SOME PRINCIPLES OF FIELD EXPERlMENTS WITH SHEEP By P. G. SCHINCICEL *, and G. R. MOULE *

Transcription

1 SOME PRINCIPLES OF FIELD EXPERlMENTS WITH SHEEP By P. G. SCHINCICEL *, and G. R. MOULE * Summary The principles of scientific method, with particular reference to the role of hypotheses and experiments are outlined. Operational aspects of the design, execution, analysis and interpretation of experiments with sheep are discussed and some of the more common problems considered. I. INTRODUCTION Investigations with sheep may be grouped into three broad categories. 1. Result demonstrations, in which the outcome of a particular series of treatments is already established. The object is to demonstrate these results to a wider group of people. Such work is frequently carried out as a means of disseminating research results to industry. It is not proposed to discuss these further here. 2. General investigations include observations that do not fall into either of the other categories; e.g. pilot trials, general observations, field trials, surveys, etc., in which no clear hypothesis is being examined, nor are the results of the treatments known in advance as in result demonstrations. A great deal-of general observational work is still necessary in agricultural research in order to define the problems and to develop hypotheses for critical experimental attack. 3. Scientific experiments, in which, according to the nature of the problem, a clear hypothesis is being tested, or specific questions are being asked. The validity of a scientific experiment is determined by the precision of the hypothesis being examined, the design and conduct of the experiment, and of the analysis and interpretation of the results. Validity is not a function of geographic location. Relatively, there are as many invalid experiments carried out in Warburg baths as there are on multi-thousand-acre field stations. This paper is concerned primarily with this last category of investigations, although reference will also be made to some features of general investigations. II. THE LOGIC OF EXPERIMENTS The common sequence of events in scientific investigations is as follows. 1. The assembly of existing information on a problem, or the conduct of a series of observations designed to provide data; a detailed survey may be required. 2. The development of a hypothesis on the basis of this information and on a knowledge of biological principles which are, or might be involved. 3. The design, conduct and analysis of experiments to test the hypothesis. 4. Interpretation -of the results obtained and the formulation of new hypotheses or theories which are to be the subject of further experiments. * Division of Animal Physiology, C.S.I.R.O., The Ian Clunies Ross Animal Research Laboratory, Prospect, N.S.W. 190

2 (a) Hypotheses (i) Definition-Feibleman ( 1959) defines a hypothesis as a proposition which seems to explain observed facts and whose truth is assumed tentatively for purposes of investigation. A good hypothesis is one that offers a possible explanation or that ascribes an adequate cause. (ii) Criteria of a good hvpothesis (Feiblewzan 19.59)- 1. It should adequately explain known facts. 2. It should, in general, offer the simplest explanation, but be broad enough to cover all observed facts., 3. It must lend itself to experimental investigation: if a hypothesis cannot be examined experimentally it is scientifically valueless and belongs to the realm of metaphysics rather than science. 4. It should be sufficiently strong and scientifically interesting to demand inquiry. (b) Experiments (i) Definition- Dictionaries are not particularly helpful in defining the word experiment in the sense that it has come to acquire in science. The first definition in the Shorter Oxford English Dictionary is- The action of trying anything - but many workers appear to have missed the qualification that this meaning is now archaic! Feibleman ( 1960) def mes an experiment as a deliberate interference with phenomena in such a way as to aid a decision concerning a hypothesis. The central position of a hypothesis in the operation of an experiment is clear in this definition. Comparisons are an essential feature of an experiment in the sense that the term is used here: there must therefore be at least two treatments (using the word in the broadest sense to include control groups also). Statistical methodology is designed to increase the precision of these comparisons, and the testing of the hypotheses. An observation on a single group of animals, all treated alike, is not an experiment in the accepted context-it is an observation. (ii) Criteria of a good.experiwzent (Feibleman 1960)- 1. It should be properly isolated, i.e. uncontrolled variables should be eliminated, or, if this is not possible, then they should be randomized over the treatments. It is particularly important to avoid the confounding s of an uncontrolled variable with one of the treatments. 2. It should be analytical. Basically we are seeking knowledge of causes of observed phenomena; the identification of causes of events as distinct from a simple catalogue of effects is part of the difference between experiments and observations. 3. Experiments must be repeatable and should be repeated. 4. An experiment should be crucial, i.e. it should support or negate the hypothesis being examined. It is here that there is frequently room for great ingenuity in the planning of experiments. 5. It is desirable that experiments be heuristic, i.e. they should open up new avenues of research and ask more questions than they answer. 191

3 III. OPERATIONAL ASPECTS OF EXPERIMENTS WITH SHEEP The principles of experiments with sheep, or with any other domestic animal, do not differ from those in other fields of scientific endeavour. The early logic of scientific method was evolved very largely in association with physical sciences; the same logic applies to research in biological sciences. Partly as a consequence of the inherent variability of biological material, progress in agricultural research has required the development of a relatively sophisticated statistical methodology. The weakness of many field investigations with sheep is frequently the logical basis, rather than the statistical techniques employed. Advanced statistical analyses, after observations have been completed, are not a substitute for an efficient experimental design based on an accurate formulation of the biological problem to be investigated. The conduct of an experiment involves three interdependent phases: design, execution, and analysis. It is impossible to consider these exhaustively; we can do little more than enumerate some of the principles and mention a few of the more common pitfalls and fallacies. All experiments involve the measurement of differences, particularly those arising from the application of treatments. In the final analysis we are concerned with differences arising from three main sources: firstly differences -between individual animals; secondly, differences arising from the application of experimental treatments; and thirdly, miscellaneous differences arising from the operation of extraneous factors which may or may not be identified and measured. Recognition of, and attention to all these sources of variation is essential in the design, execution and analysis of any experiment. (a) Conduct of Experimem (i) Selection of animals-if it is advisable to reduce the variation between animals, it may be desirable to select carefully for uniformity of the experimental animals. This approach has been exploited particularly with identical twins in cattle. No such studies of variation appear to have been made with sheep, but there may well be instances where selection of twins or half sibs offers considerable economy in experimental material. On the other hand, if it is desired to make inferences from the experimental results to wider populations, the chosen animals must be representative of those populations. (ii) Ahmbers of aniwaals -The number of animals required per group varies directly with the variance between animals in the character to be measured, and inversely with the square of the magnitude of differences to be detected. There is no justification for using numbers of animals greatly in excess of those needed to test the hypothesis being examined. Increasing group size does, to a point, increase precision, but increasing the probability from 0.05 to O-00 1 that the differences between treatments are not due to chance does not alter the interpretation of the experiment, so far as treatment differences are concerned. Replication is a desirable practice in most experiments. Thus, if physical facilities allow 12 sheep per treatment cell in a particular design, it is much more efficient to provide 3 or 4 replications, each with 4 or 3 sheep per treatment cell in each replication, than to have no replication and one treatment cell group of

4 The number of animals per group also depends on the nature of the measurements to be made. Experiments involving quanta1 characteristics (e.g. all or none responses) generally require very much greater numbers than those in which quantitative characters are measured. It is sometimes possible to reduce the sample size by replacing the discrete variate by a related quantitative one, e.g. days to death instead of the dead/live alternative.. (iii) A Ilocation of animals-the need for randomization of animals to treatments cannot be over-emphasized. Groups should be balanced, however, with respect to such factors as age, sex, previous history which might have affected body weight, and so on. If this is not done, there is serious risk (particularly in small groups) that the structure of the groups will be biased, leading to a confounding of a non-treatment variable with a treatment, e.g. unequal distribution of sexes in treatment groups. (iv) Treatwzen ts-the levels of treatments should be extreme enough to give unequivocal effects. These levels will be partly determined from existing knowledge of their probable effects and partly from a knowledge of the numbers of animals per group. It is essential in many experiments that the treatments applied are actually those scheduled. This is especially so in grazing experiments, for example, where uncontrolled animals-rabbits, kangaroos, etc.-may involve an unscheduled treatment load. (v) The characters to Wteafswe- Only those characters should be measured that are necessary for the examination of the questions being investigated. One should beware of measuring a host of others on the ground that it would be nice to have the information. Objective measures are superior to subjective ones, although there is a place for subjective scoring when objective measurement is either not possible or is prohibitively expensive. Whenever subjective scores are used, the desirability of total number of classes considered. using photographic standards, and the restriction of the to less than 12 (5 or 6 is usually adequate) should be (vi) Techniques of measurement-techniques of sampling and measurement should not introduce bias. Characters such as body weight, area of tattoo patches on the mid-side of the body, and blood levels of various metabolites are related to the duration of fasting. It is necessary that measurements are made in such a way as to ensure that the effects of fasting are not confounded with treatments. This problem frequently arises in field experiments in which large numbers of animals in several paddock groups are involved. If all animals are brought to central handling facilities at about the same time, but are then examined in treatment groups, substantial bias may be introduced into the measurements. (vii) Analysis of results of experiwzents- In general, the statistical technique to be used is determined by the hypothesis being tested and the design of the experiment. In the planning, it is important to consider computing facilities among the physical needs for completion of the experiment. 193

5 (b) Interpretation of Results At least one of the following three questions arises in the interpretation of most experiments. 1. How large are the differences between treatments? (i.e. the estimation of treatment effects.) 2. What is the relative importance of the variables studied with respect to total variation? (i.e. estimation of variance components.) 3. How reliable are the treatment differences which have been observed? (i.e. making significance tests.) The nature of the hypothesis being examined determines which of these questions receives the greater emphasis. In experiments with sheep the magnitude of treatment effects is commonly of paramount interest. This information may be obtained by simple arithmetic or by more sophisticated methods where necessary, but it is not obtained from the significance tests in an analysis of variance. Such tests give an estimate of the probability of the observed differences being due to chance, and depend on the total number of observations and the number of treatments as well as on the magnitude of the treatment differences and general variability of the data. Statistical significance should not be confused with biological significance, which very largely depends on the magnitude of treatment differences. Where one is interested in the comparative importance of different treatment classifications as causes of variation in a character, then some form of variance component analysis is required. A simple comparison of the significance levels attached to the different treatment classifications in an analysis of variance is not always enough. Significance tests are only part of the story, albeit usually a necessary part. (i) Some fallacies-the fallacy of interpreting statistical significance for biological significance has been referred to above. A second common fallacy is that of post hoc, ergo propter hoc i.e. after it, therefore due to it. It is the fallacy of confusing consequence with sequence. On Sunday we prayed for rain; on Monday it rained; therefore prayers caused the rain (Fowler 1957). A somewhat similar problem is that of confusing correlation with causation. These fallacies seem to be rather more common in investigations of an observational kind than in well-designed experiments. They are particularly likely to arise when it is logical, on the basis of other biological principles, that one thing should cause another; particularly when we want it to. Finally, the biologist s duty is not complete until he has reported the results of his experiments. Work not published is, in effect, work not done. REFERENCES FEIBLEMAN, J. K. (1959).-Perspectives in Biology and Medicine 2: F IEBLEMAN, J. K. (1960).-Perspectives in Biology and Medicine 4: F OWLER, H. (1957).-Dictionary of Modern English Usage. (Oxford, Clarendon Press. ) 194