• TABLE OF CONTENTS
HIDE
 Front Cover
 Title Page
 Preface
 Table of Contents
 Chapter 1: Introduction
 Chapter 2: Terminology and experimental...
 Chapter 3: Problems
 Chapter 4: Solutions
 The analysis of variance: A general...
 Index 1: General
 Index 2: Experimental designs
 Index 3: Analysis of variance
 Further reading
 Back Cover






Group Title: On-farm experimentation : a manual of suggested experimental procedures
Title: On-farm experimentation
CITATION PAGE IMAGE ZOOMABLE PAGE TEXT
Full Citation
STANDARD VIEW MARC VIEW
Permanent Link: http://ufdc.ufl.edu/UF00054844/00001
 Material Information
Title: On-farm experimentation a manual of suggested experimental procedures
Physical Description: iii, 87 p. : ill. ; 28 cm.
Language: English
Creator: Hammerton, John L
Lauckner, F. B
Caribbean Agricultural Research and Development Institute
Publisher: Caribbean Agricultural Research and Development Institute
Place of Publication: Saint Lucia
Publication Date: [1984]
 Subjects
Subject: Agriculture -- Research -- On-farm -- Caribbean Area   ( lcsh )
Agricultural systems -- Research -- Caribbean Area   ( lcsh )
Field experiments -- Caribbean Area   ( lcsh )
Experimental design   ( lcsh )
Genre: bibliography   ( marcgt )
non-fiction   ( marcgt )
 Notes
Bibliography: Bibliography: p. 87.
Statement of Responsibility: John L. Hammerton and F.B. Lauckner.
General Note: Includes index.
General Note: "An output of the CARDI/USAID FSR/D Project #538-0099."
General Note: "April 1984."
Funding: Electronic resources created as part of a prototype UF Institutional Repository and Faculty Papers project by the University of Florida.
 Record Information
Bibliographic ID: UF00054844
Volume ID: VID00001
Source Institution: University of Florida
Holding Location: University of Florida
Rights Management: All rights reserved by the source institution and holding location.
Resource Identifier: aleph - 002199173
oclc - 13983256
notis - ALD9055

Table of Contents
    Front Cover
        Front Cover
    Title Page
        Title Page
    Preface
        Page i
        Page ii
    Table of Contents
        Page ii-a
        Page iii
    Chapter 1: Introduction
        Page 1
        Page 2
        Page 3
    Chapter 2: Terminology and experimental designs
        Page 4
        2.1. Terminology
            Page 4
        2.2. Randomised complete block designs
            Page 5
            Page 6
            Page 7
            Page 8
            Page 9
        2.3. Incomplete block designs
            Page 10
            Page 11
            Page 12
            Page 13
            Page 14
            Page 15
            Page 16
            Page 17
            Page 18
            Page 19
        2.4. Factorial experiments
            Page 20
            Page 21
            Page 22
        2.5. Confounding
            Page 23
            Page 24
            Page 25
            Page 26
        2.6. Fractional replication
            Page 27
            Page 28
            Page 29
            Page 30
            Page 31
        2.7. Unequal replication
            Page 32
            Page 33
            Page 34
            Page 35
            Page 36
        2.8. One or more blocks per farm
            Page 37
            Page 38
            Page 39
            Page 40
            Page 41
        2.9. Partitioning of the error S.S.
            Page 42
        2.10. Comparison of zones
            Page 42
            Page 43
            Page 44
        2.11. Summary
            Page 45
    Chapter 3: Problems
        Page 46
        3.1. Physical
            Page 46
        3.2. Biological
            Page 46
        3.3. Technical
            Page 47
        3.4. Farmers
            Page 47
            Page 48
        3.5. Planning and design
            Page 49
        3.6. Management
            Page 50
        3.7. Data collection
            Page 51
        3.8. Missing plots and blocks
            Page 52
    Chapter 4: Solutions
        Page 53
        4.1. Physical
            Page 53
        4.2. Biological
            Page 53
        4.3. Technical
            Page 54
            Page 55
            Page 56
            Page 57
        4.4. Farmers
            Page 58
        4.5. Planning and design
            Page 59
            Page 60
            Page 61
            Page 62
            Page 63
        4.6. Management
            Page 64
        4.7. Data collection
            Page 64
            Page 65
            Page 66
            Page 67
        4.8. Missing plots and blocks
            Page 68
            Page 69
    The analysis of variance: A general method for designs arranged in blocks, and accommodating incomplete block designs, missing plots, and unequal replications
        Page 70
        Page 71
        Page 72
        Page 73
        Page 74
        Page 75
        Page 76
        Page 77
    Index 1: General
        Page 78
        Page 79
        Page 80
        Page 81
        Page 82
    Index 2: Experimental designs
        Page 83
        Page 84
    Index 3: Analysis of variance
        Page 85
        Page 86
    Further reading
        Page 87
    Back Cover
        Back Cover
Full Text









CARIBBEAN AGRICULTURAL RESEARCH AND DEVELOPMENT INSTITUTE







ON-FARM EXPERIMENTATION
A MANUAL k H b KI <.
OF
SUGGESTED EXPERIMENTAL PROCEDURES





& c d e b






JOHN L. HAMMERTON
AND
FP.B.LAUCKNER







e cA c a b d
E.... .. d1Kl aI_ _T__ _


An output of
The CARDI/USAID FSR/D Project
#538-0099














CARIBBEAN AGRICULTURAL RESEARCH AND DEVELOPMENT INSTITUTE
CARDD)


ON-FARM EXPERIMENTATION

A MANUAL
OF SUGGESTED EXPERIMENTAL PROCEDURES









John L. Hammerton
and
F.B.Lauckner








An output of
The CARDI/USAID FSR/D Project
#538-0099


SAINT LUCIA


1


APRIL 1984













PREFACE


The yield gap that exists in crop and animal productivity
between Experimental Stations and farmers' fields in the Eastern
Caribbean is currently exercising the minds of both agro-biological and socio-:
economic researchers in CARDI. CARDI"s approach to agricultural research
in the sub-region is based'bh'its experience in attempting to.concentrate
its limited human and physical resources on finding solutions to the numerous
biological, social and econrmie constraints that affect small and medium :
size farm households.


CARDI's Farming Systems Research and Development methodology lays
particular emphasis on On-farm Experimentatio' at several stages, viz: i
1) On-Farm Production Systems Analyses; -
2) On-Farm Validation with Farmer Control and extensive
supervision,
3) On-Farm Testing with researcher control and supervision;
4) Applicability testing with Farmer Control and supervision.

The needs of all these various On-Farm Testing Schemes vary because
objectives are different, thus necessitating varying design management
and analysis considerations.

Since On-Farm experimentation is fundamental to CARDI's Farming
System Research and Development methodology it follows that for success
On-Farm experiments must be carefully planned and managed. Close
collaboration with farmers and extension agents is also vital. However,
none of these is sufficient unless the experimental designs are efficient
and well conceived.

The nature of most small farms in the Eastern Caribbean small
size, prevalence of steep slopes, complexity of the farming systems -
makes On-Farm Experimentation difficult and certainly far more difficult
than traditional Field Station Experimentation.













This Manual provides guidelines that should enable both Country
Teams and Technical Specialists to design, plan, manage and analyse
On-Farm Experiments. The Manual stems basically from the experiences
gained in the design, management and analysis of On-Farm Experiments in
the Eastern Caribbean. The Authors, Dr. John Hammerton, Technical Co-
ordinator (Windward Islands) of the USAID funded Farming Systems Research
and Development (FSR/D) Project and Mr. Bruce Lauckner, Biometrician at
CARDI Headquarters, Trinidad, must be commended for their efforts in pro-
ducing the Manual. It is hoped that the Manual will be of tremendous
benefit to the scientists conducting On-Farm Experiments in the FSR/D
Project as well as those others in the region interested in this approach
to agricultural research and development.





CALIXTE GEORGE :
Project Manager
Farming Systems Research and Development -
Project #538-0099.


lei .:


:.;;: :r-'lf:~r'! ~,:i














(ii)


Chapter 1. Introduction

Chapter 2. Terminology, and Experimental Designs

2.1. Terminology
2.2 Randomised Complete Blbck Designs
2.3. Incomplete Block Designs
2.4. Factorial Experiments
2.5. Confounding
2.6. Fractional Replication
2.7. Unequal Replication
2.8. One or more blocks per farm
2.9. Partitioning of the Error S.S.
2.10. Comparison of Zones
2.11. Summary
Chapter 3. Problems


3.1.
3.2.
3.3.
3.4.
3.5.
3.6.
3.7.
3.8.


Page No.


1

4
4

5
10
20
23
27
32
37
42
42.
45
46


Physical
Biological
Technical
Farmers
Planning and Design
Management ;!. ; :
Data Collection
Missing plots (and blocks)













( iii)


Page No.


Chapter 4. Solutions


4.1.
4.2
4.3
4.4
4.5
4.6
4.7
4.8


Physical
Biological
Technical
Farmers
Planning and Design
Management
Data Collection
Missing plots (and blocks).


53
53
54
58
59
64
64
68


APPENDIX:








INDEX 1.
INDEX 2
INDEX 3
FURTHER READING.


The Analysis of Variance: a 70
General Method .fetDesigns arranged in
blocks and accommodating
Incomplete Block Designs,. Missing Plots and
Unequal Replication


General 78
Experimental Designs 83
Analyses of Variance 86

87










CHAPTER 1, INTRODUCTION




On-farm experimentation is basic to Farming Systems Research and
Development (FSR/D). In CARDI's FSR/D methodology (Fig.l) on-farm
experimentation is carried out at four steps in sequence of activities
leading to the transfer of improved technologies. These steps are:-

On-farm Production Systems Analysis (Step 5) which includes
exploratory experiments and technology screening. At this step the
number of treatments in an experiment may be relatively large. These
experiments are very much under the control of the researcher.

On-farm Testing of Alternatives (Step 9) compares those
technologies and components evaluated in steps 4 to 7. Design and
synthesis of components is done at step 8. The number of treatments
at this step is likely to be small, and to include a farmer practice
control treatment. These experiments are also under the researcher's
control, but with the farmer's active assistance and participation.

-On-farm Testing with farmer control (step 10) is likely to haveno
more than two treatments farmer practice and one alternative
selected from those tested at step 9. These tests are supervised
by Extension Officers, but the researcher must be responsible for
general oversight, and for planning, treatment specification and the
design of data collection.

Applicability testing (step 11) may or may not involve experi-
mentation: an improved technology may be advocated as a replacement
for the farmer's traditional technology, or a farmer involved in
steps 9 ahd 10 may decide to adopt this improved technology.

Thus it is likely that the number of treatments to be tested will
decrease as work progresses from step 5 to steps 9, 10 and 11.
Experimental designs eill accordingly become simpler.

The FSR/D approach to technologyy generation does not preclude
Field Station and laboratory research as Fig. 1 demonstrates.
These types of research are complementary to, and supportive of, on-
farm research. Some types of research are unsuited to on-farm
experimentation: examples are varietal screening, livestock feeding
trials with several rations and/or regimens, and the screening of
pesticides to evaluate efficacy, optimal frequency of application and
rates and so on.

It should be noted that Field Station research does not necessarily
require the physical facility of a field station. Such research can be
done on a farmer's land: it is the single site, the total control
exercised by the researcher and, usually, the emphasis on a commodity
and/or a discipline or a technology component that distinguishes field
station type research from on-farm research.
.../












FIG. 1 CARD'S FARMING SYSTEMS RESEARCH
METHODOLOGY


AND DEVELOPMENT


Production
System


Production
System
Components


1. Target Area & Farmer Selection



2. Reconnaisance


Descriptive
Phase


Testing
Phase


3. Specific Problem


Transfer
phase 11. Applicability testing


Eastern
Caribbean


Island
System


Farm
System


Survey


Mass Transfer by Extension
Agencies


- l


i J s '


I


I. ,













Most researchers are familiar with at least a few experimental designs
appropriate to field station research, the techniques for managing and
conducting such experiments, and the basics of data analysis. On-farm
research uses the same designs, techniques and methods of data analysis,
but there are problems peculiar to such research, and designs which are
not commonly..used in field station research but may be appropriate to
on-farm re.e'arch. These problems and designs form the subject matter
of this manual.

This manual is intended to stimulate thought, to encourage
imaginative planning of experiements, and to avoid inadequate experimenta-
tion arising from ignorance of appropriate designs and the relevant
analyses. It does not purport to provide definitive solutions to all the
problems discussed, nor;does it consider such topics as farm surveys,
farm studies or island studies, although these steps are important
components of the CARDI FSR/D methodology (Fig.l)

Section 2.describes the main types of design likely -to be useful. It
includes some worked examples and discusses'the pros and cons of the various
designs, and. somerelated topics such as replication and variability.

Section 3 poses some of the problems that can arise in on-farm
experimentation without offering solutions. Some possible solutions are
suggested in Section 4.














CHAPTER 2: TERMINOLOGY AND EXPERIMENTAL. DESIGNS


This section defines the terminology of experimentation, and
discusses those experimental designs appropriate to on-farm research.

2.1 Terminology

Experiment refers to the entire set of plots of a single investiga-
tion. An experiment comprises a minimum of two treatments which are
replicated or repeated. Treatments are allocated to individual plots
in some organized random fashion, and plots are arranged in blocks,
except in the completely randomised design. This design is not suitable
for on-farm experimentation however. Each block may comprise a
complete replicate or set of treatments, when it is a complete block.
Alternatively, blocks may comprise subsets of the treatments, when they
are known as incomplete blocks, so that more than one block is necessary
to make up a single replicate. In some designs blocks may contain more
plots than there are treatments, with one or more treatments allocated
to two or more plots in each block.

On-farm experiments may be sited on a single farm or distributed
over several farms. The first arrangement of course is equivalent
to a field station experiment, except that the blocks may be sited on
different parts of the farm, and problems of the designs and management
of this type of experiment will not be further discussed.
Where an experiment is
spread over several farms, individual farms may accommodate one or
more complete or incomplete blocks.

Decisions as to the "best" design for an on-farm experiment must
take into account the number and nature of the experimental treatments,
the availability of land suitable for experimentation on the participating
farms, and the resources especially of manpower available. It is a
basic principle that plots within blocks be as uniform as possible with
respect to slope, soil texture, weediness, plant number (except where this
is a treatment variable), plant height and girth and so on, so that block
size the number of plots per block is ofter a major factor determining
appropriate designs. Plots within blocks need not be contiguous, and
blocks can differ with respect to the above, and other, characteristics.














CHAPTER 2: TERMINOLOGY AND EXPERIMENTAL. DESIGNS


This section defines the terminology of experimentation, and
discusses those experimental designs appropriate to on-farm research.

2.1 Terminology

Experiment refers to the entire set of plots of a single investiga-
tion. An experiment comprises a minimum of two treatments which are
replicated or repeated. Treatments are allocated to individual plots
in some organized random fashion, and plots are arranged in blocks,
except in the completely randomised design. This design is not suitable
for on-farm experimentation however. Each block may comprise a
complete replicate or set of treatments, when it is a complete block.
Alternatively, blocks may comprise subsets of the treatments, when they
are known as incomplete blocks, so that more than one block is necessary
to make up a single replicate. In some designs blocks may contain more
plots than there are treatments, with one or more treatments allocated
to two or more plots in each block.

On-farm experiments may be sited on a single farm or distributed
over several farms. The first arrangement of course is equivalent
to a field station experiment, except that the blocks may be sited on
different parts of the farm, and problems of the designs and management
of this type of experiment will not be further discussed.
Where an experiment is
spread over several farms, individual farms may accommodate one or
more complete or incomplete blocks.

Decisions as to the "best" design for an on-farm experiment must
take into account the number and nature of the experimental treatments,
the availability of land suitable for experimentation on the participating
farms, and the resources especially of manpower available. It is a
basic principle that plots within blocks be as uniform as possible with
respect to slope, soil texture, weediness, plant number (except where this
is a treatment variable), plant height and girth and so on, so that block
size the number of plots per block is ofter a major factor determining
appropriate designs. Plots within blocks need not be contiguous, and
blocks can differ with respect to the above, and other, characteristics.













2.Z. Rand-.=ised Complete Block Designs

The completely randomised design is the simplest. Treatments are
replicated but allocated at random to the total array of plots. Such
a design is appropriate only where all the plots are uniform. Clearly
this condition will not be met where plots are spread over a number of
farms. In such a case it is essential to take account of the expected
differences between farms.

The simplest design for on-farm experimentation is therefore the
razdomised complete block design (RCB), with one (complete) block per farm.
Fig. 2 gives an example with four treatments (a d) and eight farms.
The analysis of variance is straight-forward, and the apportionment of the
degrees of freedom (d.f.) is as follows where b number of blocks and
t = number of treatments. With one complete replicate per block, the
number of replicates(r) equals the number;of blocks and the number of forms.
A significant difference for blocks in the analysis of variance therefore
indicates a significant difference between farms.


Blocks (b 1) = (r 1)
Treatments (t 1)
Error (b -1)(t-1) (r -1)(t-l)
Total (bt -1) W (rt-l)












Fig. 2 A randomised complete block (RCB) design with one complete
replicate per block. There are four treatments (a-d)
and one block per farm on eight farms. Note the
variations in block shape and non-contiguity of some plots
in some blocks.


SFarm- A



c a b


Farm D


Farm B


dF


Farm E


Farm G


c d


Farm H


a c b


Farm C


Farm F


b d


C


c


# .













A variation of this design is to have two (or more) complete replicates
per block. This design could be used where it is possible to find blocks
of uniform plots such that the number of plots is twice, or some multiple
of, the number of treatments. Fig. 3 gives an example of such a design,
where t 3, b 4 and 4r 8. The analysis of variance would be as shown
above, but the divisors in the calculation of the sums of squares for treat-
ments would be.r and not b as would be the case with only one complete
replicate per block. This variant is unusual, and unlikely to be
important. More likely to be useful and practicable is two complete blocks
per farm ( see 2.8).

A randomised complete block experiment with only two treatments
(i.e. two plots per block) can be analysed by a paired t test.
Equally an on-farm experiment with only two treatments a comparison
of a new technology against farmer practice at step 10 for example can
be designed as a paired t-test comparison with two plots per farm on a
large number of farms. Such an analysis is not appropriate if there is
more than one replicate (i.e. pair of plots) per farm (see 2.8)

Table 1 gives an example of a paired 't' test for a hypothetical data
set. The mean difference D, is divided by S- the standard error of
the mean difference, to calculate 't', with n-1 .f., where n a number
of pairs. The data have also been analysed by analysis of variance. Both
't' and F are highly significant in this instance.












Fig. 3. A randomised complete block (RCB) with two complete
replicates per block. There are four treatments
(a d) and four blocks, one per farm. Note the
variations in block shape and non-contiguity of some
plots.

Farm A Farm B


a b |d a
! Tl "7


Id c d b


a c






d


Farm C


b

d


I


b
!


Farm D


Note:this is distinct from the more usual and more useful design with two
complete blocks per farm.


c b d


c a ,













Table 1. A


9

paired't' test from a hypothetical experiment with
11 pairs of plots, (or 11 blocks of two plots). The
two treatments are a and b.


Pair D = 't' test
a b (b -a)
1 7.3 9.8 2.5
2 5.8 7.7 1 .9 S
3 6.1 9.4 3.3 D
4 8.3 10.2 1.9
5 9.9 14.3 4.4 D/ ~
D
6 6.8 8.8 2.0
7 8.2 11.3 3.1 SD .4D2 D)2/n
8 9.1 12.5 3.4
9 11.0 12.9 1.9 1
10 8.9 12.0 3.1 n number of pairs
11 10.5 15.3 4.8 SD = 105.15 94
105.15 94.84
Total 91.9 124.2 32.3 10
Mean 8.35 11.29 2.94
= 1.0154

S = 1.0154
J 11
0.3061
t 2.94 9.60
0.3061
(with n 1 d.f.)

Analysis of Variance:

S.S. d.f. M.S. F.

Blocks 80.63 10
Treatments 47.42 1 47.42 92.08
Error 5.15 10 0.515

Total 133.20 21













2.3 Incomplete Block Designs


As the number of treatments increases, block size in a RCB design
obviously increases. The variability of terrain, soil depth and other
factors on small farms may make it difficult to find blocks of adequate
size, without sacrificing the criteria (of uniformity) for blocking. It
then becomes necessary to use incomplete blocks, such that each incomplete
block contains a subset of the treatments. Allocation to subsets (i.e.
to incomplete blocks) follows certain rules, and some designs are
available from reference works. Improved methods of analysis have
resulted in greater flexibility in the choice of incomplete block designs.

The simplest incomplete block design is the balanced lattice. In
this, the number of treatments must be an exact square, and the number of
plots per block is the corresponding square root. This design is
therefore suitable for an experiment with nine treatments, with blocks of
three plots. A design is shown in Fig. 4 it has four replicates, with
a total of twelve blocks each of three plots. Every pair of treatments
occurs once, and only once, in the same block, so that all pairs of treat-
ments are compared with about the same precision, even though differences
between blocks may be large. This might well be the case if single blocks
were located on twelve different farms. As far as possible, similar
blocks to the extent that this can be ascertained should be placed in
the same replicate. Eight replicates, involving 24 farms, each with one
block, could also be used.


Fig. 4. A balanced lattice design for nine treatments (a-i) in 12
blocks ( (1) (12) ) of three plots with four simple
replications (t 9, k-3, b-12, r = 4)


a b c (4) a d g (7) a e i (10) a h f


d e f (5) b e h (8) g b f (11) d b i


g h i (6) e f i d h c (12) g e c










Where
designs are
some of the
block sizes


the number of treatments is not a square,balanced incomplete block
available. Figs. 5 and 6 give two examples, and Table 2 lists
designs available for different number of treatments (t) and
(k number of plots per block).


There are also partially balanced designs, of which the simplest
examples are the lattices. As for the balanced lattices, the number of
treatments must be a square. Partially balanced designs are less suitable
than balanced designs: the statistical analysis is more complex, and when
variation among blocks is large, as must be expected in on-farm research,
some pairs of treatments are compared less precisely than others.


Fig. 5 A balanced incomplete bli
in ten blocks ( (1) (1
replication (t-5, k-3, b


Reps I, II & III


a

a


b

b

d


b c d


c d e


(6)

(7)

(8)


(9)


(10)


ock design for five treatments (a-e)
0)) of three plots with group
- 10, r 6).


Reps IV, V & VI


a

a


d

e


Fib. 6 A balanced incomplete


21 blocks
(t -
Reps I & II

a b


c

d


d

g


e f

c g


((1) 21))
7, k 2,


Block design for seven treatments (a-g) in
of two plots with group replication
b 21, r 6)


Reps III & IV


(8)

(9)


(10)

(11)

(12)

(13)

(14)


e g

a f

b g


(15)

(16)


(17)

(18)

(19)

(20)

(21)


Reps V & VI


c


c f

d e


' *


c e


f g

a 8











Table 2. Examples of balanced incomplete block designs
for different numbers of treatments (t) and
numbers of plots per block (k)


Number Number Number Number Total Efficency
of of plots of of number 1 2
Treatments per block replicates blocks of plots factor
(t) (k) (r) (J ( i)

5 2 4 10 20 0.62
3 6 10 30 0.83
6 2 5 15 30. 0.60
3 5 10 30 0.80
4 10 15 60 0.90
7 2 6 21 42 0.58
3 3 7 21 0.78
4 4 7 28 0.88
9 2 8 36 72 0.56
4 8 18 72 0.84
5 10 18 90 0.90
6 8 12 72 0.94
11 2 10 55 :110 0.55
5 5 11 55 0.88
6 6 11 66 0.92



1Total number of plots (t x r) (k x b).

2The efficiency factor (E) is a lower limit to the efficiency
relative to a randomised complete block (RCB) design. This
assumes that a RCB design could have been used instead of a
balanced incomplete block design. Usually this is not so: the
incomplete block design is chosen because a RCB design cannot
be used. The "true efficiency therefore is greater than 1.00.













In Figs. 5 and 6 it will be noted that blocks are arranged in groups
of replications. This arrangement does not apply to all incomplete block
designs. Where the designs permits simple replication, the analysis of
variance and allocation of degrees of freedom is as follows:


Replications (r 1)
Treatments (unadjusted) (t 1)
blocks within replications (adjusted) (b r)
Intro-block error (tr t b +1)
Total (tr 1)

An adjusted treatment sum of squares can be calculated and used for a
significance test of treatment effects.

Where designs are arranged in groups of replications, the analysis
of variance is as follows (where c the number of groups, which is two in
Fig. 5 and three in Fig. 6).



Groups of replications (c 1)
Treatments (unadjusted) (t 1)
Blocks within groups (adjusted) (b c)
Intra-block error (tr t b +1)
Total (tr 1)


Some balanced incomplete block designs cannot be arranged in
replications or groups of replications, so that these terms disappear
from the analysis of variance. Note that the analysis requires the
computation of adjusted sums of squares and means, and is consequently
much more complex than for randomised complete block designs.

Recent developments in biometrics, computing and experimental designs,
have resulted in greater flexibility of design and analysis, so that
there can be much more flexibility in block size and in replication.

Another group of incomplete block designs are those with supplemented
balance. In this group one or more control treatments occur in every
block with different subsets of the other treatments. Fig. 7 gives
examples for different numbers of treatments (t) and different block sizes (k)
with either one or two control treatments per block. Such designs are
useful where increased replication of a control treatment (or of more than one)
is desirable. The occurence of the control treatment in every block also
has considerable demonstration value. Table 3 gives further examples
for different values of t and k, and of c, the number of control treatments.













The examples of Fig. 7 and Table 3, are based on the full array
of possible treatment sets per block. If t = 7, k 5 and c 2, for
example, sets of three treatments must be chosen from the five non-
control treatments for each block, since two plots per block are
already assigned to the control treatments (a and b ). The number of
combinations of three from five, which equals the number of blocks
(b) is given by -

b 5 x 4 x 3 10.
3x2x1
This design is shown in Fig. 7E. For

t 8, k 4 and c 2, then

b 6x5 15
2x1
Fig. 7 Incomplete block designs with supplemented balance. Five examples
are shown for different numbers of treatments (t) and numbers of plots per
block (k), with either one or two control treatments (c) per block. Each
design is a complete set.


A. t 4, k 3, c 1

(1) a b c



(2) a b d




(3) a c d


Replication: a 3- b, c d = 2


B. t -5., k 3, c 1

(1) a b E (4) 1a c d



(2) a b d (5) a c e




(3) a b e (6) a d e


Replication: a a 6; c,d,e 3














C. t 6: k 3, c = 1


(1) b c (6) a c e




(2) a b L (7) a c f



(3) a b e (8) a d




(4) a b f (9) a d f



(5) a c d (10) a a f


Replication: a10;
b,c,d,e,f 4


D. t 6, k 4, c 2



(1) a b c d




(2) a b c e



(3) a b c f




(4) a b d



(5) a b d f



(6) b e f


Replication: a, b = 6
cd,e,f 3















E. t 7, k 5, c 2




(1) a b c d e (6) a b c f g




(2) a b c d f (7) a b d e f





(3) a b c d g(8) a b d a g





(4) a b c e f (9) a b d f g









Replication: a,b 10 c, d, e, f, g 6.


Note: Treatments are not randomised within blocks.













Table 3. Examples of incomplete block designs with supplemented balance
for different numbers of treatments (t) and numbers of plots per block (k).



Number
Number Number of Total Replications
of of plots control Number number of
Treatments per block treatments of blocks of plots controls) others
(t) (k) (c) (b)

4* 3 1 3 9 3 2
4 3 2 2 6 2 1
5* 3 1 6 18 6 3
5 4 1 4 16 4 3
5 3 2 3 9 3 1
5 4 2 3 12 3 2
6* 3 1 10 30 10 4
6 4 1 10 40 10 6
6 3 2 4 12 4 1
6* 4 2 6 24 6 3
6 5 1 5 25 5 4
6 5 2 4 20 4 3
7 3 1 15 45 15 5
7 4 1 20 80 20 10
7 5 1 15 75 15 10
7 4 2 10 40 10 4
7* 5 2 10 50 10 6


1Number of blocks for the complete array


of possible treatment combinations.


2Total number of plots (k x b)

3Replication of controls b, since the control treatments) occur in
every block. Those designs marked with an asterick are illustrated
in Fig. 7.
















For some design arrays, replication may be excessive, and a subset
may provide adequate replication. The subset should be balanced with equal
replication of the non-control treatment. For example, blocks (1), (3)
(5), (9) and (10) of Fig. 7C would give a balanced design, with
five replicates of treatment (a) and two of (b) (f). If replication is
inadequate, as in the examples in Fig. 7 A and B, double or treble arrays
could be used, or, where feasible, one-and-one-half arrays.

Supplemented balanced designs can accommodate double replication
of one control treatment in each block. (e.g. a, a, b, c, d; a, a, c, d, e, etc)
To be avoided is a .disconnected design. (Fig. 8 A). The design of
Fig. 8 B is analysable but unsatisfactory in other ways. Note the
overlapping of treatments.

Recent developments in biometrics, computing and experimental design
have resulted in much greater flexibility of design and analysis so
that there can be much more flexibility in block size and in replication.
Unequal replication is further discussed in 2.7.

Analysis of many of the incomplete block designs discussed is
not simple. Some such analyses can be done on hand calculators, but
large experiments with complex designs require computer analysis. The
availability of suitable programmes should be considered in selecting
a design. A general method of analysis is given in the Appendix.
















Fig. 8. Two further incomplete block designs. A is disconnected
with no overlap of treatments, and should never be used. B has an
overlap of treatments but should be avoided.


A. t=6; k 3; c o



(1) Fa b


B. t 6 'k 4 c o



(1) a b c d





(2) a b e f




(3) c d e f


Replication: 2


Replication: 2












2.4 Factorial Experiments

Factorial designs are well known, particularly for fertilizer
experiments. In such designs the effects of two or more factor 2are
investigated simultaneously. The simplest case is a 7 x 2 or 2
factorial, comq.aring two factors each at two levels, one of which
might be nil.

This clearly gives four treatment combinations. If there
are three factors, each at two levels, there3are eight treatment
combinations, and this is a 2 x 2 x 2 or 2 factorial. There can
be any number of factors, but clearly, even with only two levels, 6
the number of treatment combinations becomes large. For instance a 2
has 64 treatment combinations. The number of levels can also vary,
so that one might have a 3 3 or 3 factorial, with
respectively 9, 27 and 81 treatment combinations. Additionally, the
design includes experiments in which the factors vary in the number
of levels compared. Thus one can have a 2 x 3, a 2 x 2 x 4 or a
2 x 3 x 4 factorial, with respectively 6, 16 and 24 treatment combinations.

Factorial designs estimate3both main effects and interaction
effects. For instance in a 2 factorial the main effects of the
three factors A, B and C are estimated, plus the effects of the first-
order interactions AB, AC and BC, and of the second-order inter-
action ABC. Two factors are said to interact when the effect of
one is dependent on the presence or absence (or level) of a second.
In example (1) below A and B do not interact: the effects of both A
and B are independent of the presence of the other. In (2), however,
A and B do interact: the average effect of A is nil, but A gives a
lower value in the absence of B (i.e. 8 vs. 18), but a much higher value
in the presence of B (i.e. 24 vs. 14). Similarly B gives a lower
value in the absence of A, but a higher value in its presence.

(1) (2)


Three (or more) factors can interact. For instance, factor B may
only increase yields in the presence of A and C.

The analysis3of variance, and apportionment of degrees of freedom
(d.f) for a 2 factorial is as3follows, assuming a RCB arrangement
of plots (i.e. complete blocks of 2 8 plots) and four blocks or
replicates.).


-A +A

- B 8 18 13

+ B 14 24 19

11 21
_______ _______&______


-A +A

- B 18 8 13

+ B 14 24 19

16 16
I ,__ ,


















Blocks

Main Effects





Interactions


BC

ABC


1

1

1


1

1

21

31

I


Total


It should be noted that, with only two levels of each factor, there
is a single degree of freedom (d.f) for each treatment effect.
Generalizing to a 2 factorial (i.e. n factors each at two levels),
the analysis becomes, again assuming an RCB arrangement:


Blocks (b 1)
Main effects n
Interactions (2n n )
Error (2 l)(b 1)
Total (2zb 1)


------ ------------ -- --- -- --

















With more than two levels, the analysis of variance changes.
For a 3 factorial three factors each at three levels with 27 treatment
combinations the analysis is as follows, (again assuming an RCB
arrangement):


Blocks


(b 1)


Main Effects


2


Interactions


Error

Total


4

4

4

8

(33 1) (b 1)

33b -. 1


A refinement of this analysis


is to test for linearity of the main


effects. Details of this latter type of analysis, and of more

complex factorials of the 2 x 3 x 4 type, will not be given here.


____











2.5 Confounding

Factorials tend2to have large numbersof treatments:
the smallest is a 2 and if three factors or three levels
are to be tested, treatment number rapidly become large.
Imagine attempting to find 16, 27 or 32 plots per farm3so as5
to lay down one complete block of respectively,a 2 3 or. 2
factorial! The problem is multiplied if it is wished to replicate
the experiment over five or ten farms! One way of reducing
block size in factorials is the technique of confounding.

This3technique can be illustrated by taking the simple
case of a 2 factorial. The eight treatment combinations can
be split into two sets of four, so that an experiment with
three replicates would be laid down in six blocks each of
four plots. Figs. 9 and 10 give examples of such designs, and
the derivation of the subsets of treatments is shown in Table 4.
The latter shows the treatment combinations that contribute
to the estimation of main and interaction effects: a priori
the effect of A is the total of all treatmentscontaining
less the total of those from which a is absent and so on,
Interaction effects are derived by "multiplying" the A and B
lines, the A and C lines and so on. If the effect of ABC is
considered likely to be small and this is often so the
ABC interaction can be completely confounded with blocks
by taking, as subsets of the eight treatment combinations,
those with a plus sign (+) and those with a minus sign (-)
in the ABC line of T.-1e 2, and allocating these to separate
blocks, as in Fig. 9. The analysis. of variance

Fi. 9. A Z3 factorial experiment, arranged in blocks of
four plots, with ABC completely confounded with blocks.

Re. I Rep. II Rep. III


b ab abc (1) a be


a (1) a be c ab

abc ac c ab abc ac

c b b ac b (1)










3
Fig. 10. A 2 Factorial experiment, arranged in blocks of
four plots, with AC, BC and ABC partially confounded.


Rep. I


a ac


-*- *(1)


abc be


b ab


ABC
confounded


(1)


ac


b


abc


II


c


ab


be


a


AC
confounded


Rep.


abc


a





be


III


ac


b


c


ab


BC
confounded


TAble 4. Main and interaction factorial effects in terms of
individual treatment combinations.


*(1) conc-iti:onally represents the combination of a, b, and c
all at the lowest, nil or absence level.
Note that in analysis of variance, the sum of squares for the
main effect of A can be computed directly, from the totals, as
S.S.A = (a + ab + ac + abc (1) b c be)2
2nr
Similarly for B, C, .nd the interaction effects. The sum
of squares for the effect of ABC,for example, would be given by
S.S. ABC (a + b + C + abc (1) ab ac -bc)
2nr












now becomes:


Blocks 5
Main Effects A 1
B 1
C 1
Interactions AB 1
AC 1
BC 1
Error 12
Total 23



Note that no test of the effect of the ABC interaction effect


can be made.


The S.S. for ABC has been pooled with the blocks


S.S. Loss of information on ABC is the price paid for the
convenience of having smaller blocks.

Fig. 10 illustrates partial confounding: one replicate has
ABC confounded, another AC and the third BC. The make-up
of subsets derives, as explained above, from Table 4. The
analysis of variance now allows a test of all interactions,
but the tests for AC, BC and ABC are each based on two
replicates only. (For ABC on replicates II and III, for AC
on I and III add for BC on I and II).


Blocks 5
Main Effects A 1
B 1
C 1
Interaction AB 1
effects
AC 1')Based on
BC 1')only two
)replicates.
ABC 1')
Error 11
Total 23











Additional replication could be included in the experiment,
with the degrees of freedom for blocks, error and total increasing
from those shown in the example above, and with greater precision
accorded to the tests of the partially confounded interaction
effects.

A 2 factorial, which has 16 treatment combinations, can be
grouped into balanced sets of eight or four. In the latter
instance four blocks of four plots are needed for one complete
replicate. Several interactions must be confounded, but if the
experiment is large enough -.with sufficient blocks partial
confounding can be used so that the4effects of all interactions
can be estimated. For example, a 2 factorial with six replicates
(24 blocks each of four plots) can be partially confounded with
first-order interactions (AB, AC, AD, BC, BD, CD), confounded in
one replicate each, and second-order interactions (ABC, ABD,
ACD, BCD) each confounded in three replicates.

As the size of the (confounded) factorial6increases,
so the need for replication decreases. A 2 factorial,
which has 64 treatment combinations, can be laid dowv in-eight
blocks of eight plots, with no replication. Several of the
higher order interactions would be confounded with blocks.
The analysis of variance would be:



Blocks 7 .;
Main Effects 6
First-order Interactions. 5' 1
Second-order interactions 20O
Third-order interactions 15
Total 63 '

The d.f. and S.S. for the second and third order interactions
would be pooled and used as the "error" to test the significance
of the main effects and first-order interactions. Such an
experiment could be laid out over eight ferse but plot selection
for blocking would require special care.
n
Although attention has been focused on 2 -designs,
confounding: can also be used for 3n factorials, using blocks of
nine plots, and for 2 x 3 x 4 type-designs,, using blocks of
12 plots and so on.











2.6 FractJional Replication

In a single replication .of a 2 factorial, each5main effect
is averaged over 32 treatment combinations, and in a 2 factorial
over 16 treatment combinations. Such precision of estimation
may be.totally unnecessary. Lest it be thought unlikely that
a large factoria'1could be useful and relevant in on-farm research,
consider the'follovwig:two hypothetical experiments both 25
factorials which the five factors listed are compared each
at two lev.es (presence or absence):


Minimum tillage
experiment .
cultivation
Labicide
Mulch
Soil insecticide
Fertilizer


Micro-nutrient foliar
spray experiment
Cu
Fe
Mn
Mo
Zn


It would be difficult if not impossible to lay down such factorial
experiments on-farm as complete blocks (of 32 plots). Blocks of
eight might be feasible for a confounded design, but the question
remains: is it necessary to average main effects over 16 treatments
and plots? One answer is fractional replication.


Fig. 11.


A half-replicate of a 25 factorial in four blocks
of four plots. ABCDE is the defining contrast
and:the first-order interactions CD, CE and DE
are.confounded with blocks.


(1)

(1)


ab

acde


b de


(2)

ac


be


ade

abde


(3)

ae


be


cd

abcd


Note that treatments are not randomised within blocks.
















Fractional replication enables five factors or four or six -
to be tested in an experiment of practical size. Only a subset
of the full factorial array of treatment combinations is used, with
no replication of these combinations. An example of a half -
replicate of a 2 factorial, in blocks of fur plots, is shown in
Fig. 11. Some first order interactions are confounded with
blocks, and the analysis of variance is as follows:


Blocks 3
Main Effects 5
First-order interactions 7
Total 15


The interaction line is used as the error line for tests of
significance of main effects.

To examine the derivation of the subset of treatment
combinations used, it is convenient to consider a 23 factorial.
Table 4 shows the 8 treatment combinations. Using the ABC
interaction as the cc trast to split the factorial into two
halves, a, b, c and abc would form one subset and (1), ab, ac
and be the other. ABC is know as the defining contrast.
In larger factorials, where a quarter or even one-eighth replicate
is taken, there will be several defining contrasts.

Experiments with fractional replication are open to
interpretation, or misinterpretation, in a way that does not
occur with replicated designs. Table 5 shows the individual
treatment combinations that contribute to the estimatinn3of the
main and interaction effects for the two subsets of a 2
factorial. Looking at subset 1, it is clear that the quantity
used to estimate the effect of AB (i.e. (abc) + (c) (a) (b) )
is the same as that used to estimate the effect of C. C and AB
are know as aliases, and are written as C = AB. The Table
further shows that A BC and B AC. Note that ABC cannot
be estimated at all. The effect of using fractional replication
then is to lose the effect of ABC entirely and to confuse main effects
each with a first-order interaction. If a different defining
contrast had been used, a different set of aliases would be found.

Aliases pose problems of interpretation: is the apparent
effect of A due wholly to A, or to the BC interaction, or
to a mixture of the two? If the researcher knows that the
interaction of B and C is negligible, then the observed effect
of A can be attributed to A. But if there is a positive
interaction of B and C, then the effect of A will be over-
estimated.















Subset 2 shows another sort of alias: the effect of A
is equal to the BC interaction, with the siguc charned.
That is:
A (ab) + (ac) (be) (1), and
BC .(ab) -(ac) (be) + (1), and the alias is now written
as A BC.
If B and C positively interact, this wil! tend to make the effect
of A apparently smaller than its true effect.


Table 5. The two su sets of treatucnts combination for a
half replicate of a 2 factorial, ;with ABC an the d-Zining
contrast, and the main and interaction effects in terms of
the treatment combinations.


The choice of a fractional factoriel design clearly requires
some prior information on expected main effects and interaction
effects. Since the sum of squares for the interaction effects
is used as the error sum of squares it is important to be fairly
sure that interactions are small or absent.

In a half-replicate of a 25 factorial, with defining
contrast ABCDE, each main effect has a ihird order interaction
as alias, and each first-order interaction has a second-order
interaction as alias The analysis of variance of a half-re
replicate of a 2 factoriall ith four blocks of four plots
(Fig. 9) is (as before):





















Blocks 3
Main Effects 5
First order interactions 7
Total 15


I Note that seven of the ten first-order interactions can be
estimated: three are confounded with blocks.

If now two blocks of eight plots were used, confounding one
first-order interaction, the analysis becomes:


Finally, if there was one block of 16 plots, all first-order
interactions could be estimated with a total of 10 degrees of
freedom, and there would be no block effect.

Fractional replication assumes a single part-replication.
However, it may be useful and sensible to select a subset of
factorial treatment combinations and to replicate these on
several forms. For example, if A, B and C are, respectively,
pruning, fungicide application and fertilizer application to
cocoa, it might be useful and economical of effort to test
the subset a, b, c and abc only (excluding (1), ab, ac and bc).
This makes sense if the primary objective of the experiment
is to see if and to demonstrate that the abc combination
is more effective than a, b or c alone. With b blocks
(or farms) of four plots, the analysis of variance would be:


Blocks
Treatments
Error
Total


(b 1)
3
(3 (b -1))
(4b 1)


Blocks 1
Main Effects 5
First Order interactions 9
Total 15












31

The 3 d.f. could be divided into single d.f. for main effects,
but because of the aliases (A -BC, B AC and C- AB) it would
be preferable to test for significance among the four treat-
ments (with 3 d.f.). Care would be necessary in interpretation
of the results.

A subset of eight treatment combinations from a 2
factorial could also b.e tested on a number of farms, in blocks
of four plots, with one block per farm. The two sets of four
treatment combinations might be b, c, ad and abed
and a, bd, cd and abc. There would be several aliases, so
that a prior knowledge of the more important interactions would
be necessary in selecting the subset, in order to avoid problems
of interpretation.













2.7 Unequal Replication

All the designs discussed above have had equal replication
of all treatments there are circumstances however where it
may be useful to adopt unequal replication. It may be desirable
to increase replication of the "nil' control treatment in a
crop protection experiment for example, so as to obtain a more
accurate base against which to measure the performance of the
treatments. Or it may be desirable to examine, on a limited
number of farms, the effect of "probe" treatments higher levels
of fertilizer for instance in order to obtain an indication
of the response curve.

In the former case it is usual to include two "nil' control
plots in each block (and there is no reason why there should
not be three or more control plots except that this unduly
increases block size). This situation with one treatment
uniformly replicated more than once in each block is easy to
analyse. An example will help; assume a RCB experiment
with four treatments (a -, d), and one block per farm, on 17 farms.
Without extra replication of any treatment, the apportionment
of d.f. is straightforward.



Blocks 16
Treatments 3
Error 48
Total 67


With double replication of the control treatment (say,.a), blocks
now comprise 5 plots (with treatments a,a,b,c, d,), so that the
experiment comprises 85 plots (17 x 5). Thirty-four of these
would receive the control treatment d. The d.f. are nowl



Blocks 16
Treatments 3
Error 65
Total 84

Note that the error d.f. are increased by 17. The treatment
sum of squares (S.S.T) can be divided into two components :
'control versus the others (i.e. 'A. vs. C. and D) with
1 d.f. and "within others'" (i.e. A vs B, C and D) with 2 d.f.















Computation of the treatment S.S. differs.
double replication, the formula is:


2
+ Tb
b


+ T
c


Without the


2
+ T
d


G2
68


where T T T and T are respectively the totals for treatments a to d,
and G i8 th grand total. With double replication of treatment a the
computation of treatment S.S. is:


2 2 2
T2 + T2 + Td2
b c C
S.S. *
T ..


2
+ a
34


The block S.S., total S.S. and error S.S. are derived in the usual way.

The case of an experiment with limited replication of a "probe"
treatment is more difficult to analyse. Again an example will help. Assume
14 farms with one block per farm. All farms have the four treatments
(a d), but six have the extra "probe" treatment (e). Block size
therefore varies: eight blocks or farms have four plots and six have
five plots, giving a total of 62 plots. Two separate analyses could be
done, firstly analysing the data from treatments a d in all 14 blocks,
and secondly analysing the data from treatments a e from the six blocks
with the five treatments.

Alternatively a single analysis can be done, computing treatment
S.S. from:


+
+ T
b


1 -
+ T2
c


T2
+ *d


T2
e
+


and block S.S. from:


S.S.B


2 2
- +B B2


+ B3 +;. B8


2 2 2
Bg + B10 +...B
+


where B1 to B8 are the block totals for the eight blocks with four treatments,
and B9 to B14 are the block totals for the six blocks with five treatments,
the apportionment of d.f. in the analysis of variance is as follows:
















Blocho T


Erzror4
Total 61


It is of course pcrsible to pn-titc- the t*aMsat S.S. 1r. the above
analysis Into t113
would of course vat-, ,3?r~nc:tw:, on a:W n n ibe: c-* 7'i':M co:zt:C-1.uti.g
to the troa2tri~s:n3 tot.-ac.

Thelrc is also t h fere blaoc!;s 2 e :tal ~1ot n':m0Ct
cannot be found, wCnhour: c~prcn.si-. ur unIj.1o0.ty ttZhin blocks. One
option would be to tnh-e th,;, ctalle::il aumb'r r;f plC:E per block (Ic) that
can be acco-r-odatcd P.nd uce an inccrp!p.htc block. *InrLZVn bt,-ed on this number.
For instance, suppose tha rnuii&cr of tr-4et3 is U~ve, but ol the twelve
farmers killing to ccl bo~ae a only thr:2e c:.a comaoda.te bloClZs of fit.e
plots, Sup!)oje that r' 1x farmers ccn Occvr z':e Uc cks o u ~otr pl.ots, and
thr-ee have .uitabil 1a7! for Llck o"ir'rc i~jtt. A 5trz~i inconpite
block design bascs ca bon lc o: tb-rcB plct, -oul.c! be r Talb.- 2
gives a suitable doert4-. t?:W7) .;! Ur. tca 7) ) t-. m
with each treatment rriiitcd s In: fLes. 3 -' 4 i t.j use blocite
of diffeCf-nt 1zec. a~e -C.r~gj 1Ao~it be 7 es ,- O giave more-
or-:ess equal replication of- 1l tri-etrtrs !. T~cosible deoig! is shon
in Fig. 12. The a:!C.jz7s 1-110 I : t'1 'ifercilcas =_ 5lclc'
size, and rust also cdjrsj tsrt tcn=r3 O:

If it is oz.24ersd to 1 r_:ro. t -nt in evey
block a desi,a si-I1 a 7rg,. !3 couiA b- tic-ed. V-io -is iJ -.4 --.comrets
block design wctth cub;le ~'. 2 bal~nc ~ C:Ai blocir of -.o': siZes.
Addition of f1rt'rVr bloc!- wB1d chrn,7 2tI:K;aicr ~ ne z a, ba cd
array was addz-d 2" ox 2 .2 'Pig. 7-

Anal7s 1.3 of Ic.zs With t'nz.'ei% b3.7k -c unae'jna ralcatiorn
is not sirnmic. A gere::l met%r-d is. -.7nih: rt-lw t 1-: ix~. If there
are cc;icra &: bs u:-yna, ,' ,-od bi -,.:S:L1C 1,1 Ch
the avair.l"I1bl cC i P s *'.'x Ct*> '~2!2eC.


















A design with block of different sizes, so that some
blocks are incomplete. There are five treatments
(a e), with block sizes (k) of five, four and
three plots.


k = 5 and 3


(6)


(7)


b c d e






a b c e


a


c


a b c


d


d


e


d


e


(8) a b e






(9) a c d






(10) c d a


Replication:


Fig. 12.


a


t 5,


d e


c


(1)






(2)


a


d


e


(3)






(4)






(5)1





--


i Ii





a e = 8
















Fig. 13 An incomplete block design with supplemented balance and
blocks of different sizes. The number of treatments (t)
is six (a f), block size is five, four and three plots,
and one control treatment occurs in all blocks.

t 6, k 5, 4 or 3, c = 1


a b c d e





a c d a f




a c d f





a b d e





a b c f





a b e f


(7) a d e





(8) a b f




( 9) a b c





(10) a e f





(11) a c d


Replication a 11, b e 6


(1)





(2)



(3)
(3)





(4)





(5)





(6)


















2.8 One or More Blocks per Farm?

Where a field experiment is laid down on a uniform area of land,
nothing is gained by using a randomized complete block design instead of a
completely randomised design. On, oucn an area there are no grounds for
blocking: plots do not differ in some characteristic that enables them to
be allocated to blocks of similar plots. The analysis of variance will
show very small and non-significant block effects. In the absence of
any adequate grounds for blocking, superimposition of a RCB design may
result in inappropriate blocking, resulting in a higher error mean square
than would (ssult from using a completely randomised design, or an
appropriately blocked RCB design. A large and significant block effect
in an analysis of variance of a field station experiment is an indication
that the blocking was appropriate.

In on-farm research, farms are likely to be selected for a certain
homogeneity of environment, cropping system and management. However, it is
almost inevitable that, with blocks of different farms, large and statistically
significant difference between blocks will be found in the analyses of
variance. If there is one block per farm, so that block effects in the
analyses of variance are farm effects, and if treatments and farms interact,
then the error sum of squares will be large. This is because the error
S.S. is in fact the block (or farm) X treatment S.S.















Table 6. Plot values (hypothetical) for a RCB experiment with four
treatments (a-d) and ten blocks, considered both as an experiment with
one block per farm, and with two blocks per farm.



Treatments Totals
Farms Block # a b c d Blocks Farms


A 1 10 11 15 20 56 111
2 9 9 16 22 55

B 3 12 10 5 7 34 64
4 10 11 4 5 30

C 5 11 12 20 23 66 128
6 9 9 23 21 62


D 7 8 10 8 .3 29 57
8 7 11 6 4 28

9 9 11 10 8 38 74
E 10 7 10 9 10 36
434


Farm X Treatment Totals


A 19 19 31 42 111
B 22 21 9 12 64
C 20 21 43 44 128
D 15 21 14 7 57
E 16 21 19 18 74

Treatment Totals 92 103 116 123 434














































. p P


1 2 3


4 5 6 7
BLOCK


Graph of plot values for the four treatments of Table 6
against blocks, to illustrate variabilitY and interactions.


Fig. 14


PLOT


VALUE


alBd


8 9 10



















An example will illustrate this: the data are given in Table 6,
and have been plotted in Fig. 14. It is clear that treatments c and d give higher
values in blocks 3 and 4. There are only small differences between the four treat-
ments in blocks 9 and 10. The data may also be looked at in another way:
treatments a and b are less variable among blocks than c or d. Assuming one
block per farm, so that there are ten farms involved, the analysis of variance
is:



Source of variation S.S. d.f. M.S. F.

Blocks ( Farms) 486.6 9 54.07 2.70
Treatments 56.9 3 18.97 0.94
Error 539.6 27 19.99
Total 1083.1 39

M.S. is the mean square (i.e. the S.S. divided by the corresponding d.f.), and
F is the variance ration, (i.e. the M.S.s fivided by the H.S. for error.).
F. is used to test for significance by comparison with tabulated values.

Neither the effects of blocks large as it is nor that of treatments,
are significant. If the experiment had been laid down on five farms with
two blocks per farm (blocks 1 and 2 on Farm A, 3 and 4 on B and so on), the effect
of the farm X treatment interaction could be tested: the error S.S., in the
above analysis is now partitioned into an interaction and an error component.
The analysis is as follows:



Source of variation S.S. d.f. M.S. F.

Farms 481.9 4 120.48 128.17***
Block-within-farms 4.7 5 0.94
Treatments 56.9 3 18.96 9.92***
S Farms X Treatments 510.4 12 42.53 21.81***
Error 29.2 15 1.95
Total 1083.1 39
















Thi3a cf.ect cf farrm is tested against the "blocks-within-farms" M.S.,
.? t". i. value is highly significant. Treatment, and farms X treatment
effects are also highly significant. The co-efficient of.variation (CV),
-Thich is the square root of the error M.S. divided by the overall mean
and multiplied by 100, is 41.2% for the first analysis and 12.9% in the
second analysis. Note that the error S.S. and d.f. of the first
analysis are indeed partitioned into two components (ie 539.6 510.4 + 29.2
and- 27 = 12 + .15) Note also that the "blocks-within-farms" S.S. is
derived fro-.th. blocks C.S. less the farms S.S.

Frc:n- a ;actic.l .vie-.oint, farm X treatment interactions can.arise .,
because farms a'ea not a's hotmoeneous as originally thought, or because
some treat=mnto are not properly applied or are not applied uniformly over
farms. Faras n.y be homogeneous in ters of soil, rainfall and major
productcioi systc=r brt may be heterogeneous in terms of cultivars and
an at least score cultural practices. It follows that where homogeneity is
in doubt, t-o 31loc'Is (or mora)per farm are "safer" than one.

Iowe'. er, e7vn if an experiment with one block per farm had been done,
with results such as those of Table 6 showing no significant effect of
t-~-atmnts, ,:he experiment should.not be regarded as a loss. Useful .
infortm.ntion can be gathered frcm the data by asking, inter-alia, the
follow-ing questions:

Thy do farms differ so markedly in total or mean values?
17- do certain treatments perform well only on some farms?
ahy are some treatments more variable among blocks or
,f'J*L-r: th'.n others? '

Concomitant obser-vations will assist in answering some of these questions.
..ihly vri.abl. '-r.'r.;t; may b( agronomically unsound. or require an
unreaiiistically h.-gh level of management: they should probably not be
recoma.r.dcd as pr.ctipes to farmers, at least not without further research.
(for the data .. "bli 6q. the standard errors of the means of the four
treatments are rcppectively 1.54, 1.10, 6...22 and 77.7 which quantifies the
311serve. ;w't-Lly.).

Th, e::Fp~ri.L-.nt vlith t-;o blocks per farm does not in itself answer any of the
above cuestior.-:. In fact it poses the same questions. It does provide estimates
of I th i'-i..- o: the interacti.on however. In less extreme cases than
that illustr----d the error S.S. might still be large (because the farm X treat-
meat effect w..c relativ-ely sail s o that its S.S. was small), in which case the
vari-ation bet'ean blocks within farms would be relatively large.














2.9 Partitioning of the Error S.S.

In many experiments, the treatment S.S. can be partitioned into
components as in the factorial designs already discussed where main
effects and interaction effects may each have a single d.f.. The
error S.S. can also be partitioned, though this is seldom done. It is
useful where variability is found in treatment effects as in the
illustration above. The computations are not discussed here, but it
should be borne in mind that the technique exists and may be required
in order to carry out valid t-tests, where treatments differ sufficiently
in variability such that errors are not homogeneous.





2.10 Comparison of Zones

One final "arrangement" of blocks should be mentioned. Where it
is desired to compare a set of treatments over a wide area possibly island-wide -
thus spanning several agro-ecological zones or several recommendation domains,
there are two options. The first is to carry out separate experiments
in each zone (with separate analyses of variance). The second is to
carry out one large experiment with "zones" as a component in a single
hierachical analysis of variance. If the number of farms that can be
supervised is limited the second option is preferable, since the size of
the separate experiments may be too small to give precise estimates of
effects.

The, allocation of degrees of freedom in the analysis of variance
is shown below, assuming for simplicity, one complete block per farm and the
same number of blocks (or farms) in each zone (z = number of zones):



Zones (z 1) 4
Blocks-within-zones (b -)-(z-l) 10
Treatments (t -1) 2
Zones X treatments (z 1)(t 1) 8
Error (t 1) ((b-l)-(z-l)) 20
Total (bt 1) 44

The right hand column gives the d.f. for an experiment where z 5
b 15 (with three blocks per zone) and t=3. The "blocks-within-zones" S.S.
would be calculated as the difference between the blocks S.S. and the zones S.S.
The "blocks-within-zones" mean square would be used to test the effect.
of zones. Separate analysis of five experiments (one per zone:"option one")
would give the following analysis and d.f. allocation for each experiment:














2.9 Partitioning of the Error S.S.

In many experiments, the treatment S.S. can be partitioned into
components as in the factorial designs already discussed where main
effects and interaction effects may each have a single d.f.. The
error S.S. can also be partitioned, though this is seldom done. It is
useful where variability is found in treatment effects as in the
illustration above. The computations are not discussed here, but it
should be borne in mind that the technique exists and may be required
in order to carry out valid t-tests, where treatments differ sufficiently
in variability such that errors are not homogeneous.





2.10 Comparison of Zones

One final "arrangement" of blocks should be mentioned. Where it
is desired to compare a set of treatments over a wide area possibly island-wide -
thus spanning several agro-ecological zones or several recommendation domains,
there are two options. The first is to carry out separate experiments
in each zone (with separate analyses of variance). The second is to
carry out one large experiment with "zones" as a component in a single
hierachical analysis of variance. If the number of farms that can be
supervised is limited the second option is preferable, since the size of
the separate experiments may be too small to give precise estimates of
effects.

The, allocation of degrees of freedom in the analysis of variance
is shown below, assuming for simplicity, one complete block per farm and the
same number of blocks (or farms) in each zone (z = number of zones):



Zones (z 1) 4
Blocks-within-zones (b -)-(z-l) 10
Treatments (t -1) 2
Zones X treatments (z 1)(t 1) 8
Error (t 1) ((b-l)-(z-l)) 20
Total (bt 1) 44

The right hand column gives the d.f. for an experiment where z 5
b 15 (with three blocks per zone) and t=3. The "blocks-within-zones" S.S.
would be calculated as the difference between the blocks S.S. and the zones S.S.
The "blocks-within-zones" mean square would be used to test the effect.
of zones. Separate analysis of five experiments (one per zone:"option one")
would give the following analysis and d.f. allocation for each experiment:



















Clearly these are too few d.f. for error to give a precise test of treatment
effects. The larger combined analysis also tests zone X treatment effects,
and information on these may well be useful in planning further experiments
zone by zone.

Should the number of farms vary from zone to zone, a larger combined
analysis is still possible, but the computation of S.S.s will be slightly
more complicated'(see 2.7).


Table 7 Plot values (hypothetical) for a hierachical RCB experiment
with three treatments ( a q) two blocks per farm and four
farms in each of three agro-ecological zones..


Zone Fara Block 1 B ock 2 Farm Totals
# o p q Total o p q Tota o p q

1 1 5 6 7 18 4 6 7 17 9 12 14 35
2 4 5 6 15 5 5 7 17 9 10 13 32 1
3 5 5 8 18 4 5 7 16 9 10 15 34
4 3 5 7 15 4 4 6 14 7 9 13 29

Zone Totals 34 41 55 130
2 5 7 9 5 21 6 10 5 21 13 19 10 42
6 8 10 4 22 7 9 3 19 15 19 7 41
7 9 9 6 24 10 11 5 26 19 20 11 50
8 7 10 7 24 8 9 9 26 15 19 16 50
Zone Totals 62 77 44 183
3 9 9 6 7 22 10 5 5 20 19 11 12 42
10 10 6 5 21 12 7 7 26 22 13 12 47
11 11. 7 7 25 10 5 6 21 21 12 13 46
12 10 5 6 21 8 6 4 18 18 11 10 39
Zone Totals ____80 47 47 174

Grand Totals 176 165 146 487


Blocks 2
Treatments 2
Error 4
Total 8
I_ _____________,,I












If there are two blocks per farm the hierachical analysis of variance has
some additional components. This can be illustrated by a numerical example
(Table 7). The experiment compares three zones, with four farms per zone,
and two complete blocks per farm. There are three treatments (o,p and q).
That is z 3, f (farms) 12, b 24 and t 3. The data have been
devised so that q gives the highest values in Zone 1, p in Zone 2 and
o in zone 3. In the analysis of variance (see below) the d.f. for
"farms-within-zones" is given by (f-l)-(z-l), and for "blocks-within-farms'
by (b-l)-(f-1). The corresponding S.S. are calculated from (farms S.S. -
zones S.S.), and (blocks S.S. farm S.S.), respectively. The "farms-within-
zones M.S."is used to test the effect of zones. The analysis of variance is:


Source of variation S.S. d.f. M.S. F


Zones 67.0 2 33.50 13.40**
Farms-within-zones 22.5 9 2.50
Blocks-within-farms 13.5 12 1.13
Treatments 19.2 2 9.60 13.71***
Zones X Treatments 168.4 4 42.10 60.14***
Farms X Treatments 22.4 22 1.02 1.46
Error 14.0 20 0.70
Total 327.0 71


There are clearly significant differences between zones, and the effects
of treatments and of zones x treatments are both highly significant.

It is worth noting that, with no hierachy and no partition into zones
and farms, the analysis would be:


Source of variation S.S. d.f. M.S. F

Blocks 103.0 23 4.48 1.01
Treatments 19.2 2 9.60 2.16
Error 204.8 46 4.45
Total 327.0 71


Neither block nor treatment effects are significant.















-As already pointed out, the analysis can accommodate different
numbers of farms per zone. It should also be evident that the analysis
of non-RCB designs where there is partition into zones, and where there is
interest in zone X treatment and farm X treatment interactions is vastly more
complicated than the analysis of RCB designs. This should not preclude or
discourage the useof such designs where they are necessary, but great care
in design and allocation of blocks would be necessary.


2.11 Summary

For on-farm experimentation, the simplest, most familiar, and
easiest to analyse design is the rendomised complete block (RCB).

If the homogeneity of farms is in doubt it is safer to
have two complete blocks per farm, rather than one, so that
any farm X treatment effect can be estimated and separated
from the error S.S.

Where the block size (i.e. the number of plots per block)
is limited by the availability of suitable uniform land
on farms it may not be possible to use complete blocks.

In such circumstances designs other than randomised complete
block designs must be used. These include balanced lattices
and balanced (and partially balanced) incomplete block designs.
The analysis of these is more complete than for randomised
complete blocks.

Where the treatments structure is factorial, confounding can
be used to reduce block size, and fractional replication of
factorials can:also be so used.

Increased replication of a control treatment, and testing
one (or more) probe treatments with fewer replications, are
ways of improving, or increasing, the information gathered.

-Where sufficient blocks of the desired size cannot be sited
on farms, blocks varying in size (i.e. in number of plots)
can be used. "Balanced" designs should be used, but the
analysis is less straightforward than for randomised complete
blocks.










46-


CHAPTER 3. :* PROBLEMS


These are discussed under eight main heads, but topics inevitably overlap.
Some of the problems,have been referred to in Chaptcr 2 with some solutions
suggested but are reiterated here for emphasis.



3.1 Physical

Small farmers in the Eastern Caribbean typically. farm marginal lands
on hillsides. Their lands are often characterized by -

Slopes, which may be steep and irregular. Any one parcel may
have areas differing in slope and in aspect.

Gullies and rocky outcrops, and differences in depth of soil.

The presence of trees, which offer uneven shading and root
interference. If trees have been felled stumps usually remain.

If a part of the land has been terraced, the terraces may' be narrow
and uneven in width, and limited in area.

The selection of a number of uniform plots on such land is not easy.
Even if the land is relatively flat, or uniform in slope, rocky outcrops
and trees may be present. A consequence is that block size may have to
be small. What must be avoided is excessive reductions in plot size,
so as to increase the number of plots, relaxation of the criteria
for blocking and selection of only those farmers with flat, ideal land,
and the exclusion of those with more difficult lands.

3.2. Biological

The complexity of many of the cropping systems practiced by small
farmers, both in time and space, also makes selection of uniform plots
difficult. Adjacent areas of land may differ widely in cropping history:
one area may have been weed allowed with an adjacent area just out of bananas
and another adjacent area may have carried a sequence of vegetables.
These areas will differ in fertility, weed flora, quantity and quality of
crop residues, cultivation history and so on.. Some areas may have been
grazed by tethered animals and so trampled and manured. There may be
no clear evidence of previous cropping so that it is difficult to
determine boundaries. This heterogeneity of history and use can lead to
intra-plot variations, as well as to inter-plot (and intra-block) variation.










46-


CHAPTER 3. :* PROBLEMS


These are discussed under eight main heads, but topics inevitably overlap.
Some of the problems,have been referred to in Chaptcr 2 with some solutions
suggested but are reiterated here for emphasis.



3.1 Physical

Small farmers in the Eastern Caribbean typically. farm marginal lands
on hillsides. Their lands are often characterized by -

Slopes, which may be steep and irregular. Any one parcel may
have areas differing in slope and in aspect.

Gullies and rocky outcrops, and differences in depth of soil.

The presence of trees, which offer uneven shading and root
interference. If trees have been felled stumps usually remain.

If a part of the land has been terraced, the terraces may' be narrow
and uneven in width, and limited in area.

The selection of a number of uniform plots on such land is not easy.
Even if the land is relatively flat, or uniform in slope, rocky outcrops
and trees may be present. A consequence is that block size may have to
be small. What must be avoided is excessive reductions in plot size,
so as to increase the number of plots, relaxation of the criteria
for blocking and selection of only those farmers with flat, ideal land,
and the exclusion of those with more difficult lands.

3.2. Biological

The complexity of many of the cropping systems practiced by small
farmers, both in time and space, also makes selection of uniform plots
difficult. Adjacent areas of land may differ widely in cropping history:
one area may have been weed allowed with an adjacent area just out of bananas
and another adjacent area may have carried a sequence of vegetables.
These areas will differ in fertility, weed flora, quantity and quality of
crop residues, cultivation history and so on.. Some areas may have been
grazed by tethered animals and so trampled and manured. There may be
no clear evidence of previous cropping so that it is difficult to
determine boundaries. This heterogeneity of history and use can lead to
intra-plot variations, as well as to inter-plot (and intra-block) variation.










46-


CHAPTER 3. :* PROBLEMS


These are discussed under eight main heads, but topics inevitably overlap.
Some of the problems,have been referred to in Chaptcr 2 with some solutions
suggested but are reiterated here for emphasis.



3.1 Physical

Small farmers in the Eastern Caribbean typically. farm marginal lands
on hillsides. Their lands are often characterized by -

Slopes, which may be steep and irregular. Any one parcel may
have areas differing in slope and in aspect.

Gullies and rocky outcrops, and differences in depth of soil.

The presence of trees, which offer uneven shading and root
interference. If trees have been felled stumps usually remain.

If a part of the land has been terraced, the terraces may' be narrow
and uneven in width, and limited in area.

The selection of a number of uniform plots on such land is not easy.
Even if the land is relatively flat, or uniform in slope, rocky outcrops
and trees may be present. A consequence is that block size may have to
be small. What must be avoided is excessive reductions in plot size,
so as to increase the number of plots, relaxation of the criteria
for blocking and selection of only those farmers with flat, ideal land,
and the exclusion of those with more difficult lands.

3.2. Biological

The complexity of many of the cropping systems practiced by small
farmers, both in time and space, also makes selection of uniform plots
difficult. Adjacent areas of land may differ widely in cropping history:
one area may have been weed allowed with an adjacent area just out of bananas
and another adjacent area may have carried a sequence of vegetables.
These areas will differ in fertility, weed flora, quantity and quality of
crop residues, cultivation history and so on.. Some areas may have been
grazed by tethered animals and so trampled and manured. There may be
no clear evidence of previous cropping so that it is difficult to
determine boundaries. This heterogeneity of history and use can lead to
intra-plot variations, as well as to inter-plot (and intra-block) variation.















3.3. Technical

There is usually no difficulty on a field station in finding areas to
accommodate rectangular or square blocks of contiguous rectangular or
square plots. Marking out is relatively straightforward: blocks can be
pegged out and divided into plots.

On farmer's lands it may be difficult to find areas of sufficient
size into which contiguous and uniformly-shaped plots can be fitted for
the reasons outlined above. Contiguity is not essential, nor is equality
of shape and size, although extreme variation should be avoided. The
criterion of uniformity of plots within blocks must not be compromised
however.

If terraces are, to be used these may curve and vary in width, and
the extent of admixture of subsoil with topsoil may vary both along
terraces and between terraces.

Application of treatments uniformly to plots differing in size and shape
and to plots that differ between blocks in slope and in the regularity
of the terrain is also a brobiem. This is particularly acute with
fertilizers and pesticides that must be applied at a specific rate per unit
area. Calibration of a sprayer on flat or regular surfaces will
underestimate the volume rate and hence the application rate applied
to plots with slopes and irregular terrain..

3.4 Farmers

The farmer is a partner in on-farm experimentation, and so must be fully
aware of the objectives of the experiment, of his responsibilities and
expected contribution vis-a-vis those of the researcher. He should also
understand the expected benefits, both short- and long-term.

Some farmer problems that may arise are:

Reluctance to apply a particular treatment or treatment component,
or to carry out certain basal operations, as and when required by the
specifications of the, experiment, because it conflicts with his way of doing
things or with his beliefs. For example, he may not believe in applying
fertilizer to yams or may not believe in..controlling weeds early.

Conflict between the farmer's commercial and domestic needs and those
of the experiment. Thus a farmer may reap only a few yam mounds at any one
time, the number of mounds being determined by how much he can sell and use
in the household. This poses problems in the collection of harvest data
from a block of four plots each of ten mounds. On-farm research is usually -
and should be preceded by a thorough study of the target farmers' practices,
but details such as harvesting procedures may be overlooked.















3.3. Technical

There is usually no difficulty on a field station in finding areas to
accommodate rectangular or square blocks of contiguous rectangular or
square plots. Marking out is relatively straightforward: blocks can be
pegged out and divided into plots.

On farmer's lands it may be difficult to find areas of sufficient
size into which contiguous and uniformly-shaped plots can be fitted for
the reasons outlined above. Contiguity is not essential, nor is equality
of shape and size, although extreme variation should be avoided. The
criterion of uniformity of plots within blocks must not be compromised
however.

If terraces are, to be used these may curve and vary in width, and
the extent of admixture of subsoil with topsoil may vary both along
terraces and between terraces.

Application of treatments uniformly to plots differing in size and shape
and to plots that differ between blocks in slope and in the regularity
of the terrain is also a brobiem. This is particularly acute with
fertilizers and pesticides that must be applied at a specific rate per unit
area. Calibration of a sprayer on flat or regular surfaces will
underestimate the volume rate and hence the application rate applied
to plots with slopes and irregular terrain..

3.4 Farmers

The farmer is a partner in on-farm experimentation, and so must be fully
aware of the objectives of the experiment, of his responsibilities and
expected contribution vis-a-vis those of the researcher. He should also
understand the expected benefits, both short- and long-term.

Some farmer problems that may arise are:

Reluctance to apply a particular treatment or treatment component,
or to carry out certain basal operations, as and when required by the
specifications of the, experiment, because it conflicts with his way of doing
things or with his beliefs. For example, he may not believe in applying
fertilizer to yams or may not believe in..controlling weeds early.

Conflict between the farmer's commercial and domestic needs and those
of the experiment. Thus a farmer may reap only a few yam mounds at any one
time, the number of mounds being determined by how much he can sell and use
in the household. This poses problems in the collection of harvest data
from a block of four plots each of ten mounds. On-farm research is usually -
and should be preceded by a thorough study of the target farmers' practices,
but details such as harvesting procedures may be overlooked.
















Premature reaping in advance of the expected date may be done as
a response to a market opportunity or to a need for cash. At worst there
may be total loss of data from one or more plots, or at best a partial loss,
as with crops that are serially reaped (e.g. tomatoes, peppers). Even the
most co-operative farmer may find it impossible to advice the researcher of his
wish to start reaping earlier.

Excessive helpfulness, when the farmer, with every good intention,
hinders the collection of data or causes a loss of data.. Examples
include the farmer who clean-weeds all the plots of a herbicide experiment
prior to the evaluation of weed control and the farmer who reaps an entire
experiment before the researcher's rrivali putting all the produce in one
large heap.

Premature adaption of the technology under test will lead to
a loss of data, encouraging as it may be. An example is the farmer who,
impressed with the logic of mulching, decides to mulch the unmulched'
plots as well.

r- Bias in favour of one particular treatment sometimes occurs or is
suspected. "The farmer may favour what he regards as "his" plot, which will
usually be one of the control treatments. This may be weeded first or more
frequently than the others. This problem may arise because the farmers
consider responsibility for the other plots to rest with the researcher.

Drop-outs can occur for several- reasons, resulting in the loss of
one or more blocks from the experiment. Farmers may-.drop-out because
they disagree with the practices required, or prefer to do things their way;
or because they consider the demands of the plots on their time and resources
excessive and unreasonable: or because they fail to see any potential
benefits from the experiment.


1*'


.f .


' I
















3.5 'Planning and Design

There are several questions to be asked and answered.

How many treatments to include in the experiment? This will depend
in part on the objectives of the experiment and on the step- in the programme.
(Fig. 1) For instance, an experiment on fertilizer rates and times of
application at Step 5 will have more treatments than an alternative system
experiment at Steps 9 or 10. Not all the treatment combinations of a factorial
array need to be tested: a subset of those with most potential may be
adequate.

How many farms, and how many blocks or replicates per farm?
This will depend on the logistics of laying-down and conducting the experiment,
and on the homogeneity of farms within the agro-ecological zone. At step 5
it may be useful to cover a wide range of zones, in order to estimate and
evaluate zone X treatment interactions. At steps 9 and 10 separate
experiments in each zone are preferable, with these experiments differing
perhaps in some details of the treatments. Where farms are expected or
suspected to be heterogeneous more than one block per farm is to be
preferred. It may be desirable to select farms with some heterogeneity at
least at Step 5 to investigate interactions.

Equal or unequal replication? In designing an on-farm experiment,
it may be useful to increase replication of one or more treatments.
These might, for example, be the farmer's practice and the basic recommended
practice, with the other treatments with less replication being variations
on the basic recommendations. In a crop protection experiment it may be
useful to have increased replication of the untreated control treatment,
so as to obtain a more precise basis against which to measure the performance
of the treatments. Or on a subset of farms, selected perhaps because they
can accommodate larger blocks, one or more "probe" treatments could be
included. Both complete and incomplete block designs to accommodate
unequal replication can be used, and appropriate methods of analysis are
available.

What control (or check) treatment (or treatments) to include?
If the control is to be g farmer practice" how uniform is it? In a yam
experiment for example, one treatment factor was "farmer bit size", but
this ranged from 11 to 64 oz, and probably contributed to the large error
S.S. in the analysis of variance.

What plot shape and size? There are no hard and fast rules. Plot:
size must be adequate to represent the crop being grown and to provide
reasonable estimates of yield, pest attack and so on. Plot shape
should not vary so much within blocks that the intre-plot environment varies.
A square plot and a long narrow plot comprising one crop row are clearly
not comparable. Guard rows are necessary in some experiments, especially














crop protection experiments: but may be unnecessary in other types of experiment,
particularly if plots are contiguous or surrounded by the crop so that edge
,effects are minimal. Plot shapes may have to differ within and between
blocks to conform with. the land areas available (Figs. 11 and 12).

How much overall replication? How many plots and blocks can be
accommodated on the selected farms? What experimental design to use? These
questions are inter-related and depend on' the antvrs to the above questions.
Some rethinking of treatment numbers maybe necessary, if block stze must
be small. Or an incomplete block design may be necessary if treatment
number cannot be reduced. Attention must also be given to the expected
heterogeneity of farms;, and possible interactions.

Clearly, planning and the' choice of the overall design must be an
interactive process.






3.6 Management

S The farmer must be clear as to his responsibilities in the management
and conduct of the experiment. Equally the researcher must be clear
as to his responsibilities. Problems that can arise, for a variety of
reasons include:

Wrongly-applied treatments. The wrong plot may be treated,
or the treatment may be applied at the wrong time, or may be applied to
all the plots 'in the block or on the farm. Some information may be.
salvageable, but the block or blocks may be totally lost depending on the
nature and extent of the error.

Non-uniform application of experimental treatments to plots. This
will lead to intra-plot variability and increase the error S.S; in the
analysis of variance. Half a plot may be weeded today and the remaining
half weeded next week, for example.

Non-uniform application of a non-varying (or basal) practice. This can
increase both intra- and inter-plot (intra-blqck) variability. For instance
a basal fertilizer application may be spread unevenly, or applied over
a period of time to different plots.














3.7 Data Collection


This is the responsibility of the researcher. Even if Extension
Officers are responsible for overseeing the experiment (as in Step 10;
see Fig. 1) the researcher must decide what data.is to be collected, how and
when. He should-prepare guidelines and proformae -to ensure, as
far as possible, uniformity of data collection and of recording.

Data collection costs time and money, so a problem to be
addressed is what (or how much) data to collect. This must be resolved
and determined at the planning stage.

The data and information to be collected is of four main types.:

Primary data: that data essential to evaluate the
experiment and achieve the objectives.

S Secondary data! that data which is desirable to assist
in interpretation of the results.

S Supporting data andplta~'fra.on the calendar or diary of
the experiment.

Farm and production'-eeten Information; information on
each participating farm that imay help in the design of
alternative systems and in technology transfer.

Examples of these different types are given below. Specific needs
will vary with the crop and the nature of the experiment. More data
and information are necessary at steps 5 and 9 than at steps 10 and 11.
Primary and secondary data must be collected plot-by-plot, but it will
usually be sufficient to record supporting data by blocks or by farms.

Primary Data! Total yields, marketable yields, numbers, sizes,
average weights, etc. In crop protection experiments primvory data includes
counts or estimates of weed numbers or cover crop damage, insect
or lesion numbers and so on.

Secondary Data! Plant numbers, heights, branching. time of flowering,
lodging, shattering, weeds and weediness, pest and disease incidence,
soil nutrient levels, soil moisture levels and so on.

Supporting Data Dates of land preparation, planting, thinning,
fertilizing, weeding, spraying, reaping and so on.

Farm and Production System.Isnfa nation: Physical data on rainfall,
soil type, slope, aspect- biological data on cropping history, other
crops grown, intercrops, major weeds, pests and diseases! socio-economic
data on farm and family size, labour resources, level of purchased inputs
and sales; and information on cultural practices used.














3.8 Missing Plots and-Blocks

Plots can be "lost' as a result of some of the problems discussed
above. No data at all or incomplete data, may be obtained from one
or more plots in'an experiment.


An entire block may also be "lost", and where there are two or
more blocks per faer., one or more entire farms may be"lost" or
provide only partial data.

Data that is suspect because of suspected misapplication or
wrong application of a treatment should be regarded as "lost .

Missing data complicates the analysis of variance, and reduces
the precision of ..significance tests.














CHAPTER 4. SOLUTIONS

There are no simple universal solutions to the problems posed above.
Researchers engaged in on-farm research mukt be pragmatists, willing and
able to develop solutions to problems as and when they arise. The following
discussion provides suggestions only as to how some problems of on-farm
experimentation can be addressed.

4.1 Physical

Thorough site inspection is essential to decide the siting of plots
and blocks. Plots within blocks must be as uniform as possible with regard
to soil type and depth, slope and so on. Some variation in plot size
within blocks can be tolerated, and certainly such variation can be allowed
between blocks and between farms. Perhaps a variation of up to 20% less
than the desired or optimal size can be tolerated. Plots need not be
contiguous and can be separated by outcrops, trees, ditches or gullies, etc.,
provided they satisfy the criteria for blocking.

If site inspection suggests that several of the selected farms
cannot accommodate complete blocks of adequately sized plots, then
three options are available'

review the array of treatments to see if the number of
treatments can be reduced, or if a subset could achieve
the objectives of the experiments'

look for.farms that can accommodate complete blocks of
the desired size;

consider an incomplete block design.


4.2 Biological

Site inspection must take cognisance of shading, cropping history,
crop and weed distribution and so on in siting plots and choosing blocks
on farms. The farmer should be consulted on his cropping patterns and
cropping history, use of fertilizer and so on, on-site.














CHAPTER 4. SOLUTIONS

There are no simple universal solutions to the problems posed above.
Researchers engaged in on-farm research mukt be pragmatists, willing and
able to develop solutions to problems as and when they arise. The following
discussion provides suggestions only as to how some problems of on-farm
experimentation can be addressed.

4.1 Physical

Thorough site inspection is essential to decide the siting of plots
and blocks. Plots within blocks must be as uniform as possible with regard
to soil type and depth, slope and so on. Some variation in plot size
within blocks can be tolerated, and certainly such variation can be allowed
between blocks and between farms. Perhaps a variation of up to 20% less
than the desired or optimal size can be tolerated. Plots need not be
contiguous and can be separated by outcrops, trees, ditches or gullies, etc.,
provided they satisfy the criteria for blocking.

If site inspection suggests that several of the selected farms
cannot accommodate complete blocks of adequately sized plots, then
three options are available'

review the array of treatments to see if the number of
treatments can be reduced, or if a subset could achieve
the objectives of the experiments'

look for.farms that can accommodate complete blocks of
the desired size;

consider an incomplete block design.


4.2 Biological

Site inspection must take cognisance of shading, cropping history,
crop and weed distribution and so on in siting plots and choosing blocks
on farms. The farmer should be consulted on his cropping patterns and
cropping history, use of fertilizer and so on, on-site.














CHAPTER 4. SOLUTIONS

There are no simple universal solutions to the problems posed above.
Researchers engaged in on-farm research mukt be pragmatists, willing and
able to develop solutions to problems as and when they arise. The following
discussion provides suggestions only as to how some problems of on-farm
experimentation can be addressed.

4.1 Physical

Thorough site inspection is essential to decide the siting of plots
and blocks. Plots within blocks must be as uniform as possible with regard
to soil type and depth, slope and so on. Some variation in plot size
within blocks can be tolerated, and certainly such variation can be allowed
between blocks and between farms. Perhaps a variation of up to 20% less
than the desired or optimal size can be tolerated. Plots need not be
contiguous and can be separated by outcrops, trees, ditches or gullies, etc.,
provided they satisfy the criteria for blocking.

If site inspection suggests that several of the selected farms
cannot accommodate complete blocks of adequately sized plots, then
three options are available'

review the array of treatments to see if the number of
treatments can be reduced, or if a subset could achieve
the objectives of the experiments'

look for.farms that can accommodate complete blocks of
the desired size;

consider an incomplete block design.


4.2 Biological

Site inspection must take cognisance of shading, cropping history,
crop and weed distribution and so on in siting plots and choosing blocks
on farms. The farmer should be consulted on his cropping patterns and
cropping history, use of fertilizer and so on, on-site.















4.3 Technical

It has already been stated that plots within blocks do not need to be
contiguous, nor exactly the same shape and size though extreme differences
must be avoided, Apart from "statistical" considerations, the data from
plots differing in area must be adjusted to a standard area before analysis
The need for guard rows should be critically examined for each experiment.
Differences in plot shape and size between blocks are preferable to
differences within blocks, but a flexible approach is necessary. Fig. 15.
shows an extreme case where plots differing in shape might have to be
used. Fig. 16 shows the simplest and ideal arrangement, but Fig. 17 is
also perfectly satisfactory.

Marking out may require some ingenuity and will entail more work
if plots are not contiguous. If plots of different shapes have to be
used, then some simple calculations of the linear dimensions necessary to
give equal areas will be necessary. A sketch map, with approximate
dimensions, will help in deciding what plot shapes and sizes can be used.
Where terraces vary in width and curvature, plots of very similar area
can be marked out fitting geometric shapes (Fig. 18). Alternatively,
the "Linear run of rows" can be used.

The problem of basal or treatment application at a specified rate to
plots of different shapes and sizes can be resolved by application to a
larger more conveniently shaped plot (Fig. 19), it space allows, or by
application on a row-by-row or plant-by-plant basis where this is possible.
Where application is by sprayer, on-site calibration is essential,
adjusting the amount of concentrate accordingly.

One obvious solution to these problems is to choose only farms with
adequate space and easy terrain. Such farms may not be representative of
all those in the domain,however.;. Additionally, it would be wrong to exclude
co-operative and enthusiastic farmers on the grounds that their land was
less than ideal. Where plots are scattered on a farm (i.e. not continuous)
proper pegging and labelling of each plot is essential.







Fig. 15


o e -o- U U )Jr^23

-woo C)
Aboe


If the only relatively homogeneous areas are non-contiguous
and differ in shape, could not these four plots constitute
a block?


An ideal situation permitting several arrangements of
contiguous plots.







Fig. 17









0)0. .4, 18
X X-//-





A situation where plots must be ncn-contiguous, but can be
standard in size and shape.
















differ but areas are approximately equal Plot size might
comprise a specified length of crop row.

comprise a specified length of crop row.
















I*1

Vii

c e .a~-R


I
3 a
3e
I


?1 ,7
IP


Cv ci:)z: of non-rectangular plots to rectangles for
sirzlicity oi applying treatments varying and non-varying,
:.;t c2 spac'- allo0was.


- I


















4.4. Farmers

Most "farmer problems" can be avoided by clearly explaining to the
farmers either on an individual basis or in a small workshop meeting -
the following:

the objectives and rationale of the experiment,

the expected long-term benefits that should result,

the experimental procedures proposed, including the
"critical" requirements,

the anticipated contribution of the farmer (e.g. land, labour
planting materials, etc.),

the inputs, material and otherwise from the researcher,

the short-term benefits to the farmers and any guarantees
against failure or loss;

the time schedule involved.

Farmer response may require modifications to the procedures. The farmers
contribution will change as the programme advances: he will make greater
inputs at step 10 than at steps 9 and 5. Extension officers should be
involved from an early stage. They can assist in farmer selection, and in
supervision of the experiments and in data collection. At step 10
extension officers are very much involved, more so than at the earlier
steps, but should be involved at every step.

Specific points that require resolution are conflicts between
farmers' practices and experimental and data collection procedures, and
the willingness and competence of the farmer and his workers to
carry out tasks which may be unfamiliar. It may be necessary for the
researcher to demonstrate and train workers in such tasks.

Regular visits by the researcher must be scheduled, to monitor
the experimental plots, to assist in unfamiliar tasks, to apply certain
treatments if this is not the farmers responsibility and to collect
data, including concomitant observations. The farmer may request advice
on other aspects of his farming system,and willingness to give such advice may
help to engender a spirit of co-operation and mutual goodwill.














4.5 Planning and Design

Some of the problems raised in 3.5 have already been addressed and
solutions suggested.

The most appropriate design will depend on the type of on-farm test.
Steps 9 and 10 may involve only two treatments but a large number of farms,
whereas a step 5 test may have many treatments and require fewer
replications. Some tests may require on-fadrm replications whereas others
will not.

There may need to be a compromise between what is statistically ideal
and what is possible given the resources available. An increase in the
number of farms, for example, must be weighed against the increased mileage,
manpower and materials required. It may also be desirable to carry out, say,
five rather than four on-farm tests, so as to service a greater number of
production systems and farmers.

One of the most important questions to be answered is the number of
replicates. 'As a general rule, less replication is needed as the number
of treatments increases. This is because there should be in the analysis
of variance a "reasonable" number of d.f. for error. Table 8 shows the
number of blocks ( number of replicates) required to give about 20 and
about 30 error d.f. in a RCB design with one block per farm. Note that
neither 20 nor 30 d.f. for error are advocated as the optimal numbers; but
they are "reasonable" numbers.

With two or more cnmpiete blocks per 'farm and a RCB design, the d.f.
are partitional so as to test farm effects and farm X treatment effects
(2.8). Table 9 shows the allocation of d.f. for different numbers of
treatments, farms and blocks. Note that with more than one block per
farm a greater total number of blocks is necessary, than with only one block
per farm. For instance, with five treatments, seven blocks are necessary,
with one block rer farm, to give 24 d.f. for error, compared with 12 blocks
with two each oi six farms. However, the increased number of blocks and
plots should not entail anything like a proportional increase in mileage
or manpower requirements. Two blocks per farm also enables farm X treatment
interactions to be evaluated. Increasing the number of blocks per
farm to three increases the number of -*..?. for- e:or (Table 9), but if
it is considered important to examine fara X treatment interaction effects,
it would be preferable to include more farms with two blocks than
ferer with three. If fa-rm are relatively homogeneous that is to say,
the farm X treatment interaction effect is expected to be negligible one
complete block per farm should suffice. But where homogeneity cannot be
assumed, or where farms are known to be heterogeneous, two blocks per farm
are preferable and a useful insurance. It has already been suggested that
exploratory experiments (as at st.p 5), it may be useful to cover several
agro-ecological zones, or in other words to seek heterogeneity among farms.
In other experiments the converse may be true.
















TABLE 8. The number of blocks required in a randomised complete block
design for different numbers of treatments, to give
approximately 20 or 30 error d.f., assuming no partition
of error.


For approximately 20 error d.f.
No. of treatments 2 3 4 5 6 7 8

No. of blocks 21 11 8 6 5 4 4
Error d.f. 20 20 21 20 20 18 21





For approximately 30 error d.f.

No. of treatments 2 3 4 5 6 7 8


No. of blocks 31 16 11 9 7 6 5

Error d.f. 30 30 30 32 30 30 28














TABLE 9. The allocation of d.f. in the analysis of variance
for different number of treatments and farms, with
two or three blocks per farm, assuming a randomised
complete block design.



No. of treatments 2 2 2 2 3 3 3
No. of farms 12 20 8 12 6 12 6
Blocks per farm 2 2 3 '3 2 2 3
Total No. of blocks 24 40 24 36 12 24 18

DEGREES OF FREEDOM I.f,)

Farms 11 19 7 11 5 11 5
Blocks -within ,
farms 12 20 16 24 6 12 12
Treatments 1 1 1 1 2 2 2
-:.. nt 11 19 7 111 10 22 10
Error 12 20 16 24 12 24 24
Total 47 79 47 71 35 71 53

No. of treatments 4 4 5 5 6 6 8
No. of farms 9 6 6 4 5 4 4
Stocks per farm 2 3 2 3 2 3 2
Total No. of Blocks 18 18 12 12 10 12 8


DEGREES OF FREEDOM (d.f.)


Farms 8 5 5 3 4 3 3
Blocks-within
farms 9 12 6 8 5 8 4
Treatments 3 3 4 4 5 5 7
Farms X Treatments 24 15 20 12 20 15 21
Error 27 36 24 32 25 40 28
Total 71 71 59 59 59 71 63















Note also that with a RCB design, as the number of d.f. for treatment
increases, so the."acceptable" d.f. for ertor decreases. For instance,
with 3 d.f. for treatment, 18 d.f. for error would be acceptable, but with d.f.
for treatment, it would be preferable to aim for 24 d.f. for error. The
two experiments would comprise 7 x 4 28 plots and 4 x 9 36 plots.
Where experience suggests that coefficients of variation are high, additional
replication (i.e. more d.f. for error) is advisable.

Experience with incomplete block designs for on-farm experimentation
is limited. With one incomplete block per farm, block totals may vary
widely, and no test for farm X treatment interaction can be made. Such a
design should be used only where necessitated by the number of treatments
and by limits to block size per farm. Farms should be reasonably
homogeneous, however. The same constraints apply to several other designs
including fractional replication of factorials, confounded factorials
and designs with varying block sizes. In fact, more than one incomplete
block, or more than one block of a confounded factorial could be located
on a single farm. Nor is it essential for all farms to have the same
number of blocks, complete or incomplete, although uniformity in block
number per farm simplifies analysis and is to be preferred.

The;choice of the control treatments) is important and requires
careful thought. There are three options :

"researcher control" which might be unrealistic in practice,
but which provides a base for comparisons. This might be no
fertilizer, complete removal of weeds, no pest control etc.,

"average farmer practice" which requires a full understanding
of farmer practice and its variations;

"individual farmer practice" that is the practice of each
farmer collaborating in the experiment.

The first of these may be necessary, but may "interfere" with
the other treatments, as in the example of no pest or disease control.
If all farmers use fertilizer; use some pest and disease control
and so on, this treatment can probably be dispensed with. The second
option is perhaps the best control treatment, since the intention of the
experiment is to improve upon farmer practice and this provides a consistent
and uniform control. The third is valuable in demonstrating to individual
farmers how his practices could be improved, and perhaps in showing the
researcher how his practices could be improved. The control treatment may be
very inconsistent between farms, however. The individual farmers' practices
must be well-documented if this treatment is to be of value.

It would, of course, be possible to include all these control treatments
in the experiment but this would increase block size. Not all need be
included in the analysis of variance however: "individual farmer practice"
might give extremely variable data. It would be important to calculate
the variances of the individual treatments in any case, since the analysis













of variance model requires variances to be broadly similar. In determining
"average farmer practice' it might be possible to separate farmers into
homogeneous groups with respect to one or more component practices and to
include this grouping in the analysis of variance (as zones or domains -
see 2.10) . -

Where the number of treatments is large, so that it-will be difficult
to find and for two complete blocks per farm, it may be desirable to reduce
the number of treatments by further. :field. station research. This will-delay
the start of on-farm experimentation, but should result in the rejection
of some,at least,of the poorer treatments If this cannot be done, then
an incomplete block or confounded factorial design may be necessary so as to
reduce block size. Such designs tend.to require greater overall
replication however, and therefore more plots, than complete block designs.













4.6 M.anagemen~

Problems of management can generally be resolved by careful
explanation to the farmer of the time schedule and of the importance
of timeliness and uniformity of treatment and basal treatment application.
Regular visits to on--farm plots are essential for proper monitoring and
correction of any departures from the intended schedule.


4.7 Data Collection

The collection, recording and storage of data must be organised
so as to avoid omissions, errors and losses. This is particularly
so where several technicians are involved, each overseeing a subset of
the farms.

Pro-foimae will facilitate accurate recording, and can serve
as reminders of the data to be collected and of observations to be
made at each farm visit. They may need to be designed so as to be compatible
with computer systems for data storage and analysis. Dates of'recording
must be noted. this is easily overlooked.

Regular observations of on-farm plots can often suggest concomitant
variables that should be recorded. As far as possible, such observations
should be anticipated and planned for. Something unexpected may show up
however for example the incidence of a disease or pest may appear to differ
between treatments. Some standard method of observation should then be
used. This might be a score or rating and many scoring or rating schemes
have been developed and widely used. Even if the pest or disease problem
is serious on only a few farms the information is important and should be
recorded.

An oramplc of the value of concomitant observations and their use in co-
variance analysis is given below. The data (Table 10) represent yields
(0) and weediness scores ( ) from a RCB experiment on five farms (A-E) with
two blocks per farm. Weediness was estimated on each plot a few weeks
before reaping on a scheme in which ) = no weeds and 9 = complete weed cover.
Analyses of variance show that treatments differed significantly both in
yield (-) and wsedine!s (:'). Farms differed significantly in yield,
but not in Teedineso. To what extent is the effect of treatments
on yield attributable to their effect on weediness, recognizing that
weeds affect y::clds? Is there any relationship between weediness
and yield?













4.6 M.anagemen~

Problems of management can generally be resolved by careful
explanation to the farmer of the time schedule and of the importance
of timeliness and uniformity of treatment and basal treatment application.
Regular visits to on--farm plots are essential for proper monitoring and
correction of any departures from the intended schedule.


4.7 Data Collection

The collection, recording and storage of data must be organised
so as to avoid omissions, errors and losses. This is particularly
so where several technicians are involved, each overseeing a subset of
the farms.

Pro-foimae will facilitate accurate recording, and can serve
as reminders of the data to be collected and of observations to be
made at each farm visit. They may need to be designed so as to be compatible
with computer systems for data storage and analysis. Dates of'recording
must be noted. this is easily overlooked.

Regular observations of on-farm plots can often suggest concomitant
variables that should be recorded. As far as possible, such observations
should be anticipated and planned for. Something unexpected may show up
however for example the incidence of a disease or pest may appear to differ
between treatments. Some standard method of observation should then be
used. This might be a score or rating and many scoring or rating schemes
have been developed and widely used. Even if the pest or disease problem
is serious on only a few farms the information is important and should be
recorded.

An oramplc of the value of concomitant observations and their use in co-
variance analysis is given below. The data (Table 10) represent yields
(0) and weediness scores ( ) from a RCB experiment on five farms (A-E) with
two blocks per farm. Weediness was estimated on each plot a few weeks
before reaping on a scheme in which ) = no weeds and 9 = complete weed cover.
Analyses of variance show that treatments differed significantly both in
yield (-) and wsedine!s (:'). Farms differed significantly in yield,
but not in Teedineso. To what extent is the effect of treatments
on yield attributable to their effect on weediness, recognizing that
weeds affect y::clds? Is there any relationship between weediness
and yield?

















Plot values (hypothetical) of yield (y) and weediness
Scores (x) for a RCB experiment with three treatments


(a c), two blocks per farm and five farms.


(See 3.7).


Treatment Totals Treatment Total
Farm Blocks a b c (y) a b c (x)

1 11 5 9 25 2 8 4 14
A
A2 10 9 8 27 3 3 5 11

21 14 17 52 5 11 9 25

3 14 7 12 33 1 8 3 12
B 4 15 11 10 36 1 5 4 10
29 18 22 69 2 13 7 22

C 5 13 7 9 29 2 6 5 13
6 12 8 10 30 3 6 4 13
25 15 19 59 5 12 9 26

D 7 9 8 7 24 3. 5 6 14
8 11 4 6 21 4 9 6 19
20 12 13 45 7 14 12 33


9 12 11 13 36 4 6 3 13
E 10 15 14 10 39 1 1 8 10
27 25 23 75 5 7 11 23

TOTALS 122 84 94 300 24 57 48 129


TABLE 10.












TABLE 11 (A-D) Covariance analysis of the data of Tables 11 (A-D).
Table 10 gives the sums of squares (S.S.y and S.S.x)
and products (S.P.xy) Tables 11B and D show the
calculations of the regression co-efficients and of
adjusted S.S. y's and M.S.'s, and Table 11 C shows the
calculation of adjusted means.

Table 11A
d.f. S.S.y S.P.xy S.S.x

Farms 4 99.3 -29.7 12.5
Blocks-within-farms 5 5.4 6.0 7.8
Treatments 2 77.6 -67.2 58.4
Farm X treatments 8 14.1 -12.6 24.7
Error 10 39.6 -39.5 40.9
Total 29 236.0 -155.0 144.3
TABLE 11B
LL:L .,. .... .- .....-i.. ., ..... 3 --...- -
(S.P.xy) S.P.xy
S.S.y S.P.xy S.S.x S.Sx S. d.f. M.S. F.

Farms 99.3 -29.7 12.5 41.1 4 10.3 51.5
Blocks-within-
farms 5.4 6.0 7.8 4.6 0.8 (5-1) 0.2 -.
Farms + Blocks
within-farms 104.7 -35.7 20.3 62.8 41.9

b' -0.769 F 4.6/0.2 23.0 (1 84 d.f.)

TABLE 11C ___

x (x-i) b'(x-x) y7' y-b'(x-x)

A 4.17 -0.13 +0.10 8.67 8.57
B 3.67 -0.63 +0.48 11.50 11.02
C 4.33 +0.03 -0.02 9.83 9.85
D 5.50 +1.20 -0.91 7.50 8.41
3.83 -0.47 +0.36 12.50 12.14


TABLE 11D
(S.P.xy)2 S.S.y- 2
S(S.P.xy)
S.S.y S.P.xy S.S.x S.S.x S.S.x d.f. M.8. F

Treatment 77.6 -67.2 58.4 1.0 2 0.50 2.94
Error 39.6 -39.5 40.9 38.1 1.5 9 0.17

Treatment +
Error 117.2 -106.7 99.3 114.7 2.5


F = 38.1/0.17 224(1&9 d.f.)


b' -0.966















For analysis of co-variance, the sums of square for yield (S.S.9)
and for weediness (S.S.x) and the sums of products (S.P. ky) are required.
TheS.S. z's and S.S.y's will have been calculated for the analyses of
variance. Note that the sums of products are all negative in this
example (Table 11 A). Since one of the objectives of covariance analysis
is to ;xamine inter-relationships, the first steps are to estimate a
regression co-efficient and determine its significance. Looking first
at farms, the blocks-within-farms regression co-efficient (b') is calcualted
from
b = S.P.ty
S. S.z.
using the blocks-within-farms S.S.x and S.P.xy (Table 11 B). In this
z:ample the value of b' 6.0/7.8- -0,769. An F-test to determine if this
value is significant, if it is not, further calculations are unnecessary.
F is calculated -using the blocks-within-farms line only from

F (S.P.:f)2 / S.S. ((S.P.kf)2 S.S.i))
S.S.x d.f. 1

In this example F 4.6/0.2 230, which, with 1 and 4 d.f. is highly
significant. Note that the 5 d.f. for blocks-within-farms is partitioned
into 1 d.f. for the regression and a "residual" with 4 d.f..

The yield sums of square (S.S.Y) for farms is now adjusted for the
regression. This is done in a roundabout way, using the farms and blocks-
within-farms totals; from this line is calculated:

S.S.y -((S.P.xy)2 / S.S.x)
In the example, this is -

104.7 (35.7 /20.3) 41.9:
from this is subtracted the comparable quantity calculated from the blocks-
within-farms line, which is -
5.4 (-6.02/7.8) 0.8
to give the adjusted farms S.S.y (41.9 0.8 = 41.1). The mean squares are
now derived, noting that the adjusted mean square for blocks-within-farms
has one less d.f. than in the original analysis one d.f. has been "lost"
to the regression. The F value for farms (51.5) is highly significant.
It might have happened that the effect of farms was no longer significant
after adjustment, indicating that the differences in yield were largely
accounted for by the differences in weediness.

Farm mean yields are now adjusted, as shown in Table 11C. Each
farm mean for y is adjusted by_an amount which varies according to the deviation
of the farm mean for x from x the overall mean of x. Tests of
significance of differences between pairs of adjusted means requires the
calculation of separate 't' values, but this is not shown here.















Turning to the treatment and error lines (Table 11B), a comparable
series of calculations is done. The value of b' (-0.966) is highly
significant, but the adjusted mean square for treatment is not significant.
There is no point therefore in computing adjusted means. This result can
be interpreted as indicating that differences between treatments in yield
were largely due to differences in weediness. A cautionary note is necessary:
covariance analysis does not necessarily indicate a casual relationship.
Yield might have been determined before differences in weediness become
apparent, and these differences in weediness may be due to differences in
crop growth, plant form, shading and so on. Generalising, y may not be
casually dependent on x, both y and x being casually related to an
unsuspected (or unrecorded) variable z.



4.8 Missing Plots and Blocks

The best laid plans and most meticulous execution, cannot ensure
no loss of data, but can reduce the likelihood. The loss of recorded
data by carelessness is inexcusable and can be avoided. Loss of data
from one or more plots in a block, from an entire block and from
an entire farm can occur as a result of misunderstandings with the farmer,
livestock damage, praedial largeny and so on. This should be borne in
mind at the design stages there should be sufficient d.f. for error to
accommodate some loss.

A value for a single missing plot in a RCB experiment can be easily
computed. If a' is the missing value (of treatment a), then an estimate
of a' is given by -

a' = r B' + ET G
(r 1) (t 1)

where B' is the total of the remaining plots in the block, T' is the total
of treatment a from the remaining blocks and G is the grand total.
If data from several plots are missing (a', b' and c' for instance)
values are assumed for b' and c' -and a value for a' estimated as above.
Using this value, and the assumed value of c' an estimate is then made of
b', and then c' using the estimated values of a' and b'. The calculations
are repeated iteratively until the estimated values do not differ substantially
from those found in the previous cycle. One error d.f. is lost for each
estimated plot value.

For incomplete block designs more complex formulae than the above
must be used. -But thd general method of analysis (Appendix ) can
accommodate some missing plots, and even blocks.














If the data from an entire block is lost, or from both blocks on a
farm where the design has two blocks per farm, no estimation of the missing
plot and block values can be made. However, the loss of, say, two plots out
of four in one block should not cause the researcher to abandon the entire
block: data from the two remaining plots is still useful, and methods
of analysis are available to accommodate this situation.

A more serious situation arises where one or more entire blocks are
lost, perhaps because the farmer reaps the plots without advising the
researcher, or because of livestock damage. Suppose for example that
in the data of Table 6, Farm E was entirely lost (e.g. both blocks reaped
pprematuerly) and that blocks 6 and 8 were also lost, due to severe
livestock damage. The data now comprise plot values from only six blocks,
two each on Farms A and B, and one each (5 and 7) on Farms C and D. No
longer can the effect of farms be estimated, nor the farm x treatment
interaction effect, in the analysis of variance. The analysis now becomes:



Source of variation S.S. d.f. M.S. F

Blocks 316.0 5 63.20 2.72
Treatments 40.5 3 13.50 1.0
Error 348.0 15 23.20
Total 704.5 23

letting the data, as in Fig. 14 (see 2.8) would indicate that there is
evidence of a block x treatment interaction.


Since methods of analysis are available for experiments with unequal
replication, data from experiments with more than one missing plot per block
from several blocks, can be analysed. Clearly, if data from only one or
two plots of a particular treatment are available, that treatment cannot be
included in the analysis. But if the loss of those plots was due to disease or
lack of rainfall, that is a "significant" result, indicating disease or drought
susceptibility.,
Clearly, every effort must be made to avoid loss of plots and blocks and
of recorded data. This may require fencing (which is an added cost) or simply
securing the full co-operation and understanding of the farmer. It is also
advisable to increase the overall replication, so as to ensure, as far as
possible, sufficient replicates, in the event that one or more replicates are
lost. This will usually mean increasing the number of farms but in an
experiment with one complete block per farm it may be possible to put
additional blocks on two or three farms at minimal extra cost.














APPENDIX

The Analysis of Variance: A General Method for Designs
arranged in Blocks, and accommodating Incomplete Block
Designs, Missing Plots and Unequal Replication.



The general method of analysis described below can handle most designs
arranged in blocks. Difficulties arise if there are disconnections in
the design, that is, some treatments occur only in certain blocks with the
other treatments occurring only in the other blocks. This can occur in
confounded designs.

The data used as an example are arranged in two ways: Firstly,
as an incomplete block design with some double replication within blocks (Fig.
20 A)", and secondly, as a randomised complete block design (Fig.20B)
Both designs have 20 plots, with five treatments replicated four times.
The design of Fig. A has nothing to commendit, and is used for its
illustrative value only.

The data of the incomplete block design give an incidence matrix
as follows to show the number of times each treatment occurs in
each block:


BL 0 C K
(1) (2) (3)
a 2 0 2
b 2 2 0
c 1 1 2
d 1 2 1
e 0 2 2

Block totals are 59, 81 and 83 based on 6,7 and 7 plots respectively (Table
20 A .) Block means are therefore 9.833, 11.571 and 11.857. Treatment
totals are:
a, 30 B b, 35; c, 46; d, 51; e, 61.
















Fig. 20. An incomplete
design (B), to show the
The plot values are the


b a c d a b
10 8 12 14 7 8



c b e d b e d
11 10 14 12 7 16 11




a c d e c e a
6 13 14 15 10 15 9


block design (A), and a randomised complete block
use of the general method of analysis of variance.
same for the two experiments.


e b a d c
16 10 8 14 12



c a e b d
11 7 14 8 12




b c d e a
10 13 14 15 9



a d c e b
6 11 10 16 7















Plot values from Fig. 20 A and B arranged in order with block
and treatment totals.


A. Incomplete block design (Fig. 2D A)
Blocks
(1) (2) (3)
a, 8 b, 10 a, 6
a, 7 b, 7 a, 9
b, 10 c, 11 c, 13
b, 8 d, 12 c, 10
c, 12 d, 11 d, 14
d, 14 e, 14 e, 15
e. 16 e. 16 Grand t


Treatment
Totals
a, 30
b, 35
c, 46
d, 51
e, 61


total 223.


59 81 83


B. Randomised


complete block


Blocks


design (via 20 BI


Treatment
Totals


30
35
46
51
61


60 52 61 50


Table 12.


Total


?--


--- -- -r --


Total














The adjusted treatment totals (Q) are calculated by taking each
treatment total and substracting the block means, weighing for the number
of times the treatment occurs in each block. For instance:
Qa 30 ((2 x 9.833) + (2 x 11.857))= -13.380;
Qb 35 ((2 x 9.833) + (2 x 11.571))-- -7,808
Qc = 46 ( 9.833 + (2.x 11.571) + 11.857) = + 0.882
and so on. Qd + 6.168 and Qe = + 14.144. The sum of the Q's should be
zero, but rounding-off may give a small deviation from zero.

The main part of the calculation is an iteration, shown below. This
is continued until further repetition has no effect. The purpose of this
iteration is to find the true effects of treatments after allowing for
differences due to blocks. The vectors v1 v,2 v3 etc. are calculated for
each treatment and in comparable fashion values for blocks (al, au2. ,3' etc

The vector v1 is estimated by dividing adjusted treatment totals by
the number of plots receiving each treatment in this case 4 for all
treatments. Thus for treatment a. the value is -13.380/4 3.345, for
b-7,808/4 1.952 and so on. The u1 values.for blocks, are estimated
from the v1 values multiplying each element by the number of times it occurs
in each block. For example, for block 1, ul is estimated from
((2 x -3.345) + (2 x -1.952) + (+0.220) + (+ 1.542))/ 6 -1.472
and for block 2, from
((2 x -1.952) + (+0.220) + (2 x +1.542) + (2 x +3.536)) / 7 = +0.925
and similarly for block 3.
Next v2 is projected, using the values in ul. For treatment a, each
element of u1 is multiplied by the number of times a occurs in the block, thus,
((2 x 1.472) + (2 x +0.338))/4 -0.567
and for treatment d,.
(-1.472 + (2 x +0.925) + 0.338)/4 + 0.179.
The sum of the v1 elements should be zero, allowing for small deviations due
to rounding-off.
From v2, the values of u2 are projected. Thus for block 2,
((2 x -0.274) + 0.032 + (2x0.179) + (2 x 0.632))/7 = + 0.158
Then from u2, the elements of v3 are derived, and so on. At each step, the sum
of the v1 v2 v3 elements etc. should equal zero, Any sizeable deviation
from zero should be checked for errors. The iteration continues until only
zero values, or values close to zero are ..derived.















v1 V2 V3 V4 v5 v6
2 0 2 (4) -3.345 -0.567 -0.097 -0.016 -0.003 0.000
2 2 0 (4) -1.952 --0.275 -0.044 -0.001 -0.001 0.000
1 1 2 (4) +0.220 +0.031 +0.005 +0.001 0.000 0.000
1 1 2 (4) +0.220 +0.031 +0.005 +0.001 0.000 0.000
1 2 1 (4) +1.542 +0.178 +0.031 +0.006 +0.001 0.000
0 2 2 (4) +3.536 +0.632 +0.105 +0.008 +0.003 0.000
(6) (7) (7)

-1.472 +0.925 +0.338 u1

-0.245 +0.158 +0.053 u2

-0.041 +0.027 +0.009 u3

-0.007 +0.005 +0.002 u

-0.001 +0.001 0.000 u5



The purpose of iteration is that the effects of treatments, known as
the treatment parameters, are best estimated by the elements v, v2, v3......

Thus for treatment a, the parameter is given by (-3.345) + (-0.567)+(0.097) +
(-0.016) + (-0.003) -4.028. So the treatment parameters are:
a -4.028- b .-2.279; c. +0.257; d +1.757: e +4.294.

A check is to multiply each treatment parameter by the respective treatment
replication and sum the products, which should sum to zero
(4 x -4.028+ (4 x -2.279) + (4 x 0.257) + (4 x 1.758) + (4 x 4.294) 0.008.
The deviation is accounted for by rounding-off errors. Note that with equal
replication, there is no need to include the 4 in each bracket for this check.















The adjusted treatment means are given by adding the general mean (223/20 = 11.15) to
each parameter'
a 11.15 + (-4.028) 7.122, and b 8.871:
c 11.407, d 12.908; e = 15.444.
The sum of squares for treatments can now be calculated by multiplying
each adjusted treatment total (Q) by the corresponding parameter and summing the
products, thus:


(-13.380 x -4.028) + (-7.808 x 2.279) + (0.882 x 0.257) + (6.168 x 1.757)
+ (14.144 x 4.294) 143.49.

An analysis of variance can now be done. The within-blocks S.S. is
calculated from the sum of the squared individual plot values less the block totals
squared and divided by the number of plots in each block:
(82 + 72 + 102 ... 152 + 162) ((592/6) + (812/7) + (832/7) =

2667.00 2501.60 165.40


S.S. d.f M.S. F.
Treatment 143.49 4 35.87 21.22
Error 21.91 13 1.69
Within-blocks 165.40 17


The d.f. are 5-1 for treatments and within-blocks the total number of
plots less one (19) minus 2 for blocks (3 1) = 17. So for error there
are 17 4 13 d.f.. The F value of 21.22, with 4 and 13 d.f. is highly
significant.

It is possible to adjust for blocks, in similar manner to the adjustment
for treatments and to estimate residuals (i.e. the difference between
the "expected" and actual values) for each plot. The sum of the plot
residuals equals the S.S. for error.

Had the experiment been laid down as a RCB design, with plot arrangement
and values as shown in Pig.203, the above method of analysis could also be used.
This example is given solely to illustrate the versatility of the general method.











76
76


Qa 30 (12,00 + 10.40 + 12.20 + 10.00) 14.60
Qb = 35 .44.6 = -9.60
Qc 46 44.6 +1.40 and
Qd + 6.40 and Qe = +16.40.


The incidence matrix comprises ones only, as shown.


1
1
1
1
1
(5)
0.000


1 1
1 1
1 1
1 1


1
(5)
0.000


1
(5)
0.000


1 (4)
1 (4)
1 (4)
1 (4)
1 (4)
(5)
0.000 i,


v1 V2

-3.650 0.000
-2.400 0.000
+0.350 0.000
+1.600 0.000
+4.100 0.000


The u1 elements are all zero, and the v elements are also all zero. Treatment
parameters are therefore the v elements only. The S.S. for trontm"rnt IJf rhcrevfor
given by:


(-14.60x-3.650)+(-9.60x -2.400) +
(+16.40 x +4.100) = 154.30
and the within-block S.S. by
2 2 2 2 2
(8 + 10 + 12 + 14 .. 11 + 1
2667 2505 162.00
So the analysis is:


(+1.40 x +0.350) + (+6.400x +1.600) +



62) -- (602 + 522 + 612+502)/5=


S.S. d.f M.S. F
Treatment 154.30 4 38.58 60.27
Error 7.70 12 0.64
Within-blocks 162.00 16















This may be compared with the more familiar method of analysis of a.
RCB design:


This gives a blocks S.S., and the effect of blocks is clearly significant.
The general method of analysis is versatile and can handle, inter alia
the following:

incomplete block designs,
designs with planned unequal replication;
experiments with incorrect application of treatments
(so giving unplanned unequal replication)


- data sets with missing plot values.













INDEX 1: GENERAL


Page No.



66 67
75

28 -29
.1- 2
:64 -68
85-86
23- 26
20 22
27 -31
70 -77
42
10-19 .62
5- 9
1, 2


adjusted treatment means
in analysis of covariance
in analysis of variance

aliases
alternatives, testing of
analysis of covariance
analysis of variance
confounded factorials
factorials
-: :r. *C-"1 aOplicaticn
General method
hierarchical
incomplete block designs
randomised complete block
applicability testing

balance, supplemented
balanced incomplete block designs
balanced lattices


basal treatment application
bias
biological problems
blocks
c-: c Ic:e
different sizes
incomplete
number per form
number required
blocks-within-f arms
blocks-within-zones


4-7,83
83
4, 10-19,83
5,7,37-41, 59,60
59,60
41,44
42


13 -17
10 19
10


54 57
48
46















Page No.


calibration of Sprayers
coefficient of variation
completely randomised designs
concomitant observations


complete
partial
contiguity of plots
control treatments
choice of-
extra replication of
covariance analysis
cropping history


d.f.
-.. allocation in analysis of variance

data
primary
secondary
supporting


47
,41
5
41, 64
23 26
23 25
24 -25
4,6,8


49-62
13-19
64-68
46,53


data collection 51-52, 58,64-68
defining contrast 28
degrees of freedom see d&f.
disconnected designs 18,19


efficiency factor (of incomplete block designs)













FSR/D methodology
F test
factorial
2n
3n
cofoundinn
farm x treatment int
farmers
bias
conflicts
drop outs
explanation to
premature adopt
premature reapii
reluctance
farming systems
fdrms, how many
fractional replication


group replication
gullies


half-replicate
hierachical analysis
homogeneity
of environment
of error
incidence matrix
interaction effects


lattices


main effects
management
marking out
mean square
missing plots and blocks











Page No.


non-uniform application

on-farm
production systems analysis
testing
testing of alternatives

paired t test
partially balanced designs
partition of
error S.S.
treatment S.S.
physical problems
planning
plot
arrangement
shape
size
problems
biological
physical
technical
production systems analysis
proformae


randomised complete block designs
with one block per form
with two or more blocks per farm
with two replicates per block

replication
fractional
how much ?
unequal


1, 2
1, 2
1, 2

7, 9
11


42
20-22
46
35,36


5,6,7,55,57,83
49,55
49


5 9
5,6,7
59-62
7, 8


27-31
49,59-61
32-36,49












slopes
subsets of treatments
fractional replication
incomplete block designs
sum of products
sum of squares
supplemented balance

t test, paired
technical problems
terminology
terraces
treatment application
treatment combinations
treatment parameters
treatments
how many
trees

unequal replication
uniformity of plots

variance,analysis of
within-blocks S.S.
wrongly applied treatments

zones
zonex x treatment interaction


Page No.


46


24,28-31
10-19
64-67
70-77,85
13-17,36

7, 9
47
4
47,56
54
20,23,24,28
74,76


49,53
47


32-36,49
46,47


85,86
75,76
50

42-65
42,44







83

Pave 0o.,
Tndex 2 Experimental resi.ns


balanced lattice 4 10
(t = 9, k 3 b 12. r = 4)
Balanced incomplete block F. 5 11
(t 5, k 3 b = 10, r = C)
Balanced incomplete block Fi 11i
(t 7, 7 2 b 21 r 6)
Blocks of different sizes .i. 12 34
(t 5 1: 5 an 3 r = 8)
Elocks of different cise with
supplemented balance Fir 13 36
(t = C. k = 5,4 and 3 c = 1)
Confoundin:.* complete of a 2"
factorial Fi2. S 23
Ccnfounding partial of a 23
factorial Fiz. 10 24
Half-replicate (fractional
replication) of a 2' factorial in
4 blocks of 4 plots ip' 11 27
Incomplete block with disconnection Fio. "A 19
(t 6 k 3)
Incomplete block witl overlapping FiF. 19
(t = 6 k 6 4)
Incomplete block with surplemented
balance
(t = 4 k = 3 c 1) 'i. 7A i"
(t = 5 k = 3. c 1 ) 7i. 7)- 14
(t = C, k = 2 c 1 i) Fir. 7, 15
(t = 6 k 4 c 2) Fi2, 7T 15
(t = 7. k 5 c = 2) Fi- 7E 15
-.andonised complete '-lock one
replicate per block ?i ?
"andomised complete block two
replicates per block ?iro 3 E

St = number of treatments. k = number of plots per block
(i.e, block cize ), b = number of blocks. r replication
and c = number of control treatre-nt in eact block For RCD
designs c = 1.













Table 2 (p. 12 ) lists balanced incomplete block designs
available for various values of t and k-

Table 3 (p. 17 ) lists incomplete block designs with
supplemented balance for various values of t,k and c.









Page N6.

Index 3: Analyses of Variance



Factorial! randomised complete
block design
3x 4 blocks
2 x b blocks 21
33 x b blocks 22
33 x b blocks 22



Factorial: complete confounding
23 x 3 replicates in 6 blocks 25
26 x 1 replicate in 8 blocks 26
Factorial: partial confounding
23 x 3 replicates in 6 blocks 25

Factorial: fractional replication
25 half replicate in 4 blocks 28,30
2 half replicate in 2 blocks 30

23 subset with b replicates 30-

General method* 70

Incomplete block design
simple replication generalisedd) 13
group replication generalisedd) 13

Randomised complete block design
generalised 5
one block per farm
(t 4, b = 17) 32
(t = 4, b = 17, but double replication of
one treatment) 32
(t 4 with an extra probe treatment, b = 14) 35
(t 4, b 10)* 39
two blocks per farm
(t 4, b 10)* 39


*Indicates worked examples












Page No.

hierachial classification

zones 42
zones and farms within zones* 43,44
degrees of freedom
t 2-8: blocks required 60
for 20 or 30.error d.f. with
1 block per farm
t 2-8: error d.f. with 2 or 3 blocks
per farm. 61

t test (paired) 9


Analysis of covariance* 64-68


*Indicates worked examples.




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