Experimental design treatment

D. R. Cox, P/anning of Experiments,]ohxi Wiley Sons, Inc., New York, 1958. This book provides a simple survey of the principles of experimental design and of some of the most usehil experimental schemes. It tries "as far as possible, to avoid statistical and mathematical technicalities and to concentrate on a treatment that will be intuitively acceptable to the experimental worker, for whom the book is primarily intended." As a result, the book emphasizes basic concepts rather than calculations or technical details. Chapters are devoted to such topics as "Some key assumptions," "Randomization," and "Choice of units, treatments, and observations."... 

With two of the concentrations in large excess, the fourth-order kinetic expression has been reduced to a first-order one, with considerable mathematical simplification. The experimental design in which all the concentrations save one are set much higher, so that they can be treated as approximate constants, is termed the method of flooding (or the method of isolation, since the dependence on one reagent is thereby isolated). We shall consider the method of flooding further in Section 2.7. Here our concern is with the data analysis it should be evident that the same treatment suffices for first-order and pseudo-first-order kinetics. 

The experimental design should include a weed-free control, a weedy control, a weed free but with weed residue treatment, and at least one treatment with weeds and residue present. Various levels of weeds and weed residue could be incorporated into the study. 

Soybean bloassays of root exudates. Four soybean seeds ( Bragg ) were planted In each of 100 12.5 cm plastic pots filled with an artificial soil mix consisting of perlite/coarse sand/coarse vermiculite 3/2/1 by volume. After one week the plants were thinned to two per pot and the treatments were begun. The experimental design was a completely randomized design with 10 replications (pots) per treatment. On the first day of each week each pot was watered with 300 ml effluent from the appropriate growth units. On the fifth day of each week all pots were watered with Peter s Hydro-sol solution with CaCNOj. At other times the pots were watered as needed with tap water. On the second and fifth day of each week the height of the soybeans (base to apical bud) was measured. 

Root elongation bloassay of root exudates. Five ml aliquots of the root exudates were pipetted onto three layers of Anchor1 germination paper In a 10 by 10 by 1.5 cm plastic petri dish. Twenty five radish or tomato seeds were placed in a 5x5 array in each petri dish. Radish seeds were incubated at 20C for 96 hours tomato seeds were incubated at 20C for 168 hours, before the root length was measured. Experimental design was a completely randomized design with three replications (dishes) per treatment per bioassay seed species. The bioassay was repeated each week for 23 weeks. 

The experimental design was a randomized complete block with eleven treatments, two soybean varieties and five blocks (reps). The experiment was conducted six times at two week intervals, starting four weeks after the weeds were planted in the pipes. 

Random allocation of animals to treatment groups is a prerequisite of good experimental design. If not carried out, one can never be sure whether treatment-... 

For the reader who would like to further explore experimental design, there are a number of more detailed texts available which include more extensive treatments of the statistical aspects of experimental design (Cochran and Cox, 1975 Diamond, 1981 Federer, 1955 Hicks, 1982 Kraemer and Thiemann, 1987 and Myers, 1972). 

The third type of experimental design is the factorial design, in which there are two or more clearly understood treatments, such as exposure level to test chemical,... 

In previous chapters, many of the fundamental concepts of experimental design have been presented for single-factor systems. Several of these concepts are now expanded and new ones are introduced to begin the treatment of multifactor systems. 

The saturated fractional factorial designs are satisfactory for exactly 3, or 7, or 15, or 31, or 63, or 127 factors, but if the number of factors is different from these, so-called dummy factors can be added to bring the number of factors up to the next largest saturated fractional factorial design. A dummy factor doesn t really exist, but the experimental design and data treatment are allowed to think it exists. At the end of the data treatment, dummy factors should have very small factor effects that express the noise in the data. If the dummy factors have big effects, it usually indicates that the assumption of first-order behavior without interactions or curvature was wrong that is, there is significant lack of fit. 

As analytical chemists, we are often called upon to participate in studies that require the measurement of chemical or physical properties of materials. In many cases, it is evident that the measurements to be made will not provide the type of information that is required for the successful completion of the project. Thus, we find ourselves involved in more than Just the measurement aspect of the investigation —we become involved in carefully (re)formulating the questions to be answered by the study, identifying the type of information required to answer those questions, making appropriate measurements, and interpreting the results of those measurements. In short, we find ourselves involved in the areas of experimental design, data acquisition, data treatment, and data interpretation. 

These four areas are not separate and distinct, but instead blend together in practice. For example, data interpretation must be done in the context of the original experimental design, within the limitations of the measurement process used and the type of data treatment employed. Similarly, data treatment is limited by the experimental design and measurement process, and should not obscure any information that would be useful in interpreting the experimental results. The experimental design itself is influenced by the data treatment that will be used, the limitations of the chosen measurement process, and the purpose of the data interpretation. 

All were double-blind controlled evaluations and established iprindole as at least as effective as imipramine, and one study [195] included an examination of the doctor-patient interaction as a factor in such work (a similar discussion was felt necessary, as noted above [179] in the evaluation of oxpertine). In only two [192, 194] of the above reports is it possible to estimate the frequency and severity of anticholinergic side effects, thou in the one case [192] the care taken in the experimental design and the number of patients observed leaves little doubt that the dry mouth, constipation, etc. characteristic of imipramine therapy is either greatly reduced or even absent during iprindole treatment. This point is confirmed in an extension of this team s work to include a 12 month toxicity study [197] which, in addition, failed to produce evidence of haemopoitic, hepatic, cardiac, ocular or renal damage. Similar results followed other work. 

The above treatment has implicitly assumed that the experimental design was such that the number of trials was fixed at 12 and the observation was the number of heads. However, an alternative design could have been to continue tossing the coin until 3 tails were obtained, and the observation would be n, the number of tosses required to produce the 3 tails. In this case, the statistic for judging the data is just n. But the distribution of n, the number of tosses to produce 3 tails, is given by the negative binomial ... 

Experimental design and methods depend primarily on the questions to be answered (Kraemer and Telch, 1992). Clinical trials are meant to address clinically relevant questions and generate data that are ultimately relevant to the treatment of patients in usual practice. The importance of clearly identifying the primary experimental question cannot be over-... 

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