Methods for experimental design principles and applications for physicists and chemists (Jacques L Goupy) (Z-Library)

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Methods for experimental design 
DATA HANDLING IN SCIENCE AND TECHNOLOGY 
Advisory Editors: B.G.M. Vandeginste and S.C. Rutan 
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Volume 12 Methods for Experimental Design: principles and applications for physicists and 
chemists by J.L. Goupy 
DATA HANDLING IN SCIENCE AND TECHNOLOGY -VOLUME 12 
Advisory Editors: B.G.M. Vandeginste and S.C. Rutan 
Methods for 
experimental design 
principles and applications 
for physicists and chemists 
JACQUES L. GOUPY 
7, Rue Mignet, 75016 Paris, France 
ELSEVIER 
Amsterdam - London - New York -Tokyo 1993 
ELSEVIER SCIENCE PUBLISHERS B.V. 
Sara Burgerhartstraat 25 
P.O. Box 211,1000 AE Amsterdam, The Netherlands 
Translation and revised edition of: 
La Methode des Plans d’Experiences. 
Optimisation du Choix des Essais et de I’lnterpretation des Resultats 
0 Bordas, 1988 
0 Dunod for updatings 
Translated by: 
C.O. Parkes 
ISBN 0-444-89529-9 
0 1993 Elsevier Science Publishers B.V. All rights reserved. 
No part of this publication may be reproduced, stored in a retrieval system or transmitted in any 
form or by any means, electronic, mechanical, photocopying, recording or otherwise, without the 
prior written permission of the publisher, Elsevier Science Publishers B.V., Copyright & Permis- 
sions Department, P.O. Box 521,1000 A M Amsterdam, The Netherlands. 
Special regulations for readers in the USA - This publication has been registered with the Copy- 
right Clearance Center Inc. (CCC), Salem, Massachusetts. Information can be obtained from the 
CCC about conditions under which photocopies of parts of this publication may be made in the 
USA. All other copyright questions, including photocopying outside of the USA, should be 
referred to the publisher. 
No responsibility is assumed by the publisher for any injury and/or damage to persons or pro- 
perty as a matter of products liability, negligence or otherwise, or from any use or operation of 
any methods, products, instructions or ideas contained in the material herein. 
This book is printed on acid-free paper. 
Printed in The Netherlands 
To my wife Nicole 
This Page Intentionally Left Blank
PREFACE 
This book is devoted to researchers who, because of limited time and resources, must 
use a minimal number of experiments to solve their problems. It was written with the aim of 
avoiding theoretical statistics or mathematics. It is not intended to replace the texts on analysis 
of variance, regression analysis or more advanced statistical treatments. It was written for 
experimenters by an experimenter. It is an introduction to the philosophy of scientific 
investigation. 
This book has grown out of my consulting practice and a series of short courses given to 
industrial researchers. These experiences taught me that a good method and solid concepts are 
more useful than complex theoretical knowledge. Therefore, I have attempted to preserve the 
balance between the practice necessary to carry out a study and the theory needed to 
understand it. I have tried to write a book that is usehl and clear. While mystudentsmay have 
learned something from me, I have certainly learned from them. As a result this new English 
edition contains considerable additional material not included in the original French book. 
The presentation makes extensive use of examples and the approach and methods are 
graphical rather than numerical. All the calculations can be performed on a personal computer. 
Conclusions are easily drawn from a well designed experiment, even when rather elementary 
methods of analysis are employed. Conversely even the most sophisticated statistical analysis 
cannot salvage a badly designed experiment. 
Readers are assumed to have no previous knowledge of the subject. The presentation is 
such that the beginner may acquire a thorough understanding of the basic concepts. There is 
also sufficient material to challenge the advanced student. The book is therefore suitable for an 
introductory or an advanced course. The many examples can also be used for self-tuition or as 
a reference. 
ACKNOWLEDGEMENTS 
I am gratehl to the many researchers whose work provided the examples cited in this 
book and who have asked me so many questions on how to use experimental designs 
efficiently. 
I am also grateful to Owen Parkes who translated this book and was a continual 
source of advice. 
I wish to thank the staff at Dunod, particularly Maryvonne Vitry and Jean-Luc Sensi, 
and the staff at Elsevier, for their encouragement and support. 
A special thanks to my wife who sustained me with love and made this work possible. 
Paris 
February 1993 
Jacques GOUPY 
This Page Intentionally Left Blank
Preface 
Acknowledgements 
ix 
CONTENTS 
vii 
vii 
Chapter 1 
1. Introduction 
2. The process of knowledge acquisition 
Research strategy : Definition and objectives 
2.1. Gradual acquisition of results, 4 
2.2. Selection of the best experimental strategy, 4 
2.3. Interpretation of results, 4 
3.1. The classical method, 5 
3.2. Experimental design methodology, 6 
3. Studying a phenomenon 
4. Historical background 
Chapter 2 
1. Introduction 
2. Two-factor complete designs: 22 
3. General formula of effects 
4. Reduced centred variables 
5 . Graphical representation of mean and effects 
6. The concept of interaction 
7. General formula for interaction 
Chapter 3 
1. Introduction 
2. Complete three factor design: 23 
3. The Box notation 
4. Reconstructing two 22 designs from a Z3 design 
5 . The relationship between matrix and graphical representations 
6. Construction of complete factorial designs 
7. Labelling of trials in complete factorial designs 
8. Complete five factor designs: 25 
Two-level complete factorial designs:2* 
2.1. Example: The yield of a chemical reaction, 10 
6.1. Example: The yield of a catalysed chemical reaction, 21 
Two-level complete factorial designs: 2k 
2.1. Example: The stability of a bitumen emulsion, 29 
of experimental design 
1 
1 
2 
4 
7 
9 
9 
10 
15 
16 
19 
21 
24 
29 
29 
29 
34 
35 
36 
37 
38 
38 
X 
8.1, Example: Penicillium chrysogenum growth medium, 38 
9. Complete designs with k factors: 2k 
10. The effects matrix and mathematical matrix 
10.1. Matrix transposition, 45 
10.2. Matrix multiplication, 45 
10.3. Inverse of X, 46 
10.4. Calculation of X'X, 47 
10.5. Measurement units, 47 
43 
44 
Chapter 4 Estimating error and significant effects 49 
1. Introduction 49 
2. Definition and calculation of errors 50 
2.1. Arithmetic mean, 5 1 
2.2. Dispersion, 51 
3. Origin of the total error 53 
56 4. Estimating the random error of an effect 
4.1. The investigator knows the experimental error of the response, 56 
4.2 The experimental error of the responseis unknown, 59 
Several measures on the same experimental point, 59 
Repeat the whole experimental design, 60 
4.3. The experimental error of the response is unknown, and the 
experimenter does not want to perform any supplementary 
experiments, 62 
5. Presentation of results 63 
5.1. Numerical results, 63 
5.2. Illustration of results, 63 
Chapter 5 
1. Introduction 
2. Weighing and experimental design 
2.1. Standard method, 70 
2.2. Hotelling method, 70 
2.3. Strategy for weighing four objects, 71 
3.1. Unit matrix criterion, 76 
3.2. Maximum determinant criterion, 77 
3.3. Minimum trace criterion, 79 
3.4. "The largest must be as small as possible" criterion, 80 
4.1. Positioning experimental points for one factor, 8 1 
Example: Measuring an electrical resistance, 83 
The concept of optimal design 
3. Optimality criteria 
4. Positioning experimental points 
5. Measurement of an electrical resistance 
6. Positioning experimental points for two factors 
7. Positioning the experimental points for k factors 
67 
67 
69 
76 
80 
83 
85 
89 
xi 
Chapter 6 Two-level fractional factorial designs: 2k-P 
The Alias theory. 91 
1. Introduction 91 
2. First fractional design: Z3-' 92 
3. Interpretation of fractional designs 94 
4. Calculation of contrasts 95 
5. Algebra of columns of signs 98 
Alias generators, 99 
100 
7. Notation of fractional designs 104 
8. Construction of fractional designs (two extra factors) 104 
9. Construction of fractional designs (p extra factors) 108 
10. Practical rules 110 
10.1 Going from AGS to contrasts, 110 
10.2 Going from contrasts to the AGS, 110 
1 1.1. Total number of factors to be studied, 1 1 1 
1 1.2. Number of trials to be performed, 112 
2.1 Example: Bitumen emulsion stability (continued from Chapter 3), 92 
6. Construction of fractional designs (one extra factor) 
1 1. Choosing the basic design 111 
Chapter 7 Two-level fractional factorial designs: 2k-P 
Examples 
1. Introduction 
2. 2*-' fractional design 
2.1. Example: Minimizing the colour of a product, 1 16 
2.2. Techniques for dealiasing main effects from interactions, 119 
2.3. Construction of the complementary design, 121 
2.4. Contrast calculation, 122 
2.5. Interpretation, 123 
3. 274 fractional designs 
3.1. Example: Settings of a spectrofluorimeter, 127 
3.2. Calculation of contrasts, 130 
3.3. Interpretation of the initial design, 132 
3.4. Construction of the complementary design, 134 
3.5. Interpretation of the initial and complementary designs, 140 
4. Studying more than seven factors 
5. The concept of resolution 
5.1. Definition of resolution, 142 
5.2. An example of a 2:: design: Plastic drum fabrication, 144 
115 
115 
116 
127 
142 
142 
xii 
Chapter 8 Types of matrices 
1. Introduction 
2. The experimental matrix 
3. The effects matrix 
4. The basic design matrix for constructing fractional designs 
151 
Chapter 9 Trial sequences: 
Randomization and anti-drift designs 
1. Introduction 
1.1. Drift errors, 161 
1.2. Block errors, 161 
2. Small uncontrollable systematic variations 
3. Systematic variations: Linear drift 
4. #en should trials be randomized? 
Example: The powder mill, 166 
4.1. Powder mill: First investigator's strategy, 167 
4.2. Powder mill: Second investigator's strategy, 168 
4.3. Powder mill: Third investigator's strategy, 171 
5 . Randomization and drift 
151 
151 
153 
154 
159 
159 
162 
162 
166 
175 
Chapter 10 Trial sequences: Blocking 179 
1. Introduction 179 
2. Block variations 180 
3. Blocking 180 
4. Blocking on one variable 185 
190 
Example: Preparation of a mixture, 180 
Example: Penicillium chrysogenum growth medium (continued), 185 
5.1. Example: Yates' bean experiment, 190 
5.2. Interpretation of experimental results, 194 
5 , Blocking on two variables 
6. Blocking of a complete design 20 1 
Chapter 11 Mathematical modelling of factorial 2k designs 203 
1. Introduction 203 
2. Mathematical modelling of factorial designs 204 
3. Formation of the effects matrix 208 
4. Evaluation of responses throughout the experimental domain 209 
4.1. Example: Study of paste hardening, 210 
4.2. Interpretation, 21 1 
5. Test of the model adopted 
6. Selection of a research direction 
6.1. Mathematical model, 21 5 
6.2. Isoresponse curves, 216 
213 
213 
... 
X l l l 
6.3. Steepest ascent vector, 2 17 
7. Choice of complementary trials 
8. Analysis of variance and factorial designs 
Example: Sugar production, 220 
8.1. Analysis of the problem by factorial design 
8.2 Analysis of the problem by analysis of variance 
8.3 Analysis of the problem by factorial design 
8.4 Analysis of the problem by analysis of variance 
(one response per trial), 220 
(one response per trial), 223 
(two responses per trial), 226 
(two responses per trial), 227 
9. Introduction to residual analysis 
10. Error distribution 
220 
220 
23 0 
234 
Chapter 12 Choosing complementary trials 239 
1. Introduction 
2. A single extra trial 
3. Two extra trials 
4. Three extra trials 
5. Four extra trials 
Example: Clouding of a solution, 240 
Example: Clouding of a solution ( block effect), 244 
5.1, Reconstruction of the experimental design, 252 
5.2. Presentation of results, 252 
239 
240 
244 
246 
250 
Chapter 13 Beyond influencing factors 257 
1. Introduction 257 
1.1. IdentifLing the domain of interest, 257 
1.2. Looking for an optimum, 258 
1.3. Finding the minimum response sensitivity to external factors, 258 
2.1. Example: Two-layer photolithography, 258 
2.2. Examination of the results for response Lz, 263 
2.3. Examination of the results for response L,, 265 
3.1. Example: Cutting oil stability, 268 
3.2. Interpretation, 270 
4.1. Example: thickness of epitaxial deposits, 271 
4.2. Interpretation, 275 
2. Identifying the domain of interest 258 
3. Finding an Optimum 268 
4. Finding a stable response 27 1 
xiv 
Chapter 14 Practical method of calculation 
using a quality example 
1. Introduction 
2. A quality improvement example 
3. Interpretation, step 1 
Example: Study of truck suspension springs, 284 
3.1. Calculation of responses, 287 
3.2. Analysis of results (interpretation, step 1) , 289 
4. What is a good response for dispersion? 
4.1. Variance, 292 
4.2. Logarithm of variance, 293 
4.3. Comparison of variance and logarithm of variance, 293 
4.4. The signal-to-noise ratio, 295 
5.1. Calculation of responses, 295 
5.2. Analysis of results (second step of interpretation), 296 
5. Interpretation, step 2 
6. Optimization 
Chapter 14 (continued) 
Detailed calculations for the truck suspension springs example 
1. Calculation for the first interpretation 
2. Calculation for the second interpretation 
3. Calculation for optimization 
Chapter 15 
1. Introduction 
2. Example 1, Propane remover optimizing 
Experimental designs and computer simulations 
2.1. The problem, 335 
2.2. Simulation, 337 
2.3. Interpretation, 337 
3.1. The problem, 340 
3.2. Calculations, 343 
3.3. Interpretation, 345 
3.4. Conclusion, 346 
3. Example 2: Optimization of a hydroelastic motor suspension 
4. Example 3: Natural gas plant optimization 
4.1, The gas production system and the problem to be solved, 347 
4.2. Choice of responses, 349 
4.3. Choice of calculation design, 351 
4.4. Calculations, 352 
4.5. Interpretation, 353 
4.6. Optimization, 361 
4.7. Conclusion, 363 
283 
283 
284 
287 
292 
295 
3 02 
309 
3 09 
316 
326 
333 
333 
335 
339 
347 
Chapter 16 Practical experimental designs 
xv 
365 
1. Introduction 
2. Calculation of effects and interactions 
3. Calculation of effects and interactions 
4. Error transmission 
5. Experimental quality 
when an experimental point is misplaced 
when all the experimental points are misplaced 
Chapter 17 Overview and suggestions 
1 . Introduction 
2. Selection of the best experimental strategy 
2.1. Defining the problem, 392 
2.2. Preliminary questions, 394 
2.3. Choice of design, 397 
3. Running the experiment 
4. Interpretationof results 
4.1. Critical examination of the results, 398 
4.2. Follow up, 400 
5. Gradual acquisition of knowledge 
6. What experimentology will not do 
Appendix 1 Matrices and matrix calculations 
1. Introduction 
2. Definitions 
2.1. General, 403 
2.2. Definitions for square matrices, 405 
3.1. Operation on array, 407 
3.2. Operations between arrays, 408 
3.3. Calculation of an inverse matrix, 41 I 
3. Matrix operations 
4. Matrix algebra 
5 . Special matrices 
Appendix 2 
1 . Normal distribution 
Population, 4 18 
Sample, 418 
Variance, 419 
One random variable, 419 
Error of the mean, 420 
Statistics useful in experimental designs 
2. Variance Theorem 
365 
3 66 
3 72 
377 
388 
391 
391 
3 92 
398 
398 
40 1 
402 
403 
403 
403 
407 
413 
414 
417 
417 
419 
xvi 
Appendix 3 Order of trials that leaves the effects 
of the main factors uninfluenced by linear drift. 
Application to a Z3 design 
Bibliography 
Author index 
Example index 
Subject index 
421 
43 1 
440 
443 
447 
CHAPTER I 
R E S E A R C H S T R A T E G Y : 
D E F I N I T I O N A N D O B J E C T I V E S 
1. INTRODUCTION 
Experimental scientists and technicians employed in laboratories, industry, medicine or 
agriculture throughout the world run experiments. The classical experimental approach is to 
study each experimental variable separately. This one-variable-at-a-time strategy is easy to 
handle and widely employed. But is it the most efficient way to approach an experimental 
problem? The first people to ask this question were English agronomists and statisticians 
working at the beginning of the century. Agronomy is somewhat different from most 
experimental sciences in that there are almost always a large number of variables and each 
experiment lasts a long time. As they could not run large numbers of trials, they worked to 
develop the best research strategy. They found that the classical method was not appropriate 
and developed a revolutionary approach which guaranteed experimenters an optimal research 
strategy. 
2 
Since then, many investigators have contributed with such topics as: optimal experimental 
designs, study of residuals, composite designs, Latin squares, fitting equations to data, 
multivariate calibration, empirical model building, response surface methodology, etc. All these 
techniques can be thought as components of a new discipline which, strangely, has no name. 
The name suggested for the field is Experimentics or Experimentology [ 11. But the scientific 
community has yet to decide. The factorials designs which are the subject of this book form just 
one part of Experimentics. 
This first chapter outlines the areas in which experimental designs can be applied, defines 
objectives and raises the general problem of how to study a phenomenon. The main points 
covered will be: 
I . The general process by which experimental knowledge is acquired. 
2 . The three essential aspects of knowledge acquisition using the methodology of 
Experimental Designs: 
Gradual acquisition of results. 
Interpretation of results. 
Selection of the best experimental strategy 
3 . A comparison of classical approach and experimental design to study a phenomenon 
4. A brief historical background. 
2. THE PROCESS OF KNOWLEDGE ACQUISITION 
Any search for new information begins by the investigator asking a number of questions 
(Figure 1.1). For example, if we want to know the influence of a fertiliser on the wheat yield of 
a plot of land, we could ask several questions, such as : 
How much fertiliser is needed to increase the yield by 10% ? 
How does rainfall affect fertiliser efficiency ? 
Is the wheat quality influenced by the fertiliser ? 
These questions define the problem and determine the work to be carried out to solve it. 
It is therefore important to ask the right questions: those that can help us to resolve the 
problem. This is not quite as simple as it may appear. 
Before actually beginning any experiments, it is always wise to check that the 
information required does not already exist. The experimenter should first prepare an inventory 
of the available information, by compiling a bibliography, consulting experts, theoretical 
calculations, or any other method which provides himher with answers to the questions asked 
without actually carrying out any experiments. This preliminary survey may answer all the 
questions, resolving the problem. If it does not, some questions may remain to be answered, or 
they may be modified in the light of the information obtained. It will then be necessary to carry 
out experiments to obtain all the answers required. 
discuss it further. Our concern is not with this initial phase, but with those that follow. 
This preliminary study is a routine part of all experimental work and we shall not 
These are the steps in which the experimenter thinks about the experiments to be 
3 
performed, and our problem is how to select the experiments that must be done and those 
which need not be done. Is there a single ideal strategy? Such an ideal strategy should: 
give the desired results as quickly as possible. 
avoid carrying out unnecessary experiments. 
ensure that the results are as precise as possible. 
enable the experiments to progress without setbacks. 
provide a model and optimisation of the phenomena studied. 
There is such an ideal strategy, and it is effective because it simultaneously takes into 
account three essential aspects of knowledge acquisition. 
gradual acquisition of results. 
0 
interpretation of results. 
selection of the best experimental strategy. 
SYSTEM TO STUDY 
QUESTIONS Q1, Q2 ... Qn 
INFORMATION INVENTORY 
J 
I OlCE OF AN EXPERlMENTAL STRATEGY 
I 
GRADUAL 
ACQUISITION 1 
EXPERIMENTATION 
1 OF RESULTS 
INTERPRETATION OF THE RESULTS 
5 
KNOWLEDGE OF THE SYSTEM STUDIED 
Figure 1.1 : The boxed steps define the areas of Experimentics. 
4 
The experiments should be organised to facilitate the application of the results. They 
should also be organised to allow the gradual acquisition of relevant results. 
2.1. Gradual acquisition of results 
The experimenter clearly does not know the results when the study begins. It is therefore 
wise to work progressively and to be able to reorientate the study in the light of the early trial 
results. A preliminary rough outline can be done and then used to select any change in research 
direction that may better identi@ the most important points of the study and those avenues that 
should be abandoned to avoid any waste of time. 
This is why we recommend working progressively. An initial series of trials can provide 
provisional conclusions. A new series of trials can be done based on these provisional 
conclusions. The results of both these series should then be used to obtain a better picture of 
the results. Then, a third series of trials can be run if necessary. In this way the experimenter 
accumulates only those results that he requires, and the study stops when the original questions 
have been answered. 
2.2. Selection of the best experimental strategy 
This strategy should facilitate the organisation of gradual acquisition of results. It should 
also minimise the number of trials, but it must not compromise the quality of the 
experimentation. On the contrary, it should ensure that the results are the most precise 
possible. Experimental designs, response surface methodology, and other approaches, such as 
steepest ascent and Simplex, are perfect for our requirements : 
0 progressive acquisition of knowledge. 
0 the most precise results. 
0 only the required number of experiments 
We will see that they provide the maximum of usefid information for the minimum 
number of experiments. 
2.3. Interpretation of results 
The initial choice of experiments should facilitate interpretation of the results. Results 
should be readily interpreted and easily understood by both specialists in the field and those 
that are not. The methodsrecommended above can help us attain both these objectives. 
Microcomputers have made what used to be a long and tedious process of calculating 
results much more accessible. Not only are the calculations done quickly and accurately, but 
graphical outputs are a spectacular means of displaying results. 
3. STUDYING A PHENOMENON 
The study of a phenomenon can be outlined as follows: the scientist may want to know, 
for example, the yield of wheat from a plot of land, the profit made on a chemical product or 
5 
the wear on a car motor component. This yield, price, or wear depends on many variables. The 
grain yield will vary with the nature of the soil, the amount and type of fertiliser, the exposure 
to the sun, the climate, the variety of wheat seed sown, etc. The profit from sale of a chemical 
may depend on the quality of the feedstock, industrial production yields, product 
specifications, plant conditions, etc. A similar set of variables will influence the wear of the car 
motor component. 
We can assess this as the response, y. This quantity is a finction of several independent 
variables, xi.which we shall call factors. It is possible to link mathematically the response y to 
the factors, Xi, as follows : 
y = f ( x l , x2> x 3 7 . , . > xn..,.) 
The study of a phenomenon thus requires measuring the response y for different sets of 
factor values. Let us, first, examine briefly the "classical" method of establishing the fhction. 
3.1. The classical method 
The levels of all the variables except one are held constant. The response y is then 
measured as a hnction of several values of this unfixed variable xI. 
A B C D E X 
Figure 1.2 : Only the levels of the variable x, are modified, the 8 other variables are held 
constant. 
6 
At the end ofthe experiment on this first variable, a curve is drawn of y = f (x,) (Figure 
1.2). If the experimenter wishes to study all the variables, the whole experiment must be 
repeated for each one. Using this method, if he wanted to study just seven factors, with only 
five points per variable, he would have to carry out = 78,125 experiments or trials. This 
represents an enormous amount of work, and is clearly not feasible. The experimenter must 
therefore find a way of reducing the number of tnals. There are only two ways of doing this: 
reduce the number of experimental points per variables or reduce the number of variables. 
Reduce the number of experimental points 
If he elects to examine only three points per variable instead of five, he would have to 
carry out 37 = 2 187 trials. 
Two points per variable would require 27 = 128 trials. This is still a lot of work, and is 
often too much for either the budget or the time available. As there must be at least two 
experimental points per variable, the experimenter has no option but to: 
Reduce the number of variables 
But even a system with four variables, testing each of them at three values, requires 34, 
or 81 trials. This way of working is both tedious and unsatisfactory. If some variables are 
ignored, people could be dubious about the results, and the investigator will be obliged to 
apologise for presenting incomplete conclusions. 
The inconvenience of this approach is particularly evident when safety or large sums of 
money are involved. This is precisely why we shall now proceed to examine the method of 
experimental design. 
3.2. Experimental design methodology 
The essential difference between the classical one-variable-at-a-time method described 
above and the experimental design is that, in the latter, the values of all the factors are varied in 
each experiment. The way in which they are varied is programmed and rational. While this may 
appear somewhat disturbing at first sight, this approach of multiple simultaneous variable 
settings, far from causing difficulties, offers several advantages. Some of these are : 
fewer trials. 
large number of factors studied. 
detection of interaction between factors 
detection of optima. 
best result precision. 
0 optimisation of results. 
model-building from the results. 
Experimental designs can be used to study a great number of factors while keeping the 
total number of trials within reason. This is why one of its major applications is the search for 
influencing factors. 
7 
Instead of limiting the number of factors studied, the experimenter initially reduces the 
number of experimental points per factor. The term factor will be used rather than variable 
because it can include both continuous and discrete variables. 
The search for influencing factors consists of 
setting only two values for each factor, these values are called the levels. 
studying as many factors as possible, even those that may appear, at first sight, 
to have little influence. 
Many of the factors studied will probably have no influence, only a few will act upon the 
response. The results can then be used to choose new experimental points to define one or 
more specific aspects of the study. Thus, all the influencing factors will have been detected and 
studied, while keeping the number of trials to a minimum. Hence, the study can be completed 
without waste of either time or money. 
4. HISTORICAL BACKGROUND 
Agronomists were the first scientists to confront the problem of organising their 
experiments to reduce the number of trials. Their studies invariably include a large number of 
parameters, such as soil composition, effect of fertilisers, sunlight, temperature, wind exposure, 
rainfall, species studied, etc., and each experiment tends to last a long time. At the beginning of 
the century Fisher [ 2 , 31 first proposed methods for organising trials so that a combination of 
factors could be studied at the same time. These were the Latin square, greco-Latin square, 
analysis of variance, etc. The ideas ofFisher were taken up by agronomists such as Yates and 
Cochran, and by statisticians such as Plackett and Burman [4], Hotelling [S], Youden [6] , and 
Scheffe [7], and used to develop powerful methods. However, their studies were often highly 
theoretical, and involved difficult calculations. These difficulties, plus the revolutionary 
concepts developed by these pioneers, undoubtedly hindered the rapid spread of the new 
methods into the worlds of industry and universities. During the World War 11, major industrial 
companies realised that these techniques could greatly speed up and improve their research 
activities. Du Pont de Nemours adapted the techniques employed in agronomy to chemical 
problems, some years later ICI in England and TOTAL in France began using experimental 
designs in their laboratories. Other major companies, such as Union Carbide Chemicals, 
Proctor and Gamble, Kellogs, General Foods, have also adopted this approach. But the 
applications of these methods have never become generally known and for the most part have 
remained restricted to their original discipline of agronomy. They feature in few courses and 
despite the efforts of certain teachers, few students have learned them. The outstanding 
teachers in this field include Professors Box [8], Hunter and Draper [9], Benken in the USA, 
Phan Tan Luu in France, and Taguchi [ 101 in Japan. 
Thus, although they have been known and applied in certain areas for over half a century, 
the techniques are poorly understood and not generally used. The calculations are no longer a 
problem, thanks to the widespread availability of microcomputers. The challenge now is to 
overcome the reticence of users by clearly demonstrating the advantages afforded by 
8 
experimental design. The method described in the foilowing chapters, together with the 
examples which are given, will, it is hoped, make experimental designs accessible to 
researchers in both the industrial and academic worlds. 
CHAPTER 2 
T W O - L E V E L C O M P L E T E 
F A C T O R I A L D E S I G N S : 2 2 
1. INTRODUCTION 
Two-level factorial designs are the simplest, but are widelyused because they can be 
applied to many situations as either complete or fractional designs. This chapter deals with 
complete designs. We will first examine a simplified example using only two factors. We will 
use it to introduce several important basic concepts which will be used in later chapters: 
experimental matrix, effect of a factor, iInteraction between factors, reduced centred variables, 
etc. This chapter also indicates how to calculate the effects of each factor and the interactions 
between factors. The reader will find usefkl tools to facilitate the interpretation of results and 
the presentation of conclusions. 
10 
2. TWO-FACTOR COMPLETE DESIGNS: 22 
The important concept of effect is best understood with the help of an example. 
2.1. Example: The yield of a chemical reaction 
The Problem: 
The yield from this reaction depends on two factors: temperature and 
pressure. The chemist carrying out the study needs to know if the yield 
' increases or decreases with increasing temperature. He also wants to 
$2 know the effect of pressure changes on the yield. The experirnental set- 
up allows the reaction temperature to be varied from 60°C to 80°C, and 
~ the pressure from 1 to 2 bar The experimental domain (Figure 2.1) is I 
thus defined by the four points I 
60" C 80" C 60" C 80" c 
A 1 lbar { lhar 1 2 h a r { 2bar 
The experimenter must adopt a specific research strategy in order to obtain the responses 
he requires. He could, €or example, fix the temperature at 70°C and carry out 3 experiments at 
1, 1.5 and 2 bar as shown in Figure 2.2. The yield increases with pressure from 70°C to 75OC 
and 80°C. 
Pressure 
2 bar 
1 bar 
8o oc Temperature 60 OC 
Figure 2.1: Definition of the experimental domain . 
11 
The effect of temperature can then be studied by keeping pressure constant at 1.5 bar 
and carrying out 3 experiments at 60"C, 70°C and 80°C. The yield increases with temperature, 
65%, 75% and 85%, indicating that both temperature and pressure must be increased to obtain 
the best yield. A final experiment at 80°C and 2 bar confirms these assumptions and the study 
is complete. But it has taken six experiments to obtain this result. 
Pressure 
Figure 2.2: Example of a research strategy. 
The experimenter could have selected another strategy by using other experimental 
points. These points could be evenly distributed throughout the experimental domain, or they 
could be selected randomly. But is there a best strategy? Clearly it is one that minimises the 
number of experiments without sacrificing precision, so that the same conclusions are reached. 
This best strategy exists; it consists of using the points A, B, C and D, the extremities of the 
experimental domain (Figure 2.3). This is the strategy adopted for two-factor experimental 
designs. While it provides the same results as the above experiment, it requires only four 
experiments. Let us now see how this approach can be used to provide a hller analysis of the 
results. 
We shall use the convention of -1 for the low level of each factor and +I for the high 
level. We can then place all the experimental information in a table, called the Experimental 
Matrix or Trial Matrix (Table 2.1). Each experiment is defined in this matrix. For example, in 
trial no 3, factor 1 (temperature) will be held at 60°C and factor 2 (pressure) at 2 bar. The trial 
is run under these conditions and the yield is measured. The other three trials shown in the 
matrix are carried out in a similar fashion and the results entered into a specific column in the 
experimental matrix and on the graph representing the experimental domain (Figure 2.4). 
Pressure 
2 bar +I 
1 bar -1 
A t 
D 
B - 
-1 +I Temperature 
60 "C 80 "C 
Figure 2.3: Location of experimental points to obtain an optimal research 
strategy. 
TABLE 2.1 
EXPERIMENTAL MA= 
THE YIELD OF A CHEMICAL REACTION 
Pressure 
-1 
4 + 1 
I 1 
Level (+) 8OoC 2 bar 
13 
Pressure 
2bar +I 
1 bar -1 
4 
-1 +I Temperature 
60 OC 80 OC 
Figure 2.4: Results are entered in the experimental domain. 
Results: 
Four trials are sufficient, and the experimenter can conclude that the 
greatest yield is obtained by working at 80°C and with a pressure of 2 
bar. 
This experiment introduces the important concept of the effect of a factor. When the 
temperature is increased from 60°C (level -1) to 80°C (level +1), the yield increases by 10 
units (Figure 2.5), regardless of the pressure. Thus the overall effect of temperature on the 
yield is + 10 units. The main effect or effect of temperature is by definition, hay of this value, 
or +5 yield units. 
14 
pressure 
2 bar +I 
1 bar -1 
A 
I 
Temperature -1 +I 
60 OC 80 OC 
Figure 2.5: Main effect of temperature: 5 YO yield units. 
When pressure is increased from 1 bar (level -1) to 2 bar (level +I), the yield increases 
by 20 units (Figure 2.6), regardless of the temperature. Thus the overall effect is +20 units and 
the main effect or effect of pressure is +I0 yield units. 
Pressure 4 
' 70% 
1 bar -1 
I 
-1 +1 Temperature 
60 OC 80 OC 
Figure 2.6: Main effect of pressure: 10 YO yield units. 
3. GENERAL FORMULA OF EFFECTS 
The above results can be generalised by using literal values. We shall call y , the response 
of experiment 1, and y , the response of experiment 2, etc. The global effect of temperature is 
defined as the difference between the average of the responses at the high temperature and the 
average of the responses at the low temperature (Figure 2.7). 
-1 
-1 +I X l 
Figure 2.7: y+ is the average response at the high temperature level. y - is 
the average response at the low temperature level. 
There are two responses at the high temperature level, y , and y, . The average response 
at the high temperature level, y+ , is therefore given by: 
The average response at the low temperature level, y-, is: 
y- = -[Yl 1 +Y,l 
2 
The effect I?, of temperature is, by definition, half the difference between these two 
averages, 
16 
or 
Similarly, the effect Ep of pressure, is given by the expression: 
E =-[-yl 1 -Y, +y3 + Y ~ I P 4 
Inserting the numerical values of the responses ( Table 2. l), we get: 
1 E - -[-60+ 70-80+ 901 = 5% 
‘ - 4 
E,= -[-60-70+80+90] 1 =10 % 
4 
The average, I, of all the responses is given by 
I=-[+60+70+80+90]=75% 1 
4 
The formulae for calculating the values of the effects are easily remembered: the 
responses occur in the order of the trials and are preceded by the signs + or - that appear in the 
column of the corresponding factor in the experimental matrix. Thus the sequence of signs for 
the temperature column is: 
- + - + 
This method is general and we shall use it to calculate the effects in all two-factor 
factorial designs, whatever the number of factors. We assume that, in the above calculations, 
all the phenomena studied vary linearly between the experimental points. This assumption is 
justified by its simplicity and by all the consequences that can be deduced fiom it. This is a very 
usefbl assumption at this stage, and we shall see that it is a first step towards more complex 
concepts later. So that we do not forget that there are both measured responses and calculated 
responses, we shall indicate measured responses as filled circles and calculated responses as 
open circles in all fbture diagrams or figures. 
4. REDUCED CENTRED VARIABLES 
The logic behind assigning the value -1 to the low level and +I to the high level merits 
closer examination, as it leads to two major changes. The first is a change in the unit of 
measurement and the second is a change in origin. 
17 
60 'C 80 "C 
Normal Variables 1-1 . 20 "C - (Temperature) 
Centred Reduced . * CRV --+ 
-1 +1 
Variables - 
Figure 2.8: Comparison of normal units and reduced units. 
Change in units of measurement 
The temperature increases fkom a low level (-1) of 60°C to a high level (+1) of 80°C. 
There are thus 20 normal temperatureunits between the extremes of this experimental domain. 
But if we use -1 and +1 there are only two temperature units between the same two extremes. 
The new unit introduced by the notation -1 and +1 thus has a value of 1O"C, or ten normal 
temperature units. This is therefore a reduced variable, and the value of the new unit in terms 
of normal units is a step. In this case the temperature step is 10°C. 
Similarly, the pressure step in the above example is 0.5 bar. 
Change in origin 
The mid point of the [-1, +1] segment is zero, and this is the origin of the measurements 
in the new units. In normal units, the origin is not in the middle of the [-1, +1] segment; it lies 
outside the 60-80°C interval. The origin of the pressure values is similarly changed. The new 
variables are said to be centred. 
0 "C 60 "C 80 "C 
Normal Variables 1-1 
(Temperature) 
Centred Reduced 
Variables c--c--I 
-1 0 +1 
Figure 2.9: Normal origin and centred origin. 
18 
The value of the new origin expressed in normal units can be obtained by taking the 
Then, if 
centre of the experimental domain, which is 70°C for the temperature and 1.5 bar for pressure. 
. A- is the low level of a variable expressed in normal units, and . A+ is the high level of a variable expressed in normal units. 
so that 
A,, is the midpoint ofthe [-1,+1] segment, or zero level of the variable 
expressed in normal units: 
A +A, 
2 
A,= 
For temperature, this gives 
60+80 
2 
A"= ~ =70"C 
and for pressure 
1 +2 
2 
A,= ~ = 1.5 bar 
Thus, assigning the value -1 to the low level value of a factor and +1 to its high level 
value leads to 
a change of units, and 
a change of origin. 
These new variables are therefore named reduced and centred variables, or coded 
variables. 
Normal Variables 60°C 70% 80°C 
(Temperature) 
Centred Reduced 
Variables 
I I 
I I 
0 +I 
I 
I 
-1 
Normal Variables 1 bar 1.5 bar 2 bar 
(Pressure) 
Figure 2.10: All normal variables can be transformed into centred reduced 
variables. 
19 
The use of centred reduced variables greatly simplifies the presentation of the theories 
underlying two-level factorial designs. These centred reduced variables will be used in all 
subsequent discussions. 
Normal variables can be converted to centred reduced variables using the formula: 
A-A, x=- 
step 
where, . x is the centred reduced variable measure in units of step, 
A is the variable in normal units (e. g., degrees Celsius or bar), - A, is the value (in normal units) of the variable at the mid-point, i.e., the point 
chosen as the origin for the centred reduced variable. 
In this case A, is 70°C for temperature and the step is 10°C 
Applying the formula to temperature, we get: 
A-70 
10 
x=- 
Substituting A for the temperatures of 60°C , 70°C and 80°C gives the values of -1, 0, 
and + 1 for x. 
5. GRAPHICAL REPRESENTATION OF MEAN AND EFFECTS 
The mean of all responses, which can be denoted as I or yo, is given by the expression: 
I = Y o = q [ + Y , + Y , + Y , + Y 4 ] 1 
or 
or, using the low and high temperature means: 
I = y =-[y+ 1 f Y - ] 
0 2 
As the response is assumed to vary linearly, the point represented by y+ is at the centre 
of the segment [ y,, y , 1, i.e. at the zero pressure level (Figure 2.11). The same is true for y- , 
the centre of the segment [ y l , y3 1. Using the same reasoning, the mean y o ofy+ and y - is at 
the centre of the segment [ y+ , y- 1. The mean of the responses is thus the value of the 
response at the centre of the experimental domain: level zero for temperature and level zero for 
pressure. 
20 
Y 
+ Y 
X l 
-1 0 +I 
Figure 2.11: A 22 experimental design and the response surface. 
If we now consider the plane passing through the zero pressure level and including the 
three responses y+, yo and y-, we observe that the straight line joining the responses y+ and y- 
(Figure 2.11) represents the variation in the response on going from the low to the high 
temperature levels. It therefore illustrates the overall effect of temperature. The mean 
temperature effect, or more simply, the temperature effect, is half the overall effect. The effect 
of temperature is shown by the change in the response on going from the zero temperature 
level to the high temperature level. We will use this concept frequently in the coming pages and 
we will use diagrams like Figure 2.12 to represent factor effect. 
21 
RESPONSE 
I 
EFFECT OF 
FACTOR 1 
-1 0 +1 FACTOR 1 
Figure 2.12: Classical diagram to represent factor effect. 
6. THE CONCEPT OF INTERACTION 
The following example introduces the concept of intera d o n between factors. 
6.1. Examp1e:The yield of a catalysed chemical reaction 
The problem: 
iif The same chemist studied the same reaction under the same d 
conditions But this time a catalyst was added in order to improve the 
I yield The question now is how pressure and temperature should be f+ 
regulated. The experimental conditions and results are summarised in J 
9 the experimental matrix (Table 2 2). 
In the previous example, the mean effect of a factor was defined at the zero level of the 
other factor. But we can also define the effect of a factor for any level of the other factor, for 
example the low or high level. We shall now do this to examine the concept of interaction. In 
Figure 2.12, the effect of pressure at the low temperature level is: 
1 E ~ =-[SO% - 60%] =10 % 
P(t 1 2 
while the effect of pressure at the high temperature level is: 
22 
Trial no 
1 
2 
3 
4 
1 
2 
Ep(t+) = -[95% - 7O%] =12.5 % 
Temperature Pressure 
-1 -1 
+1 -1 
-1 +1 
+1 +1 
Thus, the effect of a factor is not the same at the high and low levels of the other factor. 
The interaction between temperature and pressure is defined as half the difference 
It is said that there is interaction between the two factors. 
between the effects of pressure at the high and low temperature levels: 
1 E = -[12.5% -lo%] ~ 1 . 2 5 % 
Pt 2 
TABLE 2.2 
EXPERIMENTAL MATiUX 
THE YIELD OF A CATALYSED CHEMICAL REACTION 
60% 
70% 
80% 
95% 
We can calculate the interaction for the temperature in the same way. At the low 
pressure level it is 
1 E = - [ 70% -6O%] =5 % 
t(P-) 2 
While at the high pressure level it is: 
1 
E + = -[95% -SO%] =7.5 % 
t(P 1 2 
The value of the interaction is thus: 
1 E = -[7.5% -5%] ~ 1 . 2 5 % 
tP 2 
23 
which is the same as we calculated earlier. This result applies whether we refer to the 
pressurehemperature interaction or to the temperature/pressure interaction. 
Pressure 
+l Temperature -1 
60 OC 80 OC 
Figure 2.13: The effect of temperature is not the same at the low and high 
pressure levels: there is interaction. 
The main effect of temperature is defined and calculated as in the first example - the 
study of the yield of a chemical reaction, i.e., which is calculated with respect to the zero 
pressure level. The average response at the high temperature level is: 
1 
2 
y + = --[95%+70%] =82.5 % 
and the average response at the low temperature level is: 
1 
- 2 
y = -[60%+80%] =70 % 
The effect of temperature, E, is thus: 
1 
2 
E t = -[82.5% -7O%] = 6.25% 
24 
andthe effect of pressure is: 
1 
P 2 
E = -[87.5% -65%] = 11.25% 
With these results the experimenter can conclude his study. 
Results : 
The four trials indicate that the best yield is obtained with a 
I temperature of 80°C and pressure of 2 bar. The catalyst has no effect 
at 60°C or 1 bar. Increasing the temperature alone does not reveal the 
effects of the catalyst. Neither does increasing pressure alone. Both 
@ temperature and pressure must be increased for the catalyst to 
8 operate 
7. GENERAL FORMULA FOR INTERACTION 
We can now develop the general formula for calculating interaction using the responses 
measured at the experimental points. The definition of effects remains the same, whether or not 
there is interaction. The formulae for the response mean, temperature and pressure effects arethus unchanged: 
I = -[+y, 1 +Y, +Y3 + Y s ] 4 
E =-[ -y 1 - 
P 4 ' 
The interaction between temperature and pressure is indicated by Etp. At the high 
pressure level, the effect of temperature E (p+ ) is: 
while at the low pressure level, the effect of temperatureE is: 
t(P- ) 
1 
Et@- )= TEY2 - Y1 I 
25 
The interaction Etp is defined as half the difference of these two effects: 
This can be simplified to: 
This formula looks very like the one used to calculate the mean and effects. It can be 
obtained by constructing a list of the +1 and -1 having the same sequence as in the formula. 
This is easy as long as we note that the products of the pairs of elements in the temperature 
and pressure factor columns give a 12 column in which the signs are in the same order as those 
of the interaction (Figure 2.13). We can therefore construct an effects matrix (Table 2.3) fiom 
which we can obtain: 
the mean: using a column of four + signs. 
the effects of factors: using the sequence of signs in columns of the 
experimental design (experimental matrix). 
interaction between factors: each sign is calculated by applying the sign rule to 
the corresponding factors. e.g. in trial number 1, factor one is - and factor 2 is 
-; thus the interaction 12 has the sign (- ) x (- ) = (+) (Figure 2.14). 
Factor 1 Factor 2 Interaction 
I I + 
+ Multiplication 
I I 
sign - - 
+ 
+ 
+ sign 
I 
+ 
Figure 2.14: Calculating the interaction column using the sign rule. 
26 
Effects 
The effects matrix therefore has four main columns: one for calculating each effect, one 
for the interaction, and one for the mean. Columns for the trial number and for the responses 
are normally included in the table. The divisor and the calculated results are placed beneath the 
mean, factors and interaction columns. The arrangement is shown in Table 2.3 
76.25 6.25 11.25 1.25 
TABLE 2.3 
EFFECT MATRIX 
THE YIELD OF A CATALYSED CHEMICAL REACTION 
Interaction Response 
60% 
80% 
70% 
95% 
27 
RECAPITULATION 
Our analysis of the yield of a chemical reaction has shown: 
The strategy used in a two-level experimental design. Using experimental points 
that are the extremies of the experimental domain for each factor gives the best 
estimate of the effect of each factor. 
The notion of effect and the calculation of effects. 
The tools used: 
-experimental matrix, 
-graphical representation of the experimental domain on which are placed 
-graphing the effects in a plane passing through the centre of the 
the experimental results. 
experimental domain. 
The definition of reduced centred variables. 
The example of the yield of a catalysed chemical reaction: 
Introduces the concept of interaction. 
Gives the general formula for calculating interaction 
Shows how to construct an effects matrix. 
CHAPTER 3 
T W O - L E V E L C O M P L E T E 
F A C T O R I A L D E S I G N S : 2 k 
1. INTRODUCTION 
Two-level factorial designs are the simplest, but are widely used because they can be 
applied to many situation as either complete or fiactional designs. This chapter deals with 
complete designs. We will first examine a simplified example using only two factors. It will 
allow us to introduce several important basic concepts which will be used in later chapters. We 
will analyse a three-factor design and extrapolate the ideas acquired in this first example to an 
actual experimental design having five factors. Lastly, we will use the matrix approach to 
interpret two-factor complete factorial designs. 
2. COMPLETE THREE FACTOR DESIGN: 23 
2.1.Example: The stability of a bitumen emulsion 
The Problem: 
A manufacturer of bitumen emulsion wants to develop a new ak 
formulation. He has two bitumens, A and B. He wants to know the I 
30 
9 effects of a surfactant (fatty aad) and hydrochloric acid on the stability 
2 of the emulsion 
As there are three factors, he decides to use a 23 design with the following factors and 
response 
Factors 
= Factor 1 high and low fatty acid concentrations. . Factor 2 diluted and concentrated HCI. . Factor 3 bitumen A and B. 
Response 
Emulsion stability index, measured in stability points .The scientist knows that the 
experimental error of the response is plus or minus two stability points. He wishes to find the 
most stable emulsion: the one with the lowest stability index. 
Domain 
The two levels of each factor are indicated by +1 and -1 as reduced centred (or coded ) 
variables. The experimental domain is a cube (Figure 3 .1 ) and the eight experimental points 
chosen are at the corners ofthe cube. 
7 8 
6 
4 
Figure 3.1: Distribution of experimental points within the experimental domain.of a Z3 
design. 
31 
Trial no 
1 
2 
3 
4 
5 
6 
7 
8 
The experimental matrix (Table 3.1) is constructed in the same way as for the 22 design, 
but contains eight and not four experiments. To simpli@ table 3.1 we have used the signs + and 
- without the figure 1. The factors studied are not necessarily continuous variables, and two 
level factorial designs may include both continuous and non-continuous or discrete variables. 
Factor 1 Factor 2 Factor 3 
(fatty acid) (HCl) (Bitumen) 
- - - 
- - + 
- + 
+ + 
- 
- 
+ 
+ 
+ + 
+ + + 
- - 
- + 
- 
Level (-) 
Level (+) 
Response 
~~ 
low conc. diluted A 
high conc. concentrated B 
The effects of each factor and the interaction values are calculated fi-om the effects 
matrix (Table 3.2) as they were for the 23 design, i.e. by taking the experimental matrix signs 
for the main factors and using the sign rule for the interactions. The effects and interactions are 
obtained by a three-step calculation: 
0 The response is multiplied by the corresponding sign in the factor (or interaction) 
column, 
The products obtained are added, 
The sum so obtained is divided by a coefficient equal to the number of experiments 
For example, the effect of factor 3 is obtained fiom the formula: 
1 
8 
E, = -[-38- 37-26-24 + 30+ 28+ 19 + 161 = -4 
similarly, the third order interaction, 123, is obtained from: 
1 
8 
E 123= -[-3 8+37+26-24+30-28-19+ 161 = 0 
32 
Effects 27.25 -1 -6 -4 -0.25 -0.25 0.25 
r' 
+ 
6 + 
7 + 
8 + 
0 
TABLE 3.2 
EFFECTS MATRIX 
STABILITY OF A BITUMEN EMULSION 
+ + 
+ 
+ 
+ + 
Inter. 
23 
+ 
+ 
- 
- 
- 
- 
+ 
+ 
Response ~1 
The experimenter then analyses the results by drawing up a table of effects indicating, 
whenever possible, the experimental error estimated by the standard deviation (Table 3.3). 
TABLE 3.3 
TABLE OF EFFECTS 
STABILITY OF A BITUMEN EMULSION 
Mean 27.25 k 0.7 points 
1 -1.00 k 0.7 points 
2 -6.00 +_ 0.7 points 
3 -4.00 * 0.7 points 
12 -0.25 k 0.7points 
13 -0.25 k 0.7 points 
23 0.25 k 0.7 points 
123 0.00 k 0.7 points 
33 
0 
We can now begin to interpret these results. All the interactions are smaller than the 
standard deviation. These can therefore be considered to be zero and neglected. Factors 2 and 
3 are much greater than the standard deviation, and thus have an influence, while factor 1 is 
just a little larger than one standard deviation and much smaller than two standard deviations. 
It is thus unlikely to have any influence 
STABILITY A 
33.25 
27.25 
21.25 
-1 o + 
DILUTE CONCENTRATED 
HCI CONCENTRATION 
Figure 3.2: Effect of hydrochloric acid (factor 2) on bitumen emulsion stability. 
STABILITY 
31.25 
27.25 
23.25 
-1 +l 
A B 
BITUMEN 
Figure 3.3: Effect of bitumen type (factor 3) on bitumen emulsion stability. 
34 
Therefore, the concentration of fatty acid (factor 1 ) probably has no influence on 
The plane passing through the centre of the experimental domain and parallel to factor 2 
The plane passing through the centre of the experimental domain and parallel to factor 3 
emulsion stability over the range of concentrations tested. 
shows the effect of hydrochloric acid. 
reveals the effect of bitumen. 
We can now state the results of the experiment: 
Results: 
B The fatty acid concentrationhas little or no influence on the emulsion * 
g stability. The hydrochloric acid concentration has a large effect The ; 
I type of bitumen used is also important, the best stability (lowest Q 
i response) will be obtained with type B and dilute HCI There IS no xx 
s significant interaction. 
Note: 
A negative effect is not necessarily an undesirable one. An effect is negative when the 
response falls as the factor increases from -1 to + I . Conversely, a positive effect occurs when 
the response increases as the corresponding factor goes from -I to + I 
3. THE BOX NOTATION 
We could also use the Box notation [8] to indicate the effects and interactions. With this 
notation El is represented by a bold figure 1 (I), and E, = 2, E, = 3, etc. The mean is 
represented by the letter I 
3 The general formulae for the effects and interactions of a 2 design are’ 
1 
8 
Mean = 1 = -[+Y, +Y , + y 7 +Y, + Y ~ + y 6 +y7 +y81 
35 
4. RECONSTRUCTING TWO 22 DESIGNS FROM A 23 DESIGN 
Examining the results in a little more detail, we see that, as factor 1 is without influence, 
the experimental domain is reduced to a design in which only factors 2 and 3 have any 
influence. This also indicates that the response does not depend on the level of factor 1, but 
only on the levels of factors 2 and 3 . The responses can therefore be rearranged in pairs 
ignoring the factor 1 level, as shown in the following table (Table 3.4). 
TABLE 3.4 
EXPERIMENTAL MATRIX REARRANGED 
STABILITY OF A BITUMEN EMULSION. 
Trial no 
7 8 + + 
Response 
38 37 
26 24 
30 28 
19 16 
These results can also be displayed graphically, as in Figure 3.4 
29 [ fx 
CONCENTRATED 
+1 
HCI 
A B 
-1 Bitumen +1 
19]i7.5 16 
Average 
37.5 
25.0 
29.0 
17.5 
Figure 3.4: The bitumen emulsion is most stable when the hydrochloric acid is dilute and 
bitumen B is employed. 
36 
5. THE RELATIONSHIP BETWEEN MATRIX AND GRAPHICAL 
REPRESENTATIONS OF EXPERIMENTAL DESIGN 
This relationship is easy to understand for a 22 experimental design. An experimental 
point A can be defined: 
1 . by its coordinates in a Cartesian two dimensional space: a on the Ox, axis (horizontal) 
and b on the Ox, axis (vertical) as show in Figure 3.5. This is the graphical representation. The 
coordinates of a and b can be expressed in centred reduced (or coded) units or in classical 
units. 
" T / A 
Figure 3.5: Geometric representation of experimental points 
2. by the level of the two factors studied, trial A is defined by level a of factor x, and 
level b of factor x2. The coordinates of experimental points are the levels indicated in the 
experimental matrix 
X 2 
b 
a' - 
7- 
P 
b' 
- 
TRIAL 
NAME 
P 
P' 
- 
Figure 3.6: The matrix diagram of experimental points is equivalent to the geometric 
representation 
37 
A set of experiments is defined by several points with geometrical representation and by 
several trials with matrix representation. Figure 3.6 illustrated these two ways of representating 
two experimental points and the two corresponding trials. While it is also possible to produce a 
graphical representation of a three factor experiment in a three dimension space it is clearly 
impossible to do so for four and more factors. It is therefore necessary to find a way of 
representing experimental points in these hyper-spaces which is both convenient and applicable 
to any number of dimensions. The most common solution is to use matrix representation, 
which works for any numbers of factors. Table 3.5 shows four trials defined by the level of 
seven factors. 
TABLE 3.5 
The geometrical counterpart of Table 3.5 is a set of four points defined by their seven 
coordinates. Hence the experimental matrix gives the location of experimental points in the 
experimental space, Anyone producing experimental designs must learn to think in n- 
dimensional space without graphical representation. It is easy to pass from geometrical to 
matrix representation for two or three factors and experimenters must become accustomed to 
switching from n factor matrices to n dimensional space and vice versa. 
6. CONSTRUCTION OF COMPLETE FACTORIAL DESIGNS 
All factorial designs are constructed in the same way as those shown in Tables 2.2, 2.4 
and 3.7. The sequence of the signs for factor 1 is: 
- + - + - + - + ,etc. 
They alternate, commencing with a negative (-), 
The sequence of the signs for factor 2 is a series oftwo -, followed by two +: 
+ + - - + + ,etc. _ _ 
38 
The sequence for factor 3 is four negatives (-), followed by four positives (+). Any 
There is always the same number of + and - signs in the column for each factor. 
hrther factors have 8, 16, 32, - signs followed by 8, 16, 32 + signs. 
7. LABELLING OF TRIALS IN COMPLETE FACTORIAL DESIGNS 
When the + and - signs for each factor are laid out as shown above, the trials are 
numbered sequentially using whole numbers.(see Tables 2.2, 2.4 and 2.7). This is Standard 
numbering. 
As we will see later, the order of the trials can be changed, for randomisation, drift or 
blocking designs. But the number of each trial will be retained, regardless of its position in the 
layout. For example, trial number 23 of a complete 25 design (Table 3.7) always has the 
sequence of levels taken by factors 1 , 2 , 3 , 4 and 5: 
- + + - + 
There are other ways of labelling trials, but we shall not discuss them here 
8. COMPLETE FIVE FACTOR DESIGNS: 25 
8.1. Example: Penicillium chrysogenum growth medium 
The Problem: 
This design was used in a study to increase the yield of a penicillin 
production plant It was reported by Owen L Davies [Ill in his book 
"The design and analysis of industrial experiments" Penicillium 
chrysogenum is grown in a complex medium, and the experimenter 
wanted to know the influence of five factors 
1 concentration of corn liquor 
2 concentration of lactose 
3 concentration of precursor 
8 
%- 4 concentration of sodium nitrate 
f 
3. * 
y. 
i 
F 
-f 5 concentration of glucose 
5 
The response was the yield of penicillin, as weight (the units were not given in the 
original text). The experimental matrix of the 22 design summarizes the experimental data and 
the results of each of 32 trials. 
39 
Level- I 2% 1 2% 1 0 
Trial no 
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 
0 I 0 
TABLE 3.6 
EXPERIMENTAL MATRIX 
PENlClLLlUM CHRYSOGENUM GROWTH MEDIUM 
Level + I 3% 
Factor 1 
(corn liq.) 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
3% I 0.05% [ 0.3% I 0.5% 
Factor 2 
(lactose) 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
Factor 3 
:precursor) 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
Factor 4 
(sod.nit.) 
Factor 5 
(glucose) 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
Response 
142 
114 
129 
109 
185 
162 
200 
172 
148 
108 
146 
95 
200 
164 
215 
118 
106 
106 
88 
98 
113 
88 
166 
79 
101 
114 
140 
72 
130 
83 
145 
110 
40 
The effects were calculated by the standard procedure and the results are shown in the 
table of effects (Table 3.7). 
TABLE 3.7 
TABLE OF EFFECTS 
PENlClLLlUM CHRYSOGENUM GROWTH MEDIUM 
Mean 
1 
2 
3 
4 
5 
12 
13 
14 
15 
23 
24 
25 
34 
35 
45 
123 
124 
125 
134 
135 
145 
234 
235 
245 
345 
1234 
1235 
1245 
1345 
2345 
12345 
129 6 
-17 6 
0 6 
16 1 
1 0 
20 9 
-5 9 
-6 1 
-5 0 
2 6 
4 4 
-1 0 
3 0 
-1 0 
-10 5 
2 2 
- I 3 
-2 9 
-1 6 
1 7 
-3 2 
2 8 
-2 6 
2 7 
2 3 
0 6 
4 0 
2 6 
1 8 
4 2 
1 1 
6 3 
41 
Analysis of the effects of the factors showed that two factors have no influence: 
Factor 2, the concentration of lactose. 
Factor 4, the concentration of sodium nitrate 
And that the effects of three factors aresignificant: 
Factor I, the concentration of corn liquor 
Factor 3, the precursor concentration. 
0 Factor 5, the glucose concentration. 
A second order interaction appears to be significant: 
0 
0 
Interaction 35, between precursor and glucose. 
interaction 12345 seemed to be abnormally large. We will leave this for the 
time being, but come back to it later. 
TABLE 3.8 
EXPERIMENTAL MATRIX REARRANGED 
PENlClLLlUM CHRYSOGENUM GROWTH MEDIUM 
Trial no 
1 3 9 1 1 
2 4 10 12 
5 7 13 15 
6 8 14 16 
17 19 25 27 
18 20 26 28 
21 23 29 31 
22 24 30 32 
Factor 
1 
- 
+ 
- 
+ 
- 
+ 
- 
+ - 
Factor 
3 
- 
- 
+ 
+ 
- 
- 
+ 
+ - 
Results 
142 129 
114 109 
185 200 
162 172 
106 88 
106 98 
113 166 
88 79 
148 
108 
200 
164 
101 
114 
130 
83 
- 
146 
95 
215 
118 
140 
72 
145 
110 
Average 
141.25 
106.50 
200.00 
154.00 
108.75 
97.50 
138.50 
90.00 
If we look at the three factors which do influence the growth of Penicillium 
chrysogenum, we see that there are 32 trials, but we know that only 8 trials are required to 
study three factors. We can therefore group together the trials having the same levels for 
factors 1 , 3, and 5, regardless of the levels of 2 and 4. For example, trials 1, 3, 9, and 1 1 were 
carried out at the low level of factors 1, 3 and 5, so that the results of four trials should be the 
same, allowing for experimental error. The 32 trials are used as if four 23 designs had been 
performed. Table 3.9 shows the rearrangement of trials and the mean responses for each 
group. Thus, it appears as if a three factor design was repeated four times. 
42 
TABLE 3.9 
TABLE OF EFFECTS 
PENICILLIUM CHRYSOGENUM GROWTH MEDIUM 
Mean 1 2 9 . 6 i 6 
1 -17.6i-6 
3 16.1 k 6 
5 -20.9+6 
13 -6.1 + 6 
15 2.6*6 
35 -10 .5 f6 
135 -3 .2+6 
The experimental domain is reduced to a cube for the three influencing factors. We can 
therefore introduce the mean of each response at each corner of the cube to facilitate 
interpretation (Figure 3.7) 
GLUCOSE 
(5) 
(0.9 
/ 
108 
138 
+ 
200 
97 
90 
Figure 3.7: Diagram showing the results of the trials on Penicillium chrysogenum 
medium. 
43 
A high percentage of corn liquor (factor 1) evidently reduced the yield of penicillin. At a 
low level of factor 1, the yield was clearly improved by the addition of precursor and the 
absence of glucose. 
The presence of glucose reduced the effectiveness of the precursor. 
Results: 
Y 
I obtained 
b 0 with a low (2%) concentration of corn liquor 
I 0 with precursor. 
Q 0 without glucose, which reduces the yield and inhibits the precursor 
Under the experimental conditions used, the best yield of penicillin is 
108 138 
141 200 
Precursor 
0 % 0.05 % 
Figure 3.8: Influence of precursor and glucose at a corn liquor concentration of 2%. 
The interaction 12345 appears to be too great; and we will look at the reason for this in 
the chapter on blocking (Chapter 10). 
9. COMPLETE DESIGNS WITH k FACTORS: 2k 
We have seen that 22 , 23 and 25 designs can be used to study two, three or five factors. 
A 2k design can be used when there are more factors, with k having any desired size. 
The experimental matrix and the effects matrix are constructed according to the same 
rules as were used previously. The calculation of the k major effects and the 2k-k-1 
interactions are similarly performed. There is thus no theoretical limit to the number k of 
44 
Trial no 
1 
2 
3 
4 
factors that may be studied. But in practice the number of trials needed quickly becomes very 
large. A total of 27 (128) trials are required to study only 7 factors. This is a considerable 
number, and is rarely compatible with the facilities generally available in industry or university. 
This brings us to a most troublesome problem. We must find a way of reducing the 
number of trials without reducing the number of factors studied. We will examine this problem 
in Chapter 6. 
Mean Factor 1 Factor 2 
+I -1 -1 
+ I + I -1 
+1 -1 +I 
+ 1 +1 + I 
10. THE EFFECTS MATRIX AND MATHEMATICAL MATRIX 
The effects can be calculated from the experimental results using an effects matrix, 
which, for a 22 experiment, looks like (Table 3.10). 
Interaction 7 
This array of numbers can be used for a calculation; it is thus a mathematical tool, a 
Matrix. It can be written: 
+ I -1 -1 +1 
+I +1 -1 -1 
+ I -1 +1 -1 
+I + I +1 + 1 
A mathematical matrix is simply a table containing elements (here they are numbers) 
arranged in rows and columns. When the number of rows equals the number of columns the 
matrix is said to be square - otherwise it is rectangular. A matrix may contain just a single row 
and several columns (a linear matrix) or a single column and several rows ( a column matrix, or 
vector matrix). We will use matrices to express experimental results. Theyi may be shown in a 
rather special table because its contains only one column. They response vector matrix is: 
Y2 
Y3 
Y4 
Y = 
An analogous matrix can be written for the effects: 
45 
t x = 
E = 
+1 + I + I +1 
-1 +1 - 1 +1 
-1 -1 + 1 +l 
+1 -1 -1 +1 
Before we use these matrices we will examine the operations which can be performed on 
a single matrix, or between matrices themselves. The operations we need are transposition for 
a single matrix, and matrix multiplication for two or more matrices. 
+ I +I +1 + 1 
-1 +I -1 +1 
-1 -1 +1 +1 
+I -1 -1 +1 
Xt Y = 
y1 
y1 
y2 
y4 
The second operation we will need is the multiplication oftwo (or more) matrices 
10.2. Matrix multiplication 
Any reader not familiar with matrix calculations should read Appendix 1 before 
If we multiply matrix Xt by Y we get: 
continuing with this Chapter. 
The first element of the matrix-product is: 
[+Yl +Yz +Y3 +Y'll 
or four times the mean of the responses. Similarly the second element is: 
[-Y1 +Y2 -Y3 +Y,I 
46 
+ I +1 + l +1 
-1 + I -1 +1 
-1 -1 + I + 1 
+I -1 -1 + I 
or four times El, the effect of factor 1 . The calculations for the results of the third and fourth 
elements of the matrix-product are similar. We can therefore write: 
y , I 
El y 2 =4 
~3 E, 
y , El, 
which can be condensed to 
or 
X'Y = 4E 
1 t E = - X Y 
4 
This relationship for a 22 design can be extended to all two level complete factorial 
designs. When n is the number of trials we have 
1 
E = -X'Y 
n 
We now have, in the form of a matrix, the technique we used to calculate the effects and 
interaction of 2k designs. The matrix form clearly shows that the experimental responses y j 
have been transformed by the matrix Xt so as to be more readily interpreted. A factor increases 
(or reduces) the mean of responses I by a quantity equal to its effect. 
In the first example we examined, the yield of a chemical reaction, the four responses 
6O%, 70% 80% and 90% were difficult to interpret. But when they are transformed by the 
matrix Xt, the effect of each factor is obtained as if it were alone. A 10°C rise in temperature 
increases the yield from 75% to 8O%, while a pressure rise of 0.5 bar increases the yield fiom 
When the responses of a 2k are examined it is impossible to distinguish the influence of 
each factor. But the transformation by the Xt matrix displayed the useful information in the set 
of responses more clearly, revealing the effect of each factor as if it were alone. 
As the matrix X is the mathematical translation of the location of the experimental points, 
it is clearly most important that these points should be optimally placed in the experimental 
domain. Poorly positioned experimental points obscure the information instead of highlighting 
it. Well positioned experimental points clarifl the information (Chapter 16). 
The analysis of the specific X matrices which are use in all two level factorial designs can 
be developed a little. These are the Hadamard matrices, and they have quite remarkable 
properties. Let us first calculate the reciprocal of the X matrix andthen examine the product of 
X and its transpose, XtX. 
10.3. Inverse of X 
75% to 85%. 
The calculation of the inverse of a matrix is complicated for the general case, requiring a 
computer for high order matrices. But the calculation for X matrices of factorial designs 
(Hadamard matrices) is greatly simplified because of the following relationship: 
47 
+ 1 +1 +1 +I 
- 1 + 1 -1 +1 
--1 - 1 +1 +1 
+1 -1 -1 +1 
The inverse of X can be obtained by transposing X and dividing all the elements of the Xt 
The relationship 
matrix by n, the number of trials. 
X'Y =nE 
then becomes 
or 
X-'Y = E 
Y = X E 
+ 1 -1 -1 +1 4 0 0 0 1 0 0 0 
+1 +1 -1 - 1 0 4 0 0 0 1 0 0 
0 0 1 0 + 1 - 1 + I -1 0 0 4 0 
+I +1 +1 +1 0 0 0 4 0 0 0 1 
= 4 - - 
This formula can be used to calculate the responses from the effects 
which can be condensed to 
XtX =41 
For this design, the product of the matrix of effects by its matrix transpose is 4 times the 
The general form of the formula for all two level complete factorial designs is 
unit matrix. 
X'X =nI 
where n is the number of trials. 
The matrix XtX is equal to n times the matrix unit in the case of two level factorial 
designs. It can be demonstrated that, in this case, the precision obtained for the effects is the 
best than might be hoped for (see Chapter 5). Experiments in which a two level complete 
factorial design is used are certain to provide calculated effects with maximum precision. 
10.5. Measurement units 
The responses yi were measured with a unit, metre, centimetre, volt, etc., or a less usual 
unit, such as an index, percentage or variance. 
The matrix Xt does not change the unit in which yi is measured, it simply transforms the 
trials results into a system that is easier to interpret. As a result, the mean, the main effects and 
the interactions are evaluated in the unit used to measure the responses. 
48 
RECAPITULATION. 
We have used the example of bitumen emulsion stability to: 
Extend the concepts acquired with 22 design to a z3 design. 
Extend the concept of interaction. 
Examine the rules for calculating effects and interactions from an effects matrix. 
Introduce Box notation. 
Present the results as a table of effects. 
Show that both continuous variables (temperature and pressure) and discrete 
variables (type of bitumen) can be studied simultaneously within the same 
experimental design. 
Using a 25 design allowed us to: 
Apply the principles acquired to a real case. 
Use the fact that some factors were without influence to construct a replicate 
factorial design. 
The mathematical matrix representation of two-level factorial designs was used to: 
Calculate effects, interactions and mean from the responses. 
Introduce transposed matrices, product matrices and vector matrices. 
To simplify the interpretation of results which are transformed into mean, 
effects and interactions. 
Guarantee that the effects and interactions calculated have the highest possible 
precision. 
Define the units for measuring effects and interactions. 
CHAPTER 4 
E S T I M A T I N G E R R O R 
A N D S I G N I F I C A N T E F F E C T S 
1. INTRODUCTION 
Let us now examine a problem that we touched on lightly when we discussed the 
bitumen emulsion stability example in Chapter 3. The problem raises two questions, which we 
shall attempt to answer in this chapter: 
When can an effect be considered significant? 
On what criteria can such a conclusion be based? 
The method generally used to answer them requires estimating the error AE in the 
determination of the effect E, and comparing this error with the effect itself. There are three 
possible situations: 
The effect is much larger than the error: 
E>> AE 
In this situation, there is no problem, the effect clearly has an influence. 
50 
The effect is smaller than the error: 
E < < A E 
In this case, the effect is without influence in most situations 
The sizes of the effect and error are similar: 
E - A E 
This situation is not so clear, the effect may have no influence or it may have a small 
influence. 
Common sense, a knowledge of the phenomenon and statistical tests are required to 
reach an appropriated conclusion. If the effect has no major role in the study, and if a poor 
decision has little or no consequence, it is not worth spending time to find out. But if there are 
high financial stakes or dangers linked to the decision, statistical studies should be performed 
and complementary tests should be considered in order to evaluate the risks. 
We will not describe statistical tests here, the interested reader should consult 
appropriate texts [12, 13, 14 and 151. But we will examine the aspects that fall within the 
domain of the experimenter: the definition and origin of the measurement error and how to 
estimate the error of an effect. 
2. DEFINITION AND CALCULATION OF ERRORS 
The total error of a measure may be considered to be the sum of two errors: random 
error and systematic error. For example, if an investigator repeats the same measure several 
times under the same conditions (same method, same instrumentation, same starting materials, 
etc.) he will not obtain exactly the same result each time: 
78.8 
80.4 
81.4 
79.8 
80.2 
80.2 
78.0 
79.7 
82.1 
80.4 
Although the investigator has performed ten measures, he does not record all ten of them 
in his report. Instead, he summarizes the information as two numbers, one reflecting the most 
probable true value of the measure, the other estimating the dispersion of measures around this 
most probable true value. The arithmetic mean is used as the best estimation of the true value, 
while the square root ofthe variance is generally used to estimate the dispersion. 
5 1 
2.1. Arithmetic mean 
If n measures are obtained, and if the individual values are indicated by yi, the mean is 
given by the relationship: 
For the above example, the mean of the 10 results is calculated as: 
1 
10 
7 = -[78.8+80.4+81.4+79.8+80.2+80.2+78+79.7-t82 1+80.4] = 80.1 
2.2. Dispersion 
The dispersion of measures is rather more difficult to define. We need to find a number 
to estimate dispersion. But the estimate may vary depending on the assumptions made and the 
definitions selected. We will adopt the most widely-used definitions, variance and standard 
deviation. These are defined in Appendix 2 for an inftnitely large population of measurements. 
An estimation of standard deviation is calculated for a smaller sample (fewer than about 50 
measures) as follows. First, the difference between each measure yi and the mean y is 
calculated, these differences are squared, the squares summed and the sum divided by the 
number of measures, n, minus 1. This gives an estimation of the variance. The standard 
deviation (denoted by the letter s) is the square root of the variance. 
The divisor n-1 is used because only n-1 independent measures were used to calculate 
the variance, as there is a relationship between the n initial measures: the definition of the 
mean. We will now look at the step-by-step calculation of standard deviation, using the ten 
measures: 
1 . Calculation of deviations and their squares 
Table 4.1 shows the calculation the deviation and their squares 
52 
TABLE 4.1 
Results 
78.8 
80.4 
81.4 
79.8 
80.2 
80.2 
78.0 
79.7 
82.1 
80.4 
Mean 
80.1 
80.1 
80.1 
80.1 
80.1 
80.1 
80.1 
80.1 
80.1 
80.1 
~ 
Deviation 
-1.3 
0.3 
1.3 
-0.3 
0.1 
0.1 
-2.1 
-0.4 
2.0 
0.3 
Deviation Square 
1.69 
0.09 
1.69 
0.09 
0.01 
0.01 
4.41 
0.16 
4.00 
0.09 
2. Sum of deviations squared (SDS) 
The ten squared deviations are summed: 
SDS = [ 1.69+0.09+ 1.69+0.09+0.0 1 +O.O 1 +4.4 1 +O. 16+4+0.09] = 12.24 
3. Variance 
The variance, 5’. is obtained by dividing the SDS by 10-1-;1 
=1.36 12.24 
9 
s2 =-- 
4. Standard deviation, s, is the square root of the variance 
Thus, the set of ten measures can be summarized by the meun, 80.1 and the dispersion, 
estimated by the standarddeviation, 1.2. 
In this book we will use the standard deviation to estimate the dispersion of measures. 
But there are other methods. The uncertainty due to the dispersion of measures around the 
mean is called random error. 
In addition to this random error, there may also be variations affecting all the measures. 
All the results may be greater, or smaller, than one, two or several units. This error is no longer 
random as it affects all measures in the same way: this is a systematic error. 
Random error is most readily appreciated; it is also the most easily detected and 
estimated. Hence, the topic is well documented. Systematic error is much less evident, and its 
discovery often requires some detective work. The investigator must always remember that the 
total error is the sum of the two types of error, and that both must be kept to a minimum. 
53 
TOTAL ERROR = RANDOM ERROR + SYSTEMATIC ERROR 
Note: 
the random dispersion around the mean. 
In this book, we will consider the random error to be equal to one standard deviation of 
3. ORIGIN OF THE TOTAL ERROR 
The dispersion is due to small variations in the experimental conditions, such as ambient 
temperature, reading errors, or small changes in electrical voltage, etc. The investigator 
controls certain factors very carefully when making his measurements, but all the factors 
influencing the results cannot be controlled. The factors whose levels are voluntarily fixed are 
the controlled factors, the others are uncontrolled factors. Controlled factors do not 
introduce experimental errors. Only variations in the uncontrolled factors give rise to the total 
error. 
Errors due to random variations in the uncontrolled factors are random eryors, The 
investigator may estimate them from the standard error or any other value characteristic of the 
dispersion. 
Errors due to systematic variations in uncontrolled factors are systematic errors. In 
general, an experimenter does not suspect the existence of this sort of uncontrolled factor and 
special techniques must be used to detect them. In order to analyse total experimental error in 
more detail, we must consider the mathematical model. A response y depends on a large 
number of variables, x,: 
y = . f (X, , x2, %...> x, ,... 1 
These variables do not all have the same influence, they can be classified into the 
following five categories: 
1, The variables studied in the experimental design to which two levels are assigned 
Level +I 
Level -1 
7 
0 
0 0 
' 
1 2 3 4 5 6 
Figure 4.1: Factor 1 studied in the experimental design. 
0 
I 
8 
54 
These factors are controlled, and their levels are accurately defined. Such variables 
introduce no error. Their variations explain the different values of the response. For example, 
there are three controlled factors in a 22 design. Each of them takes level + 1 or -1 (Figure 
4. I), perfectly defined by the experimental matrix. If there were no other influencing factors, 
the response would always be the same in all the replicate trials, i.e. trials with the same levels 
of controlled factors. 
2. Uncontrolled variables which remain invariate throughout the experiment 
These variables do not change, but they do introduced a constant displacement in the 
measurements ofy; these give rise to systematic errors. 
For example, if an experiment was carried out in two separate sub-experiments, this 
uncontrolled variables may have different levels in each of the sub-experiments. Level a in the 
first sub-experiment and level b in the second (Figure 4.2).The experimenter does not know 
about this factor, but the responses are altered depending on the level of this factor. We will 
see that precautions can be taken - Blocking - against this type of uncontrolled factor. 
Levela 6 6 6 6 6 Level a 
Levelb 6 b e Level b 
Figure 4.2: Uncontrolled factor which remains invariate throughout each sub- 
experiment: level a in the first sub-experiment and level b in the second 
one. 
3. Uncontrolled factors whose levels change in a regular fashion during the experiment. 
These variables give rise to a drift in the response. The experimenter is generally ignorant 
of these uncontrolled factors. We will see how to combat these systematic errors later with 
anti-drift designs. 
Level a 0 
Level b 0 
Level c .. 
Level d * 
Level e .. 
Level f * 
Level g 0, 
Level h 0 
1 2 3 4 5 6 7 8 
I ' I l l 1 
Figure 4.3: Uncontrolled factor whose level changes regularly. 
4. Uncontrolled variables whose levels are fixed at a constant value during a trial or during 
several trials, but differ during the overall experiment. 
They introduce systematic errors which are difficult to counteract and generally ignored 
by the experimenter. The best way to master these factors is to include their systematic 
variations in random errors by the technique of randomization. 
Level a o m . 
Level b o * o 
Level c o m 
/ l / l l / I l 
1 2 3 4 5 6 7 8 
Figure 4.4: Uncontrolled factor whose level is constant during one or more trials. 
5. Uncontrolled variables whose levels do not change in any specific fashion either during a 
trial or throughout the experiment. 
These are the random variables which give rise to random or experimental errors. 
Statistical calculations can be used for this type of error. 
56 
Level a 
Level b 
Level c 
Level d 
Level e 
Level f 
Level h 
Level g e 
1 2 3 4 5 6 7 8 
Figure 4.5: Uncontrolled factor whose level changes randomly. 
4. ESTIMATING THE RANDOM ERROR OF AN EFFECT 
The random error of a response has repercussions for the calculated effects and 
interactions. We shall see that the error of effects can be estimated in several ways, depending 
on what is known of the phenomenon studied andlor the time available for this estimation, 
There are several situations, which range from excellent to not so good (We shall begin with 
the best ): 
The experimenter knows the value of the experimental error Ay affecting the 
response. 
The experimenter does not know the value of the experimental error affecting 
the response, but is able to estimate it by carrying out extra experiments. 
The experimenter does not know the value of the experimental error of the 
response, and does not want to perform any extra experiments. 
4.1. The investigator knows the experimental error of the response 
This error was established from a series of measures containing enough measures to 
draw the distribution curve. For sake of simplicity, we will adopt a Gaussian (or bell-shaped) 
distribution (Appendix 2) . 
This distribution has two characteristic parameters: the mean ~1 and the standard 
deviation, 0. The standard deviation can be used to define the experimental error because, odd 
as it may seem, the value taken as the experimental error Ay may vary, and it is left to the 
judgement of the investigator to establish a value appropriate to the requirements of his 
problem. Only the standard deviation CJ is mathematically defined, and we will refer to this 
value. 
A numerical result yi is obtained when a response is measured. This value differs from 
the true value, which cannot be known, by an amount which is also unknown. But we do know 
that the true value has certain probability of being within an interval around yi. This is the 
57 
cofidence interval; the smaller it is, the smaller the probability that the true value y , lies within 
it. The larger it is, the greater the probability that y , lies within it. Figure 4.6 shows the 
probability associated with the confidence interval, expressed as standard deviation, for several 
cases. 
f f f 
1 
I 1 I 
Figure 4.6: Percentage associated with the confidence intervals: f 0, f 20, k 30. 
y , has a 68% probability of lying within the interval yi !C 0 
and a 32% probability of lying outside the interval yi f 0. 
y , has a 95% probability of lying within the interval yi + 2 0 
and a 5% probability of lying outside the interval yi f 20. 
y , has a 99.9%probability of being within the interval yi f 30 
and a 0.1% probability of being outside the interval yi f 30. 
If the investigator chooses Ay = + 20, there is a 95% probability that he is correct in 
saying that the true value lies within the interval yi f 20 and a 5% chance that he is wrong to 
say so. The value that the investigator adopts for the experimental error depends on the 
problems, the risks and the stakes involved, knowing that there is always a certain percent 
chance of being wrong. 
It is convenient to choose plus or minus one standard deviation as experimental error, 
knowing that this will be right about two times out of three, and wrong once in three. 
Multiplying this value by a coefficient greater than one reduces the chances of being wrong. 
We have simply given an evaluation of the experimental error Ay of the response. But we 
are actually looking for the error of the effect of a factor. An effect is calculated with n 
responses. If the experimental error is the same for all responses, the error AE on the effect is 
given by the relationship (Appendix 2): 
AY 
& 
A E = - 
If the distribution of the error Ay is normal (Gaussian), that of AE around E is also 
normal. If we take the standard deviation 0 as experimental error, the error on E becomes: 
58 
This error depends on the number of measures, n, used to calculate E. The more 
measures used, the smaller the error of the effect. 
In the study of bitumen emulsion stability discussed in Chapter 3, the investigator used an 
experimental error of plus or minus two points on a response. The calculation of an effect in 
the complete Z3 design required eight responses. The error of the effect is thus estimated to be: 
0 
All the effects and interactions between -0.7 and +O 7 are very likely to have a numerical 
value close to zero (i.e., 0.7 and zero are statistically indistinguishable). If the effect is a little 
larger than 0.7, there is less chance that it is zero. We have seen how to estimate this 
probability with the help of statistics. The investigator must select an appropriate value for AE 
as a hnction of the risks and the stakes of the problem investigated. In the case of this 
example, the investigator chose a limit of 1 stability point, knowing that an effect of this 
magnitude may be negligible, while still having a little influence. 
The above discussion can be illustrated by a graph with the values of the effects on the 
abscissa and the percent probability that the effect is significant on the ordinate (Figure 4.7). 
This graph can be made general by measuring the effect with d& as unity, so that the effect 
is measured in terms of oE (standard deviation of the effect). 
If the effect equals 3 standard deviations, it will be without influence in 0.1% of cases 
and have a small influence in 99.9% of cases. 
If the effect equals 2 standard deviations, it will be without influence in 5% of cases and 
have a very small influence in 95%. 
Lastly, if the effect equals one standard deviation, it will be without influence in 32% of 
cases, and have a very very small influence in 68%. 
Probability 
100 
90 
80 
70 
60 
5 0 
10 
30 
20 
10 
0 
0 1 2 3 J 
Effects measured with standard deviation 
Figure 4.7: Plot of effect measured with a standard deviation of unity against the percent 
probability of it being significant. 
59 
Clearly, it is absolutely imperative that the investigator knows the estimation of the 
precision of the responses measured. The most favourable case is the one we have discussed, in 
which the distribution of measurement errors and the corresponding standard deviation are 
known. Under these circumstances, it is possible to select an appropriate value for the 
experimental error of one, two or three standard deviations, and to evaluate when a factor is 
significant or not. 
In the second, less satisfactory situation, the investigator does not know all these 
elements. But we shall see that there are several ways of estimating errors, and that all is not 
lost even when the situation is less than ideal. 
4.2. The experimental error of the response is unknown 
In this situation, the investigator can carry out a few supplementary trials to obtain an 
estimation. There are then two possibilities: repeat several measures on the same experimental 
point or repeat the same experimental design once more. 
Several measures on the same experimental point 
A point in the centre of the experimental field is generally chosen, and it is assumed that 
the error remains the same throughout the domain. The problem is to calculate an estimate of 
the standard deviation with only a few experimental points. If the distribution of the whole 
population is Gaussian, the distribution of a small sample is a Student curve. If 4 or 5 measures 
are performed, an estimate s of the standard deviation can be obtained from: 
In this situation the confidence interval is larger for the same risk of mistakes and the 
same probability of being wrong. Table 4.2 shows the multiplication coefficients employed, 
depending on the number of measures used, to calculate standard deviation and the desired 
degree of confidence. For a very large number of measures, the Student distribution is very like 
the Gaussian curve. The Gaussian curve is produced when N = co. 
For example, if the standard deviation is estimated from 5 measures, the 95% confidence 
interval is k 2.78s around the value measured. When the investigator knows the standard 
deviation CT of the population, the confidence interval for the same percent success is -t 1.96 o. 
The multiplication coefficient is generally called t for Student curves (Table 4.2). 
60 
TABLE 4.2 
VALUE OF t AS A FUNCTION OF THE CONFIDENCE EXPECTED AND THE 
NUMBER OF MEASURES PERFORMED 
Number of measures used to calculate s. 
, 
Repeat the whole experimental design 
This provides a total of two responses for each experimental point, so that a mean value 
of the standard deviation over the whole experimental domain can be calculated. Let us use a 
Z 3 design camed out twice as the basis for our calculation. Table 4.3 shows the trials 
performed and the responses obtained. The variance of each trial is calculated first, then the 
mean variance of all the trials. This variance is then used to deduce the mean error of a 
measure. which is itself used to calculate the error of the effect. The step-by-step calculations 
are : 
TABLE 4.3 
CALCULATION OF THE VARIANCE OF RESPONSES IN A 
DUPLICATED 23 EXPERIMENTAL DESIGN 
Trial no Factor 
2 
- 
- 
+ 
+ 
- 
- 
+ 
+ - 
Factor 
3 
- 
- 
- 
- 
+ 
+ 
+ 
+ - 
First 
result 
60 
74 
49 
70 
52 
81 
46 
77 
Second 
result 
56 
42 
84 
44 
18 
2 
2 
61 
1. Variance of the first and subsequent trials 
For the first trial, the mean value of 62 is calculated from two results, 60 and 64. The 
variance, s:, is calculated from: 
s: = -[(60-62)2 1 +(64-62)2] 
2- 1 
The variance for the other trials in Table 4.3 are calculated in the same way. 
Note: 
The difference in the meaning of the two values, s and B, is theoretical: B measures the 
standard deviation of a population and s is an estimate of B deduced from a random sample of 
that population. In practice, only s is known, and we shall refer to this standard deviation in the 
following pages. 
2. Mean variance of a response 
The above calculation gives 8 variances; the mean variance s:, is: 
1 96 
S; = -[8+18+2+32+8+18+8+2] = - =12 
8 8 
The mean standard deviation for the response of a single trial is the square root of the 
mean variance: 
S , = fi =3.46 
3. Variance of an effect 
from: 
An effect is calculated with 16 responses and the variance sg of an effect is calculated 
4. Standard deviation of an effect 
This is the square root of the variance of an effect 
.sF, = 6% =0.86 
62 
In practice, the same experimental design is rarely repeated in order to estimate 
experimental error because it is much too costly in termsof time and money. If more tests can 
be done, it is better to study more factors. Nevertheless, the above calculation is far from 
useless, as it is important in the frequent situation in which there is a clearly non-influencing 
factor In this case, the complete 2k design run can be considered as a repeated 2k-1 design. 
The result of a trial is unchanged if the level of the level of a non-influencing factor is higher or 
lower We can therefore rearrange all the trials of the 2k design in pairs according to the levels 
of the influencing factors This gives us two results per trial in a Zk-' design. which therefore 
gives two results per test We examined an example in which two factors were without 
influence in Chapter 2 (Penicillium chrysogenum growth medium). In this particular case, the 
experiments were regrouped to give 4 results per trial. 
4.3. The experimental error of the response is unknown, and the 
experimenter does not want to perform any supplementary experiments 
There is a way of estimating error under these circumstances, but it must be assumed that 
the high order interactions are zero and their values are estimates of experimental error. Let us 
assume that the results o fa 24 design are those shown in Table 4 4 
If the third and fourth order interactions are estimates of the effect or interaction errors, 
the mean of this error is obtained by calculating the variance of each interaction, followed by 
computing the mean variance 0: 
TABLE 4.4 
TABLE OF EFFECTS 
Mean 82.30 
1 -2.00 
2 -10.80 
3 30.2s 
4 -4.75 
12 1 00 
13 -2.50 
14 0.30 
23 s 7s 
24 -0.50 
34 0.60 
I23 -0.25 
I24 0 80 
134 0.50 
234 -0.30 
1234 0.10 
63 
1. Interaction variances: 
Variance of 123 = (-0.25)2 = 0.0625 
Variance of 124 = (0.80)2 = 0.6400 
Variance of 134 = (0.50)2 = 0.2500 
Variance of 234 = (-0.30)2 = 0.0900 
Varianceof 1234= (0.10)2 = 0.0100 
2. Mean variance of the effect: 
1 
5 
o = - [ 0.0625+0.64+0.25+0.09+0.0 I] 
Hence, the mean standard deviation of the effect is: 
= 0.46 
5. PRESENTATION OF RESULTS 
5. I . Numerical results 
We have examined the techniques for calculating the standard deviation of the effects. 
The results should be presented by indicating the value of the effect followed by plus or minus 
the standard deviation. The units for both the effect and its standard deviation should also be 
mentioned: 
3 + 0.3 cm3 (effect, + 0, units) 
This indicates that the real value of the effect has 68% probability of being between 2.7 
and 3 . 3 cm3 (provided the distribution is normal). If we wish to increase the probability of 
being correct, the confidence interval must be increased. Thus, if we wish to be right at least 95 
times in 100, we must use two standard deviations and write: 
3 rf- 0.6 cm3 (effect, k 20, units) 
5.2. Illustration of results 
The presentation suggested by Daniel [ 161 can be used to show all the results, in addition 
to the table of effects presented at the end of each study. 
64 
All the effects and all the interactions resulting from a study are arranged in ascending 
order. For example, in a study on the fabrication of plastic drums (Chapter 7) the investigator 
arranged the 15 results in ascending order (the mean is not included here): 
-2.7-0.3-0.3-0.25-0.2-0.15-0.1 -0.1 -0.05-tO.l +0.2+0.5+1.9+2.5+3.2 
These values are plotted on Gaussian-linear axes using graph paper which has linear 
graduations on the abscissa and a Gaussian scale on the ordinate. Some of the points are 
generally grouped around zero. If these points form a line their distribution is normal and their 
numerical values can be considered to be estimates of the experimental error. The other points 
which do not line up indicate a non-random distribution. This method of displaying the results 
reveals the two groups of interest: 
The effects and interactions having no significant influence . 
The influential effects and interactions . 
Gaussian 
scale 
Effects and Interactions 
Figure 4.8: Illustration of the result, from Daniel 1161. There are two groups of results: 
1) significant effects. 
2) non-significant effects which may be considered as estimations of 
random error. 
65 
RECAPITULATION 
Total error contains two components: random error and systematic error. Random error 
is relatively easy to evaluate, while systematic error is difficult to detect. But the investigator 
must neglect neither. 
TOTAL ERROR = RANDOM ERROR + SYSTEMATIC ERROR 
A response y depends on several variables or factors which can be assigned to one of 5 
categories: 
0 Factors controlled by the investigator during the tests. 
Uncontrolled factors whose levels remain fixed throughout the performance of 
an experimental design. 
0 Uncontrolled factors whose levels vary regularly throughout the performance of 
an experimental design. 
0 Uncontrolled factors whose levels remain fixed during a trial but not at the same 
level from one trial to another. 
Uncontrolled factors whose levels vary randomly during the execution of an 
experimental design. 
The influence of a factor is determined with reference to the known experimental error. 
This may be evaluated by one of the following methods: 
With reference to the distribution of measures around a central value and an 
estimate of the standard deviation of the response. These are used to calculate 
the standard deviation of the effect. 
By measuring a few values to obtain an estimate of the response standard 
deviation, followed by calculation of the standard deviation of the effect. 
By using high order interactions to calculate an estimate of the effect standard 
deviation. 
The probability that the effect has an influence can be estimated by comparing the effect 
itself with the standard deviation of the effect. 
It is good practice to present results with their standard deviations, because two values 
cannot be considered to be the same unless both the values and the standard deviations are. For 
example, a result of 2 cm is not the same if the two values are 2 ?C 0.1 cm and 2 k 1 cm. 
The presentation proposed by Daniel gives a graphical idea of the dispersion and of 
dispersion normality. It is also a way of showing influencing factors. 
This Page Intentionally Left Blank
CHAPTER 5 
T H E C O N C E P T O F 
O P T I M A L D E S I G N 
1. INTRODUCTION 
It is by no means easy to choose the best strategy for performing measures. We will examine 
the problem using a series of weighings. Any investigator carries out an enormous number of 
weighings during hidher working life, but few have ever wondered if they are doing it in the best 
possible way The first person to study this question was Hotelling [17]. The surprising thing is 
that this question was not examined until relatively recently, in 1944, although people have been 
weighing things for centuries. 
Let us assume that an investigator has used an old two-pan balance to weigh two objects, A 
and B, having masses of ma and mb. He placed object A on one pan and read off the weight to 
obtain p, . As he was aware that he could not avoid an error 0, he wrote: 
68 
Object B was weighed in the same way to give: 
and 
mb = p2 * (J 
If p, and p2 had values of 10 and 25 grams respectively, and o was 0.1 gram, then 
m a = l O + O . l g 
m h = 2 5 F 0 . 1 g 
Thus, the investigator made two weighings and obtained two results with an error of 5 o. 
This is how everyone weighs things throughout the world. But Hotelling noticed that greater 
precision could be obtained for the same effort if both objects were included in each weighing. 
He camed out a first weighing with A and B together in the same pan, and then placed A on 
one pan and B on the other to obtain the difference. He was then able to deduce the masses m, 
and mb as follows: 
m,+m, =P1 
ma -mb =P2 
Hence, 
Applying the variance theorem (Appendix 2) gave: 
1 1 
4 2 
v(ma)= -[02 +02] = -02 
The error of the results of these measures is ol& and not 0, so that: 
ma =10 5 0.07 g 
mb = 25 k 0.07 g 
69 
The usual weighing method could only give the same result by weighing both A and B twice, 
four measures rather than two. This indicates one of the reasons for including all variables, or all 
factors, in each trial: for the same number of trials, the precision can be improved. 
2. WEIGHING AND EXPERIMENTAL DESIGN 
Let us treat the Hotelling example using the formalism introduced in Chapter 2. The factors 
are A and B and the responses are the weights returning the pans to equilibrium at each weighmg. 
We must also adopt the convention of considering the weight of the object placed in the left hand 
pan to be positive, and the weight of an object placed in the right hand pan to be negative (Figure 
5.1). 
Figure 5.1: Sign convention adopted for weighings 
The range of weights for object A is thus -pa to +pa, depending on whether it is on the left 
or right-hand pan. Using coded variables, -pa is -1 and +pa is +1 , while zero is the absence of A. 
- Pa 0 + Pa 
-1 0 +1 
The same convention can be adopted for B, and the effect of B on the balance pan is: 
- ph 0 + ph 
-1 0 +1 
The two ways of weighmg, the standard method and Hotelling's method can thus be 
presented as experimental matrices. The calculations are performed as for an experimental design 
and the effects are the weights of each object. 
70 
2. I . Standard method 
First weighing: A on left-hand pan, B is not weighed 
The responsey, is log. 
Second weighing: A is replaced by B 
The response, y2 is 25g. 
TABLE 5.1 
EXPERIMENTAL MATRIX 
Standard method of weighing two objects i’-tl-”i Fl 
25 grams 
I Effect I 10 grams 1 25 grams I 
As there is no interaction between A and B, the experimental and effects matrices are 
The matrix X for the standard weighing method is: 
identical. 
X=JLI 0 + I 01 
It is not surprising that the effects equal the responses: the effects matrix is a unit matrix. 
2.2. Hotelling method 
First weighing: A + B on the left-hand pan 
The response y , is = 3 5g. 
Second weighing: B on the left-hand pan, A on the right-hand pan 
The response yz is = 15g. 
71 
TABLE 5.2 
EXPERIMENTAL MATRIX 
Hotelling method of weighing two objects 
35 grams 
-1 15 grams 
I Effect I 10grams I 25 grams I 
The effects matrix is identical to the experimental matrix: 
This matrix, in which there is no zero, is characteristic of the Hotelling method, in which all 
The effects are certainly the same (the same weights) as in the standard method, but the 
objects are included in all tests. 
precision is greater. 
2.3. Strategy for weighing four objects 
Different strategies can be adopted for weighing four objects 
a. Standard strategy 
If we had not read the above section, we would weigh each of the four objects one after the 
other, and the experimental matrix would be: 
X = 
1 0 0 0 
0 1 0 0 
0 0 1 0 
0 0 0 1 
72 
If the responses are 10, 2.5, 1.5 and 30 grams, measured with a precision of 0.1 gram, the 
measured effects are exactly as the same as the responses, with the same precision. This is not 
surprising as the matrix is a unit matrix. 
b. Intermediate strategy 
We can use the same approach as for weighing two objects: A + B and C + D, by 
performing the following weighmgs (Figure 5.2). 
A B B 
Figure 5.2: Weighing four objects using a specific strategy 
First weighing: A+B on the left-hand pan 
Responseyl = 35g. 
Second weighing: A on the right-hand pan, B on the left-hand pan 
Response yz = 15g. 
Third weighing: C + D on the left-hand pan. 
Responsey3 = 45g. 
Fourth weighing: C on the right-hand pan, D on the left-hand pan. 
Response y4 = 15g. 
73 
The system of equations from this is: 
y , = +ma + mb 
y 2 = - m a + mb 
y 3 = + m c + md 
y4 = - mc + md 
from which can be calculated the mass of each object 
1 
2 mb =-[Yl + Y 2 ] 
me = - [ Y ~ - Y ~ I 1 
md =-[Y3+Y41 1 
2 
2 
The theorem of variance can then be used to calculate the error of ma and the three other 
masses: 
Thus the error for ma is o/J2 = 0.07, from which: 
1 
2 
ma = -[35-15]=10+0.07 g 
1 
2 
mb = -[35+15] =25*0.07 g 
1 
2 
mc = --[45-15] =15&0.07 g 
1 
2 
md = -[45+15] =30+0.07 g 
74 
The system ofequations can be display by using the matrix form: 
x = 
tl + I 0 0 
-1 t l 0 0 
0 0 +1 + I 
0 0 -1 tl 
tl + I 0 0 
-1 + I 0 0 
0 0 +1 +1 
0 0 -1 +1 
This strategy, illustrated by the X matrix, is better than the one-object-at-a-time strategy, but 
is it the best? How can we obtain the smallest possible error? Could we do better than O.O7g, 
without increasing the number of trials or weighings? This is not possible unless we include more 
objects in each test. Let us try to use all the objects in each weighing (Figure 5.3) 
Figure 5.3: Weighing four objects using an optimal strategy. 
75 
c. Optimal strategy 
The following weighings are performed: 
First weighing: all objects on the left-hand pan. Responsey, = 80g. 
Second weighing: A + C on the left-hand pan, B + D on the right-hand pan. 
Response y2 = -3Og (weights on the left-hand pan are considered negative). 
Third weighing: A + B on the left-hand pan, C + D on the right-hand pan. 
Response y3 = -1Og. 
Fourth weighing: A + D on the left-hand pan, B + C on the right-hand pan. 
Response y4 = Og. 
The resulting set of equations is: 
y , = + ma + mb +m, + md 
y2 = + m a - mb + m, - md 
y , = + m a + mb - m, - md 
y 4 = + m a - m h - m , + m d 
The mass ofeach object can be calculated using the following formulae: 
ma = - [ + Y I + Y ~ 1 + ~ 3 + ~ 4 1 
mb = - [+YI - ~ 2 + ~ 3 - Y ~ I 
mc = - [ + Y I + ~ 2 - Y ~ - Y ~ I 
4 
1 
4 
1 
4 
1 
4 
md = -[+Y, -Y2 -Y3 + Y 4 1 
The variance of ma is given by: 
The error of ma is the square root of the variance: 
76 
1 1 
2 2 
urn, = -0 = - 0.1=0.05 gram 
We have reduced the error by half without increasing the number of weighmgs. The 
precision cannot be further improved, which can be seen intuitively as all the objects were used in 
each test. This extremely important property is related to the X effects matrix, which in this case 
is: 
+ I +I +I +1 
+ 1 -1 +I -1 
+ I +I -1 - 1 
+ I -1 -1 +1 
X = 
This is exactly the same matrix as that for a 22 design, and therefore satisfies the 
relationship: 
X'X = nI 
showing that the best precision for effects is obtained and cannot be improved. 
We can therefore reduce the error to 0.05 g for the weighing of four objects if the precision 
of each weighing is * 0.1 g. 
In general, if the error of the response is cs and n tests have been performed using X matrices 
such as XtX = nI, the error of the effect of a factor is OIL and it can be shown that the greatest 
precision is obtained in this case. 
3. OPTIMALITY CRITERIA 
An experimental design is said to be optimal if it allows the most precise calculation of 
effects. It can be demonstrated that this precision is directly correlated with the X'X matrix. 
Optimality criteria therefore involve this matrix and, depending on the experimental 
conditions, one of them must be chosen by the investigator. The criteria, in order of their quality 
are: 
3.1. Unit matrix criterion 
The X matrix must respect the relationship 
X'X = nI 
where n is the number of experiments. X matrices which fulfil this criterion are called Hadamard 
matrices, after the French mathematician who studied them. This is the best criterion. It can be 
77 
demonstrated that the most precise possible values for the effects (or interactions) are then 
obtained. We have seen how this criterion was applied to the weighings problem, but it remains 
true when there are interactions. 
Unfortunately these matrices are not available for all values of n, only for 
n = 2 
n = 4 
n = 8 
n = 12 
n = 4 x d (where d is a positive whole number). 
When the number of trials is not a multiple of 4, the optimality criterion, X'X = nI, cannot be 
satisfied. The problem then is to find, despite this restriction, a designthat provides the best 
possible precision. Other criteria of optimality must be employed. 
3.2. Maximum determinant criterion 
The value of the determinant of X'X must be as great as possible. Thus a design is required 
in which 
Det( X'X ) is as large as possible. 
We know that a determinant is a number and that, although it is in the form of an array, it 
must not be confused with a matrix. In this book, determinants are shown by Det( ). 
The elements of a square matrix may be considered as elements of a determinant. The X'X 
matrix is a square matrix; it is therefore quite possible to calculate the value of the corresponding 
determinant. If we use the example of the weighmg design for 4 objects, we can calculate the 
determinants for the three strategies. 
a. Standard strategy 
The X matrix is 
1 0 0 0 
0 1 0 0 
0 0 1 0 
0 0 0 1 
X = 
The determinant of X'X is unity 
Det( X'X ) = 1 
78 
' x = 
b. Intermediate strategy 
The X matrix is 
+1 -1 0 0 
+I +1 0 0 
0 0 +1 - 1 
+ 1 +1 0 0 
-1 +1 0 0 
0 0 +1 + I 
X = 
1 0 0 -1 +1 
+1 -1 0 0 
+I + I 0 0 
0 0 +1 - 1 
0 0 +1 + 1 
X'X = 
The X' matrix is 
+1 +1 0 0 
- I +1 0 0 
0 0 + 1 +1 
0 0 -1 +I 
I 0 0 +1 +1 / 
hence: 
12 0 0 01 
0 2 0 0 
x ' x = l 0 0 2 0 
10 0 0 21 
The value of the determinant for this matrix is: 
Det( X'X ) = 2' = 16 
Indicating that this strategy is already better than the standard one 
c. Optimal strategy 
All the objects are involved in each weighing, and the X matrix is 
+ I + I +1 +1 
+ I -I +1 -1 
+1 +1 -1 - 1 
+ I -1 - 1 + 1 
X = 
79 
t l +1 +I +1 
t l -1 +I -1 
t l + 1 - 1 - 1 
t l - 1 -1 + I 
The X' matrix is 
+ 1 +1 + 1 + 1 
+I -1 + I -1 
+1 +I -1 -1 
+ I -1 -1 +1 
hence: 
x'x = 
t x = 
+1 +1 + I +1 
+ I - 1 +1 -1 
+1 + I -1 -1 
+1 -1 -1 +1 
4 0 0 0 
0 4 0 0 
0 0 4 0 
0 0 0 4 
X'X = 
The matrix X is a Hadamard matrix, giving the best precision for the effects. The 
corresponding determinant of X'X is: 
Det( X'X) = 44 = 256 
This is the highest value that the determinant can have, hence the strategy is the best. 
3.3. Minimum trace criterion 
The trace of the matrix ( X'X) 
The trace of a matrix is the sum of the elements along the main diagonal. For example, the 
must be as small as possible. 
trace of the following matrix: 
0.25 -0.02 -0.03 -0.02 
-0.02 0.35 -0.03 0.01 
-0.03 -0.03 0.47 -0.15 
-0.02 0.01 -0.15 0.72 
(X 'X) - I = 
trace of ( X k - ' = tr ( X'X) - I = 0.25 + 0.35 + 0.47 + 0.72 = 1.79 
80 
This criterion can be applied to the three weighing strategies. Clearly, the same classification 
(for 4 objects) is obtained: 
standard strategy: 
intermediate strategy: 
optimal strategy: 
trace of ( X'X) - 1 = 4 
trace o f ( X'X) - l = 2 
trace o f ( x'x)-* = I 
3.4. "The largest must be as small as possible" criterion 
diagonal of ( X'X) 
following with one arrangement of experimental points: 
This rather cryptic statement indicates that the value of the largest element in the main 
matrix may be the must be as small as possible. For example, a ( X'X) 
0.25 -0.02 -0.03 -0.02 
-0.02 0.35 -0.03 0.01 
-0.03 -0.03 0.47 -0.15 
-0.02 0.01 -0.15 0.72 
(Xt X) -'= 
The value of the largest element on the principal diagonal is 0.72. The investigator's problem 
is to choose another arrangement of experimental points to obtain a value of less than 0.72, and as 
small as possible. We will not continue with this problem as it requires a considerable theoretical 
treatment and long computer calculation (see Chapter 16). 
The above criteria are not mutually incompatible. For example, if a matrix satisfies the first 
criterion, XtX = nI, then it satisfies the other three. 
Two-level factorial designs all satisfy the optimality criterion, XtX = nI. We are therefore 
sure of always obtaining the best precision for effects when they are used. 
4. POSITIONING EXPERIMENTAL POINTS 
The positioning of the experimental points in the experimental domain is a major question. 
There appear to be two contradictory requirements: the fewest possible tests, and the best possible 
precision. In other words, we must look for the best compromise, or as we saw in the weighmg 
experiment, the best strategy. 
The solution to this problem can be very complex, sometimes requiring extensive 
calculation, and a great deal has been published on it [ 181. A general treatment is outside the scope 
81 
of this book. We shall restrict ourselves to two level factorial designs, first examining a single 
factor, then two, and finally the general case for k factors. 
4.1. Positioning experimental points for one factor 
If a response y depends only on a single factor x, how can the experimental points be chosen 
so as to give an optimal experimental design? 
The variable x can have any value between -1 and + l . If we carry out two trials, the 
experimental points A and B could be at two specific locations on the abscissa, a and f3, (Figure 
5.4). The experimental domain is then reduced to the straight segment of the axis Ox and limited by 
the points -1 and + 1 . Experimental points A and B are between -1 and +l. 
Our problem is to find the values for x such that points A and B produce an optimal design, 
i.e., they satis@ the optimality criterion. 
I 
Q 
b 
-1 A B +1 
Figure 5.4: Are the experimental points A and B optimally positioned? 
Assuming that the response y is the following function of x: 
y = + al x 
The two experiments give the following system of equations: 
y 1 = % + a l a 
Y2 = a0 + a1 P 
OK 
82 
+I a a(] 
I N = I + 1 PI Ia,i 
The response surface is a straight line, and we need to know how can we position A and B 
in the experimental domain to obtain and a, with the best precision. Intuitively, we can see that 
the response line PQ (Figure 5.4) is best defined when the points P and Q are as far apart as 
possible. The optimality criterion can be used to show this: 
X ~ X = nI 
The X matrix is represented by: 
The X ' matrix is then 
+1 +1 
=la iil 
We must now find the values of CL and which allow the XLX matrix to satisfy the unit 
matrix optimality criterion, X'X = nI: 
First calculate X'X 
or 
and calculate nl: 
To satisfy the optimality criterion we must have 
83 
This matrix relationship is analogous to a system of two equations with two unknowns (the 
corresponding elements must be equal): 
a2 + p2 = 2 
which has two solutions: 
a = + 1 a=-1 1 ( 3 = - 1 and 1 p = + 1 
These indicate that the points must be located at each extremity of the experimental domain. 
The same applies to two level factorial designs in which the response depends on several 
factors: the experimental points must be selected so as to be at the limit of the field for each factor. 
Let us now apply these concepts to a specific problem, measuring electrical resistance. This 
example illustrates a general principle, and it is fairly easy to adapt it to suit any situation in which 
the response is a first degree function of the factor studied. 
5. MEASUREMENT OF AN ELECTRICAL RESISTANCE 
Example: Measuring an electrical resistance 
The Problem: 
A technician has just enough time and finances to allow him to carry 
out ten tests in order to measure an electrical resistance as accurately as 
# possible. The current varies from 10 A (level -1) to 20 A (level +I). Voltage 
fk is measured at each level of current Where should he place the 
@ experimental points to obtain the most precise measure of the resistance7 
Ohm’s Law states that voltage (the response) is a linear hnction of current. Thus it is not 
necessary to make measurements equally spaced throughout the domain, as in Figure 5.5 to check 
the shape of the response. We have seen that we can obtain the best precision for resistance if the 
experimental points are at the limits of the field. We therefore make five measures at level + 1 and 
five at -1, as shown in Figure 5.6. 
84 
10 15 20 Amps 
Figure5.5: Poor method of measuring resistance. 
Volts 
10 15 20 Amps 
Figure 5.6: Good method of measuring resistance. 
85 
6. POSITIONING EXPERIMENTAL POINTS FOR TWO FACTORS 
The preceding calculation was for a single factor. When two factors are involved, the 
positions of the experimental points must be chosen with great care. 
Let us first assume that the experimental points for factor 1 are placed at the extremities of 
the field at -1 and +1 on the x1 axis and that those for factor 2 are also at the ends of the field on 
the x2 axis (Figure 5.7). This disposition immediately provides the effects ofxl and x2. It also has 
the advantage of basing the calculation of effects on the experimental points. 
However, it does not allow calculation of the interaction. We are therefore faced with 
problem of finding the optimal disposition of the experimental points. We can use the optimality 
criterion of the maximal determinant. The best precision is obtained when the determinant is equal 
to 44 = 256. 
D t +I x1 
Figure 5.7: Poor distribution of experimental points within the experimental field. 
86 
Point A 
Point B 
Point C 
Point D 
The X matrix is deduced from the effects matrix (Table 5.3): 
+1 -1 0 0 
+I +I 0 0 
+ 1 0 -1 0 
+1 0 +1 0 
TABLE 5.3 
EFFECT MATRIX 
+1 +1 + 1 +1 
-1 + 1 0 0 
0 0 -1 +1 
x'x = 
+ 1 -1 0 0 
+ I +1 0 0 
+1 0 -1 0 
0 0 0 0 + 1 0 + 1 0 
hence: 
Calculating X'X 
+1 -1 0 0 
+1 +1 0 0 
+ I 0 -1 0 
+1 0 + 1 0 
x = 
0 2 0 0 1 x'x = 
0 0 0 0 0 0 2 0 1 
Det( XLX ) = 0 
87 
The value of the determinant of X'X is zero, indicating that the best precision has not been 
attained. But the four points are at the extremities of the domain of each factor. What went 
wrong? 
Only x, was involved in trial A, x2 was not used. Similarly for points B, C and D. Thus 
placing the points at the extremities of the domain of each factor is not sufficient, all the variables 
must contribute, and must therefore be involved in all the trials. If we adopt a configuration in 
which the points A, B, C and D are at the corners of the domain, they are all involved in each trial, 
and we get the system shown in Figure 5.8, to which we can apply the same optimality criterion. 
Figure 5.8: Good positions for experimental points in the experimental domain. 
88 
Trial no I XI x2 
Point A +1 -1 -1 
Point B +I +1 -1 
Point C +I -1 + I 
Point D +1 +1 +1 
The X matrix is deduced from the effect matrix (Table 5.4) 
"1x2 
+1 
-1 
-1 
+ 1 
TABLE 5.4 
EFFECT MATRIX 
+I +1 +1 +I 
-1 +1 -1 +1 
-1 -1 +1 +1 
+1 -1 - 1 +1 
x'x = 
+I -1 -1 + I 
+1 +1 -1 -1 
+ 1 -1 +1 -1 
+1 +1 + 1 +I 
And the mathematical matrix X is: 
I+l -1 -1 + 1 ( 
/ + I +I + I 1 1 1 
Calculating X'X 
xtx=l 0 4 0 0 I 
0 0 4 0 
Det( X'X ) = 256 
The determinant of X'X is 256, the largest value possible. Thus, this configuration gives the 
maximum precision, and the disposition of points is the best. This is the disposition used for two 
level factorial designs. 
89 
7. POSITIONING THE EXPERIMENTAL POINTS FOR K FACTORS 
If we use the same reasoning for all two-level factorial designs, it can be demonstrated that 
the experimental points must be at the comers of the domain and that they must all be involved in 
each trial. 
The experimental points for three factors must be at the eight corners of a cube. Those for 
four factors are placed at the sixteen corners of a hyper cube in a 4-dimensional space. Finally, for 
k factors the experimental points must lie at the Zk comers of a hyper cube in a k-dimensional 
space. 
The designs that we examined in Chapters 2 and 3 are optimal designs. Using them, the 
experimenter can be sure of having the best research strategy. 
90 
RECAPITULATION 
1 We used the weighing design example to show the importance of including all 
factors in each trial. 
2 We also discussed criteria of optimality of experimental designs. Four criteria were 
mentioned, and the most frequent two of them were applied to the weighing design 
and resistance measurement examples. A research strategy can be evaluated, and 
there is an optimum strategy. 
3 There is a best strategy: the optimal strategy. The positioning of experimental points 
within the experimental domain is of great importance to obtain the best precision 
on the effects and interactions. When only two trials are performed per factor, the 
experimental points must lie at the limits of the domain in such a fashion that all 
factors are involved in all trials. This is the case for the factorial designs covered in 
this book. The investigator who uses such designs can be sure of having the best 
possible strategy. 
CHAPTER 6 
T W O - L E V E L F R A C T I O N A L 
F A C T O R I A L D E S I G N S : 2k-p 
- T H E A L I A S T H E O R Y - 
I . INTRODUCTION 
In this chapter our goal is to show how it is possible to reduce the number of trials run 
without reducing the number of factors. The trials themselves must be chosen carefilly, and the 
results interpreted with great care to ensure that the conclusions are valid. We shall begin by 
examining designs which involve half the number of trials of a complete design. We will 
introduce the TheoIy of Aliases and the Box notation with the help of an example. Then, we 
will continue to reduce the number of trials with more and more fractionated designs. The rules 
deduced from the first example will be extended to all fractional factorial designs. 
The reader should study this chapter with particular care, as fractional designs are 
extremely powerful tools for conducting fast, precise experiments. 
92 
~~ 
Level (-) 
Level (+) 
2. FIRST FRACTIONAL DESIGN: z3-I 
low conc dilute A 
high conc concentrated B 
2.1 Example: Bitumen emulsion stability(continued from Chapter 3) 
Let us go back to the problem that we solved in Chapter 3 using a 23 design: the stability 
of a bitumen emulsion. The experimenter camed out eight trials. Could he, for example, have 
camed out only half that number? Let us assume that he ran only four trials, and that these 
were trials 5, 2, 3, and 8. The corresponding design matrix is shown in Table 6.1; in it, the 
responses are those given in Chapter 3, as this is the same experiment. 
We can apply the same rules for calculating the effects, but we shall label them differently 
because fewer responses are used in the calculation. We will record the effect of factor i as hi 
and indicate the mean of the responses as hM 
TABLE 6.1 
EXPERIMENTAL MATRIX 
STABILITY OF A BITUMEN EMULSION (CONTINUED) 
Trial no IT 
I 
Factor 1 Factor 2 
(fatty acid) I (HCO 
Factor 3 
(bitumen) 
+ 
- 
- 
+ 
Response 
93 
Mean 
1 
2 
3 
The effects calculated from this fractional design can be compared to those obtained with 
the complete design (Table 6.2). 
Complete Fractional 
Design. Design. 
27.25 27.25 
-1 .oo -0.75 
-6.00 -6.25 
-4.00 -4.25 
TABLE 6.2 
RESULTS COMPARISON 
STABILITY OF A BITUMEN EMULSION (CONTINUED) 
Evidently, the results obtained from the fractional design and those of the complete 
design with eight trials are very similar. Somewhat surprisingly, we have obtained the same 
result with less effort. But nothing is free in this world, so what is the price we must pay for 
carrying out four fewer trials? In order to answer that question, we must look more closely at 
the values of effect 3 and interaction 12 obtained with the complete design. 
Adding them together, we get: 
This is equivalent to h,, hence: 
Thus, h is equal to the main effect E, plus the interaction E,,. The effect E, and the 
interaction El, are said to be aliased, and the quantity h , can be called the alias, or contrast 
or simply the effect. In this book, we will use the term contrast, but the reader should be 
aware that these other terms are often used. 
It can be similarly shown that: 
h = E, + E,, 
94 
h , = E, + El, 
A,= I + E,,, 
The contrast h indicates that the main effectE, is aliased with interaction 23. Contrast 
h indicates that the main effect E, is aliased with interaction 13, and lastly contrast h , is 
aliased with the mean I and the interaction 123. Thus, all the main effects are aliased with 
interactions. 
So this is the price that must be paid. The number of trials was reduced to half, but the 
effects calculated from them are no longer pure, but mixed, or aliased, with the interactions. 
We obtained very similar results with eight and four trials in the bitumen emulsion example 
because interaction 12 was negligible. 
Thus 
h 3 Z E , 
It is therefore possible to obtain results with four, rather than eight trials, so long as we 
remain aware that the main effects are aliased with interactions. Hence, the result will be 
satisfactory only as long as the interaction is negligible compared to main effect. 
Clearly, the interpretation of fractional designs is more complex than that of complete 
designs. The following section describes the method presently used for interpretation. The 
method is convenient and generally reliable, but the reader should remember that it is always 
possible that there may be exceptions. 
3. INTERPRETATION OF FRACTIONAL DESIGNS 
The interpretation of all fractional designs present similar problems. The working 
hypotheses generally used are the following: 
Third or higher order interactions are considered to be negligible 
A zero contrast could indicate: 
a. that the aliased effects are all zero. 
This is the most likely situation. We will frequently use this hypothesis to 
analyse the results of factorial designs. 
This is unlikely, and we will not perused it in this book. 
b. that the aliased effects and interactions cancel each other. 
The interaction of two small effects is also small 
The interaction of a small effect and a large effect is generally small 
There is a strong possibility that the interaction of two large effects is also large. 
We will make extensive use of this hypothesis to analyse fractional 
designs. 
95 
These hypotheses are useful when interpreting the results of a fractional design. But, 
while they are often right, they are sometimes wrong. They are just helpful in a first practical 
approach and a more carefbl examination is sometimes necessary to extract the right 
information from the results of the experiment. 
Clearly, before we can interpret the results of a fractional design we must know how the 
effects and interactions are aliased. We will now examine this important topic in more detail. 
4. CALCULATION OF CONTRASTS 
The selection of trials no 5, 2, 3 and 8 may have seemed strange, but there was a good 
reason for doing so. Table 6.3 shows the effects matrix of a Z3 design in which the sequence of 
trials was chosen to display two 22 designs for factors 1 and 2. The z3 design can thus be 
divided into two half-designs. 
TABLE 6.3 
EFFECTS MATRIX 
STABILITY OF A BITUMEN EMULSION (CONTINUED). 
+ 
6 + 
7 + 
4 + 
Initially, we shall consider only the upper half-design (trials 5 , 2, 3 and 8), the one used 
to study bitumen emulsion stability. In this half-design the column of factor 3 signs is the same 
as the column of signs for interaction 12. This equality of the signs columns can be represented 
using the notation of Box by writing that 3 and 12 are equal as they have the same sequence of 
signs. Hence: 
3 = 12 
Thus, in this half-design, a contrast is the sum of elfect and interaction having the same 
and- sips. We can therefore see that the notation of Box and the contrast sequence of 
value are equivalent. It is thus possible to go from one to the other. 
96 
We will frequently use this correspondence between the two relationships when 
interpreting and constructing fractional designs. We can use the Box notation to deduce how 
effects are aliased. We can deduce the Box notation from the relationship of the aliases, and 
hence construct appropriate designs to solve specific problems. 
and 
3 = 12 is equivalent to h , = E, + El, 
h = E, + E,, is equivalent to 3 = 12 
or 
3 = 12 e h,= E,+ El, 
The eight columns of signs in the first half-design lead to the following relationships: 
1 = 23 
2 = 13 
3=12 
I = 123 
From which the contrasts are deduced: 
h , = El + E,, 
A,= E,+ El, 
1, = E2 + El, 
a,= I + E,,, 
Thus the Box notation can be readily used to find the effects and interactions aliased in a 
contrast. This method will be used throughout this book. 
Returning once again to the bitumen emulsion stability example, we could have used the 
other, lower, half-design. Examination of the effects matrix (Table 6.2) reveals that the column 
of signs for factor 3 (- + + -) is the same as that for interaction 12 multiplied by -1. Thus, 
using the Box notation, we have 
3 = -12 
We can now calculate contrast h', from the column of signs for factor 3 in the lower 
half-design (trials 1, 6, 7, 4) to obtain: 
A, = 
1 
4 
-[-Y, - 
We now need to know how the factor 3 effect and interaction 12 are aliased in this 
contrast. We can take the formula for the effect of factor 3 and interaction 12 used in the 
complete design: 
97 
Subtracting El, from E, , we get: 
Thus 
1, = E,- El, 
Hence, in this half-design, a contrast is the difference between the effects and interactions 
having the opposite sequence of signs. Again, there is an equivalence relationship: 
and 
. or 
3 =- 12 is equivalent to h3 = E, - El, 
i3 = E, - E,, is equivalent to 3 = - 12 
3 = - 1 2 1 3 = E,- El, 
The eight columns of signs in the lower half-design lead to the four relationships: 
1 = - 2 3 
2 = - 13 
3 = - 12 
I = - 123 
Which give the following formulae for the contrasts: 
hi = El - E,, 
i2 = E,- El, 
h3 E,- El, 
iM = I - El,, 
Here, again, the Box notation is used to find the effects and interactions aliased in each 
contrast. 
98 
5. ALGEBRA OF COLUMNS OF SIGNS 
We can now manipulate the columns and signs in order to find all the columns of signs in 
a fractional design that are identical or opposite. We can then apply the equivalence 
relationship to obtain the aliased effects and interactions in a contrast. There are two rules 
governing the algebra of column signs. These calculations are valid for all fractional designs. 
Rule one: 
A column of signs multiplied by a column of + signs does not change, e.g.; 
~ - + 
~ + multiply by + - + 
- - + 
+ + + 
Or, using the Box notation 
1.I= 1 
and we also have 
2.1 = 2 
3.1 = 3 
Rule two: 
A column of signs multiplied by itself gives a column of + signs, e.g.: 
~ - + 
+ multiply by + ~ + - 
+ 
f + + 
- - 
Written in Box notation, this is: 
l . l = I 
or 
2 . 2 - 1 
3.3=1 
We will use these two rules throughout this book 
99 
Alias generators 
All the formulae for the upper half-design can be obtained from: 
I = 123 
This is called an alias generator because its enables us to find all the equal and opposite 
columns in a 2” design. If the two sides of the alias generator are multiplied by 1 we obtain: 
1. I = 1.123 
applying rule one to the left hand side, we get: 
1 . I = I 
applying rule two to the right hand side, we get: 
hence: 
1.123 = 1.23 
1 = 1.23 
Lastly, by again applying rule one, we get: 
1 = 23 
Similarly, starting from the alias generator, we get: 
2 = 13 and 3 = 12 
By applying the equivalence relationship we can obtain contrast: 
1 = 23 gives A 1 = El + EZ, 
2 = 1 3 gives A,= E,+ E,, 
3 = 12 gives A,= E,+ El, 
I = 123 gives A,= I + E,z3 
The two alias generators, I = 123 and I = - 123, show that the signs column of 
interaction 123 is divided into two parts the first contains all the + signs, and the second all the 
- signs The complete 23 design is divided into two half designs The upper one contains all the 
+ signs of interaction 123, while the lower one contains all the - signs of this interaction 
The reader will now understand why trials 5 , 2, 3 and 8 were chosen for the fractional 
design, they are the trials for whichthe 123 interaction signs were + 
The generator for the lower half-design is 
100 
I 1 - 123 
From it, by applying rules one and two, we can obtain the three relationships: 
1 = -23 
2 = -13 
3 = -12 
From these, we deduce how the effects and interactions are aliased in the lower half- 
design. 
hi = El - E,, 
h, = E,- E,, 
h, = E,- El, 
h, = I - E,,, 
We could just as well have chosen trials 1, 6, 7, and 4 (the half-design generated by 
minus signs of interaction 123). We could have used the contrasts to calculate the effects. In 
our example we would have found the same values because the interactions were negligible. 
But is there any danger in aliasing? There is absolutely no danger, provided that we do 
not depart from the spirit of the interpretation hypothesis. If we have begun our study by 
carrying out half of the 23 design, but were then not sure about the results, we could always go 
on to do the second half to obtain all the information. All that we have done is taken a risk in 
order to obtain the results twice as fast. This is the best type of gamble: one which you cannot 
lose, and can often win. The main point is to evaluate the risk. We will see how to cope with 
this difficulty in the following example. 
We can therefore see that experimental designs are tools which are perfectly suited to the 
progressive acquisition of knowledge. 
An experimenter may be initially reluctant to employ fractional designs for fear of 
missing important information or results. He or she may believe that there is a risk and that it 
would be better to use a complete design. This makes little difference while only a few trials 
are involved. But when there is a large number of trial, the experimental cost becomes 
prohibitive and the risk of a mistake during the experiment increases considerably. It is 
therefore better to get into the habit of carrying out fractional designs and learning to analyse 
the results carefully. The following pages will show the reader that this is the safest and fastest 
approach. 
6. CONSTRUCTION OF FRACTIONAL DESIGNS (ONE EXTRA 
FACTOR) 
If we consider Table 6.4 (which is the same as Table 6.3) and examine the columns for 
factors 1, 2 and 3 in the upper half-design, we see that these are exactly the same as the table 
101 
the 22 design to study factor 3 . 
TABLE 6.4 
We will use this similarity to explain how we can quickly construct fractional designs: 
1 We start by selecting an experimental design and drawing up an effects matrix. This effects 
matrix, called the basic design, is the foundation on which we build the fractional design. 
Thus, for a 22 design we get: 
2 We then select the highest order interaction, as this is most likely to be small. The only 
interaction in a Z2 design is 12, but if we were working with a z3 basic design we would 
choose 123 rather than 12, 13 or 23. 
3 We use the signs of this interaction to study the extra factor by attributing the - sign to the 
low level and the + sign to the high level. 
We can illustrate the construction of fractional designs by using a 24 basic design matrix 
(Table 6.5), in which there are six second order interactions, four third order interactions and 
one fourth order interaction. The complete design can be used to study four factors in columns 
1,2, 3 and 4. If we want to study a fifth factor, we keep the four columns of signs for the four 
initial factors and select an interaction column for the fifth factor. For example, we shall use the 
1234 interaction column and say that by the signs of this interaction are attributed to the level 
of the extra factor 5. 
5 = 1234 
102 
Trial no 
I 
2 
3 
4 
5 
6 
7 
8 
9 
10 
1 1 
12 
13 
14 
15 
16 
TABLE 6.5 
z4 BASIC DESIGN MATRIX 
I 1 2 3 4 12 13 14 23 24 34 123 124 134 234 1234 
+ - - - - t t + + + + - - - - t 
+ + - - . . - - - + t + + + t - 
+ - + - - - t + - - + + + - + -~ 
+ + + - - + - - - - + - - + + + 
+ - - t - + - + - + - t - + + - 
+ + - . f - - - + - _. t - - t - -t + 
+ - + + - - - + + - - - + t - + 
+ + + + - + + - + - - + - - - 
+ - - - + + + - + - - - + + + - 
+ + - - + - - + + - - + - - + t 
t - + - + - + - - + - + - t - t 
+ + + - t + - t - t - - + - - 
t ~~ ~ + + + - - ~ - - - t + i t 
+ + - + + - + t - - + - - + - 
+ - + + + - - - + + + - - - + - 
+ + + + + + t + t t + t t t + + 
- 
- 
- 
The experiment is carried out by attributing the high level to factor 5 each time there is a 
+ sign in the 1234 column and the low level each time there is a - sign in this column. At the 
end of the study column 1234 will be used to calculate a contrast by applying the usual rules. 
We apply the equivalence relationship in order to find out what this contrast contains. 
S = 12340 h , = E,+ E,,,, 
Contrast h is the sum of the effect of factor 5 and of the interaction 1234. 
If we again take the expression 5 = 1234, and multiply both sides by 5 to extract the alias 
generator, we get: 
5.5 = 12345 
1 = 12345 
We can then multiply this generator by 1, 2, 3, 4 and 5 to obtain the contrasts h ,, h 2, 
h,, h4and h,. 
103 
We can also analyse the expression 5 = 1234 in order to try and understand what it 
represents in the complete 25 design. As in the z3 design we studied previously, this 
relationship divides the complete 2’ design into two parts. The first half-design contains the + 
signs of the 12345 interaction and the second half-design contains the - signs of this 
interaction. The complete 25 design has thus been divided into two half-designs, one defined by 
I = 12345 and the other by I = -12345. 
If we examine the effects matrix of the half-design defined by I = 12345, we can see that 
it contains thirty two columns of 16 signs and that these columns form identical pairs. As in the 
23 example, the effects and interactions having the same signs are aliased. 
TABLE 6.6 
12345 I 
+ + 
32 columns = + + 
identical 2 by 2 
16 rows 16 columns 
+ + 
+ + 
1 
32 columns = 
16 columns 
opposing 2 by 2 d 16 rows 
+ 
+ ~ 
I = 12345 
1 = - 12345 
Similarly, when we examine the effects matrix for the half-design defined by 1 = -12345, 
we see that it too contains 32 columns of 16 signs and that these columns form opposite pairs. 
As for the z3 design, the effects and interactions having sequences of opposing signs are 
104 
aliased. The alias generator of this half-design, I = -12345, gives, from the equivalence 
relationship, the contrasts 
In practice, there is no need to write out a complete design and select the + or - signs of 
an interaction in order to obtain the trials of the ftactional design. We use the basic design 
(effects matrix of a complete design) and select an interaction column in order to study the 
extra factor. But in order to understand the reasoning behind this, we must bear in mind the 
implications of this approach. This will be most useful when we come to examine designs with 
several extra factors. 
7. NOTATION OF FRACTIONAL DESIGNS 
Fractional designs are indicated by a notation which shows how the design is subdivided. 
Thus, for a 25 that has been divided into two equal halves, each half is designated as !h 25, or 
25. 2-', or 25-'. Each of the digits in this last expression has a meaning. The 2 indicates that 
the factors have two levels; the 5 indicates the number of factors studied; while the 1 indicates 
that there is one extra factor more than in the basic design. 
If six factors were studied using a 24 basic design, the fractional design would be written 
26-2. 
This notation system for fractional designs provides at least three pieces of information - 
the number of factor levels, the total number of factors studied and the number of extra factors. 
It also provides information on the number of trials. Thus, 24 = 25-1 = 26-2 = 16, which is the 
number of trials to be performed. We can therefore say that a 2k-P design contains 2k-p trials. 
8. CONSTRUCTION OF FRACTIONAL DESIGNS (TWO EXTRA 
FACTORS) 
Imaginethat we have 6 factors to study. We could use a 26 complete design, but that 
would require 64 trials, which is generally far to many. We could also use a 26-' design, which 
would only require 32 trials, but even this is too many. If we want to carry out just 16 trials, 
we must use a 26-2 design. The corresponding basic design is the effects matrix of a Z4 
complete design (Table 6.5). We can study four factors in columns 1 , 2, 3 and 4, and select an 
105 
interaction column for each of the extra factors by using the signs + and - for the high and low 
levels. We can illustrate this approach assuming that we have chosen interaction 123 for factor 
5 and interaction 124 for factor 6. We would then write, using the Box notation: 
5=123 and 6=124 
If we multiply the first relation by 5 and the second by 6, we get two alias generators 
I=1235 and I=1246 
These two generators are called the independent generators because they were 
obtained independently. Multiplying these two generators together, we get 
1.1 = 1235.1246 
And this expression can be simplified using the two rules described earlier: 
I = 1.1.2.2.3.4.5.6 
I = 1.1.3.4.5.6 
I = 3456 
We thus have a new alias generator, called the dependent alias generator. Combining all 
these generators, we have: 
I = 1235 = 1246 = 3456 
There are four alias generators. This set of generators is called the Alias Generator Set 
(AGS). This AGS tells us the contents of the contrasts. Each column of the 26-2 fractional 
design allows us to calculate the contrasts containing the effects and interactions of the 
complete design. If we multiply each generator in the AGS by 1, we get: 
1.1 = 1.1235 = 1.1246 = 1.3456 
or 
1 = 235 = 246 = 13456 
We can now apply the equivalence relationship to obtain the contrast k 
Instead of writing the effects and interactions with the letter E, we can use just the digits, 
so that the above relationship becomes: 
h 1 + 235 +246 + 13456 
106 
When we multiply the AGS by 2, 3, 4, 5 and 6 we get the contrasts h 2, h 3, h 4, h and 
6 . 
h 2 = 2 + 135+146+23456 
h = 3 + 125 + 12346 + 456 
h , = 4 + 12345 + 126 + 356 
h 5 = 5 + 1 2 3 + 1 2 4 5 6 + 3 4 6 
h , = 6 + 12356 + 124 +345 
We can see that each contrast contains four terms, or 22 terms, or 2 to the power of the 
Let us look at the shorthand designations 
number of extra factors. 
5 = 123 and 6 = 124 
to see exactly what is behind them. Consider a complete 26 design. Here, the first generator, I 
= 1235, groups together all the + signs of the interaction 1235 and define a 26-' fractional 
design The - signs of this interaction define a second 2"' design (second generator I = - 
1235). The 26 design has therefore been divided into two half-designs defined by the two alias 
generators, I = 1235 and I = -1235). 
Let us focus on the I = 1235 half-design and use the second alias generator, I = 1246. 
The + and - signs of the 1246 interaction divide this half-design into two new parts (Table 
6.7), or two quarter-designs with respect to the original complete 26 design. The first quarter- 
design is defined by the two independent alias generators 
1 = +I235 and I = +1246 
The second quarter-design is defined by the two independent alias generators 
I = +1235 and 1 = -1246. 
The half-design I = -1235 is divided into two quarter-designs by the + and - signs of 
1246. The first of these two 26-2 designs are defined by: 
I = -1235 and I = +1246, 
and the second of these two 26-2 designs are defined by: 
I = -1235 and I = -1246 
The complete 26 design contains 64 columns of 64 signs. The quarter-designs each 
contain 64 columns and each column contain 16 signs. These columns can be rearranged in 
groups offour which are either identical or opposite. In the quarter-design defined by the 
AGS. 
I = 1235=1246=3456 
107 
TABLE 6.7 
1235 1246 I 
+ + + 
64 columns + + + 
identical 4 by 4 16 rows 
+ + + 
+ + + 
16 rows 
16 rows 
f 16 rows 
64 columns 
opposing 4 by 4 
+ - + 
+ - + 
+ 
+ - + 
+ - 
- + + 
64 columns - + + 
opposing 4 by 4 
+ + 
+ + 
- - + 
- 
- 
64 columns - - + 
identical 4 by 4 
I = + 1235 
I = + 1246 
I = + 1235 
I = - 1246 
I = - 1235 
I = + 1246 
I = - 1235 
I = - 1246 
108 
The columns for the average and interactions 1235, 1246 and 3456 all contain 16 plus 
(+) signs. We can find all the columns having the same signs by multiplication of the AGS. For 
example, if we multiply the AGS by 3 we get 
3 = 125 = 12346 = 456 
and we can deduce that columns 3, 125, 12346 and 456 have the same sequence of signs in this 
quarter-design. 
In the quarter-design defined by the AGS 
I = 1235 = -1246 = -3456 
The average I and 1235 interaction columns contain 16 + signs, while the 1246 and 3456 
interaction columns contain 16 minus (-) signs. We can find all the columns having identical or 
opposite signs by multiplying the AGS of this quarter-design. For example, if we multiply the 
AGS by 3, we get: 
3 = 125 = -12346 -456 
and we can affirm that columns 3 and 125 are identical, that columns 12346 and 456 are 
identical, while columns 12346 and 456 have a sequence of signs opposite to those of 3 and 
125 in this quarter-design. 
It is practically impossible to write out the 26 design and look for the fractional design 
trials by using the interaction signs, It is much easier to use a basic design and the alias theory 
(Box notation and equivalence relationship) to find the trials of a fractional design. This is why 
we have emphasised the alias theory. 
9. CONSTRUCTION OF FRACTIONAL DESIGNS 
(p EXTRA FACTORS) 
The concepts we have used to study one or two extra factors can be extended to p 
factors. A fractional design is constructed as follows: 
1. The experimenter chooses a 2" basic design by writing the effects matrix for a complete 2" 
design. If the total number of factors to be studied is k, and the number of extra factor is p, 
we can write: 
n = k - p 
For example, nine factors (k = 9) can be studied with a 24 basic design (n = 4), and there 
are five extra factors (p = 5), we still have: 
4 = 9-5 
109 
2. The experimenter selects p, generally high order, interactions. He writes that the extra 
factors are aliased with the selected interactions. This allows him, using Box notation, to 
write the independent alias generators. If we take a 26-3 fractional design, we can write that 
the initial three factors will be studied in columns 1, 2 and 3 and that factors 4, 5 and 6 will 
be studied in columns 12, 13 and 23. For these last three columns: 
4 = 1 2 
5 = 13 
6 = 23 
Applying the calculation rules given earlier we can establish the following independent 
alias generators: 
I = 124 
I = 135 
I = 236 
It is only possible to interpret the results of a fractional design if we know how the 
effects and interactions are aliased in each contrast. Thus the experimenter must establish the 
AGS and apply the equivalence relation. 
The AGS is calculated from the independent generators to which are added the 
dependent generators. These last are obtained by multiplying together pairs or threes of 
independent generators. Keeping the same example, we get: 
124.135 = 2345 
124.236 = 1346 
135.236 = 1256 
124.135.236 = 456 
hence the AGS: 
I = 124 = 135 = 236 = 2345 = 1346 = 1256 = 456 
The AGS contains 2P terms. The AGS can be used to calculate all the contrasts in the 
fractional design. Contrast h , is obtained by multiplying all the AGS terms by 1 and adding the 
results 
1.1 = 1.124 = 1.135 = 1.236 = 1.2345 = 1.1346 = 1,1256 = 1.456 
simplifling, 
1=24=35=1236=12345=346=256=1456 
and applying the equivalence relationship 
k , = 1+ 24 + 35 + 256 + 346 + 1236 + 1456 + 12345 
110 
The other contrasts, h 2, h 3, h 4, h and h are obtained in the same way. 
Because of the importance of these calculations we shall now look at some practical 
rules for going from the AGS to the contrasts and vice versa. 
10. PRACTICAL RULES 
10.1 Going from AGS to contrasts:Write the AGS taking care to include the signs, e.g.: 
+I = -124 = +235 = +1345 
Multiply all the AGS generators by 1 to obtain contrast h 
+1.I = -1.124 = +1.235 1 +1.1345 
simpli@, 
+ I = -24 = +1235 = +345 
and remove the equals sign 
1 - 24 + 1235 + 345 
This expression is equal to contrast h I . We can order the terms, starting with the 
shortest: 
h = 1 - 24 + 345 - 1235 
The same can be done for h 2, h 3, h etc 
10.2 Going from contrasts to the AGS 
First write the contrast, e.g. h , : 
h , = 1 - 35 + 234 - 1245 
Keep only the right hand side terms 
1 - 35 + 234 - 1245 
Separate the terms with equals signs 
1 1 1 
1 = -35 = +234 = -1245 
Multiply by 1 to obtain the AGS 
I = -135 = + 1234 = -245 
11. CHOOSING THE BASIC DESIGN 
The most appropriate basic design for a specific experiment can be chosen by 
considering: 
The total number of factors to be studied 
The number of trials to be performed. 
11.1. Total number of factors to be studied 
If the experimenter wishes to study k factors, he could use the n initial columns to study 
the n initial factors. He could then use the k-n interaction columns for the additional factors. 
This is clearly only possible if there are k-n interaction columns available. 
For example, if the experimenter wants to study six factors, he could choose a 23 basic 
design, and study the three first factors in the first three columns and the three extra factors in 
three of the four interaction columns. But if there are eight factors, this will be impossible 
because there will be no column for the eighth. In this case, he must use a 24 basic design, and 
then study the four first factors in the initial four columns and the four additional factors in four 
of the eleven available interaction columns. 
Table 6.8 shows the maximum number of extra factors that can be studied with two level 
designs. In this Table, C : is the standard notation for the number of possible combinations of 
k objects taken q at a time: 
cq -- 
q ! (k-q) ! 
k! 
k - 
In this relationship k is the number of main factors in the basic design and q the order of 
interaction, 
112 
Maxi 
number of 
aliised 
factors. 
1 
4 
11 
26 
57 
120 
2k-k-1 
TABLE 6.8 
CONSTRUCTION OF FRACTIONAL DESIGNS 
Maxi 
number of 
studied 
factors. 
3 
7 
15 
31 
63 
127 
2k-1 
11.2. Number of trials to be performed 
The basic design indicates the number of trials that must be performed. A 22 basic design 
contains four trials, a basic 23 design contains 8 trials, etc. It is thus easy to choose the basic 
design. But we must also take into account the degree of confounding in the design. 
Confounding is the number of terms within each contrast. The greater the confounding, the 
more words there are in each contrast, and consequently, the more difficult the interpretation. 
For example, an experimenter wants to study 7 factors. If he chooses a 23 basic design, 
he will carry out a Z7" fractional design. The contrasts will contain Z4, or 16 terms. But if he 
chooses a 24 basic design and cames out a 27-3 fractional design the contrasts will contain only 
23, or 8 terms. The risk of ambiguity will thus be reduced by half. With a Z5 basic design, the 
contrasts of a 27-2 design will contain only four terms. Thus, each study contains a 
compromise between the number of trials and the increasing difficulty of interpretation as the 
number of terms in the contrasts increase. 
113 
RECAPITULATION 
This chapter introduces the alias theory which is very important for understanding and 
preparing fractional designs. A good interpretation of the results cannot be achieved without a 
complete knowledge of the alias theory. We have examined: 
A 23-1fractional design: the stability of a bitumen emulsion. Four trials are 
sufficient to obtain the effects of the three main factors. But the interactions are 
unknown and aliased with the main factors. 
Hypotheses for interpreting fractional designs. 
Methods for calculating contrasts. 
A new algebra based on the Box notation: the algebra of columns of signs. 
Alias generators. 
Notation of fractional designs. 
Methods for constructing fractional designs: 
One extra factor. 
Two extra factors. 
p extra factors. 
Practical rules for moving between AGS and contrasts. 
How to choose the basic design, taking into account the number of trials to be 
performed and the number of factors to be studied. 
This Page Intentionally Left Blank
CHAPTER 7 
T W O - L E V E L F R A C T I O N A L 
F A C T O R I A L D E S I G N S : 2k-p 
- E X A M P L E S - 
1. INTRODUCTION 
Chapter 6 introduced fractional factorial designs, and we used a simple example to 
illustrate the theory of alias. This example was useful for showing how to construct fractional 
designs, how to calculate contrasts and how to interpret results. But we need a little more 
information in order to be able to use the powerful tool of fractional designs. In this chapter we 
will apply our knowledge to three examples: 
Minimizing the colour of a product using a 25-2 design. 
Optimizing spectrofluorimeter settings using a 274 design. 
Plastic drum fabrication using a 284 design. 
These examples show us how to use experimental design methodology, how to choose 
the initial design, and how to find the complementary design which resolve ambiguities 
between main effect and interactions. 
116 
2. 25-2 FRACTIONAL DESIGN 
2.1. Example: Minimizing the colour of a product 
The problem: 
The product must have as little colour as possible. This colour is @ 
measured using a coiour index. Fabrication of the product involves & 
several factors. The makers believe that the factors which influence the 
colour of the final product are. 
!! 0 Factor 1 reaction temperature. 
9 Factor 2: origin of the raw material (2 suppliers) 
i# 0 Factor 3: mixing rate 
0 Factor 4: storage time. 
0 Factor 5. type of additive. 
- 
All five factors must be studied. A 25 complete factorial design involves 32 trials. This is 
far too much for the budget, and could take too long time to execute. The technician in charge 
of this study decides to use a fiactional factorial design. He begins by running 8 trials (initial 
design) which may then be followed, if necessary, by eight trials to resolve any ambiguities 
(complementary design). 
The initial design is easily constructed. Two interactions of a basic design are selected 
and aliased with the extra factors. For example: 
4 = 123 
5 = 13 
He could just as easily have selected: 
4 = 13 and 5 = 12, or 4 = 23 and 5 = 12 
For the one he has chosen, the contrasts can be calculated using alias generators. The 
two independent generators are: 
I = 1234 
I = 135 
Multiplying them together gives the dependent generator: 
I = 1234.135 = 245 
The three generators, with the mean, give the AGS: 
117 
I = 135 = 245 = 1234 
The AGS will allow him to calculate the contrasts, each of which has four terms. The 
terms of the AGS are multiplied by 1, they are then added together to give the contrast h 
The same terms of the AGS are multiplied by 2 and added together to give the contrast h 2, 
etc. For h 
1. I = 1 
1.135 = 35 
1.245 = 1245 
1.1234 = 234 
hence: 
h , =1+35+234+1245 
and the other seven contrasts: 
h , = 2 +45 +134+ 1235 
h , = 3 +15 +124+2345 
h , = 4 + 25 + 123 + 1345 
h , = 5 +13 + 24+12345 
h, , = 12+34 +145+235 
h23 = 23+ 14 + 125+345 
h , = I +135+245+1234 
Table 7.1 shows both the experimental matrix and the effects matrix. The columns for 
factors 1, 2, 3, 4 and 5 form the experimental matrix and the same columns are used to 
calculate the contrasts h h 2, h 3, h , and h 5. The interaction 12, 23 and the mean I columns 
are used to calculate the contrasts h 12, h 23 and h M. 
The results are analysed by applying the interpretation hypothesis indicated previously: 
Interactions of orders above 2 are ignored. 
If a contrast is zero, each of its terms is assumed to be zero. 
All results smallerthan the calculated error are considered to be zero. 
The non-significant contrasts are: 
h 2 = 2 + 4 5 = 0 or 2 = 0 and 4 5 = 0 
h , = 4 + 2 5 - 0 or 4 = 0 and 2 5 = 0 
h , , = 1 2 + 3 4 ~ 0 or 12 = O and 3 4 = 0 
h , , = 2 3 + 1 4 ~ 0 or 2 3 = 0 and 14=0 
The following contrasts appear to be significant: 
h , = -2.18 or 1 + 35 = -2.18 
h , = -3.33 or 3 + 15 = -3.33 
h , = -4.55 or 5 + 13 +24 = -4.55 
118 
Factor 1 is aliased with interaction 35. We do not know if the value of -2.18 is due to 
factor 1 alone, interaction 35 alone, or to a combination of the two 
Level - 
TABLE 7.1 
EFFECTS MATRIX: INITIAL DESIGN 
COLOUR OF A PRODUCT 
low 1 slow short A 
- 
remp. 
1 
Contr. 
- 
R.Mat 
2 
26.05 -2.18 -0.55 -3.33 0.10 -4.55 0.63 -0.68 
- 
Mix.R 
3 
Stor. 
4=123 
- 
Add.. 
5=13 
ILeveI+) I high 1 2 1 fast I long 1 B I 
Response 
27.4 
31.1 
26.6 
32.4 
31.4 
16.5 
27.5 
15.5 
According to the interpretation hypothesis indicated earlier ( Chapter 6), interaction 3 5 
could be zero if the contrasts h are zero, but this is not so. The result is thus 
ambiguous, and we cannot reach any conclusion. We can use the same reasoning for factor 3 
and interaction 15. If we examine contrast h we see that factor 5 is aliased with two 
interactions. One, interaction 24, is probably zero, but the other, interaction 13 may be influent 
as h , and h are not zero. 
We must always be aware of the risks we take in interpreting the results of a design. 
Saying that an interaction is zero implies that this interaction is very likely to be statistically 
equivalent to zero when compared to the standard deviation. 
Saying that an interaction is zero when the effects contributing to it are zero is a risky 
hypothesis which is often true, but can sometimes unfortunately be wrong. We must therefore 
not automatically use statistical tests to interpret the results. We should use them intelligently. 
We should above all rely on our experience and knowledge. 
and h 
119 
Provisional conclusion: 
Factors 2 and 4 have no influence, but effects 1, 3, and 5 seem to be I 
1 influent, and there may be interactions between them. A second series 
~ of trials is required to resolve these ambiguities This new set of 
experiments should allow the experimenter to calculate effects 1, 3 and 6 
5 alone, I e , without the influence of interactions 13, 15, and 35 The 
L' main effects are then said to be dealiased from the second order 
interactions I 
2.2. Techniques for dealiasing main effects from interactions 
The contrasts h ,, h , and h , are, if we neglect interactions above order 2: 
h , = 1 + 35 
h , = 3 + 15 
1, = 5 + 13 
We need to calculate new contrasts, such as: 
h', = 1 - 35 
h'? = 3 - 15 
h, = 5 ~ 13 
We can obtain the main effects 1, 3, and 5 and interactions 13, 15 and 35 by a simple 
calculation. The sum of h , and h', gives: 
1= -[h, 1 +h',] 
2 
and their difference: 
3 5 = - 1,- , 2 " h ' l 
The sum h + h', and the difference h , - h'? give 3 and 15. The sum h , + h', and the 
We must now find an experimental design from which we can calculate the contrasts: 
difference h , - h', give 5 and 13. 
h', = 1 - 35 
h'? = 3 - 15 
120 
TABLE 7.2 
FOUR 2"' FRACTIONAL DESIGNS IN A COMPLETE DESIGN 
1234 135 1 
I + + + 
25-2 Fractional Design. + + + 
+ + + 
8 rows 
+ + + 
+ - + 
25-2 Fractional Design. + - + 
8 rows 
- + + 
+ - + 
- + + 
25-2 Fractional Design. - + f 
8 rows 
- + + 
+ t 
- - + 
- 
2s-2 Fractional Design. - - + 
8 rows 
- - + 
- - + 
I = + 1234 
1=+135 
1 = + 1234 
I = - 135 
1 = - 1234 
1=+135 
1 1 - 1234 
I = - 135 
121 
If we apply the equivalence relationship in the opposite sense, i.e. from contrasts to the 
We used one of the four 25-2 fiactional designs of the complete 25 design in our first 
AGS, we see that these contrasts come from a design that has the alias generator I = - 135. 
design. This was defined by the two independent generators (Table 7.2): 
I = + 1234 and I=+135 
There are three other 25-2 fractional designs, and two of them contain the alias generator 
I = -135. We could therefore take either one of them: 
or 
I=+1234 and I=-135 
I=-1234 and I=-135 
The experimenter has chosen the I = + 1234 and I = -135 fiactional design. These two 
independent generators give the dependent generator: 
I = 1234. -135 = -245 
Which gives the AGS of the complementary 25-2 design that can be used to dealias 
We can now construct the complementary design and calculate the contrasts. 
effect 1 and interaction 35, effect 3 and interaction 13, and effect 5 and interaction 15. 
2.3. Construction of the complementary design 
The two independent generators give: 
and 
4 = 123 
5=-13 
In the basic design from which the complementary 25-2 design is constructed, the 123 
interaction column is used to study factor 4. The signs of interaction 13 are changed to study 
factor 5. The resulting complementary design is shown in Table 7.3. 
122 
Trial no 
9 
10 
1 1 
12 
13 
14 
I5 
16 
TABLE 7.3 
EFFECTS MATRIX: COMPLEMENTARY DESIGN 
COLOUR OF A PRODUCT 
Temp. R.Mat 
' 1 2 
- - + 
+ + 
+ + 
+ + + 
+ 
+ + 
+ + 
+ + + 
- 
- 
- - 
- 
- 
Mix.R 
3 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
Stor. 
4=123 
- 
+ 
+ 
- 
+ 
- 
- 
+ 
Add.. Inter. Inter. J-JT 
Level - low 1 slow short A 
Level + high 2 fast long B 
Contr 2485 -05 - I 00 3 18 -1 84 -3 13 
Response 
24.8 
34.6 
26.0 
26.7 
-045 -068 
2.4. Contrast calculation 
The alias generators set is: 
I = 1234 = -135 = -245 
We can obtain the contrasts by multiplying the AGS successively by 1, 2, 3, 4, 5, 12, 23 
and I 
h', = 1 -35 + 234- 1245 + h', E 1 - 35 
h', = 2 -45 + 134-1235 j h, 1 2 - 45 
h'3 = 3 - 15+ 124-2345 4 h', 3 - 15 
h, = 4 - 25+ 123-1345 h, z 4 - 25 
h5 = 5 - 13- 24+ 12345 + h5 E 5 - 13- 24 
123 
h ’ l 2 = 12 + 34- 145-235 + iI2 5 1 2 + 34 
h2,= 23 + 1 4 - 125-345 + i23 z 14+ 23 
h ’ ~ = I - 135 - 245+ 1234- h’M I 
The combined initial and complementary designs can now be used to remove the 
ambiguities. If we neglect the interactions of order higher than 2, we have from contrasts h , 
and A,: 
h , + i, = I + 35 + 1 - 35 =two times 1 
h , - i, = 1 + 3 5 - 1 + 3 5 = t w o t i m e s 3 5 
Substituting the numerical results of the two designs in the above formula gives: 
h , + i1 = -2.18-0.5 
h , - h‘, = -2.18+ 0.5 
1 = -1.34 
35 = -0.84 
The same calculation can be done with the other contrasts to obtain: 
The five main effects dealiased from second order interactions 
The second order interactions, either alone, or aliased together, but dealiased 
from the main effects. 
We can then draw up the table of effects (Table 7.4) a,nd use it to interpret the results of 
the two experimental designs. 
2.5 Interpretation 
The experimenter estimates that any effects smaller than k 1 colour index units are 
negligible. Using this criterion, there are only two influencing factors to be considered. 
Factor 1 - the reaction temperature 
Factor 5 - the type of additive. 
We can also see that there is a very strong interaction between these two factors. The 
high value of contrast h found in the initial design is due to interaction 15 and not to factor 3. 
Similarly, the high value of contrast h , is due to factor I and not to interaction 35. The 
high value of contrast h is due to factor 5 and not to interaction 13. 
124 
TABLE 7.4 
TABLE OF EFFECTS 
COLOUR OF A PRODUCT 
I + 1234 25.45 f 1 
1 -1.34 1 1 
2 -0.78 1 1 
3 -0.07 * 1 
5 -3.84 1 1 
4 -0.87 f 1 
15 - 
25 
35 - 
45 
-3.26 f 1 
0.97 k 1 
-0.84 1 1 
0.22 * 1 
12 + 34 0.09 k 1 
13 + 24 -0.71 * 1 
14 + 23 -0.68 f 1 
The ambiguities are now resolved. As there are only two influencing factors we could 
have camed out only a 22 design of four trials. In fact, we have camed out sixteen trials during 
the experiment. The sixteen responses can be arranged in four groups of four trials as if we had 
performed the same 22 designfour times. We can see that factors 2, 3 and 4 have no influence. 
Thus the response, the colour index, does not change whether they are at high or low levels. 
TABLE 7.5 
EXPERIMENTAL MATFUX REARRANGED 
COLOUR OF A PRODUCT 
Trial no I 
I 
5 7 9 1 1 
2 4 14 16 
1 3 13 15 
6 8 10 12 + + 
Results I 
31.4 27.5 27.0 23.6 
31.1 32.4 34.6 26.7 
27.4 26.6 24.8 26.0 
16.5 15.5 17.0 19.1 
Average 
31.2 
26.2 
17.0 
125 
We can then reconstruct a 22 design taking into account the levels of factors 1 and 5. 
There are four trials (numbers 5, 7, 9 and 11) in which factors 1 and 5 are both at low level. 
We can group together the four corresponding responses (31.4, 27.5, 27 and 23.6) and use 
their mean value, 27.4. The same can be done for the other combinations of levels of factor 1 
and 5. Table 7.5 shows the results ofthis rearrangement. 
The results can be conveniently presented as a diagram (Figure 7. I), which is easier to 
read and analyse than a set of numbers. 
27.4 16.5 
26.6 15.5 
17.0 
Tern perature 
23.6 26.7 
A. D B 
Additif 
Figure 7.1: Colour of a product. Graphical display of results. 
Examination of this figure shows: 
1 . The additive type has no influence at low temperature, the colour changes very 
little, from 27.4 to 26.2. 
2. Additive A gives a more highly coloured product at high temperature (31.2) 
than at low temperature (27.4). 
3. At high temperature, additive B gives a slightly coloured product, while additive 
A gives a highly coloured product. 
4. Additive B gives a coloured product at low temperature, but it gives a colourless 
product at high temperature. 
We can therefore conclude that we can obtain a colourless product by using a 
combination of additive B and working at high temperature. 
126 
However, we must not neglect the non-influencing factors. They are often the source of 
most usehl savings or simplifications. 
. Factor 2 Origin of the raw material: 
As this factor has no influence on product colour, we can select either of the two 
suppliers. For example, we could choose the least expensive, or the one with the best 
delivery schedule. We could also stimulate competition between them without 
endangering the quality of the final product. 
. Factor 3 . Stimng speed: 
As stimng speed has no influence, we can choose the lowest speed, and economise 
by using less energy We could also check to see if any stimng at all is required. Perhaps 
it could be dispensed with. It is impossible to decide immediately because it is outside the 
domain of the study. But we could propose a complementary study to see if stimng 
could be dispensed with. This would save on energy, maintenance and capital investment. 
Factor 4. Storage time: 
Storage time has no influence. We need therefore not worry about this storage time 
(within the limits examined in the experiments) on product colour. 
Clearly, the analysis we have carried out is only relevant for product colour. The final 
Once the results are interpreted, the experimenter may publish his conclusion. They will 
conclusion could be very different if other responses were to be considered. 
be short and include only the essentials of the analysis. 
Conclusion: 
Only two effects influence product colour the reaction temperature 
and the additive These two factors interact strongly Additive A gives a 
F dark colour, regardless of the reaction temperature Additive B gives a 
a light colour if the reaction is carried out at a high temperature Thus the 
reaction should be performed at high temperature using additive B 
The stirring speed has no influence, the slowest speed should be 
chosen so as to save energy The study could be extended to see 
whether stirring can be abandoned, saving energy, reducing capital 
investment and running costs The origin of the raw material has no 
influence, hence the least expensive supplier should be chosen 
127 
High 
26.2 
0 4 
Temperature 
Low c 
27.4 
17.0 
b 
-0 
31.2 
Additif 
A- CB 
Figure 7.2: Reaction should be performed at high temperature using additive B. 
The next example shows how it is possible to satisfy simultaneously the constraints 
imposed by each of the responses studied to attain the desired objectives. 
3. 27-4 FRACTIONAL DESIGNS 
This example is taken from a four-laboratory co-operative study to develop an assay for 
the suspected carcinogen, benzo-a-pyrene. The experimental designs were directed by Total, 
and were published in Analusis [ 191. 
3.1. Example: Settings of a spectrofluorimeter 
The Problem: 
We needed to define the optimum conditions for the quantitative 
analysis of benzo-a-pyrene. The technique used was r 
spectrofluorimetry, and the tests were carried out to determine the best g- 
k settings for analysis of low and high concentrations of benzo-a-pyrene B 
in mixtures. The experimenters required. - high sensitivity - high 1 
selectivity - low background noise ai 
128 
Response selection 
Figure 7.3 shows a typical fluorescence emission spectrum for benzo-a-pyrene. The peak 
height at 481 nm, 4 was chosen for sensitivity, the width at half-height, B, of peak A as an 
index of selectivity, and the parameter D as background noise. 
- 
481 nm 
Figure 7.3: Definition of the responses. 
Factor selection 
The seven factors chosen are all critical parameters in spectrofluorimetry. As can be seen 
in Figure 7.4, the beam of a xenon lamp passes through a monochromator. This light is 
diffracted by the excitation monochromator, and a specific wavelength hits the sample. The 
sample absorbs part of this monochromatic light and emits fluorescent light in all directions. 
The fluorescence emitted at 90" is passed through the emission monochromator and the 
emission spectrum is collected by a photomultiplier. The seven factors studied were: 
. Factor I : Excitation slit width. . Factor 2: Emission slit width. 
Factor 3: Sample temperature. . Factor 4: Scan speed. . Factor 5: Recorder gain. 
Factor 6: Photomultiplier voltage. . Factor 7: Recording pen amplitude. 
129 
excitation emission 
monochromator monochromator 
Figure 7.4: Spectrofluorimeter schematic 
Experimental domain 
High and low levels were set for each factor, as follows: 
Level - Level + 
Factor 1: Excitation slit width (nm). 2.5 7.5 
Factor 2: Emission slit width (nm). 2.5 7.5 
Factor 4: Scan speed (ndmin). 20 100 
Factor 5: Recorder gain. 1 10 
Factor 7: Pen amplitude. 2 4 
Factor 3: Sample temperature (“(2). 20 40 
Factor 6: Photomultiplier voltage (V). 310 460 
Choice of pxperimental design 
It was decided to use a fractional design based on a 23 basic design. The four 
interactions were used to study the extra factors. Thus the design was saturated. The extra 
factors were aliased as follows: 
4 = 123 
5 = 12 
6 = 23 
7 = 13 
I30 
3.2. Calculation of contrasts 
The contrasts were calculated from the AGS. This was established by writing the 
independent generators and then calculating the dependent generators of the 27" design used. 
From the aliases listed above, the four independent alias generators are: 
I = 1234 = 125 = 236 = 137 
The dependent generators were calculated by multiplying the independent generators in 
Multiplication in twos ( C i = 6) 
twos, threes, and fours. 
1234.125 = 345 
1234.236 = 146 
1234.137 = 247 
125.236 = 1356 
125.137 = 2357 
236. 137 = 1267 
Multiplication in threes ( C j = 4) 
1234.125.236 = 2456 
1234.125.137 = 1457 
125.236.137 = 567 
1234.236.137 = 3467 
Multiplication in fours ( C i = 1) 
1234.125.236.137 = 1234567 
The 27 design contains 128 effects and interactions, the 27-" design allows calculation of 
only eight contrasts. There will thus be sixteen terms or words in each contrast, and these will 
be obtained using the alias generators set we have calculated: 
I =1234=125=236=137= 345=146=247=1356 
=2357=1267=2456=1457= 567=3467=1234567 
The complete calculation of a contrast is shown here for factor 1 . Each term of the AGS 
is multiplied by 1 andthe resulting sixteen terms are added together to give contrast h , 
h , = I+ 234 + 25 + 1236 + 37 + 1345 + 46 + 1247 + 356 
+12357+267+ 12456+457 +1567+13467+234567 
If we neglect the interactions greater than second order, then: 
h , = 1 + 2 5 + 3 7 + 4 6 + ... 
13 1 
Sensi 
tivity 
1.22 
0.90 
5.33 
5.64 
3.89 
3.88 
2.82 
2.33 
And the other six contrasts 
h , = 2+ 15 + 36 + 47 +... 
h 3 = 3+ 17 + 26 + 45 +.,. 
h , = 4+ 16 + 27 + 35 +.,. 
h , = 5+ 12 +34 +67+. . . 
h , = 6 + 1 4 + 2 3 + 5 7 + ... 
h , = 7+ 13 + 24 + 56 +,., 
Selec Noise 
tivity 
5.5 -1.47 
9.0 -1.47 
20.0 2.30 
12.0 -0.69 
7.5 0.69 
8.0 0.40 
13.0 0.26 
23.0 -3.91 
Once the contrasts have been calculated, we can set up the experimental design, carry 
out the trials and enter the results in an effects matrix. In this case, the effects matrix is 
identical to the experimental matrix because all the interactions were used. Table 7.6 shows the 
experimental design and the results obtained for each trial. 
Scan 
4=123 
- 
+ 
+ 
- 
+ 
- 
- 
+ 
TABLE 7.6 
EFFECTS MATRIX: INITIAL DESIGN 
Gain P.M. 
5=12 6=23 
+ + 
+ - 
- - 
- + 
+ - 
- - 
+ 
+ + 
- 
SPECTROFLUORIMETER 
Level - 
Level + 
Trial 
no 
1 
2 
3 
4 
5 
6 
7 
8 
- 
2.5 2.5 20°C 20 1 310v 2 
7.5 7.5 40°C 100 10 460v 4 
Excit 
1 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
132 
3.3. Interpretation of the initial design 
The results of these eight trials are interpreted by examining one response at a time 
Sensitivity 
TABLE 7.7 
TABLE OF EFFECTS 
SPECTROFLUORIMETER 
(Sensitivity) 
Mean 3.25 
I -0.06 
2 0.78 
3 -0.02 
4 -0.14 
5 0.02 
6 -1.43 
7 -0.06 
Sensitivity appears to be influenced by two factors - the emission slit width (2) and the 
photomultiplier voltage (6). 
Interaction 26 is the only one which could be influent. Let us see if the contrast 
containing this interaction is significant. 
h = 3+ 17 + 26 + 45 +...= -0.02 
This is one of the smallest contrasts. The interpretation hypothesis we have adopted 
assumes that in this case all the terms of the contrast are zero. Thus, interaction 26 is also zero. 
We conclude that there are only two factors (2 and 6 ) that influence sensitivity, and that there 
is no interaction between them. 
133 
Selectivity 
TABLE 7.8 
TABLE OF EFFECTS 
SPECTROFLUORIMETER 
(Selectivity) 
Mean 12.25 
1 0.75 
2 4.75 
3 0.63 
4 2.63 
6 0.38 
7 1.88 
5 -0.25 
Three contrasts appear to influence selectivity: h *, the emission slit width (2); h , scan 
speed (4); and h 7, recorder pen amplitude (7). 
h , = 2 + 1 5 + 3 6 + 4 7 + ... 
A, = 4+ 16 + 27 + 35 +,.. 
h = 7+ 13 + 24 + 56 +.., 
Examination of the contrasts shows that the main effect of factor 2 is aliased with 
interaction 47. Contrasts h , and h are large. The interpretation hypothesis adopted assumes 
that, in this case, interaction 47 could be significant. We cannot, therefore, reach any 
conclusion, as the high contrast h may be due to either a large main effect, 2, or to a strong 
interaction, 47, or to the effect and the interaction. The same ambiguity appears with factor 4 
and interaction 27 in contrast h 4; and with factor 7 and interaction 24 in contrasts h 
Background noise 
There seem to be three influencing factors: excitation slit width (l), recorder gain (5) and 
Factors 1, 5 and 6 are not aliased with interactions 15, 16 and 56. There is thus no 
photomultiplier voltage (6). 
apparent ambiguity for this response. 
The results for the three responses show that we should consider a complementary 
design to obtain more information on selectivity. We must establish a complementary design in 
order to study this response more precisely. For each of the eight new trials we will measure 
the three responses, sensitivity, selectivity and background noise, and make our interpretation 
based on all sixteen trials. 
I34 
TABLE 7.9 
TABLE OF EFFECTS 
SPECTROFLUORIMETER 
(Noise) 
Mean -0.48 
1 -0.93 
2 -0.02 
3 -0.15 
4 -0.11 
5 -0.86 
6 -1.61 
7 -0.18 
3.4. Construction of the complementary design 
We defined the initial Z7-' design by the independent alias generators: 
I = + 1234 = + 125 = + 236 = + 137 
This is only one of the sixteen fractional 274 designs forming a complete 27 design. The 
sixteen 27-4 designs are defined by all the combinations of 8 generators: 
1 = + 1234 
l = + _ 1 2 5 
1 = k 236 
I = + 137 
Our problem is to select one of the I 5 remaining fractional designs which will allow us to 
dealias the effects of factor 2 from interaction 47. We could choose a fractional design giving 
the contrast 
h'; = 2 + 15 + 36 - 47 
This contrast associated with I , gives the system: 
h 2 = 2 + 1 5 + 3 6 + 4 7 
(, = 2 + 15 + 36 - 47 
We could then calculate: 
135 
h , + L2 = 2 + 15 + 36 + 47 + 2 + 15 + 36 - 47 =two times (+ 2 + 15 + 36 ) 
h , - h'; = 2 + 1 5 + 3 6 + 4 7 - 2 - 15-36+47 =twotimes 47 
And this would give us factor 2 associated with interactions 15 and 36. But it is 
preferable to have factor 2 completely dealiased from interactions. We must therefore try to 
obtain the contrast: 
h2 + 2 - 1 5 - 3 6 - 4 7 
and hence the system: 
h , = + 2 + 1 5 + 3 6 + 4 7 
h2 = + 2 - 15 - 36 - 47 
which gives: 
h , +- h2 = + 2 + 15 + 36 + 47 + 2 - 15 - 36 - 47= two times + 2 
1 2 ~ 
i 2 = + 2 + 15 + 36 + 47 - 2 + 15 + 36 + 47=two times(+ 15+ 36 + 47) 
The 274 fractional design which allows us to calculate h'; must contain the generators: 
1 = - 125 
I = - 236 
I = - 137 
Two fractional designs have these generators: 
The first one is 
I = + 1234=- 125 = - 236 = - 137 
and the second is 
1 = - 1234 = - 125 - 236 = - 137 
We could choose either. Let us use the design: 
I = + 1 2 3 4 ~ - 125=-236=- 137 
The eleven dependent generators of the complementary design are obtained from the 
four independent generators using the same technique as was used in the initial design. 
Multiplication in twos (C: = 6) 
1234. ( - 125 ) = - 345 
136 
1234.(-236) =-146 
1234. ( - 137 ) = - 247 
- 125. ( - 236 ) = + 1356 
- 125. ( - 137) =+2357 
-236.( -137) =+1267 
Multiplication in threes (Ci = 4) 
1234. ( -125) . ( -236) =+2456 
1234. ( - 125 ) . ( - 137 ) = + 1457 
-125. ( - 236). ( - 137) =- 567 
1234. ( - 236 ) . ( - 137 ) = + 3467 
Multiplication in fours (C: = 1) 
1234. ( - 125 ) . ( - 236 ) . ( - 137 ) = -1234567 
From this we obtain the sixteen AGS terms of the complementary design: 
I 1234 = - 125 = - 236 = - 1 3 7 ~ - 345 = - 146 = - 247 = 1356 
=2357=1267=2456=1457=-567=3467=-1234567 
The contrasts, ignoring interactions greater than second order, are then obtained directly 
fi-om the AGS: 
h', = 1 -25 - 37-46 
L2 = 2 -15 - 36-47 
h'? = 3 - 17- 26-45 
h, 4 - 16- 27-35 
h'5 = 5 - 12 - 34-67 
h6 = 6 - 14 - 23-57 
h, 7 - 13 - 24-56 
Using both the initial and the complementary designs gives the main effects dealiased 
from the second order interactions: 
1= -[A, 1 + i,] 
2 
137 
Sensi 
tivity 
4.14 
3.18 
2.82 
2.74 
2.44 
0.98 
5.66 
5.63 
1 
2 
2= -[k2 + h;] 
Selec Noise 
tivity 
3.5 3.56 
12.0 -2.41 
14.0 1.39 
14.0 -1.90 
8.0 -0.62 
6.0 -3.22 
14.0 0.02 
14.0 -1.61 
etc. 
and the associated second order interactions: 
Level - 2.5 2.5 20°C 20 1 310v 
Level 4 7.5 7.5 40°C 100 10 460v 
etc. 
2 
4 
TABLE 7.10 
EFFECTS MATRIX: COMPLEMENTARY DESIGN 
SPECTROFLUORIMETER 
t- 
+- 
+- 
P.M. 
6= -23 7= -13 
+ 
138 
The complementary design is constructed from a basic 23 design with the independent 
generators: 
1 = f 1234 = - 125 = - 236 = - 137 
These generators can then be used to establish the columns of signs for each of the 
factors. Multiplying + 1234 by 4 gives: 
4 = 123 
Thus, the column of signs drawn up for factor 4 are those for column 123 of the initial 
design. Multiplying - 125 by 5 gives: 
5 = -12 
So the column of signs attributed to factor 5 is column 12 multiplied by -1. It is thus the 
opposite, all the signs are changed. We can continue by multiplying - 236 by 6 and then - 137 
by 7. 
6 = -2 3 
7 = - 1 3 
The signs of columns 6 and 7 of the original design are changed to give the columns of 
the complementary design. 
Thus, the signs ofthe columns for factors 1, 2, 3, and 4 remain unchanged, while those 
for factors 5, 6 and 7 are changed. Table 7.10 shows the trials performed for the 
complementary design together with the experimental results and the contrast values. 
The results of all sixteen trials can be used to calculate the main effects dealiased from 
second order interactions. If we now go back to the problem of selectivity encountered for 
factors 2, 4 and 7, we see: 
2 =-[hz 1 +&I=-[4.75+3.31]=4.03 I 
2 2 
h2 - A 2 ] ' I = -[4.75-3.31]=0.72 
2 
4 =-[A4 1 + ~ q ] = ~ [ 2 . 6 3 + 1 . 3 1 ] = 1 . 9 7 
2 
1 I 
2 7 - -[h4 2 -h,]=-[2.63-1.31]=0.66 2 
139 
1 
2 
7 = - [ h 7 +h' 7]-:[ - - 1.88+1 31]=1.59 
We can calculate the effects and interactions for all the factors in this way. The results 
are shown in the table ofeffects (Table 7.11) 
TABLE 7.11 
TABLE OF EFFECTS 
SPECTROFLUORIMETER 
(Initial and Complementary Experimental Designs) 
Mean 
1 
2 
3 
4 
5 
6 
7 
25 + 37 + 46 
15 + 36 + 47 
17 + 26 + 45 
16 + 27 + 35 
12 + 34 + 67 
14 + 23 + 57 
13 + 24 + 56 
Sensitivity 
3 . 3 5 
-0.19 
0.77 
0.10 
-0.03 
-0.13 
-1.32 
0.00 
0.13 
0.0 1 
-0 12 
-0.10 
0.15 
-0.11 
-0.06 
~ ~____ 
Selectivity 
1 I .47 
0.78 
4.03 
0.22 
1.97 
0.28 
0.10 
1.59 
-0.03 
0.72 
0.41 
0.66 
0.29 
0.28 
-0.53 
Noise 
-0.46 
-0.99 
0.11 
-0.03 
-0.20 
-0.97 
-1.26 
-0.38 
-0.06 
-0.13 
-0.12 
0 08 
0.12 
0.10 
0.20 
140 
- ~ 
Excitation ( I ) + 
Emission (2) + - 
Temperature (3) 
3.5 Interpretation of the initial and complementary designs 
We use all sixteen trials for the interpretation. In this case, the precision of effects and 
interactions is better than that from the results of the initial design having only eight trials. Let 
us examine each response in turn: 
Sensitivity 
The results of the initial design are confirmed. There are two influencing factors - 
excitation slit width (2) and photomultiplier voltage (6). There is no interaction 26 as the 
corresponding contrast is small. 
Selectivity 
The results in Table 7.10 show that there are three influencing factors: excitation slit 
width (2), scan speed (4) and pen amplitude (7). 
The contrasts containing interactions 47 and 27 are a little high, but the experimenters 
considered them to be too small to be taken into account. They therefore decided that there is 
no significant interaction. 
Background noise 
interactions 
give the conclusion of the study. 
Conclusion: 
The results of the initial design are confirmed, there are three influencing factors and no 
The complementary design removed the ambiguities and the results are clear enough to 
There is no significant interaction . The influencing factors are not the @ 
- same for the three responses. The results can be summarized in a 
B table that also shows the optimal setting levels. 
TABLE 7.12 
SPECTROFLUORIMETER 
Factors influencing the selectivity, sensitivity and 
background noise in setting up a spectrofluorimeter 
I Sensitivity I Selectivity I Noise I 
I I 
:\ I I 
141 
I 
Rules for settina UD the spectrofluorimeter: 
1. The experimenters were not concerned with sample temperature. 
2. The spectrofluorimeter should therefore be set up as follows: 
0 excitation slit width (1) level + 
0 scan speed (4) level - 
0 recorder gain (5) level + 
pen amplitude (7) level - 
3. Two factors are difficult to control: the emission slit width (2) and the 
photomultiplier voltage (6). It would be best to adjust them for specific 
assay conditions, i.e., the emission slit should be wide for high 
sensitivity when determining traces, and narrower for high selectivity 
when assaying mixtures. Photomultiplier voltage should be adjusted 
last so as to minimize background noise without reducing sensitivity. 
L 
These recommendations were followed and the chemists obtained extremely precise 
determinations (Figure 7.5) 
481 nm 
Figure 7.5 Fluorescence spectrum of benzo-a-pyrene, obtained for an optimum 
sensitivity/selectivity ratio. 
142 
We have used all the techniques presented so far to analyse a 274 design. We studied 
seven factors using just eight trials in the initial experiment. This is called a saturated design as 
it does not allow evaluation of interactions. This type of design is extremely usefbl in the initial 
phase of a study. Its particular strength is that it provides the influencing and the non- 
influencing factors within the experimental domain. If there are ambiguities in interpreting the 
initial design, the technique of progressive knowledge acquisition can be applied by running a 
complementary design to obtain hrther information, and hence resolve the problem. The 
theory of aliases is indispensable in looking for ambiguities. This is the only way of detecting 
the main factors which could be aliased with non-negligible interactions. 
4. STUDYING MORE THAN SEVEN FACTORS 
The 274 design is constructed from a basic z3 design having three columns of main 
factors and four interaction columns. It therefore cannot be used to study more than seven 
factors. For eight or more factors, we must use a basic 24 design to build the design we need. 
With eight factors, we use the four initial columns to study four factors and select four 
interactions for the other four factors. The choice of interactions requires some care. We must: 
a. Take into account anything we know of the phenomenon, so as to choose the 
interactions that are most likely to be zero or small. 
b. Take the precaution of aliasing on interactions of the highest possible order, as these 
are the one that, without any particular knowledge of the phenomenon, are most likely 
to be small or zero. 
We would use a 284 design to study eight factors, and a 29-s design to study 9 factors. 
The basic 24 design can be used to study up to 15 factors (215-'* ). Once we get to 16 factors, 
we must use a basic Z5 design. Table 6.8 can be used to select the basic design in connection 
with the number of factors to be studied. This number could, in theory, be as large as wanted 
by the investigator. 
c Avoid aliasing the main factors together or with low-order interactions, especially 
second order interactions. This precaution is automatically taken if we are carehl to 
use a high resolution design. 
5. THE CONCEPT OF RESOLUTION 
5.1. Definition of resolution 
When we are constructing a fractional design, we must consider the matrix of effects of a 
basic design and select columns of interactions for studying the extra factors. We generally 
choose high order interactions as these are likely to be small or zero. But this is not enough. 
We must also be sure that the main factors are aliased with interactions having the highest 
143 
possible order. It is better to alias the main factors with third order interactions than with 
second order ones. The concept of resolution is based on this idea. 
A resolution 111 design is a fractional design in which the main factors are aliased with 
second order interactions. This is the case with a 23-L design defined by 1 = 123. When the 
contrasts h h and h are calculated we have: 
h 1 = 1 + 2 3 
h 2 = 2 + 1 3 
h 3 = 3 + 1 2 
A resolution IV design is a fractional design in which the main factors are aliased with 
third order interactions, and never with second order interactions. For example, a 24-1 design 
having the alias generator I = 1234: 
h l = 1 + 2 3 4 
h , = 2 + 134 
h = 3 + 124 
h = 4 + 123 
In a resolution 1V design the second order interactions are aliased between themselves or 
with higher order interactions: 
h , 2 = a 34 = 12 + 34 
h 1 3 = h 24 = 13 + 24 
h ,1 = h23 = 14 + 23 
Let us look at an example in which several extra factors are aliased with interactions. If 
we wanted to study eight factors in sixteen trials, we would select a basic Z4 design, so thatwe 
could write 
5 = 1234 
6 = 123 
7 = 124 
8 = 234 
We can now find the resolution of this 28-4 design. The independent alias generators are: 
1 = 12345 = 1236 = 1247 = 2348 
We can then deduce the dependent generators 
I =456=357=158=3467=1468=1378=12567=23568=2678=24578=1345678 
These independent and dependent generators are used to write the AGS 
144 
I =12345=1236=1247=2348=456=357=158=3467=1468 
=1378=12567=23568=2678=24578=1345678 
When the terms of the AGS are multiplied to obtain the contrasts (equivalence 
relationship), the three-component generators give second order interactions, for example in 
contrast h in this example: 
h , =4+56+ ... 
The resolution is 111: a main effect is aliased with a second order interaction. The 
resolution of a design is equal to the number of components in the shortest alias generator in 
the AGS. The shortest generators in the AGS of the present example have three components: 
456,357 and 158. 
Let us return to the 2x4 and use other interactions to alias the four extra factors: 
5 = 234 
6 = 134 
7 = 123 
8 = 124 
The alias generators set is: 
1 =2345=1346=1237=1248=1256=2578=2345=1678 
=1346=3478=3567=4568=2467=1457=12345678 
The shortest generator contains four components, hence the resolution of the design is 
IV. The main effects are aliased with third order interactions, while the second order 
interactions are aliased between themselves. This way of aliasing main factors 5, 6, 7 and 8 
with interactions is better than the first method because the resolution is higher. 
Notation: The resolution is given in roman numerals, and is shown as an index. We 
would therefore write 2:i4, and call it a two to the power eight-minus-four, resolution four 
design. 
5.2. An example of a 2;; design: Plastic drum fabrication 
The problem: 
e An investigator desires to rigorously control the volume of the plastic 
drums The design volume of 2 litres was found to vary too much 
= around this value. Careful examination of the fabrication conditions - showed that eight factors could slightly alter the capacity of the drums 
z A complete factorial design was not possible because it requires 
running 256 trials The investigator decided to carry out only sixteen 
145 
trials, and then, depending on the results, carry out either a D 
complementary sixteen-trial design or just a few complementary trials. p "* 
Factors . Factor 1 : injection speed. . Factor 2: injection temperature. . Factor 3: injection pressure. . Factor 4: moulding temperature . Factor 5: feedstock input speed. . Factor 6: feedstock supplier. . Factor 7: mixing speed. . Factor 8: dwell time. 
Response 
between the true volume and 2000 cm3. The responses could be positive or negative. 
and if possible not greater than 2002 cm3. 
The objective is to obtain a volume of 2000 cm3. The response chosen is the difference 
The experimenter must propose a solution with a volume never smaller than 2000 cm3 
Design 
The initial design is thus a 2;: constructed from a basic Z4 design. Factors 1, 2, 3 and 4 
were studied in the first four columns of the design, and factors 5, 6, 7, and 8 were associated 
with high-order interactions, so as to obtain a resolution IV design as follows: 
5 = 234 
6 = 134 
7 = 123 
8 = 124 
There are thus four independent alias generators: 
1=2345=1346=1237=1248 
The eleven dependent generators were calculated by multiplying the independent 
generators in pairs, threes and fours. The fifteen contrasts were calculated from the AGS: 
I =1237=1248=1256=1346=1358=1457=1678=2345=2368 
=2467=2578=3478=3567=4568=12345678 
Each contrast contains sixteen terms, but we shall write only the main effects and the second 
order interactions. Hence: 
h , = L + ... 
h 2 = 2 +... 
h , = 3 f . . . 
146 
h , = 4 + . . 
h , = 5 + . . . 
h , = 7 + . . . 
h , = 8 + . . 
h , = 6 + . . . 
h , , = 12+ 37 + 48 + 56 
h , , = 13+ 27 + 46 + 58 
h , , = 14+ 28 + 36 + 57 
A,, = 15+ 26 + 38 +- 47 
h , , = 16+ 25 + 34 + 78 
h , , = 17+ 23 + 45 + 68 
h , , = 18+ 24 + 35 + 67 
The sixteen trials were carried out according to the design shown in table 7.13, the 
responses were the differences in volume from a reference volume of 2000 cm3. 
The resolution IV of this design provides the main effects unaliased with second order 
interactions. This means that we can probably obtain a good estimate of the main effects and 
immediately detect the influencing factors. However the second order interactions are aliased 
together, so that if one of the corresponding contrasts is high, we would be unable to decide 
whether second order interaction was responsible. 
TABLE 7.13 
28-4 
1" DESIGN (I = 2345 = 1346 = 1237 = 1248) 
PLASTIC DRUMS 
Response 
4 7 
3 5 
-0 2 
-1 0 
0 5 
10 7 
15 0 
7 2 
-0 5 
-0 1 
6 6 
2 6 
15 9 
7 3 
0 8 
9 4 
147 
TABLE 7.14 
TABLE OF EFFECTS 
PLASTIC DRUMS 
Mean 
1 
2 
3 
4 
5 
6 
7 
8 
12 
13 
14 
15 
16 
17 
18 
5.15 cm3 
-0.20 
-0.10 
3.20 
0.10 
-2.70 
-0.05 
0.20 
1.90 
11 
I1 
I , 
I1 
,I 
I, 
,I 
,I 
-0.30 I1 
0.50 II 
-0.25 II 
2.50 
-0.10 
-0.15 
-0.30 
11 
,I 
I1 
I 1 
Three factors seem to influence the final volume (Table 7.14): injection pressure (factor 
3), feedstock input speed (factor 5) and the dwell time (factor 8). 
VOLUME 
VARIATION 
(cm3 ) 
A 
c 
-1 0 +l 
INJECTION PRESSURE 
Figure 7.6: Influence of the factor 3: injection pressure. 
148 
VOLUME 
VARlATlON 
(m3) 
1 0 +I 
FEEDSTOCK INPUT S P E E D 
Figure 7.7: Influence of the factor 5: feedstock input speed. 
VOLUME 
4 
3 
2 / 
-1 0 +I 
DWELL TIME 
Figure 7.8: Influence of the factor 8: dwell time. 
We can also see that contrast h ,5 is high. We will therefore have to do another study to 
identify the second order interaction responsible for this high contrast value, 15, 26, 38 or 47: 
I , , = 15+ 26 + 38 + 47 
We will cover this question in Chapter 12. 
149 
Provisional conclusion: 
- 
zi The average excess drum volume found during the trials was about 
5 cm3 This average value can be reduced by lowermg the injection 
pressure (factor 3), increasing feedstock input speed (5) and reducing 
the dwell time (8) These emergency measures will reduce the excess 
volume, but a complementary study will be necessary to explain the 
high value of the contrast h ,5, and to define the set-up values to be 
used to come closer to the specifications. 
150 
RECAPITULATION 
The three examples in this chapter have shown: 
The use of alias generator sets (AGS) for calculating contrasts 
The method for constructing and choosing a complementary design. 
How to dealias the main factors from second order interactions 
One major point of interpretation should be emphasised: it concerns the use of 
factors which do not influence the response 
They can often provide savings (e.g., stirring speed, supplier) and provide 
considerable flexibility when a compromise must be found between 
several responses. A factor may influence one response but not another. 
The choice of interactions to use in studying extra factors must take account of 
the resolution concept to avoid, whenever possible, associating the main effects 
with second-order interactions. The higher the resolution, the better the choice 
of design. 
CHAPTER 8 
T Y P E S O F M A T R I C E S 
1. INTRODUCTION 
In the preceding chapters we have introduced three types of matrices: 
The experimental matrix. 
The effects matrix. 
The basic design matrix for constructing fractional designs 
These three types of matrices can be confused, especially in the early stages, because 
they are so similar, and sometimes even identical. This Chapter makes it easier to identie each 
of these matrices by examining the principal similarities and differences between them. It will 
be easier to identifjr each of these matrices if we know more about them. 
2. THE EXPERIMENTAL MATRIX 
The experimental matrix is a table containing allthe trials to be performed. It includes: 
a. all the factors to be studied. 
b. the number of trials to be run. 
c. the levels assigned to each factor in each trial 
152 
Factor 2 
(HCI) 
diluted 
diluted 
concentrated 
concentrated 
d i 1 u t e d 
diluted 
concentrated 
concentrated 
The standard table can be drawn up in two different, but equivalent ways. In the first, the 
factor levels are given in usual or normal units (bar, cm, hour, etc.). In the second, these levels 
are expressed as coded units, with the significance of the -1 and +1 being shown in an 
appendix table. 
The first type is simpler and should be used if the trials are to be run by anyone who is 
not familiar with experimental designs. 
Factor 3 
(bitumen) 
A 
A 
A 
A 
B 
B 
B 
B 
TABLE 8.1 
EXPERIMENTAL MATFUX 
STABILITY OF A BITUMEN EMULSION 
Trial no 
I 
Factor 1 
(fatty acid) 
1 
2 
3 
4 
5 
6 
7 
8 
low conc. 
high conc. 
low conc. 
high conc. 
low conc. 
high conc. 
low conc. 
high conc. 
Let us return to an example we looked at in Chapter 3, the complete z3 design adopted 
for the bitumen emulsion stability example. The experimental matrix shown in Table 8.1 has 
been prepared using the first style. 
We have not adopted this form of presentation in this book as it is not suitable for 
developing the theoretical background of experimental designs and the general calculations 
involved. All the experimental designs are presented using coded units. The low levels of 
factors are indicated by -1 and the high levels by + l . This type of table contains only numbers 
that are easily read and remain valid regardless of the absolute level expressed in the usual 
units. A complementary table containing the specific values, in normal units, of the high and 
low levels of each factor, must be added in order the carry out the trials. Table 8.2 shows the 
complete 23 design for the bitumen emulsion stability example. It is the same as Table 3.1 in 
Chapter 3 
Tables 8.1 and 8.2 are the same experimental design presented in two different ways. 
These two tables show that the experimental matrix is simply a working plan. This plan is used 
by the experimenter to perform the programmed trials. 
153 
Trial no 
I 
2 
3 
4 
5 
6 
7 
8 
TABLE 8.2 
EXPERIMENTAL MATRIX 
STABILITY OF A BITUMEN EMULSION 
Factor 1 Factor 2 Factor 3 
(fatty acid) (HCI) (bitumen) 
- - - 
- - + 
- + 
+ + 
- 
- 
+ 
+ 
+ + 
+ + + 
- - 
- + 
- 
Level (-) 
Level (+) 
low conc. diluted A 
high conc. concentrated B 
3. THE EFFECTS MATRIX 
This matrix is used to calculate the effects. It is no longer a working plan, but a mathematical 
tool for interpreting all the responses measured during the experiment. The signs +1 and -1 are 
no longer the levels, but are real figures, and these figures are used in the calculations. It is no 
longer possible to replace the +1 and -1 signs by the values in normal units as these figures no 
longer represent the levels. 
TABLE 8.3 
1 2 3 
-1 -1 -1 
+I -1 -1 
-1 +I -1 
+1 +1 -1 
-1 -1 +1 
+1 -1 + I 
-1 +1 +I 
+1 +I +1 
154 
The effects matrix for factorial designs is a Hadamard matrix. It can be constructed 
using the columns of the experimental matrix (second form), assuming for the calculation that 
the signs representing the levels are real numbers (Table 8.3), to which can be applied the signs 
rule to obtain the other columns of the matrix. This subterfuge allows us to quickly and easily 
find all the columns to be used in calculating the effects and interactions. We must add a 
column of + signs to obtain the X Hadamard matrix. This column of + signs is used to 
calculate the mean (Table 8.4). 
TABLE 8.4 
Hadamard matrix derived from the 
experimental matrix 
by applying the signs rule 
1 2 3 12 13 23 123 I 
-1 -1 -1 + 1 +1 +1 -1 +1 
+1 -1 -1 -1 -I +I +I +1 
- I + l -1 -1 +1 -1 + I + I 
x = +1 + I -1 +I -1 -1 -1 +I 
-1 -1 +1 +1 -1 -1 +I + I 
+1 - 1 +1 -1 +1 -1 -1 +1 
-1 +1 +I -1 -1 +I -1 +1 
+1 +I +1 +1 + I +I +I + I 
This X Hadamard matrix links the response vector-matrix Y to the effects vector-matrix 
E according to the matrix equation: 
Y = X E 
The experiments give the elements of the vector matrix Y. The rules set out in Chapter 3 
are used to caIculate the elements of the vector matrix E (i.e., the mean, main effects and 
interactions) from Y and X. It can be seen that the X matrix is really a mathematical tool. 
4. THE BASIC DESIGN MATRIX FOR CONSTRUCTING 
FRACTIONAL DESIGNS 
This matrix is used to construct a fractional factorial experimental design. It is therefore, 
by its nature identical to the experimental matrix. 
155 
The problem is to construct this type of matrix taking into account the number of trials to 
be carried out and the number of factors to be studied. Lists of all the principal matrix cases 
have been published in tables, and the reader can refer to them. However, the experimenter 
must be able to readily find the matrix that he needs for a specific study. The method of finding 
such a matrix is closely linked to the theory of aliases, and is of considerable help to the reader 
in interpreting results. A fiactional factorial design is easily obtained from an effects matrix. 
The first step is to choose an effects matrix having a number of lines equal to the number 
of trials to be performed. In the case of factorial designs this number is not any number, it is 
equal to 2" : 2, 4, 8, 16, 32, etc. trials. We have called this matrix the basic design because the 
- 1 and +I of the effects matrix are considered as levels of factors and not figures. 
The second step is to choose as many columns from the basic design as there are factors 
to be studied. The experimenter thus obtains a rectangular matrix having as many lines as there 
are trials and as many columns as there are factors. For example, we can construct a design 
with eight trials to study five factors as follows: 
I . We first write out a Z 3 experimental matrix ( three columns, 1, 2 and 3) for eight trials 
(Table 8.5). 
TABLE 8.5 
1 2 3 
-1 -1 -1 
+ I -1 -1 
-1 +I -1 
+ I +1 -1 
-1 -1 +1 
+ I -1 +1 
-1 +I + I 
+ I +I + I 
Levels are considered as figures and the signs rule is applied to calculate the interaction 
columns, giving an effect matrix without the mean column I (Table 8.6). This is the 23 basic 
design. This matrix seems to be the same as an effects matrix, except that the -1 and +I are no 
longer figures, but experimental levels. 
I56 
TABLE 8.6 
Z3 BASlC DESIGN 
I 2 3 12 13 23 123 
+ + - + 
+ + 
+ - + - 
- + + - 
+ + + + 
- - 
+ 
+ - 
+ + 
- + 
- - 
- + 
- - 
+ - 
+ + 
2 We then select five columns from the seven in the 23 basic design (Table 8.7). 
Theoretically we could use any column for any factor. But in practice, we select the 
columns so as to obtain the greatest possible resolution. We also take into account the 
experimental constraints. For example, if we know that an interaction is important, we 
do not choose its column to study an extra factor. 
TABLE 8.7 
25-2 EXPERIMENTAL DESIGN 
1 2 3 4 = 1 2 5 = 1 3 
- + 
+ - 
- + 
+ 
+ + 
+ + 
- 
+ 
- 
+ 
+ 
- 
+ 
3. The numbers -1 and + 1 are considered to be the low and high factor levels. Then, in 
order to define the trials to be performed, we can either add an extra table (Table 8.8), 
or replace the + I and -1 by their values in normal units. Lastly, the trials are 
numbered. 
157 
Trialn" I 
1 + 
2 + 
3 + 
4 + 
5 + 
6 + 
7 + 
8 + 
TABLE 8.8 
EXPERIMENTAL MATRLX 
25-2 FRACTIONAL DESIGN 
1 2 
- - 
- + 
+ 
+ + 
- 
- - 
+ - 
+ 
+ + 
- 
Response i- 
The fractional experimental design matrix can be transformed into a calculating tool as 
explained for the effects matrix. But this time only the contrasts can be determined, and the 
results correctly interpreted by using the alias theory. This topic was covered in Chapters 6 and 
7, and we will examine it in more detail in the following chapters. 
I58 
ValuesLevels 
Levels 
Values 
RECAPITULATION 
The significance of -1 and +1 in the different types of matrices are summarized in Table 
To calculate main effects 
and interactions 
To construct fractional 
designs. 
To choose levels of extra 
factors 
To perform experiments 
To calculate contrast. 
8.9. 
TABLE 8.9 
THE DIFFERENT TYPES OF MATRICES 
Type of matrix 
Experimental matrix of a 
complete design 
Effects matrix of a 
complete design 
Basic design 
Experimental matrix of a 
fractional design 
Effects matrix of a 
fractional design 
Significance of 
-1 and +I 
Levels To perform experiments 
CHAPTER 9 
T R I A L S E Q U E N C E S : 
R A N D O M I Z A T I O N 
A N D A N T I - D R I F T D E S I G N S 
1. INTRODUCTION 
Does the order in which trials are carried out make any difference to the results? In order 
to answer this question we must examine several aspects of experimental design, some 
practical and others theoretical. The sequence of trials is selected bearing both these aspects in 
mind. 
A sequence may be determined by experimental constraints. For example, let us assume 
that a fragile component of some equipment must be studied at two levels. To avoid breaking 
this component, it would be wise to carry out the low level trials first, followed by the high 
level trials. Another possible constraint is that setting up a system could be long and complex, 
and the experimenter may not wish to repeat it several times. This occurred during an 
experimental design run in a glass works. The experimenters wanted to study the influence of 
160 
furnace temperature. But changing the temperature has a certain inertia, so that it is impossible 
to go from a low temperature to a high temperature and back again between each trial. They 
decided to cany out all the low temperature trials first, and then the high temperature trials. 
There is only one column of signs which allows this strategy in a factorial design. If there are 
two factors that are difficult to set up, the trial order must be rearranged to reduce the number 
of changes. The first factor can be studied on the one-change column: 
+ 
+ 
+ 
+ 
and the second factor on the two-change column 
+ 
+ 
This arrangement is easily obtained with several trial orders, e.g.: 
Trial no 
3 
7 
5 
1 
2 
6 
4 
8 
factor 1 factor 2 
+ 
+ 
- 
~ 
There are many examples in which the experimental conditions themselves determine the 
sequence in which the trials are performed; they may be material, temporal or other constraints. 
Experimental constraints are often more important than statistical constraints. Systematic 
errors must also be taken into account when the order of trials is being decided. We shall 
analyse two types of systematic errors: drift errors and block errors. 
161 
1.1 Drift errors 
The experimenter may suspect that there is a regular change over time or space in the 
phenomena that he is studying. This change leads to systematic variations in the response. For 
example, the ageing of a catalyst which progressively becomes less active. The yield of the 
chemical reaction will be different if the same trial is carried out at the beginning of the series 
or at the end. But this type of error does not prevent us using factorial designs. On the 
contrary, we will see that it is possible, despite any response drift, to obtain effects and 
interactions whose values are correct. 
1.2. Block errors 
This type of error is mainly due to uncontrolled factors which remain fixed throughout a 
series of trials, but have different values for another series. This type of error can be seen in the 
fertility of two plots of land. An experimenter wanting to study the intluence of rain, fertilizer, 
temperature and sowing date on crop yield may be obliged to run his trials on two plots whose 
fertilities are not necessarily the same. We will see that, despite this handicap, it is possible to 
obtain correct values for the effects of the factors studied. 
The reader will undoubtedly be able to find other examples, such as experiments carried 
out at two different times (night and day, summer and winter) or at two sites (two regions or 
two laboratories). 
Lastly, the variations may be due to causes that are not regular, periodical, or organised. 
These variations are random variations. Random variations are not treated in the same way as 
systematic ones. 
We will examine examples of several strategies that can be adopted depending on what 
we know of the perturbations that may occur during the course of an experiment. 
But before doing so, we must be sure that altering the sequence of trials does not change 
the effects calculated. Let us examine the effect of factor 1 in a z3 design. 
Each term in this effect is obtained by multiplying +1 or -1 in the effects matrix by the 
response yi. Permutating two responses, i.e., two trials, 3 and 6 for instance, does not change 
the sum of these products, only the order of the calculations: 
As the addition is commutative, the value of E, does not change when the yis are 
permuted. Consequently, the effect calculation does not depend on the order in which the trials 
are carried out. 
Let us now return to the subject of the sequence in which the trials must be performed. 
We shall begin by learning how to deal with small uncontrollable systematic errors, then 
examine systematic drift errors and, lastly (in Chapter 10) block errors. 
162 
2. SMALL UNCONTROLLABLE SYSTEMATIC VARIATIONS 
The experimenter knows that small variations due to uncontrolled factors can slightly 
alter the values of the responses he wants to measure, but he does not know exactly what these 
variations are. These small variations will introduce errors into each measurement. If they are 
purely random, the trials may be carried out in any order as they will introduce no systematic 
error. But if they are not, they will introduce systematic errors, and then statistical tests will no 
longer be valid, as they assume that errors are randomly distributed. However, if we can 
randomize the small unknown systematic errors, then we can use statistical tests. For this we 
must carry out the trials in a random order. This is called randomizing the trials. 
The technique of randomization is very simple. The trial numbers are written on pieces 
of paper, mixed well, and randomly selected; the first number drawn is the trial performed first, 
and so on. A more sophisticated way is to use a spreadsheet program which can generate 
random sequences of numbers. 
Randomization should be used whenever there is any suspicion of an uncontrolled 
variation in the levels of factors which cannot be detected, measured or controlled. This is 
often the case in agricultural trials in which soil fertility varies from one area to another, but the 
factors giving rise to it cannot be controlled. These uncontrolled factors lead to both random 
and systematic errors (Chapter 4). Randomization of trials makes the distribution of the 
systematic errors random, so allowing the application of statistical tests. We should not forget 
the importance of these tests for determining the influence of a factor by comparing the effect 
to the random error. Randomization is a way of obtaining really random error. But 
randomization can lead to serious misinterpretation as it tends to increase the value of the 
random error. With randomization, the systematic errors inflate the random error. This is the 
opposite of a good strategy for the experimenter, who must look for the smallest possible 
random error in order to best evaluate the influence of the factors studied. Hence, 
randomization must be used carefhlly: it must allow statistical tests to be used, but must not 
inflate the random error too much. These two objectives are not incompatible, and we shall see 
that the best approach is to first control the systematic errors - whenever that is possible - and 
then randomize those trials which may still be randomized.The experimenter can reduced and 
obtain a good estimate of the experimental error by choosing the appropriate trial sequence. 
When trials are randomized, the order in which they are carried out does not conform to 
their original numbering. We must therefore distinguish between the name of the trial and the 
order in which it is performed. We use the convention of indicating the trial by its number and 
the order of trial execution by a number in brackets following it (see Tables 9.4 or 9.6). 
3 SYSTEMATIC VARIATIONS: LINEAR DRIFT 
Let us look at drift, which is a form of systematic variation. Drift occurs when the 
response of each trial increases or decreases by an increasing amount over the drift-free 
response. 
This is shown more clearly by examining the theoretical case of linear drift. 
The response of the first trial is y , when there is no drift. When there is drift it is yl, 
where y ; =y , + h and h is the incremental increase in drift. 
163 
Drift 
The drift-fiee response for the second trial is y2, and the response with drift is y; , where 
y; = y2 + 2h. Table 9.1 summarizes all the responses for a Z3 design. 
4.5h 0.5h I h 2 h Oh Oh Oh Oh 
TABLE 9.1 
Linear Drift 
Responses 
without 
drift. 
Responses 
with 
drift. 
y' = y + I h 
1 1 
y',=y + 2 h 
2 
y' = y + 3 h 
3 3 
y' = y + 4 h 4 4 
y' = y + S h 
5 5 
y' = y + 6 h 
6 6 
y', =y , + 7 h 
y' = y + 8 h 
8 8 
The effects matrix of a 23 design allows us to calculate the influence of the drift on each 
effect and each interaction. Table 9.2 shows such a calculation. 
TABLE 9.2 
Influence of drift on the effects and interactions of a Z3 design 
Trial no 
- 
I 
- 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ - 
Response 
I h 
2 h 
3 h 
4 h 
5 h 
6 h 
7 h 
8 h 
164 
We can see that the effects are modified as follows: 
E', = El + 0.5 h 
El2 = E, + 1.0 h 
E', = E, + 2.0 h 
Ell2 = El2 
Ell, = El, 
El23 = E23 
E'l2, = El23 
I' = I + 4.5 h 
The four interactions are not biased by the drift, while the main effects are. Clearly, it 
would be much better if we could arrange things so that the main effects are not biased by drift. 
It can be seen that the order in which the + and - signs appear in the columns of the 
interactions cancels the influence of drift. We must therefore organise the trials so that the main 
effects use this special order of signs. Written in Box notation, three of the four interactions in 
the original design, 12, 23, and 123, are chosen to give their columns of signs to the three main 
effects, l', 2' and 3', of the new design. 
1' = 123 
2 '= 12 
3 = 23 
The first column of signs, l', will contain the - and + signs of interaction 123; the second 
column contains those of interaction 12, while the third column contains those of interaction 
23 
TABLE 9.3 
Order of trials to obtain drift-free main effects 
Old Design 
Trial no 1 2 3 
New Design 
2' 3' 
+ + 
+ - 
- - 
- + 
+ - 
~ - 
+ 
+ + 
- 
Trial no 
7 
6 
2 
3 
4 
1 
5 
8 
165 
Drift 4 .5h Oh Oh Oh 
This produces the new experimental matrix, in which the trials are the same as those of 
the original matrix, but they are in a different order (Table 9.3). 
According to the hypotheses we have adopted, we must use the trial sequence: 7 6 2 3 4 
I 5 8. The main effects are then independent of drift, but the interactions still contain an error, 
as shown by the effects matrix of the new design (Table 9.4) 
2 h 0.5h Oh l h 
TABLE 9.4 
Influence of drift on the effects and interactions of a Z3 design 
2'3' 1'2'3' 
+ - 
- - 
- + 
+ 
+ + 
- 
Response 
6 h 
8 h 
The reader should remember that the results are affected by the order of the trials when 
there is drift; this order should therefore be chosen to provide pertinent conclusions about the 
main effects and interactions. 
We should be particularly careful about those interactions which, in this case, do not 
represent true interactions or an estimate of experimental error, but also include an estimate of 
drift. 
This gives us a way of detecting drift, as there are three values which are proportional to 
each other in the ratio 1: 2: 4. 
The order of trials shown above is not the only one which provides the main effects 
unaffected by a linear drift. A total of 144 different orders will give the same result for a 23 
design. Table 9.5 shows some of these, and the complete list is given in Appendix 3 [20]. 
Provided that we have taken the precaution of arranging the trials according to oneof the 
orders given in Table 9.5, we can detect drift (by examining the interactions) while still 
obtaining a good estimation of the main effects. 
166 
7 
6 
4 
7 
4 
6 
4 
6 
7 
7 
4 
6 
4 
TABLE 9.5 
Main effects free from the influence of linear drift 
z3 Factorial Design 
6 2 3 4 1 5 8 
7 3 2 4 1 5 8 
7 5 2 6 1 3 8 
4 2 5 6 1 3 8 
6 5 3 7 1 2 8 
4 3 5 7 1 2 8 
5 7 2 6 3 1 8 
3 7 2 4 5 1 8 
2 4 5 6 3 1 8 
2 6 3 4 5 1 8 
5 6 3 7 2 1 8 
3 4 5 7 2 1 8 
7 6 1 5 2 3 8 
etc 
4. WHEN SHOULD TRIALS BE RANDOMIZED? 
We can understand the consequences of randomization and the choice of anti-drift 
designs a little better with the aid of an example. We shall call this the powder mill example. 
Three investigators working in three separate laboratories carry out the same study. They 
choose three different strategies - simple randomization, a specific order to take into account 
linear drift and a complete set of experiments to measure effects, interactions and drift. 
Example: The powder mill 
The problem: 
* Three investigators want to increase the amount of powder produced 
by their mills They have exactly the same kind of mill and all must I 
4 grind the same product The factors to be taken into account by the 
three experimenters are Ibi 
ii 
0 The rotation speed (factor I) 
0 The crushing pressure (factor 2) 
The grinder head clearance (factor 3) 
They are aware that grinder wear could introduce drift The response 
~ IS the mass of powder (grams) of the correct particle size produced by 
167 
Level - 1 
Level +1 
the mill after each trial of the same duration. But each investigator 
chooses a different experimental strategy Let us examine these three 
!f 
~ strategies. 
7r: 
40 4 0.20 
60 8 0.30 
4.1. First investigator's strategy 
The first investigator analyses his problem and decides to use a 23 design. He decides to 
randomize the trials in order to overcome the systematic error introduced by grinder wear. The 
sequence drawn is: 1 5 8 7 4 6 2 3. He carries out the trials and the results are shown in Table 
9.6. 
TABLE 9.6 
POWDER MILL 
First experimenter 
Trial no Factor 1 
(rotation) 
Factor 2 
(pressure) 
+ 
Factor 3 
(air clear.) 
Response 
43 3 
337 
332 
The eight responses are used to calculate the effects and interactions shown in the effects 
table (Table 9.7) 
168 
TABLE 9.7 
TABLE OF EFFECTS 
POWDER MILL 
First experimenter 
Mean 369 grams 
1 25 
2 8 
3 9 
9 , 
II 
11 
12 5 1 
13 3 
23 22 
, 
,I 
,, 
123 -13 II 
The first investigator interprets his results as follows: he knows that the error of each 
response is k 1 gram, so the standard error of the effects and interactions is then slightly less 
than 0.5 gram. If he take three times the standard deviation as experimental error, then the 
interpretation is: 
- one major effect - rotation speed (1). 
- two minor effects, crushing pressure (2) and grinder clearance (3). 
- one very large interaction (1 2). 
- one large interaction (23) and one smaller interaction ( 1 3). 
4.2. Second investigator's strategy 
The second investigator also decides to use a Z3 design, but to guard against the 
systematic error introduced by grinder wear he uses a trial sequence that eliminates the drift 
error from the main effects. To take into account statistical constraints, he selects at random 
one of the trial orders in Appendix 3 - order number 107, which is: 6 7 3 2 4 1 5 8. The results 
of his experiments are shown in Table9.8. 
169 
Factor 1 
(rotation) 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
TABLE 9.8 
POWDER MILL 
Second experimenter 
Factor 2 
(pressure) 
- 
+ 
+ 
- 
+ 
- 
- 
+ 
Trial no 
Level - 1 
Level +1 
40 4 0.20 
60 8 0.30 
Factor 3 
(air clear.) 
+ 
+ 
- 
- 
- 
- 
+ 
+ 
Response 
216 
338 
TABLE 9.9 
TABLE OF EFFECTS 
POWDER MILL 
Second experimenter 
Mean 
1 
2 
3 
12 
13 
23 
123 
371 grams 
48 
26 
-6 
9 , 
I, 
-58 
3 
-16 
,I 
,, 
I 1 
-29 8 , 
The interpretation takes drift into account. Order number 107, the anti-drift sequence 
(Appendix 3), shows how drift modifies interactions. We therefore know that the main effects 
170 
Level - 1 
are not corrupted by drift, and that interaction 13 is not corrupted, while the other three are 
biased as follows: 
- interaction 23 contains 0.5 x the drift error. 
- interaction 123 contains 1 .O x the drift error 
- interaction 12 contains 2 x the drift error. 
If we examine these three interactions we can see that they are almost in the ratio 1 :2:4, 
so that it is very likely that the interactions are negligible and that they measure a systematic 
drift error of about 30 grams between each trial. 
The most important influencing factors are: 
- The rotation speed ( 1 ) and 
- the crushing pressure (2). 
40 4 0.20 
TABLE 9.10 
POWDER MILL 
Third experimenter 
Level +1 
Response 
500 
493 
460 
410 
426 
402 
3 93 
410 
363 
434 
335 
26 1 
309 
216 
285 
338 
263 
60 8 0.30 
Level 0 I 50 I 6 I 0.25 I 
171 
4.3. Third investigator's strategy 
The third investigator has the time and budget to study the drift by carrying out about 20 
trials. Like the first two investigators, he decides to use a 23 design. He studies the driR by 
sandwiching between each trial of this design a trial at the centre of the experimental domain. If 
there were no drift, the response of this point should always be the same. If, however, there is 
drift, the response will vary in a regular fashion. These trials at the centre of the experimental 
domain are numbered with a 0 before the trial number. 
The investigator thus plans 9 + 8 = 17 trials. Table 9.10 shows the trials and the 
responses. 
These trial results are interpreted in two steps. The first examines the drift and the 
second corrects the responses and calculates the effects and interactions. 
Examination of Drift 
The drift can be followed by the changes in the central point response (trials 01, 02, 03, 
04, etc.) as the experiment progresses. The curve in Figure 9.1 shows this change. The drift is 
marked and non-linear, being greater at the start than towards the end. 
Grams 
500 
400 
300 
200 
01 02 03 04 05 06 07 08 09 
Trial number 
Figure 9.1: Powder mill study. Ordinate: yield at each trial. Abscissa: chronological 
sequence of trials. 
172 
Correction of the responses 
The results of the 2j design trials are shown on the same graph, we can therefore refer 
their position to that of the drift curve. The point for trial number 6 (fist executed trial) is 
placed between trials 01 and 02. The point for trial number 7 (second executed trial) is placed 
between trials 02 and 03. The remaining points are arranged in the same fashion (Figure 9.1). 
The effects and interactions are calculated by eliminating the influence of drift &om each 
response. Thus, for trial number 6, the mean variation in the yield between points 01 and 02 is 
500 - 460 = 40 grams 
We assume that this variation is linear between the two trials, 01 and 02, so that the 
value on the drift curve at trial number 6 is 480 grams. The measured response of trial number 
6 is 493 grams, or 13 grams greater than the value on the drift curve. If there were no drift the 
value of the response at the central point would have remained at 500 grams. We must 
therefore add these 13 grams to the 500 to obtain the drift-free response of trial number 6, 513 
grams. 
The difference between 500 grams and the response calculated for the central point is 57 
grams for trial number 7. This must be added to that of trial number 7 to obtain the corrected 
response. 
410 + 57 = 467 grams. 
This process must be repeated for all eight responses in the design. The results are shown 
in Table 9.1 1. 
TABLE 9.11 
TABLE OF EFFECTS 
POWDER MILL 
Responses corrected from drift 
Trial 
number 
6 
7 
3 
2 
4 
1 
5 
8 
Corrected 
responses 
513 
467 
492 
530 
584 
438 
420 
566 
173 
These corrected responses can be used to calculate the effects and interactions as if there 
were no drift, as shown in Table 9.12. 
TABLE 9.12 
TABLE OF EFFECTS 
POWDER MILL 
Third experimenter 
Mean 501 grams 
1 47 
2 26 
3 -10 
12 1 
13 1 
23 -1 
123 1 
II 
II 
11 
$9 
,, 
I, 
0 
This clearly shows that the interactions are non-significant and that they may be 
considered as zero. The three factors studied all influence the results; their effects are shown in 
Figures 9.2, 9.3 and 9.4 
GRAMS 
550 
500 
450 
-1 0 +l 
ROTATION SPEED (1) 
Figure 9.2: Influence of factor 1 on powder mill yield. 
174 
500 - 
450 - 
GRAMS 
550 
/ 
I 
, 
b 
Figure 9.3: Influence of factor 2 on powder mill yield. 
t GRAMS 
550 
500 
450 
GRINDER AIR CLEARANCE (3) 
GRAMS A 
I 
I 
500 - < 
550 - 
450 - 
I 
I 
-1 0 +I 
I 
1 
Figure 9.4: lnfluence of factor 3 on powder mill yield. 
175 
Second 
Experimenter 
Special Order 
371 
48 
26 
-6 
-58 
3 
-16 
The third investigator can therefore conclude: 
Third 
Experimenter 
Corrected 
501 
47 
26 
-10 
1 
1 
- 1 
Conclusion: 
The three factors studied influence the powder mill yield. The most d 
important is rotation speed, which must be at least 60 rpm Crushing 
pressure must be as great as possible, 8 in this case, while the grinder 
clearance must be 0 20, the lowest setting. 
These factors do not interact There IS a large drop in yield from one 
trial to another due to grinder wear 
Recommendation. 
A different type of grinder should be used to avoid loss of yield. The 
experimenter could propose a new study in which a higher rotation 
speed and greater crushing pressure are examined to see if they will 8 
increase yield I 
5. RANDOMIZATION AND DRIFT 
The approaches used by the three investigators can be compared by regrouping effects 
and interactions in Table 9.13. 
TABLE 9.13 
POWDER MILL 
Comparison of the effects obtained by the three methods 
Mean 
1 
2 
3 
12 
13 
23 
123 
First 
Experimenter 
Randomization 
369 
25 
8 
9 
51 
3 
22 
-13 
1 76 
We can now examine the results of each strategy, knowing that those of the third 
investigator are the best. 
Simple randomization 
The effects and interactions are incorrect. The investigator’s lack of foresight could result 
in a catastrophe. Randomization is a useful technique that should be used as much as possible, 
but it provides no protection from experimental traps. The problem is not due to 
randomization, but to the investigator not thinking enough about the problem. Randomization 
is no substitute for reflection. In this example randomization obscured the systematic drift 
error. 
Specific order to obtain the main effects free of drift. 
The investigator was not sure that there was drift, but he could only run eight trials. He 
selected the best experimental conditions, and obtained good results for the main effects, but 
could not come to any conclusion about the interactions. This strategy is usem when only a 
few trials can be run. 
Complete correction of all responses for drift 
The effects and interactions are correct, but the price paid is a large number of trials. 
I77 
RECAPITULATION 
1, The order in which trials are carried out is most important. 
2. If only random errors are suspected, the trials can be run in any order. 
3. Randomization of trials allows errors due to uncontrolled factors whose level 
variations introduce systematic errors that are not controlled to be considered as 
random. Hence statistical tests can beused despite the presence of these 
systematic errors. 
4. If drift is suspected, a sequence of trials must be selected that provides drift-free 
main effects, but gives incorrect estimations of the interactions and average. The 
list of these sequences for a 23 design is given in Appendix 3. 
5 . Drift can be measured by carrying out regular measurements at the central point, 
using this to correct the responses and thus obtain drift-free effects. This 
method requires a few more trials but has the advantage of giving accurate main 
effects, interactions and average. 
6. If systematic errors due to drift are suspected, and the investigator wishes to 
randomize the trials, it is always possible to choose at random one of the special 
orders (for 8 trials) shown in Appendix 3. 
This Page Intentionally Left Blank
CHAPTER 10 
T R I A L S E Q U E N C E S 
B L O C K I N G 
1. INTRODUCTION 
Chapter 9 dealt with the systematic error due to drift. The present chapter deals with the 
second type of systematic error, block errors. This type of error is mainly due to uncontrolled 
factors that remain fixed throughout a series of trials, but have different values in different 
series of trials. One of the best examples is the fertility of two plots of land. An experimenter 
wanting to study the influence of rain, fertiliser, temperature and sowing date on crop yield 
may be obliged to run his trials on two plots whose fertilities are not necessarily the same. We 
will see that, despite this handicap, it is possible to obtain correct values for the effects of the 
factors studied. 
The reader will undoubtedly know of other examples, such as experiments carried out at 
different times (night/day, summer/winter), at two different sites (regions or laboratories) or by 
two different persons. 
180 
2. BLOCK VARIATIONS 
The investigator could cany out his research in two or more groups of trials. Factors act 
similarly on the responses, but there may be a systematic difference because the trials were not 
run in the same batch. For example, an agronomist may be studying the yield of cereal fiom 
two similar plots having different fertilities. Similarly, a technician may be studying the setting 
up of some apparatus whose response is influenced by the difference between the morning and 
evening ambient temperatures. 
These systematic differences may be overcome by arranging the trials in groups - 
generally called blocks. We will examine three examples of blocking - which is the art of 
arranging trials to eliminate the influence of a troublesome factor, such as differences in 
fertility, ambient temperature, etc. 
3. BLOCKING 
Example: Preparation of a mixture 
The problem: 
The investigator cannot prepare all the mixture he required to carry 
p out a z3 design at one time He was obliged to prepare the mixture in 
two batches, and the two were not completely identical. Let us assume 
f that they were very similar, but that one was a pale red (r) and the other 
@ was a deep pink (p) 
* Can the planned experiment be performed despite this difference? 
s And if so, how should the trials be run to ensure that the effects 
s calculated would be the same as if the two mixtures had been 
& identical7 
A way must be found by which the deviations due to the different mixtures cancel each 
other during the calculation of the main effects and interactions. We assume that the red 
mixture introduces an error into the response with reference to the homogeneous mixture, 
and that the pink mixture introduces an error E ~ . 
Had a single, uniform mixture been used, the effect E, in a z3 design would be: 
When the pink mixture is used for trial i, yi becomesy'i = yi + E ~ . 
When the red mixture is used for trial i, y, becomes y', = yi+ E,. 
The arrangement of trials which leaves E, with the value of the homogeneous mixture 
should incorporate E, and E~ with + signs as many times as with - signs. We could, for 
181 
example, use the pink mixture €or trials 1 , 4, 6 and 7 and the red mixture €or trials 2, 3, 5 
and 8. 
- Pink mixture: trials: I , 4, 6, 7 
- Red mixture: trials: 2, 3, 5, 8. 
We can then calculate the effect E‘, of factor 1 under these experimental conditions: 
simplifylng 
then 
E; = E, 
The effect of factor 1 is thus the same as if there was a single mixture for all eight trials 
The effects of factors 2 and 3 can be similarly obtained. The effect of factor 2 is: 
This can be simplified to: 
or 
The effect of factor 2 calculated with the two mixtures, red and pink, is equal to the 
The effect E’3 of factor 3 is as follows: 
effect that would be obtained using a single homogeneous mixture in all trials. 
simplifying 
I82 
or 
E3 = E3 
Here again the effect calculated using the red and pink mixtures is the same as that which 
would have been obtained with a single homogeneous mixture for all 8 trials. 
The choice of trials is thus quite suitable, as we have obtained the three main effects as if 
there had been a single mixture. These results can be explained graphically, with the 
experimental domain being a cube, as there are three factors (Figure 10.1). The red and pink 
mixtures are arranged so that there are two types of mixture on each side of the cube. 
I I 
7 
3 
8 
4 
Figure 10.1: There are two red and two pink mixtures on each side of the cube 
We know that the effect of a factor is half the difference between the average response at 
the high level of a factor and the average response at the low level of the same factor. The 
mean of the responses at the high level of a factor always includes two red trials and two pink 
trials (Figure 10.1) The mean of the low level responses of this factor also includes two red 
trials and two pink trials When the difference of the means is taken, the error E, appears twice 
with + signs and twice with - signs, and the same for E*, so that the effects are the same as if 
the mixture had been homogeneous 
We now calculate interaction 12 from the trials arranged as in Figure 10 1 
I83 
Once more, the error due to the two mixtures does not corrupt the value of the 
interaction. The arrangement of the experimental points provides the same value for the 
interaction as would be obtained if a homogeneous mixture have been used. 
The reader can check to make sure that the same holds true for the second order 
interactions, 13 and 23. 
But what about interaction 123? 
So El,, is not equal to El,,. El,, measures the interaction plus half the 
difference between E, and E ~ . What does this half-difference mean? E, and E measure the 
variation in the response due to the different natures of the two mixtures. The {alf-difference 
between them is thus a measure of the effect of the type of mixture It is just as if we had 
introduced an extra factor, with the high level being the red mixture and the low level the pink 
one. This fourth factor was studied on interaction 123. 
The experiment is said to have been performed in two blocks: 
First block, the red mixture, trials 2, 3, 5 and 8, i.e., using the + signs of 
interaction 123 
Second block, the pink mixture, trials 1 , 4, 6 and 7, i.e., using the - signs of 
interaction 123 
We can use the concepts introduced during our study of fractional designs (Chapters 6 
and 7) There were three initial variables, 1 , 2 and 3 and a fourth was introduced, variable 4 
The blocking resulted in the column of signs of interaction 123 being used to study variable 4 
184 
E,. 
&P 
This is equivalent to studying four factors using a basic Z3 design, i.e. there is an extra factor - 
the type of mixture. We can therefore apply the alias theory to blocking. 
EFFECT OF /, I MIXTURE 
A 
I 1 
I I I c 
-1 0 +I Mixture 
PINK RED 
1 
2 
Figure 10.2: -[cr - e p ] measures the effect of the type of mixture. 
Blocking can be expressed in Box notation as: 
4 = 123 
This introduces the alias generator 
I = 1234 
We carried out a 24-1 design in which factor 4 is aliasedwith interaction 123. We 
therefore have: 
El,, = 4+123 
The technique of blocking is used each time systematic variations between groups of 
trials are suspected. This technique allows us to calculate the effects and interactions free from 
the influence of these systematic variations. 
185 
Conclusion: 
Despite the difficulty posed by using two different mixtures instead of 
one homogeneous one, it was possible to measure the main effects 
and all the interactions except one without bias. This could be done 
because the experimenter used the technique of blocking in choosing 
the trials of each block. Only one interaction is incorrect, it is aliased 
with the blocking factor ti 
Note: 
Blocking assumes that the effects are the same in the two blocks. Here, the 
effects of factors 1, 2 and 3 were assumed to be the same in the red and pink 
mixtures. Blocking cannot be used unless this assumption is verified. 
Blocking is easy to perform. In a design, a high order interaction is chosen as 
this is likely to be almost zero, and the + signs are used to form one block of 
trials, while the - signs are used for the other. The design is thus divided into 
two half-designs. 
0 Blocking can be done on more than one factor. The same technique is repeated 
choosing several interactions. We shall examine an example of this in the next 
section. 
Blocking and randomisation are not incompatible. It is always possible to 
randomise the trials within each block. 
Blocking and drift are not incompatible. A special order can be selected within 
each block in order to eliminate the influence of drift on the main factors (see 
Appendix 3 for an example). 
4. BLOCKING ON ONE VARIABLE 
Example: Penicillium chrysogenum growth medium (continued) 
We examined the experiments of Owen L. Davies [ 1 1 1 on the nutritional medium of 
Penicillium chrysogenum in Chapter 3 . One point was not clarified at that time - interaction 
12345 appeared to be too great. This was because the investigator had not run all his trials at 
once, but performed them at two different times and in two separate sub-experiments. As he 
suspected systematic errors between each sub-experiment, he camed out a blocking using 
interaction 12345. He thus introduced an extra factor, factor 6, the sub-experiment. The design 
used can then be thought of as a ffactional 26-' design, with the alias generator: 
186 
J = 123456 
Interaction 12345 is thus aliased with factor 6, and contrast h, is measured. This is 
equal to: 
h, = 6 + 12345 
If we assume that interaction 12345 is zero, then contrast h6 measures the effect of 
carrying out the two batches of trials at different times. The levels of several uncontrolled 
factors could change. 
It is interesting to take a closer look at the way in which these trials were run. Dr Davies 
chose the - signs of interaction 12345 to select the trials for the first batch; so he ran a first 
block of trials as follows: 
1 4 6 7 10 11 13 16 18 19 21 24 25 28 30 and 31 
This block is half the 2"' design, or a sixteen-trial 26-2 design (Table 10.1) with the 
independent alias generators: 
1 = 123456 
and 
I = - 6 
The AGS is thus 
I = -6 = -12345= 123456 
This can be used to calculate the contrasts. For the main factors, we get: 
h, = 1 - 16 +23456 -2345 + h, I 1 - 1 6 
h, = 2 -26 + 13456 -1345 + h, E 2 - 2 6 
h, = 3 - 36 + 12456 - 1245 + h, F 3 - 36 
h, = 4 - 46+12356 -1235 + h, 4 - 46 
h, = 5 - 5 6 + 12346 -1234.. . . + h j I 5 - 56 
h, = 6 - I +123456 - 12345 _.. + h, I 6 - I 
I87 
Contr 
Trial 
no 
-18.6 -3.6 14.2 -1.6 -24.9 -123.2 
1 
4 
6 
7 
10 
11 
13 
16 
18 
19 
21 
24 
25 
28 
30 
31 
7om Iq. 
1 
TABLE 10.1 
EFFECTS MATRIX: FIRST BATCH 
PENlClLLlUM CHRYSOGENUM GROWTH MEDIUM 
- 
Lactose 
2 
- 
Precurs 
3 
- 
;od. nit. 
4 
- 
3ucose 
5 
Batch 1 
5 = -12345 
Response 
142 
109 
162 
200 
108 
146 
200 
I18 
106 
88 
113 
79 
101 
72 
83 
145 
Dr Davies chose the + signs of interaction 12345 for the second batch of trials. Thus the 
second block contained trials: 
2 3 5 8 9 12 14 15 17 20 22 23 26 27 29 32 
These sixteen trials were organised in a 26-2 design (Table 10 2) having the AGS: 
1=6=12345=123456 
188 
Contr. 
Trial 
no 
2 
3 
5 
8 
9 
12 
14 
15 
17 
20 
22 
23 
26 
27 
29 
32 
-16.6 4.75 17.87 3.6 -16.9 135.87 
TABLE 10.2 
EFFECTS MATRIX: SECOND BATCH 
PENlClLLlUM CHRYSOGENUM GROWTH MEDIUM 
Lactose 
2 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
Precurs 
3 
Sod. nit. 
4 
Glucose 
5 
Batch 1 
i = +12345 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
Zeesponse 
114 
129 
185 
172 
148 
95 
164 
215 
106 
98 
88 
166 
114 
140 
130 
110 
The contrasts of the main factors were deduced from the AGS: 
al = 1 +16 + 2345+23456 + h', z 1 + 16 
h2 = 2 +26 + 1345+13456 + h2 2 + 26 
h', = 3 +36 + 1245+ 12456 + L3 E 3 + 36 
h, = 4 +46 + 1235+12356 + h, z 4 + 46 
h, = 5 +56 + 1234+12346 + hs I 5 + 56 
h,= 6 + I + 12345+ 123456 + h, z 6 + I 
The results of the two designs can be interpreted in two ways 
189 
1. By using the addition and subtraction formulae and neglecting high order interactions : 
=-17.6 
16 = -[-Al 1 + h’,] = +[+18.6-165] =+1.1 
2 
-3.624.75] =+0.6 
+3.62+4.75] = 4 . 2 
3 =-[+A, 1 +h’,]=~[+14.25+17.87]=+16.1 
2 
-14.25+17.87] =+1.8 
-A, +h,]=2[+1.6+3.6]=+2.6 * 1 
-24.9-16.91 = -20.9 
+24.9-16.91~ +4.0 
-123.25+135.87] =+6.3 
I = -[-h, 1 +h’,] = $+123.25+135.87]=+129.6 
2 
This approach is inconvenient, but it has the advantage of showing that there may be 
interactions between the blocking variable (in this case number 6) and the main factors. 
I90 
2. By treating the 32 trials as a single unit and calculating the effects directly from the 
responses. This was the technique used in Chapter 3, but it has the shortcoming of 
masking the second order interactions between the blocking variable and the main 
factors, except if we note that: 
16 = 2345 
26 = 1345 
36 = 1245 
46 = 1235 
56 = 1234 
The fourth order interactions (1234 and 1345) which appear to be high, are thus only 
second order interactions between factor 6 and factors 2 and 5 . 
It is certain not worth correcting the responses by +6.3 or -6.3 in order to recalculate the 
effects, as the appropriate choice of trials in each of the two blocks allowed the effects of the 
main factors to be obtained free from the effect of running the two batches of trials at different 
times. 
5 BLOCKING ON TWO VARIABLES 
5.1. Example: Yates' bean experiment 
The Problem: 
This example is one of the oldest published experimental designs. It i$ 
was performed in 1935 by Yates, and published in 1937 [21]. He was 
interested in the influence of five factors on the yield of a specific 
The triat results should form the basis of advice to growers to help I 
them obtain the best harvest at the lowest cost We shall retain the .@ 
original units used by Yates for the sake of historical accuracy, but we @ 
will use the calculation and notation which we have adopted throughout D 
this book a 
- 
species of bean. i2 
9 
Factors and domain 
The five factors studied were: 
level - level + 
Factor 1 : Space between rows 
Factor 2: Amount of manure 
Factor 3 : Amount of nitrate, 
18 inches, 24 inches 
0 tonslacre I0 tonslacre 
0 Iblacre, 50 Iblacre 
191 
level - level + 
Factor 4: Amount of superphosphate 0 lblacre, 60 lblacre 
Factor 5: Amount ofpotash 0 Ib/acre, 100 Ib/acre 
Response 
The response was the weight of beans harvested per trial. Yates decided to use a 
complete factorial 25 design, but was carefil to divide the experiment into four blocks of 8 
trials, each block on a separate plot. 
He knew that there could be differences in the fertilities of the plots, and attempted to 
obtain more homogeneous results by separating the trials into the 4 blocks. The underlying 
reasoning was that, although there are systematic differences in plot fertility, the effects of the 
factors studied would be thesame regardless of the plot used. Blocking thus allowed him to 
measure the effects directly without extra calculations. It also allowed him to assess the 
differences in the fertility of the plots 
BLOCK 
I 
124 - 
135 - 
BLOCK 
IV 
124 + 
135 + 
BLOCK 
II 
124 + 
135 - 
BLOCK 
111 
124 - 
135 + 
Figure 10.3: Yates' bean experiment-arrangement of the four blocks on the plot of land. 
Yates chose interactions 124 and 135 for the blocking, i.e., the signs of the 32 trials of 
interaction 135 were divided into two blocks; the first half contained all the - signs of 135 and 
the second contained the + signs. Interaction 124 then divided these blocks into two. Table 
10.3 shows the assignment of trials to the four blocks, labelled I, 11, 111 and IV. This 
introduced two extra factors: 
192 
Block I 
Block I1 
Block I11 
Block IV 
- Factor 6, which measured the effect of the difference in fertility between blocks I1 
and IV for one part, and blocks I and 111 for the other. 
6 = 124 7 = 135 
- - 
- + 
~ + 
+ + 
- Factor 7, which measured the effect of the difference in fertility between blocks 
I11 and IV for one part, and blocks I and I1 for the other. 
Figure 10.4 shows how blocking was carried out and the arrangement of trials in each 
block. The trials within each block were randomised. 
, 
Figure 10.4: Random distribution of trials within each block. 
193 
Level- I 18 
TABLE 10.4 
EXPERIMENTAL MATRIX 
YATES' BEAN EXPERIMENT 
0 0 0 0 
Trial no 
Level + I 24 
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 
10 50 60 100 
Factor 2 
(manure) 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
- 
- 
+ 
+ 
Factor 3 
(nitrate) 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
Factor 4 
(s. phos.) 
- 
- 
- 
- 
- 
- 
- 
- 
+ 
-t 
+ 
+ 
+ 
+ 
+ 
+ 
- 
- 
- 
- 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
Factor 5 
(potash) 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
Response 
66.5 
36.2 
74.8 
54.7 
68.0 
23.3 
67.3 
70.5 
56.7 
29.9 
76.7 
49.8 
36.3 
45 7 
60.8 
64.6 
63.6 
39.3 
51.3 
73.3 
71.2 
60 5 
73.7 
92.5 
49.6 
74.3 
63.6 
56.3 
48.0 
47.9 
77.0 
61.3 
194 
Experiment 
Table 10.6 summarizes the experimental parameters plus the responses measured in each 
trial. 
5.2. Interpretation of experimental results 
We shall carry out an overall analysis of effects and interactions of the factors studied by 
Three factors appear to influence the yield: 
Yates (Table 10.5). 
Factor 1 : distance between rows 
Factor 2: amount of manure. 
Factor 5: amount of potash. 
The results for the main factors are shown in Figure 10.5, 10.6 and 10.7 
66 
64 
62 
60 
58 
56 
54 
52 
-1 0 +I 
ROW SPACING (1) 
Figure 10.5: Influence of row spacing (Factor 1) 
195 
TABLE 10.5 
TABLE OF EFFECTS 
YATES' BEAN EXPERIMENT 
Mean 
1 
2 
3 
4 
5 
12 
13 
14 
15 
23 
24 
25 
34 
35 
45 
123 
124 
125 
134 
135 
145 
234 
235 
245 
345 
1234 
1235 
1245 
1345 
2345 
12345 
58 91 
-3 90 
7 85 
1 6 2 
-2 75 
3 80 
2 52 
1 66 
1 4 7 
4 37 
2 57 
-0 24 
-1 98 
-2 58 
2 17 
-0 21 
0 99 
-5 85 
-0 76 
0 45 
-3 08 
- 1 74 
0 54 
1 1 2 
-0 87 
-2 42 
-0 31 
-1 01 
-1 86 
-3 17 
1 56 
2 38 
196 
A 
66 - 
64 - 
62 - 
60 - 
58 - 
56 - 
54 - 
52 - 
66 
64 
62 
60 
58 
56 
54 
52 
-1 0 +l 
MANURE (2) 
Figure 10.6: Influence of manure (Factor 2) 
-1 0 +I 
POTASH (5) 
Figure 10.7: Influence of potash (Factor 5) 
197 
Factors 3 and 4 may have a small influence. It is difficult to judge from the data available. 
There are several high values among the interaction: 
15 = 4.4 
124 = -5.85 
135 = -3.1 
1345 = -3.2 
The value of interaction 15 is not surprising as factors 1 and 5 are influencing. 
Factors 6 = 124 and 7 = 135 measure the effects of blocks. This explains the high values 
of interactions 124 and 135. The fertilities of the four plots were very different, and this 
difference can be shown in Figure 10.8 in which each corner of the square represents a plot and 
the response is the average harvest from each. 
135 
111 
-4 
60.1 51.5 
54.6 
-4 
IV 
B 
’ II 
124 
I 4 ,+ 
Figure 10.8: Differences in the fertility of the four plots. 
198 
TABLE 10.6 
YATES' BEAN EXPERIMENT 
Experimental matrix rearranged as four blocks using interactions 135 and 124 
- 
rrial 
no 
1 
26 
11 
20 
21 
14 
31 
8 
9 
18 
3 
28 
29 
6 
23 
16 
17 
10 
27 
4 
S 
30 
15 
24 
25 
2 
19 
12 
13 
22 
7 
32 
- 
- 
Factor 3 
nitrate 
;actor 4 
5. phos. 
;actor 5 
potash 
Lteraction 
135 
iteraction 
124 
199 
It is not easy to explain the high value of interaction 1345. It is aliased with interaction 
47. This may indicate that superphosphate (factor 4) does not have the same influence on 
blocks I11 and IV as it does on blocks I and I1 (factor 7). But this is just an assumption which 
could be verified if necessary. 
This analysis shows that: 
- Three factors influence the yield: 1, 2 and 5. 
- One interaction must be taken into account: 15. 
- The interactions representing the effects of blocks are large 
A Z3 design can be constructed ifwe consider only factors 1, 2 and 5 . As there are 32 
trials, this is equivalent to having run this design four times. Table 10.9 shows this 
interpretation. It is thus possible to enter the average responses into the experimental domain 
(Figure 10.9). 
TABLE 10.7 
YATES' BEAN EXPERIMENT 
Results for the three factors influencing yield, arranged by blocks 
I Trial number I I Factors and interactions I I Response I j 
21 29 
26 18 
31 23 
20 28 
- 
111 
5 
10 
15 
4 
17 
30 
27 
24 
- 
- 
- 
IV 
13 
2 
7 
12 
25 
22 
19 
32 
- 
- 
ji + - + 
- - + + 
+ - + - 
+ - - 
L I i I 
i + 
I 
I 
66.5 
45.7 
76.7 
70.5 
71.2 
74.3 
77.0 
73.3 
- 
- 
11 
56.7 
23.3 
74.8 
64 6 
48.0 
39.3 
73.7 
56.3 
- 
111 
68.0 
29.9 
60.8 
54 7 
63.6 
47.9 
63.6 
92.5 
- 
49 6 
60.5 
51.3 
I Effect I ( ~ 3 . 9 1 7 . 8 1 3 . 8 1 2 . 5 1 4 . 4 1 - 1 . 9 1 - 1 . 9 1 5 8 . 9 1 169.4154.6160.1151.51 
We can interpret these results as follows: 
When the distance between rows was great and no fertilizer is added, the yield was 
poor (34 Ib/plot). 
Almost the same improvement was obtained by reducing the distance between rows 
(57 Ib/plot), adding manure (60 Ib/plot), or adding potash (55 Ib/plot). 
200 
0 The yield could be increased still hrther by: 
- adding manure and planting the rows 18 inches apart. In this case potassium 
makes no improvement and may even be deleterious. 
- adding manure and potash and keeping the row spacing at 24 inches. In this case, 
a single fertilizer is insufficient: both are needed. 
66 71 
6 00) 
Potash 
0 
,-- ' 
~ 70 ,*-- 
55 
I 60 
{18)-+41 ~ 1 
Row Spacing 
Figure 10.9: Experimental results entered in the experimental domain to show that the 
effects are not additive. 
Yates could therefore make the following recommendations. 
Conclusion: 
Bean yield can be improved by f 
0 either reducing the distance between rows and using a single 
fertilizer, manure. il 
20 1 
k3 0 or spacing the rows 24 inches apart and using two fertilizers, Z 
The yields from these two growing methods are equivalent. The farmer 
must thus choose the most convenient andlor economical one. 
B manure and potash. 4 
6. BLOCKING OF A COMPLETE DESIGN 
One of the inconveniences of complete factorial designs is that all the trials must be run 
before the results can be interpreted. However, the investigator can sometimes use an elegant 
solution to satisfl his curiosity. For this, the complete design is divided into several fractional 
design and blocking is used. For example, if we wish to run a 25 design, we can divide it into 
four fractional 25-2 designs. This organisation has twoadvantages: 
We can calculate the contrasts at the end of the first 25-2 design to obtain an 
indication of the influence of the main factors. The second 25-2 design is then 
selected to dealias the interactions and main effects that contain ambiguities. 
Running the trials in this way also follows our original concept of the 
progressive acquisition of knowledge. 
The results of the first design may make it possible to avoid running the initially planned 
2’ design. Even if it becomes necessary to run the thirty-two trials, we will be able to more 
closely monitor the experiment and obtain partial results before completing the design. 
202 
RECAPITULATION 
1. The technique of blocking is analogous to that used for fractional designs. High 
order interactions are aliased with the blocking variable. The sign of this 
interaction divides the design into two half-designs: one with the - interaction 
signs and the other with + interaction signs. Alias theory applies to blocking. 
2. The Yates bean yield experiment shows that we can use the technique of 
blocking on two variables. This technique introduces two extra factors into the 
original study. In addition to five original factors, Yates studied the difference in 
the fertilities of four plots of land. The advantage of blocking is that the thirty 
two responses are used to calculate the effects of five factors without the 
differences in ground fertility corrupting the results. 
3. Blocking can be performed on any variable. As the alias theory developed for 
fractional designs can be applied to blocking, it is always possible to know how 
the effects and interactions are aliased with the blocking variables. 
4. The Yates' bean yield experiment also shows that the presence of non- 
influencing factors allows all the responses to be used to reconstruct duplicate 
or quadruple designs. This possibility is important because it shows that we 
should never initially plan to duplicate a design. It is better to study extra 
factors. 
5 . This chapter has shown how important it is to select the order in which trials are 
run. This must be carefully defined before beginning the experiment. If there is a 
risk that the responses may be affected by overall variations, the investigator 
must consider blocking. A specific order should be chosen if drift is suspected. 
We can even consider carrying out measurements at the central point of the 
experimental domain (or at another point if the central point cannot be used). 
Lastly, the trials should be randomised to transform small systematic errors into 
random errors. The three techniques of blocking, anti-drift and randomisation 
are partly compatible; the investigator should use them because they help him 
overcome systematic errors and obtain the lowest possible random error. 
6 . We saw in Chapter 4 that high order interactions could sometimes be considered 
as measurements of experimental error. The present chapter on the order of 
trials shows the influence of systematic errors on the results of the main effects 
and interactions. As a result, there is some risk in determining the experimental 
error by examining interactions. This method is usehl, but it must be applied 
with great care. 
CHAPTER 11 
M A T H E M A T I C A L M O D E L L I N G O F 
F A C T O R I A L 2 k D E S I G N S 
1. INTRODUCTION 
The designs that we have discussed in the preceding chapters and all the concepts that 
we have developed so far are based on a mathematical model. Although we have implicitly 
made use of this model, we have not yet explored its implications. Now it is time to lift the veil 
and examine the mathematical model underlying all that we have discussed so far. 
We will begin this chapter by outlining the mathematical model on which the simplest 
design is based, one-factor designs: 2l. This will allow us to identify the basic hypotheses and 
show how the average and effect of the studied factor are taken into account by the 
mathematical model. We will then examine the model for two- and three-factor designs, 22 and 
23, and see how interactions are expressed by the mathematical model. Lastly, we will extend 
the model to k factors. 
The mathematical model for a factorial design allows us to widen the field of application. 
We will therefore examine several applications of the model, each of which can give rise to 
important developments for all investigators. We will use several examples to clearly 
demonstrate the range of applications of the mathematical model. These complement and 
204 
extend the preceding chapters. It provides a deeper interpretation, more fruitful predictions and 
safer decisions on the directions of future research. The experimental results are better 
presented and the available information is fully extracted (wherever possible). 
2. MATHEMATICAL MODELLING OF FACTORIAL DESIGNS 
Let us assume that we need to study only one factor in order to solve a problem. We set 
the experimental points at levels -1 and +1, and we measure the corresponding responses: y, 
and y2 (Figure 1 1.1). 
But what happens between -1 and + I when the factor studied covers the whole variation 
interval? We have assumed that the change in the response is linear, Le., we have adopted a 
mathematical model with the form: 
y = a. + a,r 
where . y is the response and x is the level of the factor studied (it varies continuously from -1 
. and al are coefficients 
to +1 and can thus have all the values between these two limits). 
Y 
Y2 
YO 
Yl 
' Q 
X B 
-1 0 +I 
Figure 11.1: Factor x varies continuously between -1 and +1. The response y varies 
linearly with x. 
205 
The significance of and a, are readily seen. Let us apply the mathematical model to 
experimental point A (x = -1) we get: 
Y1 = a0 - a, 
If we do the same for experimental point B (x = +1), we get: 
Y2 = + a, 
8This gives us a system of two equations with two unknowns, and a,. 
Y , = a0 - a, 
Y2 = a0 + a1 
Solving this system for and a,, 
1 
2 ao = - [ + Y l + Y z ] 
a l = - [ - Y ~ + Y Z ] 1 
2 
We can see that: 
. . a, is the slope of the line PQ (Figure 11.1). But this latter relationship also defines the 
is equal to yo, the average of the two responses y1 and y2 . 
effect of the factor. Coefficient a, is thus the effect of the factor studied. 
We can write the mathematical model in a new form: 
y = I + E x 
where I is the mean of the responses and E is the effect of the factor studied. 
If two factors are studied, we assume that each of them acts linearly and additively on 
the response. If the two variables x1 and x2 are continuous, the mathematical model takes the 
following form when there is no interaction: 
y = a. + al xl + 3 x2 
and when there is interaction. the mathematical model becomes: 
y = ao+ a, x1 + 3 x 2 +aI2x1 x2 
where: 
.y is the response. . x, is the variation in the level of factor 1 between -1 and +1 
206 
. x2 is the variation in the level of factor 2 between -1 and + I . a,,,, al and aI2 are coefficients. 
What is the significance of these coefficients? When the experimenter carries out trial 
number 1 of a 22 design he sets x1 at - I , x2 at - I and measures the response y and finds y, . If 
this value is inserted in the mathematical model for a 22 design we get: 
The experimenter then runs trials 2, 3 and 4. He now has a system of four equations 
with four unknowns: 
Y4 - a0 + al + a2 + a12 
From which we get 
1 
4 
a0 = -[+h +4’2 +Y3 +Y4 1 
These relationships show that: 
. a,, is the mean 
al is the effect offactor 1 . is the effect of factor 2 . a12 is the interaction between 1 and 2 
The mathematical model for a 22 design can thus be written as 
Y ~ I + El XI + E2 ~2 + El2 XI ~2 
or using the Box notation 
207 
I' I + 1 x, t 2x2 + 12x1 x2 
It is thus particularly easy to produce a mathematical model from the results of a factorial 
22 design, because the model coefficients are given directly by using the effects and interaction.This modelling can apply to all Zk designs. The model for these designs includes: 
. a constant term, aa, which is the mean I of all the responses, . k coefficients for the factors, these coefficients are the main effects of the 
corresponding factors, 
. C: coefficients for the interactions of order q, these coefficients are the values of the 
interactions calculated from the effects matrix. 
The response for each trial may be written with reference to the 2k mathematical model. 
For a 23 design we have: 
.Y ~ I + El XI + E2x2 + E, x3 + E 1 2 X 1 x2 + E I ~ ~ I Xi + E23X2 X? + E123x1 x 2 X 7 
The mathematical model for 2k designs thus opens the way to a number of interesting 
applications, and we will examine examples of these. The model should be used whenever the 
investigator wishes to interpret experimental results with more than a simple table of effects. 
We will use four examples to examine these applications: 
Paste hardening (new example), 
Yield of a chemical reaction (see Chapter 2), 
Sugar production (new example), 
0 Yates' bean experiment (see Chapter 6). 
We will use these examples to: 
explain the formation of the effects matrix, 
evaluate the responses throughout the experimental domain without running 
new trials. 
0 test the validity of the linear model and, if necessary, to develop a more suitable 
model. 
0 select a working program for orienting the ongoing study (steepest ascent) 
towards the desired solution. 
0 select complementary trials for a fractional design and dealiasing certain 
interactions. 
compare factorial designs and analysis of variance. 
introduce residual analysis. 
0 find the error distribution over the response surface. 
208 
I 1 1 1 1 
El - - 1 xll x12 x14 
E2 n x21 x22 x23 x24 
E l 2 x11x21 x12x22 x13x23 x14x24 
- 
3. FORMATION OF THE EFFECTS MATRIX 
Yl 
Y2 
Y3 
Y4 
As the experimental points are at the limits of the domain, the factor levels have only the 
values -1 and +I . The experimental matrix indicates the levels assigned to each factor for each 
trial. The effects matrix is obtained from the design matrix by applying the signs rule. The 
model clearly shows this approach. 
Let us use a 22 design as an example, and write the system of equations as a matrix: 
Y = X E 
developing this condensed form, we get: 
I 
E l 
E 2 
El2 
where xi. is the level of xi for the jth trial. For example, x23 is the level of factor 2 in trial 
number 1. We can readily find the value of this level by examining the experimental matrix. In 
this case, x23 is equal to + I . 
We have seen that, for factorial designs, the X-' matrix, the inverse of X, is simply the X' 
transpose of X divided by the number of trials, n. We can write: 
1 ' 
n 
E=-X Y 
This relationship can also be developed: 
The mean I is obtained by multiplying the first line of the X' matrix by the Y matrix, or 
(as n = 4): 
1 
I = ~ [ + . Y I + ~ 2 + ~ 3 + ~ 4 ] 
The effect El of factor 1 is obtained by multiplying the second line of the X' matrix by 
the vector matrix Y: 
209 
When the are replaced by their numerical values, i.e., by the levels of factor 1 in the 
experimental design, we have 
XI, = - 1 XI2 = + I XI?= -1 XI3 = +1 
hence: 
The effect E2 of factor 2 is obtained in the same way, by multiplying the third line of X‘ 
by Y and replacing xij by their numerical values: 
E2 = -[-4’l 1 -1’2 fY3 +y4I 4 
Lastly, El? is obtained by multiplying the fourth line of X’ by the elements of Y and 
giving the xi, their numerical values: 
One of the advantages of using the matrix form is that it combines all the relationships in 
a single formula. 
We can also see that the product of the levels of the two factors, 1 and 2, are shown in 
the X‘ matrix, and that this product is taken into account in calculating the interactions.The 
levels x, and x2 take the values -1 and +1, and the product xIx2 is either -1 or + 1 , the 
interaction signs. This satisfies the signs rule that we have used to establish the interaction 
signs. 
4. EVALUATION OF RESPONSES THROUGHOUT THE 
EXPERIMENTAL DOMAIN 
The experimental points were placed at the limits of the domain, but the mathematical 
model may be used to calculate y for any value of x. If we assume that the model is valid when 
the factors vary fi-om -1 to +1, we can calculate responses for all points within the domain. All 
the responses make up the response surface, and it is possible to plot isoresponse curves on the 
experimental domain. The following example of paste hardening shows how the mathematical 
model can be applied. 
210 
Level (-1 15°C 0 1 Yo short 
Level (+) 25°C 0 5 % long 
4.1. 
The problem: 
Example: study of paste hardening 
6 months 
a week 
A paste must be usable for at least one hour after the tube is 
opened. Certain tubes are known to contain paste that hardens in 30 
minutes, i.e , much too fast. The person in charge of this study must # 
: provide instructions such that clients can be sure of having at least 60 8 
g minutes to work the paste before it becomes too hard 
Factors 
The experimenter assumes that the following factors are among those that influence the 
usable time: 
Factor 1 : ambient temperature. - Factor 2: water content. . Factor 3 : mixing time during manufacture . Factor 4: time in storage. 
TABLE 11.1 
EXPERIMENTAL MATRIX 
STUDY OF PASTE HARDENING 
Trial no remperature 
1 
- 
+ 
- 
+ 
- 
+ 
- 
+ 
Water cont. 
2 
Mixing time 
3 
- 
~ 
- 
- 
+ 
+ 
+ 
+ 
Storage 
4= 123 
Response 
33 
68 
21 1 
Response 
The response is the time (in minutes) required for the paste to reach a defined 
consistency. The error of the response is +2 minutes. The experimenter decides to use a 24-' 
design with I = 1234 as alias generator. The experimental conditions and the responses are 
given in the design matrix (Table 1 1 . 1 ) . 
4.2. Interpretation 
The calculated effects are shown in the table of effects, and the experimenter estimates 
that these results are sufficient, so that no extra trials are required. Only two factors are 
influencing, water content (2) and storage time (4), and there is a strong interaction between 
them. Factor 1 has only a slight influence, and can be neglected. 
As the error of the response is k 2 minutes, the error of the effects is k 2& = -f 0.7 
minutes. 
TABLE 11.2 
TABLE OF EFFECTS 
STUDY OF PASTE HARDENING 
Mean 
1 
2 
3 
4 
12 + 34 
13 + 24 
14 + 23 
60.4 k 0.7 minutes 
-1.4 i 0.7 minutes 
-9.9 k 0.7 minutes 
0.4 k 0.7 minutes 
14.4 k 0.7 minutes 
-0.6 i 0.7 minutes 
5.1 k 0.7minutes 
-0.4 -f 0.7 minutes 
The mathematical model is easily written, but the experimenter can choose one of several 
solutions, depending on the factors selected and the way in which the results are rounded off 
Without rounding off and keeping all the factors, 1 , 2 and 4 plus interaction 24, the model is: 
y = 60.4 - 1.4 XI - 9.9 ~2 + 14.4 ~4 + 5.1 XZ ~4 
Rounding off the numbers to the nearest half-minute gives: 
J '= 6 0 . 5 - 1 . 5 ~ l - 1 0 ~ , + 1 4 . 5 ~ ~ + 5 ~ ~ ~ ~ 
Eliminating factor 1 which has a slight influence gives: 
2 12 
J = 60.5 - l o x * + 1 4 . 5 ~ , + 5 ~ , ~ , 
We will use this model to produce a graphical representation of the results. As there are 
now only two factors, the experimental domain becomes a square. The isoresponse curves for 
y can be projected onto this square to give the isoresponses. The response values vary from 3 1 
to 80 minutes, and we can draw isoresponse curves for 35, 40, 45 min., etc. From this, we can 
simply read off the setting time for the paste for a given water content and storage time (Figure 
11.2). 
STORAGE 
TIME 
(MONTH) 
0.1 0.3 0.5 
WATER CONTENT 
Figure 11.2: Changes in paste setting time as a function of water content (2) and storage 
time (4). 
The isoresponse curves are segments of a hyperbola when there is an interaction and 
straight lines when there is no interaction. 
Conclusion: 
The experimenter can use the resultsdiagram to inform the 
Management of the criteria to be used for policy selection 
. If they wish to impose no constraint on fabrication 
d (increased costs) by allowing the water content to rise to 0 5%, the 
tubes should carry a use-by date. tubes that have been in stock for 
over a month and a half will have working times of less than 1 hour 
. If production constraints can be imposed to keep the 
water content below 0 3%, the storage time can be extended to 3 
months 
I- 
213 
. The acceptable storage time will be 4.5 months at a i~i 
water content of 0.2%, and 6 months for a 0.1 % water content. 
d Given this technical knowledge, the final decision will be based on 4 
9 commercial and economic criteria, according to the industrial strategy Y 
& of the Company j , 
5. TEST OF THE MODEL ADOPTED 
Let us stay with the example of paste hardening and use it to illustrate this application of 
the mathematical model of factorial designs. 
The experimenter had run eight trials and is sure that the response surface lies close to 
the experimental values, i.e. close to the points at the extremes of the domain. He assumes that 
responses corresponding to all the other points within the domain could be calculated using a 
mathematical model in which the factor effects are linear and additive. The validity of this 
hypothesis, and the model derived from it, must be checked. He does this by running 
experimental points within the domain and comparing the measured response to the response 
calculated from the model. The validity of the model can be conveniently checked by running 
trials at the centre of the experimental domain. In the paste hardening example, the 
experimenter runs a trial with the temperature set at 20°C, water content at 0.3% and uses a 
paste that has been stored for 3 months. He obtains a hardening time of 62 min. 
If we compare this value to that given by the model - 60.5 minutes - we see that there is 
good agreement given the error of the response. The model is therefore valid. 
If the experimenter had found a value very different from the model mean, i.e differing 
by several standard errors, he would have to: 
. either question the measurements at the centre of the domain. This is why he generally 
carries out not just one, but two or three measurements at this point. . or question the model adopted. In this case he must consider another more 
complicated model, e.g., a model in which factors are of second degree or a more 
complex mathematical fimction. We will not go into this extremely important topic 
here, but this is the logical extension of factorial designs in the progressive acquisition 
of knowledge. 
6. SELECTION OF A RESEARCH DIRECTION 
We can illustrate this application by going back to the first example we studied, the yield 
of a chemical reaction (Chapter 2). The yield of this reaction depends on two factors, 
214 
Trial no Temperature 
1 -1 
2 +1 
3 -1 
4 + I 
temperature and pressure. The limits of the experimental domain, the design matrix and the 
trial results are shown in Table 1 1 . 3 . 
Pressure 
-1 
-1 
+1 
+ I 
Level (+) 
60 % 
80 % 
70 Yo 
90 Yo 
80°C 2 bar 
Interpretation of the results produces the following table of effects: 
TABLE 11.4 
TABLE OF EFFECTS 
THE YIELD OF A CHEMICAL REACTION 
Mean 75% 
1 5% 
2 1 0% 
12 0% 
We can use these results to set up a mathematical model and draw the isoresponse curves 
in the experimental domain. 
215 
6.1. Mathematical model 
Using coded variables, the temperature xl varies from -I to + I , as does the pressure x2. 
The yield y is then given by: 
v = 75+5X l+ IOX2 
It is sometimes convenient to use normal values of temperature and pressure (degrees 
Celsius and bar) for the interpretation. The relationships between coded variables and normal 
variables are. 
0 = 0,) + (Step,) x1 
P = Po + (Step,) x.2 
where 
- 0 is the temperature in "C it varies from 60°C to 80°C 
.6, is the mean temperature in "C at the mid point, 
0, = 70°C 
xI is the temperature measured as a coded variable: it varies from - 1 to + I 
- Step, is the step selected for converting normal units to coded units; the temperature 
step is 10°C 
. p and po are the pressures measured in bar. p varies from 1 to 2 bar and po is 1 5 bar. 
. x2 is the pressure measured in coded units; x2 varies from -1 to + 1 
Step, is the pressure step, 0.5 bar in this example 
Substituting numerical values in the above equations gives: 
8 = 7 0 + l o x l 
p = 1.5 + 0.5 x.2 
or 
1 
XI = -8 -7 
10 
216 
Introducing these values into the model equation gives a relationship in which the yield p 
is a hnction of temperature in "C and pressure p in bar: 
1 
2 
p = 1 0 + -0 +20 p 
This relationship is valid in the experimental domain studied 
6.2. Isoresponse curves 
Once we have checked the validity of the model by comparing measured and calculated 
values at the centre of the experimental domain, we can draw the isoresponse curves. 
If we now want to know how to alter the temperature and/or pressure to approach a 
100% yield, we must leave the experimental domain. We are thus obliged to develop 
hypotheses which must be later verified. Let us assume that the model remains valid outside the 
experimental domain. We have the greatest chance of finding a 100% isoresponse in a direction 
perpendicular to the isoresponse lines within the experimental domain (Figure 11.3). We can 
even draw 95% and 100% isoresponse curves and calculate the pairs of temperature/pressure 
points which could give a 100% yield. There is an infinite number of solutions. The 
experimenter must choose those which are compatible with the constraints of his installation or 
products, and which permit him to attain his aim at the lowest cost. 
Let us assume, for example, that the temperature cannot be increased, but that the 
installation can withstand a pressure of 2.75 bar. It is then easy to calculate possible 
experimental points: 
for 0 = 80°C 
1 
2 
100 = 10 + - 80 + 20p 
p = 2.5 bar 
for 0 = 70°C 
1 
2 
100 = 10 + - 70 + 20p 
p = 2.75 bar 
The experimenter can thus identifl the points giving him the best chance of success. He 
must, however. check the hypotheses adopted by running trials. 
217 
2 bar 
PRESSURE 
1 bar 
60°C 80°C 
TEMPERATURE 
Figure 11.3: lsoyield curves for the chemical reaction example 
6.3. Steepest ascent vector 
The reader will have noticed that, in the preceding example, yields increased in a 
direction perpendicular to the isoresponse lines. This point is important, and this direction is 
given by a vector, the steepest ascent (V). The projections of V along the axes 0 x1 and 0 x2 
are v , and v2. 
The general equation for isoresponse curves is: (setting the value ofy constant). 
or 
This is the general equation for a straight line and the coefficients of x1 and x2 are the 
direction cosines of the straight line which is at right angle to the isoresponse curve. E, and 
E2 are therefore, allowing for a proportionality coefficient K, equal to the direction cosines of 
the steepest ascent vector. This is only true when the unit of measure is the same on the two 
axes. This shows the importance of coded variables. We have: 
218 
+I 
v, =I 
Figure 11.4: Construction of the steepest ascent vector. 
For the chemical reaction yield example, we have: 
orwith K =0 .2 
We will now see how the steepest ascent vector is constructed (Figure 1 1 4). The 
relationships giving the values of the components of V are only valid for coded variables, the V 
vector must therefore be constructed retaining these units on the factor axes. In the present 
case, axis x1 is one coded temperature unit, so v1 =. 1 and two coded pressure units on axis x2, 
or v2 = 2. The steepest ascent vector V is thus readily constructed. 
It is useful to return to the original variables when presenting results or calculating new 
experimental points. But with the original variables we must always rememberthat the units on 
the temperature and pressure axes are no longer the same. The coefficients of variables 8 and p 
in the isoresponse line equation are no longer the direction cosines of the steepest ascent 
vector. This equation therefore cannot be used to establish the direction of V. The coded 
variable units must be retained to obtain the direction cosines which are then transformed to 
the original units. We therefore multiply the values of projections v I and v2 by the step of the 
corresponding coded variable. Thus: 
v1 = K El (stepH) 
or 
219 
and 
or 
$ 1 , = K 5 x 10 = 50 K in degrees Celsius 
v2 = K E2 (step,,) 
v2 = K 10 x 0.5 = 5 K inbar 
But as the choice of K is arbitrary, with K = 0.2 we have: 
I), = 0.2 x 50= 10°C 
vz = 0.2 x 5 = 1 bar 
This indicates that the temperature 6 must be increased by 10°C and the pressure p by 1 
bar simultaneously to move along the steepest ascent (Figure 1 1.4). 
This relationship for two factors can be extended to any number of factors. For three 
factors, the isoresponse surfaces are planes, and the steepest ascent vector is perpendicular to 
these planes. This vector indicates the direction in which the responses increase (or decrease) 
most rapidly. For four factors, the isoresponse surfaces are hyperplanes in a four-dimensional 
space, the normal to this hyperplane is defined as above and the steepest ascent vector is 
defined by four components. 
The isoresponse hyperplanes for k factors have a steepest ascent vector with k 
components. These components may be expressed in coded variables or in normal variables. 
When coded variables are used, the components of the steepest ascent vector V are, 
within an arbitrary constant, the effects of the corresponding factors: 
L’k = K Ek 
When normal variables are used, the components of the steepest ascent vector V are, 
within a arbitrary constant, the effects of the factors multiplied by the step chosen for each of 
them when coding the variables 
v1 = K E, (step,) 
v2 = K E2 (step2) 
vi = K El (stepl) 
vk = K Ek (stepk) 
It is thus possible to calculate the direction in which there is the greatest chance of 
improving the results, for any number of influencing factors. 
220 
7. CHOICE OF COMPLEMENTARY TRIALS 
There are generally ambiguities that remain to be resolved when a fractional design is 
interpreted. This can be done either by running a complementary design, or simply by running a 
few extra trials. The choice of these extra trials and the way in which the calculations are done 
depends on alias theory and on the mathematical model for the factorial designs. The following 
chapter (Chapter 12) is devoted to this question. 
8. ANALYSIS OF VARIANCE AND FACTORIAL DESIGNS 
In this section we will analyse a single set of data by two methods: factorial design and 
analysis of variance. This will allow us to compare the results and recognize analogies between 
these two techniques for interpreting data. Let us first assume that the experimenter has only a 
single response per experimental point. In this way we will develop a formula illustrating the 
similarity between the two methods. We will then assume that the experimenter has two 
responses per experimental point, These results will be used to calculate a value for the error of 
the effects. A comparison of the results will show that the two methods are identical. A new 
example, sugar production, will be used to examine this problem. 
Example: Sugar production 
The problem: 
The weights of sugar obtained using two treatments, treatment A 
and treatment B, are measured while varying the temperature between 
5°C and 15°C. The investigator wants to know the conditions providing 
the greatest yield of sugar. 
8.1. Analysis of the problem by factorial design (one response per trial) 
experimental data and the results are shown in Table 1 1 . 5 . 
Factor 1 is the type of treatment and factor 2 is the temperature. A 22 design is run. The 
22 1 
Trial no Treatment Temp. 
1 2 
.- - I 
2 + 
3 - 
4 + f 
- 
+ 
TABLE 11.5 
Interaction 
12 I 
+ + 
+ 
+ 
+ + 
~ 
- 
Level (-) 
Level (+) 
Response 
125 
198 
142 
B 5°C 
A 15°C 
Effect -8.5 28 -19.5 142 
Factor 1 has a negative effect, i.e., treatment B gives a greater yield than treatment A 
(Figure 11 5 ) 
SUGAR 
(Grams) 
150.5 
142 
131.5 
-1 0 +1 
B) 
- TREATMENT 
i a \I 
Figure 11.5: Effect of treatment type on sugar production. 
222 
Factor 2 has a positive effect, i.e., increasing the temperature favours sugar production 
(Figure 1 1.6). 
SUGAR 
(Grams) 
170 
142 
114 / 
-1 +’ TEMPERATURE 
5 o c 15 o c 
Figure 11.6: Effect of temperature on sugar production. 
And there is a very strong interaction between factors 1 and 2 -19 5 grams (Figure 
1 1 7) 
198 142 
15 O C 
lb 
b 
103 125 
0 
Treatment 
Ba ,A 
Figure 11.7: Influence of treatment and temperature on sugar production. 
223 
I 
Conclusion: 
B A Mean 
I 
iii The investigator chooses the conditions giving the best yield 
3 treatment B and a temperature of 15°C These settings take advantage 
of the strong interaction between the two factors 
15°C 198 TEMPERATURE 
8.2 Analysis of the problem by analysis of variance (one response per trial) 
142 170 
The same trials were run, treatments A and B were both run at 5°C and 15°C. The 
responses, given in Table 1 1.6, show: 
5°C 
- The means for each treatment are: 150.5 and 133.5. 
- The means at each temperature are: 170 and 114. 
- The mean of all results. or the overall mean is: 142. 
103 125 114 
TABLE 11.6 
ANALYSIS OF VARIANCE 
SUGAR PRODUCTION 
Non-duplicated design 
where 
. c y : is the sum of the squares ofthe responses 
C f = (198)’+(142)* +(103)2+(125)2 = 85 602 
227 
2. Hence the mean variance of the effects is: 
2 1 2 1 CTE = -Oy, = - 35 
n 8 
3 . and the standard deviation of the effects is: 
The calculated effects and interaction are therefore significant because they are several 
times the standard deviation, For example, for temperature we have: 
TABLE 11.8 
EXPERIMENTAL DESIGN 
SUGAR PRODUCTION 
Duplicated design 
Trial no 
4 
First 
result 
108 
120 
194 
I44 
Second 
result 
98 
130 
202 
140 
198 
142 
Deviation Variance Fi 
8.4 Analysis of the problem by analysis of variance (two responses per trial) 
We can carry out an analysis of variance on the eight responses by calculating the sums 
of squares from the table of results (Table 1 1.9) and applying the analysis of variance formula. 
The analysis of variance formula contains an extra term to allow for the duplicated trials. 
CYt = Y , Y 
228 
TABLE 11.9 
ANALYSIS OF VARIANCE 
SUGAR PRODUCTION 
Duplicated design 
TEMPERATURE 
15°C 
5°C 
TREATMENT 
202 140 
Mean 150.5 133.5 142 
Numerical calculations give the following values: 
c y z = 171344 
c”- J -161312 
c(+yl - y ) 2 =578 
2 
z(j70 - y ) = 6272 
x(j-jo - J T +y,) = 3042 2 
c(j7, - y , ) 2 = (198-194)2 +(198-202)2 +(142-144)2 +(142-140)2 
(103-98)2 +(103-108)2 +(125-120)2 +(125-130)2 
We thus have all the elements required to construct the analysis of variance table (Table 
11.10). 
229 
Variance due 
to 
mean 
treatment 
temperature 
interaction 
dispersion 
Total 
TABLE 11.10 
ANALYSIS OF VARIANCE TABLE 
SUGAR PRODUCTION 
Duplicated design 
Sum of 
Squares 
161312 
578 
6272 
3042 
140 
Degrees of 
Freedom 
171344 I 8 
Mean 
Squares 
161312 
578 
6272 
3042 
35 
I 
Mean Squares computed 
with the effects 
8 x (1 42)2 
8 x (28)2 
8 x (19.5)2 
8 x (8.5)2 
The significance of a mean square is generally evaluated as the ratio of the mean square 
itself to that of the response dispersion. If the ratio is large, then the mean square is significant. 
For an experimental design, this involves comparing the mean variance of the effects (obtained 
by duplicating the trials) to the square of the effects themselves, the ratio: 
E? 
0; 
__ 
In order to understand the similarity between analysisof variance and experimental 
designs, let us look the effect E, of temperature. The mean square, derived from the 
temperature variations, is 6272, or eight times the square of the temperature effect E,. 
6272 = 8x(28) 2 = 8xEi = nEi 
The dispersion of responses gives a mean square of 35 which is, in reality, the mean 
variance 0: of the responses. As there are eight responses for calculating an effect, the 
variance of the effects 0; is given by: 
230 
The ratio of the mean squares is again the comparison of the square of an effect to the 
square of the error of the effect: 
If the errors have a normal distribution, this ratio follows Fisher's law, and there are 
tables showing the probability that the effect is significant. If the value of F from the table is 
high, the effect is significant, otherwise it is not. 
We can also take the square root of this ratio and use Student's t test to estimate the 
probability that an effect is significant. The effect is compared directly with its standard error. 
Applying this to the temperature, we have: 
3 = 1 3 . 3 
(JE 
This value is the same as the one we calculated by the experimental design method 
9. INTRODUCTION TO RESIDUAL ANALYSIS 
The mathematical model for experimental designs focuses on synthesising trial results. 
The information in the results has been transformed into a mathematical formula. Even if the 
investigator decides that the model is valid, all the information in the trial results may not be 
entirely expressed by the model. Any information that remains to be extracted from the 
experimental data is contained in the residuals. But what are residuals? A residual ri is the 
difference between the measured value of a trial y , and the value calculated from the model y,. 
We can see how residuals are used by examining the Yates' bean growing experiment. 
We will see that the choice of mathematical model is not without consequence, and that the 
conclusions can depend on this choice. But the choice is not automatic and it is the investigator 
who must decide. He must take great care to choose the model that best reflects the 
phenomenon studied. We will examine two models ( 1 and 2). The residuals for these two 
models are shown in Table 1 1.1 1. 
23 1 
TABLE 11.11 
Trial no 
I 
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 
YATES' BEAN GROWING EXPERIMENT 
Calculation of residuals for model 1 and 2 
neasured 
value 
66 5 
36 2 
74 8 
54 7 
68 0 
23 3 
67 3 
70 5 
56 7 
29 9 
76 7 
49 8 
36 3 
45 7 
60 8 
64 6 
63 6 
39 3 
51 3 
73 3 
71 2 
60 5 
73 7 
92 5 
49 6 
74 3 
63 6 
56 3 
48 0 
47 9 
77 0 
61 3 
Model 1 
Calculated 
Value 
55.62 
39.08 
71.32 
54.78 
55.62 
39.08 
7 1.32 
54.78 
55.63 
39.08 
71.32 
54.78 
55.62 
39.08 
71.32 
54.78 
54.48 
55.42 
70.18 
71.12 
54.48 
55.42 
70.18 
71.12 
54.48 
55.42 
70.18 
71.12 
54.48 
55.52 
70.18 
71.12 
Residue 
10.88 
-2.88 
3 -48 
12.38 
-0.08 
-15.78 
-4.02 
15.72 
1.08 
-9.18 
5.38 
-4.98 
-19.32 
6.62 
9.82 
9.12 
-10.52 
-16.12 
-18.88 
2.18 
16.72 
5.08 
3.52 
21.38 
-4.88 
18.88 
-6.58 
-14.82 
-6.48 
-7.52 
6.82 
-9.82 
Model 2 
Calculated 
Value 
66.07 
3 1.63 
67.07 
56.03 
56.87 
34.83 
63.87 
65.23 
51.37 
40.33 
81.77 
47.33 
48.17 
49.53 
72.57 
50.53 
55.73 
51.17 
62.73 
81.57 
64.93 
47.97 
65.93 
72.37 
47.03 
65.87 
71.43 
66.87 
50.23 
56.67 
80.63 
63.67 
Residue 
0 43 
4 57 
7 73 
-1 33 
11 13 
-11 53 
3 43 
5 27 
5 33 
-10 43 
-5 07 
2 47 
-11 87 
-3 83 
- 1 1 77 
14 07 
7 87 
- 1 1 87 
-11 43 
-8 27 
6 27 
12 53 
7 77 
20 13 
2 57 
8 43 
-7 83 
-10 57 
-2 23 
-8 77 
-3 63 
-2 37 
232 
Model 1 
We have seen that only three factors and one interaction have major effects 
. row spacing ( I ) -3.9 
. interaction (1 5) 4.4 
.manure (2) 7.8 
.potash (5) 3.8 
The overall mean is 58.9, and we can write the equation for model 1 as follows: 
y = 58.9 - 3.9 x1 + 7.8 ~2 + 3.8 xg + 4.4 XI xg 
We can use this model to calculate all the responses for the thirty two trials and obtain 
the residuals (Table 1 1.1 l), i.e., the differences between the yields actually measured and those 
calculated from the model. If this difference is positive, the yield was better than that predicted 
by the model. The significance of these differences can be appreciated by entering them in the 
area of the corresponding trial (Figure 11.8) We can now see that almost all the positive 
differences lie around a continuous band of ground. So there are two parts in this plot of land: 
a high fertility area and a low fertility area. 
Figure 11.8: Analysis of residuals reveals a high fertility zone when model 1 is used. 
233 
So, studying the residuals has revealed hidden information that was not apparent from 
analysing the effects and interactions. 
Model 2 
But Model 1 does not take into account the effects of blocking, and we can discover 
whether there are high fertility zones by studying the residuals obtained with a second model 
that allows for variations in fertility between blocks. We must add the terms for the interactions 
124, 135 and 2345, which are linked to differences in fertility between blocks. Model 2 can be 
written: 
y = 58.9 - 3.9 XI + 7.8 ~2 + 3.8 ~5 + 4.4 XI ~5 - 5.8 ~ 1 . ~ 2 x4 - 3 . 1 XI ~3 xg + 1.5 12 ~ 3 . ~ 4 x5 
The residuals are calculated in the same way as before and entered on the ground plan in 
the plots for each trial (Figure 1 1.9). Block I1 does not seem to uniform and there is a band of 
high fertility running through blocks I1 and 111. This more detailed analysis reveals a high 
fertility area. If the investigator wishes, he could carry out further research to explain this 
phenomenon, which may be due to a band of different soil or an unsuspected layer of subsoil 
water. 
Figure 11.9: Analysis of residuals reveals a stripe of high fertility when model 2 is used. 
234 
10. ERROR DISTRIBUTION 
In a 22 design, the response surface is defined by the following relationship: 
YPaf )+a ,x l+a2~2+a12XlX2 
The coefficients 3 in this relationship are equal to the effects and interactions. They are 
thus known with a certain imprecision. These errors of the model coefficients influence the 
calculated response y. The response is therefore affected by an imprecision which we can 
evaluate. We assume that the levels xi are accurately determined and introduce no error. 
The surface is defined with a margin of error that must be determined and which, as we 
will see, is not the same throughout the experimental domain. Let us apply the variance 
theorem to the response surface: 
We can now calculate each variance of the right hand side, remembering that the error of 
the measured response o,, is assumed to be the same throughout the experimental domain. In 
order to calculate the variance of coefficient a, as a hnction of the error of each response, we 
must write the relationship defining 
a. = - [ + ~ 1 1 + ~ 2 + ~ 3 + ~ 4 1 n 
and apply the variance theorem 
If we assume that the error is the same for all the measured responses, we can simplifL 
this relationship as follows: 
or by changing the notation 
23 5 
1 . 
n 
V(ao) = - 0; 
We can calculate the other variances in the same way, remembering that the xi are 
constants which introduce no error. 
2 1 2 V ( a , x , ) = x, v ( a l ) = x: 
v ( a 2 x2) = x;v(a2) = x2 2 1 -0 2 
n y 
Entering these values in the variance equation gives the response variance calculated 
from the mathematical model: 
v(y) = -Oy 1 2 + X I 2 1 -Oy 2 + x2 2 1 -0; + x1 2 2 1 x2 ,Gr 2 
n n n 
1 
n 
v(y) = -0; [I+ x: + x; + x:.;] 
and if we make 
f 2 ( x ) = [l+x;+x;+x:x;] 
we obtain 
The function f2(x) varies with the values of xi, hence the error of the response calculated 
from the model also varies and depends on the coordinates of x, and x2. The levels of these 
factors vary from -1 to +l ; the hnction f 2(x) thus varies from 1 to 4.it is minimal when x, 
and x2 are zero, i.e. at the centre of the domain. Table 1 1.12 shows the values o f f (xi and the 
position of the points where this hnction is constant within the experimental domain are shown 
in Figure 1 1.10. We can see that the responses calculated from the model become less and less 
precise with their distance from the centre of the domain. 
23 6 
f 2(x> I 1 2 1.5 2 3 
f (4 1 1 09 1.22 1.41 1.73 
TABLE 11.12 
4 
2 
0 
f (x)= 1.41 ’ b 
f(x) = 1.22 * ’ 
In the paste-hardening example the standard deviation of the responses was estimated as 
& 2 minutes. Eight trials were run. If we apply the above formula, we get: 
Xl 
\ 
/ 
1 4 1 
n 
v(y) = -D; [I+ x; + x4‘ + x:xqz] = - 8 f 2 (x) - 2 f 2 (x) 
a 
The standard deviation of the responses calculated from the mathematical model,oyc, is 
the square root of this variance: 
1 
0% - - f (x ) - f i 
We only need to divide all the values of f(x) by fi to know the confidence we can have 
Figure 1 1.10 shows the standard deviation curves cYc of the responses calculated for the 
paste hardening example. These deviation curves can be superimposed on the isoresponse 
curve network. 
in the model for the paste hardening example. 
f(x) = 2.0 - T x2 
Figure 11.10: The precision of calculated responses is not the same throughout the 
experimental domain. It is best at the central point. The further from 
this point, the less accurate the model. 
237 
RECAPITULATION 
1. The mathematical model associated with factorial designs is a first degree polynomial 
for each of the factors taken independently. 
0 The effect of a factor is assumed to add algebraically to the effects of other 
factors. 
0 The mathematical model for factorial designs is established with coded 
variables. The polynomial coefficients are thus simply the mean, main effects 
and interactions. 
0 The model is valid for continuously varying variables. 
The yield of a chemical reaction example has provided us with formulae which 
can be used to go fi-om values in coded units to values in the more usual 
physical units, and vice versa. 
The sign rule is used to establish the + and - sign columns for the interactions 
derives from the mathematical model for factorial designs. 
2 . The paste hardening example showed that, despite the fact that the trials were run at 
the extremities of the domain, they provide predictions for the whole of the 
experimental domain. 
The validity of the model must be checked. Supplementary trials should be run, 
if possible, at the centre of the experimental domain. The calculated and 
measured responses at this point are then compared. 
We have also used this example to show how the mathematical model can be 
used to draw isoresponse curves within the experimental domain, or even 
outside it. 
3 . The main effects of factors are the direction cosines of the steepest ascent vector 
(coded values). 
4. Isoresponse curves and the steepest ascent vector can be used to predict the regions 
in which there is the greatest likelihood of success. Confirmatory experiments are 
required to verify the assumptions made. 
5. The sugar production example revealed the analogies between analysis of variance 
and factorial designs: the same mathematical model, same results, and the same way 
of determining significant effects. These similarities are summarized in the formula: 
YtY = n E'E 
The main inconvenience of analysis of variance is that this method uses squares: 
the signs are lost and comparisons made difficult. Factorial designs give the 
effects themselves, together with their signs, making interpretation much easier 
23 8 
6. Residuals analysis is used to extract information still contained in the responses after 
model-fitting. Interpretation is often delicate and relies on the good sense and 
intelligence of the investigator. 
7. The mathematical model does not have the same precision throughout the 
experimental domain. It is most accurate at the central point. 
CHAPTER 12 
C H O O S I N G 
C O M P L E M E N T A R Y 
T R I A L S 
1. INTRODUCTION 
In the preceding chapters we have seen that a problem is first studied by testing several 
factors using a fractional experimental design. But this approach has the disadvantage of 
providing contrasts in which the effects are aliased. This results in ambigpities which must be 
resolved by carrying out more trials. The setting up of the spectrofluorimeter example showed 
how a complementary design was constructed to dealias the contrasts giving difficulty. It is 
sometimes possible to run just a few extra trials rather than a complete complementary design. 
This chapter shows how to make such a choice. Any doubts remaining after the initial 
fractional design can be eliminated by running one, two, three or four extra trials. 
240 
2. A SINGLE EXTRA TRIAL 
Example: Clouding of a solution 
The problem: 
ti 
-r; study were: 
The experimenter wishes to know what is causing a slight cloudiness # 
in a solution containing several components. The factors chosen for 
. Factor 1: temperature. 
+. . Factor 2: product A. 
Factor 3: product B. 
. Factor 4: stirring speed. 
3 The response is an index of opacity which accurately reflects the 
9 way in which the cloudy appearance of this solution varies with the I 
F factors studied. 
The experimenter has carried out a fractional Z4-' design using I = 1234 as alias 
generator. The contrasts are therefore: 
h, = 1 + 234 
h,= 2 + 134 
h,= 3 +124 
h4= 4 +123 
I , , = 12 + 34 
h , ,=13+24 
3Llq = 14+ 23 
h = I +1234 
24 1 
TABLE 12.1 
EXPElUMENTAL MATRIX 
CLOUDING OF A SOLUTION 
Response 
17.0 
The contrasts are calculated from the experimental results and entered in the table of 
effects (Table 12.2) 
TABLE 12.2 
TABLE OF EFFECTS 
CLOUDING OF A SOLUTION 
Mean 
1 
2 
3 
4 
12 + 34 
13 + 24 
11.01 
3.86 
1.96 1 
0.34 
14 + 23 0.34 
242 
Product B 
3 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
There are two influencing factors. 
Stirring Spd 
4 = - 123 
+ 
- 
- 
+ 
- 
+ 
+ 
- 
. Temperature : factor 1 
.Product B : factor3 
Level (-) 
Level (+) 
We can see that the sum of interactions 12 + 34 is large. Which is larger, 12 or 34? To 
find out, we must dealias 12 from 34. The design chosen (I=1234) gives the contrast: 
15°C 0 Yo 0 Yo I00 rpm 
30°C I Yo 0.5 Yo 300 rpm 
h,, = h,, = 12 + 34 
We must find a trial which gives 
h',, = h ' 3 4 = 12-34 
This trial is in the complementary design I = -1234 (equivalence relationship), and was 
therefore not run during the first set of trials. Table 12.3 shows the eight possible trials. 
TABLE 12.3 
EXPERIMENTAL MATRIX 
CLOUDING OF A SOLUTION 
Trial no 
9 
10 
I 1 
12 
13 
14 
15 
16 
remperature Product A 
1 l 2 Respo r 
If we assume that only influencing factors are 1 and 3 and the influencing interactions are 
12 and 34, the mathematical model of the responses from this design is given by the formula: 
243 
yi = 1 + 1 + 3 f ( 1 2 - 3 4 ) 
The difference 12 - 34 can be determined using any of the trials in Table 12.3, e.g., the 
easiest one to run under the particular experimental conditions, 
Let us assume that the experimenter has chosen trial number 10. The response y,, is 
obtained when factor 1 is at the high level (+) and factor 3 at the low level (-), The 
mathematical model gives the value of this response as: 
ylo = l + l - 3 - ( 1 2 - 3 4 ) 
The numerical values of 1, 1 and 3 were calculated from the initial design and the value 
ofy,, was determined by the extra trial. 
I = 11.01 
1 = 4.34 
3 = 3.86 
ylo = 13.03 
We get, 
13.03 = 11.01 + 4.34 - 3.86 - (12 - 34) 
or 
12 - 34 = -1.54 
The first set of eight trials gave: 
12 + 34 = 1.96 
and hence the system: 
12 + 34 = +1.96 
12 - 34 = -1.54 
adding this two equations 
12 = 0.21 
and subtracting them: 
34 = 1.75 
Interactions 12 and 34 were dealiased and we can conclude that interaction 34 makes the 
greatest contribution to 12+34.244 
The extra trial was not run at the same time as the eight trials of the initial design. It 
could thus produce a distortion due to the fact that the non-controlled factors were set at 
different levels. This then results in a change in the mean of the mathematical model of factorial 
designs. When we set up the system of equations to calculate 12 and 34, we assumed that the 
mean I was the same as that of the initial trials. This may be a bit risky. If we want to avoid any 
risk, we need an additional equation to measure the mean I' of the mathematical model of the 
extra trial. Hence we must run two extra trials rather than one. 
3. TWO EXTRA TRIALS 
Example: Clouding of a solution ( block effect) 
The experimenter suspects a shift in the mean. He has available the eight trials of the 
These two trials were chosen from the eight trials of the complementary design 
The choice is very wide as 12 - 34 can be calculated from all the trials. We will use as an 
This means we must run trials 10 and 12 (Table 12.3). The results of these two extra 
initial design, to which he adds the results of new two extra trials. 
I = -1234. 
example the high level of factor 1 and the low level of factor 3 . 
trials are: 
y , , = 13.03 
y, , = 9.73 
These results are all shown in Table 12.4 as two blocks, one with the eight initial trials 
having a mean I, and the other with the two extra trials having a mean 1'. 
The second block may my considered as a Z4" design containing two trials and having 
the alias generator set: 
From which we can calculate the value ofthe contrast hI2 
iI2 = 12- 34 + 2 - 123 - 134 + 4 - 23 +14 
But we know that: 
2 = 1 2 3 = 1 3 4 = 4 = 2 3 = 1 4 0 
Thus: 
h',2 = 12- 34 
245 
Trial no 
- 
1 
2 
3 
4 
5 
6 
7 
8 
TABLE 12.4 
Temperature Product A 
1 2 
- - 
- + 
+ 
+ + 
- 
- - 
- + 
+ 
+ + 
- 
EXPERIMENTAL MATRIX 
CLOUDING OF A SOLUTION 
Initial design + complementory trials 
Product B 
3 
- 
- 
- 
- 
+ 
+ 
+ 
+ 
Stirring Spd 
4 = 123 
- 
+ 
+ 
- 
+ 
- 
- 
+ 
Trial no Temperature 
1 
10 + 
12 + 
Product A Product B Stirring Spd 
2 3 4 = -123 
- - - 
+ - + 
Response 
5.2 
9.5 
1.1 
12.8 
11.8 
17.0 
8.6 
22. I 
Response 
13.03 
We obtain a system without the means. In fact, they appear the same number of times 
with + signs and - signs in the expressions giving h,, (first block) and h,, (second block): 
1 
8 
1~12 = 12 + 34 = -[ +YI - Y2 - Y3 f Y4 + Ys - Y6 - Y7 + Y s ] 
Substituting the experimental data: 
I 
8 
h,, = 12+34 = -[+5.2-9.5-1.1+12.8+11.8-17-8.6+22.1] 
246 
15.7 
8 
h,, = 12+ 34 = __ = 1.96 
1 -3.3 
2 2 
i,, = 12-34=-[-13.03+9.73]=-==1 65 
hence the system: 
12 + 34 = 1.96 
12-34:-1.65 
giving: 
12 = 0.15 
34 = 1.80 
Again, interaction 34 clearly makes the greatest contribution to the sum 12+34. The 
small difference between the values of 12 and 34 obtained with a single extra trial and two 
extra trials indicates a shift in the mean of the two blocks from 1 1.01 to 1 1.38. 
The experimenter can thus come to the following conclusions: 
Conclusion: 
Product A has no influence on cloudiness , and can thus be used 
Clouding always occurs when the temperature is set at the high 
At low temperature, there is always cloudmess when product B is b 
between 0% and 1% 
level. The low temperature (1 5°C) must therefore be used. J 
present. Cloudiness can be avoided by 
- 
I 
1. Using product A 1 
3 2 Working at low temperature 15°C 3$ - 
4. THREE EXTRA TRIALS 
Let us now leave the solution clouding example and return to the fabrication of plastic 
drums discussed in Chapter 7. 
247 
The problem was: 
& The plastic drums must have a volume of two litres We need to find 
the fabrication condittons which provide a volume of at least two Iltres, 
4, but not more than 2 002 litres At least two lttres to give clients full 
value, and not more than 2 002 lltres to avoid being too generous 
A 284 design was run and there were four significant contrasts 
h, = 3+127+146+158+245+268+478+567 
h, =5+126+138+147+234+278+367+468 
h8 =8+124+135+167+236+257+347+456 
h,, = 15+26+38+47+.. 
We can see that the main effects are aliased with third order interactions. The 
interpretation hypotheses we have adopted allow us to assume that these interactions are 
negligible. There are thus only three significant effects, and their values can be calculated from 
the initial design (Chapter 7, section 5.2): 
h, = 3 = +3.2 c m3 
hi = 5 = - 2 . 7 c m 3 
h, = 8 = + 1 . 9 c m 3 
h15 = 1S+26+38+47 = + 2.5 c m’ 
We do not know what interaction is responsible for the large value of contrast his. We 
must therefore run extra trials in order to calculate each of the four interactions making up 
contrast This requires three extra trials. These three extra trials and the contrast A,,, 
obtained from the initial design, lead to a system of four equations and four unknowns. The 
signs of the iiiteractions are selected so that the system is a Hadamard matrix: 
-15-26+38+47 
+I5 -26 - 38 + 47 
-15+26-38+47 
+15+26+38+47 
Many of the 240 trials that were not run satisfy these conditions. We can write only those 
interactions having the assigned levels and deduce the signs of the main factors from them. 
248 
1 2 3 4 5 6 7 8 15 26 38 47 
- - + + 
C - - + 
signs to deduce - + - + 
+ + + + 
We can choose at random, or we could impose extra constraints. For example, we could 
choose the levels of influencing factors so that the new trials can be included in the calculation 
of the effects of these factors. To do so, factors 3, 5 and 8 should have the signs of a 
Hadamard matrix, while 3 and 8 should correspond to the signs of interaction 38. 
1 2 3 4 5 6 7 8 
- + - 
+ - - 
+ 
+ + + 
- - 
The signs for columns 1 , 2,4, 6 and 7 are deduced from those of columns 3, 5, 8, 15, 26, 
38 and 47, again with a certain freedom, producing the following table: 
TABLE 12.5 
ITriinOI 1 ; I ; ; 1 8 
3+8 471 
- + + + - - + - + - - + 
+ + - + - + + + - + - + 
Response 
7.6 
4.4 
We can now write the three responses y,,, y,, and y,, and the contrast A,, using the 
mathematical model: 
Y , ~ = 1 - 3 + 5 - 8 - 15 - 26 + 38 + 47 
y,, = I + 3 - 5 - 8 + 15 - 26 - 38 + 47 
J J , ~ = I - 3 - 5 + 8 - 15 + 26- 38 + 47 
115 = + 15 + 26 + 38 + 47 
These four relationships form a system of equations. The unknowns are the second order 
interactions. The known elements are the mean I and effects 3, 5 and 8, that were calculated 
from the results of the initial design. The value of contrast A,, is also obtained from the initial 
design. 
249 
h, = I = + S . I S C ~ ~ 
h3 = 3 = +3.2cm3 
hj = 5 = -2.7cm' 
h, = 8 = +1.9cm3 
hi5 = 15 + 26 + 38 + 47 = +2.5 cm3 
with these values the system of equations becomes: 
~ 1 7 = 5.15-3.2-2.7- 1.9- 15-26+38+47 
yi, = 5.15 + 3.2 + 2.7 - 1.9 + 15 -26 - 38 + 47 
~ 1 9 = 5.15-3.2+2.7+ 1.9- 15+26-38+47 
h,, = 2.50 
or 
Y , ~ = -2.65 - 15 - 26 + 38 + 47 
yi8 = +9.15 + 15 - 26- 38+47 
yI9 = +6.55 - 15+26- 38+47 
2.5 = + 15 + 26- 38 +47 
Replacing the responses by their numerical values: 
-15 -26 + 38 + 47 = +2.65 + 0.20 = +2.85 
+15-26-38+47=-9.15 +7.60= -1.55 
-15 +26 - 38 + 47 = -6.55 + 4.40 = -2.15 
+15+26+38+47= = +2.50 
Lastly., resolving the system: 
15 = +0.06 
38 = +2.26 
47 = +0.4 1 
26 = -0.23 
Thus, interaction 38 is significant. 
But we have assumed that the mean of the second block was the same as that of the first 
block. If we wish to take into account any shift in this mean we must run one more trial and 
carry out the calculations on twenty trials, sixteen initial trials and four extra ones. 
250 
Trial no 1 2 3 4 5 6 7 8 15 26 38 47 
17 - + - + + - + - - - + + 
18 - - + + + - - + - + - - + 
19 + + - + - + + + - + - + 
20 + + + + + + + + + + + + 
5. FOUR EXTRA TRIALS 
In addition to trials 17, 18 and 19, we shall run trial 20, whose mathematical 
representation contains the expression: 
+15 +26 + 38 + 47 
The four extratrials are shown in the following table (Table 12.6). 
Response 
10.2 
TABLE 12.6 
We can write the four responsesyl, , y,,, y,9 and y20 using the mathematical model: 
y , , = 1 ' - 3 + 5 - 8 - 1 5 - 2 6 + 3 8 + 4 7 
y ,8 = I ' + 3 - 5 - 8 + 1 5 - 2 6 - 3 8 + 4 7 
y,!, = 1 ' - 3 - 5 + 8 - 1 5 + 2 6 - 3 8 + 4 7 
y20 = 1' + 3 + 5 + 8 + 1 5 + 2 6 + 3 8 + 4 7 
This system can be resolved by assuming that the effects and interactions are the same as 
those given by the initial design: 
A3 = 3 = +3.2cm3 
h j = 5 = -2.7 cm3 
h, = 8 = +19cm3 
h,, = 15 + 26 + 38 + 47 = +2.5 cm3 
Entering these values in the system ofequations, we get: 
yI7 = 1 ' - 3 2 - 2 7 - 1 9 - 1 5 - 2 6 + 3 8 + 4 7 
.yI8 = 1 ' + 3 2 + 2 7 - 1 9 + 1 5 - 2 6 - 3 8 + 4 7 
y , , = 1 ' - 3 2 + 2 7 + 1 9 - 1 5 + 2 6 - 3 8 + 4 7 
= 1 ' + 3 2 - 2 7 + 1 9 + 1 5 + 2 6 + 3 8 + 4 7 4'20 
25 1 
The fourth equation allows calculation of I' 
10.2 = 1' + 4.9 
I' = 5.3 
Substituting this value in the four equations gives a system analogous to that of the 
previous section, and from which the values of each interaction can be deduced. 
-15 -26 + 38 + 47 = + 2.50 + 0.20 = +2.70 
+15 -26 - 38 + 47 = - 9.30 + 7.60 = -1.70 
-15 +26 - 38 + 47 = - 6.70 + 4.40 = -2.30 
+I5 +26 + 38 -t 47 = - 7.70 + 10.20 = +2.50 
or 
15 = -0.10 
26 = -0.20 
38 = +2.30 
47 = +0.30 
Again, the result is similar, with interaction 38 being significant 
Comments 
The results of four extra trials may be added to the sixteen results of the first set of trials 
to calculate the effects of 3, 5 and 8. The contrasts then contain twenty terms and there is, 
theoretically slightly better precision. Take, for example, contrast h, : 
1 
If the standard deviation of the response y is o whatever the value of the response, then 
the standard deviation of the contrasts is of&, where n is the number of responses. When the 
four extra responses are included in the calculation of contrasts, the standard deviation changes 
from o ~ f i to o1J20. 
---[-y, -)'2 - ) '3 -)'4 +)'5 + y 6 +?'7 +)'8 -)'9 -1110 -yll - ) 'I2 +)113 +yl4 +yl5 + y 1 6 -)'17 'y18 ->'I9 +).20] 
- 20 
As there are only 3 influencing factors we can: 
reconstruct the experimental design as a duplicate 2, design as there are sixteen 
trials. We can thus calculate the effects and interactions, and adopt a model. 
present the results on a cube (experimental domain) with the response surface of 
interest y = 0. 
252 
5.1 Reconstruction of the experimental design 
All the trials with the same levels for factors 3, 5 and 8 (Table 12.7) are grouped 
together, and the effects and interactions calculated from the sixteen initial trials. The extra 
trials are shown in brackets, and not used to calculate the effects and interactions. 
TABLE 12.7 
EXPERIMENTAL MATRIX REARRANGED 
PLASTIC DRUMS 
Reconstruction of the effects matrix from the results of the initial 2u design 
Trial no 
10 (17) 
15 
2 12 (19) 
7 13 
3 9 
6 16 (20) 
Effects 5.15 3.2 -2.7 1.9 -0.3 2.5 0.5 -0.2 
The model is thus readily obtained by rounding off and neglecting small interactions: 
y 5.2 +3.2 x3 - 2.7 x5 + 1.9 x8 + 2.5 x3 XS 
5.2 Presentation of results 
The values of the responses at each corner are calculated from the model, and the 
isoresponse surface drawn: 
The zero isoresponse surface, which is the limit that must not be crossed. 
The + 1 cm3 isoresponse surface. 
253 
The best settings that can be suggested are chosen as follows: 
Changes in influencing factors have little effect on changes in drum volume. 
Changes in influencing factors around their settings that avoid crossing the zero 
isoresponse surface. 
Examination of Figure 12.1 shows that these conditions are satisfied when factor 5 is 
high and factor 8 low (segment AB in figure 12.1). Factor 3 can thus vary without causing 
excessively large changes in volume. An injection pressure ( 3 ) set to the middle of the selected 
segment AF3 should be suitable: point R in Figure 12.1. We can see that, for this point, changes 
in factors 5 or 8 never produce volumes less than 2000 cm3. However, factor 3 must vary 
within strictly defined limits to avoid producing drums that do not meet the specifications. 
4.1 
(3.05) 
Dwell 
Time 
(8) 
15.5 
(1 5.45) 
5.3 
(5.65) 
Y 
6.7 Flow Rate 
Injection Pressure 
(3) 
Figure 12.1: Isoresponse surfaces were drawn using the mathematical model. The 
calculated point R is only a first approximation which must be refined 
by supplementary trials. 
The setting point has been determined by the mathematical model giving the drum 
volume under specific conditions. But we must be careful, because if the mean experimental 
responses from the trials are recorded at the comers of the cube representing the experimental 
254 
domain (shown in parentheses in Figure 12 I) , then the zero response area is slightly different 
from that obtained &om the mathematical model. The recommended point R could be too close 
to the real zero surface. A complementary study near point R is required to accurately define 
the best settings. 
We can thus extend to the first provisional conclusion fiom this study of plastic drum 
fabrication given in Chapter 7 as follows: 
Conclusion from the study of plastic drum fabrication: 
The volume of the plastic drums is generally too great, due to three I 
g 
. Injection pressure (3) 
. Feedstock flow rate (5) 
. Dwell time (8) 
. There is a strong interaction between injection 
pressure (3) and dwell time (8) c 
The settings must be: 
. Feedstock flow rate (5) at high level 
. Injection pressure, selected between levels 0 and +I 
in the domain defined for this factor. 
. Dwell time (8) at low level. 8 
These settings ensure that no drum has a volume less than 2000 
om3, and should produce no drums larger than 2002 cm3 
The sensitivity of volume to changes in the three influencing factors 
around the set point R should be studied to optimize fabrication 
conditions 
255 
RECAPITULATION 
1. It is not always necessary to run a complementary design when there are ambiguities in 
interpreting the results of a fractional design. It is sometimes possible to carry out just 
a few extra trials. 
2. Block effects are better taken into account by running two or four extra trials and 
using a Hadamard matrix than by running one or three trials. 
3 . The extra trials for dealiasing doubtful interactions are selected on the basis of the 
mathematical model for the factorial design. This can resolve several problems. But it 
is nevertheless wise not do this blindly. It is absolutely necessary to go back to the 
experimental results for the best interpretation and check them with confirmatory 
trials. 
This Page Intentionally Left Blank
CHAPTER 13 
B E Y O N D 
I N F L U E N C I N G F A C T O R S 
1. INTRODUCTION 
All the examples we have described in the preceding chapters were used to detect 
influencing factors, but we have seen that a complementary study is often usefbl (e.g., in the 
study of plastic drum volume). This complementary study can be used to obtain three types of 
information: 
to identi@ the domain of interest. 
to find an optimum. 
to find the minimum response sensitivity to external factors 
1.1. Identifying the domain of interest 
The choice of experimental domain is important. The desired solution may well be 
outside the domain selected for the initial design. This is useful for selecting influencing factors 
and producing an approximate model of the phenomenon. It is possible that the initial trials 
may not meet the experimenter's requirements. In this case, the initial results can be used by the 
258 
experimenter to define a new domain in which there is a good chance of finding the solution to 
the problem. This new part of the experimental domain that best fulfils the requirements of the 
experimenter is called the domain of interest. 
1.2. Looking for an optimum 
Factorial designs are not suitable for optimizationstudies, because they use only two 
levels for each factor, so that the model contains no second degree terms. We have only 
covered the search for influencing factors in this book. This is thus only the initial stage in 
Experimentology. Once the influencing factors have been identified, it is often necessary to run 
an optimization design. These designs are no more complicated that those we have already 
studied, but the calculations are much longer and require a microcomputer. We will not study 
these designs, but simply indicate that they are readily obtained by adding extra experimental 
points to the original fractional design. 
All the results obtained in the first experimental phase are reused for optimization. This 
satisfies one of our original objectives: the progressive acquisition of knowledge by running the 
fewest possible trials. We will examine how best to verify that the mathematical model of the 
factorial designs is valid or invalid for previsions within the experimental domain. 
1.3. Finding the minimum response sensitivity to external factors 
Application to Quality 
An important application of experimental design is in Quality improvement. It can be 
used for both product design and for manufacturing process development. The Japanese 
expert, Taguchi, has been responsible for applying factorial designs to the concept of quality in 
industrial development. In order to persue this and obtain clear results of all the tools of 
Experimentology must be used: influencing factors, optimisation and modelling, etc. However, 
it is possible to understand the fimdamental concepts of this method using a simple example. 
Even a search for influencing factors can resolve many of the problems of Quality. Modelling 
and optimization provide yet more power and efficacy. 
2. IDENTIFYING THE DOMAIN OF INTEREST 
2.1. Example: Two-layer photolithography 
There are several critical steps in the production of the microchips bearing the thousands 
of transistors required for integrated circuits. High performance two-layer photolithography is 
one of the key steps in the fabrication. Two-layer photolithography involves several operations 
which must be closely controlled to obtain the submicroscopic sculpture of microchips. 
259 
The following example is quoted with permission from a study carried out by RTC- 
Compelec (France). Some of the data have been changed for the sake of confidentiality. 
The problem: 
* 
Photolithography is used to prepare two types of microchip: lift off 
and etching. Many steps are involved in this process, but just two of 
them can be used to understand the problem. 
Deposition of two layers of photosensitive resin (resin A and resin 
6) onto a semiconductor substrate. 
This groove must have a specific profile for each of the two 
applications. the lift off profile and the etching profile. This study 
was carried out to define the operating conditions providing these 
B Photographic engraving of a groove in the resins 
k 
I 
k i 
il profiles. 
The problem was defined at a meeting. The responses were defined first. The list of 
factors which it was considered may influence the responses defined above was then 
established. ARer considerable discussion, the levels of each factor were defined, and thus the 
experimental domain. Lastly, the experimental design was selected. 
Responses 
The responses chosen were L2 and L3 as indicated on Figure 13.1. The experimenter is 
looking for two different applications, the kjit ofland the etching application. 
L2 
Resin A 
Resin B LIFT OFF - 
L3 
L2 
Resin A -7 I s i n B ETCHING 
.--. 
L3 
Figure 13.1: Lift off and etching profiles 
260 
The two applications, lift off and etching, have different profiles (Figure 13.1), so that 
the dimensions of L2 and L3 are not the same. They are indicated in the following table: 
TABLE 13.1 
PHOTOLITHOGRAPHY 
Selection of Factors 
A total of eleven factors were initiallv identified, but after examination, seven were 
selected for hrther study. 
. Factor 1 : thickness of resin B. - Factor 2: curing temperature. 
Factor 3: plasma 1 time. 
Factor 4: W dose (millijoules) . Factor 5 : development method. . Factor 6: development time. . Factor 7: plasma 2 time. 
Definition of the domain 
It is important to define the domain of each factor, i.e., the low and high levels. The 
combined levels define an experimental domain in a seven-dimension space. 
Level - Level + 
Factor 1 : thickness of resin B 
Factor 2: curing temperature ("C) 
Factor 3 : plasma 1 time (min.) 
Factor 4: UV dose (millijoules) 
Factor 5: development method 
Factor 6: development time (min) 
Factor 7: plasma 2 time (min) 
thin thick 
150 200 
0.5 3 
500 1000 
dip stir 
1 4 
1 4 
Choice of initial design 
As so often happens, the experimenter was not certain that the defined experimental 
domain contained the solution to the problem. He preferred to begin with an exploratory 
26 1 
Level- thin 150°C 30sec 500 dip 
Level + thick 200°C 3 min 1000 stir 
design. He selected a Z74 design with only eight trials. He feared that certain factors that had 
been abandoned would have very slight influences, but as he did not wish to monitor them 
later, he decided to consider them as background noise and include them in experimental error. 
The trials were randomized. 
The planned trials were run according to the design shown in Table 13.2. Unfortunately, 
some responses were not measurable, so that three trials were unusable. Nevertheless, 
measurements could be made with the thin resin layers. The experimental domain chosen was 
not appropriate for these resins, but was suitable for the thick resin layers. 
1 min 1 min 
4 min 4 min 
TABLE 13.2 
DESIGN NO1 
PHOTOLITHOGRAPHY 
Temp. 
2 
Metd. 
5=12 
- 
Time 
6=23 
- 
Plm 2 
7=13 
It was decided to choose different experimental domains for each of the two resins. One 
study was run on thin resins and one on thick resin layers, so that only six factors - 2, 3, 4, 5, 6 
and 7 - were studied. It was decided that: 
The limits of factor 4 (UV dose) were changed only for the thin resin layers. 
0 A completely different domain was defined for the thick resin layers. As the 
experimental domains for the thick and thin resin layers do not overlap, two 
separate designs must be used, one for each thickness. 
We will confine our attention to the study of the thin resin layer. A design was run with 
the new domain (slightly smaller for factor 4, 350-750 millijoules rather than 500-1000). To 
262 
avoid any confusion in the overall analysis of results, the numbering of the factors was not 
changed and the trials were numbered subsequently. (Table 13.3) 
The new design is a 26-3 as there only six factors to be studied. We know that there are 
23 terms in the AGS, and the columns of the design are aliased as in the initial 274 design: 
4 = 123 
5 = 1 2 
6 = 23 
7 = 13 
We may therefore be tempted to write the independent generators as: 
1 = 1234 = 125 = 236 = 137 
but we must take into account the fact that the first column (factor I, the resin factor) no 
longer represents a factor and thus we must remove it from the alias generator. We have: 
I = 123.23 = 4.6 
Column 1 now represents interaction 46. If we replace 1 with 46 in the alias generators 
we have: 
I = 46234 = 4625 = 236 = 4637 
SimplifLing and ordering, 
1=236=2456=236=3467 
Two independent generators are equal, hence the four remaining independent alias 
generators are: 
1=236=2456=3467 
Multiplying them by twos and by threes gives the dependent generators, and we can 
write the AGS. 
1=236=2456=3467=345=247=2357=567 
From which the contrasts are: 
h, = 2 + 3 6 + 47+ ... 
h, = 3 + 26 + 45 + .._ 
h, = 4 +27 + 3 5 + ... 
h, = 5 + 34 + 67 +... 
h, = 6 + 23 + 57 f ... 
263 
Level- 
Level + 
h,= 7 f 24 + 56 i- ... 
h, = & = 46 + 25 + 37 + 
The eight trials were run as indicated in design number 2 (Table 13.3). The results and 
the effects calculations ofthe two responses L2 and L3 are shown in the same table. This time 
all the responses can be measured, the domain is better defined but we must still be sure that 
the values required for L3 and L3 lie within the domain examined. 
150°C 30 sec 350 dip 1 min 1 rnin 
200°C 3 rnin 750 stir 4 rnin 4 rnin 
TABLE 13.3 
L, 
L, 
DESIGN NO2 
PHOTOLITHOGRAPHY 
3.75 11.25 5.5 0.75 17 14.25 2.5 65 
0.5 8 9.25 -2.5 13.25 33.5 -0.75 46.75 
Plm 
3 
-22 
45 
2.2. Examination of the results for response L2 
The influencing factors are: 
. Plasma 1 (3). . The development time (6). . Plasma 2 (7). 
264 
0 Factor 4 may have a slight influence. 
0 Curing temperature (2) has no influence. 
0 The development method (5) has no influence. 
Examhation of the contrasts shows that there is no significant interaction between the 
factors. If we adopt this hypothesis we can use the following model (neglecting factor 4): 
L 2 = 6 5 + l l x 3 + 17x6+14x7 
where L2 is measured in hundredths of microns. 
experimental domain (Figure 13.2). 
This relationship can be represented by drawing the isoresponse surfaces in the 
85 107 
Plasma 2 
(7) 
23 45 Time 
* c (6) 
Plasma 1 
(3) 
Figure 13.2: lsoresponse curves calculated for L2 values of 0.30, 0.50 and 0.70 micron. 
We can see that the planned dimensions for L2 (0.3 p) is located in one comer of the 
domain. 
265 
2.3. Examination of the results for response L3 
0 The influencing factors are the same as for L2 with the UV dose (4) having a larger, 
non-negligible influence. 
The curing temperature (2) and the development method (5) are both without 
influence. 
Examination of the contrasts shows that there is no ambiguity and that there are no 
interactions. 
We will therefore adopt the following model: 
L3 =47 + 8x3+ 9x4 + 13 x6 + 35 x7 
It is difficult to plot the isoresponse surface within the experimental domain because we 
cannot draw them in a four-dimensional space. However, we can get a geometric 
representation of L3 by setting one of the factors at a given value. For example, we can 
compare L2 and L3 by setting x4 to 0. This is a convenient value, but another could be chosen. 
The model is then written: 
L3 = 47 + 8 x3 + 13 x6 + 35 x7 
And this allows us to draw Figure 13.3 
a7 103 
Plasma 2 
(7) 
61 
@ 
@ 
-9 
, 
33 
7 
,/Development 
7 Time 
Figure 13.3. Isoresponse curves calculated for L3 values of 0.1 and 0.3 micron (with the 
UV dose set at level zero). 
266 
The interesting values of L3 (from 0.1 to 0.3 p) lie in the region of the domain where 
we found the appropriate dimensions for L2. The problem may thus be resolved We must find 
the region where L3 varies from 0.1 to 0.3 p and L2 remains below 0.3 p. The isoresponse 
surfaces indicate that this region exists, and is probably slightly outside the domain studied. We 
can look for this region by using mathematical models. But as we approach the domain of 
interest we must not neglect the influence of factor 4 on L2. The models are therefore: 
L2 = 65 + 11 x3 + 5 x4 + 17 x6 + 14 x7 
L3 = 47 + 8 x3+ 9 x4 + 13 X6 + 35 x7 
-2 -1 0 +I 
x3 Plasma 1 (sec) 
750 UVdose 
Development time (min) 
x4 t , ~ ~ T " 1:: 1 
x6 
x7 Plasma 2 (min) 
0 ' 4 
Figure 13.4: Definition of theoretical study domain. 
This theoretical search will allow us to define a new domain in which there is a good 
chance of finding the required solution. We can illustrate the approach by setting x3 and x4 and 
studying the isoresponse curves in the plane x6 x7. The variable x3 is set at 30 seconds (level - 
1 ) and variable 4 at 150 (level-2) (Figure 13.4) 
L2=44 + 17x6+ 14x7 
L 3 = 2 l +13x6+35x7 
Naturally, this must be confirmed experimentally. These extrapolations are only 
We can draw the isoresponse curve for L2 and L3 in this domain using the above 
guidelines. 
formulae (Figure 1 3.5). 
267 
Lift off 
Plasma 1 30 sec 
w. 150 
Development time 15 sec 
Plasma 2 3 min 40" 
4' 
Etching 
30 sec 
150 
78 sec 
2 min 30" 
Plasma 1 2'30" 
1' 
1' 2'30' 
Development time 
Figure 13.5: Region in which the experimental condition providing the lift-off (L) and 
etching (E) profiles will probably be found. 
Examination of figure 13.5 shows that the operating conditions providing the required 
lift off and etching profiles can be defined. The following table (Table 13.4) indicates one 
possible solution. 
TABLE 13.4 
PHOTOLITHOGRAPHY 
But it would be unwise to consider these values as certain. We have employed several 
assumptions for calculating them and they may be questioned. They simply permit us to 
roughly define a region in which the solution to a problem may be found. It is now time to 
confirm that we can really obtain the lift off and etching profiles by running an extra set of 
trials. 
The new experimental domain will be reduced to four factors, as the curing temperature 
(2) and the development method (5) are without influence. The new domain for the remaining 
factors may be: 
Level - Level + 
Factor 3: plasma 1 (sec) 10 70 
Factor 4: UV dose 100 500 
Factor 6: development time (sec) 10 130 
Factor 7: plasma 2 (sec) 120 240 
268 
As the domain has been clearly defined and probably contains the required solutions, the 
experimenter can plan two or four measures at the central point to check the validity and 
quality of the model. 
We will not show the final results of the study. We assume that the experiments were 
carried out as indicated in the partial conclusions set out below. 
Partial conclusion: 
~ 
7 The thin and thick resin layers must be studied separately. 
For thin resin layers, there are two non-influencing factors, curing 
temperature and development method. We will choose: 
. The lowest curing temperature (energy saving) 
. Dipping development method (simplest operation) 
The trials run allowed definition of a small domain probably 
containing the solutions required to produce the lift off and etching 
profiles. The operating conditions given by the calculations must be 
confirmed by an experiment studying four factors: plasma 1, plasma 2, 
UV dose and development time. A 24 design will be run with four 
8 central points to check the quality and validity of the model. 
We will now examine a case in which the methods that we have studied (factorial 
designs) are not powerfbl enough to provide the desired solution. This is finding an optimum. 
3. FINDING AN OPTIMUM 
3.1. Example: Cutting oil stability 
This unpublished study was carried out in the Total laboratories. It shows how, despite 
their power, factorial designs are sometimes not suficient for solving a problem, and that 
studying the domain of interest sometimes requires even more complex methodological tools 
than those we have discussed so far. 
The problem: 
Cutting oil is used to facilitate metal machining: it lubricates the 
machined metal and cools the cutting tool. A cutting oil is a milky 
f looking emulsion of water and oil. The emulsion must remain stable in 
9 the machine shop, and this is ensured with a chemical additive. The 
1 investigator must determine the quantity of additive necessary to keep 
269 
Trial no 
1 
2 
3 
4 
5 
6 
'" 
the emulsion stable under normal working conditions. He IS looking for 
a stability of at least 100. 
* 
Temperature Add. conc. 
I 2 
- - 
- + 
+ 
+ + 
- 
0 0 
0 0 
Factors studied 
The investigator selected two factors: 
- Factor 1 : temperature. . Factor 2: additive concentration 
Response 
The response is the index of cutting oil stability, measured with a precision of 2. The 
higher the index, the greater the stability. 
Domain 
Low temperature level: 5°C. 
High temperature level: 45°C. 
Low additive concentration: 0.4% 
High additive concentration: 0.8% 
Design 
The investigator decided to use a 22 design, but he adds two points at the centre of the 
experimental domain to check the validity of the model. 
TABLE 13.5 
EXPERIMENTAL MATRIX 
CUTTING OIL STABILITY 
Response 
100 
2703.2. Interpretation 
concentration. their interaction and the mean. The error on the effects was: 
The first four trials were used to calculate the effects of temperature and additive 
+2 
- = k 1 stability point A 
TABLE 13.6. 
TABLE OF EFFECTS 
CUTTING OIL STABILITY 
Mean 107.5 
1 -3 * 
2 12.5 k 
12 -4 k 
point 
point 
point 
point 
It is wise to determine whether the calculated mean can be considered equal to the 
measured mean (central point) before beginning to build a model. 
The average of the two trials at the centre was 99 and the standard deviation was 
With a 95% probability of this being true (i.e., k two standard deviations) we have: 
model mean: 107.5 5 2 
measured mean: 99 k 2.8 
These two means are clearly different (Figure 13.6), making it impossible to use the 
How can we explore the domain of interest in more detail? We do not have enough 
factorial design model. 
information to answer this question, so we need more experimental points. But: 
Where should these new experimental points be placed? 
How can we define an optimal design? 
How do we do the calculations? 
How can we use and present the results? 
271 
99 107.5 
Figure 13.6: The two means are clearly different. 
All these questions require detailed answers, but they exceed the original objective of this 
book, which is to find influencing factors. Let us use this example to begin our study of 
modelling and optimization. These two problems fall within the range of questions treated by 
Experimentology . 
We can use matrix and statistical techniques that are as powerful as those for factorial 
designs to solve the problems. These techniques and their application will be the subject of a 
new book. 
Provisional conclusion: 
The results show that the objective of a 100 point stability can be 
achieved For example, at the high additive concentration (0 8%) level 
the stability is over 100 at both the temperatures tested But this result 
is incomplete because the additive concentration is too high - it is not 
optimized. The economic aspect most be reconciled with demands of 
quality, I e , the lowest additive concentration which ensures a stability 
of 100 points between 5°C and 45°C 
The difference between the calculated and measured means makes 
it impossible to use the mathematical model associated with factorial 
designs to plot the isoresponse curves The investigator cannot make 
any recommendations with the information available 
Complementary experiments are necessary to establish a second 
t degree model and plot isoresponse curves for the phenomenon 
4. FINDING A STABLE RESPONSE 
4.1. Example: thickness of epitaxial deposits 
Taguchi [22] proposed an interesting approach for finding a robust solution to a 
problem. When factor levels are chosen so that the response of interest is minimally influenced 
272 
by factor variations, the response is said to be robust. The fundamental concept of robustness 
can be illustrated by a quality study carried out at AT&T in the USA, as reported by Kackar 
and Shoemaker [ 2 3 ] . 
The equipment used for preparing epitaxial deposits was set up to give thicknesses of 14- 
15 microns. The epitaxial deposits are formed on wafers in a heated chamber. A total of 14 
wafers are arranged on a support, the susceptor, that can be rotated or oscillated (Figure 13.7). 
Wafer 
Figure 13.7: 14 wafers placed on the susceptor. 
The problem: 
- 8 The deposits are not uniform, some are thinner than 14 microns, 
while others are thicker than 15 microns. Although the mean thickness 
of 14.5 microns is satisfactory, the number of rejects is high, resulting in 
unacceptable costs. The objective is to find new settings for the 
installation that give the smallest possible dispersion around the 
B nominal value of 14.5 microns. 
Production set-up values 
The pre-study production set-up parameter values were: 
. Arsenic flux 5 7% . Depositing temperature 1215°C 
273 
Susceptor motion oscillation . Deposition time short . Hydrochloric acid temp. 12OOOC . Injection nozzle position 4 
Hydrochloric acid flux 12% 
The investigators decided to use two types of wafer in the study: type 66864 and 
678D4. An eighth factor was therefore added to the seven listed above, the wafer code. They 
also decided to stay fairly close to the normal conditions by setting the study domain around 
the production set-up values. 
Factors 
The factors are the set-up parameters plus the wafer code. The domain is defined by the 
following table: 
Level - Level + 
Factor 1: arsenic flux 
Factor 2: deposition temp. 
Factor 3: wafer code 
Factor 4: susceptor movement 
Factor 5 : deposition time 
Factor 6: HCl temp. 
Factor 7: injection nozzle position 
Factor 8: HCI flux 
55% 
66864 
rotation 
long 
1 180°C 
2 
10% 
1210°C 
59% 
1220°C 
678D4 
oscillation 
short 
1215°C 
6 
14% 
Responses 
The susceptor carried 14 wafers in each trial, and the thickness dispersion was measured 
at 5 points on each wafer. 
Figure 13.8: Arrangement of points for measuring wafer thickness. 
274 
Level - 55 
Level + 59 
Thickn -003 
log s2 -0005 
There are thus seventy measurements of thickness per trial. The responses chosen were 
the mean thickness and the dispersion of thickness. 
1210 668 Rot long 1180 2 10 
1220 678 Osc short 1215 6 14 
-005 003 -002 -041 003 007 -004 1439 
0 0 5 2 0061 0 176 -0 124 -0035 -0282 -0 05 -0648 
mean thickness 
If e, is the measured thickness and E the mean of the 70 measurements in each trial, then 
- 1 'O e = - E e i 
70 1 
TABLE 13.7 
EXPERIMENTAL DESIGN (1=2345=1346=1237=1248) 
EPITAXIAL DEPOSIT 
Trial no 
1 
2 
3 
4 
5 
6 
7 
8 
9 
10 
11 
12 
13 
14 
15 
16 
1 2 3 4 5=234 5=134 
- 
7=123 P=124 I 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
+ 
Thick. 
14.821 
14.888 
14.037 
13.880 
14.165 
13.860 
14.757 
14.921 
13.972 
14.032 
14.843 
14.415 
14.878 
14.932 
13.907 
13.914 
log s* 
-0.4425 
-1.1989 
-1.4307 
-0.6505 
- 1.4230 
-0.4969 
-0.3267 
-0.6270 
-0.3467 
-0.8563 
-0.4369 
-0.3131 
-0.61 54 
-0.2292 
-0.1190 
-0.8625 
275 
thickness dispersion 
The dispersion was defined as the log of the variance: 
log s2 = log [ -X(ei-e) ;9 7: '1 
Experimental design 
A resolution IV fractional factorial design 2;: was selected. 
4.2. interpretation 
Table 13.7 shows the trials run and the responses obtained. The results were interpreted 
by first examining the variance of the set-up factors. This approach is emphasised by Taguchi, 
who used it routinely to improve the quality of products or processes. The initial objective was 
to select the levels of factors which give the smallest possible variations in the response of 
interest. Once these levels have been determined for the factors influencing the variance, the 
nominal deposit thickness is then adjusted using the factors that influence thickness but not the 
variation in thickness dispersion. This provides a set-up with the correct thickness and minimal 
dispersion. Under these conditions the number of rejects is very small, and may even be zero if 
the dispersion is sufficiently small. 
Thickness dispersion 
The factois influencing the thickness variance are shown in Table 13.8 
TABLE 13.8 
TABLE OF EFFECTS 
EPITAXIAL DEPOSIT 
Thickness variance 
Mean 
1 
2 
3 
4 
5 
6 
7 
8 
-0.6484 
-0.005 
0.052 
0.061 
0176 
-0.124 
-0.035 
-0.282 
-0.050 
276 
The three influencing factors are, in order of importance: 
. Factor 7: injector nozzle position . Factor 4: susceptor rotation . Factor 5: deposition time. 
Figu :s 13.9, 13.10 and 13.1 1 show that the thickness variance will be redu 
. Factor 7 is set at the high level, position 6, 
Factor 4 is set at the low level (continuous rotation) 
Factor 5 remains unchanged (short deposition time). 
Log s2 
- 0.366 
- 0.648 
- 0.930 
-1 0 +I 
(;i . /, i(6') , 
INJECTION NOZZLE (7) 
:d if 
Figure 13.9: Influence of injection nozzle position (Factor 7) on thickness variance. 
277 
Log s2 t 
-1 0+I 
Rotation Oscillation 
SUSCEPTOR MOVEMENT (4) 
Figure 13.10: Influence of susceptor rotation (Factor 4) on thickness variance. 
s2 t 
-1 0 +I 
Long Short 
DEPOSITION TIME (5) 
Figure 13.1 1: Influence of deposition time (Factor 5) on thickness variance. 
278 
All that remains is to interpret the results of the experimental design for the thickness 
itself 
Thickness 
Table 13.9 summarizes the effects and interactions of the factors studied 
TABLE 13.9 
TABLE OF EFFECTS 
EPITAXIAL DEPOSIT 
Thickness 
Mean 
1 
2 
3 
4 
5 
6 
7 
8 
12 
13 
14 
15 
16 
17 
18 
14.39 micron 
-0.03 micron 
-0.05 micron 
0.03 micron 
-0.02 micron 
-0.41 micron 
0.03 micron 
0.07 micron 
-0.04 micron 
-0.01 micron 
0.02 micron 
0.00 micron 
-0.01 micron 
0.02 micron 
0.01 micron 
-0.03 micron 
Only one factor is influent: 
. Factor 5 : the deposition time. 
There is no apparent interaction. Figure 13.12 shows the influence of deposition time on 
the mean thickness of the epitaxial deposit. 
The exact deposition time providing a thickness of 14.5 microns is readily calculated if 
the values of the short and long levels are known in minutes and seconds. These values are not 
available for obvious industrial reasons. We can however do the calculation using coded 
values. The mathematical model is: 
y = 14.39 - 0.41 x 
279 
14.80 
14.39 14.50 
13.98 
--\ 
-0.27 
Long Short 
DEPOSITION TIME (5 ) 
Figure 13.12: Influence of deposition time (Factor 5) on the mean thickness of the 
epitaxial deposit. 
setting y = 14.5, we get: 
14.5 = 14.39 - 0 . 4 1 ~ 
hence: 
-14.5+14.39 0.11 - -o,268 
- X = 
0.4 1 0.41 
This value can be used to calculate the optimal deposition time in coded variable (Figure 
13.12) and given as a recommendation. 
The information provided by the experimental design allows: 
Reduction of the dispersion of deposit thickness by changing the injection 
nozzle position and using continuous rotation instead of oscillating. 
The nominal thickness of 14.5 microns can be obtained by changing the 
deposition time. This slightly increases the thickness variance, but fortunately 
factor 5 is not the most important for dispersion. 
280 
Arsenic flux 
Deposition temperature. 
Susceptor movement 
Before giving the results and making recommendations for setting up the industrial 
production, the interpretation must be verified. A series of trials was therefore run with the 
new settings - the confirmatory trials. The standard deviation was found to be 0.24 micron, the 
thickness was 14.5 microns and there were almost no rejects. 
5 7% 5 7% 
1215°C 1215°C 
oscillation rotation 
Conclusion: 
i The dispersion of epitaxial deposit thickness can be reduced by 
6 adjusting the set-up factors as shown in the following table. 
I Factor 1 Original setting I New setting I 
Deposition time variable 
HCI temperature 1200°C 1200°C 
Injection nozzle 
HCl flux 12% 12% 
The deposition time will be set to obtain the required mean thickness 
of 14.5 microns. The recommended settings guarantee a standard 
deviation of k 0.25 microns around this thickness. 
This example illustrates an important concept emphasized by Taguchi: there is one 
setting, among all the possibilities, that minimizes the variance in the target response. In order 
to ensure the Quality of a product or process the stable or robust settings must be found. But 
Taguchi went further. Not only did he study the factors influencing fabrication, he also studied 
the factors that could influence the life of the product after it had left the factory. He examined 
all the conditions, from product design, to manufacture and subsequent client use. This 
approach to research and development, coupled with cost control, illustrates a particularly 
interesting application of experimental design to quality improvement. 
28 1 
RECAPITULATION 
1 . The photolithography example has emphasized one of the key points in experimental 
design: the search for the domain of interest. A combination of a progressive 
approach and detailed analysis at each stage will invariably lead to a solution 
whenever such a solution exists. Only experimental design can provide a rapid, 
reliable solution to a problem involving several factors. We must therefore again 
emphasize that non-influencing factors are not necessarily of no importance. No 
change in the response can produce savings (see also the examples on the colour of a 
product, bean-growing experiment and epitaxial deposits) and facilitate the production 
of optimal settings. 
2. The cutting oil example shows that we must be extremely carefil before adopting a 
model, even for a very simple case. It is vital to carry out trials at the centre of the 
domain to test the model. Central point trials must be run as soon as the investigator 
believes he is within the domain of interest and wishes to begin model-building. They 
are immediately usehl for estimating the standard deviation, and will remain usehl for 
finding a second degree model, if required. Model-building and optimization are 
almost always the experimenter's goal. Identifylng influencing factors and using the 
first degree model are often only the initial phase of the study. 
3. An important application of experimental design is the use of the variance as the 
response. It is possible to identifl factors that minimize the dispersion of responses so 
as to make them less sensitive to external factors. This is an effective way of 
improving the quality of a product or process, Applying this technique right fiom the 
design of a product, i.e. during the R&D phase, is the surest method of ensuring 
quality, reduced product control costs and the widest market for the product. 
This Page Intentionally Left Blank
CHAPTER 14 
P R A C T I C A L M E T H O D 
O F C A L C U L A T I O N 
U S I N G A Q U A L I T Y E X A M P L E 
1. INTRODUCTION 
It is much easier to interpret experimental designs and allied methods if the calculations, 
outlines and isoresponse curves are prepared quickly and accurately. This can only be done 
with a microcomputer. But this does not imply that it always requires expensive, dedicated 
software. All the examples in this book were prepared using a simple spreadsheet, Lotus 123. 
In general, the calculations involved in searching for influencing factors and evaluating 
variance are simple. However, those for optimization designs and identifirlng the best 
experimental points when preparing special optimal designs (mixture designs or designs with 
constraints) are not. Specific softwares are then necessary. These dedicated programs (see 
Nachtsheim [24] vary in complexity and ease of use, and require careful selection. The 
experimenter must choose carefully at all phases: design selection, aliase selection, factor 
284 
selection, mathematical model, residuals calculation, domain selection, etc. The software 
should help the experimenter make decisions and not make them for him! 
It is a good idea for the experimenter beginning to use factorial designs to do the detailed 
calculations himself, so that he can better understand the si@cance of each result. The 
quality of his interpretation and conclusions depend on this. This is why we will now go step 
by step through an example. 
The presentation has been made more accessible by separating the calculations from the 
descriptive section. The first part of this chapter describes the problem to be studied, and 
references are given for each detailed calculation. The second part of the chapter covers the 
details of each operation; these can be reproduced by anyone with a copy of the Lotus 
spreadsheet or an equivalent. In this way the reader can follow the reasoning and check the 
calculations. 
2. A QUALITY IMPROVEMENT EXAMPLE 
Example: Study of truck suspension springs 
This example is taken from Pignatiello and Ramberg [25] . It was carried out by the firm 
of Eaton Yale to improve the manufacture of truck suspensionsprings. It is the type of design 
that provides quality improvement, as defined by Taguchi, by reducing response variance and 
then adjusting the response to the required value. 
The problem 
Truck springs are made up of leaves having a precisely defined 
curvature. The curvature must be exactly eight inches, with a very small 
variation around this value. The leaves undergo several treatments 
during manufacture, including: 
0 Heating to high temperature in a furnace. 
Bending in a special forming machine. 
0 Immersion in an annealing oil bath. 
The study was carried out to determine the factors influencing the 
curvature and the dispersion of the curvature during the three phases 
described above. This information was used to advise on how: 
0 The mean curvature could be kept at 8 inches, 
0 The dispersion of curvature around 8 inches could be as small 
as possible. 
It is important to clearly define the factors to be studied, the 
experimental domain and the responses, before beginning any 
experiments. 
285 
Factor 1 (OF) 
Factor 2 (sec) 
Factors 
1840 1880 
25 23 
The fabrication engineers believed there to be four influencing factors that may show 
important interactions. This was kept in mind when choosing the experimental design and the 
aliases. They also believed that a fifth factor (the temperature of the annealing bath) could be 
influencing,, but its control during fabrication would require extra equipment. They therefore 
preferred to consider it as a non-controlled factor contributing to the experimental error; this 
factor could also be said to increase the background noise. Nevertheless, steps were taken to 
give it two levels during the study (low and high), but these levels were defined approximately 
because temperature was not accurately regulated. 
Factor 3 (sec) 
Factor 4 (sec) 
Factor 5 (“F) 
. Factor 1 : 
.Factor 2: 
Factor 3 : 
. Factor 4: . Factor 5: 
12 10 
2 3 
130-1 50 150-170 
furnace temperature. 
heating time. 
transfer time between leaving the furnace and placing in the 
bending machine. 
bending time. 
annealing bath temperature. 
. Interactions 12, 13 and 23: The experimenters believed that they could not 
be neglected. 
The level of factor 5 is difficult to keep constant because there is no regulation of the 
bath temperature. This factor could be considered as background noise, and the experimenters 
preferred ta treat it as part of the experimental error. This factor is not, therefore studied in the 
initial interpretation (step l), and the six responses of each set of trials will be treated as 
equivalent. 
Domain 
The experimental domain for the five factors studied is shown below (Table 14.1). 
TABLE 14.1 
TRUCK SUSPENSION SPRINGS 
286 
Experimental design 
The engineers had defined four factors and wished to carry out only eight trials. They 
therefore chose a 241 design. Factor 4 is aliased with interaction 123. The reader can see that 
this is a resolution IV design. For each trial, three experiments are run at the low level of factor 
5, and three at the high level. This provides an indication of the background noise introduced 
by this factor for each of the eight trials. 
The engineers want to know the values of interactions 12, 13 and 23, in addition to those 
of the four factors. The three remaining columns of the 2&' design are therefore assigned to 
these three interactions. 
Responses 
The responses must be chosen so as to reflect both the value of the curvature and the 
dispersion ofthe curvature around the mean value. The engineers selected one response for the 
curvature and three responses for the dispersion: 
Curvature 
The mean curvature is selected as the sole response for curvature 
Dispersion of curvature 
The three responses are: 
1 . The variance of the curvature for each set of trials. 
This variance will be indicated by s", with a subscript indicating the set of trials. 
2. A variance fhction, Z, defined by 
z=10 logs2 
3. The signallnoise hnction proposed by Taguchi, Z' 
Z' = 10 log1 Y 2 
s 
Experiments 
Table 14.2 shows the experimental design and the six responses obtained per trial 
The results are interpreted in two steps: 
Step 1: There are four main factors, factor 5 was set at two levels but is not taken into 
account. It is treated as an uncontrolled factor. The six responses from each trial are 
therefore equivalent and are analysed together. 
287 
~ ~~ 
5 - 
7.78 7.78 7.81 
8.15 8.18 7.88 
7.50 7.56 7.50 
7.59 7.56 7.75 
7.94 8.00 7.88 
7.69 8.09 8.06 
7.56 7.62 7.44 
7.56 7.81 7.69 
Step 2: As the influence of factor 5 could not be ignored, the experimenters use the trial 
results to construct a design including al l five factors. As factor 5 is a controlled 
factor, its effect on the responses is determined. 
~~ ~ 
5 + 
7.50 7.25 7.12 
7.88 7.88 7.44 
7.50 7.56 7.50 
7.63 7.75 7.56 
7.32 7.44 7.44 
7.56 7.69 7.62 
7.18 7.18 7.25 
7.81 7.50 7.59 
6 + 
7 
+ 
TABLE 14.2 
EXPERIMENTAL MATRIX 
TRUCK SUSPENSION SPRINGS 
Responses 
3. INTERPRETATION, STEP 1 
3.1. Calculation of responses 
3.1.1. Mean curvature 
For trial number 1, the six values are used to calculate the mean 7, 
1 
6 
yl = -[ 7.78+7.78+7.81+7.50+7.25+7.12] 
The same calculation is performed for the seven remaining sets of trials (see calculations, 
screen 14.1, p. 310). 
288 
Level - 
Level+ 
3.1.2. Dispersion of curvature 
1. Variance 
For trial number 1, the variance 2 is given by the formula: 
(see calculations, screen 14.2, p. 3 11) 
1840 25 12 2 
1880 23 10 3 
(7.78-7.54) 2 +(7.78-7.54)2 +(7.81-7.54)2 +(7.50-7.54)2 +(7.25-7.54)2 +(7.12-7.54)2] 
6-1 
S: = 0.0900 
TABLE 14.3 
EFFECT MATRIX 
TRUCK SUSPENSION SPRINGS 
+ 
+ 
+ 
+ 
289 
2. Eunction Z 
For trial number 1, the Z hnction is Z, : 
(see calculations, screen 14.3, p. 3 12) 
Z, = 10 logsf = 10 log 0.09 
Z,= -10.45 
3. Function Z' (see calculations, screen 14.3, p. 312) 
For trial number I, the Z' hnction is Z;: 
-2 (7.54)2 z;= 10 log% = 10 log ~ 
0.09 s1 
Z;= 28.00 
These four responses (7, 9, Z and Z') calculated from the raw experimental results can 
be used to calculate the effects of each factor. The effects matrix is shown in Table 14.3, which 
also contains the effects and interactions. (see calculations, screens 14.4 - 14.8, p. 313, 314, 
315) 
We can now analyses these results knowing that the influence of factor 5 remains to be 
examined. We will take this factor into account in step 2 of the interpretation. 
3.2. Analysis of results (interpretation, step 1) 
3.2.1. Mean curvature 
The mean standard deviation of one trial is 0.2147 (screen 14.2, p. 3 11). Each effect is 
calculated from the 48 experimental results, giving a standard deviation of 
0.2147 0.2147 
J48 6.928 
- - = 0.031 OE =-- 
The results can be summarized in a table of effects, Table 14.4. (see calculations, screen 
14.5, p. 314) 
290 
TABLE 14.4 
TABLE OF EFFECTS 
TRUCK SUSPENSION SPRINGS 
First interpretation 
1 Mean 7.64 f 0.03 
1 0.11 f 0.03 
2 -0.09 f 0.03 
3 -0.01 L 0.03 
4 0.05 f 0.03 
12 + 34 -0.01 & 0.03 
13 + 24 -0.01 f 0.03 
14 + 23 -0.02 5 0.03 
It appears that 
= Factor 1 (furnace temperature) is influent. 
- Factor 2 (heating time) is influent. 
= Factor 4 (bending time) has a small influence. 
Factor 3 (transfer time) and all the interactions have no influence. 
3.2.2. Dispersion of curvature 
The results can be summarized in a table of effects, Table 14.5 (see calculations, screens 
14.6, 14.7 and 14.8, p. 314, 315) 
29 1 
variance 
0.0460 
-0.0088 
0.0037 
-0.0300 
-0,001 1 
0.0054 
0.0079 
-0.0057 
TABLE 14.5 
Z 
-16.02 
0.29 
2.27 
-4.73 
-1.41 
1.14 
2.57 
-1.73 
TABLE OF EFFECTS 
TRUCK SUSPENSION SPRINGS 
Dispersion of spring curvature 
First Interpretation 
Effect 
Mean 
1 
2 
3 
4 
12 + 34 
13+24 
14 + 23 
Z' 
33.67 
-0.16 
4.63 
-2.28 
1.47 
-1.15 
1.72 
-2.59 
Factor 2 (heating time) had a great influence on the variance of curvature.The fbnctions 
Z and Z' confirm the influence of factor 2, and suggest that factor 3 and interaction 23 could be 
influent. 
3.2.3. Effect of factor 5 on curvature 
Factor 5, which has been considered as background noise until now, remains to be examined. 
As this factor was studied at two levels we can calculate its effect: the average of the low level 
is 7.76, and the high level average is 7.50 (see calculations, screen 14.9, p. 316). 
1 
2 
E5= -[7.50-7.76]= - 0.13 
This factor has the greatest influence on spring leaf curvature! The experimenters 
consider it to be unreasonable to leave it unregulated during fabrication. But, before deciding 
to make the investment required to control it, they check that the objective could be attained. 
They therefore carry out a further analysis of the results. 
292 
Curvature 
7.76 
7.63 
7.50 
\ . -0.13 
-1 +I 
140°F 160°F 
TEMPERATURE (5) 
Figure 14.1: Influence of annealing bath temperature (Factor 5) on curvature 
4. WHAT IS A GOOD RESPONSE FOR DISPERSION? 
We will begin by studying the dispersion of curvature in order to identi@ the settings of 
factors that minimize it. The reader may well ask why three responses were used to define this 
one property. One would have been enough, but it would have to accurately define the 
dispersion. Unfortunately, this ideal response does not exist. In this situation we generally try 
to substitute quantity for quality. But as we will see, it is a vain hope, and each of the 
responses has a weakness. The three responses, variance, logarithm of variance and signal-to- 
noise ratio will be examined individually. 
4.1. Variance 
This is, a priori, a good response as it measures the dispersion of a set of measures 
around the mean. But variance must always be positive, like all algebraic squares. This 
property may not be respected when the mathematical model of factorial design is used. There 
is a risk of having a negative variance. To avoid this problem, statisticians use the logarithm of 
variance. 
293 
4.2. Logarithm of variance 
The logarithmic function, log x, has a great advantage. It can be positive or negative, but 
it always gives a positive x (Figure 14.2). Using it, therefore avoids any problems of impossible 
variance. But, the problem with the log hnction is that it distorts the original information. It 
emphasises small differences in the variance when the variance is very small. As a result, the 
effects depend more on the difference between small variances than on the variances 
themselves . 
Figure 14.2: Plot of the logarithmic function. 
4.3. Comparison of variance and logarithm of variance 
Let us assume that we have to interpret the results of a 22 experimental design. We study 
the dispersion and have two responses, the mean variance and the log of the mean variance. 
The mean variance of the high level of factor 1 (indicated as s z ) is 0.30 and the mean variance 
of the low level is 0.10 (indicated as s!). We can calculate the effects of the factor with the 
two responses .? and 10 log .?: 
Variance 9 
1 
2 
EsZ = -[0.30-0.10]= 4 . 1 0 
294 
z = 10 log s2- 
1 
2 
E, =-[101og0.30-10log0.10] 
1 1 
2 2 
E, = --[-5.23-(-lo)] = - 4.77 = 2.36 
The mean variance for the high level of factor 2 is 0.01, and the mean variance at low 
level is 0.001. We can also calculate the effects of factor 2 with the two responses, variance 
and log of the variance. 
Variance 9 
1 
2 
Es2 = --[0.01-0.001] = +0.0045 
z = 10 log .9 
1 E, = 2[10 log 0.01-10 log 0.0011 
1 
2 
E L = -[-20-(-30)] = 5 
Figure 14.3 compares the two methods, showing the effects of factors on dispersion. 
With variance .-?, factor 1 has the greatest influence, while with 10 log >?-, factor 2 has the 
greatest influence. Thus, interpretation is not easy in this case. 
S2 10 Log s2 
E1=0 1000 
E2=0.0045 
I 
-1 +I 
b 
E2= 5 
E l = 2 36 - 
-1 +I 
Figure 14.3: The response selected (9 or log s2) may influence the evaluation of effects. 
295 
4.4. The signal-to-noise ratio 
The signal-to-noise ratio, Z', is no better. We can write: 
Y2 2 z' = 10 log- = 10 logy2 -10 logs 
s2 
As J 2 varies little, log p2 can be considered to be constant. We can calculate the effects 
E zr of a factor with the function Z': 
EZ,=,((1010gJ2 1 -1010gs:)-(1010gY2 -lOlogs?)] 
L L J 
1 
E,,= [ (-10 logs: ) - (-10 logs- 
or simply 
Thus the function Z' has the same advantages and disadvantages as Z , except that the 
signs are inverted, providing a further risk of error in interpretation. In our study of spring 
leaves, we will use 2 and log 2. Let us now continue with the second stage of interpretation. 
5. INTERPRETATION, STEP 2 
5.1. Calculation of reponses 
The results are completely reanalysed as if there are five factors and sixteen trials. A 25-1 
design is constructed by adding the two levels of factor 5. The preceding 24-1 design is used, 
first with the low level of factor 5 (trials 1-8 in Table 14.6), and then a second time using the 
high level of factor 5 (trials 9-16 of Table 14.6) This new design may be considered as a 24+1-1 
design, which is more simply written as Z5-'. The alias generator is I = 1234, which can be used 
to calculate the contrasts. The four responses ( y , 9, Z and Z') are calculated: screen 14.9 
296 
p.316, screen 14.10 p. 317 and screen 14.1 1 p. 318. The results of these calculations are 
shown in Table 14.6. 
TABLE 14.6 
EXPERIMENTAL MATRIX 
TRUCK SUSPENSION SPRINGS 
1 
2 
3 
4 
5 
6 
7 
8 
9 
10 
11 
12 
13 
14 
15 
16 
Responses 
- 
7.78 
8.15 
7.50 
7.59 
7.94 
7.69 
7.56 
7.56 
7.50 
7.88 
7.50 
7.63 
7.32 
7.56 
7.18 
7.81 
7.78 
8.18 
7.56 
7.56 
8.00 
8.09 
7.62 
7.81 
7.25 
7.88 
7.56 
7.75 
7.44 
7.69 
7.18 
7.50 - 
- 
7.81 
7.88 
7.50 
7.75 
7.88 
8.06 
7.44 
7.69 
7.12 
7.44 
7.50 
7.56 
7.44 
7.62 
7.25 
7.59 
- 
L 
7.79 
8.07 
7.52 
7.63 
7.94 
7.95 
7.54 
7.69 
7.29 
7.73 
7.52 
7.65 
7.40 
7.62 
7.20 
7.63 
3 
273 
12 
104 
36 
496 
84 
156 
3 73 
645 
12 
92 
48 
42 
16 
254 
- 
Z 
-35.22 
-15.64 
-29.21 
-19.81 
-24.44 
-13.04 
-20.76 
-18.06 
-14.28 
-11.90 
-29.21 
-20.34 
-23.19 
-23.73 
-27.87 
-15.94 - 
- 
Z' 
53.06 
33.77 
46.73 
37.43 
42.43 
31.04 
38.30 
35.77 
31.54 
29.67 
46.73 
38.01 
40.57 
41.37 
45.02 
33.60 
The reader will note that controlling factor 5 reduces the standard deviation of one trial 
from 0.21 to 0.13. In general the more factors that are controlled, the smaller the experimental 
error (see calculations screen 14.1 1 p. 3 18). 
5.2. Analysis of results (second step of interpretation) 
The experimental matrix can be used to construct the effects matrix, whose results for 
variance of curvature are shown in Table 14.7 and for curvature in Table 14.8. 
5.2.1. Dispersion of curvature 
The results are shown in Table 14.7 (see calculations, screen 14.17 p. 324, screen 14.18 
p. 325, screen 14.19 p. 325) 
297 
TABLE 14.7 
TABLE OF EFFECTS 
TRUCK SUSPENSION SPRINGS 
Dispersion of curvature 
Second Interpretation 
Effect 
Mean 
1 + 234 
2 + 134 
3 + 124 
4 + 123 
5 + 12345 
12 + 34 
13 + 24 
14 + 23 
15 + 2345 
25 + 1345 
35 + 1245 
45 + 1235 
125 + 345 
135 + 245 
235 + 145 
variance 
0.0165 
0.0092 
-0.0074 
-0.0023 
0.0014 
0.0020 
-0.0032 
0.0003 
0.0060 
-0.00 19 
-0.0017 
-0.0071 
0.0040 
0.0038 
-0.00 18 
0.0076 
Z 
-2 1.40 
4.10 
0.54 
0.47 
0.60 
0.00 
-0.92 
1.45 
-1.23 
-1.28 
-1.30 
-2.41 
0.28 
2.36 
0.94 
1.85 
z' 
39.07 
-3.90 
1.13 
-0.55 
-0.41 
-0.75 
-0.01 
0.91 
-1.48 
1.33 
1.39 
2.38 
-0.26 
-2.37 
-0.91 
-1.88 
These data show that the influent factors are different, depending on w..:ther 2 or log 2 
is used for interpretation. This is not surprising. 
z = 1Olon s2- 
The influent factors and interactions are: 
.Factor 1 . Interaction 35 . Interaction 125 . Interaction 235 
4.10 
2.41 
2.36 
1.85 
298 
Variance .2 
Factor I is again influent, while factor 2 appears to have a negative influence. 
Interactions 35 and 235 are influent,while interaction 125 has little influence. The high value 
of 125 given by Z is due to a large difference between two small values. 
The influent factors and interactions are thus: 
.Factor 1 . Factor 2 
+0.009 
-0.007 
. Interaction 35 -0.007 
Interaction 23 5 +0.007 
The influence of factor 1 on curvature variance is shown in Figure 14.4; the variance is 
smaller if the low level of factor 1 is selected. The influence of factor 2 is shown in Figure 14.5; 
here, in contrast, the high level should be chosen 
S 2 
0.0257 
0.0165 
0.0073 
/ 
+ 
1840 F 1880 F 
FACTOR (I) 
+ 0.0092 i 
Figure 14.4: Influence of furnace temperature (Factor 1) on the variance of curvature. 
299 
S 2 
0.0239 
0.0165 
0.0091 
-1 + 
- 0.0074 
25 sec 23 sec 
FACTOR (2) 
Figure 14.5: Influence of heating time (Factor 2) on the variance of curvature. 
3 00 
5.2.2 Curvature 
The results are shown in Table 14.8 (see calculations screen 14.16 p. 323) 
TABLE 14.8 
TABLE OF EFFECTS 
TRUCK SUSPENSION SPRINGS 
Second interpretation 
Mean 
1 + 234 
2 + 134 
3 + 124 
4 + 123 
5 + 12345 
12 + 34 
13 + 24 
14 + 23 
15 + 2345 
25 + 1345 
35 + 1245 
45 + 1235 
125 + 345 
135 + 245 
235 + 145 
7.63 k 0.02 
0.11 f 0.02 
-0.09 f 0.02 
-0.01 * 0.02 
0.05 k 0.02 
-0.13 f 0.02 
-0.01 f 0.02 
-0.01 * 0.02 
-0.02 f 0.02 
0.04 f 0.02 
0.08 f 0.02 
-0.03 k 0.02 
0.01 f 0.02 
-0.005 * 0.02 
0.02 k 0.02 
-0.02 k 0.02 
It is hardly surprising that the effects are the same as those previously (first 
interpretation) calculated for curvature: they are derived from the same data and treated in the 
same way. The inclusion of factor 5 allows calculation of sixteen contrasts instead of eight and 
reveals new interactions. 
There are three influencing factors: 1, 2 and 5 , and one interaction that cannot be 
ignored, interaction 25. 
30 I 
Curvatu re 
7.74 
7.63 
7.52 
+ 0.11 i 
-1 +I 
1840 F 1880 F 
FACTOR (1) 
Figure 14.6: Influence of furnace temperature (Factor 1) on spring curvature. 
Curvature 
7.72 
7.63 
7.54 \ -0.09 
-1 +I 
25 s 23 s 
TIME (2) 
Figure 14.7: Influence of heating time (Factor 2) on spring curvature. 
3 02 
Factorsor interactions 
Variance of curvature 
Curvature 
Curvature 
7.76 
1 2 3 4 5 23 25 35 235 
+3 0 0:. 0:. .:* 
.:. .:. .:. .:. .:. 
7.63 
7.50 
-1 +I 
140°F 160°F 
1 
-0.13 
I 
TEMPERATURE (5) 
Figure 14.8: Influence of annealing bath temperature (Factor 5) on spring curvature. 
6. OPTIMIZATION 
As the average curvature is low, 7.63 inches, the levels of factors that increase it as much 
as possible should be selected. But we must also keep the variance of curvature to a minimum. 
Table 14.9 shows the elements of the discussion that we will use to choose the factor levels, 
listing the significant factors and interactions for the corresponding responses. 
TABLE 14.9 
TRUCK SUSPENSION SPRINGS 
Factors and interactions significantly influencing the responses 
3 03 
The high level of factor 4 may be chosen to increase curvature. It is more difficult to 
choose the levels of the four other factors as the interactions must be taken into account. The 
easiest way to resolve this problem is to write mathematical models for the two responses. 
Curvature = 7.63 + 0.1 1 x1 - 0.09 x2 + 0.05 x4 - 0.13 xs + 0.08 x2 x5 
Variance = 0.0165 + 0.009 x, - 0.007 x2 + 0.006 x2 x3 - 0.007 x3 xs + 0.007 x2 x3 xS 
The two responses, curvature and variance of curvature, are calculated (see calculations 
screen 14.20 p. 326, screen 14.21 p. 328, screen 14.22 p. 329, screen 14.23 p. 330) for all the 
possible combinations of the four factors 1, 2, 3 and 5 (Table 14.10). Factor 4 is held at the 
high level. 
TABLE 14.10 
TRUCK SUSPENSION SPRINGS 
Calculation of curvature and dispersion of curvature 
for all combinations of x1 x2 x3 and xs 
Case 
no 
1 
2 
3 
4 
5 
6 
7 
8 
9 
10 
11 
12 
13 
14 
15 
16 
-1 
+1 
-1 
+I 
-1 
+I 
-1 
+1 
-1 
+1 
-1 
+I 
-1 
+1 
-1 
+I - 
-1 
-1 
+1 
+1 
-1 
-1 
+1 
+1 
-1 
-1 
+1 
+1 
-1 
-1 
+1 
+I - 
-1 
-1 
-1 
-1 
+1 
+1 
+1 
+1 
-1 
-1 
-1 
-1 
+1 
+1 
+1 
+1 - 
-1 
-1 
-1 
-1 
-1 
-1 
-1 
-1 
+1 
+1 
+1 
+1 
+1 
+1 
+1 
+1 - 
~~ 
Dispersion 
of curvature 
65 
245 
-55 
125 
225 
405 
65 
245 
345 
525 
-5 5 
125 
-55 
125 
65 
245 
Curvature 
7.87 
8.09 
7.53 
7.75 
7.87 
8.09 
7.53 
7.75 
7.45 
7.67 
7.43 
7.65 
7.45 
7.67 
7.43 
7.65 
The results in the table show that an eight-inch curvature is obtained in two cases: 
3 04 
1. Case 2: I + 2- 3- 4+ 5- produced a curvature of 8.09 inches with a variance 
of 0.0245 
2. Case 6: I + 2- 3+ 4+ 5- gives the same curvature (8.09 inches) but the 
variance of curvature is greater, at 0.0405. 
It would thus be best to select the low level of factor 3 to minimize the variance of 
curvature. This selection has no influence on the curvature itself, as curvature is independent of 
xj. Examination of Table 14.6 shows that Case 2 is the same as Trial number 2. The 
experimental values confirm the values calculated from the model. The study could therefore 
be stopped at this point and these setting used. But perhaps we could try to reduce the 
variance of curvature still further. For this purpose, we adopt a special representation of a four 
dimensional space. The levels of factors 1 and 2 are represented as in a 22 design (Figure 14.9). 
We then plot the isoresponse curves for curvature for each level of the pair of factors 1 and 2 
in the plane of factors 3 and 5. 
160°F 
(5) 
140°F 
160°F 
(5) 
140°F 
12" (3) 10" 
(2) U 
160°F / (l) \ 
(5 ) 
7.8 
140°F 140°F 
12" (3) lo" 12l (3) 10" 
Figure 14.9: Isoresponse curves of curvature variance. 
305 
This diagram shows that a curvature of 8 inches can only be obtained in the region of 
comer where factor 1 = +1 and factor 2 = -1. If we assume that the smallest possible value of 
factor 5 is -1, we can calculate the location of points where curvature is 8 inches within the 
space of factors 1 and 2. For this we write that curvature is eight inches. 
or 
8 = 7.63 + 0.1 1xl - 0.09 x2 + 0.05 ~4 - 0.13 ~5 + 0.08 ~2 ~5 
The trajectory where the curvature is 8 inches when x5 = -1 and x4 = +I is given by: 
8 = 7.63 + 0.1 1 x1 - (0.09 + 0.08) ~2 + 0.05 + 0.13 
0.1 7 x2 = 0.1 1 x1 - 0.19 
or 
11x1 19 
x2 =--- 17 17 
this relationship is represented by a straight line (Figure 14.10). It shows all the possible 
settings of factors 1 and 2 to obtain a curvature of eight inches. The final choices of setting will 
depend on the variance, which must be as small as possible. We have: 
V 0.0165 + 0.009 x1 - 0.007 x2 + 0.006 x1 x3 - 0.007 ~3 x5 + 0.007 ~2 ~3 ~5 
Ifwe apply the preceding hypothesis x3 = -1, x5 = -1 and x2 = 1 1x1/17-19/17, we get: 
V = 0.0162 + 0.0051 x1 
This relationship can be used to place a scale on the straight line found previously. The 
different values of the variance of curvature are shown on Figure 14.10 
3 06 
Factor 2 
+ I 
- 1 
A;;l*; Factor 1 
v = 0.0213 
v= 0.0171 
Figure 14.10: Optimizing the variance of curvature. 
The smallest variance is given when xz is at its low level and x1 equals 0.18. If we 
remain within the domain studied, the settings providing a curvature of eight inches with the 
smallest possible variance are (in coded units): 
x, = 0.18 
x2= -1 
x 3 = -1 
x4= +1 
x5= -1 
In real-world units these are: 
.Factor I 1863.6 deg F . Factor 2 25 seconds . Factor 3 I2 seconds . Factor 4 3 seconds 
Factor 5 I30 - 150 deg F 
If the manufacturing constraints allow us to move outside the experimental domain, the 
investigators should be able to reduce the variance of curvature still further while maintaining 
an average curvature of 8 inches. They could: 
Reduce the furnace temperature (factor 1). 
Increase the heating time (factor 2). 
More closely regulate and reduce the annealing bath temperature (factor 5) . 
307 
Whatever the results of the theoretical study, trials must be carried out to continn that 
the predictions are accurate andthat the objective could be attained. 
Conclusion 
a 
rli can be reduced by setting: 
iii 0 The furnace heating time to 25 sec. 
II 
fi sec. 
The dispersion of the curvature of truck suspension spring leaves 
0 The furnace temperature at 1863 deg F. 
0 The transfer time between furnace and bending machine to 12 
0 The bending time to 3 sec. 
The annealing bath temperature cannot be considered to be 
I! background noise as it strongly influences the degree of curvature. If it 
fr is not regulated all the other efforts are worthless Therefore the 
41 required investment must be considered. Thus, the annealing bath 
B temperature should be set at the lowest temperature used in this study, 
130 deg F. 
Confirmatory trials should be run to verify the predicted settings 
308 
RECAPITULATION 
This study of the curvature of truck spring leaves has highlighted several points. 
1 . The difficulty and the importance of interpretation. The experimenter must make the 
results speak, which requires considerable calculation to extract their useful 
information content. Interpretation is never automatic; it requires intelligence and 
imagination. The experimenter must select the most appropriate hypothesis in order to 
present clear, useful conclusions. 
2. The use of variance as a response. This technique is often used to improve quality. 
The first step is to reduce dispersion by choosing the appropriate levels that influence 
it; the other factors are then adjusted to reach the target value. 
3. The selection of the right response is often tricky, and requires a great deal of care. 
The variance example clearly illustrates this. 
4. The setting of a factor influencing the response studied can reduce experimental error. 
The more factors that are controlled, the more the experimental error is reduced. 
The next part of the chapter covers the details of calculation. It shows how to obtain the 
results used in the first part of the chapter. We recommend that this second section should be 
accompanied by the calculations run on a microcomputer. 
CHAPTER 14 (CONTINUED) 
D E T A I L E D C A L C U L A T I O N S F O R 
T H E T R U C K S U S P E N S I O N 
S P R I N G S E X A M P L E 
The calculations are readily performed using a spreadsheet. This example was prepared 
with Lotus 123 running on a PC compatible microcomputer. The reader can transpose the 
calculations to hidher particular softwarehardware system. 
1. CALCULATION FOR THE FIRST INTERPRETATION 
a) Calculating the mean curvature for each trial 
is calculated by placing the instruction : 
Open the first worksheet : sheet 1, and enter the 48 trial results (screen 14.1). The mean 
@AVG(B9. .G9) 
310 
in cell 19. The other means are calculated by copying this instruction to cells I10 to 116. 
SCREEN 14.1 
Calculation of mean curvature for each trial 
Trial 
no 
8 
1 
2 
3 
4 
5 
6 
7 
8 
Y1 
7.78 
8.15 
7.50 
7.59 
7.94 
7.69 
7.56 
7.56 
Y2 
7.78 
8.18 
7.56 
7.56 
8.00 
8.09 
7.62 
7.81 
Y3 
7.81 
7.88 
7.50 
7.75 
7.88 
8.06 
7.44 
7.69 
Y4 
7.50 
7.88 
7.50 
7.63 
7.32 
7.56 
7.18 
7.81 
Y5 
7.25 
7.88 
7.56 
7.75 
7.44 
7.69 
7.18 
7.50 
Y6 
7.12 
7.44 
7.50 
7.56 
7.44 
7.62 
7.25 
7.59 
Mean 
7.540C 
7.9017 
7.520C 
7.640C 
7.670C 
7.785C 
7.3715 
7.660C 
18 
19 
2 0" 
b) Calculating the curvature variance 
There are several ways of doing this calculation. This is one way. The data on screen 
14.1 are used to construct the deviation squared table (y, -Fil2. The term in cell B25 in 
screen 14.2 is obtained from the instruction : 
(B9 - $19)*(B9 - $19) or (B9 - $19)*2 
and copying it to cells B25 to G32. The variance, .$, of a trial is obtained by adding the squares 
of the differences and dividing the sum by 6 - 1. For trial number 1, the instruction : 
@SUM(B25. .G25)/5 
is placed in cell 125, and copied to cells I26 to I32 (screen 14.2) 
311 
SCREEN 14.2 
Calculation of curvature variance, SZ 
A 
standard deviation 0.214681 
VARIANCE CALCULATION 
Variance 
0.0576 0 .0576 0 . 0 7 2 9 0 . 0 0 1 6 
0 . 0 6 1 7 0 . 0 7 7 5 0 .0005 0 .0005 
0 . 0 0 0 4 0 . 0 0 1 6 0 .0004 0 .0004 
0 . 0 0 2 5 0 .0064 0 . 0 1 2 1 0 . 0 0 0 1 
0 . 0 7 2 9 0 . 1 0 8 9 0 . 0 4 4 1 0 . 1 2 2 5 
0 .0090 0 . 0 9 3 0 0 .0756 0 .0506 
0 .0355 0 . 0 6 1 7 0 .0047 0 . 0 3 6 7 
0 .0100 0 .0225 0 . 0 0 0 9 0 . 0 2 2 5 
0 . 0 8 4 1 
0 . 0 0 0 5 
0 . 0 0 1 6 
0 . 0 1 2 1 
0 .0529 
0 .0090 
0 .0367 
0 .0256 
0 . 1 7 6 4 
0 . 2 1 3 1 
0 .0004 
0 .0064 
0 .0529 
0 . 0 2 7 2 
0 .0148 
0 .0049 
0 .09004 
0 . 0 7 0 7 3 
0.0009E 
0 .00792 
0.09084 
0 .05291 
0 .03801 
0 .01728 
mean variance 0.046088 
These calculations can be used to obtain the mean variance of all the trials : the variances 
in column I are added together and divided by 8 using the instruction 
@SUM(I25.. I3 2)/8 
placed in cell 135. The square root of the mean variance gives the standard deviation of an 
individual response. It is obtained by placing : 
@SQRT(I35) 
in cell I37 (screen 14.2) 
c) Calculating the Z function 
The variance in cell I25 is used to calculate the Z hnction for trial number 1 by placing 
the instruction : 
lO*@LOG(125) 
312 
in cell L25 (screen 14.3). The instruction is copied to obtain the eight Z hnctions (L25 to 
L32). 
SCREEN 14.3 
Calculation of the responses s2, Z and Z' 
Variance z Z' 
0 . 0 9 0 0 4 - 1 0 . 4 5 5 6 2 8 . 0 0 3 
0 . 0 7 0 7 3 - 1 1 . 5 0 3 5 2 9 . 4 5 8 
0 .00096 - 3 0 . 1 7 7 2 4 7 . 7 0 1 
0 . 0 0 7 9 2 - 2 1 . 0 1 2 7 3 8 . 6 7 4 
2 8 . 1 1 3 0 . 0 9 0 8 4 - 1 0 . 4 1 7 2 
0 . 0 5 2 9 1 - 1 2 . 7 6 4 6 3 0 . 5 9 0 
0 . 0 3 8 0 1 - 1 4 . 2 0 0 2 31.551 
0 . 0 1 7 2 8 - 1 7 . 6 2 4 2 3 5 . 3 0 9 
d) Calculating the 2' function 
For trial number 1, js, (cell 19) and sf (cell 125) are used to calculate Z' with the 
instruction : 
1 O*@LOG(I9*19/125) 
in cell 025. The other values for Z are obtained by copying the formula to cells 026 to 032 
(screen 14.3). 
e) Calculating the effects 
A new worksheet is opened (sheet 2) and the matrix of effects is entered (cells B9 to 116, 
screen 14.4). The responses from worksheet 1 are copied to cells f9 .. M16, alongside the 
effects matrix (screen 14.4). 
313 
SCREEN 14.4 
Effects matrix of the z4-' design plus the four calculated responses 
EFFECT MATRIX 
4 = 
1 2 3 12 13 23 123 
-1 -1 -1 1 1 1 -1 
1 -1 -1 -1 -1 1 1 
-1 1 -1 -1 1 -1 1 
1 1 -1 1 -1 -1 -1 
-1 -1 1 1 -1 -1 1 
1 -1 1 -1 1 -1 -1 
-1 1 1 -1 -1 1 -1 
1 1 1 1 1 1 1 
I CURV. 
1 1.54 
1 7 . 9 0 
1 7 .52 
1 1 . 6 4 
1 7 .67 
1 7 .79 
1 7 .37 
1 7 .66 
82 
0.090 
0 . 0 7 1 
0 . 0 0 1 
0 . 0 0 8 
0 . 0 9 1 
0 .053 
0 .038 
0 . 0 1 7 
z Z' 
- 1 0 . 5 28 .00 
-11 .5 29 .45 
-30 .2 47 .70 
-21 .0 38 .67 
- 1 0 . 4 2 8 . 1 1 
-12.8 30 .58 
- 1 4 . 2 31 .55 
-17 .6 35 .30 
The data are then used to calculate the effects of each factor as follows. Using the mean 
curvature as an example, the instruction : 
+$J9*B9 
in cell B26 gives the product of the mean curvature of trial 1 multiplied by - 1. This instruction 
is copied to the cell range B26 _ . I33 to give all the products. The columns are then added and 
divided by eight to give the effect (screen 14.5). 
The instruction in cell B35 : 
gives the effect of factor 1. The effects of the other factors are obtained by copying this 
instruction to cells B35 to I35 (screen 14.5). 
314 
SCREEN 14.5 
Calculation of the effects of factors on the curvature 
B26 : + $J9*B9 
CURVATLTRE 
-7.54 
7.90 
-7.52 
1.64 
-7.67 
1.79 
-7.31 
7.66 
- - - - - - - -. 
2 
-7.54 
-7.90 
7. 52 
7. 64 
-7.67 
-7. 79 
I. 37 
7. 66 
. - - - - - - 
3 12 13 23 
-7.54 1.54 7.54 7.54 
-7.50 -7.90 -7.90 7.90 
-7.52 -7.52 7.52 -7.52 
-1.64 7.64 -7.64 -1.64 
7.67 1.61 -7.67 -1.67 
7.79 -1.19 7.19 -1.79 
1.31 -1.31 -7.37 1.31 
7.66 1.66 1.66 1.66 
- - _ - _ - _ _ _ _ - - - __ - - - - - ------_ - 
4=123 
-7.54 
7.90 
7.52 
-1.64 
7. 67 
-7.79.-7.31 
7.66 
- - - _ _ _ -- 
1 
I. 54 
7.90 
7. 52 
I. 64 
7. 67 
1.19 
1.37 
1.66 
0.1106 -0.0881 -0.0143 -0.0085 -0.0098 -0.0177 0.0518 7.63601 I 35 
The effects of factors for the three other responses are obtained in the same way using an 
analogous series of instructions. These instructions are indicated in the top left-hand cell of 
each screen. 
SCREEN 14.6 
Calculation of effects of factors on curvature variance 
B44 : i $K9*B9 
VARIANCE OF THE CURVATURE 
44 1 -0.0900 -0.0900 -0.0900 0.0900 0.0500 0.0900 -0.0900 0.0900 
45 2 0.0707 -0.0707 -0.0707 -0.0707 -0.0707 0.0707 0.0707 0.0707 
46 3 -0.0010 0.0010 -0.0010 -0.0010 0.0010 -0.0010 0.0010 0.0010 
7 4 0.0079 0.0079 -0.0079 0.0079 -0.0079 -0.0079 -0.0079 0.0079 
5 -0.0908 -0.0908 0.0908 0.0908 -0.0908 -0.0908 0.0908 0.0908 
6 0.0529 -0.0529 0.0529 -0.0529 0.0529 -0.0529 -0.0529 0.0529 
I -0.0380 0.0380 0.0380 -0.0380 -0.0380 0.0380 -0.0380 0.0380 
8 0.0173 0.0173 0.0173 0.0173 0.0173 0.0173 0.0173 0.0173 
315 
SCREEN 14.7 
Calculation of the effects of factors on function Z 
B62 : + $L9*B9 
EQNCTION Z 
23 4=123 I 
1 1 0 . 4 6 1 0 . 4 6 1 0 . 4 6 -10 .46 - 1 0 . 4 6 -10 .46 1 0 . 4 6 -10.4E 
2 -11 .50 1 1 . 5 0 1 1 . 5 0 1 1 . 5 0 1 1 . 5 0 - 1 1 . 5 0 -11 .50 -11.5C 
3 30 .18 -30 .18 3 0 . 1 8 30 .18 -30 .18 30 .18 - 3 0 . 1 8 -30 .18 
4 - 2 1 . 0 1 - 2 1 . 0 1 2 1 . 0 1 - 2 1 . 0 1 2 1 . 0 1 2 1 . 0 1 2 1 . 0 1 - 2 1 . 0 1 
5 1 0 . 4 2 1 0 . 4 2 -10 .42 - 1 0 . 4 2 1 0 . 4 2 1 0 . 4 2 - 1 0 . 4 2 -10 .42 
6 -12 .76 1 2 . 7 6 -12 .76 1 2 . 7 6 - 1 2 . 7 6 1 2 . 7 6 1 2 . 7 6 -12.7E 
1 4 . 2 0 -14 .20 - 1 4 . 2 0 1 4 . 2 0 1 4 . 2 0 - 1 4 . 2 0 1 4 . 2 0 -14.2C 
8 - 1 7 . 6 2 -17 .62 - 1 7 . 6 2 -17 .62 - 1 7 . 6 2 - 1 7 . 6 2 - 1 7 . 6 2 -17 .62 
0 . 2 9 3 -4.734 2 . 2 6 8 1 . 1 4 2 - 1 . 7 3 6 2 . 5 7 3 - 1 . 4 1 1 -16 .019 
_ _ _ _ _ _ - _ _ - _ - - _ -_----- ------- - - _ _ _ _ _ __----- ------- - _ _ _ - - - 
SCREEN 14.8 
Calculation of the effects of factors on function Z' 
B80 : + $M9*B9 
F"CT1ON Z ' 
23 4=123 I 
1 -28.00 -28 .00 -28 .00 2 8 . 0 0 2 8 . 0 0 2 8 . 0 0 -28 .00 28 .00 
2 2 9 . 4 6 -29 .46 -29 .46 - 2 9 . 4 6 - 2 9 . 4 6 2 9 . 4 6 2 9 . 4 6 29.46 
3 -47 .70 47 .70 -47 .70 -47 .70 4 7 . 7 0 -47 .70 4 7 . 7 0 47 .70 
4 3 8 . 6 7 3 8 . 6 7 - 3 8 . 6 7 3 8 . 6 7 -38 .67 -38 .67 -38 .67 3 8 . 6 7 
5 - 2 8 . 1 1 - 2 8 . 1 1 2 8 . 1 1 2 8 . 1 1 - 2 8 . 1 1 - 2 8 . 1 1 2 8 . 1 1 2 8 . 1 1 
6 3 0 . 5 9 -30 .59 3 0 . 5 9 - 3 0 . 5 9 3 0 . 5 9 -30 .59 -30 .59 3 0 . 5 9 
7 -31.55 3 1 . 5 5 3 1 . 5 5 - 3 1 . 5 5 - 3 1 . 5 5 3 1 . 5 5 - 3 1 . 5 5 3 1 . 5 5 
8 3 5 . 3 1 3 5 . 3 1 35.31 3 5 . 3 1 3 5 . 3 1 3 5 . 3 1 3 5 . 3 1 3 5 . 3 1 
_ _ _ _ _ _ ------ ------- ------_ ------- ------_ - - _ _ _ _ _ - - -_-_- 
-0 .167 4.634 -2 .284 -1 .150 1 . 7 2 6 - 2 . 5 9 5 1 . 4 7 0 3 3 . 6 7 5 
316 
f) Calculating the mean curvature at the low level of factor 5 
The data are contained in columns B, C and D of worksheet 1 (screen 14.1). They are 
used to calculate the mean curvature by placing the instruction : 
@AVG(B9. .D 16) 
in cell El8 (screen 14.9) 
g) Calculating the mean curvature at the high level of factor 5 
Columns F, G and H are treated in the same way using the instruction 
@AVG(F9..H16) 
in cell I18 (screen 14.9) 
SCREEN 14.9 
Calculation of mean curvatures at levels 5+ and 5- 
CURVATDRES AT LEVELS 5- AND 5+ 
5+ Mean 
1 1.78 7.78 1.81 1.19 1.50 1.25 1.12 1.29 1.54 
2 8.15 5.18 7.88 8.01 7.88 1.88 7.44 7.73 7.90 
3 1.50 1.56 1.50 1.52 1.50 1.56 1.50 1.52 1.52 
4 1.59 1.56 7.15 7.63 7.63 7.15 7.56 7.64 7.64 
5 7.94 8.00 7.88 7.94 7.32 7.44 1.44 1.40 1.67 
6 7.69 8.09 8.06 1.94 7.56 7.69 1.62 7.62 1.78 
7 7.56 7.62 7.44 7.54 7.18 7.18 1.25 7.20 7 .37 
8 7.56 7.81 1.69 7.68 7.81 7.50 7.59 7.63 7.66 
2. CALCULATION FOR THE SECOND INTERPRETATION 
Two new worksheets are opened; worksheet 3 is used to calculate the elaborated 
responses from the raw responses, while worksheet 4 is used to calculate the effects. The 
calculations themselves are analogous to the ones camed out for the Z4-' design. 
317 
a) Calculating the mean curvature for each trial 
Each trial now contains only three results. The data in worksheet 1 are copied to 
worksheet 3. The 48 results on 16 lines occupy the range B9..D24 (screen 14.10). The mean 
curvature for trial number 1 is calculated with the instruction : 
@AVG(B9..D9) 
in cell F9, and this instruction is copied to cells F10..F24. 
SCREEN 14.10 
Calculation of mean curvatures for the trials in the $'-' design 
T r i a l 
no 
1 
2 
3 
4 
5 
6 
7 
8 
9 
1 0 
11 
1 2 
13 
14 
1 5 
1 6 
Y1 
7.78 
8 . 1 5 
7 .50 
7 .59 
7 .94 
7 . 6 9 
7 . 5 6 
7 . 5 6 
7 . 5 0 
7 .88 
7 . 5 0 
1 . 6 3 
7.32 
7 .56 
7 .18 
7 . 8 1 
Y2 
7 .78 
8 .18 
7 .56 
7 . 5 6 
8 .00 
8 . 0 9 
7 . 6 2 
7 . 8 1 
7 . 2 5 
7 .88 
7 .56 
7 . 7 5 
7 .44 
7 .69 
7 .18 
7 .50 
Y3 
7 . 8 1 
7 .88 
7 .50 
7 . 7 5 
7 .88 
8 . 0 6 
7 . 4 4 
7 . 6 9 
7 .12 
7 .44 
7 .50 
7 . 5 6 
7 . 4 4 
7 .62 
7 . 2 5 
7 .59 
M e a n 
7 . 7 9 
8 .07 
1 . 5 2 
7 . 6 3 
7 .94 
7 .94 
7 .54 
7 . 6 8 
1 . 2 9 
1 . 7 3 
7 .52 
7 .64 
7 . 4 0 
7 . 6 2 
7 .20 
7 . 6 3 
b) Calculating s2, 2 and 2' 
The squares of the differences are calculated in cells H9..J24 using the instruction (screen 
14.11) : 
copied to all the cells of this range (screen 14.11). The curvature variance of trial number 1 is 
obtained by placing the following instruction in cell L9 : 
@SUM(H9. .J9)/2 
This instruction is copied to cells L9 to L24 (screen 14.1 I). 
318 
SCREEN 14.11 
Calculation of variances 
1 7.78 
2 8.15 
3 7 .50 
4 7 . 5 9 
5 7 .94 
6 7 .69 
7 7 . 5 6 
8 7 . 5 6 
9 7 .50 
1 0 7 .88 
11 7.50 
7.78 
8.18 
7 . 5 6 
7 . 5 6 
8 . 0 0 
8 . 0 9 
7 . 6 2 
7 . 8 1 
7 .25 
7.88 
7 . 5 6 
7 . 8 1 7 .79 
7.88 8.07 
7 .50 7.52 
7 .75 7 .63 
7 .88 7 . 9 4 
8 .06 7.94 
7 . 4 4 7 . 5 4 
7 . 6 9 7 . 6 8 
7 .12 7 .29 
7 . 4 4 7 .73 
7 .5 7 . 5 2 
12 7 .63 7 .75 7 . 5 6 7 . 6 4 
1 3 7.32 7.44 7.44 7 .40 
square deviation Variance 
0 . 0 0 0 1 
0 .0064 
0.0004 
0 .0019 
0 .0000 
0.0659 
0 .0004 
0 . 0 1 6 0 
0 . 0 4 4 1 
0 . 0 2 1 5 
0 .0004 
0 .0003 
0 .0064 
0 .0040 
0.0005 
0 .0312 
0 . 0 0 0 1 
0 . 0 1 2 1 
0 .0016 
0 .0054 
0 .0036 
0.0205 
0 .0064 
0 .0152 
0 . 0 0 1 6 
0 . 0 2 1 5 
0 .0016 
0 .0107 
0 . 0 0 1 6 
0 .0044 
0 .0005 
0 .0178 
0.0004 
0 . 0 3 6 1 
0.0004 
0 . 0 1 3 6 
0 .0036 
0.0128 
0 .0100 
0 .0000 
0 . 0 2 8 9 
0 . 0 8 6 0 
0 .0004 
0.0075 
0 .0016 
0 .0000 
0.0022 
0 .0019 
1 4 7 .56 7 .69 7 .62 7.62 
1 5 7 .18 7 . 1 8 7 .25 7 . 2 0 
1 6 7 . 8 1 7 .5 7 . 5 9 7 . 6 3 
Mean variance 
Standard deviation 
0.00030 
0 .02730 
0.00120 
0 .01043 
0.00360 
0 .04963 
0 .00840 
0 .01563 
0 .03730 
0 .06453 
0 .00120 
0 .00923 
0 .00480 
0.00423 
0.00163 
0 .02543 
0 .01655 
0 .12866 
The mean variance is obtained by placing : 
@SUM(L9.. L24)/ 16 
in cell L26, and the standard deviation ofeach response using the instruction 
BSQRT(L26) 
in cell L28 (screen 14.1 1) 
The hnctions Z and Z' are calculated from the variance using the instructions (screen 
14.12) : 
10*@LOG(L9) in column P to obtain Z 
3 19 
I O*@LOG(F9*F9/L9) in column R to obtain Z'. 
The expression 10 log y 2 can also be calculated to check that it varies little (column N in 
screen 14.12) 
SCREEN 14.12 
Calculation of 9, Z and Z' 
0.00030 
0.02730 
0.00120 
0.01043 
0.00360 
0.04963 
0.00840 
0.01563 
0.03730 
0.06453 
0.00120 
0.00923 
0.00480 
0.00423 
0.00163 
0.02543 
17.83075 
18.13747 
17.52436 
17.65428 
17.99641 
18.00370 
17.54743 
17.71476 
11.25455 
17.76733 
17.52436 
17.66944 
17.38463 
17.64290 
17.15067 
17.65428 
-35.22879 
-15.63837 
-29.2 0819 
-19.81577 
-24.43697 
-13.04227 
-20.75721 
-18.05948 
-14.28291 
-11.90216 
-29.20819-20.34641 
-23.18759 
-23.73318 
-27.86925 
-15.94597 
53.05954 
33.77584 
46.73254 
37.4700: 
42.43335 
31.04597 
38.30463 
35.77425 
31.53746 
29.66945 
46.73254 
38.01586 
40.51222 
41.37607 
45.01992 
33.60025 
320 
c) Preparing the effects matrix 
The effects matrix of the 25-1 design is entered into worksheet 4, cells B9..Q24. The 
signs ofthe interaction columns are calculated according to the signs rule (screen 14.13). 
SCREEN 14.13 
Effects matrix of the 2'-' design 
no 1 2 3 123 5 12 13 14 15 25 35 45 125 135 235 I 
1 -1 -1 -1 -1 -1 1 1 1 1 1 1 1 -1 -1 -1 1 
1 -1 -1 1 -1 -1 -1 1 -1 1 1 -1 1 1 -1 1 
3 -1 1 -1 1 -1 -1 1 -1 1 -1 1 -1 1 -1 1 1 
1 1 -1 -1 -1 1 -1 -1 -1 -1 1 1 -1 1 1 1 
5 -1 -1 1 1 -1 1 -1 -1 1 1 -1 -1 -1 1 1 1 
1 -1 1 -1 -1 -1 1 -1 -1 1 -1 1 1 -1 1 1 
7 -1 1 1 -1 -1 -1 -1 1 1 -1 -1 1 1 1 -1 1 
1 1 1 1 -1 1 1 1 -1 -1 -1 -1 -1 -1 -1 1 
9 -1 -1 -1 -1 1 1 1 1 -1 -1 -1 -1 1 1 1 1 
10 1 -1 -1 1 1 -1 -1 1 1 -1 -1 1 -1 -1 1 1 
11 -1 1 -1 1 1 -1 1 -1 -1 1 -1 1 -1 1 -1 1 
12 1 1 -1 -1 1 1 -1 -1 1 1 -1 -1 1 -1 -1 1 
13 -1 -1 1 1 1 1 -1 -1 -1 -1 1 1 1 -1 -1 1 
14 1 -1 1 -1 1 -1 1 -1 1 -1 1 -1 -1 1 -1 1 
15 -1 1 1 -1 1 -1 -1 1 -1 1 1 -1 -1 -1 1 1 
16 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 
32 1 
The experimental results are copied to R9..T24 fiom worksheet 3, and the means of the 
trials entered in column U (screen 14.14). 
SCREEN 14.14 
Calculation of mean curvatures 
Mean 
8.00 7.88 7.94 
8.09 8.06 7.94 
7.62 7.44 1.54 
7.81 7.69 7.68 
7.25 7.12 7.29 
7.88 7.44 7.13 
7.52 
7.75 7.56 1.64 
7.44 7.44 7.40 
3 22 
The variance is shown in column AA, Z in column AC and Z in column AE (screen 
14.15). 
SCREEN 14.15 
Calculation of variance, Z and Z' 
0.0001 
0.0064 
0.0004 
0.0019 
0.0000 
0.0658 
0.0004 
0.0160 
0 . 0 4 4 1 
0.0215 
0 .0004 
0.0003 
0.0064 
0.0040 
0.0005 
0.0312 
0 . 0 0 0 1 
0 . 0 1 2 1 
0.0016 
0.0054 
0 .0036 
0.0205 
0.0064 
0 .0152 
0 .0016 
0.0215 
0 .0016 
0.0107 
0.0016 
0 .0044 
0 .0005 
0.0178 
deviation square Variance Z 
0.0004 
0 .0361 
0.0004 
0.0136 
0.0036 
0.0128 
0.0100 
0.0000 
0 .0289 
0.0860 
0.0004 
0.0075 
0 .0016 
0.0000 
0.0022 
0.0019 
0.00030 
0.02730 
0.00120 
0 .01043 
0 .00360 
0.04963 
0 .00840 
0.01563 
0.03730 
0 .06453 
0.00120 
0.00923 
0 .00480 
0.00423 
0.00163 
0 .02543 
-35 .2 
-15 .6 
- 2 9 . 2 
-19.8 
-24.4 
-13 .0 
-20.8 
- 1 8 . 1 
-14 .3 
-11.9 
-29.2 
-20 .3 
-23.2 
-23.7 
-27 .9 
-15.9 
5 3 . 1 
3 3 . 8 
4 6 . 1 
3 7 . 5 
42.4 
31 .0 
3 8 . 3 
35 .8 
3 1 . 5 
29.7 
4 6 . 1 
3 8 . 0 
4 0 . 6 
41 .4 
45.0 
3 3 . 6 
man variance 0.016554 
atandard deviation 0.128663 
3 23 
d) Calculating the effect of factors on curvature 
the instruction: 
The effects are calculated by multiplying the effects matrix by the mean curvatures using 
+$U9*B9 
copied to the range B32..Q47, then adding the columns and dividing this sum by 16 using the 
instruction (cell B49): 
@SUM(B32..B47)/16 
which is copied to cells B49 - 449 (screen 14.16). 
SCREEN 14.16 
Calculation of the effects of factors on curvature 
1 2 3 123 5 12 13 14 15 25 35 45 125 135 235 
1-1.79-1.19 -1.19-1.79-1.19 1.19 1.79 7.19 1.79 1.19 1.19 1.19-1.79-1.19-1.79 1.1 
2 8.01 -8.07 -8.07 8.01 -8.01-8.07-8.07 8.01-8.07 8.07 8.07 -8.07 8.07 8.07 -8.07 8.0 
3 -1.52 1.52 -1.52 1.52 -7.52-7.52 1.52-7.52 7.52-1.52 1.52-7.52 7.52-7.52 1.52 1.5 
4 1.63 1.63 -1.63-1.63-7.63 1.63-1.63-1.63-7.63-1.63 1.63 1.63-7.63 1.63 7.63 1.6 
5 -7.94 -1.94 1.94 7.94 -1.94 1.94 -1.94 -1.94 1.94 1.94 -1.94 -1.94 -1.94 1.94 1.94 7.9 
6 1.95 -1.95 1.95 -1.95 -1.95 -1.95 1.95 -1.95 -7.95 1.95 -1.95 1.95 1.95 -1.95 7.95 7 .9 
1 -1.54 1.54 1.54-7.54 -1.54-1.54-7.54 7.54 7.54 -7.54-7.54 7.54 1.54 7.54 -1.54 7.5 
9 -1.29-7.29 -1.29-7.29 7.29 1.29 1.29 7.29-1.29-1.29-1.29-7.29 1.29 1.29 1.29 1.2 
8 1.69 1.69 7.69 1.69-7.69 1.69 1.69 7.69-7.69-1.69-1.69-1.69-1.69 -1.69-7.69 1.6 
10 1.13-7.73 -7.73 1.13 1.13-1.13-1.13 1.13 1.73-1.13-7.13 1.13-7.13-1.73 1.13 1.1 
11-1.52 7.52 -1.52 7.52 1.52-1.52 1.52-7.52-1.52 1.52-1.52 1.52-1.52 7 . 5 2 -1.52 1.5 
12 1.65 7.65 -1.65-1.65 7.65 1.65-1.65-7.65 7 . 6 5 1.65-7.65-7.65 1.65-1.65-7.65 1.6 
13-1.40-1.40 1.40 7.40 1.40 1.40-1.40-7.40-1.40-1.40 7.40 1.40 1.40-7.40-7.40 7.4 
14 1.62 -7.62 7.62-7.62 7.62-7.62 1.62-1.62 7.62-1.62 1.62-1.62-7.62 1.62-7.62 7.6 
15-7.20 7.20 1.20-7.20 1.20-1.20-1.20 1.20-7.20 1.20 1.20-7.20-1.20-7.20 1.20 1.2 
16 1.63 1.63 1.63 1.63 1.63 7 . 6 3 1.63 1.63 1.63 1.63 1.63 1.63 7.63 1.63 1.63 7.6 
- _ _ _ - _ - _ _ _ _ _ _ _ _ _____- -_ -_ -___ -___ -___ ---- ---- ---- ---- - -__ ---- ---- ---- 
3 24 
e) Calculating the effect of factors on curvature variance 
The effects of factors on curvature variance are calculated in the same way as the effect 
of factors on curvature itself The effects matrix is multiplied by the variance using the 
instruction (in cell B55): 
+$AA9*B9 
copied to all cells in the range B55 ...Q 70. The elements of each column are then added and the 
sum is divided by 16 (instruction in cell B72): 
@SUM(BSS.. .B70)/16 
SCREEN 14.17 
Calculation of the effects on curvature variance 
1-0.0003 -0.0003 -0.0003 -0.0003 -0.0003 0.0009 0.0003 0,0003 0.0003 0,0003 0 .0003 0 .0003-0 .0003 -0.0003 -0.0003 0,0003 
2 0.0273 -0.0273 -0.0273 0.0273 -0.0213-0.0273-0.0273 0.0213-0.0213 0.0273 0.0273 -0.0273 0,0273 0.0273 -0,0273 0.0273 
3-0.0012 0.0012 -0.0012 0.0012 -0.0012-0.0012 0.0012 -0.0012 0.0012 -0.0012 0.0012 -0.0012 0,0012 -0.0012 0,0012 0.0012 
4 0.0104 0.0104 -0.0104 -0.0104 -0.0101 0.0104 -0.0104 -0.0104 -0.0104 -0.0104 0.0104 0.0101 -0,0104 0.0104 0,0104 0.0104 
5-0.0036-0.0036 0.0036 0.0036 -0.0036 0.0036-0.0036 -0.0036 0.0036 0.0036-0.0036-0.0036-0.0036 0.0036 0.0096 0.0036 
6 0.0496 -0.0496 0.0496 -0.0496 -0.0496-0.0196 0.0496 -0.0496-0.0496 0.0496-0.0096 0.0496 0.0996 -0.0496 0.0496 0.0496 
1-0.0084 0.0084 0.0084 -0.0084 -0.0084 -0.0084-0.0081 0.0084 0.0084 -0.0084 -0.0084 0.0084 0.0081 0.0084 -0.0084 0.0084 
8 0.0156 0.0156 0.0156 0.0156 -0.0156 0.0156 0.0156 0.0156-0.0156-0.0156-0.0156-0.0156-0.0156 -0.0156-0.0156 0.0156 
9-0.0373 -0.0313 -0.0373 -0.0313 0.0313 0.0373 0.0373 0.0373~0.0313-0.0373-0.0373-0.0373 0.0373 0.0313 0.0373 0.0173 
10 0.0645 -0.0645 -0.0645 0.0645 0.0645-0.0645-0.0645 0,0645 0,0645 -0,0645-0.0645 0,0645-0.0645 -0,0645 0.0645 0.0645 
11-0.0012 0.0012 -0.0012 0.0012 0.0012-0.0012 0.0012 -0.0012-0.0012 0.0012-0.0012 0.0012-0.0012 0.0012 -0,0012 0.0012 
12 0.0092 0.0092 -0.0092 -0.0092 0.0092 0.0092-0.0092 -0,0092 0.0092 0.0092-0.0092 -0,0092 0.0092 -0,0092-0.0092 0,0092 
13-0.0048 -0.0048 0,0048 0.0048 0.0048 0.0048-0.0018 -0.0048-0.0048 -0.0048 0.0018 0.0018 0.0048 -0,0048 -0.0048 0.0048 
14 0.0042 -0.0042 0.0042 -0.0042 0.0042-0.0012 0.0042 -0.0012 0.0012-0.0042 0.0042 -0.0042-0.0042 0.0042 -0.0012 0.0042 
15-0.0016 0.0016 0.0016 -0.0016 0.0016-0.0016-0.0016 0.0016-0.0016 0.0016 0.0016 -0.0016-0.0016 -0.0016 0.0016 0.0016 
16 0.0254 0.0251 0.0254 0.0254 0.0251 0.0251 0.0254 0.0254 0.0254 0.0254 0.0254 0.0251 0.0254 0.0254 0.0254 0 . 0 2 5 4 
..-- - ..... ~ - - - - ..... ..._. ..~. _... .... .... .... .... . .~~ .... ~ ~ . . ...~ ~~.~ 
0.00925 -0.0074 -0.0024 0.00140 0.00199-0.00320.00031 0.00601 -0.0019 0.00176-0.00710.00403 0.00386 -0.0018 0.00766 0.0165 
The effects of factors on the fbnctions Z and Z are calculated in the same way, using the 
instructions: 
and 
+$AC9*B9 
+$AE9*B9 
325 
SCREEN 14.18 
Calculation of the effects of factors on the function Z 
1 2 3 123 5 12 13 14 15 25 35 45 125 135 235 
1 35 .23 35 .23 35.23 35 .23 3 5 . 2 3 - 3 5 . 2 3 - 3 5 . 2 3 -35 .23 -35.23 -35 .23 - 3 5 . 2 3 - 3 5 . 2 3 35 .23 35 .23 35.23 -35 .23 
2 -15.64 15 .64 15 .64 -15.64 1 5 . 6 4 15 .64 15 .64 -15.64 15 .64 -15.64 -15.64 15 .64 -15.64 -15.64 15 .64 -15 .64 
3 2 9 . 2 1 -29 .21 2 9 . 2 1 -29 .21 2 9 . 2 1 2 9 . 2 1 -29 .21 2 9 . 2 1 -29 .21 2 9 . 2 1 -29 .21 2 9 . 2 1 -29 .21 2 9 . 2 1 -29 .21 - 2 9 . 2 1 
4 -19 .82 -19 .82 19 .82 19 .82 19 .82