q-. 0 63
DEVELOPMENT OF DESIGNS
TO IMPROVE EFFICIENCY OF OFR
Training Working Document No. 3
with CIMMYT staff
Apdo. Postal 6-641,
06600 M6xico, D.F., Mexico
This is one of a new series of publications from CIMMYT entitled Training Working
Documents. The purpose of these publications is to distribute, in a timely fashion,
training-related materials developed by CIMMYT staff and colleagues. Some Training
Working Documents will present new ideas that have not yet had the benefit of extensive
testing in the field while others will present information in a form that the authors have
tested and found useful for teaching. Training Working Documents are intended for
distribution to participants in courses sponsored by CIMMYT and to other interested
scientists, trainers, and students. Users of these documents are encourage to provide
feedback as to their usefulness and suggestions on how they might be improved. These
documents may then be revised based on suggestions from readers and users and
published in a more formal fashion.
CIMMYT is pleased to begin this new series of publications with a set of six documents
developed by Professor Roger Mead of the Applied Statistics Department, University of
Reading, United Kingdom, in cooperation with CIMMYT staff. The first five documents
address various aspects of the use of statistics for on-farm research design and analysis,
and the sixth addresses statistical analysis of intercropping experiments. The documents
provide on-farm research practitioners with innovative information not yet available
elsewhere. Thanks goes out to the following CIMMYT staff for providing valuable input
into the development of this series: Mark Bell, Derek Byerlee, Jose Crossa, Gregory
Edmeades, Carlos Gonzalez, Renee Lafitte, Robert Tripp, Jonathan Woolley.
Any comments on the content of the documents or suggestions as to how they might be
improved should be sent to the following address:
CIMMYT Maize Training Coordinator
Apdo. Postal 6-641
06600 Mexico D.F., Mexico.
DESIGN OF ON-FARM EXPERIMENTS
1. Experiments at Different Stages of OF Research
Like any other form of research project an OF research project passes through different stages from the
exploratory through the detailed examination of components to the verification. These stages are rarely
completely separable. For example, at verification there will sometimes be additional treatments of
It is, of course, crucial that the objectives at each stage of the experimentation are clearly identified and
relevant to that stage. The choice of treatments is discussed in general in section 3. Here it is worth noting
that there will be a general tendency for the number of experimental treatments to decline through the
programme. At the earliest stages there should be many treatment factors, each with few levels. In
subsequent development the number of factors in a single experiment will tend to decline with the number
of levels tending to increase. At no stage should there be many factors each with many levels since such an
experiment would appear to be asking whether interactions were important and simultaneously assuming
that they were while trying to identify best levels of each factor. It is not just the impossibility of managing
such a trial but the contradiction in objectives that makes it inappropriate.
Many of the concepts discussed later in this paper are relevant to most stages but there will be differences
at least of emphasis. There will be differences in the number and distribution of farms with larger numbers,
certainly, for the verification stage. I assume that the questions of choice of sample farms and the definition
of recommendation domains are not covered in this paper, being discussed in CIMMYT Training Working
Documents Nos. 4 and 5.
2. General Statistical Principles of Precision, Replication and Resource
2.1 Precision of Results
It is extremely important to assess, before the experiment, the precision of the information to be obtained
from the experimental results. This involves thinking about three quantities. First the likely background
variability, as measured by the Coefficient of Variation. CV, or the plot Standard Deviation, s; second, the
difference in yield (or other performance variable) which is important, d, or A if the difference is expressed
as a percentage of the experimental mean yield; the third component is the number of replications n for
Assume that we are interested in the comparison between two treatments each having a total of n
observations across the whole experiment. The crucial statistical result is that the standard error of the
difference between two mean is:
SE (XI X2) = q(2s2 /n) = Sq(2/n)
To have a realistic chance of identifying whether the true difference between the treatments (P l-42) is as
large as our critical difference d we must make the SE a good deal smaller then d. How much smaller
depends on the significance level we propose to use and the risk we are prepared to accept of missing a true
difference as big as d. A useful rule of thumb is to try to make the SE no bigger than d/3. This means that d
is 3 standard errors which allows 2 standard errors for achieving a 5% significance level and an extra
standard error for bad luck in getting (XI X2) smaller than d (the risk of missing a true difference ofd is
Consider an example where we expect a mean experimental yield of 3000 kg/ha, a CV of 20% which
implies s = 600 kg/ha and where we would hope to detect a true difference, if it exists, of 750 kg/ha. The
SE should therefore be no bigger than 250 kg/ha and we thus require that n shall be at least big enough to
250 = 600 4(2/n)
This implies that
n/2 = (600/250)2 = 5.76
and n should be at least 12.
We can approach the problem from the other end, and consider what precision would be achieved and what
differences detected for various possible n.
If we can afford 8 observations per treatment our standard error will be
SE (for n=8) = 600 4(2/7) = 300.
This would give us a 5/6 chance of detecting a difference of 900 kg/ha using a 5% sig. level.
If we could use 20 observations.
SE (for n = 20) = 6004(2/20) = 186,
and we would now have a 5/6 chance of detecting a difference of 560 kg/ha.
There are a few additional comments. We can work with CV and A rather than s and d and everything is
expressed in percentages but gives the same answer:
CV = 20%, A = 25%
25/3 = 204(2/n)
which gives n/2 = (20x3/25)2 = 5.76.
These calculations assume that the experimenter can assess the appropriate value for d. More crucially the
calculations assume that s is known. In practice previous experience with the same crop for similar plots in
similar conditions will often provide, through the "EMS. a credible value for s; sometimes less closely
related information will have to be used to guess the likely value of s. If the actual experimental value of s
is smaller than the assumed value, then our detection chances improve.
Note that although the SE decreases as n is increased, the reduction of SE for an increase of 1 to n gets
smaller as n increases (the law of diminishing returns). We can make the statements about detection
probabilities and significance probabilities more precise by expressing
d as Za + Zp
where Zp is the standardized normal deviate corresponding to an *a % significance level (Za = 1.96 for a
= 0.05) and Z is the standardized normal deviate for a risk of non-detection (Zp = 1.0 for P = 1/6).
Finally if we want to think about precision for interaction effects or other effects than the simple difference
for two treatment means, then our formula for the standard error will change. For an interaction of two 2-
level factors, which is the difference between two differences,
SE = 4(2s2/n + 2s2/n) = (4s2/n).
2.2 Replication, Hidden and Total
The actual number of observations relevant to a comparison may involve hidden replication as well as the
apparent, explicit replication. Further, we may have to think which replication is relevant to our question.
Suppose we have a set of 16 treatments comprising all combinations of 24 factorial structure with factors
density, weed control, nitrogen and phosphorus. The full set of combinations are represented in Table 1 for
a single site with 2 replications of each combination. Suppose further that we have 5 sites.
If we are interested in detecting an average nitrogen effect at one specific site, we have 16-fold replication
for each N level (n=16) being made up of 2 explicit replicates x 8 hidden replicates since each N level
occurs for the same eight combinations of density, weed control and phosphorus.
If we are interested in the average nitrogen effect averaging over all five sites than we have 80-fold
If we are interested in the density x nitrogen combinations at one site we have 8-fold replication.
If we are interested in comparing the nitrogen effect at high density, no weed control and no P average
across sites, we have 10-fold replication.
Thus the amount of replication, and equivalently, the information, for any comparison must be assessed for
each specific comparison of interest.
The use of replications in assessing precision in the previous section has a further potential complication
because the variability between plots within a site may be different (smaller) from the variability between
sites. Thus, if we are considering the 80-fold replication for the N effect average over all sites our CV will
tend to be higher than the 20% within site CV. The increase will depend on the CV of sites and if this were,
say, 50% the overall CV would be approximately.
4(20%2 + 1 (50%2 20%2)) = 23%
Note that the increase in the SD or CV depends on the proportion of site replication in the total replication
which is 1/16 in the example but would be 1/2 for the fourth example above with a much larger consequent
increase in the CV. The amount by which the between-site CV is greater than the within-site CV may vary
widely, but a factor of 2 or 3 might be a reasonable guess.
2.3 Efficient Use of Resources
In section 2.1 we considered the choice of n, the treatment replication, which must be considered in the
context of different forms or replication (2.2). We now consider the efficiency of use of total resources in
Suppose that in an experiment there are a total of N plots. Consider the total df (N-l). We use these in three
(i) Estimating the error or random variance, s2
(ii) Controlling, or identifying and allowing for causes of variation. This includes blocking,
covariance adjustment, possible losses of plots.
(iii) Answering questions through treatment comparisons. Here, questions include those relating to
main effects and interactions, but also possibly the modification of treatment effects by
If we consider (i) first then it is usually accepted that a good experiment should have at least 12 df for error
(some might say 10 or 15 instead of 12). It is equally important to recognize that there is very little benefit
in having more than 20 df for error. An experiment with more than 20 df for error is inefficient. Surplus d.f
should be transferred to (ii) to reduce s2 and hence improve precision or to (iii) to provide answers to more
For example, a simple Randomised Complete Block Design with 4 blocks and 12 treatments in each block
is an inefficient design because it allocates 33 df to error. To redesign the experiment to make better use of
the resources, we could try to use more df in (ii) or (iii).
One way of using more df in (ii) would be to use smaller blocks, dividing each complete block of 12
treatment plots into incomplete blocks of 4 or 6 treatment plots. The construction of incomplete block
designs [(see Mead (1988) chapters 7 and 15] but will be worthwhile only if reducing block size reduces s2
as should often be possible. More df could also be used in (ii) by identifying covariates which might
explain some of the plot-to-plot variation.
More df could alternatively be used in (iii) by including an additional treatment factor at two levels and
assessing the main effect of the factor and interactions with the original treatment factors. The upper level
could be applied to six treatments in block 1 and the lower to the other six treatments with the pattern
reversed in block 2, and the whole pattern or a similar one repeated in blocks 3 and 4. Further discussion of
such confounded designs is given in Mead (1984, 1988).
I believe it is crucial in OFR that we do not simply transfer the often thoughtless and inefficient recipe
designs used widely in research station experimentation. We must design experiments efficiently to use
On station experiments are often regarded as good. I believe, on the contrary that they are often
unimaginative, inefficient and boring and they achieve information only because of the overall high level
of control and by being big.
Good designs could, in fact, reap very much greater rewards in OFR than they have been allowed to on
3. Plot Sizes
3.1 Plot size, choices and implications
It is quite widely believed that the variability which results when using small plots for OFR experiments is
such as to make small plot OFR experimentation inappropriate. It is not clear that there is anything peculiar
about the variability of plots on farms except that it is rather larger than that on research stations. The
normal statistical expectation would be that the relation between the plot standard deviation, s, and plot
area would be of the form
s = K/ 4Area.
This is essentially the same pattern as for replication
s = oajn.
Data from uniformity trials on farms collected and analysed by Hector Barreto seem to confirm the
relationship between plot standard deviation and plot area. Hence, we should expect the usual statistical
benefits of using smaller plots, allowing better control of the random variation, to apply on farms.
There are, however, other considerations. One is that the researcher (with the farmer) may not be able to
use an appropriate form of blocking because of inadequate time to examine the particular farm situation
and likely pattern of yield variation. Hence, the experimental design will not be efficient in controlling
random variation and small plot benefits will be dissipated.
A second consideration is that small plots may seem quite unrealistic to the farmer and he may not apply
the care of management which he would to larger plots.
Another consideration is that the total area of an experiment on farm is less than one on-station, and it is
also true that the absolute level of variability, per area, on farms is greater than on station. Hence, it is
inevitable that precision of results on farms will be reduced compared with that expected from station
experiments. The disappointment with the level of precision on farms, ignoring information about expected
precision which can be calculated as in section 2.1, may be partly responsible for the belief that small plots
are the cause of poor precision in OFR.
The choice of plot size for future OFR experiments must continue to be a matter of judgement. If the level
of control of variation through the researcher's knowledge of the particular farm conditions, expressed in
careful choice of blocking, is good, then smaller plots may be appropriate. If such control is not feasible or
if farmer preference and difficulty of management make small plots unacceptable, then we may have to use
An almost inevitable consequence of using larger plots is that the number of plots per farm will be reduced
and it is then possible that the precision of information on a singlefarm will be inadequate to produce
useful conclusionsfor thatfarm. The implication would then be that we have to expect that most
information would derive from analysis of the total (multiple farm) experiment. This further implies that
the design of the whole experiment be considered as a whole rather than repeating an identical experiment
at a number of farms. It is, of course, possible more generally that designing the whole experiment, with
non-identical site-experiments, will be beneficial.
Certainly the use of larger plots does not necessitate a reduction in the total number of treatments
(corresponding to the total number of questions asked). We may well need to use subsets of the total set of
treatments at each farm and the design of experiments with different treatment subsets is discussed later.
We must be prepared to design OFR Experiments to fit the particular resources and questions according to
the principles of Sections 2.1 2.3.
4. Managing Variation
4.1. Information About Variation at the Farm Level
In some situations it may not be possible for the experimenter to make any assessment of the variability
within the area made available for experimentation by the farmer. This necessarily makes designing
efficient experiments much more difficult. If it can be assumed that the person responsible for local
arrangements for the experiment both understands the concept of blocking and is capable of identifying the
likely patterns of variation between plots then it is reasonable to use blocking in the design. In such a
situation, where the experimenter cannot control, directly, the decisions about plot and block design I think
the correct philosophy is to try to limit the potential for the choice of unsuitable blocks. This can probably
be achieved by setting an upper limit of 8 plots per block and requiring that the blocks be made compact.
However I shall assume that the experimenter does have the opportunity to assess variation within the
proposed experimental area and that (s)he, in collaboration with the farmer, can make judgements
identifying those plots likely to produce similar results. To avoid the suggestion that a "Block" must be
rectangular in nature, I propose to call sets of plots judged to be similar "Groups". It is crucial that this
identification of groups be separate from decisions about the choice of treatments. These two aspects of
design inevitably interact later but we must first try to ensure that we have the best possible grouping of
plots (as well as the most relevant set of treatments.
Let us consider an example from one of the on-farm experiments in the Poza Rica area. There were 24
plots in three rows of eight plots, as shown:
Row 3 17 18 19 20 21 22 23 24
Row 2 9 10 11 12 13 14 15 16
Row 1 2 3 4 5 6 7 8
Row I is at the bottom of the hill, row 2 above row 1, and row three above both.
The correct grouping system, identified by the experimenter, was three groups
The experiment was actually designed in four blocks of six plots
You can probably guess how many treatments there were!
The correct design would have three blocks of eight plots each with each block containing all six
treatments plus extra plots for two of the treatments, the extra two being different in each block. The irony
of this particular situation is that the actual allocation of treatments to blocks was inevitably equivalent to
the correct design (can you see why?) and the analysis that should be applied to the results should treat the
data as if the design had been intended to be the correct design (i.e. 3 blocks of eight plots, not 4 blocks of
six plots). However there is one difference between the allocation of treatments to plots in the ideal design
and in that actually used and this is that the randomisation of the design in three blocks would include all
possible allocations of treatments to the eight plots (see design example 1, section B).
Naturally experimenters cannot always expect to achieve the ideal design when trying to use an
inappropriate block structure. Another example in the Poza Rica farms had 24 plots as shown:
Row 5 19 20 21 22 23 24
Row 4 13 14 15 16 17 18
Row 3 7 8 9 10 11 12
Row 2 4 5 6
Row 1 1 2 3
The site was clearly very variable with the rows climbing steeply from row 1 to row 5 and with poor
growth at the right hand side of the area which curled some way round the hill. Sensible groupings would
appear to be
(A) row 5,
(B) rows I and 2
with either (Cl)row 3 or (C2) plots (7,8,9,13,14,15)
and (DI)row 4 and (D2) plots (10,11,12,16,17,18)
The actual design had two blocks of twelve plots (for the twelve treatments) and there was plainly a great
deal of variation within the blocks (to be fair some of that variation would have remained even within the
One more example from the Poza Rica experiments to show how too swift assumptions about natural
patterns may lead to faulty conclusions. The 14 plots (for seven treatments) were as shown:
14 13 12 11 10 9 8
1 2 3 4 5 6 7
There was a small road running along the side of plots 1 to 7. Each row of seven plots covered a long area
and it seemed unlikely that plots (1 to 7) and (8 to 14) would be sensible blocks. However when walking
between the two blocks there was a very strong suggestion that those plots on the left (plots 1 to 7) for each
treatment showed better crop growth than those on the right. This impression can obviously be verified at
harvest but if true demonstrates how first impressions can be misleading. Further examination of the site
showed that the second block (8 to 14) was clearly, if only slightly, higher than the first, providing further
justification for the blocking pattern used.
In each on-farm experiment it is important, at the planning stage, to identify how the plots should be
grouped so as to both minimise variation within groups and maximise that between groups. This may, and
perhaps often should, produce groups of different sizes and later in the design process these ideal groupings
may be modified. Nevertheless it is vital that the ideal grouping be first identified.
4.2. Recording and Use of Ancillary Information
Whenever experimenters, or even statisticians, observe field plots during an experiment there are many
differences and patterns of growth which are apparent. Two which we observed during observation of the
Poza Rica experiments concerned patchiness of Johnsongrass and a possible trend along each block away
from the edge of the field. Field notebooks should, and often do, include anecdotal information collected in
a systematic manner. If that anecdotal information were recorded in a crude quantitative form it could be
used, later, through covariance analysis to improve the precision of treatment comparisons. The minimum
form of record would be presence(l) or absence(0) of a characteristic. More usefully a three- or two- point
scale to record nil(0) mild(l) substantial(2) or total(3) level of the defect characteristic should allow
adjustment for the effect of the characteristic.
The possible distance adjustment occurred for a tillage and cover crop experiment, for which the plots were
Orange 15 16 17 18 19 20 21
14 13 12 11 10 9 8
Orchard 1 2 3 4 5 6 7
The visual impression was of increased growth at the orange orchard end of the experiment. If the trend is
gentle then a covariate of the distance from the left-hand end of the experiment may be adequate. If the
reduction in yield near the orange orchard is more sudden and severe then using the reciprocal of distance
may be appropriate (see Example 10.2 in Mead (1988))
43 Discarding or Adjusting Data
It is expected, as part of the general philosophy of OFR, that considerable variability of results will be
experienced, and there is an argument that, consequent on this expectation, all data should always be used
precisely so that this expected variability should be displayed. A counter argument is that sometimes
extreme observations or sets of data are patently not representative of the same population as the rest of the
data and this should be recognized and the analysis and interpretation amended accordingly.
There are different levels at which the discarding of data may be considered. Within a site there are
sometimes obvious causes for reduced yields on some plots. A very common example for maize is plots
having a markedly low number of plants. Although total plot yield compensates partially for lower density
through reduced competition there is usually a clear tend relating yield and plot density. This is an
appropriate situation for covariance analysis and adjustment with total discarding of plot data only in
extreme cases. In covariance the relationship between the principal variate (yield) and the concomitant
variate (density) is assessed for each treatment (allowing for block effects if this is necessary) and the
average trend is calculated. The treatment means are then adjusted to a common density level enabling
valid comparison of treatments unaffected by particular deviations of density. The progress of the
technique is demonstrated for four treatments each with two plots in Figure 1.
Rep 1 Rep 2
Yield (kg/ha) Density/plot Yield Density
2.25 33 1.45 22
1.90 30 2.15 40
1.95 16 2.80 35
2.55 32 2.85 39
The four slopes (in g/ha per plant/plot) are:
and the average slope is
0.8 + 0.25 + 0.85 + 0.1 2 = 0.425
The adjustments are:
Mean to 35 Adjusted
Yield Density plants/plot Yield
1.85 27.5 + 7.5 x 0.0425 2.17
2.025 35 Nil 2.02
2.375 25.5 + 9.5 x 0.0425 2.78
2.6 36.5 1.5 x 0.0425 2.52
It may be decided to adjust yields to some value other than 35, for example, to average achieved plot
density. The principles and treatment differences are unchanged and the level of the covariate (density) to
which the yields are adjusted should be chosen subjectively to obtain the most relevantly representative
yields (to adjust to a target of 40 plants/plot would result in over-optimistic yields).
The linearity assumption required for covariance analysis may be improved if I/density is used as the
covariate. Whichever gives the greater Sums of Squares for the covariance term in the analysis may be
If covariance adjustment is used at several sites, the adjustment rates = covariance coefficient may be
different at different sites. This may be due to random variation or to real differences in yield-density
curves. Unless there are compelling reasons for believing that the covariance coefficients should be the
same there is no reason against using different adjustments at different sites.
If there is no obvious covariate, it is still possible to make adjustments for any observed and quantifiable
concomitant information. Thus, for example, if the end plot of each block give a unusually low yields a
covariate taking the value zero for end plots and one for other plots can be used adjusting yields to a
covariate value of one.
The decision whether or not to use covariance adjustment of treatment mean yields is, ultimately, a
subjective one. It should certainly involve looking at the plots of the data (as in Fig. 1). The effectiveness
of covariance adjustment will vary, but there will usually be some benefit in accuracy or precision if the
data plot suggests a relationship. Covariance adjustment remains valid if the covariate is apparently
dependent on treatments. The adjusted values then represent what would have been expected if a uniform
value of the covariate had occurred and this can sometimes provide valuable information (in parallel with
the treatment means of the covariate and of the unadjusted mean yields).
The basis for discarding values completely is more difficult and should normally be on the basis of the
researcher's knowledge of unusual circumstances rendering a plot unrepresentative. In cases of real doubt
it is legitimate to calculate analyses with and without the dubious data.
When the discard possibility refers to a whole site the situation is rather different. It is not usually
appropriate to consider adjusting site results to a common level because one of the purpose of using
multiple sites is to examine behavior of treatments over varying sites. It is much more appropriate then to
consider the set of treatment effects and relate them to possible causative variables measures at each site.
Essentially rather than discarding "unrepresentative" sites we should seek to separate them from the rest
and analyze them in parallel with the main data.
Finally, various rules have been advocated for discarding sites based on CV, overall mean, check treatment
performance, or % Error SS of Total SS. Counter examples demonstrating the inappropriateness of any of
those rules can be easily constructed. The safe approach is to retain all data but to seek to understand the
effects of causative factors and to identify different groups of sites showing different patterns of results.
5. Choice of Experimental Treatments
There are four main types of experimental treatment structure. First, the essentially unstructured set of
alternative treatments, such as a set of varieties or herbicides, where each treatment is of equal potential
importance. Second, the complete factorial structure including, equally, each combination of levels of the
factors included in the experiment. The third type could be defined simply as "the rest" between these two
extremes. Typical examples are control treatments in the unstructured set; stepwise combinations, where
each treatment is a particular modification of the previous treatment; subsets of a factorial structure
omitting inappropriate combinations. The fourth type, which may also be within types two or three, is for
levels of a quantitative factor where the particular levels are not chosen primarily for their direct interest
but rather as representatives of the range of interesting levels of the quantitative factor.
The only general rule is that the selected set of treatments shall provide the best possible information about
the questions which the experiment is purposed to answer. This statement,of course, assumes that the
questions precede the choice of treatments rather than the reverse (which is not scientifically justifiable).
There is relatively little to say about type 1 structures except that the number of treatments should be
determined by the number of interesting alternatives, always within the limitations of resources. The range
of incomplete block design structures now available for testing large numbers of varieties, using any
appropriate block sizes, is so comprehensive that there is no excuse for tailoring the number of varieties to
suit a particular design structure.
5.1 Complete Factorials
Complete factorial structures, possibly omitting one or two unsuitable combinations, always provide a very
powerful method of acquiring information because of their twin advantages: first they allow us to
investigate whether there are important interactions, and second, whether or not there are interactions, the
information about each separate factor effect will be more precise with factorial structure.
For initial experiments within a research programme factorial structured treatments will be suitable because
they provide information about the existence of interactions between factors, thus allowing those
interactions which are found to be unimportant to be ignored in subsequent experiments. The second
advantage of factorial structures in giving more efficient information about main effects and two.factor
interactions through the use of every combination in each effect estimate will, of course, also be beneficial
in initial experiments.
However this second advantage becomes much more important in subsequent experiments where it is more
efficient to continue to ask several questions in each experiment rather than relapsing to the classical
scientific approach of asking only a single question in each experiment.
5.2 Quantitative Factor Levels
For the choice of levels of a quantitative factor we should be concerned to maximise the information about
the pattern of response as a whole or about a particular characteristic of the response, such as the position
of the maximum. General statistical theory shows clearly that both forms of information are maximised by
(1) choosing as wide a range of values of the quantitative factor as is consistent with the assumption that
the general pattern of response over that range can be summarised by a simple form of response
(2) using as few different levels as are required to estimate the response curve with one extra for
assessing the adequacy of the response curve (or one for luckl).
These requirements are widely applicable and should be ignored only to use particular levels of
For the actual choice of levels it will often be at least approximately correct to use equally spaced levels
(possibly on the log scale). If the pattern of the response curve is expected to be strongly skewed then the
levels should be closer together where the response is changing rapidly and further apart in areas of lesser
53 Incomplete Factorial Structure
When the set of treatments is to be a subset of a factorial structure (that is several factors are varied in the
set of treatments, but less than all the possible combinations are to included) then the consideration of the
precision of comparisons from different subsets is very important. Precision increases according to the total
number of combinations providing information about each comparison. This is the power of hidden
replication. For a very simple example consider two alternative subsets each of four combinations from
three two-level factors.
Subset(l) A B C
Treatment 1 0 0 0
Treatment 2 1 0 0
Treatment 3 1 1 0
Treatment 4 1 1 1
Subset(2) A B C
Treatment 1 0 0 0
Treatment 2 1 1 0
Treatment 3 1 0 1
Treatment 4 0 1 1
The precision of the estimate of the difference between levels 0 and 1 of factor A (or B or C) is more than
twice as good for subset (2). That is the variance of the estimate of the difference using (2) is less than 50%
of that using (1). The advantage derives from the use in (2) of all four combinations for estimating the
difference as compared with using only two combinations in (1) plus the non-independence of the three
estimates of differences in (1).
In general I believe the choice of treatments for an incomplete factorial structure has to reflect a balance
between the objective of comparing, and being seen to compare, particular treatment combinations and that
of estimating effects precisely. In a situation where previous experimentation has established that factors A,
B and C act almost completely independently and where each main effect is believed to be substantial then
the benefits for presentation of subset (1), may outweigh the consideration of precision. For example a
sequence of treatments following the expected adoption sequence of farmers may be more understandable
The statistical theory on simple subsets of factorial structures which are efficient for the estimation of main
effects and two-factor interactions is well established. Nice fractions containing four, eight or sixteen
combinations from structures with three, four, five or six two-level factors are easily found. Some
examples are shown:
3 factors: 4 combinations
(000,011,101,110) or the complement (100,010,001,111)
4 factors: 8 combinations
(0000,0011,0101,0110,1001,1010,1100,1111) or complement
4 factors: 4 combinations
(0000,0110,1001,1111) or (0010,0101,1001,1110
5 factors: 16 combinations
5 factors: 8 combinations
Suppose it is decided that a particular number of combinations are to be used and, further, that the
presentation purposes both the combination of the lower level for all factors and the combination of the
upper levels of all factors are to be included (note that this will not normally be statistically beneficial. The
principles for choosing the other combinations are
(1) the two levels of each factor should be nearly equally represented,
(2) the four combinations of levels for each pair of factors should be equally represented,
(3) to remember the ideal properties of the "nice" fractions in maximising information about main effects.
Many practical situations using subsets of factorial structures require two-level factors and the logic of
selecting appropriate subsets is clearer for two levels per factor. Nevertheless it is possible to select subsets
from three- or four- level factors using the same principles. Thus, suppose we require twelve combinations
from a 2x3x4 structure. A suitable set would be
which includes all the 2x3 combinations twice, all the 3x4 combinations once and the 2x4 combinations
each once or twice.
5.4 An Example
To consider further the arguments pertinent to the choice of experimental treatments for type 3 structures
we shall use an example of a verification trial from Ipiales (Woolley et al. 1988). The experiment was for a
beans/maize intercropping mixture and the actual treatments used were
Variety Density Seed
Beans Maize Beans Maize Fertiliser Treatment
1) 1 A 8 16 100
2) 1 A 8 16 100
3) 2 A 12 16 100
4) 2 A 16 16 100
5) 3 A 16 16 100
6) 2 A 16 16 300
7) 2 B 16 16 300
8) 2 A 16 16 300 Yes
The treatments were designed in a step-wise fashion to assess the effects of a sequence of changes,
depending on (a) the size of the effects detected in previous trials and (b) the expected adoption sequence
by farmers. Treatment 1 was intended to be the individual farmer's practice in contrast to treatment 2
which was the to be the average practice of the group; in fact they emerged as virtually identical. Treatment
3 introduced an improved bean variety. Treatment 4 changed the proportion of beans/maize. Treatment 5
introduced a possible alternative, earlier,bean variety which might take better advantage of the increased
proportion of beans. Treatment 6 added more fertilizer to treatment 4. For treatment an alternative maize
variety (at the higher fertilizer level) was tried. Finally(treatment 8) a seed treatment was added to
treatment 6. The logic of the stepwise evolution of treatments is simple and easily understood. In statistical
terms it is also, unfortunately, inefficient in the use of resources. Each question which the treatments were
selected to answer is answered with minimum precision at each site because the answer involves the simple
comparison of two experimental treatments. A full factorial experiment with 3 bean varieties, 2 maize
varieties, 3(7) bean densities,2 fertilizer levels and + or the seed treatment would require 72 experimental
treatments and is plainly unthinkable.
The sequence of treatments 3 -4 -5 -6 -7 includes trying alternative varieties of beans and of maize
increasing bean density and increasing fertilizer level. Because these changes occur in a particular order
there is no opportunity to test different orders which would be appropriate if the relative sizes of the main
effects differ from site to site. Moreover, if we wish to demonstrate the benefit of
(a) increased fertilizer,
(b) bean variety 2,
(c) maize variety B, and
(d) increased bean density
a subset of factorial structure provides much better estimates of the four effects than a sequence. Some
possible changes to the treatment structure could involve:
(1) including all 8 combinations of bean(2or3) maize (A or b) and fertiliser(1 or 3) either at each site or in
sets of 4 combinations per site;
(2) considering the seed treatment as an extra factor and treating half the combinations in each replicate;
(3) eliminating treatment 1 or 2;
(4) other variations on the lines of (1) incorporating the density change(treatment 4 to 5).
The detail of any experiment must always be determined through discussion and joint decision of the
experimenter and statistician. However, a possible design in two blocks of eight plots per block would be
Variety Density Seed
Block Beans Maize Beans Maize Fertiliser Treatment
1 1 A 8 16 100 NO
1 2 A 12 16 100 YES
1 3 B 12 16 100 NO
1 3 A 16 16 100 YES
1 2 B 16 16 100 NO
1 2 A 16 16 300 YES
1 3 A 12 16 300 NO
1 3 B 16 16 300 YES
2 1 A 8 16 100 YES
2 2 A 12 16 100 NO
2 3 A 12 16 100 YES
2 2 A 16 16 100 NO
2 2 B 16 16 300 YES
2 2 A 12 16 300 NO
2 3 B 12 16 300 YES
2 3 B 16 16 100 NO
All but three of the factorial combinations of bean variety, maize variety, bean density and fertilizer level
are included, with two standard treatments repeated in each block, and the seed treatment imposed as an
extra across the sets of treatments in each block.
There are always two levels of replication to consider for on-farm trials. Replication within each farm and
replication between farms (and years). The purposes of these two forms are rather different. Replication
within a farm provides a (usually) rather limited level of information about the precision of the results from
that farm and also gives some protection against loss of individual plot information. Replication between
farms provides information about the overall precision of the average results over farms and also allows the
estimation of the variability of results between locations (and years).
The replication of the set of experimental treatments within sites was discussed in the report from my
previous consultancy My conclusions then remain valid. Where there is a minimum of five sites, chosen
fairly carefully to represent the variation between sites, then the use of two replicates of the set of
treatments per site is sensible, except in those experiments where the primary interest is in the variation of
effects over sites when a large number of sites is needed and within-site variation has little benefit. If fewer
than five sites are used then it is likely that the replication may need to be more than two to achieve the
necessary within-site precision.
One point that must never be forgotten is that factorial structures always provide hidden replication and
when quite large factorial structures(at least 16 treatment combinations) are being considered, as they must
be if maximum use is to be made of resources, then the insurance benefits of two explicit replicates are
much less important since even with several missing values the factorial structure permits the
reconstruction of values for all combinations.
7. Different Treatment Subsets at Different Farms
When discussing the choice of experimental treatments in section 3 we considered how a subset of the
possibly interesting treatment combinations should be selected in such a way as to give good information
about as many of the more important treatment effects as possible. Suppose we have a particular situation
where we only have room for six combinations from four two-level factors, and these must include both
(0000) and (1111). Suitable subsets would be
If the experiment is to be at a number of farms there is a choice between selecting one subset and using it at
all farms or using different subsets at different farms. Since the different subsets each provide only partial
information and the partiality varies there is clearly advantage in changing the subsets between farms so
that the combined information will be greater.
The following material from the 1989 Consultancy Report provides some additional ideas on the design
and analysis of different factorial subjects on different farms.
7.1 Some Possible Development of Designs
With the development of computers it is possible to develop designs for experiments beyond the ideas of
the 1930's which account for almost all the experimental designs used in agricultural research to-day
(thirty years after the advent of computers).
The crucial ideas of experimental design are the use of blocking based on recognition of patterns of likely
similarity among the available plots and the use of factorial structures, particularly subsets, to provide
efficient information about main effects and 2-factor interactions. The advantages of factorial subsets can
be seen by comparing a half-replicate of a 24 with various sets of non-factorial treatments. Consider the
following three sets of treatment combinations (FP = Farmer's Practice).
Design 1 Design 2 Design 3
FP FP FP
FP+A FP+A FP+A+B
FP+B FP+A+B FP+A+C
FP+C FP+A+B+C FP+A+D
FP+D FP+A+B+C+D FP+B+C
If we consider only the estimation of (+A), (+B), (+C), and (+D), then designs 1 and 2 each provide less
than 25% of the information from design 3. Allowing for the difference in numbers of observations designs
1 and 2 are still less than 40% as efficient as design 3.
The reasons why design 3 provides so much more information are:
(i) That it includes equal numbers of observations with and without A
(ii) Those with A and those without A each include B, C and D twice.
The first point ensures that as much information as possible about A is available; the second ensures that
that information is completely unpolluted by the effects of B, C, and D.
Suppose we consider a fourth design which is allowed only six observations. We would like to have three
with A and three without A and similarly for B, C and D. We would also like to minimize the interference
between our four effects. The following design does quite well.
The three observations for A include also two B, one C and one D, while those without A include one B,
two C and two D. Given that each of B, C and D occur twice, this arrangement cannot be improved.
In thinking about constructing efficient designs with factorial subsets, we must concentrate on getting the
balance of "with" and "without" right for each factor and then on minimizing interference. A simple half-
replicate, such as design 3 allows a perfect solution, but other subsets can be nearly as good.
Of course all thi discussion has ignored the possibility of interaction. Fractions of the complete factorial
set constructed in the way outlined also provide the best possible information about interaction [Note that
design 3 has two observations each for (i) A but not B, (ii) B but not A, (iii) both A and B, and (iv) both A
and B, and that interference from C and D is zero]. Designs 1 and 2 in contrast provide no information on
If we are considering not the choice of a subset of treatments but different subsets for different blocks
within a farm or for different farms, then the same principles apply. All other things being equal, we would
prefer not to repeat subsets, but to use subsets not involving the same treatments. Thus, if design 3 were
used in one block (or one farm), the ideal subset for a second block (or farm) would be:
The combination of one block of Design 3 and one block of design 5 produces a classical confounded
design with the four-factor interaction confounded. This would be a very good design if the circumstances
were to be exactly appropriate. However, just like any other recipe design, it should be used only when the
conditions of proper blocking, total resources and relevance of questions are suitable. If blocks of size 5 or
6 or 10 or 12 are clearly more suitable, then we should construct designs for those block sizes, and the
arguments for numbers of treatments per farm are identical.
Of course there are questions about how designs such as 3,4 or 5 will be perceived by the farmer (perhaps
also by the researcher's colleagues). This may lead to some modifications in designs and some explanation
of designs in terms of capacity to examine changes, both individually and in combination. There is
considerable further scope for developing designs and explanation of these principles.
The analysis of designs involving subsets of factorial structures allocated either to different farms or to
different blocks within a farm can be completed on any computer program that can handle multiple
regression analysis. This requires the definition of variables to represent the effects of interest together with
dummy variables representing block and site differences.
To illustrate the analysis, we consider an experiment at three sites at each of which duplicate plots of a
(different) subset of treatment combinations are used to comprise the experiment for that site. The three site
experiments have six, six and nine treatments respectively; the first uses design 4, the last design 5 plus an
FP treatment, and the second a design like design 4 chosen to complement the other two by including
almost all the factorial combinations in the total experiment.
The designs and the yield data (artificial) are given in Table 2. The data format for any multiple regression
program is shown in Table 3. The results (from GENSTAT) are shown in Table 4.
This is the basic analysis which provides estimates of A, B, C, and D main effects. Interaction effects can
be estimated by constructing additional columns in Table 3 from the columns representing the relevant
Factors. Note that the first five columns after the yield column are the dummy factors for blocks and sites.
Analyses of variance to show SS for individual effects can also be constructed though the t values provide
There are some correlations between the different effect estimates and these could be checked by
requesting the correlation matrix for the estimates. For the model fitted here, the correlations are not large
and can be ignored.
8. (Non-complete) Block Designs
We consider here the situation where one or more replicates of a set of treatments are to be divided into
blocks and where the block size is less than the number of treatments. First, suppose that the experimental
treatments are simply an unstructured set or, if there is some structure the important comparisons are
between particular combinations rather than main effects and interactions. Then the division of each
replicate into two or more blocks should be such that the divisions in different replicates are as different as
possible and those treatments whose comparison is more important should tend to occur together in a
block. The sense of "as different as possible" is that the treatments occurring together in a block in one
replicate should be distributed evenly between the various blocks in each other replicate.
For structured treatment sets we first identify the treatment contrasts which are important. In a factorial
structure these will almost always be the main effects, and probably also two-factor interactions. In other
treatment structures the treatment contrasts will correspond to the questions which prompted the choice of
the particular treatments. For these important contrasts we must arrange that each block provides maximal
information. Thus, for a main effect, al-a2, each block should include equal numbers of al and a2
observations. For an interaction effect, (al-a2)(bl-b2), the four combinations, albl, alb2, a2bl, a2b2
should all occur equally frequently in each block. For a contrast between a control group of treatments and
an innovative set of treatments, each block should contain the same proportion of control:innovative.
In some cases the obvious block size does not allow a complete replicate of the set of experimental
treatments to be contained in a set of blocks. In these cases we try to arrange that each pair of treatments
occurs together in a block as nearly equally frequently as possibly. The requirement of equal occurrence for
main effects still applies.
Examples of the construction of designs are included in part B.
9. Precision in Incomplete Block Designs
In incomplete block designs we trade the hope of a reduced value of sigma, the random variance (estimated
by the error mean square) against some loss of information because we cannot compare each treatment
with every other treatment in each block. One exception to this balancing act is confounded designs where
the effects that can be estimated in each block suffer no loss of information to offset the gain from a
smaller value of sigma.
Although we cannot estimate in advance the gain achieved through a reduction in sigma, we can assess the
loss of information from having to compare treatments occurring in different blocks indirectly. If treatment
A occurs in block 1 and treatment B in block 2 and if treatments C,D and E occur in both then A and B
may be compared by comparing each with the average of (C,D,E). The use of the intermediary treatments
reduces the precision of the A-B difference by 33%. In incomplete block designs each treatment occurs
several times and the web of comparisons through intennediaries becomes very complex.
To assess the loss of information from the use of a proposed design we can pre-test the design using a
statistical analysis package. Any package capable of handling the analysis of a general block-treatment
design would provide the information, but the simplest method available at CIMMYT is to use the
statistical package REML. The method is illustrated in the attached output for a design comparing twelve
treatments in six blocks of six plots per block which is attached to the end of this document (3A).
The information required by REML is the block and treatment identification for each plot and a set of data
values. For the illustration the plot allocation to blocks is (in plot order)
S 1 1 1 1 1 2 2 2 2 2 2 3 3 3 3 3 3
4 4 4 4 4 4 5 5 5 5 5 5 6 6 6 6 6 6
and the treatment allocation (same order) is
1 2 7 8 9 11 3 4 5 6 10 12 1 3 6 8 10 11
2 4 5 7 9 12 1 4 6 7 9 10 2 3 5 8 11 12
For data we use any set of simple numbers (all different)
1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18
19 20 21 22 23 24 25 26 27 28 29 30 31 32 33 34 35 36
The output summarises the standard errors for comparing pairs of treatments by giving the average,
maximum and minimum standard errors. Since we have used nonsense data these will be nonsense
standard errors. However, the relative values will be correct because relative precision depends only on the
design and not on the data. Further REML prints the value of a2, the random variance. If we divide each
standard error by the square root of sigma squared we obtain the standard errors as multiples of sigma. We
can therefore assess exactly the loss of information which we expect to more than outweigh by the
reduction in the value of sigma
In the attached example the standard errors for the nonsense data are
AVERAGE 0.385 MAXIMUM 0.404 MINIMUM 0.361
The value of a2 is 0.196 so that a is 0.443 and the standard errors are a multiplied by
AVERAGE 0.869 MAXIMUM 0.912 MINIMUM 0.815
Note first that the range of standard errors is about 5% either side of the average so that a single standard
could be used in summarising the results of the experiment. Second the minimum possible standard error
for comparing two treatments with three observations each is
a4(2/3) = 0.816o
which is the same (apart from rounding error) as the minimum achieved in our example design.
In general incomplete block designs are much more efficient than might initially be expected. A rough
guide to precision in incomplete block designs is derived by considering the minimum possible variance
between two treatment means
MINVAR = 02 x 2/r
where r is the replication per treatment;
and the maximum possible variance which is
MAXVAR = 02 x 2/k
where k is the average number of times that treatment pairs occur together in a block.
An excellent approximation to the average variance for treatment pair differences is then
VAR = MINVAR + (MAXVAR MINVAR)/t
where t is the number of treatments.
For the example r = 3. The number of pairwise comparisons in each block is 15, so that over the set of
blocks there are 6x15 = 90 pairwise comparisons within blocks and there are 66 treatment pairs. Thus k =
MINVAR = 02 x2/3 = 0.66702
MAXVAR = 02 x(2x66/90) = 1.467o2
VAR = 02 0.667 + o2 (1.467 0.667)/12
giving an approximate standard error of 0.856 a.
10. Loss of Plots/Sites
The loss of individual plot data causes, if anything, rather less problem for incomplete block designs than
for complete block designs. For complete block designs the pattern of block-treatment structure is no
longer complete when plots are missing and the data should be analysed as an incomplete block design.
The alternative of estimating missing values is only approximately correct, is a throwback to the pre-
computer days, and should not be necessary. For incomplete block designs the loss of plot data produces a
different incomplete block design but no change in principle. We simply analyse the data we do have.
In either situation, if several, or all, plots of a particular treatment are lost the information about that
treatment is badly affected, but the two design types suffer equally. The loss will be reduced when factorial
treatment structure is used (complete or incomplete) because of the hidden replication benefits.
When different treatment subsets are used at different locations the total loss of some sites should not cause
problems provided the different treatment subsets have been chosen so that each location provides
information on all or most of the factor main effects and two-factor interactions.
11. Analysis and Computers
The analysis of experimental data is, rightly, increasingly handled by the use of computer packages. These
vary from those which can analyse a very restricted set of tightly specified designs to general statistical
packages which can handle almost any design structure.
Where computer facilities are available the analysis of incomplete block designs can be managed using a
general package, the most powerful being REML (the form of analysis information being illustrated in the
example attached to this document), GENSTAT and, rather less informatively, by SAS. In the absence of
any of these packages any block-treatment design structure can be analysed by a multiple regression
package, as illustrated in my report on my 1989 consultancy, by defining a regression variable for each
block and each treatment except block I and treatment 1. The regression coefficients then estimate the
difference of each block, or treatment, from the first block, or treatment.
To the best of my knowledge (limited) the only smaller package designed for PC's which offers the
possibility for analysing incomplete block designs is INSTAT (and even there I am not sure if that option is
yet available in the presently commercially available version). However it can only be a matter of a short
time before the better PC packages have facilities for analysing incomplete block designs.
Finally, it must be emphasised that it is possible to analyse data from any incomplete block design using
only a small pocket calculator using the method of sweeping. This methci is described in detail in part C.
The only arithmetical operations involved are
(i) the calculation of means,
(ii) subtraction, and
(iii) the summing of squares.
For a large or complex design these operations are repeated many times. If computer facilities are available
then of course they should be used. However sweeping is always a possible method of analysis and should
be understood by all users of analysis of variance, not least because it displays the logic of the analysis
clearly and because it is the principle utilised in the better statistical analysis packages.
Table 1. Plot treatments at a site
Weed Zero N 80 k2/ha N.
Density Control Phosphorus Rep 1 Rep 2 Rep 1 Rep 2
High No Zero x x x x
High No 40 kg/ha x x x x
High Yes Zero x x x x
High Yes 40 kg/ha x x x x
Low No Zero x x x x
Low No 40 kg/ha x x x x
Low Yes Zero x x x x
Low Yes 40 kg/ha x x x x
Table 2. Designs and results for three sites.
Block 1 Block 2
Table 3. Data information for multiple regression for designs of Table 2
Site 1 Site 2 Site 3 Factor
Yield Block Block Block Block Block A B C D
Table 4. GENSTAT output for data from Table 2.
Estimates of regression coefficient
Estimate SE t
Constant (site I block 1) 1672 257 6.51
Site 1 block 2 0 296 0.00
Site 2 block 1 500 296 1.69
Site 2 block 2 117 296 0.39
Site 3 block 1 629 270 2.33
Site 3 block 2 540 270 2.00
A 851 159 5.36
B 121 159 0.76
C 211 159 1.33
D 541 159 3.41
Analysis of Variance Summary
df SS MS
Regression 9 14266827 1585203
Residual 32 8382935 261967
Total 41 22649762
(a) Initial data and individual trends
b) Means and adjustment
Fig. 1. Covariance Adjustment
REML Analysis by Residual Maximum Likelihood
(C) Scottish Agricultural Statistics Service
University of Edinburgh
Analysis of Design 1 with unstructured treatments
Block 6 1 2 3 4 5 6
FACTOR Block CREATED
Treat 12 ABCDE F G HI JKL
FACTOR Treat CREATED
'FIXED' Block + Treat
FIXED MODEL READ
'READFREE' 1 Block
1 1 1 1 1 1
2 2 2 2 2 2
3 3 3 3 3 3
4 4 4 4 4 4
5 5 5 5 5 5
6 6 6 6 6 6
DATA SET READ
'READFREE' 1 Treat
A B G H I K
C D E F J L
A C F H J K
B D E G I L
A D F G I J
B C E H K L
DATA SET READ
'READFREE' 1 Yield
1 2 3 4 5 6
7 8 9 10 11 12
13 14 15 16 17 18
19 20 21 22 23 24
25 26 27 28 29 30
31 32 33 34 35 36
DATA SET READ
'MEAN EFFECT' Treat
Echos the input data
to the output stream
as they a reread
Table 5 (con't)
*** No RANDOM model specified RESIDUAL term only will be used
36 EXPERIMENTAL UNITS
FIXED DF 17
REML RESIDUAL MAXIMUM LIKELIHOOD COMPONENTS OF VARIANCE
ITERATION NO 2
Analysis of Design 1 with unstructured treatments
ITERATIONS HAVE CONVERGED
MEAN EFFES Best Linear Unbtased Estimates
MEAN EFFECTS (B.L.U.E.'S)Jof Treat
A B C D E F G from
15.917 16.361 16.750 16.972 18.083 18.306 18.583 directive
H I J K L MARGIN EFFECT'
19.028 19.917 20.306 20.694 21.083 18.500
STANDARD ERROR OF DIFFERENCES BETWEEN PAIRS
AVERAGE 0.385 MAXIMUM 0.404 MINIMUM 0.361
CANONICAL DECOMPOSITION T.INV INF MX.T TO BE DIAGONAL
DIAGONALISED INVERSE INF MATRIX (D)
SIGMA SQUARED 0.004 from
Coefficient matrix (T)
SQUARED ERROR mean square ERROR degrees
TC = T. (Components_fromg revio s_iteration) and 2*TC*TC/D i.e
Approximate Stratum Variances and effective d
SIGMA SQUARED 0.196 19.000
NOTE: In this example, the MINIMUM standard error
of differences between pairs (0361) is the
standard error of differences between pairs
of treatments concurring once, as for instance
treatments A and B. Whereas the MAXIMUM
(0.404) is the standard error of differences
between pairs of treatments not concurring
at all, asfor instance A andE.
(a) Initial data and
ni di.4..Al .....na
b) Means and adjustment
10 20 3(
Density (plan t/plot)
Fig. 1 Covariance Adjustment.
u~ r ~lruo
EXPERIMENTAL DESIGN PROBLEM EXAMPLES
These examples are intended to illustrate the general principles for fitting subsets of treatments into sets of
blocks, the sizes of the blocks being determined so as to provide homogeneous plots within a block. In
most cases it will be assumed that
(i) the set of treatments is pre-defined, possibly with factorial structure (complete or incomplete),
(ii) the experiment is to include 2, 3 or 4 replicates of the treatment set,
(iii) each replicate is to be divided into two or more blocks of the same or similar size.
The initial set of problems have been generated from the problems that (should) have been solved for
various on-farm experiments at Poza Rica and Chalco in early 1990. Other problems from the past, or for
the future, or purely hypothetical, will be added as they are suggested to me. (Such suggestions will be
1.1 Treatments Without Structure
Ideally, each pair of treatments should occur together (in a block) equally frequently, or at worst, with
frequencies differing by at most one. Particularly with relatively small numbers of treatments (e.g.twelve),
this is not always possible to achieve. So we need some "rules" for the division into blocks in each replicate
such that the resulting design will come as near to the equal pair-wise occurrence as possible.
Where each of several replicates is split into blocks the splits in the different replicates should be as
different as possible. This is to be interpreted in the sense that, for the first two replicates, each block group
of treatments in the first replicate should be split as equally as possible between the blocks of the second
replicate. For further replicates the division of treatments into blocks should be as different as possible (in
the same sense) to each of the divisions in previous blocks
1.2 Complete Factorial Structure
In each replicate the division into blocks should be such that for each factor in each block the levels of that
factor should occur as equally as possible. This requirement is intended to maximize the information about
each factor main effect. Further, for each pair of factors for which the two-factor interaction is likely to be
important, all combinations of levels from those two factors should occur as evenly as possible in each
block. Where there are still arbitrary choices to be made the equal occurrence in each block of all
combinations of levels of three factors should be aimed at.
1.3 Other Structure
For incomplete factorial structures the general principle about equal occurrence in each block of the levels
of each factor and of the combinations of levels of pairs of factors still applies. When the set of treatments
includes some non-factorial structure, the important treatment contrasts should be identified. For each
contrast each block should contain a similar balance between the groups of treatments compared in the
2.1 Twelve Treatments in Six Blocks of Six
This is the actual problem solved for the Chalco experiments being initiated at the beginning of April 1990.
Twelve, being three sowing dates x four varieties
V1 V2 V3 V4
DI 1 2 3 4
D2 5 6 7 8
D3 9 10 11 12
The factorial structure is not important for the design of this experiment. All comparisons between
treatment combinations are important. Comparisons between treatments (1,2,5,6,7,8,11 and 12) are
expected to be more important as these combinations are expected to be more successful.
Replicates and Blocks:
Each replicate is to occupy a 4 x 3 grid of plots. The plots are approximately square. It is thought that the
total area of each replicate may be rather too large to be properly homogeneous and that using two blocks
of 2 x 3 within each replicate might provide greater homogeneity within blocks (and correspondingly
differences between blocks within each replicate). If the differences between blocks within replicates turn
out to be negligible the analysis can revert to that for a RCBD since each replicate is considered as a whole
as well as being split into two blocks.
We wish to divide the twelve treatments into two groups(blocks) of six in each replicate in such a way that
the divisions are as different as possible in the three replicates. The choice is too wide and we may find it
helpful to use the two-factor structure to start the design. For the first replicate let the division be such that
each block includes two combinations for each date and at least one combination for each variety. We try
Block 1 (1,2,7,8,9,11) Block 2 (3,4,5,6,10,12)
Now the next pair of blocks must each include three combinations from block 1 and three from block 2. It
is still helpful to use the date and variety structure. So we try
Block 3 (1,3,6,8,11,12) Block 4 (2,4,5,7,9,12)
Quite a number of treatment pairs have not yet occurred together in a block (1 and 4, 2 and 3, 5 and 8, 6
and 7 and so on). We try to remember to include these as well as splitting treatments in the third replicate
so that each block includes three from each of blocks 1, 2, 3 and 4. There are still plenty of good solutions
and we try
Block 5 (1,4,6,7,9,10) Block 6 (2,3,5,8,11,12)
An alternative design with many similar patterns, but motivated by a strong desire to compare treatments 1
with 12, and 2 with 11, produced the following
Block 3 (1,4,6,7,10,12)
Block 5 (1,3,5,8,10,12)
Block 2 (3,4,5,6,9,10)
Block 4 (2 3 5 89 11)
Block 6 (2,4,6,7,9,11)
It is possible to give confidence in a proposed design by calculating, before the use of the design, the
precision that will be achieved. The relative precision of different treatment comparisons within a design,
and of alternative designs, is a property of the designs. Of course the absolute precision achieved will
depend on the data and obviously that is not available before the experiment. However we can calculate the
relative precision in advance with various computer programs (details given in main paper on "Design of
For the first design the range of standard errors for estimated treatment differences is
0.82 a to 0.91 a with a mean of 0.87 a
where a is the standard deviation of the random variation, estimated by the square root of the Error Mean
The smallest achievable standard error, with three observations per treatment would be
,(2a2/3) = 0.82 a
so that the precision of the design is really very good. Certainly we should intend to use only a single
standard error when presenting the treatment results from the analysis of the six block design.
For the second design with particular emphasis on comparing treatments 1 with 12 and 2 with 11 (this was
the design actually used at Chalco) the range of standard errors for estimated treatment differences is
0.82 a to 0.91 a with a mean of 0.87 a
exactly the same, to two figures as for the first design.
We consider four other designs to see how quickly the very high and consistent precision in both designs
thus far deteriorates as we take less thought over the design. We shall think of the treatments in terms of
their Varieties by Dates structure.
V1 V2 V3 V4
D1 1 2 3 4
D2 5 6 7 8
D3 9 10 11 12
Suppose that we decided in the first replicate to put varieties 1 and 2 in block 1 and varieties 3 and 4 in
block 2. In the second replicate varieties I and 3 in block 3, varieties 2 and 4 in block, and the other
variety pairings in the third replicate, producing the following (rather like a split-plot design!)
Block 1 (1,2,5,6,9,10) Block 2 (3,4,7,8,11,12)
Block 3 (1,3,5,7,9,11) Block 4 (2,4,6,8,10,12)
Block 5 (1,4,5,8,9,12) Block 6 (2,3,6,7,10,11)
The range of standard errors for estimated treatment differences is
0.82 a to 0.88 o with a mean of 0.87 a,
fractionally better than the two earlier designs but for all practical purposes unchanged.
Suppose we think in a "split-plot" pattern keeping similar date treatments together.
Block 1 (1,2,3,4,5,6) Block 2 (7,8,9,10,11,12)
Block 3 (1,2,3,4,11,12) Block 4 (5,6,7,8,9,10)
Block 5 (1,2,9,10,11,12) Block 6 (3,4,5,6,7,8)
The range of standard errors for estimated treatment differences is
0.82 a to 0.93 a with a mean of 0.88 o.
This time the precision is marginally worse than our first two designs but again the change is insignificant.
Suppose we just try pretty patterns within the structured set of treatments.
Block 1 (1,3,6,8,9,11) Block 2 (2,4,5,7,10,12)
Block 3 (1,2,7,8,9,10) Block 4 (3,4,5,6,11,12)
Block 5 (1,3,6,8,9,11) Block 6 (2,4,5,7,10,12)
The range of standard errors for estimated treatment differences is
0.82 a to 0.97 o with a mean of 0.90 a.
A little bit worse both in mean S.E. and in the increased range but really the penalty for lack of thought,
and even for repearing the division of replicate I in replicate 3 is very small.
Finally we actually try to make the divisions into two blocks unnecessarily similar in the different
Block 1 (1,2,6,7,11,12) Block 2 (3,4,5,8,9,10)
Block 3 (1,3,5,8,9,11) Block 4 (2,4,6,7,10,12)
Block 5 (1,4,5,8,9,10) Block 6 (2,3,6,7,11,12)
The range of standard errors for estimated treatment differences is
0.82 o to 1.10 a with a mean of 0.90 a.
Well, we have produced at least one rather poor precision comparison but the mean is still not much wo,-e
than our best efforts and even using the mean S.E. for the maximum S.E. would hardly be a disaster. A'
least for this design problem the moral is that if one makes any real attempt to produce a design according
to the defined principles it is actually rather difficult not to arrive at a good design.
2.2 Sixteen Treatments in a 4x4 Lattice
This is a problem for which there is a classical statistical design solution (lattice ) but it is included here to
illustrate the methods. The experiment, at Poza Rica, is to compare 16 varieties for drought tolerance. Four
replicates, each split into four blocks are to be used.
This time we have no structure to guide us so we make an arbitrary split in the first replicate.
Block 1 Block 2 Block 3 Block 4
(1,2,3,4) (5,6,7,8) (9,10,11,12) (13,14,15,16)
For the second replicate each block must include one variety from each of the first four blocks.
Block 5 Block 6 Block 7 Block 8
(1,5,9,13) (2,6,10,14) (3,7,11,15) (4,8,12,16)
For the third replicate each block must include one variety from each of the first four blocks and one
variety from each of the second four blocks. This requires slightly more thought than the second replicate
but can be solved for the first block(9) and systematically thereafter.
Block 9 Block 10 Block 11 Block 12
(1,6,11,16) (2,5,12,15) (3,8,9,14) (4,7,10,13)
That was probably the hardest stage, and for the fourth replicate the choices are reduced and the problem
gets a little easier. If we had made a less fortunate choice in the third replicate then we could have found
ourselves with no choice in the fourth replicate. We would then have had to try a different third replicate.
Block 13 Block 14 Block 15 Block 16
(1,7,12,14) (2,8,11,13) (3,5.10,16) (4,6,9,15)
This completes the required design. Note that if a fifth replicate were needed there is one more division
into four blocks which brings together all those pairs not previously linked. Note also that if we had only
needed three replicates we could have stopped after the third because of the sequential nature of the
The range of standard errors for the estimated treatment differences is
0.791 a to 0.817 a with a mean of 0.796 o.
The minimum possible S.E. would be
a0 q(2/4) = 0.707 o.
But, of course, with no pair of treatments repeated together we cannot hope to be very close to that. This is
a classical design of known high efficiency so that we should not be surprised that the range is very small.
We can recognize also that for the design in blocks of four to be superior to the RCB in blocks of 16 the
error variance for the blocks of four needs to be reduced by a factor of only
(0.707/0.796)2 = 0.79
which should be more than likely with a sensible choice of blocks.
2.3 Only 15 varieties in Blocks of 3 and 4, or all 5
Suppose the number of varieties had been 15. There are two interesting alternatives. One would be to use
the design for example 2 simply omitting one of the treatments and using the resulting mixture of blocks of
three and four plots. The other would be to use three blocks of five plots per replicate.
For the first design we omit treatment 13 (arbitrarily) from the design, renumbering the subsequent
treatments, and the resulting design is
Block 1 Block 2 Block 3 Block 4
(1,2,3,4) (5,6,7,8) (9,10,11,12) (14.15.16)
Block 5 Block 6 Block 7 Block 8
(1,5,9) (2,6,10,13) (3,7,11,14) (4.8,12,15)
Block 9 Block 10 Block 11 Block 12
(1,6,11,15) (2,5,12,14) (3,8,9,13) (4,7,10)
Block 13 Block 14 Block 15 Block 16
(1,7,12,13) (2,8,11) (3,5,10,15) (4,6,9,14)
For the design in blocks of five plots, we start by using an arbitrary split into the three blocks.
Block 1 Block 2 Block 3
(1,2,3,4,5) (6,7,8,9,10) (11,12,13,14,15)
Now each block in the second replicate must have one or two varieties from each of the first three blocks.
Block 4 Block 5 Block 6
(1,6,7,11,12) (2,3,8,13,14) (4,5,9,10,15)
Note that we inevitably had to repeat some joint occurrences (6 with 7, 2 with 3,etc.). It is probably useful
at this stage to keep a note of which varieties have occurred with variety 1, with 2, and so on. Whether or
not this is done we move on to the third replicate.
In the fourth replicate we try both to include those pairs of treatments which have not previously occurred
together and to avoid any third repetitions of pairs
The ranges of standard errors are:
In blocks of 3 and 4
0.790 a to 0.828 a with a mean of 0.803 a.
In blocks of 5
0.730 a to 0.809 a with a mean of 0.774 o.
Again the precision of both designs is good compared with the minimum possible S.E. of 0.707 a (and
remembering that the a in smaller blocks should be a good deal smaller). The unequal blocks of the first
design and the loss of balance compared with the exact lattice have had only a marginal effect. The slightly
less friendly blocks of five have produced a larger range (10% compared with 5%) but the average S.E.
comes down (relative to a) quite a bit with the blocks of 5.
2 4 Six Treatments in Three Blocks of Eight Plots.
An experiment from Poza Rica, mentioned in part A, in the section on variation at the farm level. Six
varieties are to be compared and the natural blocking pattern for the 24 plots is three groups (rows) of eight
plots per group. Each treatment will be replicated four times and the design problem is how to allocate sets
of treatments to the three groups of eight plots.
The allocation must allow as many comparisons between different treatments in a block as possible.
Therefore each block must include each treatment at least once.
Block 1 treatments 1 2 3 4 5 6 ? 7
Block 2 treatments 1 2 3 4 5 6 ? ?
Block 3 Treatments 1 2 3 4 5 6 ? ?
We have one more observation for each treatment and the six remaining plots occur two in each of the
three blocks. We therefore have no choice but to add two different treatments to each block. The choice of
which pair of treatments to duplicate together is arbitrary; the treatments that are duplicated together will
be slightly more precisely compared than other treatment pairs. The resulting block-treatment allocation is
Block 1 treatments 1 2 3 4 5 6 1 2
Block 2 treatments 1 2 3 4 5 6 3 5
Block 3 treatments 1 2 3 4 5 6 4 6
When the treatments are randomized in each block all the eight "treatments" listed above are considered
equally. The resulting randomization could look like
Plot 1 2 3 4 5 6 7 8
Block 1 5 1 4 2 1 3 2 6
Block 2 5 3 1 5 3 6 4 2
Block 3 6 4 4 1 2 6 5 3
Randomization always produces some odd-looking patterns and provided the blocking system correctly
identifies the underlying pattern of plot-to-plot variation any randomisation is acceptable. If some
randomisation results make us uncomfortable then the answer is to redefine the blocking system, not to try
another randomisation. For example, in the above case we could decide to work with six blocks of four
plots (a half-row per block) or to impose a column classification as well as a row classification. Neither of
these would be appropriate here, I believe, since the rows do genuinely appear to be the most appropriate
definition of blocks.
The range of standard errors for estimated treatment differences is
0.707 a to 0.718 a with a mean of 0.717 a.
Compared with the minimum possible S.E. of 0.707 c the use of the correct form of blocking has produced
virtually no penalty of variable precision.
2.5 Fourteen Treatments in Blocks of 4, 5 and 6
The experiment includes 14 treatments, being seven varieties combined with two levels of nitrogen. The
important treatment comparisons will be the difference between the two nitrogen levels for each variety
and the differences between varieties for each nitrogen level. The nitrogen main effect is well-known and
does not need to be reconfirmed.
The 28 plots for the two replicates of the 14 treatments are in two rows of ten plots and two rows of four
plots. Differences between rows are likely to be large since the rows are at different contour levels.
Arrangement of plots:
28 27 26 25
21 22 23 24
20 19 18 17 16 15 14 13 12 11
1 2 3 4 5 6 7 8 9 10
Each row of four plots should probably be treated as a block and the first replicate should be completed
with the block of plots 15 to 20. The second replicate has one block of four plots (11 to 14) and the other
ten plots should be split into two blocks of five plots. The block pattern is therefore
1 1 1 1
2 2 2 2
3 3 3 3 3 3 4 4 4 4
5 5 5 5 5 6 6 6 6 6
We now have to divide the fourteen treatments into blocks of 4,4 and 6 in the first replicate, and into blocks
of 4, 5 and 5 in the second replicate. The allocations should be such that treatments which occur together in
a block in the first replicate do not again occur together in a block in the second replicate. We shall see that
this requirement cannot be completely satisfied.
The allocation for the first replicate must be
(1,2,3,4), (5,6,7,8) and (9,10,11,12,13,14)
where we can decide later which actual treatments correspond to the labels 1 to 14. In the second replicate
the treatments in a block in the first replicate should be evenly spread between the three blocks of the
second replicate. This leads quite directly to
(1,5,9,10), (2,3,6,11,12) and (4,7,8,13,14).
Five pairs of treatments (2.3), (7,8), (9,10), (11,12) and (13,14) occur together twice and we should try to
ensure that these are treatment combinations which we would particularly like to be precisely compared.
Note, however, that the random variance with the blocks of 4, 5 and 6 should be much smaller than the
random variance within complete blocks of 14 plots ( 1 to 14, and 14 to 28) as originally planned so that
treatment comparisons should be more precise in the proposed design.
The range of standard errors for estimated treatment differences is
1.00 a to 1.26 a with a mean of 1.15 a.
Compared with the precision results for our previous designs the variation here is rather disappointing. The
minimum possible S.E. with blocks of 14 is 1.00 0(14) so we would be very confident that our more
sensible blocks will reduce a sufficiently that all S.E.'s will be smaller with the new design. The decision
on whether to use the average S.E. is marginal but the maximum would be only 10% higher than the
average so I would decide to use the average on the basis that if out S.E.'s are only 10% out from an
ordinary analysis of variance we're doing pretty well.
2.6 Factorial Structure in an Unreplicated Trial
This trial at Poza Rica Station is described as an unreplicated observation trial and I have not seen the
location of the trial. However since there are 36 treatment combinations I would question why it was not
designed as an experiment. With 36 treatment combinations it is by no means clear that direct replication is
necessary since hidden replication may be sufficient.
The 36 treatment combinations are
6 herbicides x 2 cover crops x 3 planting dates.
Assume that we are interested in main effects and in the combined effects of each pair of factors. The 36
plots should probably be grouped in six blocks of six plots per block, though detailed examination of the
site might suggest alternative blocking patterns. In deciding the allocation of treatment combinations to
blocks we would try to arrange
(i) all six herbicides (h) in each block,
(ii) both cover crops (c) to occur three times in each block,
(iii) each planting date (d) to occur twice in each block,
(iv) all six combinations of cover crop x planting date to occur in each block.
Other requirements for equal occurrence of combinations of pairs of factors in each block are impossible in
blocks of six plots (Using three blocks of twelve plots would allow all combinations of herbicide x cover
crop in each block). The design for six-plot blocks is constructed by allocating the six cover crop x planting
dates to each block and then distributing the herbicide treatments so that no herbicide level is repeated in a
Block 1 Block 2 Block 3 Block 4 Block 5 Block 6
clplhl clplh2 clplh3 clplh4 clplh5 clplh6
clp2h2 clp2h4 clp2h6 clp2h3 clp2hl clp2h5
clp3h3 clp3h5 clp3hl clp3h2 clp3h6 clp3h4
c2plh4 c2plh3 c2plh5 c2plh6 c2plh2 c2plhl
c2p2h5 c2p2h6 c2p2h4 c2p2hl c2p2h3 c2p2h2
c2p3h6 c2p3hl c2p3h2 c2p3h5 c2p3h4 c2p3h3
(The choice for the allocation of herbicides to block,c,p combinations is very wide and is equivalent to a
Latin Square solution.)
The simple analysis of variance for the experimental data has the structure shown:
Cover crops 1
Planting dates 2
All information on main effects and the Cx P interaction is fully efficient. Some information on the H x C
and H x P can be recovered if a statistical package such as Genstat is used.
If the design with twelve plots in each of three blocks is used then the design will be:
Block 1 Block 2 Block 3
ciplhl clplh2 clplh3
clplh4 clplh5 clplh6
clp2h2 clp2h6 clp2h4
clp2h3 clp2hl clp2h5
clp3h5 clp3h4 clp3hl
clp3h6 clp3h3 clp3h2
c2plh3 c2plh6 c2plh4
c2plh5 c2plh2 c2plhl
c2p2h6 c2p2h3 c2p2h5
c2p2hl c2p2h4 c2p2h2
c2p3h4 c2p3hl c2p3h6
c2p3h2 c2p3h5 c2p3h3
The analysis of variance structure is shown
Cover crops 1
Planting dates 2
All information on the main effects and on the interactions of C with H and with P are fully efficient.
Again some information on H x P could be recovered with Genstat.
SWEEPING METHODS FOR ANALYSIS OF VARIANCE
The conventional approach to analysis of variance is to calculate sums of squares for recognizable
components of the total variation and to estimate the random variance from the remaining, "error", sum of
squares. In a simple design, such as the Randomized Complete Block Design we can recognize that
because of the orthogonality of blocks and treatments (each treatment occurs once in each block) the sums
of squares for blocks and for treatments can be calculated quite independently. In more complicated, but
still orthogonal,designs, such as two replicates of a factorial structure with four two-level factors arranged
in four blocks of eight plots per block, we have to identify from the properties of the design which
interaction sum of squares cannot be calculated (because of the confounding system).
In designs where each block contains a (different) subset of the set of treatments, blocks and treatments are
not orthogonal. The sums of squares for blocks and for treatments are not now calculable independently
and we have to think about the order in which we fit the terms "Blocks" and "Treatments" in the same way
as for fitting terms in multiple regression. That is, we calculate the sum of squares for Blocks (ignoring
treatments) and then the sum of squares for Treatments (after allowing for block differences).
For some particular designs, such as lattices or Balanced Incomplete Block Designs, standard methods for
calculating the analysis of variance are given in text books (from Cochran and Cox onwards) and are
available in some statistical computing packages. For other designs, with less regular patterns of treatment
subsets in blocks, the analysis of variance can be calculated using powerful packages such as GENSTAT or
(somewhat tediously) through a multiple regression package (an example of the multiple regression
approach is given in Document 3A, section 7).
Whether our experiment is simple or more complex there is an element of the "sausage machine" about the
calculations for the analysis of variance. This is particularly true of the calculation of the error sum of
squares. There is an alternative approach to the analysis of variance and the estimation of treatment and
block effects which, I believe, provides more insight into the concepts of the analysis and particularly the
error sum of squares. It is not new and is in fact the basis of some of the better (and more flexible)
statistical packages, but it does not appear to be widely known. Using this method we can analyse any
design structure with no more than a pocket calculator (though for really complex structures the
calculations may be rather tedious). The method is that of "Sweeping" the data.
In sweeping we identify the sets of effects (Blocks, Treatments, Main Effects, Main Plot Effects. Rows,
Columns) which we wish to allow for in our analysis. Each yield will be labelled by one effect from each
set: that is, each yield is in one block, has one treatment, etc. Essentially we define a model expressing the
yield for each plot as a sum of several components.
For each set of effects in turn we estimate the effects and then subtract from each yield the value of the
appropriate effect. After adjusting the yields to allow for all the relevant sets of effects we are left with the
residuals which represent the random variation, not explicable by the sets of effects which we have
considered, and the error sum of squares is simply the sum of the squared residuals. At any intermediate
stage of the analysis the sum of squares of the currently adjusted yields provides a measure of the variation
not yet accounted for.
Example 1: Randomized Complete Block Design
We stan with a RCBD example for eight varieties in three blocks (G.Edmeades Ghana data 83T1 sitel5).
We shall consider three components in our model:-
(1) the general mean
(2) the block effect
(3) the treatment effect
The separate consideration of the overall mean is not strictly necessary but is adopted to emphasize the
1 2 3
1 270 275 360
2 390 360 425
3 290 300 235
4 250 305 240
5 220 130 33;
6 315 270 315
7 365 290 285
8 285 275 365
-28 -23 +62
+92 +62 +127
-8 +2 -63
-48 +7 -58
-78 -168 +32
+17 -28 +17
+67 -8 -13
-13 -23 +67
Mean 0 -22 +21
We first calculate the overall average.
We now sweep out this average from each plot value.
The resulting residuals are the set of deviations
from the overall mean.
The sum of squares of these "residuals about
the overall mean" is the total sum of squares = 89951.
Next calculate the mean for each block
(note that apart from rounding error they sum to zero).
We now sweep out these values from the plot values in the corresponding blocks (note that we are
sometimes subtracting negative numbers, e.g. -23 -(-22) = : 62 -(-22) = +84 )
-28 -1 +41 +4
+92 +84 +106 +94
-8 +24 -84 -23
-48 +29 -79 -33
-78 -146 +11 -71
+17 -6 -4 +2
+67 +14 -34 +16
-13 -1 +46 +11
The sum of squares of these residuals = 82293,
and the change from the total SS is
the block sum of squares = 7658.
Finally we calculate the means for each treatment as shown above and sweep these from the residuals to
give the final residuals:
-32 -5 +37
-2 -10 +12
+15 +47 -61
-15 +62 -46
-7 -75 +82
+15 -8 -6
+51 -2 -50
-24 -12 +35
Notice that because we have swept out
the effects of blocks and treatments
the block and treatment totals of these
residuals are all zero (apart from
The sum of these final residuals is the error SS = 34779.
and the change from the previous sum of squares is the Treatment sum of squares = 47514
Explaining this example in detail has spread it out so now we bring all the calculations together in a
compact form. At the same time we combine the first two stages by calculating the block means directly.
Treat 1 2 3 Means
1 270 275 360 -28 -1 -41 +4 -32 -5 +37
2 390 360 425 +92 +84 +106 +94 -2 -10 +12
3 290 300 235 -8 +24 -84 -23 +15 +47 -61
4 250 305 240 -48 +29 -79 -33 -15 +62 -46
5 220 130 330 -78 -146 +11 -71 -7 -75 +82
6 315 270 315 +17 -6 -4 +2 +15 -8 -6
7 365 290 285 +67 +14 -34 +16 +51 -2 -50
8 285 275 365 -13 -1 +41 +11 -24 -12 +35
298 276 319 (Mean = 298)
0 -22 +21
The calculation of the block deviations from the overall mean provides an alternative way of calculating
the block sum of squares. We calculate the squares of the block effects for each plot and sum them, giving
8(02 + 222 + 212)
= 8(0+ 484+441) = 7600.
Because we have worked without decimals this is only approximately equal to the value calculated
previously. The corresponding calculation for the treatment sum of squares is
again approximately as before.
Finally we calculate the treatment means and the standard error of a difference between two means. The
treatment means are calculated by adding the treatment effects (+4, +94, -23, -33, -71, +2, +16 and +11) to
the overall mean to obtain
Treatment 1 2 3 4 5 6
Means 302 392 275 265 227 300
The standard of a difference is calculated in the usual way,
(2(34779/14)/3) = 41.
Example 2: Four two-level factors in 4 blocks of 8.
This is a confounded design with much more structure than the simple RCBD. The data are from an
experiment on factors of production in Ghana ( G:Edmeades 79T1 Site 1).
The data are as shown:
Treatment 1 2 3 4
We would normally think of the analysis in two stages. First the calculation of Block, Treatment and Error
sums of squares, and second the calculation of Main Effects and Interactions and their sums of squares.
With sweeping we do the same. First calculate block means and subtract them from the yields.
532 582 537 488 MEAN = 535
+38 +3 +20
-32 +212 +90
+3 +32 +18
+368 +103 +236
-52 -68 -60
-2 +78 +38
-32 -112 -72
+358 +167 +262
-177 -238 -208
-232 +23 -104
-227 -137 -182
+38 +72 +55
-47 -97 -72
-112 -78 -105
-12 -98 -55
+138 +138 +138
The treatment means have been calculated above and we subtract them from the current residuals to obtain
the purely random residuals.
The initial analysis of variance calculated from the block deviations from the overall mean. the treatment
effects and the final residuals is
SS df MS
Blocks 35350 3 11783
Treatments 543798 14 38843
Error 135209 14 9653
Note that there are only 14 df for the treatment SS because one treatment effect, the four factor interaction,
is identical with the difference between blocks (1-2+3-4).
For the second stage of the analysis we consider the treatment means in systematic order.
Treatment Effect Treatment Combination(ABCD)
+20 +90 +18 +236 1111 1112 1121 1122
-60 +38 -72 +262 1211 1212 1221 1222
-208 -104 -182 +55 2111 2112 2121 2122
-72 -105 -55 +138 2211 2212 2221 2222
The means for the two levels of factor A are:
Level 1 (+20 +90 +18 +236 -60 +38 -72 +262)/8 = +66
Level 2 (-208 -104 -182 +55 -72 -105 -55 +138)/8 = -67.
The SS for the Main Effect of A is (662 + 672)x16= 141512
and we subtract the means from the treatment effects to get:
-46 +24 -48 +170
-126 -28 -138 +196
-141 -37 -115 +122
-5 -38 +12 +205
The means for the two levels of factor B are -9 and +10, the SS for the Main Effect of B is 2888 and the
reduced effects are
-37 +33 -39 +179
-136 -38 -148 +186
-132 -28 -106 +131
-15 -48 +2 +195
The means for the two levels of factor C are -50 and +50, the SS for the Main Effect of C is 80000 and the
reduced effects are
+13 +83 -89 +129
-86 +12 -198 +136
-82 +22 -156 +81
+35 +2 -48 +145
The means for the two levels of factor D are -76 and +76, the SS for the Main Effect of D is 184862 and
the reduced effects are
+89 +7 -13 +53
-10 -64 -122 +60
-6 -54 -80 +5
+111 -74 +28 +69
Notice that these reduced effects are now generally much less than the treatment effects with which we
started. We can observe how rapidly they diminish at each stage by summing the squares of the reduced
effects. After subtracting the effects of the four main effects the remaining sum of squares is:
(892 +72 +132 + +282 +692)x 2 = 132694 on 10 df.
compared with the total treatment SS of 543798 on 14 dfand the error SS of 135209 on 14 df.
At this stage we might decide that the reduced SS is now sufficiently close to what would be expected,
based on the error mean square, (the F ratio is
(132694/10) / (135209/14) = 1.37)
that we should not examine the interaction effects. However we shall continue a little further, if only for
To, calculate, and adjust for, a two-factor interaction effect, we must first calculate the means for the four
combinations of levels of the two factors. Consider the AxB interaction, for which the four combinations
are the four rows of the table of treatment effects. The four means are +34, -34, -34 and +34 (we should not
be surprised that the numbers are all the same since there is only one df for this interaction effect). The
reduced effects are:
+55 -27 -47 +19
+24 -30 -88 +94
+28 -20 -46 +39
+77 -108 -6 +35
Observation of the pattern in this table suggests that the four columns are each either all + or all -. This
corresponds to the CxD interaction (check with the original table of treatment combinations) and this
would seem to be the next effect to consider. The means for the four columns are +46, -46, -46 and +46.
and the reduced effects are:
+9 +19 -1 -27
-22 +16 -42 +48
-18 +26 0 -7
+31 -62 +40 -11
and are clearly now very small. The sum of squares of these reduced effects is now 27110 on 8 df and there
is clearly no point in searching for further effects. If we had wished to examine other effects we would use
the table of treatment combinations to identify the four sets of four values from which we should calculate
The tables of means which we require to summarize the results are two-way tables for (1) factors A and B
and (2) factors C and D. The means are calculated from the mean effects previously calculated and the
overall mean. Thus for the four combinations of A and B the combination means are calculated:
Factor A B
Levels 1 1 535 +66 -9 +34 = 626
1 2 535+66 +10-34 = 577
2 1 535 -67 -9-34 = 424
2 2 535-67+10+34 = 502
1 Mean 535+66 = 601
2 Mean 535 -67 = 469
Mean 1 535 -9 = 526
Mean 2 535 +10 = 545
The standard form of presentation for the two-way table is:
Factor B Factor A
1 2 Mean
1 626 577 526
2 424 502 545
Mean 601 469
Standard error for comparing marginal means:
q(2(135209/14)/16) = 35
Standard error for comparing means in the table:
q(2(135209/14)/8) = 49
The two-way table of means for factors C and D is constructed in the same manner:
Factor D Factor C
1 2 Mean
1 455 462 459
2 515 708 613
Mean 485 585
The standard errors are exactly as for the table for factors A and B
Example 3 Incomplete Block Design
When each block contains a different set of treatments the result of sweeping, first by blocks and then by
treatments. will not leave residuals which sum to zero both for each block and for each treatment. Consider
a very simple example with four treatments in four blocks, arranged so that each block includes only three
of the treatments.
1 2 3 4
A 410 260 360
B 510 370 320
C 640 590 430
D 510 640 430
To understand the process better we shall consider first the situation where all 16 combinations are
1 2 3 4
A 410 260 360 190
B 510 370 480 320
C 640 470 590 430
D 650 510 640 430
Sweeping by blocks and treatments we get
Means 552 402 517 342 Mean =454
(+98) (-52) (+63) (-112)
-142 -142 -157 -152 -148
-42 -32 -37 -22 -33
+88 +68 +73 +88 +79
+98 +108 +123 +88 +104
+6 +6 -9 -4
-9 +1 -4 +11
+9 -11 -7 +9
-6 +4 +18 -16
The mean of these residuals in each block and each treatment is effectively zero apart from rounding error.
The error sum of squares is the sum of squares of the residuals:
(+6)2 +(+6)2 +(-9)2 +...+(+18)2 + (-16)2 = 1352
Now consider the incomplete block situation where we have only three treatments in each block.
Treatment 1 2 3 4
A 410 260 360
B 510 370 320
C 640 590 430
D 510 640 430
Sweeping by blocks and treatments we get:
Means 520 380 530 393 Mean =456
(+64) (-76) (+74) (-63)
-110 -120 -170 -133
-10 -10 -73 -31
+120 +60 +37 +72
+130 +110 +37 +92
+23 +13 -37
+21 +21 -42
+48 -12 -35
+38 +18 -55
It can be seen immediately that the means in each (block) column are not zero. This requires that we sweep
again to eliminate differences between blocks. Why has this happened? If we look back at the block means
first in the complete case and then in the incomplete case we see that the means for block 1 are
552(complete) and 520(incomplete). The mean for the incomplete case is too low because treatment D,
which is the best treatment, was missing in block 1. Hence, we have not fully allowed for the high level of
yields in block 1 and the further sweeping will do this.
So we sweep again by blocks.
Mean +31 +24 -10 -44
-8 -11 -27
-10 -3 +2
+17 -2 +9
+14 +28 -11
Now, for exactly the same reason, we find that the means for the treatments are not zero. So we sweep
again by treatment and continue to sweep alternately by block and treatment until we achieve residuals
which give zero means for blocks and treatments.
-15 +7 +4 -12
-4 -6 +1 +6
+8 +9 -10 +1
+10 +4 +18 -21
So we have arrived at last! The error SS is calculated as usual by summing the squares of the final residuals
(+5)2 +(+3)2 +(-9)2 +...+(+18)2 + (-17)2 1094.
The analysis of variance needs some care because the SS for blocks and treatments depend on the order in
which they are fitted. If, as in the procedure above, we first fit blocks (ignoring treatments) the block SS is
calculated from the block totals or means. The treatment SS is calculated from the change in the sum of
squares of the residuals from those obtained after sweeping for blocks (the first time) to those after the
sweeping is completed. Thus
the block SS is((64)2 +(-76)2 +(74)2 +(.63)2)x4 = 78468,
the SS of residuals after sweeping blocks only = 110667,
the SS of residuals after the final sweeping = 1094,
and the treatment SS(adjusting for blocks) = 109573.
Hence we have the analysis of variance
SS df MS
Blocks (ignoring treatments) 78468 3 26156
Treatments (adjusting for blocks) 109573 3 36524
Error 1094 5 219
The block and treatment effect estimates are built up from the results of the repeated sweeps. Thus for
blocks we have
Block 1 2 3 4
1st sweep +64 -76 +76 -63
2nd sweep +31 +24 -10 -44
3rd sweep +3 +3 -1 -5
4th sweep +1 0 0 0
Total +99 -49 +65 -112
Treatment 1st 2nd 3rd Total
A -133 -15 -2 -150
B -31 -4 0 -35
C +72 +8 +1 +81
D +92 +10 +1 +103
Notice how closely these estimates of block and treatment effects correspond to those from the complete
block data set, which contains the same data points as the incomplete block data plus four extra
Block 1 +98 +99
Block 2 -52 -49
Block 3 +63 +65
Block 4 -112 -112
Treatment A -148 -150
Treatment B -33 -35
Treatment C +79 +81
Treatment D +104 +103
We would expect such agreement because we are trying to estimate the same quantities, the only change
being that in the incomplete design we have less information on which to base our estimation. The reduced
information is clearly sufficient to obtain estimates close to those based on fuller information. We can also
compare the final residuals for the complete and incomplete cases. Again the agreement is good and not
+6 +6 -9 -4 +5 +3 -9
-9 +1 -4 +11 -10 -2 +11
+9 -11 -7 +9 +4 -10 +5
-6 +4 +18 -16 0 +18 -17
Finally we would wish to compare the treatment mean yields. The calculation of treatment means is
already almost completed. We merely have to add the overall mean to the estimates of the treatment
effects. The calculation of standard errors is more difficult and is one aspect of the sweeping technique
where an exact solution is not possible with manual calculation. However, we can use an approximation
which generally gives excellent results.
We calculate two variances for each treatment pair, one based on the total number of observations for each
treatment (MIN), the other based on the number of blocks in which both treatments appear (MAX). If the
number of treatments in the experiment is t, then the variance for a difference between two treatment
MIN + (MAX MIN)/t.
For our incomplete block design
MIN = 2(219)/3 = 146
MAX = 2(219)/2 = 219
Var = 146 +(219 146)/4 = 164.25.
Hence we have treatment means and standard error
Treatment A B C D
Mean 306 421 537 559
Standard error of difference = 12.8
Example 4: Reblocking an on-farm experiment
Sometimes it may become clear on observing an experiment that the blocking should have been arranged
differently. It is then possible to redefine the blocking to match the pattern which is believed to correspond
to the real field variation. This should not be done lightly and particularly it is a dangerous procedure if
many alternative post-experiment blocking systems are tried, and the most successful one used, or if the re-
blocking is based on the numerical yield data rather than on practical assessment of the plot patterns.
The danger derives from the prospect that by trying too hard to define the correct re-blocking system the
estimate of the random plot variance, deduced from the error mean square, will be biased downwards. The
error mean square is, under normal randomization procedures, an unbiased estimate of the plot variability,
after allowing for block differences and treatment effects. It will underestimate the normally expected plot
variability if the form of analysis is pressured too much to make it small rather than appropriate. It is
possible to try too hard!
When we use a different blocking system from that intended in the original design specification it is very
likely that the treatments will not be complete in each block. In the example considered here the original
design was for five herbicide treatments in three randomized complete blocks. On inspecting the plot
Jonathan Woolley and I felt that there were clear patches running diagonally across the blocks. The
experimental plan was
Block 3 Plot 11 Plot 12 Plot 13 Plot 14 Plot 15
TI T4 T3 T2 T5
Block 2 Plot 10 Plot 9 Plot 8 Plot 7 Plot 6
T2 T5 T4 T3 TI
Block 1 Plot 1 Plot 2 Plot 3 Plot 4 Plot 5
T5 TI T2 T4 T3
The patches perceived by us were approximately
(1) plots 4,5,6,7,15;
(2) plots 2,3,8,13,14;
(3) plots 1,9,10,11,12.
The plots were scored by each of us and the combined score used as a measure of performance. The data
for the revised blocking were
We sweep as usual alternatively by blocks and by treatments. The figures hereafter are multiplied by 10 to
avoid decimals and reduce spatial confusion.
-5 -5 +2
-4 -4 +6
+2 +2 -4
The sum of squares of the residuals is 6010 (60.1 in terms of the original data). For comparison the Error
SS for the analysis using the original blocks was 58.3. The new blocks do not appear to be an improved
description of the pattern of variation between the plots.
Mead, R. (1984). Confounded experiments are simple, efficient and misunderstood. Experimental
Agriculture 20: 185-201.
Mead, R. (1988). The design of experiments: Statistical Principles for Practical Application. Cambridge
Woolley, J.N., Beltran, J.A., Vallejo, R.A., Prager, M. (1988). Identifying Appropriate Technologies for
Farmers: The case of the bean and maize system in Ipiales, Colombia, 1982-1986. CIAT Working
Document 31. CIAT, Cali, Colombia.
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