1. Distinguish between Design structure and Treatment structure
   1. Introduction

i.      There is a great deal of diversity in studies and it is very useful to categorize them in a variety of ways. The design structure is basically the physical layout of the study. For example, if we compare two weightings of each of ten animals with those of twenty animals, in each case there are twenty data points but the design structure is different-and the analysis will differ. The design structure must be known to correctly interpret the results and their implications. The treatment structure of a study describes the possible relationships among factors. For example, factorial treatment structure will involve the application of all possible factor combinations (or fractions thereof) to experimental units.

1. Rule of Thumb

i.      Distinguish between the design structure and the treatment structure of a study.

1. Illustration

i.      The introduction to this rule presented a simple example. A richer example is given in Rule VI, with a factorial design (treatment structure) with each treatment combination assigned to different subjects or the same subjects (design structure). In that example the treatment structure was the same but the design structure of Design A differed from that of Design B.

ii.      The example discussed in the previous rule has a factorial treatment structure, the design structure involves randomly allocating animals to the treatment combinations-identical to what would be done of the study involved six unrelated treatments.

1. Basis of the Rule

i.      The design structure determines the layout of the analysis. The treatment structure determines the finer partitioning of the degrees of freedom.

1. Discussion and Extensions

i.      The concepts of treatment and design structure are proven to be helpful in thinking about the development of designs for studies. They indicate that there are constraints imposed by the study units and the treatment units. Suppose that in the example above it was not possible to assign all treatment combinations to the same subjects (possibly because of carry-over effects or a practical problem of not being able to get the subjects to come in four times). The treatment structure is still of interest but the design structure restricts the design of experiments. A great deal of work has been done to make treatment structures and design structures compatible. For example, in factorial studies it may not be feasible (because of cost or time constraints) to study all possible factorial combinations-a four factor experiment with three levels per factor requires 3₄=81 experimental units per replication. This leads to consideration of fractional factorial designs mentioned in Rule IV. See Cox and Reid (2000) for more examples and further discussions. The treatment structure is the driver in the planning experiments, the design structure is the vehicle.

ii.      Design and treatment structures in experimental designs often require trade-offs. It is important to understand the differences between these strictures, to know about possible compromises and to be able to apply the best statistical strategies to the design and analysis of the proposed research.

IX.            Make hierarchical analysis the default analysis

1. Introduction

i.      This section assumes a factorial treatment structure with each factor at two levels such as presence or absence, low dose or high dose. Treatment effects in this kind of study can be classified as main effects (attributable to a single factor) or interaction effects (attributable to two or more factors). The interaction effects can be sorted into two-way, three-way or up to k-way interactions if there are k factors. An effect is of higher order if it involves more treatment combinations. With k factors there are 2_k possible methods to consider-very quickly a large number. The following rule gives a rationale for assessing a smaller number of models. In addition, it provides a guide to the ordering of the effects in the analysis.

1. Rule of Thumb

i.      Ordinarily, plan to do a hierarchical analysis of treatment effects by including all lower order effects associated with the higher order effects.

1. Illustration

i.      Consider a two-factor design consisting of factors A and B. Each factor can be present or absent. The possible different impacts of treatment are A (i.e., the effect of A present compared with A absent), B (present or absent) and A X B (both A and B present or both absent). If each of these can be in or out of the model there will be 2₃=8 possible models. If there are 3 factors, A, B and C, there are 2₇=128 possible models to analyse. The rule states that only hierarchical models should be considered. For example, a model consisting solely of the interaction A X B is not allowed. If A X B is to be examined, the rule states that A and B should also be in the model. Besides the null model (no treatment effects), in the three-factor example, there are 18 hierarchical models-a substantial reduction from 128. Not all of these 18 models are of equal interest. For example, one of the 18 models involves only the factors B, C, and the interaction B X C. why analyse only these two factors when A is also in the experiment? If the decision is made that only hierarchical models using all factors will be examined then only 9 models need to be assessed.

1. Basis of the Rule

i.      There are three basis for the rule. First, the concept of parsimony in connection with Ockham’s razor applies here. Second, a hierarchical analysis is more straightforward. Third, interpretation will be less convoluted.

1. Discussion and Extensions

i.      One rule sometimes stated is that if the interaction in a hierarchical model is significant then there is no need to examine the associated main effects. The basis for this agreement is that the presence of interaction implies differential effects of one factor at the different levels of a second factor. There is merit to this rule but there may be situations where there is both an interactive effect and a main effect, and it may be interesting to compare the magnitude of the two effects.

ii.      Bryk and Raudenbush (1992) provide a thorough review of hierarchical models and the advantage of using this analytic strategy.

iii.      Interpreting experimental results is difficult. Using the hierarchical inference principle provides an initial simplification and guidance through the mass of data to be analysed. If a non-hierarchical analysis is contemplated, there should be a deliberate justification for this approach.

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1.  VI.            Analysis follows design
   1. Introduction
      1.                                                               i.      It is not always clear what analysis is to be carried out on the data. One of the key considerations is to determine how the randomization was done since it provides the basis for the tests of significance and other inferential procedures.
   2. Rule of Thumb
      1.                                                               i.      The analysis should follow design.
   3. Illustration
      1.                                                               i.      Consider the two following designs assessing the effects of pollution and exercise on asthmatic subjects. In Design A, 40 asthmatic subjects are assigned randomly to one of the 4 treatment combinations. In Design B, each of 10 asthmatic subjects receives all 4 treatments in random order; thus each subject constitutes a totally randomized block. Both designs will generate 40 observations. But the analysis is going to be very different. The Design A is a completely randomized design with the four treatment combinations randomly assigned to subjects; the randomization is carried out in such a way that equal numbers of subjects are assigned to the four treatment combinations.
      2.                                                             ii.      Design B is a type of repeated measures design with all treatment combinations assessed within each subject. The analysis is quite different.
   4. The basis of the Rule
      1.                                                               i.      The sampling strategy used to generate the data determines the appropriate analysis-tying the two together tightly.
   5. Discussion and Extensions
      1.                                                               i.      The difference between the two analyses is most clearly seen in the degrees of freedom for the error terms. In Design A, the error term has 36 degrees of freedom, based on 9 degrees of freedom for each of the cells. It is a between-subject error term. In Design B, 9 degrees of freedom are subtracted to account for between-subject variability leaving 27 degrees of freedom for the error term. This is a within-subject error. Ordinarily, this error term will be smaller than the error term for Design A, so there will be greater power to detect a treatment effect.
      2.                                                             ii.      Violations of the rule usually affect the error term but not it is not necessary that they will have an impact over the estimate. For example, analyzing paired data as two independent data sets still provide a valid estimate of the difference but an invalid estimate of the precision of the estimate.
      3.                                                           iii.      There are subtle issues that are not recognized regularly. It is incorrect to analyze a two-factor design involving one factor which is the treatment factor, and the other a classification factor (for example, high school education) as a factorial design since education is not randomly allocated to the subjects. Such an analysis may be valid but will require some of the hand-waving discussed in Rule I and Rule II. Technically, the treatments are nested with education.
      4.                                                           iv.      Just as sample size calculations should be based on the proposed analysis (Rule II), the statistical analysis should follow design. These rules indicate the tight linkage between analysis and design; both forces the investigator to look forward and backward.

1. Plan to graph the results of an analysis
   1. Introduction
      1.                                                               i.      As will be discussed, statistical packages usually do not do a very good job of presenting graphical analysis of data.
   2. Rule of Thumb
      1.                                                               i.      For every analysis, there is an appropriate graphical display.
   3. Illustration
      1.                                                               i.      Nitrogen Dioxide (NO₂) is an automobile emission pollutant. Sherwin and Layfield (1976) studied the protein leakage in the lungs of mice exposed to NO₂ at 0.5 parts per million (ppm) NO₂ for 10, 12 and 14 days. Half of a total group of 38 animals was exposed to the NO₂; the other half served as controls. This is a two-factor factorial design with one factor (Pollutant) at two levels, and the other factor (Days) at three levels.
      2.                                                             ii.      Since the controls are intended to adjust for day-day variation in response, it is appropriate to subtract the control mean from the treatment mean on each day. This provides the basis for the test of interaction of treatment and days.
   4. The basis of the Rule
      1.                                                               i.      Every statistical analysis involves estimates, relationships among the estimates, the precision of these estimates and possibly covariates. These features can all be displayed pictorially.
   5. Discussion and Extensions
      1.                                                               i.      In the case of treatment, comparisons use interaction plots rather than bar graphs. A row in an analysis of variance table with, say k-1 degrees of freedom involves a comparison of k quantities. These quantities can be meaningfully graphed to illustrate the effects and their significance. Factorial designs are particularly easy to graph. Interactions involve some kind of non-parallelism and this can be nicely illustrated in a variety of ways.
      2.                                                             ii.      This rule basically illustrates the importance of thinking graphically about the interpretation of the results of a study.

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1. Agricultural Statistics
   1. Livestock Statistics
      1.                                                               i.      The livestock census conducted quinquennially by the DES constitutes the principal source of data on livestock and poultry populations and their composition.
      2.                                                             ii.      The responsibility for collecting data for the livestock census rests with the State Governments. In rural areas, the data are collected by the normal revenue agencies, if such agencies exist. In places where there are no revenue agencies, village chowkidars, school teachers or panchayat employees are asked to collect data. In urban areas, the data are collected by the sanitary staff of the municipalities. Enumerators complete all preliminary work, e.g. listing of households, contacting household heads, etc., 15 days or one month prior to the reference date (usually 15 April). The count of livestock is considered final only after the enumerator visits the household on the reference day, and the final data relate to the animals actually found living at sunrise on this day. The States furnish tehsil-wise figures on number of livestock, poultry, agricultural machinery and implements, fishing crafts and tackles to the DES. The DES compiles the data received from the States and publishes them in the Indian Livestock Census (quinquennial), a report in two volumes. Vol. I gives all-India and State-wise figures while Vol. II gives district-wise details. The rural and urban break-up of the data is also available in both the volumes. There is considerable time lag between the census and the publication of results. Provisional figures are, however, published in the Agricultural Situation in India (monthly). Each State also brings out its own Livestock Census Report, giving tehsil-wise data for the State.
      3.                                                           iii.      The position regarding the statistics on livestock products, however, is not at all satisfactory. Till the late fifties, the only available information on the production of major livestock products, viz. milk, ghee and other milk products, meat, poultry, eggs, wool, bones, bristles, etc., came from marketing surveys carried out by the Directorate of Agricultural Marketing and Inspection (DAMI) from time to time. As the surveys were not based on sound statistical methods, the data could not be considerable reliable. Some estimates of milk production are now prepared by the DAMI during each livestock census, which are presented in the CSO publication Statistical Abstract, India (annual). The NSSO also collects data on the quality and value of livestock products in some of the rounds.
      4.                                                           iv.      A few States, e.g. U.P., Gujarat and Maharashtra, have been conducting since the Fourth Plan period sample surveys for the estimation of the production of milk, eggs and wool every year based on survey techniques developed by the Institute of Agricultural Research Statistics. In the Fifth Plan period, the Union Department of Agriculture sponsored a scheme to enable the States to initiate sample surveys for estimation of production of all major livestock products on a continuing basis. So currently a system has been developed in all the States for collecting reliable statistics on livestock products year after year.

1. Fishery Statistics
   1.                                                               i.      For the purpose of collection of statistics, fish production may be considered in its two aspects:
      1. Production of marine (or sea) fish and
      2. Production of inland (or fresh-water) fish
      3.                                                             ii.      Estimates of marine fish production are being furnished annually since 1950 by the Central Marine Fisheries Research Institute (CMFRI). The CMFRI obtains, for each maritime State, information regarding total landings of marine fish by mechanised and non-mechanised boats and their variety-wise composition, the man-power used, the type of net used, etc., on the basis of sample surveys. In the case of landing by trawlers, the information on catches is obtained through complete enumeration. In this way, State-wise estimates of catches of fish are provided each month. The maritime States also make independent surveys to estimate making fish production but their estimates often vary considerably from those worked out by the CMFRI. The Indian Journal of Fisheries (half-yearly), issued by the CMFRI, sometimes publish figures of marine fish production as estimated by the CMFRI.
      4.                                                           iii.      As regards inland fish production, no direct estimates are available. Until 1960, the Fishery Development Adviser (FDA) was giving very rough indirect estimates. Since them the fish marketing officials of the different State Governments have been collecting daily statistics of landing from various sources, viz. ponds, tanks, reservoirs, lakes and river stretches. These estimates furnished by the States to the FDA are given in the CSO publication Statistical Abstract, India (annual). The estimates made by the State Governments are based on the quantities of fry and fingerling distributed, accounts of lease fees realised, quantities marketed and other factors. As the method is still not very satisfactory, pilot studies have been undertaken by the NSSO in some States to evolve a suitable methodology for estimation of inland fish resources including estimation of production. Data on the number of fishing crafts and tackles are collected during the Livestock Census.

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1. Phase III Trials
   1. Consideration in Planning
      1.                                                             v.      Treatment Allocation Ratio.
         1. Equal allocation of patients to both the two treatments is a common practice. However, it may be appropriate to allot patients randomly in the ratio of 60:40 or 67:33 (2:1) when comparing a new treatment with an old one or when treatment is much more difficult or expensive to supervise. The chance of detecting the real difference between the two treatments is not reduced much as long as the ratio is not extreme than 2:1 (Peto et al. 1976).
      2.                                                           vi.      Use of a Concurrent or Historical Control Group.
         1. A basic requirement by most clinical trials is the “controls”, which is a group of patients corresponding in characteristics to the especially treated group but is not given the treatment. The issue is whether a concurrent group should be used or whether historical controls suffice. The ethical question is whether it is appropriate to withhold from any patient a treatment that might give him benefit. Of course, the effectiveness of the treatment is not proven; if it were, there would be no need for a trial. On the other hand, the treatment has passed trials of phase I and II, so there must be some basis which is justifying a trial. The severity of the problem depends upon what is at stake. If, for example, the treatment in the trial is for fast relief of a common headache, then the morality of a rigidly controlled trial would not be seriously in doubt. However, it might be quite impossible to withhold, even temporarily, any treatment for a disease (e.g., cancer) in which life or death or serious after effects were at stake. In the other hand, it should be realized that a new treatment is certainly not always the best and by no means free of danger. For example, certain antibiotics and hormones are not always innocuous. Thus, comparative trial must be exhaustively weighed in the balance of ethics, each according to its own circumstances and its own problems.
         2. The use of historical controls has been a debatable subject, especially in clinical trials of cancer. The use of historical controls allows all current patients in the trial to receive the new treatment and results compared with that of patients previously treated with the standard treatment. The major problem with historical control is that one is unable to ensure comparability between the groups of patients and methods of evaluation.
      3.                                                         vii.      Treatment Management.
         1. It is important to manage patients on each treatment regimen in the same manner. Definitions of response and that of toxicity should be exactly the same for patients in each and every treatment group. The decision to remove the patients from a trial should be applied in the same way in each and every treatment group. If some investigators have a preference for one of the treatments so that patients are maintained on it longer or are classified as toxic only when toxicity is very severe, and the results could be biased. On the other hand, patients who are on a treatment known to be more toxic may be more likely to report an adverse effect. One way to avoid physician’s or patient’s potential bias or different managements of treatment is to do a double-blind trial. In a double-blind trial, the treatments are prepared in identical forms so that neither of the patients nor the physicians conducting the trial are aware of which specific treatment is being given. However, double-blind trials can be difficult to organise and less effective than expected in bias reduction. For example, if one wants to compare a chemotherapy with no therapy for leukaemia patients, if the therapy is in tablet form, it would be necessary to give tablets to both sets of patients (dummy tablets to the control group) and to take blood samples for each to measure the white blood cells. This could be troublesome in the case of management of the clinical trials. Also, the physician is aware of the types of toxicity to be expected and can find out, by observing toxicity, which patients are receiving each treatment. In addition, it is difficult to explain a double-blind trial to patient and his family. Therefore a double-blind study should be given careful consideration. In certain cases, they obviously cannot apply, such as for studying surgical procedure or radiation therapies.

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1. Phase III Trials
   1. The basis of phase III trials can be found in the well-known joke about the famous biostatistician, when asked how his wife was, replied, “Compared to whom?” In medicine field, the question might be, for example, how effective is BCG (an immunotherapy) as a cancer treatment? Compared to what? The Placebo, Chemotherapy, or any other immunotherapy? At what amount of dose, and for what kind and type of cancer? Phase III clinical trials are designed to answer questions like these.
   2. A phase III trial or comparative clinical trial is a planned experiment on human subjects involving two or more treatments in which the primary purpose is to determine the relative merits of the treatments. It is undertaken after the treatment has successfully passed a phase II trial. Comparative clinical trials have elicited great interest and discussion ever since they were introduced in the 1930s by A.B. Hill. Very often they are referred to as the clinical trials. The objectives of comparative clinical trial differ according to what one means by evaluating the relative effectiveness of the treatments. The primary objective may be the selection of the best treatment for future use in patients. It may to estimate the effectiveness of each treatment with some degree of precision. Or, the objective can be twofold, to select the best treatment and to estimate the treatment effect. If the primary aim is to select the best treatment, then some type of sequential plan will be appropriate in which the decision to continue the study at any stage is determined by the results accumulated to that stage. As soon as it is clear which treatment is best for patients, the study will be stopped, even though at that point it may be that, only rather non-accurate estimates of the effectiveness of each and every treatment can be deciphered. If there is a combined aim of selecting the best treatment and learning something about each, a sufficient number of patients should be entered on each treatment so that effectiveness can be estimated with a small amount of precision. Additional patients might be needed to satisfy the further selection requirement. It is implicit that for such a trial it should be ethically justifiable to continue even after sufficient data have been collected to permit a decision about the best treatment. For each particular trial, the objectives need careful consideration, and clinicians should be aware if the types of study implied by a different choice of objectives. It usually is desirable to consult a statistician concerning determination of sample size and stopping rules for the study.
   3. Phase III trials demand very careful planning. Loose plans and loose methods give loose results that may be misleading. In the following, some general guidelines are offered are offered for planning and designing phase III trials.

1. Consideration in Planning

No complete, or completely satisfactory, list of considerations can yet be given. The following are a few important points.

1.                                                               i.      Time for Planning.
   1. Several months to a year should be allowed for drawing up the rules and regulations, or the document specifying the objective of the trial and the plan for carrying it out. If the trial involves more than one institution, a longer planning time (a year or more) should be allowed.
   2.                                                             ii.      Number of Treatments Involved.
      1. The number of treatments involved in a phase III trial are closely related to the number of patients per year that can be expected to enter in a particular study. In order to guarantee enough number of the patients in each and every group’s treatment, a clinical trial should involve a small number of treatments for differentiating.
      2.                                                           iii.      Duration of the Trial.
         1. The estimated duration of a trial includes the period for entry of patients and the follow-up period for the observation of response and survival. George and Desu (1974) derive the necessary duration of a clinical trial based in the assumptions that patients enter the trial according to a Poisson process and the survival time (or time to failure) is distributed exponentially. No rules are available for general cases. However, if a clinical trial extends over a long period of time, it is likely that other treatments will appear as candidates for comparison. In practice, clinical trials extending longer than five years must be thoroughly justified.
         2.                                                           iv.      Comparability of Patients.
            1. The comparative clinical trial should be planned so that the only reasonable explanation for a difference between treatment groups is a result of the treatments. Patients must be comparable with respect to prognostic factors; otherwise, the results will very likely be misleading. A technique to achieve comparability of patients at the time of entry is formal randomisation. However, randomisation does not guarantee that patients in treatment groups will be comparable with respect to all prognostic factors. Although adjustments can often be made in analysis, comparability needs to be checked & assured before the analysis is done.

             

          

       

    

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1. Agricultural Statistics
   1. Crop Production Statistics
      1.                                                             v.      Currently, for most food crops and some of the cash crops, the estimation of yield rate is done with the help of crop-cutting experiments. The estimate is build up by actually harvesting, threshing and weighing the crop growing in small areas (called ‘cuts’) selected amongst the fields. A stratified multistage random sampling method is used for the preference, with tehsils (each containing 100 to 300 villages) as strata, a village as the primary unit, a field growing the particular crop as the secondary unit and a cut within the field as the ultimate sampling unit.
      2.                                                           vi.      For each crop, generally two to ten villages are chosen at random from each stratum; in each village, two fields growing the crop are selected; and in each field a cut of prescribed size is marked out for conducting the crop-cutting experiment. The size of the cut to be made varies from 1/500 th of a hectare (20m X 10m) in the case of cotton. But the commonest cut-size is (10m X 5m) of a hectare.
      3.                                                         vii.      The methods which used in Kerala, Orissa and West Bengal are slightly different. In West Bengal, for example, the area under a police station is taken as the stratum and the sampling unit is a square grid of area 2.25 acres. For the survey on area under crops, sampling grids are chosen at random from all the police stations at the rate of one per ½ square mile and all the plots falling wholly or partly in the grid are enumerated. For the yield survey, grids are randomly selected from each stratum and in each selected grid generally one cut is taken at random for each and every crop. The cut is  circular area composed of three concentric circles of radii 2’, 4’ and 5’7” for all crops excluding potato, arhar and sugarcane, in which case the cut is a square area of side 15’.
      4.                                                       viii.      In each stratum, a simple arithmetic mean of yield per cut is obtained. The yield from a mixed sown cut is divided by the corresponding eye-estimate of the proportion of area under the given crop; these figures for all such cuts and the yields of cuts sown solely with the given crop are added up to obtain the average of each strata. The district average is found by weighting each stratum average by the proportion of the net area sown in each of the strata. The State average in its turn, is obtained by weighting each district average by the proportion of the total net area that falls under the crop.
      5.                                                           ix.      For non-forecast and plantation crops, the available estimates are ad hoc estimates as distinct from those available for forecast crops. The estimates of area and production of tea, coffee and rubber used to be based on special returns received by the DES from the State Governments. However, in the absence of the necessary data from the State Governments, all-India figures of area and production of coffee and rubber, as available from the Coffee Board and the Rubber Board, respectively, are being used from 1965-66 and 1066-67, respectively. Data regarding tea also are being extracted from the information received from the Tea Board.
      6.                                                             x.      As regards minor crops, for State with a primary reporting agency estimates of area are made in the basis of complete enumeration, but for other States the area estimates are extremely unreliable. The available yield estimates are everywhere impressionistic and unreliable. Recently, sampling methods are being used for some of the crops, especially for those falling under fruits and vegetables and spices and condiments.
      7.                                                           xi.      The two most important DES publications in area and yield of crops are the following:
         1. Estimates of Area and Production of Principal Crops in India (annual). This gives estimates of area, production and average yield per hectare for the principal crops (both forecast and non-forecast) along with data on rainfall. The estimates of area and yield for the current year as also some previous years are given State-wise, except for coffee and rubber, for which only all-India estimates are available. The rainfall data are published for each of the 29 rainfall divisions of the country. As regards food grains, separate estimates of area and production of kharif and rabi food grains are available for all-India and the major States. The figures of rice are given separately for autumn rice and winter rice.
         2. Agricultural Situation in India (monthly). This gives the first as well as the subsequent forecasts of area and production of forecast crops. The revised estimates also appear in the publication. Similar, estimates for plantation crops are also given. (In addition, it contains data of agricultural prices, viz. Farm procurement prices, wholesale process and retail prices.)

Other publications on agriculture are:

1. Indian Agriculture in Brief (DES, annual). This gives a snapshot picture of whole agricultural economy. State-wise figures are given for some important items like land utilisation, area, production and yield rate and livestock population.
2. Bulletin in Food Statistics (DES, annual). This presents an integrated picture of the production, procurement, export and import, distribution, market arrivals and prices of food grains.
3. Tea Statistics (annual), published by the Tea Board. [Another annual publication named Tea Digest has been started by Tea Board since 1991.]
4. Coffee Statistics (annual), published by the Coffee Board.
5. Indian Rubber Statistics (annual) and Rubber Statistical News (monthly), both published by the Rubber Board.
6.                                                         xii.      One should mention here that a set of estimates of yield is prepared every year by the Agricultural Statistics Wing of the NSSO. These are based on yield rates estimated from a sub-sample of official crop cuts, whose yields are harvested, threshed and weighed under the supervision of the NSSO. For area, the official figures are utilised.
7.                                                       xiii.      The current system of estimation of area and yield of crops leaves scope for improvement in more than one respect:
   1. A uniform method of estimation should be followed in all the States. For yield forecast, alternative methods based on metrological factors and using a multiple regression model may be considered for adoption.
   2. Statistics of yields separately for irrigated areas and non-irrigated areas are still not available in most States. Area and yield data for improved agricultural practices (like use of pesticides, fertiliser and HYVs) are also not collected separately. This position calls for a change.
   3. The method of crop-cutting experiments for the estimation of yield rate has not yet been extended to commercial crops and minor crops in most States. This should be done to improve the quality of such data.
   4. A set of statistics that needs to be built up is that of land utilisation according to land use potentialities.
   5.                                                       xiv.      We shall briefly consider other types of agricultural statistics, viz. livestock statistics, fishery statistics and forestry statistics.

    

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1.  IV.            High-Order interactions occur rarely
   1. Introduction
      1.                                                               i.      An interaction of factors requires specific mechanisms. For example, suppose that the asthmatic subjects, of the illustration in the previous rule, had shown a pollutant effect during exercise but not during rest. This would require an explanation by a respiratory physiologist, who might argue that pollutants only have an effect when the subject is stressed; for example, during exercise, “Why would that be the case?” A deeper explanation might then mention the immune system and how it responds to pollutants.
      2.                                                             ii.      The more complicated an interaction, the more complicated the mechanism of the organism’s response. It is an empirical observation that such situations are relatively rare.
   2. Rule of Thumb
      1.                                                               i.      High-order interactions occur rarely, it is not necessary to design experiments that incorporate tests for high-order interactions.
   3. Illustration
      1.                                                               i.      Consider a study of decline in memory among blacks and whites (race), males and females (sex), ages 70 to 90 (age) and varying levels of schooling (education). There are four explanatory variables (race, sex, age and education). A full model would involve four-factor interactions. Note also that decline in memory itself is a change variable. If such an interaction were found in an observational study, the investigators would almost certainly explore selection biases and other reasons for this observation. If they were satisfied that the interaction was “real”, they would begin to explore mechanisms.
   4. Basis of the Rule
      1.                                                               i.      The basis for this rule is that it is difficult to picture mechanisms associated with high-order interactions, particularly in studies involving organisms. There is parsimony of mechanisms. Another consideration is that to a first order approximation, effects of factors are additive. Finally, interactions are always expressed in a scale of measurement and there is a statistical theorem that says that a transformation of the scale can be made so that effects become additive (Scheffe, 1959). In other words, some interactions are simply associated with the scale of measurement.
   5. Discussions and Extensions
      1.                                                               i.      The existence of an interaction implies that the effects are not additive. Relative risks and odds ratios essentially estimate two-factor interactions the risk of disease among the exposed compared with this risk among the non-exposed. On the log scale, of there is no interaction the log of the relative risk and the log of the odds ratio are exactly zero, so that relative risk and odds are 1.
      2.                                                             ii.      Fractional factorial designs allow the application of the two rules of thumb listed above (Rule III and Rule IV). They take advantage of factorial structure while using the higher-order interactions for estimating the error. A classic book discussing this and other issues has been updates recently; see Cox and Reid (2000). It is a part of scientific insight to know which interactions can be ignored and which should be considered in the design of a study.
      3.                                                           iii.      The assumption that high-order interactions do not occur, commonly underlies a great deal of research; it forms a frequently unstated context. It is perhaps common because it is often correct. However, it will certainly pay to itemize the more common high-order interactions assumed to be non-existent.

1.     V.            Balanced designs allow assessment of joint effects
   1. Introduction
      1.                                                               i.      Since designed studies are under the control of the investigator one choice is the allocation of resources to the treatment conditions. It turns out that “nice” things happen when the allocations are arranged in a specific way. A sufficient condition for a balanced design is that all treatment combinations are based on the same number of observations.
   2. Rule of thumb
      1.                                                               i.      Aim for balance in the design of a study.
   3. Illustration
      1.                                                               i.      In a factorial design aim for equal numbers of study units to each treatment combination. This makes the various types of analysis equivalent n statistical packages. For example, with balanced data the Type I and Type II analysis in SAS are identical.
   4. Basis of the Rule
      1.                                                               i.      This rule is based in the resulting analysis that are more straightforward and typically, allow additive portioning of the total sums of squares. Studies that are balanced are often called orthogonal because additive portioning of the sums of squares is equivalent to an orthogonal partition of treatment response in the outcome space.
   5. Discussion and Extensions
      1.                                                               i.      The concept of balance is fairly straightforward: equal allocation of samples to treatments. However, it need not be quite so restrictive. For example, in a 2 X 2 factorial design the total sum of squares can still be partitioned additively when the cell frequencies are proportional to the marginal frequencies. To determine whether this is the case, simply calculate the chi-square statistic for contingency tables on the cell frequencies. If the chi-square statistics is exactly zero, the cell frequencies are in proportion to the marginal frequencies. Given table illustrates such a design. In this design the cell frequencies are determined by the marginal frequencies: n_ij=n_i. X n_.j/n., for i= 1, 2 and j=1, 2.

1.                                                             ii.      As indicated, balanced studies provide for additive partitioning of the total sums of squares. Thus there is no need to worry about the sequence of hypotheses that are analysed. Historically there has been a great deal of emphasis on balanced experiments because the computations were much simpler. This, of course, is less of a problem now. However, there is an additional reason for striving for balanced studies: ease of interpretation. Designs such as balanced incomplete block designs & partially balanced incomplete block designs, were devised to be relatively easy to analyse and easy to interpret. Another nice feature of balanced allocation is that ordinarily the standard errors of the estimates will be minimised given that the total sampling effort is fixed.
2.                                                           iii.      For a one-way classification the numbers per treatment can be arbitrary in that it still allows an additive partitioning into treatment and error sums of squares. However, unless the frequencies are balanced, it will not be possible to subdivide the treatment sum of squares additively (of course, if there are only two treatments the further partitioning is not an issue and the sample sizes can be unequal).
3.                                                           iv.      Balance is important for additive partitioning of sources of variability. It is of less importance for precision, as Rule IX indicated (in upcoming article). If balance is required, the imbalance is not too great, and there are a reasonable number of observations per factor combination, it should be possible to randomly discard a few observations in order to obtain balance. Is this is done several times (akin to bootstrapping) the average of the results can be taken as a good summary of the analysis.

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1. Phase I and II Trials
   1. No optimal design for phase I trials can be recommended. The knowledge and intuition of the investigator is very important as in the choice of patients and in close observations. Very sick patients should not be selected for phase I studies since they have very low tolerance to toxicity and are likely to show it at very low doses, thus giving misleading results. However, this may not always be the situation. In many cancer clinical trials, patients who are no longer amenable to other treatments are recruited for phase I studies. Patient’s age should also be considered. Studies have shown that patients less than 18 years may tolerate higher doses of a drug than those older than 18 years. In cancer patients, younger (< 50 years) patient’s tumour may be more sensitive to chemotherapy than older (≥ 50 years) patient’s. Intervals between prior drug therapy and the administration of the phase I drug should be long enough to allow the toxic effect of the prior therapy to disappear. Other considerations for patient selection include concomitant medications and life expectancy long enough to complete the phase I study. The effect of concomitant drugs is often difficult to evaluate. Therefore, if possible, phase I patients should not be on medications other than the one being studied.
   2. The schedule and route of administration are determined on the basis of the type of drugs, mechanism of drug’s activity, patient convenience and preclinical animal pharmacokinetic information. A measure of response or effectiveness has to be determined, for example, a decrease of tumour cells to one-half the starting volume. In addition, changes in other relevant characteristics of patients should be used in determining the effectiveness of treatment. In a two-stage procedure, if no effect is noted in phase I, a phase IIA trial could be under-planning. After a treatment is found to be effective in phase IIA, a phase IIB trial should be conducted. If the treatment is found to be ineffective again in phase IIB, it would be considered unworthy of further study.
   3. The objective of a phase IIA or preliminary trial is to decide if a particular therapeutic regimen is effective enough to warrant further study. The decision to be reached at the end of the preliminary trial is one of the two possibilities:
      1.                                                               i.      The treatment is unlikely to be effective in x percent of patients or more.
      2.                                                             ii.      The treatment could be effective in x percent of patients or more.
   4. One would like to reject an ineffective treatment as quickly as possible and investigate further those treatments with a higher likelihood of effectiveness. The preliminary trial is designed so that a minimum possible number of consecutive failures is observed before the study is terminated. Suppose that the relevant percentage of effectiveness is 30 (x=30). Then the possible decisions for a preliminary trial are:
      1.                                                               i.      The treatment is unlikely to be effective in 30% of patients or more.
      2.                                                             ii.      The treatment could be effective in 30% of patients or more.

1. Thus if the treatment were at least 30% effective, there would be more than a 95% (1-0.0404) chance that one or more successes would be obtained in nine consecutive patients. If nine consecutive failures are observed, the treatment is unlikely to be effective in 30% of patients. Following this logic, Gehan (1961) gives the minimum number of patients necessary to decide whether a treatment is not of a given effectiveness or not worthy of further trial at a given level of rejection error (rejection error is defined as the chance of rejecting the treatment for further trial when it should have been accepted). The table below gives the sample size required for a preliminary trial of a new treatment for various levels of therapeutic effectiveness (percent) and two rejection error levels. For example, if one is interested in a treatment of 25% effectiveness and is willing to accept 5% rejection error, a sample of 11 patients is necessary. If one or more patients show response (effect of treatment), the treatment receives further trial.

1. The definition of therapeutic effectiveness requires careful assessment. In diseases for which previous procedures or therapies have been completely ineffective, the definition may pose no serious difficulties, and any objective benefit to the patient can be considered as a therapeutic effect. But if partial benefits are frequently observed, it is reasonable to require pronounced objective improvement in the patient’s disease. The preliminary trial will eliminate regimens having little or no effectiveness.
2. When a regimen has passed a Phase II preliminary trial or has been sufficiently effective in a phase I trial, then a phase IIB or follow-up trial is recommended in order to provide a precise estimate of its effectiveness. An estimate of true effectiveness is the proportion of patients in the sample who are treated successfully. For example, if a sample of 11 patients had been taken in a preliminary trial (with a 10% rejection error) in search of a 20% positive effect of treatment, and one treatment success was observed, then 60 additional patients would be required to guarantee an estimate of the true percentage effectiveness with a standard error of about 5%. If the required standard error was about 10% then 7 additional patients would be needed.
3. The sampling plan described above for the preliminary and follow-up trials is a two-stage procedure known as double sampling (Cox 1958). The initial sample is calculated to meet the probability of further trial. It requires at least a single treatment success before the second sample is taken. A complete phase II trial requires completion of both IIA and IIB if this sampling method is used, not just IIA. Although response rate is often used as the criterion for treatment success, it is not the only desirable statistic that can be obtained from phase II trials. Many phase II trials also estimate remission duration and survival time when applicable.

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Factorial designs should be used to assess the joint effects of variables

Introduction

i.      There is an old scientific “rule of thumb” recommending investigation of one factor at a time. Consider the following quote from Byte magazine (Halfhill, 1995) which summarises that view as well as any:

…. In any scientific investigation, the goal is to control all variables except the one you are testing. If you compare two microprocessors that implement the same general architecture on the same process technology and both chips are running the same benchmark program at the same clock speed, any difference in performance must be due to the relative efficiencies of their microarchitectures.

ii.      The problem with this prescription is that is most studies there are many factors that are of interest, not just one factor. The challenge is then to develop a design that allows assessment of all of the factors with minimal additional cost.

Rule of Thumb

i.      The effects of two or more factors can be assessed simultaneously by means of factorial designs in which treatment combinations are applied to the observational units. A benefit of such a design is that there may be decreased cost.

Illustration

i.      Suppose that a comparative study has been designed to study the response of asthmatic subjects to two factors: pollutant exposures (ozone and air) and two exercise levels (active and rest). Assume that it has been decided to test n subjects at each level of the two factors. Following the advice given in the introduction, the design involves two separate studies: one study to look at the effect of pollutant and the other study to look at the effect of exercise. This would take 4n subjects.an alternative approach is the factorial design which assigns n/2 subjects to each of the four treatment combinations. The design requires only 2n subjects as compared with the 4n subjects in the two, separate, single factor studies. Comparison of the means in the bottom row of the table reflects the effect of pollutant; a similar comparison of the column margin reflects the effect of exercise. Hence, this experiment contains the same information as the two independent experiments. In addition a comparison of the means within the table, the cell means, allows examinations of the question whether the effect of pollutant is the same during exercise and during test.

Basis of the Rule

i.      The variance of the differences (comparing active and rest, or comparing ozone and air) is based on the same number of subjects as the single factor study. The precision is virtually the same as that for the two independent studies; but with half the number of subjects.

Discussions and Extensions

i.      It is appropriate to contrast the above quote with another one by Fisher (1935):

No aphorism is more frequently repeated in connection with field trials, then that we must ask Nature few questions or, ideally, one question at a time. The writer is convinced that this view is wholly mistaken. Nature, he suggests, will best respond to a logical and carefully thought out questionnaire; indeed if we ask her a single question, she will often refuse to answer until some other topic has been discussed.

ii.      What did Fisher mean? Essentially that researchers are often interested in relationships between factors, or interactions. For example, it could be that the effect of ozone exposure can only be seen when exercising—a two-factor interaction. Comparison of the means in the margins, as indicated, reflect the effects of the factors separately. These are called the main effects. Thus, the factorial design provides not only the information of the two separate studies but also the potentially more important information about the relationship between the two factors.

iii.      It is useful to consider the error terms for the single factor study with n subjects per treatment, and the factorial design. In the single factor study the error term has 2n-2 degrees of freedom since each treatment has n subjects with n-1 degrees of freedom per treatment level. In the factorial experiment each cell contributes n/2-1 degrees of freedom to the error term for a total of 2n-4 degrees of freedom. So two degrees have been lost. Where did they go? One of them went to the comparison of the other factor, and the other is used in estimating the interaction.

iv.      Given this rule, why are not all studies factorial? If there are many factors at many levels, it will not be possible to carry out the full factorial analysis. For example, if there were four factors, each of three levels, then 3⁴=81 observation units are needed for only one run of study. (But see the following rule of thumb for a possible solution). Note also that the precision of the estimate of interaction effect must be large in order to be able to detect it in a factorial design.

v.      The three strategies of randomisation, blocking and factorial design are the basic elements of experimental designs. Their creative and judicious use will lead to efficient, robust and elegant investigations.

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1.        I.            Agricultural Statistics
   1. Land utilisation statistics
      1.                                                           iv.      Even for those areas of the country which are covered either by complete enumeration or by sample surveys, plots which are under mixed crops give rise to difficulties in deciding the cropping pattern. In some States, the total cropped area is apportioned among the constituent crops, at the field level, by the village officials through eye estimation. In some others, the entire area is recorded at the field level while the apportioning among constituent crops is done at the district level by means of fixed ratios that are supposed to represent average crop conditions. Recently, attempts are being made to have a uniform, satisfactory method for all the States.
      2.                                                             v.      Area sown with a crop is taken to mean the area actually sown, no matter whether the crop reaches its maturity or not, except in cases where the land is devoted, following the failure of the first crop, to a new crop. In the latter cases, the area is shown under the new crop.
      3.                                                           vi.      Each State publishes its own land use statistics. But the DES compiles the all-India figures and publishes them in the two-volume Indian Agricultural Statistics (annual). Vol. I and Vol. II which give the State-wise and district-wise data, respectively. All-India summary tables are given in both the volumes. Vo. II, in addition, gives an introductory note concerning the salient features of the rainfall, land use, irrigation and cropping pattern of the year.
      4.                                                         vii.      It should be mentioned that statistics of area irrigated area collected as part of land use statistics. This area is classified both according to source of irrigation (canals-Government and private-tanks, wells and other sources) and according to crop irrigated. In case two crops are irrigated from the same source on the same source on the same island in the same year, the irrigated area classified by source represents the net irrigated area, while the area irrigated classified by crop represents the gross irrigated area.
      5.                                                       viii.      The break-up of total cropped area according to different crops as shown in this publication is quite detailed. Separate figures are published in respect of the following groups and sub-groups:
         1. Food crops
            1. Food grains (cereals and pulses)
            2. Sugarcane
            3. Condiments and spices
            4. Fruits and vegetables, and
            5. Other food crops
         2. Non-food crops
            1. Oilseeds
            2. Fibres
            3. Dyes and tanning material
            4. Drugs, narcotics and plantation crops
            5. Fodder crops
            6. Green manure crops
            7. Guar and oats, and
            8. Other non-food crops
      6.                                                           ix.      There is considerable time lag between the collection of data and their publication in the Indian Agricultural Statistics (about 3 years for Vol. I and about 6 years for Vol. II). Currently, however, the DES is issuing in mimeographed form State-wise provisional land use statistics with a time lag of about a year only.
   2. Crop production statistics
      1.                                                               i.      For the estimation of yield, the various crops are divided into two groups;
         1. Forecast crops and
         2. Non-forecast and plantation crops
      2.                                                             ii.      Forecast crops, numbering 38 and including food grains, oilseeds, fibres and crops like potato, sugar cane, tobacco, etc., are those for which all-India estimates of area and production are issued. The periodical estimated of area and production are initially prepared by the concerned State agencies but are compiled by the DES and issued on pre-assigned dates. For each of these crops, usually two to three estimates are issued; but for cotton there are five estimates and for castor seed only one. The first forecast is based on general impression and usually one month after the sowing of the crop. The second comes about two months later and includes the area of late sowings and is based on the general condition of the crop. The final forecast, however, attempts to provide firm estimates of the total area sown and the total production. These are revised about a year later and again about the total production. These are revised about a year later and again about two years later in the light of returns received from defaulting States.
      3.                                                           iii.      The procedure formerly used for the estimation of the yield of a crop was based on the formula

Total yield=area (in hectares) X (normal yield x condition factor)

                                                            Yield per hectare

1.                                                           iv.      Thus the traditional method of estimating the yield per hectare, called the annawari method* is based in the notions of the ‘normal yield’ and the ‘condition factor’. The ‘normal yield’ refers to a district and is defined as the average yield on average soil in an average year. The ‘condition factor’ refers to a village and is taken to reflect to what extent the village yield per hectare during the given year is likely to differ from the normal yield. The factor is expressed as so many annas per rupee, the rupee representing the normal yield. Because of the vagueness of the concept of ‘normal yield’ and also because the ‘condition factor’ is based in eye-appraisal by patwaris or chowkidars, the traditional method is now being abandoned.

*An anna was a coin valued at one-sixteenth of a rupee.

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