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ON-FARM ACRONOMIC TRIALS
IN FARMING SYSTEMS
RESEARCH AND EXTENSION
ON-FARM AGRONOMIC TRIALS
IN FARMING SYSTEMS
RESEARCH AND EXTENSION
PETER E. HILDEBRAND AND FEDERICO POEY
Lynne Rienner Publishers, Inc.
Boulder, Colorado
p i ill i i: i-i ibi., ii.:L k "' "'
Published in the United States of America by
Lynne Rienner Publishers, Inc.
948 North Street, Boulder, Colorado 80302
1985 by Lynne Rienner Publishers, Inc. All rights reserved
Library of Congress Cataloging in Publication Data
Hildebrand, Peter E.
On-farm agronomic trials in farming systems
research and extension.
Includes index.
1. Agriculture--Research--On-farm. 2. Field experi-
ments. 3. Agricultural innovations--Research.
4. Agricultural systems--Research. 5. Agricultural
extension work. 6. Appropriate technology--Research.
I. Poey, Federico, 1933- II. Title.
S540.053H55 1985 630'.72 84-27597
ISBN 0-931477-10-7 (lib. bdg.)
ISBN 0-931477-11-5 (pbk.)
Distributed outside of North and South America and Japan
by Frances Pinter (Publishers) Ltd, 25 Floral Street,
London WC2E 9DS England
Printed and bound in the United States of America
Contents
Analytical Techniques and Other Calculations viii
Preface ix
Collaborating Farmers xvi
I THE ROLE OF ON-FARM RESEARCH IN TECHNOLOGY
DEVELOPMENT 1
Description of Farming Systems Research and
Extension (FSR/E) 2
Purposes of On-Farm Research 5
Types of On-Farm Trials 6
Exploratory trials 6
Site-specific trials 6
Regional trials 7
Farmer-managed trials 7
II GENERAL CONSIDERATIONS RELATED TO ON-FARM TRIALS 9
On-Farm Research Practices 10
Researcher-farmer relations 10
Listening to and working with farmers 10
The nature of the relationship 11
On-farm experimental procedures 12
Location on the farm 12
Experimental designs 13
Field Data Management 14
Recording 14
Processing 15
Unusual values 15
Standardization of field data 16
Moisture and area 17
Maize shelling percentage 18
Missing plots 19
Missing plants 21
Analysis of covariance 22
III EXPLORATORY TRIALS
Superimposed Trials 30
The 2" Factorial Trial 32
Interpretation of results 36
Comments on reducing the size of the trial 37
The "Plus" Trial 37
The "Minus" Trial 41
IV SITE-SPECIFIC TRIALS 45
Basic Considerations 46
Plot size 46
Variety evaluation 46
Crop associations 47
Plant nutrition 48
Plant protection 49
Analysis of Results 49
V RESEARCHER-MANAGED REGIONAL TRIALS:
AGRONOMIC EVALUATION 57
Design and Methodology 58
Experimental designs 59
Number of replications 59
Number of treatments 59
Control treatments 60
Kinds of treatments 60
Selection of sites 62
Complexity 63
Replication over years 63
Combining Data over Sites 63
Combined analysis of variance 64
VI RESEARCHER-MANAGED REGIONAL TRIALS:
SOCIOECONOMIC EVALUATION 73
Choice of Evaluation Criteria 74
Labor input as an evaluation criterion 75
Cash as an evaluation criterion 78
Response Surfaces 79
What they are 79
Representative forms 79
Economic analysis 81
Methods of Obtaining Response Surfaces 85
Simple regression--visiographic 85
Simple regression--least squares 92
Analysis of Response Surfaces 95
Coefficient of determination 97
Variance, standard error,and confidence
intervals 98
Significance of the coefficients 99
Significance of the equation 100
Linear versus quadratic surface 102
A prior and a posteriori information 105
Multiple Regression--Visiographic 108
VII FARMER-MANAGED TRIALS 115
Design 116
Check plots 117
Number of sites 118
Analysis and Interpretation of Results 119
Farmers' evaluation 119
Passive evaluation 120
Active evaluation 121
Researchers' evaluation 125
Modified stability analysis 126
Distribution of confidence intervals 131
Response surfaces using modified
stability analysis 142
VIII INITIATING AND MANAGING FSR/E PROGRAMS 149
Getting an On-Farm Research Program Started 150
Planning and Managing On-Farm Research 151
Defining Research Regions 153
Evaluating On-Farm Research 154
Regional Interinstitutional Cooperation 156
Bibliography 159
About the Book and Authors 162
Analytical Techniques
and Other Calculations
Acceptability, index of 122
Coefficient of variation, CV 52
Confidence intervals, distribution of 131
Covariance, to standardize plant population 22
Data standardization for
moisture and area 17
missing plants 21
missing plots 19
maize shelling percentage 18
Factorial, 2n 32
Mean separation
difference between two means 40
Duncan's new multiple range test 43
Tukey's multiple range test 53
Modified stability analysis 126
response surfaces 142
Profit maximization 82
Regression
multiple-visiographic 108
economic analysis 111
simple-least squares 92
coefficient of determination, R 97
confidence band 100
confidence interval around means 98
linear 102, 128
linear versus quadratic, ANOVA 104
quadratic 92
significance of coefficients, "t" test 98
significance of equation, "F" test 100
standard error, s 98
variance, s2 98
simple-visiographic 85
Variance, analysis of
after standardization for missing plots 21
combined 64
randomized complete blocks 51
viii
Preface
The roots of the technological revolution in
agriculture of the past century can be traced in the
history of scientific discovery and the development of
university research and training programs. Dramatic
improvements in production per hectare and per farm,
however, are a comparatively recent phenomenon. The first
major breakthroughs occurred in the biological sciences
with the development of hybrid maize in the 1930's,
followed by the expanding use of complete fertilizers and
improved weed and pest control technology following World
War II. Scientific knowledge in the basic and applied
agricultural sciences continues to advance at an
accelerating rate and is the basis for confidence that
food and fiber production can keep pace with growing world
demand.
It is clear that not all farm households and family
members have benefited equally from technological
progress. Yields per hectare and per agricultural worker
vary greatly among the regions of the world, among
countries within regions, and among farms within each
country. As a result, average farm incomes and the
percentage of a nation's population engaged in agriculture
also vary greatly among countries and regions. While the
overall pattern of differences can be explained with
reference to natural soil fertility, rainfall, product
demand, availability of inputs,and educational levels,
these only partially explain the disappointing rate of
progress in improving the productivity and income level of
the smaller farms and those with relatively severe
resource limitations.
Examining the history of research and extension (R&E)
systems in the low- and middle-income countries of the
world reveals four distinct phases. The first phase,
which began prior to World War II, was marked by the
construction of a limited number of research stations,
either by public authorities or by international
corporations interested in improved technology for
commercial export crop production. Also, technical
training programs were started, often outside colleges and
universities. The focus of this first phase was on
scientific research and the exploration of new crop
production opportunities.
The second phase, dating from the postwar period, was
characterized by a focus on rapid industrial development
and by the rapid expansion of publicly supported community
development and extension education programs for farm
families and rural residents. The explicit assumption was
that a backlog of technology available for adoption
existed, so programs should focus on technology transfer
and the motivation of target groups to accept change.
When this technology transfer strategy did not give
the desired or expected adoption rates, a third phase was
initiated in the late 1950's, with renewed emphasis on
technology development and research institution building.
Research programs emphasized genetic improvement,
agronomic practices, and livestock management in an effort
to identify "packages of practices" appropriate for small
farms for which technology was not available. In this
phase, the international research centers came into
existence with their very strong, well-financed programs
of genetic improvement for major food crop species. At
the same time, cadres of scientists and agricultural
specialists from developing countries were trained,
leading to significant strengthening of their agro-biology
research systems.
This third phase of agricultural research and
extension system development is responsible for the marked
growth in food production which has taken place in the
past two decades. Total food production in developing
countries has been increasing more rapidly than in
industrialized countries because of increased yields per
hectare on some farms and because of a significant
expansion in land under cultivation. Still, with higher
population growth rates, the rate of increase in food
availability per capital in developing countries has been
less rapid than in developed countries. On the African
continent, where agricultural research systems are less
developed, per capital food availability has been
declining.
Throughout this period, evidence began to accumulate
that the supply of unused arable land was rapidly being
exhausted and that existing research and technology
transfer systems were still not meeting the needs of a
majority of farm families who could be characterized as
being on small-scale, limited-resource holdings. If
adequate food and fiber production targets are to be met
in the future, a new approach to applied research,
technology development, and dissemination has to be
implemented to generate the kinds of new technology
acceptable to these limited-resource farmers.
Research and extension programs are now entering a
fourth, client-participatory phase. The term "farming
systems" was applied in the 1970's to several different
activities that had common threads and similar purpose,
but used different methods to pursue their goals. The
common threads were:
1. A concern with small-scale, limited-resource
family farmers who were reaping a disproportionately small
share of the benefits of organized research, extension,and
other developmental activities.
2. Recognition that a firsthand and thorough
understanding of the farmers' situation is critical in
increasing their productivity and helping to improve their
welfare.
3. The use of scientists and technicians from more
than one discipline as a means of understanding the farm
as an entire system, rather than isolating components
within the system.
Farming systems research and extension (FSR/E) is an
approach to technology generation, evaluation, and
delivery. It is applied, farmer-oriented, agro-biological
research, supported by the socioeconomic sciences in a
team effort that includes extension responsibilities. The
principal product is technology. The primary clients are
farmers. Since FSR/E concerns technology generation,
evaluation, and delivery, there are more agrobiological
than socioeconomic scientists involved, and methodology
emphasizes on-farm biological research as an integrated
and critical portion of a sequence of activities.
In that context, this book addresses an important
problem in agricultural technology innovation, namely that
of technology development methodology. The problem is not
new; it had been recognized explicitly before the rise in
popularity of so-called farming systems research.
Traditionally, agricultural personnel have seldom
made the important distinction between science and
technology and between research and development.
Counterparts in industry, with their well-known R and D
designation, have long recognized the distinction. It is
time that agricultural personnel did, and this book takes
a step in that direction.
Technology is a synthesis, and technology development
is synthesizing. Technology combines knowledge and other
pieces of information into "something that works."
Technology can be embodied in a machine, in a chemical
product, in a seed, or in a cultural practice. Technology
can be biological (seed), mechanical (machine), chemical
(fertilizer), economic (policy), or intellectual
(practice). A technology, to be useful, must serve
without control over the other variables, and the wider
the range of environments in which it can serve, the more
valuable it is.
Agricultural technology is used in production
systems. Thus, it must be tested in production systems,
it must be adapted to production systems, and it must be
integrated into these systems. An agricultural experiment
station is not a production system. This simple truism
has given rise to such terms as "farming systems research"
and "on-farm research."
In the training of agricultural personnel, research
methodology has always heavily emphasized science and a
degree of control possible only in the laboratory or on
the experiment station. The value of this activity and of
science is not being challenged in this book. Most
breakthroughs in agriculture have come from science, and
the term "science-based" agriculture is an accurate one.
However, science and new knowledge is not enough.
The new knowledge must be worked into a technology that in
turn can be worked into a production system. Note the
time span between discovery of the principles of
hybridization and the use of hybrid maize in production.
Note also all that had to happen in this period.
This book faces the technology issue squarely. It
recognizes that farmers use technology, not science, even
though the technology is science-based. It recognizes
that most agricultural workers serving the technological
needs of farmers deal more with technology than with
science. It faces the need for an authentic methodology
of technology development, to be used by those working in
innovation without the luxury of laboratory and experiment
station control. Technologists need their own technology.
It is not enough to make do with the traditional research
methodology, even with improvisations and ad hoc
adaptations.
This book is an early step toward a methodology of
technology development. It will be unfortunate, indeed,
if it is the last word.
It is the on-farm biological research sequence that
is the focus of this volume; its objective is to provide a
practical guide to the design and analysis of on-farm
agronomic experiments or field trials. Although FSR/E
involves livestock components, as well as family and
household components, this volume concentrates on the
design and analysis of the agronomic components. The
subject matter is organized following a logical sequence
of the various types of on-farm trials: exploratory,
site-specific, regional, and farmer-managed.
The book developed from a workshop on the design and
analysis of on-farm trials in San Jose, Costa Rica,
September 5-16, 1982. A number of experienced
professionals participated in this workshop and an early
version of the book was drafted. Original optimistic
plans called for rapid editing of the draft and early
publication. Subsequent revisions by the authors, an
extensive search for empirical examples, and contributions
by a number of other people eventually resulted in the
present version.
Deciding what to include or add was a formidable
task. The book reflects experience gained in the Farming
Systems Support Project and has benefited from lessons
xiii
learned in training courses offered through the FSSP in
North and South America, the Caribbean, and Africa. In
its present form, the book does three things:
1) It presents the role and philosophy of on-farm research
in FSR/E activities and describes a logical sequence
for technology development.
2) It presents the most -used statistical procedures in
simple, easy-to-follow steps. This is a service for
technicians who are often isolated and would like to or
must analyze their own data.
3) It presents new ideas and methods for analyzing
agronomic data obtained without the effect of usual
experiment station controlled conditions.
In an undertaking of this magnitude, many people are
involved. Sponsors of the workshop were the Office of
International Cooperation and Development (OICD), United
States Department of Agriculture (USDA), who funded it;
the University of Florida (International Programs and the
Food and Resource Economics Department), who arranged it;
and the Interamerican Institute for Cooperation in
Agriculture (IICA), who hosted it. The facilities at IICA
and the hospitality of its staff were greatly appreciated
by the participants, who put forth an unusual effort
themselves trying to draft a book in one week. The
authors wish especially to acknowledge the efforts of the
participants in San Jose, and those among them who
reviewed the final draft and made useful suggestions.
Special recognition is made to the Instituto de
Ciencia y Tecnologia Agricolas (ICTA) of Guatemala for
permission to use their data and to Juan Manuel Herrera,
who, with the collaboration of former ICTA scientist Rene
Velasquez, searched for and adapted many of the examples.
Ramiro Ortiz, former Technical Director of ICTA, was
especially helpful in making many suggestions regarding
the statistical analyses and provided a great deal of help
in editing several versions. Recognition is also due to
CIMMYT, IRRI, and CATIE for the data furnished by them.
Finally, particular gratitude is expressed to Jeannette
Romero for her patience, understanding, and efficiency in
preparing many drafts and the final version of the
manuscript.
The workshop participants and their
affiliations in alphabetical order follow:
AGRIDEC, Guatemala
AGRIDEC, USA
CATIE, Costa Rica
Central Bank of Ceylon,
Sri Lanka
CONACYT, Ecuador
ICTA, Guatemala
IDRC(CIID), Colombia
IICA, Peru
IICA, Costa Rica
INTA, Argentina
Lynne Rienner Publishers, USA
North Carolina State
University, USA
OICD/USDA, USA
University of Florida, USA
Ramiro Ortiz
Federico Poey
Julio Henao M.
Raul Moreno
Luis Navarro
Anila Wijesinha
Franklin Arboleda
Juan M. Herrera
Nicolas Mateo
Antonio M. Pinchinat
Rufo Bazan
Victor Quiroga
Jorge Soria
Karel Vohnout
Quentin M. West
Guillermo Joandet
Lynne Rienner
Larry A. Nelson
Donald Ferguson
Peter E. Hildebrand
Robert K. Waugh
Others who reviewed a final draft and made useful
suggestions were Louise Fresco, Wageningen Agricultural
University, The Netherlands; Tom Stillwell, Michigan State
University; and Steve Kearl, Ken McDermott, Chris Andrew,
and others of the Farming Systems Support Project at the
University of Florida. We gratefully acknowledge their
contributions. The authors, of course, accept all
responsibility for any errors of omission or commission
that may still exist, as well as for the final content of
the book.
Peter E. Hildebrand
Federico Poey
Gainesville, Florida
October 1984
current
I
The Role of On-Farm Research
in Technology Development
The client-participatory approach to the
generation, evaluation, and dissemination of technology
developed in recent years involves a sequence of
activities in which the clients (in this case, usually
small-scale, limited-resource family farmers) are involved
in most of the steps. This sequential procedure, known as
Farming Systems Research and Extension (FSR/E), is
flexible and adaptable to different conditions encountered
in the field and in the institutions involved. It is
iterative in the sense that new information is used
immediately and is also fed back into the sequence to
improve earlier stages being repeated in another cycle.
Initial activities involve a characterization of the
farming systems in an area, through discussions with the
farmers themselves and through the tentative partitioning
of the systems into homogeneous groups, or recommendation
domains, which become the basis for making specific
technology recommendations. A major portion of the
biological research conducted in an area to help solve
problems encountered there is carried out on farms with
the participation of the farmers. Eventually the farmers
are asked to manage simple trials themselves in order to
assess the acceptability of the technology when it is
completely under their control.
DESCRIPTION OF FARMING SYSTEMS RESEARCH AND
EXTENSION (FSR/E)
Although FSR/E is flexible enough to adjust to the
agricultural and institutional conditions existent in
different countries and cultural settings, it will usually
involve a sequence of steps similar to the following
within a previously determined geographical or political
region.
1. Initial characterization and analysis of existing
farming systems through close consultation with
farmers
a. First estimation of problems and constraints
b. Tentative partitioning into homogeneous farming
systems,or recommendation domains
2. Planning and design of first-phase work
a. Biological research
b. Continuing agro-socioeconomic characterization
3. Selection, generation,and evaluation of technologies
a. Commodity and discipline research on experiment
stations and laboratories
b. Researcher-managed on-farm trials with farmer
participation
(i) Exploratory trials
(ii) Site-specific trials
(iii) Regional trials
c. Farmer-managed trials
(i) Individual evaluation of acceptability by the
farmers themselves
(ii) Refined partitioning of recommendation domains
by researchers
(iii) Initiation of technology transfer activities
4. Collection and analysis of data
a. Agro-technical data from on-farm and on-station
trials
b.. Economic records of farm enterprises from farmers
c. Additional agro-socio-cultural and political
information from farmers and other area
residents
5. Frequently programmed multidisciplinary
re-evaluation of research activities and
information to do the following:
a. Redefine partitioning of recommendation domains
b. Make recommendations of acceptable technology for
dissemination into specified recommendation
domains
c. Introduce feedback into the sequential process
d. Serve as a basis for planning future work
6. Promotion of acceptable technology throughout
appropriate recommendation domain(s)
In many ways, this sequence parallels what farmers have
always done. Farmers manage a complex set of biological
processes which transform the resources at their disposal
into useful products, either for home consumption or for
sale or trade. The choice of crop and livestock
enterprises and the methods and timing of cultivation,
husbandry, and harvesting are determined not only by
physical and biological constraints, but also by economic
and sociopolitical factors which make up the larger milieu
within which the farmers operate. Conceptually, there are
many sets of choices and outcomes which would have direct
consequences on the welfare of farm families.
Within this complex milieu, through a process of
trial and error and over a number of seasons or
generations, farmers move toward appropriate technologies
and allocations of resources, given their specific
objectives. While the choices available to each farmer
are different, those with similar sets of resources and
constraints tend to make similar choices as to crops,
livestock, and management practices. Those who have
responded in similar ways can be grouped together into
homogeneous farming systems. The current technology they
are using, which has evolved over a long period of time,
will be similar within these similar groups.
FSR/E brings scientific method and additional
expertise to bear on this process of problem
identification and technology generation. Teams of
scientists from different disciplines, working with
farmers, can speed up the process and make it more
efficient in responding to a rapidly changing world. The
on-farm trials (3b and 3c, above), represent a sequence
designed to assure the advantages and acceptability of new
technology by the collaborating farmers. Materials and
methods that move through this evaluation phase come from
experiment stations and other sources. Depending upon the
nature of the technology being evaluated, it is usually
possible to initiate on-farm activities with site-specific
or regional trials.
On-farm research is not a substitute for experiment
station research--it is a means of providing much wider
exposure to station results, both with respect to
environment and to potential users. It is also a means of
conveying to station researchers any problems that require
experiment station facilities for solution. That is,
on-farm research provides an opportunity for station
researchers to expose their results to a much wider range
of environmental conditions. On-farm research also
provides an opportunity for more and smoother interaction
between extension personnel and the research procedure.
In moving through the sequence from experiment
station results to extension and farm production, the
complexity of the trials (number of treatments and
replications) at each location diminishes as plot size and
number of locations increase. In this sequence, the
extent of farmer management of the trials increases, and
the need for researcher management decreases (making
possible the larger number of locations). Concomitantly,
the capability and need to control sources of variation
decreases, while the need and possibility of measuring the
sources of variation increases. As the above changes
occur, biological precision and discrimination among
variables decreases, while the ability to test
socioeconomic interactions under farmers' conditions
increases. All of the above changes increase the number
of farmers involved in formalized research and increase
the direct investment farmers make in that research.
Finally, as the number of farmers increases, the potential
interaction of extension with research is enhanced.
PURPOSES OF ON-FARM RESEARCH
On-farm research in this context can become a focal
point for developing a technological system to serve
farmers, opening up several new possibilities for
improving the effectiveness of research:
1. On-farm research can serve as a linkage for ongoing
research and extension and the improvement of both.
2. It can make component research more purposeful. It
serves as a basis for evaluating the output from
discipline and commodity research, because it can
function to integrate the results from that research.
3. It can serve as a basis for the orientation of
component, commodity, and discipline research and the
selection of priorities.
4. It can make research more comprehensible, and
therefore more attractive to decision makers.
5. It can furnish information and introduce checks and
balances (evaluations) that can improve research and
extension management.
6. It can be a hands-on experience to improve the
effectiveness and the image of research and extension
workers, typically viewed by farmers as inhabitants of
ivory towers who do not understand the reality of
farming.
7. It can add to biological research, making it more
effective by evaluating responses when the
non-experimental variables, including management, are
allowed to fluctuate within the farmers' normal
conditions of production. The conventional research
system gives an estimate of what would happen if
farmers were to control variables as the researcher
does. It does not, however, furnish an estimate of
results if farmers were to actually use the new
technology. Both estimates are important, but without
on-farm research, the latter is missing.
8. The entire sequence can be considered as a learning
process for researchers, extension personnel and
farmers. It helps to refine both technology and the
definition of the recommendation domain(s) for which
specific technology is appropriate.
TYPES OF ON-FARM TRIALS
Types and numbers of trials are planned for each
recommendation domain previously identified by an initial
characterization of a region. The nature of the problems,
the availability of personnel, and budget considerations
all influence this allocation. Except for exploratory
trials, which can be used at any time to learn about
unknown situations, the other on-farm trials are
sequential, with specific purposes at each stage.
Exploratory Trials
Exploratory trials are used when little is known
about an area or about possible effects in an area of a
specific type of technology. They can be considered as
complementary to, or part of, characterization and usually
precede site-specific or regional trials. These trials
normally provide more qualitative than quantitative
information about several factors. Frequently, two levels
of each factor are included and few replications are used.
The most common designs are the 2n factorial and plus or
minus trials. Exploratory trials can sometimes be
superimposed on farmers' fields without the necessity of
special preparation of the experimental area.
Site-Specific Trials
These are similar in design to on-station trials, but
usually fewer treatments are involved. Perhaps as many as
20 to 25 treatments can be included, although this is not
recommended unless a more complex type of design (e.g.,
lattice or Latin square) is used to keep the experimental
error at an acceptable level. Because of the requirement
for intensive researcher management, few of these trials
are normally conducted. The most common design is
randomized complete blocks with four replications.
Analysis of variance (ANOVA) can include site as a source
of variation, and combined analyses can be performed.
Regional Trials
Regional trials are amenable to agronomic and
agro-socioeconomic analysis. They are designed to expose
the best treatments from site-specific trials to a much
wider range of environments within a recommendation
domain. Perhaps six of the best treatments are included,
and five to ten sites can be utilized. A recommended
design is randomized complete blocks with two to four
replications per site. ANOVA, regression, or modified
stability analysis (see Chapter VII)-can be utilized.
Combined analysis with site as a source of variation can
be used in ANOVA.
Farmer-Managed Trials
These trials provide the opportunity for the farmers
themselves to manage and evaluate the one or two most
promising treatments from regional trials. Large plots
with no replications are used. The purpose is for the
farmers to be able to compare the treatments with their
own practices, so one plot with these practices can be
included in the design. In practice, this check plot
serves the researchers more than the farmers, because the
farmers will be able to evaluate results based on their
own fields. If researchers wish to measure results of the
farmers' own practices, they can also sample from the
farmers' fields. However, agronomic and economic records
of the farmers' practices must be kept to provide the
necessary information. It is desirable to have at least
30 farmers in these trials in a recommendation domain.
Larger numbers improve the precision of the conclusion,
but smaller numbers can still provide useful information.
The remainder of this book deals with considerations
related to on-farm trials; the different kinds of on-farm
trials are discussed in separate chapters. Stressed
throughout is the concept that each kind of trial is part
of a sequence through which technology passes as it is
being designed, evaluated, and disseminated. None of the
steps in this sequence is sufficient in and of itself, and
all, taken together, depend on other on-farm research not
covered in the book. Some of these are preliminary or
special surveys, farm production records, and other formal
and informal contacts with the farmers and other residents
in the area.
II
General Considerations
Related to On-Farm Trials
Management practices and field conditions on most
farms differ from those found on experiment stations.
These differences need to be considered in any strategy to
obtain meaningful experimental data from on-farm trials.
On-farm trials are not meant to try to simulate experiment
station conditions in farmers' fields. Rather, they are
designed to help detect differences under typical farmer
management practices and environmental conditions.
On-farm research is characterized by farmers'
participation on their own land. This participation
varies according to the nature of the experiments. In
exploratory and site-specific trials, it is limited to
providing the land and some or all of the inputs. At this
stage, farmer participation in information gathering and
decision making is secondary to that of the researcher who
controls the trials. In regional trials farmer
participation is greater, contributing heavily to the
interpretation of results and eventual recommendations.
Finally, farmer-managed trials are conducted by the
farmer, while the researcher becomes the collaborator.
Researcher-farmer relations, location of trials on
the farm, on-farm experimental designs, and field data
management, including recording, processing, and
standardization, are a few of the many facets that need to
be viewed from a proper perspective when doing research in
farmers' fields with their active participation.
ON-FARM RESEARCH PRACTICES
Researcher-Farmer Relations
When conducting research on farms, researchers are
intruding upon the farmers' land and taking their valuable
time. The research may be using other of the farmers'
scarce resources. Because of this, it is well for the
researchers to act always in the best interest of the
farmers, treating them as equals in the research process
and considering them as desirable, not just necessary,
components in the technology generation, evaluation,
and dissemination procedure. Farmers understand exper-
imentation and are willing to participate if they
feel they will possibly benefit from it, and if they
understand what is happening. It is of utmost importance
for researchers to explain fully why they are there, what
they would like to do, what is going to be required of the
farmers, and what the farmers can expect from the results.
It is most important to explain why it will be of value
and of interest to the farmers to be participants in the
undertaking.
Listening to and working with farmers
From the very first contact made with farmers in the
initial survey, or in looking for collaborators for
on-farm trials or enterprise records, it is extremely
important that the researchers begin by listening to and
working with the farmers. Farmers resent being told by
"government people" that they are doing things wrong, and
that the "outsiders" know how the farmers should do it
better. If the researchers convey this attitude to the
farmers from the beginning, the relationship will get off
to a slow start, if it gets started at all.
Care must be exercised by the researchers to
ascertain which of the household members are the decision
makers and to talk with those who are responsible for
specific crops. A wife may know little about her
husband's cotton crop; he may know little about her
cassava or peanut crop.
The nature of the relationship
Farmers should be aware from the beginning exactly
what to expect from the relationship. Above all, they
must be informed that the work is research, from which
both researcher and farmer will learn, and not a
demonstration designed to show how much better the
researchers can do what the farmers are already doing.
(In most cases, the farmers know how to do it better, but
they cannot afford to.) Farmers must be aware of who will
be expected to provide what, who will take what risks, who
will get what product. It is critical that farmers
understand the timing of the various activities and
whether it is to be at their initiative or at the
initiative of the researchers. For example, in a yellow
maize area, if some white varieties are to be used, the
farmers should know if they can expect some yellow maize
in return for the white maize they will not want, or if
they should just expect to lose that which was produced.
They should also agree to include white maize and
understand why it should be included. They must know who
should provide the fertilizer, if it is to be used, and
when it must be available; who is going to harvest, when
and how.
Farmers understand risk and are willing to (or are
forced to) accept it as a normal part of their production
environment. If an experiment is lost because of normal
environmental conditions, farmers will understand it and
will not be concerned about compensation (although they
would probably accept it if offered). In order to avoid
paternalism in the research process, it is better not to
consider compensation for these cases. If, on the other
hand, certain treatments are lost because they were poorly
thought-out or obviously not adapted to the production
environment of the farmers, the farmers can be expected to
think compensation is warranted unless they were well
advised beforehand of this eventuality. In this case,
payment in kind, of the quantity and quality that
otherwise would have been produced, is probably indicated.
It is better, of course to avoid the situation by having
well-thought-out, simple interventions and adequate farmer
involvement in the design of the trial.
Farmers must understand the importance of the trial
to the researchers. The risk of not completing on-farm
trials is higher than with experiment station trials,
because much depends on the cooperation of the farmers.
There are many examples of "lost" on-farm trials due to
decisions made by the farmers without consultation with
the researchers. An increase in the market price of the
product might cause a decision for an early harvest of
part or all of the trial. A new variety or crop that is
considered especially attractive might promote harvest by
farmers or their neighbors before the final data are
recorded. Under some circumstances, preliminary results
satisfy the curiosity of the farmers and they lose
interest before the trial is completed. When trials
involve more than one cycle of production, or when it is
necessary to evaluate a rotation of crops, the risk of not
completing an on-farm experiment increases.
Farmers who do not fully comprehend the nature of the
trial may enter into competition with researchers. For
example, a check treatment that is meant to simulate the
farmers' practices and is to be conducted by the farmers
may receive special care because the farmers know how to
do it better and want to prove this to the researchers.
On a small plot, they can afford to do it even if they
cannot do it on their own fields. Or, the farmers may not
understand fully that they are supposed to manage the plot
exactly the way they do their own fields, so they wait for
the visits of the researchers before they carry out
practices that they normally do earlier on their own land.
In either case, errors are created in measuring the
farmers' level of production.
Finally, periodic review of all aspects of the trial,
along with frequent conversations between the researchers
and the farmers concerning the progress being observed, is
critical to fruitful on-farm research.
On-Farm Experimental Procedures
Location on the farm
Homogeneous or uniform experimental areas are the
rule rather than the exception on experiment stations.
The opposite is true on farms. Nevertheless, researchers
can reduce experimental error by following a few common-
sense rules. For example, it is never wise to locate a
research area adjacent to a habitation unless that is the
environment in which the crop in the trial is going to be
planted normally. Likewise, paths, canals, large trees,
and other conditions which are not normally part of the
environment should be avoided. If the crop is usually
planted in these special environments, of course, it is
appropriate to locate the experimental area in them.
Experimental designs
Conducting field trials on farms does not mean that
scientific methods can be overlooked. The same basic
methods are used as for any other research. The
experimental design or arrangement depends on the results
of the preliminary reconnaissance of the region, the
variables to be measured or controlled, environmental
variability, and the specific objectives of the trial. It
should be stressed that a good design is essential for
trials conducted on farms, as it is often the key to
helping farmers retain their beliefs and confidence in the
research institution and in the researchers themselves.
Using specific designs simply because they were used
elsewhere in similar experiments is discouraged. Whether
or not to use blocks, how many replications to make, plot
size, and other design considerations will depend on the
particular problem in the particular location. The number
of controlled variables and the amount of data collected
should not be more than necessary for attaining trial
objectives. There is a natural tendency to record as much
information as possible, on the assumption that it might
help explain findings that may emerge upon completion of
the trials, or simply that it might be "interesting." But
experimental information, particularly at the farmer's
field level, is costly to obtain, and it is preferable to
limit data recording only to those data which are useful.
Another consideration in planning a field trial is to
specify who will conduct it. The degree of complexity
will depend largely on who will be in charge of
implementation. Implementation may be assigned to
personnel working on an experiment station, or to a
multidisciplinary field team that planned the trials, or
perhaps to technical assistants trained for this purpose.
Extension agents or farmers may also be involved in the
management of the trials. Farmers' participation, in
particular, should be carefully defined in order to make
their contribution as effective and valid as possible. It
should be remembered that they also participate in
reaching conclusions and recommendations from the trials.
The most common experimental design used in on-farm
research is probably randomized complete blocks, usually
with four replications. Split-plot arrangements are not
encouraged, but may be necessary when ecological
conditions or the nature of the variables prevent a
complete randomization of plots, as, for example, when
comparing fertilizer levels with and without irrigation.
The fertilizer levels are randomized within larger blocks
that are either irrigated or rainfed. Another example
would be to minimize cultivar border effects by
randomizing plant populations within larger blocks that
are cultivars.
FIELD DATA MANAGEMENT
Recording
By its very nature, the information recorded in
on-farm trials must be less than in trials conducted on
experiment stations. The minimum necessary information
should be taken. Since experiments on farmers' fields
cannot receive the same day-to-day attention as station
experiments, it is advisable to increase the number of
locations rather than become involved in data collection
with too much detail in fewer locations. Those in charge
of on-farm trials must make every possible effort to
reduce to a minimum the time between completion of
recording data and the issuing of recommendations. Never
forget that farmers develop high expectations when
something is done on their farms, and their curiosity must
be satisfied as quickly as possible if their support and
assistance are to continue.
It is important to decide how records are going to be
managed before experiments are conducted. Developing
standard procedures of data recording helps speed
processing and analysis, and contributes in turn to faster
conclusions and earlier recommendations. It also makes
information more reliable and easier to file and retrieve.
The availability or absence of electronic data-processing
facilities should be a prime consideration in planning
recording techniques.
Recording sheets should meet the following require-
ments:
a. Field data should be usable directly for
processing; eliminating transcriptions saves
time, cuts the costs of trials,and eliminates
one source of error.
b. There should always be at least one
original and one copy of records.
c. Records should be easy to read; this
implies not too many records per sheet.
d. Sheet size should be such that it can easily
be handled in the field, as well as filed in
standard files.
Processing
Before data are analyzed, they must be inspected for
irregularities, processed,and standardized.
Unusual values
Before any data analysis is attempted, the patterns
of variation in the data should be studied. Attention
should be given to numbers which appear to be unusual
(called outliers), and those which are missing (called
missing plots). An attempt should also be made to see if
the variation is homogeneous throughout the data set. The
range is a useful device for this. An example of the use
of the range, to look for non-homogeneity of variation, is
illustrated with field data from a trial with six
treatments and three replications:
BLOCK I BLOCK II BLOCK III
Treatment 1 40 60 80
Treatment 2 30 55 120
Treatment 3 20 70 92
Treatment 4 20 42 60
Treatment 5 40 58 80
Treatment 6 50 68 92
The range in yield for each of the treatments is obtained
by finding the difference between the highest and lowest
values in each treatment:
Treatment 1 80-40 = 40
Treatment 2 120-30 = 90
Treatment 3 92-20 = 72
Treatment 4 60-20 = 40
Treatment 5 80-40 = 40
Treatment 6 92-50 = 42
Treatments 2 and 3 have very large ranges, so the data
should be inspected further to find out why. Upon
inspection, the value 120 for Block III, Treatment 2 seems
too high, and the value 20 for Block I, Treatment 3 seems
too low. The researcher should look for specific physical
reasons why these numbers are unusual. Sometimes they can
be traced to copying or typographical errors or to some
unusual situation that occurred in a plot but did not
affect the other plots. If a specific reason not
associated with the experiment can be found, the numbers
may be replaced by new values obtained by checking
original field records, using missing plot formulas,
covariance, or other suitable methods.
Standardization of field data
The field information taken directly from the
experimental plots (raw data) can seldom be utilized as
such for statistical analyses. Depending on the type of
crop, time of harvest, part of the plant of interest, and
many other factors, it is usually necessary to make some
numerical transformations that will provide more reliable
interpretations of the data. A common correction is made
when comparing yields of maize varieties with different
rates of maturity; if grain moisture is not standardized
to a uniform content, the excess moisture in the grain of
late-maturing varieties will cause an upward bias for
those varieties if direct plot weights are interpreted.
Also, plot size needs to be transformed in order to
produce more meaningful values. For example, it is better
to interpret tons, or kg/ha, of grain at a constant
moisture, than to consider just kilograms or grams per
plot, with no reference to the moisture content or plot
size. The correction procedures for these and other
factors are illustrated with field data.
Moisture and area. Table II-1 describes yield and
moisture content at time of harvest and the converted
yield in kg/ha at 14% moisture. There were three blocks
containing plots of 50 m2 net area.
TABLE II-1.
Field data and standardized yield of wheat
from a phosphorus experiment in Guatemala.
Field kg/ha
Moisture at 14%
Block P. level kg/plot % moisture
01 0 3.08 20.5 569
01 40 3.68 21.0 676
02 0 6.52 22.0 1183
02 40 7.44 20.0 1384
03 0 6.25 19.8 1166
03 40 6.28 20.0 1168
Source: ICTA
Correction Factor for Area (CFA) to convert
kg/ha is calculated as follows when plot size
in square meters (m2):
weight to
is measured
CFA = 10,000 / net plot size
The Correction Factor for Moisture (CFM) to convert weight
to a constant moisture content is estimated as follows:
CFM = (100 % hvst. moist.) / (100 % constant moist.)
As an example, in Table II-1, for the first row the
calculations are:
CFA = 10,000 / 50
= 200
CFM = (100 20.5) / (100 14)
= 0.924
Then, for the first row, kg/ha at 14% moisture is
3.08 x 200 x 0.924 = 569
PRACTICAL FIELD ADVICE
The farmer estimates yield without correction
for moisture. If treatment differences are so
small that moisture adjustments must be made, the
farmer will not be able to detect them.
Maize shelling percentage. In maize, field weight is
normally reported as kilograms of ears per plot.
Converting these values to grain weight is necessary when
comparing varieties that differ in the ratio of
grain-to-cob weight.
PRACTICAL FIELD ADVICE
The farmer will often express this difference
by saying the variety "does not yield as much,"
meaning a net or basketful or other standard farm
measure of ear volume does not "yield" as much
grain.
The Correction Factor for Shelling (CFS) percentage
can be obtained from the grain and ear weight of a random
sample of ears, as follows:
CFS = kg of shelled grain / kg of ear corn
For example, if 20 ears weigh 4.1 kg and the shelled grain
weighs 3.3 kg, then
CFS = 3.3 / 4.1
= 0.805
This correction factor is then multiplied by the
total ear weight of each plot of the same variety.
Missing plots. Frequently in on-farm research,
animal intervention or other unusual occurrences can ruin
one or more plots in a trial. A decision must be made by
the researcher on how to adjust the trial to account for
these missing data. There are several ways to do this:
generate a value for the affected plot, drop the block or
replication from the analysis, or analyze all remaining
plots as if they were a fully randomized design with
unequal numbers of replications. Still another
alternative, if the plot is not completely destroyed, is
to harvest the parts of the plot that are undamaged and
proceed as for missing plants (see next section).
If fewer than four replications were used in the
original design, dropping an entire replication is a
fairly drastic measure, and other alternatives should be
considered. If only one or two plots were affected and
there were several treatments in the trial, then
generation of estimated values would be the best
alternative. If regression rather than analysis of
variance is to be used to analyze the data, then a missing
plot is less of a problem and may be omitted without
significantly affecting the analysis.
Standard statistical texts recommend a procedure not
too complicated for field use, if only one, or at most
two, plots are missing. For a randomized complete block
design a single missing plot value can be estimated by the
following equation:
Y = (bB + tT G) / (b 1)(t 1)
where b and t are the numbers of blocks and treatments,
respectively, B and T are totals of observed plot values
in the blocks) and treatments) containing the missing
information, and G is the grand total of all observed plot
values. The calculated or estimated value Y is entered
into the data where the plot was missing. Analysis of
variance is performed as usual, except that one degree of
freedom is subtracted from total degrees of freedom (and
therefore error degrees of freedom will also have one less
than if the plot value had not been missing). Treatment
sum of squares will have to be reduced by an amount equal
to:
[B Y(t 1)]2 / t(t 1)
where Y comes from the previous equation. An
follows:
Treat-
ments
D
E
F
III Ti
( ) 56
33 95
45 123
Bi 108 88 78 274
Y = [3(78) + 3(56)
= 32
- 274] / (3 1) (3 1)
The value 32 is used in block III for treatment D.
For the analysis of variance, ANOVA (described in detail
later in this chapter), total degrees of freedom (d.f.) is
(rt 1) 1 = 7 and error degrees of freedom will be
[(r 1)(t -1)] 1 = 3. Treatment sum of squares when
calculated is reduced by [78 32(3 1)]2 / 3(3 1) =
32.67. Then treatment mean square and the F value can be
calculated.
Sum of squares calculated
of missing plot value:
with the estimate
Source d.f. Sum of squares
Blocks(r-l) 2 98.67
Treatments(t-l) 2 228.67
Error 4 10.67
Total rt-1 8 338.00
Note: r = Number of replications or blocks
t = Number of treatments
d.f.= degrees of freedom
BLOCKS
II
26
27
35
example
ANOVA as adjusted:
Source d.f. Sum of squares Mean square
Blocks 2 98.67
Treatments 2 228.67-32.67= 196.00 98.00
Error 4-1 = 3 10.67 3.56
Total 8-1 = 7 305.34
Fc = 98.00 / 3.56
= 27.53
CV = 5.55%
Note: Fc = Calculated F value
= Mean square of treatment/error mean square.
The calculated F value, Fc, is larger than the 5% F value
found in a table for 2 and 3 degrees of freedom (9.55), so
there is a significant difference among treatments at the
5% level based on the adjusted ANOVA. Had the ANOVA been
performed with the non-adjusted figures it would have
indicated significance at the 1% level.
Missing plants. Other common corrections include an
adjustment for plant population when this factor is
affected by an outside influence that is not part of
natural environmental conditions. This is the case, for
example, when animals (or persons) interfere in an
experiment, removing or damaging plants. Since population
correction procedures tend to favor (increase) treatment
values, these should be made only when truly justified.
Judgement should be exercised in applying these correction
factors, because generally, in on-farm research, the
differences sought among treatments is much larger than
effects from usual plant population variability. This
judgement should take into consideration the variability
that can be attributed to normal environmental or local
conditions. For example, if germination is affected by
normal environmental conditions, correction for stand
should not be practiced. This is the case in some parts
of the highlands of Guatemala where maize is planted very
deep two months before the rainy season starts. If an
experimental variety does not have the ability to
withstand that condition, correcting for plant population
would be a mistake.
PRACTICAL FIELD ADVICE
A practical method of adjusting plot yield
values for missing plants is to harvest only those
plants that have full competition, then calculate
the appropriate area for that number of plants and
adjust for normal plot size. This can work for
crops such as maize or for many vegetables, where
individual plants are easily distinguished and
harvested and for which a specified number of
plants is expected in a full plot. For example,
if 25 plants should be in a plot and only 18 are
found with complete competition, then the yield
for these 18 can be increased by multiplying by a
factor of 25/18 to get the estimated yield for the
full plot, had it not been damaged by outside
causes. An alternative method for crops which are
not so easily separated into individual plants, or
for which plant numbers are not calculated for the
plot (such as wheat), is to locate small areas in
the plot which have not been damaged and harvest
them, leaving an unharvested boundary. Then the
total area harvested can be adjusted to the size
of the normal plot and yield adjusted accordingly.
In both of these cases, the implicit assumption is
that the parts of the plot harvested were
representative of the whole plot, a possible
source of increased experimental error. However,
this reduces the calculations which are necessary
for more sophisticated adjustments.
If correction needs to be made, by no means should a
direct relationship of the average weight of all remaining
plants be used as the estimate. Those plants,
individually, would have higher than normal production
because of a lack of nearby competitive plants.
Analysis of covariance. A more complete and accepted
method to standardize plant population is through the
analysis of covariance of plot weights and number of
plants reported. The following explanation and example
illustrate the use of this method.
The analysis of covariance is a statistical method
that allows valid treatment comparisons using observations
of one variable (yield), after the effect of a possible
disturbing variable (incomplete plant stands) has been
removed. The application of covariance must be justified
in the sense that the correction is being made because of
an uncontrolled environmental condition that does not
affect all the observations (plots) in the trial in a
homogeneously constant fashion. The example to be
presented in this section is a correction of yield in a
trial where animals ate plants in different plots, more in
some than in others. This exogeneous effect is not
related to the ability of the cultivars under evaluation
to withstand adverse environments. However, if grazing is
part of the environment in which the crop will be
produced, corrections should not be made.
The example presented is an evaluation of six new
maize hybrids in a randomized complete block design with
four replications.
Step 1. Table II-2 shows the of number of plants (X) and
kilograms per plot (Y) for each cultivar.
TABLE 11-2. Number of plants (X) and kilograms per
plot (Y) of six maize hybrids.
Treat- BLOC K S
ment I II III IV TOTAL
No. X Y X Y X Y X Y X Y
1 60 3.42 59 5.25 62 4.52 60 6.24 241 19.43
2 47 2.87 60 3.97 61 3.12 51 4.82 219 14.78
3 51 4.21 35 3.29 60 5.58 40 3.82 186 16.90
4 58 2.58 32 1.93 62 3.07 50 4.05 202 11.63
5 62 3.28 54 4.13 60 4.05 62 5.38 238 16.84
6 40 1.98 62 5.02 61 3.89 61 5.20 224 16.09
TOTALS 318 18.34 302 23.59 366 24.23 324 29.51 1310 95.67
Source: ICTA, Guatemala
Step 2. Perform an analysis of variance (ANOVA) for
number of plants (X) to get the sum of squares (Ex2)
values:
(CF) = Correction Factor
= (1310)2 / 24
= 71504.17
SST = Treatment sum of squares
= {[(241)2 + (219)2 +...+ (224)2] / 4} CF
= 561.33
= (Ex2)trts
SSB = Block sum of squares
= {[(318)2 + (302)2 +...+ (324)2] / 6} CF
= 372.50
= (Ex2)blocks
SStot = Total sum of squares
= [(60)2 + (47)2 +...+ (62)2 + (61)2] CF
= 1999.83
= (Ex2)total
SSE = Error sum of squares
= SStot (SST + SSB)
= 1999.83 (561.33 + 372.50)
= 1066
= (Zx2)error
Step 3. Perform the ANOVA for yield (Y) to get the Ey2
values:
CF = (95.67)2 / 24
= 381.36
{[(19.43)2 +...+
8.47
(Ey2)treatments
{[(18.34)2 +...+
10.44
(Zy2)blocks
(16.09)2] / 4} CF
(29.51)2] / 6} CF
SST =
SSB =
SStot = [(3.42)2 + (2.87)2 +...+ (5.38)2 + (5.20)2] CF
= 29.17
= (Ey2)total
SSE = 29.17 (8.47 + 10.44)
= 10.26
= (Ey2)error
Step 4. The third ANOVA is for the cross-product XY of
each corresponding cell of Step 1, to get the Zxy values:
CF = (1310 X 95.67) / 24
= 5221.99
(Exy)T = {[(241X19.43) +...+ (224X16.09)] / 4} CF
= 34.06
(Exy)B = {[(318 X 18.34)+...+(324 X 29.51)]
= 8.96
(Zxy) tot =
/ 6} CF
{[(60 X 3.42) + (47 X 2.87)+...
+(61 X 5.20)]} CF
= 110.80
(Zxy)error
= 110.80 (34.06+8.96)
= 67.78
Step 5. Perform the analysis of covariance.
Source of Deviations
variation from regression
d.f. Zx2 Exy Ey2 d.f. SS MS Fc
Total 23 1999.83 110.80 29.17
Blocks 3 372.50 8.96 10.44
Cultivars 5 561.33 34.06 8.47
Error 15 1066.00 67.78 10.26 14 5.95 0.43
Cultivars
+ error 20 1627.33 101.84 18.73 19 12.36
Adjusted means 5 6.41 1.28 2.98
Note: SS = sum of squares
MS = mean squares
The values of the SS of the deviations from regression for
error and cultivars + error are calculated as follows:
SSdy.x(error) = Zy2error
{[(Exy)error]2 / Zx2 error)
= 10.26 [(67.78)2 / 1066]
= 5.95
SSdy.x(cultivars+error) = 18.73
[(101.84)2 / 1627.33]
= 12.36
d.f. = (t-1) + [(t-l)(b-l)-l]
SSdy.x(adjusted means) = 12.36 5.95
= 6.41
d.f. = (t-l)
The MS values for these sources are estimated by dividing
each SS by its corresponding d.f.:
MSE = SSE / d.f.
= 5.95 / 14
= 0.43 and
MS adj.means = SS adj. means / d.f.
= 6.41 / 5
= 1.28
The F test for adjusted means is performed by dividing
MS adj. means / MS error :
Fc = 1.28 / 0.43
= 2.98
d.f. = 5.14
Step 6. Since there is significance at the 5% level when
testing the adjusted means, the covariance is necessary
and the mean values for cultivars should be adjusted. The
error regression coefficient, byx, is calculated as
follows:
byx = Zxy error / Xx2 error
= 67.78 / 1066
= 0.0636
Step 7. The adjusted mean treatment values are calculated
as follows:
Yi = Yi byx(Xi X)
As an example, for cultivar 1, the adjusted mean treatment
value is:
Y = Y byx(X X)
= (19.43 / 4) 0.0636[(241 / 4) (1310 / 24)]
= 4.8587 0.0636 (60.25 54.58)
= 4.4981
and for cultivar 2,
2 = Y2 byx(X2 X)
= 14.78 / 4 0.0636[(219 / 4) (1310 / 24)]
= 3.695 0.0636(54.75 54.58)
= 3.684
Step 8. Comparison of adjusted treatment (cultivar) means
is made individually for each pair of adjusted means since
the value of Sd is different for each comparison.
Comparison of cultivars 1 and 2:
Sd(l,2)2 = (MSE){(2 / b) + [(xl-x2)2 / x2error]}
= 0.43 {(2 / 4) + [(60.25 54.75)2 / 1066]}
= 0.2272
Sd(l,2) = (0.2272)1/2
= 0.4767
where b = number of blocks, and the calculated t value
comes from:
tc(l,2) = (Y1 Y2) / Sd(1,2)
= (4.4896 3.6844) / 0.4767
= 1.6891
and since tl4df,.05 = 2.145, then tc = 1.6891 N.S.,
so there is no significance at the .05 level, and
cultivars 1 and 2 are not significantly different.
Now, doing the comparison for cultivars 1 and 4:
Sd(1,4)2 = 0.43 [(2 / 4) + (60.25 50.5)2 / 1066]
= 0.2533
Sd(1,4) = (0.2533)1/2
= 0.5033
tc(l,4) = (4.4896 3.167) / 0.5073
= 2.628
and since tl4df,.05 = 2.145, then tc = 2.628,
and cultivar 1 is significantly different from cultivar 4.
The same procedure is followed for all possible
comparisons.
Ill
Exploratory Trials
Exploratory on-farm research is normally conducted at
the same time as initial characterization, and as a
complement to that process. It can also, however, be used
throughout the technology development process.
Exploratory trials are useful in at least two types of
situations: when research is initiated in a new region,
or when no previous information to estimate response to
potential new alternatives is available. In new areas,
more efficiency can be obtained if diagnostic activities
are complemented by exploratory trials. There are two
advantages: 1) periodic interaction with farmers provides
additional information to complement the diagnosis, and 2)
these trials produce valuable information for the design
of site-specific and regional trials. In later stages of
on-farm research, exploratory trials help redefine or
produce new research guidelines, as it is common for good
research to generate new questions.
Normally, exploratory trials provide qualitative
results that later can be quantified by other types of
experiments. Exploratory trials commonly include several
(usually three or four and occasionally up to seven or
eight) factors, using at least two levels for each factor,
with few replications. When available agronomic
information is scarce, the number of variables and
treatments may be high, and the design may be relatively
complicated. One way to keep down the number of variables
in these trials, and keep them small in size, is to design
two or more different experiments. By using only three or
four variables in each trial and choosing groups of
variables that interact frequently (e.g., fertilizer and
cultivars, weed control and plant density) the design is
further simplified. For the evaluation of potential
alternatives, such as introducing a new crop in the
region, the number of treatments can be reduced and the
design will be simplified. These trials are mostly
researcher-managed, though the farmers' previous
experience makes their input and opinions in the design of
treatments essential. A discussion of the types of
exploratory trial designs follows, along with examples for
each case.
SUPERIMPOSED TRIALS
A relatively simple, convenient, and efficient means
of exploring the effect of different factors in a new area
is a superimposed trial. In this type of trial,
TABLE III-1.
Example of a superimposed six-treatment
N-P-K trial in rice.
Grain yield
Treatment Farm Number
N P K 1 2 3 4 5 6 x
(metric ton x 100)
50- 0- 0 336 434 451 411 402 375 401.5
90- 0- 0 439 416 506 459 482 431 455.5
70- 0- 0 443 398 457 370 454 350 412.0
70-30- 0 412 419 412 398 499 386 421.0
70-30-30 416 368 482 370 397 402 405.8
70- 0-30 417 377 493 364 490 387 421.3
x 410.5 402.0 466.8 395.3 454.0 388.5 419.5
Source: Zandstra et al. (1981), p.107.
treatments are placed on fields which are being managed by
the farmers themselves. Treatments are marked by stakes
or other means, and individual treatments are installed
either by the researcher or the farmer. Together, the
researcher and the farmer harvest the crop when it is
mature. The design of a superimposed trial should be
simple. Replications should be used at each location,
although data from designs without replications at each
site can be combined for regional analysis and
interpretation.
An example of a simple superimposed trial from IRRI
is shown in Tables III-1 and III-2. Previous information
indicated that rice responded to at least 50 kg/ha of
nitrogen, but response to potassium and phosphorus was
uncertain. A simple six-treatment superimposed trial was
established on a number of farms and information was
obtained from six of them (Table III-1). The design at
each location was without replication. The six treatments
included three levels of nitrogen (50, 70, and 90 kg/ha).
At 70 kg/ha of N the treatments explored the application
of 30 kg/ha phosphorus and potassium individually and
together. Analysis of variance (Table III-2) indicated a
significant effect for nitrogen but none for the other
elements. The conclusion was that more nitrogen would
have a positive effect on yield, and if the cost were less
than the value of the additional crop, more nitrogen
could be recommended. Furthermore, it would indicate that
additional work should be done with nitrogen, but the
other major elements (P and K) need not be studied further
in this context.
TABLE III-2. Analysis of variance of a superimposed
N-P-K rice trial.
Source d.f. SS MS Fc
Total 35 69,071
Farms 5 32,178
Treatments 5 11,212 2,242
N 2 9,837 4,918 4.79
Remainder 3 1,375 458 0.45
Error 25 25,681 1,027
CV = 7.6%
Source: Zandstra et al. (1981), p. 107
THE 2n-FACTORIAL TRIAL
A useful arrangement of treatments that produces
exploratory information on several factors and their
interaction is a 2n-factorial trial. This is an
arrangement of n factors taken at two levels each. An
example of a 23-factorial experiment will be used to
illustrate the detailed methodology of analysis. The
nature of the trial was to explore three factors: plant
density, nitrogen, and variety in a 23 factorial. The
levels of the variables in this trial are given for plant
density (P), nitrogen (N), and variety (V) as follows:
PO = 25,000 plants/ha
P1 = 50,000 plants/ha
NO = None applied
N1 = 100 kg N/ha
V0 = Local variety
V1 = Tuxpeio
Table III-3 shows the field design by blocks and the grain
yield in kg/plot. To estimate the factorial effects and
perform the analysis of variance, the following procedure
is applied:
Step 1. Using treatment yield totals from Table III-3, a
two-way table can be constructed in which the treatments
are placed on the horizontal axis and the factorial
effects are listed vertically as shown in Table III-4. In
each of the factorial effects, half the treatment
combinations receive a plus (+) sign and half receive a
minus (-) sign. The row corresponding to M (mean of the
entire experiment) has only plus signs. When the higher
level of a factor (PI, N1, Vl) in the factorial effect is
present in the treatment combination, it receives a plus
(+) sign; it receives a minus (-) sign if not present (Po,
No, Vo). When two or more factors at higher levels are
present in the treatment combination, the sign is found by
using the algebraic rule for signs.
Example: pn (+) = p(-) x n (-)
pnv (-) = p (-) x nv (+)
TABLE 111-3.
Example of a 23 trial on maize with
plant density (P), nitrogen (N), and
variety (V).
Treatments Treat- Treat-
Code Block I Block II ment ment
totals means
kg/plot
P N V (1)* 4.3 3.9 8.2 4.1
o 0 0
P1 N V p 4.5 5.9 10.4 5.2
1 o o
P N V n 4.5 5.4 9.9 4.95
P N V, v 5.7 6.6 12.3 6.15
P1 Nl Vo pn 6.4 6.7 13.1 6.55
P1 N V1 pv 6.9 7.1 14.0 7.0
P N1 V1 nv 6.4 7.0 13.4 6.7
P1 Nl V1 pnv 8.6 8.8 17.4 8.7
Totals 47.3 51.4 98.7
Source: Adapted from CIMMYT data.
*(1) is the local or traditional
level combination.
treatment or the lowest
Table III-4 has the following characteristics: 1)
every row has an equal number of plus and minus signs,
except for row M; and 2) the sum of products of signs in
any given pair of rows is zero (Montgomery, 1976). For
another reference on the signs for these contrast
coefficients see Cochran and Cox (1957, p 157).
Step 2. The total factorial effects are calculated by the
algebraic addition of the yields of the same treatment
using the corresponding plus (+) or minus (-) sign of each
component, and the result is written in the space for the
total of each treatment (Table III-4).
Example:
Total factorial
p = (PI No Vo)
= -8.2 + 10.4
= 11.1
Total factorial
pn = 8.2 10.4
= 3.3
effect for (p):
- 9.9 12.3 +...+ 17.4
effect for (pn) is:
- 9.9 +...+ 17.4
Step 3. In the analysis of variance (Table III-5), since
there are 16 observations (eight treatments and two
replications), the square of the total of each factorial
effect is divided by 16 to obtain the sum of squares (SS)
for each treatment.
Example: SS for (p) = (11.1)2 / 16
= 7.7
The total sum of squares (SStot), the sum of squares
for blocks (SSB), and the sum of squares for the error
(SSE) are calculated in the usual form.
TABLE 111-4.
Calculation of the total factorial effect
in the 23 factorial with two
replications.
Treatment combination:
code and total yield (kg)
Factorial (1) p n v pn pv nv pnv total
effect 8.2 10.4 9.90 12.3 13.1 14.0 13.4 17.4 98.7
M + + + + + + + +
P + + + + 11.1
N + + + + 8.9
V + + + + 15.5
PN + + + + 3.3
PV + + + + 0.3
NV + + + + 0.1
PNV + + + + 1.3
Correction factor (CF) = (Grand total)2 / n
= (98.7)2 / 16
= 608.856
where n = number of observations
Total sum of squares (SStot):
SStot = E(each observation)2 CF
= [(4.3)2 + (4.5)2 +...+ (7.0)2 + (8.8)2] CF
= 639.45 608.856
= 30.594
Sum of squares for blocks:
SSB = [Z(each block)2 / t] CF
= {[(47.3)2 + (51.4)2] / 8} CF
= 609.906 608.856
= 1.05
where t = number of treatments
The sum of squares for treatments (SST) is calculated in a
different manner because the factorial effects have
already been calculated (Table III-4).
Sum of squares for treatments (7 treatment combinations):
SST = E(each factorial effect)2 / n
= [(11.1)2 + (8.9)2
+ (15.5)2 +...+ (0.1)2 + (1.3)2] / 16
= 28.46
and SSE = SStot (SST + SSB)
= 30.594 (28.46 + 1.05)
= 1.084
Step 4. In the analysis of variance for a 2" factorial,
one degree of freedom is always assigned to each factor or
interaction of factors because the factor effect is
calculated by comparing two levels of the factor or
interaction and one degree of freedom is lost in the
estimation.
Perform the analysis of variance (ANOVA):
TABLE III-5. ANOVA for the 23 factorial
Source of Degrees of Sum of Mean Fc
variation freedom Squares Squares
Blocks (b-l)=l 1.05 1.05 6.77 *
Treatments (t-l)=7 28.46 4.066 26.23 **
Factor P 1 7.77 7.77 50.129 **
N 1 4.95 4.95 31.935 **
V 1 15.016 15.016 96.88 **
PN 1 .681 .681 4.39 NS
PV 1 .0056 .0056 .036 NS
NV 1 .000625 .000625 .004 NS
PNV 1 .1056 .1056 .68 NS
Error 7 1.084 .155
Total 15 30.594
CV = 6.38%
* Significant at 5% level
** Significant at 1% level
Interpretation of Results
By examining the treatment mean yields in Table
III-3, and the analysis of variance, Table III-5, it can
be determined that each of the three factors individually
(plant density, nitrogen, and variety) had a highly
significant effect on yield. Out of the three factors,
the new variety (V) produced the greatest increase (2.05
kg/plot), and plant density (P) was second with a 1.1
kg/plot increase. Although nitrogen (N) had a significant
effect, increasing the yield by 21%, an economic analysis
should be conducted to determine whether its application
is an economically good choice. (Does the yield increase
cover the cost of buying and applying the nitrogen
fertilizer?) On the other hand, variety produces a
significant yield increase and its effect on cost is
minimal, making it a good alternative to introduce in the
production system in which the factors were evaluated. If
the plant density change does not require too much additional
labor at planting time, this may also be a good
alternative to introduce.
Comments on Reducing the Size of the Trial
Generally, many degrees of freedom in this type of
design (2n) are associated with higher-order interactions
which are difficult to interpret. If the higher-order
interactions (third order and higher) are not considered,
the size of the trial would be substantially reduced,
keeping some of the advantages of the basic factorial
arrangements. In this case, it is advantageous to use the
fractional factorial (Cochran and Cox, 1957). Example:
with n = 8, main effects and first-order interactions can
be estimated with only (1/8) x 28 = 32 treatments.
Equally, main effects and second-order interactions can be
estimated with only (1/4) x 28 = 64 treatments.
Another way to reduce the number of treatments in a
2n factorial is to select factors based on their
importance. Factors and combinations which are considered
of little interest from the biological and economic
viewpoint, or those which do not interact, can be
eliminated. For instance, if selecting two factors, A and
B, the following treatments can be established, with two
levels each: Al Bl, A2 Bl, Al B2, and A2 B2. If there is
no interaction between the two factors, determined from
previous experimental information, the main effect of A
corresponds to the average difference between A2 Bl and Al
Bl, and the effect of B to the average difference between
Al B2 and Al Bl.
THE "PLUS" TRIAL
Exploratory information on new variables as they
relate to existing practices can be obtained by testing,
one at a time, a series of alternatives that include the
new variables. The following example compares a
traditional maize practice with three alternatives. It
treatments with two replications.
Treatment
Traditional
T + density
T + nitrogen
T + variety
Description
25,000 plants/ha,
local variety.
50,000 plants/ha,
local variety.
25,000 plants/ha,
local variety
25,000 plants/ha,
Tuxpefo variety
no N applied,
no N applied,
100 kg/ha of N,
no N applied,
Results of this trial are shown in Table III-6.
TABLE III-6.
Maize yield data for a four-treatment
"plus" trial.
Treat-
ment x
Treatment Block I Block II totals
kg/plot
Traditional (T) 4.3 3.9 8.2 4.1
T + density 4.5 5.9 10.4 5.2
T + nitrogen 4.5 5.4 9.9 4.95
T + variety 5.7 6.6 12.3 6.15
Totals 19.0 21.8 40.8 5.1
Source: Adapted from CIMMYT data.
After calculating the sums of squares the ANOVA table is
shown in Table III-7.
consists of four
TABLE III-7. ANOVA for maize "plus" trial.
Source of d.f. SS MS Fc
variation
Blocks 1 0.98 0.98 3.3 NS
Treatments 3 4.27 1.423 4.8 NS
Error 3 0.89 0.2967
Total 7 6.14
C.V. = 10.68 %
CF = [(40.8)2] / 8
= 208.08
SSB = {[(19.0)2 + (21.8)2] / 4} CF
= 209.06 208.08
= 0.98
SST = {[(8.2)2 +...+ (12.3)2] / 2} CF
= 212.35 208.08
= 4.27
SStot = [(4.3)2 +...+ (6.6)2] CF
= 214.22 CF
= 6.14
SSE = SStot [SSB + SST]
= 6.14 (0.98 + 4.27)
= 0.89
The analysis of variance does not show significant
differences at the 5% level, although it is very close to
being significant at the 10% level. It seems unlikely
with such a low C.V. value that no significant difference
has been detected when there is a 50% increase in yield
when the new variety is used. This is the type of problem
encountered in performing ANOVA when the number of degrees
of freedom for the error is small, making the Fc values
high and difficult to surpass. One solution would have
been to increase the number of replications to five to
obtain more degrees of freedom for the error.
If a "t" test is performed for the two treatments
with the largest difference (e.g., traditional vs. T + new
variety), a procedure that is not statistically orthodox,
the following would result:
t = (xl x2 ) / Sx-x2
= (6.15 4.1) / 0.4924
= 4.1629
There are 2(r-l) = 2 degrees of freedom, where r = number
of replications or blocks. The calculated t values for 2
degrees of freedom are 2.920 for a 10% level of
significance and 4.303 for a 5% level. Hence, in this
case, the use of the new variety is not significant at the
5% level, but there is a strong indication that it does
make a difference in yield under these otherwise
traditional practices. Because the seed cost of maize is
a relatively small proportion of total production cost,
this may still be worth testing further.
The step by step procedure for calculating the above
t value is as follows:
S- = (2S-2/ r)1/2
x -x x
l-X2
= [2(0.2425) / 2]1/2
= 0.4924
and
2 2 2
S- = (S + S ) /
x 1 2
= (0.08 + 0.405) / 2
= 0.2425
and
S12 = EXl2 / (r-l)
= 0.08 / 1
= 0.08
Exl2 = EXl2 [(EXl)2 / r]
= [(4.3)2 + (3.9)2] [(8.2)2 / 2]
=[18.49 + 15.21] (67.24) / 2]
= 0.08
S22 = Zx22 / (r 1)
= 0.405 / 1
= 0.405
Ex22 = EX22 [(ZX2)2 / r]
= [(5.7)2 + (6.6)2] [(12.3)2 / 2]
= 0.405
THE "MINUS" TRIAL
This is the opposite of a "plus" trial. It compares
a technological package with alternatives that reduce the
package by one variable at a time. An example consisting
of three factors follows:
Treatment
Tech. pack. (TP)
TP variety
P nitrogen
TP plant density
Description
Tuxpefo variety; 100 kg/ha of N,
50,000 plants/ha
local variety; 100 kg/ha of N;
50,000 plants /ha
Tuxpefo variety; no nitrogen;
50,000 plants/ha
Tuxpefo variety; 100 kg/ha of N;
25,000 plants/ha
Results of the trial are shown in Table III-8.
TABLE 111-8.
Maize yield data for a four-treatment
"minus" trial.
Treatment Block I Block II Treat-
ment x
totals
kg/plot
Tech. pack. (TP) 8.6 8.8 17.4 8.70
TP variety 6.4 6.7 13.1 6.55
TP nitrogen 6.9 7.1 14.0 7.00
TP plant density 6.4 7.0 13.4 6.70
Totals 28.3 29.6 57.9 7.24
Source: Adapted from CIMMYT data.
After calculation of the sums of squares for each of the
sources of variation, the ANOVA table is as follows:
TABLE III-9. ANOVA of a maize "minus" trial.
Source of d.f. SS MS Fc
variation
Blocks 1 0.2113 0.2113 11.79 NS
Treatments 3 5.91375 1.9713 110.02 **
Error 3 0.0538 0.0179
Total 7 6.17875
C.V. = 1.85%
** Significant at 1% level.
CF = (GT)2 / n
= (57.9)2 / 8
= 419.05125
SSB = {[(28.3)2 + (29.6)2] / 4) CF
= 0.21125
SST = {[(17.4)2 +...+ (13.42)] / 2} CF
= 5.91375
SStot = [(8.6)2 +...+ (7.0)2] CF
= 6.17875
SSE = SStot (SSB + SST)
= 6.17875 (0.21125 + 5.91375)
= 0.05375
The highly significant effect among treatments
indicates that a mean separation test should be performed
to look for statistical differences. For this specific
case Duncan's New Multiple Range test (Little and Hills,
1978; Steel and Torrie, 1980) is used.
First start by computing least significant ranges
(Rp) by the following formula:
Rp = qaSR
where qa = significant "studentized" ranges taken from a
table (Steel and Torrie, 1980).
a = level of significance (.05)
p = number of treatment means involved in the
comparison
= 2,3,4
The values are summarized below:
P
2 3 4
q.05(p,3df) 4.50 4.50 4.50
and Rp is 0.426 0.426 0.426
NOTE: the values for qa in the table (see Steel and
Torrie, p. 586) are taken for
p = 2, 3, 4 and
d.f. = 3
The values for Rp were calculated by using the formula
previously shown, where
S3 = (S2 / r)1/2
= (MSE / r)1/2
= (.0179 / 2)1/2,
= 0.0946
Then, a summary for the test is shown by calculating the
mean separation. First the treatments are listed in order
of decreasing means.
Treatment kg/plot
R 8.7 a
tp
x 7.0 b
tp nitrogen
x 6.7 be
tp plant density
x 6.55 c
tp variety 6.55 c
Each Rp value is compared to the observed difference
between two means. Here it is important to take into
consideration the range of number of means involved.
For example, to compare xtp with xtpv calculate
8.7 6.55 = 2.15. This is compared to Rp = 4.26, which
would be in the column p = 4, because Xtp-variety is the
fourth mean in the range starting at Xtp. The mean
separation is shown above.
The results of this test show that the "tech pack"
treatment is significantly different from the other three
treatments (95% level of probability). This means that
the lack of any of the three factors that form the "tech
pack" will cause a significant reduction in the yield of
maize under the conditions of this trial.
IV
Site-Specific Trials
Experiment station trials are often designed to
search for "potential" or maximum effect of a technology.
Experimental cultivars, for example, are frequently
screened under conditions which do not limit their
expression of genetic potential. This potential, however,
is measured only for the one location -- the experiment
station. To obtain more useful information, two or more
farm locations can be used with the same type of
experimental design and analysis in order to measure
"deviations from potential" independently at different
locations. This type of trial is called a "site-specific"
trial.
Because they are usually complex, with a relatively
large number of treatments and replications, site-specific
trials are only conducted in a limited number of
locations. Information sought is agronomic and not
socioeconomic, so plots are small. Many possible sources
of variation, such as soil fertility, are frequently
controlled at the same levels found or used on the
station. Farmers' participation is minimal in these
researcher-managed trials.
BASIC CONSIDERATIONS
Results from site-specific trials should define a
limited range of alternatives to be evaluated regionally
before a technology can be passed on for farmer-managed
trials.
When designing site-specific trials it is important
to keep the recommendation domain concept in mind in order
to make the resulting data usable for regional
interpretation. For example, all site-specific trials in
one recommendation domain should have equal treatments,
replications, and plot size. This allows researchers to
combine data for regional interpretation (see next
chapter).
Plot Size
Plot size must be adequate to achieve trial
requirements. While requirements vary from trial to
trial, the size of experimental units must both fulfill
research requirements and be adapted to practical
circumstances. What is desirable must also be in balance
with what is possible; common sense must guide the team's
work.
It is important for the number of replications to be
the same with large or small plots. There is a tendency
to believe that larger experimental units make "better"
trials and therefore fewer replications are needed. This
is not true. Larger plots will increase the cost of
trials and they will also increase the probability of a
larger experimental error due to heterogeneity within the
blocks. In general, plot size will be limited by the
amount of land available for the trial on the farm and by
the amount of labor or inputs of other resources available
during the experiment.
Variety Evaluation
Testing improved genetic material is common for
research in farmers' fields. The following five
considerations are important in variety testing:
1) Control treatments should include the recommended
variety for the region as well as one or more local
materials used by farmers. Comparison of experimental
varieties against these standards helps to make more
meaningful recommendations. The on-farm researcher will
not be interested in identifying only the highest-yielding
cultivar, but will also be interested in other agronomic
characteristics of interest to the farmer.
2) The farmers' own agronomic practices should be
strongly respected. The main objective of on-farm
evaluation of new varieties is to know their real
potential under farmers' conditions. Therefore special
"experiment station" handling of these trials should be
avoided.
3) Experimental varieties selected for testing
should include all available alternatives with a
theoretical potential of excellence. This means that not
only the experimental varieties of the official research
sector should be tested along with local materials, but
also varieties from private research programs and from
national or international centers and seed companies
should be considered.
4) Randomized complete blocks is the experimental
design most often appropriate for these types of
experiments.
5) The experimental unit should be protected from
environmental bias coming from growth habitsof neighboring
varieties. In maize, for example, where varieties may
differ widely in plant size, extra rows of the same
variety at each side of the experimental unit should be
added. Those border rows are not harvested for
experimental purposes. A common practice in maize is to
plant four rows of each variety but only use the inside
two rows to constitute the experimental unit.
Crop Associations
A common practice among small farmers is to grow two
or more crops in the same area. Different crop
combinations, row spacing, management, and planting
sequences are common. When typical farmer practices are
to be included, a superimposed field trial may be
appropriate. On the other hand, when alternatives are
dramatically different from typical practices,
conventional field trials should be defined. A split-plot
arrangement can be appropriate when working with more than
one variable. For example, when one variable requires
different row arrangements, or if there is a large border
effect and the experimental unit size is large, it can be
assigned to the main plot. The other variables, such as
planting distance, varieties, or secondary crop
alternatives can then be assigned to the subplots.
Precision will be greater for the variables in the
subplots because more degrees of freedom are associated
with subplot than with main plot error. An economic
interpretation of these types of trials is mandatory since
the crops involved generally have different market values,
making yield relatively less important (see Chapter VII).
Plant Nutrition
Fertilizer trials are commonly conducted as
site-specific experiments. Information on soil
characteristics, previous management, and soil analysis
should be determined before locating the experiment.
Generally, at least three levels of each factor should be
considered in order to estimate a response curve.
Experimental designs should allow for measurement of
interaction effects which are common in fertilizer trials.
Factorial designs arranged in randomized complete blocks
(RCB) offer a better estimate of interactions among
factors than split-plot arrangements. The reason is that,
in analysis of variance for the RCB design, the error mean
square (MSE) is estimated with more degrees of freedom.
The split-plot design has the same number of degrees of
freedom for interactions as the RCB, but the residual
degrees of freedom have to be distributed between the main
plot error and the subplot error.
Special care must be used in field design to avoid
fertilizer runoff effects from adjoining plots. Border
rows or ample distance should be considered between
experimental units. When the local practice is not to use
fertilizer, the check plot should reflect that practice.
When farmers' practices include some fertilizer use, the
check plot should not be an absolute check, but should
reflect the common practice.
Plant Protection
Evaluation of pest (insect, weed, and disease)
problems is more difficult than the other agronomic trials
discussed. The main reason is that causal agents vary in
intensity and mode of action, not only from year to year,
but also within a small area. Therefore, pest protection
trials require large experimental units with many
replications, repeated for various cycles. A factorial
arrangement in randomized complete blocks or split-plot
designs is convenient. Superimposing the trial on a
farmer's field is also a logical option.
The probability distribution of pest damage does not
commonly assume a normal pattern. Sample data need to be
transformed in order to approximate a normal distribution,
which is a theoretical requisite for common statistical
methodology. The most frequent transformations for these
kinds of data are logarithmic [log X or log (X + 1) when
zero values are present]; square root [of X, (X + 1) or (X
+ 1/2)]; and the angular transformation ARCSINE (%)1/2 when
data are given in percentage values between zero and 20 or
80 and 100.
ANALYSIS OF RESULTS
The randomized complete block design is perhaps the
most common for site-specific trials. When repeated in
other locations, the results can be grouped for a combined
analysis, allowing a more meaningful interpretation of
site-specific trials.
The example selected to illustrate the statistical
methodology is a randomized complete block design that
comes from the Chimaltenango area in Guatemala. The
experiment is a maize variety trial that was established
following a recommendation from the previous year to
compare the farmers' own varieties of the region with
varieties bred and selected at the local experiment
station. It had been concluded in exploratory trials that
the station varieties interacted with environment in the
region, in many cases yielding less than the local
farmers' own seed selections. Therefore, good varieties
selected by the farmers and identified by the FSR/E team
were compared with the station varieties.
The farmers' varieties, most of them identified by
individual farmers' names, and four station varieties are
presented in Table IV-1.
TABLE IV-1.
Description of 15 flint cultivars included
in site-specific trials of maize in
Chimaltenango, Guatemala.
Varieties Color of endosperm Code
Los Pitos White 1
Garcia Yellow 2
Cojobal White 3
Ajquejay Yellow 4
Lopez Yellow 5
Unec Yellow 6
V-304' White 7
Argueta Yellow 8
Marrin Yellow 9
Santizo Yellow 10
Tsut White 11
Ordonez Yellow 12
Don Marshalll/ Yellow 13
Sintetico Chanin Yellow 14
Chanin-4/ Yellow 15
1/ Experiment Station Varieties
Source: ICTA, Guatemala
In Table
presented for
methodology for
IV-2, the standardized field values
treatments 1, 2, and 15 to illustrate
the analysis of variance.
TABLE IV-2.
Standardized field data (partial) for yield
of maize varieties in four replications in
Chimaltenango, Guatemala.
Cultivar B 1 o c k s Total X
I II III IV
metric ton/ha
1 4.20 5.04 4.90 5.10 19.24 4.81
2 5.20 5.54 5.30 5.80 21.84 5.46
15 2.98 3.00 10.36 2.59
Totals 56.97 72.18 265.20 4.42
The sums of squares for each source of variation and the
correction factor are calculated as follows:
CF
(Grand total)2 / n
(265.20)2 / 60
1172.184
SStot = [(4.2)2 + (5.04)2 +...+ (2.98)2 +...
+ (3.00)2] CF
= 1192.564 1172.184
= 20.380
{[(56.97)2
1173.293 -
1.109
+....+ (72.18)2] / 15} CF
1172.184
SST = {[(19.24)2 + (21.84)2 +...+ (10.36)2] / 4} CF
= 1180.434 1172.184
= 8.250
SSE = (SStot)
(SSB + SST)
= 20.380 (1.109 + 8.250)
= 11.021
SSB =
Then the degrees of freedom (d.f.) are estimated for each
source of variation, considering four replications (r =
4) and 15 treatments (t = 15). With this information,
calculate mean squares by dividing the sum of squares for
each source of variation by its corresponding degrees of
freedom:
MSB = SSB / (r-l)
= 1.109 / 3
= 0.3697
MST = SST / (t-l)
= 8.250 / 14
= 0.5893
MSE = SSE / [(r-l)(t-l)]
= 11.021 / 42
= 0.2624
Now calculate F values (Fc) by dividing the MS of the
sources of variation by the MS of the error.
Fc (blocks) = MSB / MSE
= 0.3697 / 0.2624
= 1.4089
Fc treatments = MST / MSE
= 0.5893 / 0.2624
= 2.2458
The coefficient of variation of the experiment is
calculated from the square root of the MSE, and the
general mean of all observations:
CV = [(MSE)1/2 / x](100)
= [(0.2624)1/2 / 4.42](100)
= 11.59 %
TABLE IV-3. Analysis of variance for yield of 15
maize varieties with four replications,
Chimaltenango, Guatemala.
Variation d.f. SS MS Fc F.05
Blocks 3 1.109 0.3697 1.4089 N.S. 2.83
Treatments 14 8.250 0.5893 2.2458 1.94
Error 42 11.021 0.2624
Total 59 20.3800
Source: ICTA, Guatemala
CV = 11.59% N.S.: Not significant
*: Significant at 5% level
The calculated F values (Fc) are compared with the F
values from a table to determine levels of significance.
For blocks there are 3 and 42 degrees of freedom, and for
treatments 14 and 42 degrees of freedom. The statistical
significance obtained for treatments indicates that yield
of at least one of the varieties differs from the rest.
In order to further define which varieties are
statistically different, a Tukey multiple range test for
comparison of means is performed (Steel and Torrie, 1980).
This method consists of computing a difference (D), which
would be significant at the 5% level, and comparing it
with the differences between each pair of treatment means
in the experiment. If a difference between two means is
equal to or greater than the value for D, then the two
means are significantly different.
The calculations are as follows:
D = Q Sx where:
Q = Value which is taken from a statistical table
(see Steel and Torrie, 1980, pp. 588-589),
and which is a function of number of treatments
and degrees of freedom of the error.
and Sx =
where r =
(MSE / r)l/2
(0.2624 / 4)1/2
0.256
number of replications
Then D = 5.11 x 0.256
= 1.31
The 15 varieties are then grouped in descending order of
yields, as shown in Table IV-4. Taking each treatment
mean, all possible comparisons are made starting from the
top and working down. From the largest mean value (5.52)
the value of D (1.31) is subtracted to find all mean
yields which are not different from the largest.
TABLE IV-4.
Mean yields of 15 varieties of maize
evaluated in four replications,
Chimaltenango, Guatemala.
CODE Variety ton/ha
3 Cojobal 5.52 a
2 Garcia 5.46 a
9 Marroquin 5.01 a b
5 Lopez 4.93 a b
4 Ajquejay 4.83 a b
1 Los Pitos 4.81 a b
6 UNEC 4.80 a b
7 V-304 4.72 a b
10 Santizo 4.57 a b
8 Argueta 4.55 a b
11 Tsut 4.54 a b
12 Ordofez 4.00 b c
13 Don Marshall 3.14 c d
14 Sintetico Chanin 2.92 c d
15 Chanin-4 2.59 d
Source: ICTA, Guatemala
CV = 11.59; Sx = 0.256; x = 4.42
The range is indicated by the letter "a" at the right.
The range for the next highest yield is from 5.46 to
(5.46 1.31) = 4.15, which includes the same cultivars.
The range for the third highest yield is from 5.01 to
(5.01 1.31) = 3.70, which includes all but the lowest
three indicated by the letter "b". The letters at the
right of the treatment means in Table IV-4 indicate the
four groups within which there is no significant
difference.
Table IV-5 presents the agronomic characteristics of
the varieties under evaluation.
TABLE IV-5. Agronomic characteristics of 15 varieties
evaluated in a site-specific trial in
Chimaltenango, Guatemala.
Variety Days to Plant Ear
Flower Height Height
(m) (m)
1. Los Pitos 129 2.85 1.60
2. Garcia 127 3.25 2.40
3. Cojobal 127 3.35 2.20
4. Ajquejay 126 3.10 2.15
5. Lopez 128 3.45 2.30
6. Unec 127 3.15 2.90
7. V-304 117 2.25 1.15
8. Argueta 124 2.55 1.25
9. Marroquin 120 3.40 2.25
10. Santizo 119 2.50 1.45
11. Tsut 128 3.55 2.40
12. Ordoiez 129 3.40 2.25
13. Don Marshall 107 2.00 1.00
14. Sintetico Chanin 102 2.20 1.15
15. Chanin-4 103 2.70 1.20
Source: ICTA, Guatemala
The analysis shows the highest-yielding group of varieties
among which there is no significant difference (varieties
3, 2, 9, 5, 4, 1, 6, 7, 10, 8, and 11), and two
(varieties 3 and 2) which are significantly different from
the four lower-yielding varieties (12, 13, 14, and 15).
The best varieties were the local materials and the
lowest-yielding were the experiment station varieties Don
Marshall, Sintetico Chanin, and Chanin-4. These last
varieties were selected for earliness and lower plant
height.
Farmer evaluation of the materials in this trial
indicated that shorter plants were not generally desired
because corn stalks are used for fences and walls.
However, the station varieties, although lower-yielding
and more than one meter shorter, proved to be nearly 30
days earlier than most local varieties. It was concluded
that these characteristics offer good potential for
alternative cropping systems (intercropping, relay
cropping, consecutive cropping).
V
Researcher-Managed Regional Trials:
Agronomic Evaluation
Regional trials are a set of similar trials conducted
in a region previously identified as a recommendation
domain. Their main objective is the evaluation of data
from on-farm and on-station trials to define the
interaction of technology with environmental conditions,
both from an agronomic and a socioeconomic viewpoint.
Verification of homogeneity within the previously
identified recommendation domain may result, or evidence
supporting the necessity to partition the recommendation
domain can be obtained. Recommendations for treatments
(technologies) to be submitted to farmer-managed trials
should result from analysis and interpretation of regional
trials.
In designing regional trials, the number of locations
should be as high as resources permit, with the regional
experiment station serving as one site. In a single
recommendation domain there should probably be no fewer
than five locations. Analyses can be made with fewer
locations, but precision will be questionable.
Farmers should participate in the management of the
trials with full knowledge of the variables studied and
the results expected. Throughout the experiment, farmers
should be in close contact with the person or persons
responsible for the trials. Farmers' active
participation adds resources and reduces the required
researcher input at each location; it therefore
facilitates the use of more locations.
If a sufficient number of locations have been used
for site-specific trials, and if they have designs and
treatments in common, they can be analyzed as regional
trials -- a cost-effective utilization of information.
Usually though, a trial will be designed especially for
regional analysis with fewer treatments than typical
site-specific trials but with a design common for all
sites. Variables included in regional trials, then, can
be the same as those that were included in site-specific
trials, a subset of them, or others based upon different
criteria.
The methodology of combining an analysis of variance
of data from all locations permits a measurement of the
interaction of technology with environment. It also
allows for a statistical interpretation of the relative
stability of each technology by a partitioning of the
total degrees of freedom due to treatments, and for
utilizing regression techniques involving environmental
indexes (see Chapter VII for a description of modified
stability analysis).
Farmers' participation in these trials contributes to
the researchers' focus on the farmers' reality, allowing
adjustments in experimental design and generating
conclusions that would not be possible from a strict
numerical interpretation of resulting trial data. For
example, farmers could readily reject the color or shape
of an experimental bean cultivar in a variety trial, or,
in the case of maize, point out the inadequacy of husk
coverage, or the impossibility of a suggested thinning
practice because of local religious beliefs.
DESIGN AND METHODOLOGY
Technologies to be evaluated in regional trials
usually are selected on the basis of results from
exploratory and site-specific trials conducted during the
previous year or years. Perhaps such trials were
concerned with individual components, such as variety,
fertilizer, or insecticide. In regional trials these may
be combined into a more comprehensive system. From all
previous trials in a region, a consensus is formed by a
multidisciplinary team as to what factors need to be
researched on a broader basis.
The general approach is to conduct a set of trials
having standard experimental and treatment design, plot
size, and number of replications throughout the region. A
brief description of some of the more important choices to
be made in designing these experiments follows.
Experimental Designs
A randomized complete block design is preferred,
because of its simplicity and precision. Split-plot or
Latin square designs are also possibilities, but they may
be unnecessarily complex. A separate randomization should
be carried out for each block of the trial at each site.
In other words, a standard randomization should not be
used for all sites.
Number of Replications
To provide an estimate of the experimental error from
each site, replicates within sites are necessary. Three
or four randomized blocks are recommended, although in
extremely limited land situations two blocks per site
could be used if compensated for by more sites. For
highly variable conditions (such as plant disease control
experiments), more than four replications may be required.
Number of Treatments
In order to keep the land area small and to limit the
complexity of the trials from a management point of view,
the number of treatments should be as small as possible
and not exceed 15 to 20. As an example, a complete 33
factorial N-P-K rate trial would require 27 treatments,
which would be too many. The number of treatments can be
reduced by such techniques as confounding to generate
incomplete factorials or using other appropriate treatment
designs (double square, central composite, etc.).
Control Treatments
Specific treatments to include in a set of trials
will depend upon the factors being studied and the
combinations of levels needed. Whenever possible,
regional trials should include the following treatments as
controls:
1) At each site the individual farmer's own
technology for the crop;
2) Technology representative or typical for the
crop in the recommendation domain; and
3) The currently recommended technology for the
recommendation domain.
The first control is to give each farmer a basis for
comparison and to provide researchers an estimate of
experimental bias. (Is yield within the experimental area
at each site greater or less than the farmer's yield?)
The second control compares the typical practice in the
region with the other treatments. This second control,
when used unchanged year afer year, serves also as a
benchmark to evaluate the year effect for trials conducted
dver time. A third control, representing the current
recommendation, is included to see how the new technology
being studied compares. The second and third controls
provide control conditions for all remaining treatments.
If the treatments are considered additive to present
practices, the second control provides these conditions.
If the treatments are considered as additive to
recommended practices, the third control provides these
conditions.
Kinds of Treatments
Analysis of the data should be anticipated when
choosing treatments. Care should be taken to assure that
necessary comparisons can be made readily and that
differences may be found if indeed they exist. For
quantitative variables, the total range and the spacing
between levels should be carefully chosen to assure that
the treatment range will provide the response desired and
that regression may be estimated with adequate precision.
Equal spacing of the levels, although recommended and
convenient from a statistical point of view, is not always
necessary.
Two multi-location examples are given to show what
types of treatments might be chosen in particular
situations and how these treatments might relate to one
another. The first example is a set of trials at ten
locations to evaluate five varieties (V1,...V5) each at
three nitrogen fertilizer rates (N1, N2, N3), as shown in
Table V-l. The major portion of these fifteen treatments
is a 5 x 3 factorial. In addition to these 15 treatment
combinations, three controls are included.
TABLE V-l. Treatment combinations
(5 X 3 factorial + 3 controls).
VINOCPc V4NOCPc
VINICPc V4NiCPc
VlN2CPc V4N2CPc
V2NOCPc V5NOCPc
V2NlCPc V5NICPc
V2N2CPc V5N2CPc
V3NOCPc VfNfCPf
V3NICPc VcNcCPc
V3N2CPc VrNrCPr
The controls represent:
1) each farmer's variety (Vf), nitrogen fertilizer rate
(Nf), and cultural practices (CPf);
2) the variety (Vc), nitrogen rate (Nc), and cultural
practices (CPc) typical of the area, or those
commonly used by most farmers; and
3) the variety (Vr), nitrogen rate (Nr), and practices
(CPr) currently being recommended for the region.
In this trial, the variety and fertilizer treatments are
considered additive to the common technology of the area
(CPc), so those practices which constitute that technology
are used in the major portion of the treatment set.
A second example illustrated in Fig. V-l represents a
fertilizer trial in which the intention is to measure the
response to nitrogen (N) and phosphorus (P) over a range
of rates, and to estimate a yield response surface within
this range. It is assumed that a good variety has already
been adopted by the farmers within the region, so this
factor will not need to be included within the trial. The
ranges in rates to be used are 0 to 100 kg/ha for N and 0
to 120 kg/ha for P.
N
(+2,0)
(+1,-1) (+1,+i)
(0,-2) (0,0) (0,2)
(-1,-1) (-1,+1)
(-2,0)
P
The coding scale is as follows:
Actual N: 0 25 50 75 100 Actual P: 0 30 60 90 120
Coded N:-2 -1 0 +1 +2 Coded P:-2 -1 0 +1 +2
FIG. V-l. Modified central composite design.
The design selected is a modification of the central
composite response surface (described by Cochran and Cox,
1957).
Selection of Sites
Sites should normally be selected to cover a range in
the environmental characteristics whose interaction with
the technologies to be tested is considered to be of
interest. These environmental characteristics could
include soil nutrient levels, soil moisture, climatic
effects, management, etc. The number of sites required
will depend upon the variability in the region and how the
results will be used (that is, the analysis or analyses to
be employed). For example, if modified stability analysis
is to be used where an environmental index is estimated,
as suggested in Chapter VII, a minimum of eight to ten
sites (perhaps as few as five) is necessary. This may
also be a reasonable number for estimating the component
of variation due to sites by analysis of variance. One
might also consider the magnitude of differences that one
wishes to measure, and then adjust the number of sites so
that the error variance component is small enough to
detect such a difference.
Complexity
It is desirable that these trials not be highly
complex. This is one reason why use of the randomized
complete block design is recommended. As mentioned above,
treatments may be arranged with either complete or
incomplete factorial structure. Treatments in incomplete
factorials should be chosen in such a way that undue
difficulty in analysis is avoided. Every attempt should
be made to standardize the number of blocks, the
treatments, and the plot and block dimensions, and to
avoid missing values for any of the plots. Trials that
differ from the others with respect to these
considerations could complicate the analysis. All
management operations should be recorded at each site
for use in interpreting results.
Replications over Years
Multi-year testing to ascertain stability of results
occurs in the farming systems approach as alternative
technologies move through the sequence of researcher- and
farmer-managed trials. Evaluating technologies over a
range of environments also aids in the evaluation of
stability. For this reason, it is not normally necessary
to repeat the same trial for two or more years, as is
usual on experiment stations, which represent only a
single site.
COMBINING DATA OVER SITES
One of the goals in regional trials is to provide an
estimate of interaction of sites (environments) and
treatments. One way this can be accomplished is with a
combined analysis of variance over sites. If this
interaction is negligible, estimates of the treatment
effects over sites, which would be used for
interpretation, would be stable. This would imply that
the recommendation domain is homogeneous with respect to
the treatments included and need not be partitioned.
Data for the first of the three control treatments
(the individual farmer's own technology) would normally be
omitted in a combined analysis of variance because it is
somewhat different at each location. The second and third
kinds of controls would be comparable from site to site
and can therefore be included. In general, a format for
an analysis of variance which combines data over sites is
as follows:
TABLE V-2. Combined analysis of variance procedure.
Source d.f. S.S. M.S. F
Site (s) s-1 SSS SSS MSS MSS
(s-l) MS(SxT)
Blocks
within s(b-l) SSB(S) SSB(S) MSB(S) MSB(S)
sites s(b-l) MSE
Treat- t-1 SST SST MST MST
ments (t-l) MS(SxT)
Site x
treat- (s-l)(t-l) SS(SxT) SS(SxT) = MS(SxT) MS(SxT)
ment (s-1)(t-l) MSE
Error s(b-l)(t-l) SSE SSE MSE
s(b- ) (t-1)
Total sbt-1
Combined Analysis of Variance
The combined analysis of variance and a test for
multiple comparison of treatment means is the procedure
often chosen to evaluate technologies across a region
and/or over time. The new technologies under analysis are
very often new varieties or hybrids, but any other
TABLE V-3. Plot yields of 15 maize cultivars evaluated in
three sites by ICTA, Chimaltenango, Guatemala
Replications
Site Cultivar I II III IV Totals
Alameda 1 2.10 2.27 2.34 2.67 9.38
2 2.54 2.56 1.94 2.42 9.46
3 3.16 3.29 2.63 2.36 11.44
4 2.39 2.56 3.20 2.40 11.55
5 3.65 3.24 3.25 2.40 12.54
6 4.65 3.42 2.48 2.42 12.97
7 3.43 3.44 3.02 3.42 13.31
8 2.12 3.13 3.64 2.41 11.30
9 3.39 3.73 3.46 3.64 14.22
10 2.44 2.16 1.90 1.27 7.77
11 4.67 3.14 3.15 2.87 13.83
12 2.61 3.40 3.90 2.84 12.75
13 1.95 3.44 2.99 3.49 11.87
14 2.67 3.16 2.58 2.56 10.97
15 3.33 3.13 2.18 2.59 11.23
Site totals 45.10 47.07 42.66 39.76 174.59
Parramos 1 4.59 6.26 6.32 4.64 21.81
2 3.86 6.24 4.10 6.01 20.21
3 4.75 4.21 4.48 4.65 18.09
4 6.20 7.00 4.57 5.37 23.14
5 5.97 7.09 4.29 6.09 23.44
6 6.43 6.09 5.88 6.70 25.10
7 6.59 6.21 7.19 5.41 25.40
8 5.24 6.17 6.33 7.74 25.48
9 6.40 6.68 5.56 6.00 24.64
10 3.46 4.08 2.89 3.06 13.49
11 6.31 6.19 6.52 7.13 26.15
12 5.03 6.36 4.80 4.10 20.29
13 6.92 5.85 6.49 6.40 25.56
14 5.95 6.32 7.30 7.23 26.80
15 5.35 5.33 4.99 3.64 19.31
Site totals 83.05 90.08 81.71 84.17 339.01
Itzapa 1 2.56 3.40 3.68 2.22 11.86
2 3.51 3.71 3.22 3.37 13.81
3 3.78 3.15 3.27 3.48 13.68
4 3.62 2.65 3.25 3.39 12.91
5 3.64 2.39 2.37 2.76 11.16
6 3.26 3.26 3.29 2.98 12.79
7 1.92 3.68 3.53 2.40 11.53
8 2.81 3.20 4.04 3.40 13.45
9 2.90 2.78 2.99 3.04 11.71
10 1.65 1.38 2.04 1.94 7.01
11 2.82 2.03 2.75 2.73 10.33
12 4.15 3.08 2.92 1.74 11.89
13 2.53 2.42 3.54 2.29 10.78
14 3.60 3.32 3.16 3.35 13.43
15 2.08 3.04 2.26 3.33 10.71
Site totals 44.83 43.49 46.31 42.42 177.05
management practice or technological innovation generated
for the region that shows variation due to soil,
management, and/or climatic factors could be analyzed by
this procedure. Table V-3 shows a group of three trials
illustrating the combined analysis procedure. This group
of trials was evaluating the response of yield and
morphological aspects of 15 maize cultivars to prevalent
conditions in a region.
The procedure for the combined analysis of variance
for the cultivars across the three sites was shown in
Table V-2. Each of the sums of squares (SS) was
calculated as follows:
CF = Correction factor
= [(Grand total of trials)2] / tbs
= [(tot site 1 + tot site 2 + tot site 3)2]
/ (15 x 4 x 3)
= (174.59 + 339.01 + 177.05)2 / 180
= 2649.986
where t = number of treatments
b = number of blocks or replications
s = number of sites
SSS = Sum of squares sites
= {[(tot of observations in each site)2] / tb} CF
= {[(Tot site 1)2 + (tot site 2)2
+ (tot site 3)2] / (15x4)} CF
= {[(174.59)2+(339.01)2+(177.05)2] / 60}
2649.986
= 295.950
SSB(S) = SS blocks (within sites)
= [(tot observations ea/block, ea/site)2 / t]
SSS CF
= {[(tot block l,site 1)2 +...+ (tot block 4,
site 3)2] / 15} SSS CF
= {[(45.10)2 + (47.07)2 +...+ (42.42)2] / 15}
295.968 2649.986
= 5.2908
SST
SS (SxT)
= SS treatments
= [(tot of each trt across sites)2 / bs] CF
= {[(trt tot 1 all blocks and all sites)2 +...
+ (trt tot 15)2] / (4 x 3)} CF
= {[(9.38 + 21.81 + 11.862 +...
+ (11.23 + 19.31 + 10.71)2 / 12} 2649.986
= 41.3328
= Sum of squares site x treatment
= {[(trt tot ea/site)2] / b} SSS SST
= {[(tot trt 1, site 1)2 +...
+(tot trt 15, site 3)2] / 4}
SSS SST CF
= {[(9.38)2 + (9.46)2 +...+ (10.71)2 / 4}
295.950 41.3328 2649.986
= 28.5818
- CF
SS (tot) = Total sum of squares
= Z(each observation)2 CF
= [(trt 1, block 1, site 1)2 +...
+ (trt 15, block 4, site 3)2] CF
= [(2.10)2 + (2.27)2 +...
+ (3.33)2] 2649.986
= 421.049
SSE =
=
Sum of squares error
SS(tot) [SSS + SSB(S) + SST + SS(SxT)]
421.049 (295.950 + 5.2908 + 41.3328
+ 28.5818)
= 49.8936
To obtain the mean squares, each sum of squares is divided
by its corresponding degrees of freedom (Table V-4). The
F values for sites and treatments are calculated from MS
(SxT) and not MSE. The F value for site-by-treatment
interaction is calculated from MSE.
For sites: F = MSS / MS(SxT)
= 147.975 / 1.021
= 144.93**
For treatments: F = MST / MS(SxT)
= 2.952 / 1.021
= 2.89**
For site-by-treatment interaction: F = MS(SxT) / MSE
= 1.021 / 0.394
= 2.59
All of these F values are highly significant (P<0.01).
TABLE V-4 Combined analysis of variance for yield of the
maize varieties evaluated in three sites,
Chimaltenango, Guatemala.
Sources of d.f. SS MS Fc F.01
variation
-Sites (s-l)=2 295.950 147.975 144.93 7.64
-Blocks s(b-1)=9 5.2908 0.588
(within
sites)
-Trts. (t-1)=14 41.3328 2.952 2.89 2.80
-Sites x (s-l)(t-1)=28 28.5818 1.021 2.59 1.87
trts.
-Error s(b-1)(t-1)=126 49.5936 0.394
-Total (sbt)-1=179 421.049
Source: ICTA
CV = 16.4%
The treatment means for each site and overall
treatment means are presented in Table V-5. As one
studies this table, the reason for the very highly
significant effect of sites becomes obvious. The mean
yields for the cultivars in Site 2 (Parramos) are, in most
cases, nearly double those of the other sites, so this
site is responsible for the highly significant difference
among sites. The effect of the site-by-treatment
interaction is evident when studying individual cultivars.
As an example, cultivar 2 has a high yield in Site 3 and
a low yield in Site 2. Cultivar 13 responds the opposite
way. See Chapter VII for a means of further analyzing
this interaction.
TABLE V-5.
Site and overall mean yields of 15 maize
genotypes evaluated in three sites,
Chimaltenango, Guatemala.
Treatment Site 1 Site 2 Site 3 Overall
(Cultivar) Alameda Parramos Itzapa Mean
-- metric ton/ha
1 2.345 5.452 2.965 3.587
2 2.365 5.053 3.451 3.623
3 2.861 4.524 3.420 3.601
4 2.888 5.785 3.226 3.967
5 3.136 5.861 2.789 3.928
6 3.244 6.277 3.199 4.240
7 3.326 6.349 2.882 4.186
8 2.824 6.369 3.363 4.185
9 3.553 6.161 2.927 4.214
10 1.942 3.373 1.755 2.357
11 3.460 6.537 2.583 4.194
12 3.186 5.072 2.972 3.744
13 2.969 6.415 2.693 4.026
14 2.742 6.702 3.357 4.267
15 2.808 4.826 2.677 3.437
Source: ICTA, Guatemala
To determine where the
differences
cultivars, Tukey's multiple range test for
Chapter IV) was performed:
exist among
means (see
D = Q Sx
= Qt,df (S2 / bs)1/2
= 015,126 x (0.3958 / 4x3)1/2
= 4.90 x (.1816)
= 0.89 ton/ha
The smallest difference between the mean yields of two
cultivars that will make them significantly different at
the 5% level of confidence is 0.89 ton/ha.
All treatment means are listed in descending order
and the same letter is placed next to all those that are
not different when compared:
Cultivar Overall mean
(Metric ton/ha)
14 4.267 a
6 4.240 a
9 4.214 a
11 4.194 a
7 4.186 a
8 4.185 a
13 4.026 a
4 3.967 a
5 3.928 a
12 3.744 a
2 3.623 a
3 3.601 a
1 3.587 a
15 3.437 a
10 2.357 b
For this case, Tukey's multiple range test shows that with
the exception of cultivar number 10, there are no
significant differences in yield. Cultivar 10 is
significantly lower in yield.
Tukey's multiple range test for means is considered
by many researchers as too severe since differences have
to be large to be statistically significant (5% level).
For example, in this case there were differences of up to
20% in yield (.85 ton/ha) among the group where no
differences were detected. However, with this test there
is little risk of adjudging significant differences that
actually do not exist. There are a number of multiple
range tests for means and the most appropriate should
always be chosen. For a discussion on multiple range
tests for means refer to Chew (1977). Had two more sites
been included in this trial, a modified stability analysis
(Chapter VII) may have been useful for detecting superior
cultivars.
Agronomic data serve to complement yield information.
In this case, when yield shows no significant differences,
the agronomic information is particularly important.
Table V-6 shows the mean values on the farm sites for days
to flower, ear height, and percentage of rotted ears.
Varieties are ordered according to yield.
TABLE V-6.
Evaluation of days to flower, ear-height,and
rotted ears in 15 maize varieties grown in
three sites, Chimaltenango, Guatemala.
Treatment Days to Ear Rotted
(cultivar) flower height ears
(cm) (%)
14 128 117 6.3
6 127 124 6.3
9 130 132 5.0
11 132 135 6.1
7 129 127 6.1
8 134 135 5.8
13 125 105 4.9
4 129 128 6.7
5 129 130 6.9
12 132 118 5.6
2 125 121 2.5
3 130 123 4.8
1 127 125 5.5
15 131 126 7.1
10 127 119 14.2
x 129 124 6.3
CV% 2.02 9.91 50.4
Source: ICTA, Guatemala
Variety 10 showed the lowest yield and also the highest
percentage of rotted ears (14.2%). Other varieties ranged
from 2.5% to 7.1%. Days to flower and ear height show
very contrasting values. Varieties 11 and 13 are the
earliest (128 and 125 days to flower) and also have the
lowest ear height (117 and 105 cm). Concomitantly,
varieties 11 and 8 are the latest flowering (132 and 134
days) and the tallest (135 and 135 cm).
These observations contributed to the conclusion that
these varieties, in view of their contrasting phenotypes,
should be considered for further evaluation in regional
trials, as well as in exploratory trials designed to
identify novel crop associations and plant distribution.
VI
Researcher-Managed Regional Trials:
Socioeconomic Evaluation
Economic evaluation of agronomic research data from
on-farm trials can involve little more than gathering and
using appropriate information. For example, if a change
of fertilizers is involved, the researcher should have the
price of the fertilizer currently being used and the price
of the fertilizer being substituted. The difference
between the rate applied, times the price of each, is the
difference in cost of the change. Yield differences are
evaluated on the basis of the price of the crop. If
yields change sufficiently so that harvest costs are
modified, this should be taken into consideration also.
Other economic analyses, however, can be more complex and
may require or benefit from different analytical or
statistical techniques. They may also require different
experimental designs from those utilized for agronomic
evaluation. Some of these differences include choice of
evaluation criteria (the means of measuring results),
effect of a technology on other enterprises on the farm,
effect on farm labor and its distribution within the
family, the potential risk involved,and the demand created
for other kinds of inputs. Many of these considerations
are too complex to be considered in this volume. However,
some warrant discussion, since they are of basic
importance to interpreting agronomic trials and making
recommendations from them.
CHOICE OF EVALUATION CRITERIA
One of the most important and critical decisions to
be made when designing research and evaluating data is the
selection of choice criteria for evaluation. The most
common evaluation criterion used by agronomists is yield
per unit of land area, frequently kg/ha. The use of this
criterion implies that land is the most limiting resource
on the farm and that therefore productivity of the land is
the most important evaluation criterion. This is not
always the case. On many small farms, even though there
is little land, land is not the most limiting constraint.
Nor is the same constraint necessarily the most limiting
for different crops. For example, small farmers in
Nariio, in the south of Colombia, traditionally plant
their scarce potato seed by spacing it widely to maximize
the productivity per unit of potato seed. The amount of
seed determines the size of the potato field. Hence, land
is not the most limiting resource with respect to potato
production on these small farms. However, the rest of the
land on these farms is planted into grain crops. For
grain, land is a limiting resource. For this reason, in
the case of potatoes, technological changes which increase
the productivity per unit of land area but decrease the
productivity per unit of seed will not be attractive to
these farmers. On the other hand, the same kind of
technology for grain crops could be acceptable. The
importance of using the relevant choice criterion in
evaluating on-farm trials is obvious in this case.
In large areas of Africa, land is not a limiting
resource. Farmers can plant as much land as they are able
to manage. However, in these same areas, rainfall is
scarce, so weeding the crops becomes a critical factor.
These farmers tend to plant the amount of land they can
effectively weed, because planting more land is a waste of
effort if it cannot be weeded. In this case, labor for
weeding becomes the most important evaluation criterion
and changes in crop production practices must be evaluated
against this factor.
In some areas, such as eastern Guatemala, crops must
be planted as soon as possible after the initiation of the
rains. Delayed planting reduces yield heavily because of
a mid-season dry spell, increased pest problems, or
because the crop does not mature before the rains
terminate. In this case, labor available for planting
becomes the most important evaluation criterion. For
most small farmers, cash is a very limiting resource. For
these farmers, the needs of the family and the home
compete directly with the needs of the crops and livestock
for the limited cash resources available. Non-cash inputs
are more important on these farms and only a limited use
is made of inputs which require a source of cash. In this
case a relevant choice criterion is the comparison of
return to cash costs.
Labor Input as an Evaluation Criterion
In all of the above cases, it is necessary for the
researcher to have information on the use of the resource
in question in order to be able to employ the appropriate
evaluation criterion. For example, if labor at weeding
time is critical, any changes in technology which
influence weeding will create a need for the researcher to
monitor weeding labor. Weeding of the individual crop in
question is important, but the effect of utilizing more
labor on any one particular crop can also have an
influence on labor availability for other crops,
livestock, or household activities. This should also be
taken into consideration. Other important considerations
are which members of the household are involved and
whether or not labor is hired.
In order to evaluate changes in labor requirements
from on-farm or on-station research, it is usually
necessary to have larger plots than are required for
strictly agronomic evaluation. Plots need not be full
field size, however. In on-farm research, records must be
kept of the labor utilized by farmers on their own fields
for the particular operations in question. Labor use
should take into consideration the time lost in going to
and from the field, and for resting, drinking water,
eating, sharpening implements, or anything else that
reduces the amount of time that land can be worked in a
day. Records should also be kept of the labor required
for the same tasks in the trial plots. Usually, a test
plot will be completed without any rest, implement
sharpening, or other delays which are normal in field
work.
PRACTICAL FIELD ADVICE
Farmers have standard estimates of the amount
of time required to do most traditional field
operations. The amount of land a person can weed,
plant, or clear in a day is established as much by
custom as by measurement. Where these
measurements are available, they should be used
for the traditional treatments because it reflects
reality in the area.
The problem comes when changes in the amount
of labor required to accomplish specific tasks are
made. If more time is required to weed a certain
area, the people who are doing the work may demand
more pay. On the other hand, if less time is
required, the farmer may try to increase the area
which is completed in a day's time. Evaluating
these possible changes must be done by asking the
opinions of farmers and laborers or by waiting to
see what happens in practice.
Having the information from farms and plots, the
researcher can make appropriate adjustments in plot data.
By converting plot size to hectares or some other measure
of land area commonly utilized by farmers, a factor is
available for comparing plot labor usage with real farm
data. For example, if a 10 x 10 meter plot requires one
half hour for an operation, this is equivalent to 50
hours/ha or 6.25 workdays of 8 hours/day. If the same
operation on a farm basis requires 20 workdays per
hectare, then 20 / 6.25 = 3.2 is the conversion factor.
In other words, multiplying labor operations done on a 10
X 10 plot by 3.2 and adjusting plot size to a normal land
unit size results in an estimate of the labor required on
a normal land unit basis. For example, if labor required
for another 10 X 10 m plot is 20 minutes (1/24 workday),
then workdays per hectare for this technology is:
(1 / 24) x 3.2 x 100 = 13.3
If labor for weeding is the limiting resource in a
recommendation domain, then production should be divided
by weeding time to get an estimate of labor productivity
(product per unit of labor). For example, consider the
following situation: under traditional practices, 20
workdays are required to weed a hectare of land that
produces 3200 kg of product. A new arrangement in
planting density and spacing adds 20% to labor
requirements for weeding and results in 500 kg of
additional production. Traditional practices result in
160 kg per workday spent in weeding (3200 / 20) but the
alternative technology yields 3700 kg for 24 workdays or
154.2 kg per workday. Because labor for weeding is
limiting, the relevant evaluation criterion is not yield
per hectare (3700 vs. 3200 kg). If farmers are limited to
30 workdays of labor in the weeding period, during those
30 workdays they are able to weed less land in the new
system. Because each workday results in 154.2 kg of
product with the new technology, rather than 160 kg with
the traditional technology, the 30 workdays produce only
4626 kg under the alternative technology, compared with
4800 kg under the traditional technology. In this
example, it is evident that the criterion of yield per
hectare (3700 kg compared with 3200 kg) results in a false
conclusion regarding the value of the technology to the
farmers. With a limit of 30 workdays of labor available
for weeding, this leaves farmers with a choice of 4800 kg
of product with the traditional system or 4626 kg using
the new technology.
Measures of productivity of labor (kg/workday) are
subject to the same kind of variation as other measures of
productivity, such as kg/ha. A common mistake in making
an economic analysis is to make only one estimate and
assume it is firm. Measures of productivity (evaluation
criteria) can be subjected to the same kinds of
statistical analysis as are commonly used for biological
or agronomic criteria. For example, net income can be
affected by variation in yield, price of the product, use
of inputs, and price of inputs. When farmers' practices
and prices paid or received vary, separate income
calculations should be made for each farm, just as
separate yields are measured for each farm.
Cash as an Evaluation Criterion
In commercialized and monetized agriculture, cash can
effectively substitute for most other inputs. If more
seed is needed, it is purchased with cash (or credit,
which is another form of cash). If more labor is needed,
it is also purchased with cash. However, in many small,
limited-resource farm situations, nearly all resources
used in the production process come from the farm. Only
a very few inputs are purchased. These include inputs
which are not available on the farm, such as chemical
fertilizer, insecticides, herbicides, and improved or
hybrid seed. On farms where farmers are unaccustomed to
making purchases with cash, great care must be taken to
evaluate the productivity of, or return to, the additional
amount of cash required for alternative technologies.
On fully commercialized farms, where cash is
basically not a limiting factor, the criterion of profit
maximization may be relevant. Profit maximization is
achieved where the value of the product obtained from the
last unit of input is just equal to the cost of that
additional unit. However, farmers with very limited
amounts of cash will not usually be interested in
utilizing as much cash in an individual enterprise as is
required to maximize profit. Rather, they will be looking
for ways to achieve the highest return (or productivity)
per unit of cash invested in the enterprise. In this
situation, the amount of product per unit of cash (similar
to the amount of product per unit of labor) is a relevant
evaluation criterion. Calculations can be made in a
manner similar to those shown above for returns to labor.
Because cash can be converted into many different
kinds of inputs, it is more critical to look at
alternative uses for cash and not just consider return to
cash investment for individual enterprises. This is even
more critical on small farms where family necessities
compete directly for limited cash resources. If
researchers consider only the return to cash investment in
the commodity in which they are interested, they may well
find that what appears to be a "good" technology is not
acceptable to farmers, who would rather use the cash in
another way, such as for a wedding or to repair the house.
RESPONSE SURFACES*
What They Are
A response surface is a representation of the natural
relationship which exists between the quantity of a
product and various levels of one or more inputs used to
produce that product. That is, a response surface is an
estimate of the response of a product to different
quantities of one or more inputs utilized in the
production process. This representation can be physical,
tabular, graphic, or mathematical. A true response
surface with three dimensions (width, depth, and height)
results in graphic form when only two inputs are used to
obtain one product. In this form, the surface is similar
to a hill with quantities of the two inputs measured
toward the north and east and quantity of product
represented by height, or altitude. Each point on the
surface represents a combination of different quantities
of input A, input B, and yield of the product. In the
simplest case of only one input, the "surface" is a
straight line or a curve. In a more complex case with
three or more inputs used to produce one product, it is
impossible to imagine or draw the response "surface," so
it must be represented in mathematical form.
The graphic or mathematical form of a response
surface is an artificial estimate of a real phenomenon
that exists in nature. The surface can represent the
response of a product to a continuous input, such as a
crop to fertilizer or animals to feed, etc. Because the
response is a natural biological phenomenon, it is not
constant for a fixed level of inputs. Rather, it is
subjected to a random variance. The granhic or
mathematical response surface represents the central
tendency of the response in terms of magnitude (level) and
of form (curvature).
Representative Forms
To demonstrate the forms which response surfaces can
take, a two-dimensional case will be used with one input
*Much of this section was translated and adapted from
Hildebrand (1972).
and one product. Surfaces can be represented either
graphically or mathematically in generalized form.
Mathematically, yield (Y) is a function of the quantity
of input (X), that is Y = f (X).
The simplest form of a response surface, one that is
seldom useful, is a straight line (Fig. VI-la).
Generally, linear responses are found only with small
changes in the level of the input.
Product
Product
Product
Linear
Input
1c.
Square Root
Input
Product
Product
lb.
Quadratic
Input
1d.
Cubic
Input
le.
Logarithmic
Input
FIG.VI-1. Two-dimensional response surfaces.
Perhaps a more useful form of curve is the parabola,
or quadratic function (Fig. VI-lb). This type of curve is
representative of part of the law of diminishing returns.
It has a maximum and can demonstrate a decline in
production resulting from high or toxic use of an input if
that phenomenon is present. A similar form is the square
root function (Fig. VI-lc). The square root function also
has a maximum but it is less sharp than the parabola. In
some cases, data represent surfaces which are more complex
than can be represented by the previous curves. If the
response surface contains all three economic stages of
production, a form such as a cubic function (Fig. VI-ld)
is required. A cubic function can have a portion that
increases at an increasing rate (Stage I), another part
that increases at a decreasing rate (mostly in Stage II),
and finally a portion that decreases with increases in the
level of the input (Stage III). Another useful function
is the logarithmic function (Fig. VI-le), called by
economists the Cobb-Douglas function. This function does
not have a maximum and is therefore useful for responses
that display this characteristic (for example, herbicides
and insecticides if they do not induce decreasing
production). It is also an easier function to work with
than are some other forms.
Economic Analysis
The analysis of data by response surfaces is related
to analysis of variance, but it is more efficient in
describing the relationships and results in more directly
applicable information for researchers and farmers. The
least-squares method, which is used to calculate the
statistical values of the surfaces by regression, is based
on all usable observations and is therefore efficient in
the use of the data. Also, once a researcher has a
mathematical function, it is possible to interpolate and
predict responses for input levels not included in the
original experimental design. With care, estimated
responses can be extrapolated beyond the range of the
data. Also, with a curvilinear function it is possible to
find the quantity or the combination of inputs which
result in maximum physical production by equating the
first derivative of the response surface to zero.
Perhaps the most useful reason to calculate response
surfaces is to facilitate economic analysis. After
researchers have calculated the equation for the response
surface, they can calculate the quantity or combination of
inputs which are most profitable for commercial producers
from any combination of prices of inputs and product. The
economic optimum combination of inputs is the amount which
results in maximum profit for farmers (Fig. VI-2). Using
U for profit (utility), which is the difference between
income (I) and cost (C) for one input, the following
calculations can be made:
I = Y(Py)
C = X(Px) + FC
U = I-C
= Y(Py) X(Px) FC
where:
I = total income
Y = quantity of product (generally yield per ha)
and is a function of X: Y = f (X)
C = total cost (variable + fixed cost)
Py = price of the product
X = quantity of input
Px = price of the input
FC = fixed costs that include all costs except
the purchase of X, which is the input under
consideration
U = profit or net income (utility)
In the rational or economic stage of production, the
response curve is increasing, but at a decreasing rate.
Therefore, the function of I (total income) will have the
same form. Cost is a straight line with an intercept
equal to FC. The difference between I and C, which is
utility or profit, is a curve which has a maximum at the
point where the vertical difference between I and C is
greatest. The quantity of the input that results in this
value is the quantity which maximizes profit.
Mathematically, this can be calculated as follows:
U = Y(Py) X(Px) FC
dU/dX = [(dY/dX) Py] Px
= (marginal profit)
Quantity of Input X
$ i
Maximum
Profit
U
Quantity of Input X
FIG.VI-2. Variable cost (VC), fixed cost (FC), income
(I), and profit (U) functions.
When marginal profit is equal to zero, the profit curve U
is at a maximum. Therefore, in order to find the amount
of the input which results in maximum profit, the
following relationship is calculated:
[(dY/dX) Py] Px = 0 or
dY/dX = Px/Py
In other words, to maximize profit, the derivative of the
response surface (dY/dX) is equated to a ratio of the
price of the input to the price of the product (Px/Py).
The prices of the inputs and the prices of the products
must be measured in the same units used in calculating
regression.
For two or more inputs, the solution is an
extension of the above:
U = Y(Py) X1(Pxl) X2(Px2) -...- Xn(Pxn) FC
where X1, X2,..., X, are the inputs included as variables
in the response surface. The partial derivatives (these
are partial derivatives because there is now more than one
input, X) are:
6U/6X1 = [(6Y/6X1) Py] Pxl = 0
6U/6X2 = [(6Y/6X2) Py] Px2 = 0
6U/6Xn = [(6Y/6Xn) Py] Pxn = O
The simultaneous solution of this set of partial
derivatives will result in the combination of the n inputs
to produce product Y that maximizes profit for farmers.
There are various ways to estimate response surfaces.
The best in any case will depend on the quantity of
inputs, the number of treatments, and the type of
calculating or computing equipment available to
researchers.
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