A Criticism of Present-day Agricultural Research
A WANT of relation between the conventional methods of investigation and the nature of disease in plants and animals has been shown to exist. The vast fabric of agricultural research must now be examined in order to determine whether effective contact has been maintained with the problems of farming. This is the theme of the present chapter.
The application of science to agriculture is a comparatively modern development, which began in 1834 when Boussingault laid the foundations of agricultural chemistry. Previously all the improvements in farming practice resulted from the labours of a few exceptional men, whose innovations were afterwards copied by their neighbours. Progress took place by imitation. After 1834 the scientific investigator became a factor in discovery. The first notable advance by this new agency occurred in 1840, when Liebig's classical monograph on agricultural chemistry appeared. This at once attracted the attention of agriculturists. Liebig was a great personality, an investigator of genius endowed with imagination, initiative, and leadership and was exceptionally well qualified for the scientific side of his task -- the application of chemistry to agriculture. He soon discovered two important things: (1) that the ashes of plants gave useful information as to the requirements of crops, and (2) that a watery extract of humus gave little or no residue on evaporation. As the carbon of the plant was obtained from the atmosphere by assimilation in the green leaf, everything seemed to point to the supreme importance of the soil and the soil solution in the raising of crops. It was only necessary to analyse the ashes of plants, then the soil, and to apply to the latter the necessary salts to obtain full crops. To establish the new point of view the humus theory, which then held the field, had to be demolished. According to this theory the plant fed on humus. Liebig believed he had shown that this view was untenable; humus was insoluble in water and therefore could not influence the soil solution.
In all this he followed the science of the moment. In his onslaught on the humus theory he was so sure of his ground that he did not call in Nature to verify his conclusions. It did not occur to him that while the humus theory, as then expressed, might be wrong, humus itself might be right. Like so many of his disciples in the years to come, he failed to attach importance to the fact that the surface soil always contains very active humus, and did not perceive that critical field experiments, designed to find out if chemical manures were sufficient to supply all the needs of crops, should always be done on the sub-soil, after removing the top 9 inches or so. If this is not arranged for, the yield of any crop may be influenced by the humus already in the soil. Failure to perceive this obvious fact is the main reason why Liebig and his disciples went astray.
He also failed to realize the supreme importance to the investigator of a first-hand knowledge of practical agriculture, and the significance of the past experience of the tillers of the soil. He was only qualified for his task on the scientific side; he was no farmer; as an investigator of the ancient art of agriculture he was only half a man. He was unable to visualize his problem from two very different points of view at one and the same moment -- the scientific and the practical. His failure has cast its shadow on much of the scientific investigation of the next hundred years. Rothamsted, which started in 1843, was profoundly influenced by the Liebig tradition. The celebrated experiments on Broadbalk Field caught the fancy of the farming world. They were so telling, so systematic, so spectacular that they set the fashion till the end of the last century, when the great era of agricultural chemistry began to wane. During this period (1840-1900), agricultural science was a branch of chemistry; the use of artificial manures became firmly welded into the work and outlook of the Experiment Stations; the great importance of nitrogen (N), phosphorus (P), and potash (K) in the soil solution was established; what may briefly be described as the NPK mentality was born.
The trials of chemical manures, however, brought the investigators from the laboratory to the land; they came into frequent contact with practice; their outlook and experience gradually widened. One result was the discovery of the limitations of chemical science; the deficiencies of the soil, suggested by chemical analysis, were not always made up by the addition of the appropriate artificial manure; the problems of crop production could not be dealt with by chemistry alone. The physical texture of the soil began to be considered; the pioneering work of Hilgard and King in America led to the development of a new branch of the subject -- soil physics -- which is still being explored. Pasteur's work on fermentation and allied subjects, by drawing attention to the fact that the soil is inhabited by bacteria and other forms of life, disclosed a new world. A notable elucidation of the complex life of the soil was contributed by Charles Darwin's fascinating account of the earthworm. The organisms concerned with the nitrification of organic matter were discovered by Winogradsky and the conditions necessary for their activity in pure cultures were determined. Another branch of agricultural science -- soil bacteriology -- arose. While the biology and physics of the soil were being studied, a new school of soil science arose in Russia. Soils began to be regarded as independent natural growths: to have form and structure due to climate, vegetation, and geological origin. Systems of soil classification, based primarily on the soil profile, with an appropriate nomenclature developed in harmony with these views, which, for the moment, have been widely accepted. A new branch of soil science -- pedology -- arose. The Liebig conception of soil fertility was thus gradually enlarged and it became clear that the problem of increasing the produce of the soil did not lie within the domain of any one science but embraced at least four -- chemistry, physics, bacteriology, and geology.
At the beginning of the present century, the investigators began to pay more attention to what is after all the chief agent in crop production -- the plant itself. The rediscovery of Mendel's law by Correns, the conception of the unit species which followed the work of Johannsen and the recognition of its importance in improvement by selection have led directly to the modern studies of cultivated crops, in which the Russians have made such noteworthy contributions. The whole world is now being ransacked to provide the plant breeders with a wide range of raw material. These botanical investigations are constantly broadening and now embrace the root system, its relation to the soil type, the resistance of the plant to disease, as well as the internal mechanism by which inheritance takes place. The practical results of the last forty years which have followed the application of botanical science to agriculture are very considerable. In wheat, for example, the labours of Saunders in Canada led to the production of Marquis, an early variety with short straw, which soon covered 20,000,000 acres in Canada and the neighbouring States of the Union. This is the most successful wheat-hybrid yet produced. In Australia the new wheats raised by Farrer were soon widely cultivated. In England the new hybrids raised at Cambridge established themselves in the wheat-growing areas of this country. In India the Pusa wheats covered several million acres of land. By 1915 the total area of the new varieties of wheat had reached over 25,000,000 acres. When the annual dividend, in the form of increased wealth, was compared with the capital invested in these investigations, it was at once evident that the return was many times greater than that yielded by the most successful industrial enterprise. Similar results have been obtained with other crops. The new varieties of malting barley, raised by Beaven, have for years been a feature of the English country-side; the new varieties of sugarcane produced by Barber at Coimbatore in South India soon replaced the indigenous types of cane in northern India. In cotton, jute, rice, grasses, and clovers and many other crops new varieties have been obtained; the old varieties are being systematically replaced. Nevertheless the gain per acre obtained by changing the variety is as a rule small. As will be seen in the next chapter, the great problem of agriculture at the moment is the intensive cultivation of these new types; how best to arrange a marriage between the new variety and a fertile soil. Unless this is done, the value of a new variety can only be transient; the increased yield will be obtained at the expense of the soil capital; the labours of the plant breeders will have provided another boomerang.
A number of other developments have taken place which must briefly be mentioned. Since the Great War the factories then engaged in the fixation of atmospheric nitrogen for the manufacture of the vast quantities of explosives, needed to defend and to destroy armies well entrenched, have had to find a new market This was provided by the large area of land impoverished by the over-cropping of the war period. A demand was created by the low price at which the mass-produced unit of nitrogen could be put on the market and by the reliability of the product. Phosphates and potash fell into line Ingenious mixtures of artificial manures, containing everything supposed to be needed by the various crops, could be purchased all over the world. Sales increased rapidly; the majority of farmers and market gardeners soon based their manurial programme on the cheapest forms of nitrogen, phosphorus, and potash or on the cheapest mixtures. During the last twenty years the progress of the artificial manure industry has been phenomenal; the age of the manure bag has arrived; the Liebig tradition returned in full force.
The testing of artificial manures and new varieties has necessitated innumerable field experiments, the published results of which are bewildering in their volume, their diversity, and often in the conclusions to be drawn from them. By a judicious selection of this material, it is possible to prove or disprove anything or everything. Something was obviously needed to regulate the torrent of field results and to ensure a greater measure of reliability. This was attempted by the help of mathematics. The technique was overhauled; the field plots were 'replicated' and 'randomized'; the figures were subjected to a rigid statistical scrutiny. Only those results which are fortunate enough to secure what has been described as the fastidious approval of the higher mathematics are now accepted. There is an obvious weakness in the technique of these field experiments which must be mentioned. Small plots and farms are very different things. It is impossible to manage a small plot as a self- contained unit in the same way as a good farm is conducted. The essential relation between live stock and the land is lost; there are no means of maintaining the fertility of the soil by suitable rotations as is the rule in good farming. The plot and the farm are obviously out of relation; the plot does not even represent the field in which it occurs. A collection of field plots cannot represent the agricultural problem they set out to investigate. It follows that any findings based on the behaviour of these small fragments of artificially manured land are unlikely to apply to agriculture. What possible advantage therefore can be obtained by the application of the higher mathematics to a technique which is so fundamentally unsound?
With the introduction of artificials there has been a continuous increase in disease, both in crops and in live stock. This subject has already been discussed. It is mentioned again to remind the reader of the vast volume of research on this topic completed and in progress.
Side by side with the intrusion of mathematics into agriculture, another branch of the subject has grown up -- economics. The need for reducing expenditure so that farming could yield a profit has brought every operation, including manuring and the treatment of disease, under examination in order to ascertain the cost and what profit, if any, results. Costings are everywhere the rule; the value of any experiment and innovation is largely determined by the amount of profit which can be wrung from Mother earth. The output of the farm and of the factory have been looked at from the same standpoint -- dividends. Agriculture joined the ranks of industry.
Agricultural science, like Topsy, has indeed grown. In little more than forty years a vast system of research institutes, experimental farms, and district organizations (for bringing the results of research to the farming community) has been created all over the world. As this research structure has grown up in piecemeal fashion as a result of the work of the pioneers, it will be interesting to examine it and to ascertain whether or not direction has been maintained. Has the present organization any virtue in itself or does it merely crystallize the stages reached in the scientific exploration of a vast biological complex? If it is useful it will be justified by results; if its value is merely historical, its reform can only be a question of time.
In Great Britain two documents have recently appeared (Constitution and Functions of the Agricultural Research Council, H.M. Stationery Office London, 1938; Report on Agricultural Research in Great Britain, PEP., 16 Queen Anne's Gate, London, S.W. 1, 1938.) which make it easy to conduct an inquest on agricultural research in this country. They describe fully the structure and working of the official machine which controls and finances research, the organization of the work itself, and the methods of making the results known to farmers. In addition to the Treasury and the Committee of the Privy Council, official control is exercised by no less than three other organizations: (1) The Ministry of Agriculture (which administers the grants); (2) the Development Commission (which awards funds from grants placed at its disposal by the Treasury); and (3) the Agricultural Research Council (which reviews and advises on applications for grants, and also coordinates State-aided agricultural research in Great Britain). Eventually the Research Institutes, which carry out the work, are reached.
These Research Institutes are fifty in number and are of three types:
(a) Government laboratories or research stations;
(b) Institutes attached to universities or university colleges;
(c) Independent institutes.
Most of these institutes were set up in 1911 to provide for basic research in each of the agricultural sciences: agricultural economics, soil science, plant physiology, plant breeding, horticulture and fruit research, plant pathology, animal heredity and genetics, animal physiology and nutrition, animal diseases, dairy research, food preservation and transport, agricultural engineering and agricultural meteorology. These groups can again be divided into four classes: background research (dealing with fundamental scientific principles); basic research (the recognized sphere of the research institute); ad hoc research (the study of specific practical problems, as they arise, such as the control of foot-and-mouth disease); pilot or development research (such as the growing on of new strains of plants).
After research proper, the organization then deals with the results of its investigations. The first stage in this process is the Provincial Advisory Service which operates in sixteen provinces. From one to seven Advisory Officers are stationed at each centre, their specialized knowledge being at the disposal of County Organizers and farmers. The final link in the long chain from the Treasury to the soil is provided by the Agricultural Organizers of the County Councils, who act as a free Scientific Information Bureau for farmers and market gardeners. Most counties also support farm institutes which provide technical education and also have experimental farms of their own. Appended to this research structure are two Imperial Institutes and nine Imperial Bureaux, which provide an information and abstracting service in entomology, mycology, soil science, animal health, animal nutrition and genetics, plant genetics, fruit production, agricultural parasitology, and dairying. The number of agricultural research workers in Great Britain is about 1,000. The total State expenditure on agricultural research amounted in 1938 to about £700,000. This is about 90 per cent. of the total cost, the remaining 10 per cent. being met by local authorities, universities, marketing boards, private companies and individuals, agricultural societies, fees, and sales of produce. The farmers, even when organized as marketing boards, have shown little recognition of the value of research and make no serious contribution to its cost.
A formidable, complex, and costly organization has thus grown up since 1911. No less than seven organs of the Central Government have to do with agricultural research, the personnel of which has to be fed with a constant stream of reports, memoranda, and information which must absorb a large amount of the time and energy of the men who really matter -- the investigators. A feature of the official control is the committee, a device which has developed almost beyond belief since the Agricultural Research Council came into being in 1934. Six standing committees were first formed to carry out a survey of existing research. These led to a crop of new committees to go farther into matters disclosed by this preliminary survey. In addition to the six standing committees, no less than fifteen scientific committees are dealing with the most important branches of research. Twelve of these fifteen committees are considering the diseases of crops and live stock -- the main preoccupation of the Council at the present time.
Is so much machinery necessary? Between the Treasury (which decides what sum can be granted) and the Research Institutes, would not a single agency such as the Ministry of Agriculture be all that is needed in the way of control? This would appear likely when it is remembered that there is one thing only in research that matters -- the man or woman who is to undertake it. Once these are found and provided with the means, nothing else is necessary. The best service the official organization can then perform is to remain in the background, ready to help when the workers need assistance. It follows then that simplicity and modesty must always be the keynote of the controlling authority.
A serious defect in the research organization proper is encountered at the very beginning. The Research Institutes are organized on the basis of the particular science, not on recognized branches of farming. The instrument (science) and the subject (agriculture) at once lose contact. The workers in these institutes confine themselves to some aspect of their specialized field; the investigations soon become departmentalized; the steadying influence of firsthand practical experience is the exception rather than the rule. The reports of these Research Institutes describe the activities of large numbers of workers all busy on the periphery of the subject and all intent on learning more and more about less and less. Looked at in the mass, the most striking feature of these institutions is the fragmentation of the subject into minute units. It is true that attempts are made to coordinate this effort by such devices as the formation of groups and teams, but as will be shown later this rarely succeeds. Another disquieting feature is the gap between science and practice. It is true that most, if not all, of these establishments possess a farm, but this is mostly taken up with sets of permanent experiments. I know of no research institute in Great Britain besides Aberystwyth where a scientific worker has under his personal control an area of land with his own staff where he can follow the gleam wheresoever it may lead him. Even Aberystwyth stops short before the animal is reached. The improved strains of herbage plants and the method of growing them are not followed to their logical conclusion -- a flock of healthy sheep ready for the market and a supply of well-nourished animals by which the breed can be continued.
Has the official machine ever posed to itself such questions as these? What would be the reaction of some Charles Darwin or Louis Pasteur of the future to one or other of these institutes? What would have been their fate if circumstances had compelled them to remain in such an organization, working at some fragment of science? How can the excessive departmentalization of research provide that freedom without which no progress has ever been made in science? Is it rational in such a subject as agriculture to attempt to separate science and practice? Will not the organization of such research always be a contradiction in terms, because the investigator is born not made? The official reply to these questions would form interesting reading.
How does this research organization strike the tillers of the soil for whose benefit it has been created? The farmers complain that the research workers are out of touch with farming needs and conditions; that the results of research are buried in learned periodicals and expressed in unintelligible language; that these papers deal with fragments of the subject chosen haphazard; that the organization of research. is so cumbersome that the average farmer cannot obtain a prompt answer to an inquiry and that there are no demonstration farms at which practical solutions of local problems are to be seen.
There seems to be only one effective answer to these objections. The experiment station workers should take their own advice and try out their results. The fruits of this research should be forthcoming on the land itself. All the world over this simple method of publication never fails to secure the respect and attention of the farming community; their response to such messages is always generous and immediate. In Great Britain, however, the retort of the administration takes another line. The idea is fostered that the experiment stations are arsenals of scientific knowledge which actually needs explanation and dilution for the farmer and his land to benefit. Thus in dealing with this point the PEP Report states: 'One of the principal tasks of the administrator is to ensure that the general body of scientific knowledge, including recent results of the research workers' efforts, is brought to the farmer in such a way that he can understand it and apply it on his farm.' The most effective way of doing this is for the organization to demonstrate, in a practical way for all to see, the value of some, at any rate, of these researches. This simple remedy will silence the critics and scoffers; any delay in furnishing it will only add fuel to the fire. After all, a research organization which costs the nation £700,000 a year cannot afford to have its operations called in question by the very men for whose benefit it has been designed. The complaints of the farming community must be removed.
A system not unlike that just described in Great Britain has been adopted in the Empire generally. There is, however, one interesting difference. The official machinery is comparatively simple; the multiplication of agencies and supervisory committees is not so pronounced; the step from the Treasury to the farmer is much shorter. When, however, we come to the research proper, the system is very similar to that which obtains in Great Britain. There is the same tendency to divide research into two groups -- fundamental and local; to rely on the piecing together of fragments of science; to extol the advantages of co-operation; to adopt the team rather than the individual. It is the exception rather than the rule to find an investigation in the hands of one competent investigator, provided with land, ample means, and complete freedom.
The completion of an imperial chain of experiment stations for fundamental research was emphasized by a Conference (Report of the Imperial Agricultural Research Conference, H.M. Stationery Office, London, 1927) which met in London in 1927. The financial depression, which set in soon after the Report appeared, interfered with this scheme. No additions to the two original links of the chain of five or six super-Research Institutes contemplated -- sometimes irreverently referred to as the 'chain of pearls' -- have been added to the one in the West Indies (Trinidad) and the other in East Africa (Amani).
Two examples will suffice to illustrate the methods now being employed in this fundamental research work. These are taken from a recent paper by Sir Geoffrey Evans, C.I.E., entitled 'Research and Training in Tropical Agriculture', which appeared in the Journal of the Royal Society of Arts of February 10th, 1939. Sir Geoffrey selected the current work on cacao and bananas when explaining how research is conducted at the Imperial College of Tropical Agriculture in Trinidad. He laid great stress on the merits of team work, a method of investigation which we must now examine. These Trinidad examples of research do not stand alone. They resemble what is going on all over the Empire, including India. Similar work can be collected by the basketful.
In 1930 a study of cacao was commenced in Trinidad in two directions -- botanical and chemical. After a preliminary examination of the crop, which is made up of a bewildering number of types, varying widely in fruitfulness and quality, a hundred special trees were selected as a basis for improvement. As cacao does not breed true from seed, methods of vegetative reproduction by means of cuttings and bud wood were first studied. The mechanism of pollination, however, showed that cacao is frequently self-sterile and that many of the special trees required to be cross-pollinated before they could set seed. Suitable pollen parents had then to be found. Manurial experiments on conventional lines led to numerous field experiments all over the island as well as to a detailed soil survey. The biochemical study of the cacao bean produced results described as intricate and baffling; no correlation between the tannin content and quality emerged. The Economics Department of the College investigated the decline of the industry since the War, and established the interesting fact that a cacao plantation reaches its peak in about twenty-five years and then begins to decline. The causes of this decline have been studied and the system of regenerating old plantations by supplying vacancies with high-yielding types has been devised. As, however, the decline of these cacao estates is more likely to be due to wornout soil than anything else, this method by itself is not likely to succeed. Pests and diseases take their toll of cacao, so the entomologists and mycologists were called in to deal with thrips -- the most serious insect pest -- and the witch-broom disease -- a fungous pest which has done great damage in the West Indies.
The Trinidad investigations on the banana owe their origin to the outbreak of the Panama disease (Fusarium cubense) all over the West Indies and the Central American Republics. When the nature of the trouble was established by the mycologists, a search for immune and resistant varieties followed. This included plant breeding, the investigation of the causes of seedlessness, the raising of numerous seedlings, and the search for the ideal parent from which to breed a new commercial banana which is disease-resistant, seedless, of good quality, and capable of standing up to transport conditions. In this work the assistance Or the Royal Botanic Gardens at Kew was enlisted; it involved the problem of protecting the banana in the West Indies from disease, including virus, when importing from Malaya (the home of the chief banana of commerce -- the Gros Michel) and other places the material needed for the plant-breeding work. The problems of ripening during transport, including a study of the respiration processes during gas storage and the effect of humidity, and the reason for chilling also received attention.
These interesting investigations, which have as their aim the production of higher yields of better cacao and better bananas, have been carried on by what is known as team work. They have necessitated the services of botanists, chemists, mycologists, entomologists and economists, and both have involved considerable expense and much time.
As examples of the way in which the more difficult problems of tropical agriculture are now approached by a number of workers, they are typical of the methods of research everywhere. Many aspects of the cacao and banana problems have been studied; the methods of research have been clearly set out. The workers have evidently spared no pains to achieve success. Nevertheless, the results are negative. The paper under review suggests that matters are still very much in the programme stage; few if any tangible results have been obtained; neither the cacao nor the banana industry has been set on its feet.
If we take a wide view of these two problems and consider: (1) the present methods by which cacao and bananas are grown in the West Indies; (2) the indications furnished by disease that all is not well with these plantations, and (3) the best examples of cacao and banana cultivation to be found in the East where, by means of farm-yard manure only, heavy crops of fine, healthy produce are obtained, the suspicion grows that at least some vital factors have been forgotten in these Trinidad investigations. The spectacular response of cacao trees to humus seems to have been missed altogether and no attention has been given to the significance of the mycorrhizal association in the roots of both cacao trees and bananas. In the cacao and banana plantations in the West Indies, there is a want of balance between the crop and the animal. There is insufficient live stock. There is a disquieting amount of disease and general unthriftiness, which is associated with the absence of conditions suitable for mycorrhizal formation.
Practical experience of the best banana and cacao cultivation in India and Ceylon proves beyond all doubt that the two factors which are essential, if satisfactory yields of high quality are to be obtained and the plantations are to be kept healthy, are: (1) good soil aeration, and (2) supplies of freshly prepared humus from animal and vegetable wastes, which are needed to maintain in effective operation the mycorrhizal association. Want of attention to either of these factors is at once followed by loss of quality, by diminished returns, and finally by disease. A better way of dealing with these West Indian problems would have been by good farming methods, including a proper balance between crops and live stock, and by the conversion of all available vegetable and animal wastes into humus.
The Trinidad investigations are quoted as 'an example which can hardly fail to impress the student investigator with the necessity for co-operation'. In reality all they show is how employment can be found for a number of specialists for quite a long time, and indeed what a lot of scientific work can be done by competent workers with purely negative results as far as the yield and the quality of the crop are concerned.
It is not difficult to see the weakness of this method of approach. The problem is never envisaged as a whole and studied in the field from every angle before research on some branch of science is undertaken. Methods of crop improvement are now expected to come from the laboratory and not from the field as they have always done throughout farming history. The control of the team is of necessity very loose. It is normally placed in the hands of persons of administrative rather than practical experience and of limited training in research methods. Often they have other important duties and cannot give the time and thought required. Unable themselves to make a correct diagnosis of the case in the field, their only resource is to go on adding specialist after specialist to their staff in the hope that the study of a fresh fragment of the subject will lead them to some solution. It is almost certain that had the West Indian problems been tackled by one investigator with a real knowledge of farming combined with a wide training in science, and had he been provided with the necessary land, money, and facilities and with complete freedom in conducting the investigation, Sir Geoffrey Evans would have told a very different story. From the point of view of the students at the Trinidad College, it would have been still better to have used these crops for illustrating both methods simultaneously -- the banana studied by a single investigator, adequately equipped; cacao by means of a team. In this way the relative merits of the two methods could have been settled for all time. In all probability, two results would have been obtained: (1) the principle that the researcher is the only thing that matters in research would have been established; (2) team work would have ceased to be considered as an effective instrument of investigation.
Team work offers no solution for the evils which result from fragmentation of a research problem. The net woven by the team is often full of holes. Is the fragmentation of the problem accompanied by any other disadvantages? This question is at once answered if we examine any of the major problems of present-day farming. Two British examples will suffice to prove that an inevitable consequence of fragmentation and specialization is loss of direction. Science then loses itself in a maze of detail.
The retreat of the potato crop before blight, eelworm, and virus is one of the most disquieting incidents in British agriculture. One of our most important food crops cannot now be grown successfully on a field scale without a thin film of copper salts; a new rotation of crops from which the potato is omitted until the cysts of the eelworm disappear from the soil; a frequent change of seed from Scotland, Wales, or Northern Ireland. Evidently something is very wrong somewhere, because this crop, when grown in thousands of fertile kitchen gardens throughout the country, is healthy, not diseased. Agricultural science began by fragmenting this potato problem into a number of parts. Potato blight fell within the province of the mycologist; a group of investigators dealt with eelworm; a special experiment station was created for virus disease; the breeding and testing of disease resistant varieties was again a separate branch of the work; the manuring and general agronomy of the crop fell within the province of the agriculturist. The multiplication of workers obscures rather than clarifies this wide biological problem. The fact that these potato diseases exist at all implies that some failure in soil management has occurred. The obvious method of dealing with a collapse of this kind should have been to ascertain the causes of failure rather than to tinker with the consequences of some mistake in management. The net result has been that all this work on the periphery of the subject has not solved the problem of how to grow a healthy potato. This is because direction has been completely lost.
The same story is repeated in manuring: fragmentation has again been followed by loss of direction. Notwithstanding the fact that in the forest Nature has provided examples to copy and in the peat-bog examples to avoid, when devising any rational system of manuring, agricultural science at once proceeded to fragment the subject. For nearly a hundred years some of the ablest workers have devoted themselves to a study of soil nutrients, including trace elements like boron, iron, and cobalt. Green-manuring is a separate subject, so is the preparation of artificial farm-yard manure and the study of the ordinary manure heap. The weight of produce and the cost of manuring overshadow questions of quality. The two subjects which really matter in manuring -- the preservation of soil fertility and the quality of the produce -- escape attention altogether, mainly because direction has been so largely lost.
The insistence on quantitative results is another of the weaknesses in scientific investigation. It has profoundly influenced agricultural research. In chemistry and physics, for example, accurate records are everything: these subjects lend themselves to exact determinations which can be recorded numerically. But the growing of crops and the raising of live stock belong to biology, a domain where everything is alive and which is poles asunder from chemistry and physics. Many of the things that matter on the land, such as soil fertility, tilth, soil management, the quality of produce, the bloom and health of animals, the general management of live stock, the working relations between master and man, the esprit de corps of the farm as a whole, cannot be weighed or measured. Nevertheless their presence is everything: their absence spells failure. Why, therefore, in a subject like this should there be so much insistence on weights and measures and on the statistical interpretation of figures? Are not the means (quantitative results and statistical methods) and the subject investigated (the growth of a crop or the raising of live stock) entirely out of relation the one to the other? Can the operations of agriculture ever be carried out, even on an experiment station, so that the investigator is sure that everything possible has been done for the crop and for the animal? Can a mutually interacting system, like the crop and the soil, for example, dependent on a multitude of factors which are changing from week to week and year to year, ever be made to yield quantitative results which correspond with the precision of mathematics?
The invasion of economics into agricultural research naturally followed the use of quantitative methods. It was an imitation of the successful application of costings to the operations of the factory and the general store. In a factory making nails, for example, it is possible, indeed eminently desirable, to compare the cost of the raw material and the operations of manufacture, including labour, fuel, overhead expenses, wear and tear and so forth, with the output, and to ascertain how and where savings in cost and general speeding up can be achieved. Raw materials, output, and stocks can all be accurately determined. In a very short time a manufacturer with brains and energy will know the cost of every step in the process to the fourth place of decimals. This is because everything is computable. In a similar manner the operations of the general store can be reduced to figures and squared paper. The men in the counting-house can follow the least falling-off in efficiency and in the winning of profit. How very natural it was some thirty years ago to apply these principles to Mother earth and to the farmer! The result has been a deluge of costings and of agricultural economics largely based on guesswork, because the machinery of the soil will always remain a closed book. Mother earth does not keep a pass-book. Almost every operation in agriculture adds or subtracts an unknown quantity to or from the capital of the soil -- fertility -- another unknown quantity. Any experimental result such as a crop is almost certain to be partly due to the transfer of some of the soil's capital to the profit and loss account of the farmer. The economics of such operations must therefore be based on the purest of guesswork. The results can hardly be worth the paper they are written on. The only things that matter on a farm are these: the credit of the farmer -- that is to say what other people, including his labour force and his bank manager, think of him; the total annual expenditure; the total annual income and the annual valuation -- the condition of the land and of the live and dead stock at the end of the year. If all these things are satisfactory nothing else matters. If they are not, no amount of costings will avail. Why, therefore, trouble about anything beyond these essentials?
But economics has done a much greater disservice to agriculture than the collection of useless data. Farming has come to be looked at as if it were a factory. Agriculture is regarded as a commercial enterprise; far too much emphasis has been laid on profit. But the purpose of agriculture is quite different from that of a factory. It has to provide food in order that the race may flourish and persist. The best results are obtained if the food is fresh and the soil is fertile. Quality is more important than weight of produce. Farming is therefore a vital matter for the population and ranks with the supply of drinking water, fresh air, and protection from the weather. Our water supplies do not always pay their way; the provision of green belts and open spaces does not yield a profit; our housing schemes are frequently uneconomic. Why, then, should the quality of the food on which still more depends than water, oxygen, or warmth be looked at in a different way? The people must be fed whatever happens. Why not, then, make a supreme effort to see that they are properly fed? Why neglect the very foundation-stone of our efficiency as a nation? The nation's food in the nature of things must always take the first place. The financial system, after all, is but a secondary matter. Economics therefore, in failing to insist on these elementary truths, has been guilty of a grave error of judgement.
In allowing science to be used to wring the last ounce from the soil by new varieties of crops, cheaper and more stimulating manures, deeper and more thorough cultivating machines, hens which lay themselves to death, and cows which perish in an ocean of milk, something more than a want of judgement on the part of the organization is involved. Agricultural research has been misused to make the farmer, not a better producer of food, but a more expert bandit. He has been taught how to profiteer at the expense of posterity -- how to transfer capital in the shape of soil fertility and the reserves of his live stock to his profit and loss account. In business such practices end in bankruptcy; in agricultural research they lead to temporary success. All goes well as long as the soil can be made to yield a crop. But soil fertility does not last for ever; eventually the land is worn out; real farming dies.
In the following chapter an example of the type of research needed in the future will be described.
Carrel, Alexis. Man, the Unknown, London, 1939.
Constitution and Functions of the Agricultural Research Council, H.M. Stationery Office, London, 1938.
Damper, Sir William C. 'Agricultural Research and the Work of the Agricultural Research Council', Journal of the Farmers' Club, 1938, p. 55.
Evans, Sir Geoffrey. 'Research and Training in Tropical Agriculture', Journal of the Royal Society of Arts, lxxxvii, 1939, p. 332.
Liebig, J. Chemistry in its Applications to Agriculture and Physiology, London, 1840.
Report of the Imperial Agricultural Research Conference, H.M. Stationery Office, London, 1927.
Report on Agricultural Research in Great Britain, PEP, 16 Queen Anne's Gate, London, 1938.
Next: 14. A Successful Example of Agricultural Research
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