solicit the aid of luck is like stirring muddy water to bring objects submerged at the bottom to the top where they can be seen. Every observer would do well to tempt their good luck. Nevertheless, we should not depend on it too much—most of the time is it better to concentrate on systematic work. He who masters technique and keeps abreast of problems that can be solved almost always comes away with a more or less important discovery without doing a lot of unproductive experiments.

Once the first new data are obtained—and especially if they generate new currents in the scientific atmosphere— our task will be as smooth as it is brilliant because it reduces to working out the consequences of the new data for the various spheres of science. This leads to the conclusion that the first discovery is the one that counts; the rest are usually corollaries of the original. A well-known doctrine espoused by philosophers such as Taine, and by scientists such as Tyndall, is that each problem solved stimulates an infinite number of new questions, and that today’s discovery contains the seed of tomorrow’s. The peak of truth that took so much effort to scale appears to be an imposing mountain when gazed at from the valley. However, it proves to be just another mountain within a formidable succession of ranges, seen through the mist and attracting us with insatiable curiosity. We should satisfy our eagerness to climb, and take advantage of the peace one experiences in contemplating new horizons. And from the recently conquered peak, also think about the path that leads to even higher ranges.

But as we have said before, it is very rare indeed to have the good fortune of starting out with a promising study that actually produces an important discovery, and no wise investigator counts very much on doing so. Therefore, we must not hesitate when beginning our work to follow up someone else’s discovery. This is a useful task, and useful results will follow. Original data produced by others often foment revolution in the scientific atmosphere. They raise doubts about what were considered established principles; they change the equilibrium in those vague regions of conjecture that shape the transition from what is unknown to what is known; and they establish a new set of problems that the discoverer himself lacks the time to pursue.

Furthermore, the original investigator almost always leaves his discussion incomplete. He is still influenced by tradition and fails to break openly with the views of the past. Perhaps wary of arousing too much opposition in the scientific world, and anxious for approval and applause, his theory is presented as a compromise between the oldest and the newest doctrines. Thus, a less meticulous newcomer could well advance the work of the originator with little effort, and obtain the most valuable theoretical and practical results. The many problems raised by a new scientific discovery are fertile ground for the young investigator. His analytical weapons finely honed, he will respond without arrogance or great expectations—but must not count on arriving alone. He will find a host of rivals attempting to surpass him, and can excel only by virtue of hard work, clear-sightedness, and perseverance.

Finally, when we discover ourselves surrounded by a number of equally promising and fertile problems to work on, choose the one whose methodology we understand clearly, and the one we have a decided liking for. This is the good advice Darwin used to give his students when they asked for a problem to work on. The rationale for this approach is that our intellect redoubles its efforts when perceiving the reward of pleasure or utility in the distance.

As we have already pointed out on a number of occasions, the explorer of nature must view research as the best of all possible sports, whose every facet—from the execution of technique to the elaboration of theory—is a never-ending source of indescribable satisfaction. You should abandon science if you don’t feel growing enthusiasm and a growing sense of power when working with a difficult problem—if your soul isn’t flooded with the emotion of anticipated pleasure when approaching the long-awaited and solemn moment of the fiat lux. Nature grants not her favors to those with a cold heart—which is usually an unmistakable sign of impotence.

 

Notes

1. Because of growing rivalries, centers producing biological research are springing up in a number of places. Italy, France, England, and especially the United States, are now competing with, and in many cases surpassing, the work of German universities, which for decades was incomparable. (Author’s footnote, 1923.)

2. When the Spanish attend scientific congresses, they deplore the fact that their language is eclipsed by German, French, or English. Before registering complaints that automatically evoke smiles from the learned, these inopportune patriots would be well advised to think seriously about the following three undeniable observations:

a. Qualitatively and quantitatively, our scientific production is much less than that of the four nations enjoying the privilege of using their native tongues at congresses.

b. As a result, Spanish is unknown to the vast majority of scholars. If a quixotic patriotism inspires us to insist on using it at our international congresses, we should expect a mass exodus of listeners.

c. Finally, nations including Sweden, Holland, Denmark, Hungary, Russia, and Japan—whose scientific production far exceeds that of Spain—have never been guilty of boldly imposing their respective languages on such literary contests. Their scholars are far too clear-sighted not to recognize that while the task of mastering the four languages under consideration is difficult, learning one or two more languages is not an intolerable form of torture.

3. If international jealousies and suspicions could be avoided, it would be much more simple and practical to agree on the use of a living language— French, for example—for scientific communication. It would be interesting to ask Esperanto enthusiasts whether they plan to abandon the use of French while traveling in France. (As one might have predicted, the brand new Volapük has already [1920] been forgotten completely. I predict the same for Esperanto.)

4. Thanks to laudable initiative, the German language has been given special attention in the curriculum of our institute. Unfortunately, however, this has as yet done little good for our scholars. This is due as much to a lack of time for the subject as to shortsighted teaching methods. When there is not enough time to master a difficult language, it would make sense not to attempt teaching all aspects of German. Instead, it would seem logical to concentrate on scientific German—on the relatively limited set of grammatical rules and small number of voices needed to translate scientific monographs. This can be achieved with six to eight months of diligent study. We suggest to those with an interest in biological work to subscribe to a German journal in his specialty, for example, any Zentralblatt. While laborious atfirst, the reading will come easier. The pleasure of obtaining some benefit from the very outset will progressively add to the enjoyment of his research.

5. Today I do not subscribe unreservedly to this mechanistic concept, nor do I adhere strictly to the physicochemical interpretation of life. The origin and morphology of cells and organs, heredity, evolution, and so on include phenomena that depend on incomprehensible absolute causes, notwithstanding the vaunted promise of Darwinism and the postulates of Loeb’s school of biochemistry.

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