The design and analysis of split-plot experiments in industry

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The design and analysis of split-plot experiments in industry
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THE DESIGN AND ANALYSIS OF SPLIT-PLOT
EXPERIMENTS IN INDUSTRY












By

SCOTT M. KOWALSKI


A DISSERTATION PRESENTED TO THE GRADUATE SCHOOL
OF THE UNIVERSITY OF FLORIDA IN PARTIAL FULFILLMENT
OF THE REQUIREMENTS OF THE DEGREE OF
DOCTOR OF PHILOSOPHY

UNIVERSITY OF FLORIDA


1999

















ACKNOWLEDGMENTS


I would like to express my sincere gratitude to Dr. G. Geoffrey Vining for serving

as my dissertation advisor. Many thanks go out to him for allowing me the oppor-

tunity to serve as an editorial assistant for the Journal of Quality Technology. His

generosity has given me experiences that most graduate students could only dream

of having. Also, not only as he been a mentor for me statistically, but he has also

been my friend.

I would also like to thank Dr. John Cornell for his extreme interest in the work

that I have done and for being a constant resource for me. In addition, I would like

to thank Drs. Jim Hobert, Richard Scheaffer, and Diane Schaub for serving on my

committee. Also, I would like to thank Dr. Frank Martin for sitting in on my defense

and for developing my interest in Design of Experiments through his course. I extend

a big thank you to Dr. Ronald Randles, chairman of the department of statistics, for

supporting me through my many years at the University of Florida.

I thank my parents for their endless love and support. They fully believed in me

when, at times, I wasn't so sure I would finish. Finally, I have to thank my wife for

her love and especially her patience. She has stood by me through e-verytliii g and I

owe her more than I could ever repay.

















TABLE OF CONTENTS


ACKNOW LEDGMIENTS ....................................................... ii

A B ST R A C T ................................................................... vi

CHAPTERS

1 INTRODUCTION ......................................................... 1

1.1 Response Surface Methodology ............................. ......... 1

1.2 Split-Plot Designs ................................................... 3

1.3 Dissertation Goals .................................................. 13

1.4 O verview ........................................................... 16

2 LITERATURE REVIEW ................................................. 17

2.1 Split-Plot Confounding ........................................ .... .. 17

2.2 Split-Plots in Robust Parameter Designs ............................ 19

2.3 Bi-Randomization Designs .......................................... 27

2.4 Split-Plots in Industrial Experiments ............................... 31

3 INCOMPLETE SPLIT-PLOT EXPERIMENTS .......................... 40

3.1 Fractional Factorials ................................................ 41

3.2 Confounding ....................................................... 44

3.3 Confounding in Fractional Factorials ................................ 46

3.4 Combining Fractional Factorials and Confounding in Split-Plot
Experim ents ....................................................... 47













3.5 Discussion of Minimum-Aberration in Split-Plot Designs ............ 55

3.6 Adding Runs to Improve Estimation ................................ 57

3.7 An Exam ple ........................................................ 72

3.8 Sum m ary ........................................................... 78

4 A NEW MODEL AND CLASS OF DESIGNS FOR MIXTURE
EXPERIMENTS WITH PROCESS VARIABLES ...................... 81

4.1 Experimental Situation ............................................. 84

4.2 The Combined Mixture Component-Process Variable Model ........ 85

4.3 Design Approach ................................................... 89

4.4 A analysis ........................................................... 104

4.5 Lack of Fit ........................................................ 111

4.6 Exam ple .......................................................... 114

4.7 Sum m ary ......................................................... 117

5 MIXTURE EXPERIMENTS WITH PROCESS VARIABLES IN A
SPLIT-PLOT SETTING .............................................. 119

5.1 First-Order Model for the Process Variables ....................... 120

5.2 Second-Order Model for the Process Variables ..................... 135

5.3 Sum m ary ......................................................... 139

6 SUMMARY AND CONCLUSIONS ...................................... 147

APPENDICES

A: TABLES FOR CHAPTER 3 DESIGNS ................................. 149

B: TABLES FOR CHAPTER 4 DESIGNS ................................. 161

C: SAS CODE FOR PROC MIXED ....................................... 167













R EFER EN C ES ............................................................... 168

BIOGRAPHICAL SKETCH .................................................. .. 172

















Abstract of Dissertation Presented to the Graduate School
of the University of Florida in Partial Fulfillment of the
Requirements of the Degree of Doctor of Philosophy

THE DESIGN AND ANALYSIS OF SPLIT-PLOT
EXPERIMENTS IN INDUSTRY

By

Scott M. Kowalski

December, 1999


Chairman: G. Geoffrey Vining
Major Department: Statistics

Split-plot experiments where the whole plot treatments and the subplot treatments

are made up of combinations of two-level factors are considered. Due to cost and/or

time constraints, the size of the experiment needs to be kept small. Using fractional

factorials and confounding, a method for constructing sixteen run designs is presented.

Along with this, semifolding is used to add eight more runs. The resulting twenty-four

run design has better estimating properties and gives some degrees of freedom which

can be used for estimating the subplot error variance.

Experiments that involve the blending of several components to produce high

quality products are known as mixture experiments. In some mixture experiments,

the quality of the product depends not only on the relative proportions of the mixture













components but also on the processing conditions. A combined model is proposed

which is a compromise between the additive and completely crossed combined mixture

by process variable models. Also, a new class of designs that will accommodate the

fitting of the new model is considered.

The design and analysis of the mixture experiments with process variables is dis-

cussed for both a completely randomized structure and a split-plot structure. When

the structure is that of a split-plot experiment, the aiiialy.-i is more complicated since

ordinary least squares is no longer appropriate. With the process variables serving as

the whole plot factors, three methods for estimation are compared using a simulation

study. These are ordinary least squares (to see how inappropriate it is), restricted

maximum likelihood, and using replicate points to get an estimate of pure error. The

last method appears to be the best in terms of the increase in the size of the confi-

dence ellipsoid for the parameters and has the added feature of not depending on the

model.














CHAPTER 1
INTRODUCTION


A common exercise in the industrial world is that of designing experiments, explor-

ing complex regions, and optimizing processes. The setting usually consists of several

input factors that potentially influence some quality characteristic of the process,

which is called the response. Box and Wilson (1951) introduced statistical methods

to attain optimal settings on the design variables. These methods are commonly

known as response surface methodology (RSM), which continues to be an important

and active area of research for industrial statisticians.

Many times in industrial experiments, the factors consist of two types: some with

levels that are easy to change and one or more with levels that are difficult or costly

to change. Suppose for illustration that there is only one factor that is difficult to

change. When this is the case, the experimenter usually will fix the level of this factor

(ie., restrict the randomization scheme) and then run all combinations or a fraction of

all combinations of the other factors, which is known as a split-plot design. Too often,

the data obtained from this experiment are analyzed as if the treatment combinations

were completely randomized, which can lead to incorrect conclusions as well as a loss

of precision. Ainly.-i, of data obtained from experiments, such as the example above,

need to take the restricted randomization scheme into account.

1.1 Response Surface Methodology

In RSMI, the true response of interest, 7, can be expressed as a function of one or

more controllable factors (at least in the experiment being performed), x, by









2




q = .g(x) + c,

where the form of the function g is unknown and c is a random error term. The goal

is to find, in the smallest number of experiments, the settings among the levels of

x within the region of interest at which q is a maximum or minimum. Because the

form of g is unknown, it must be approximated. RSM uses Taylor series expansion to

approximate g(x) over some region of interest. Typically, first or second order models

are used to approximate g(x). The traditional RSM model would be

Yi= f(x)'/ + E,


where


yi is the ith response,

x, is the /th setting of the design factors,

f(x) is the appropriate polynomial expansion of x,

(3 is a vector of unknown coefficients, and

the ci's are assumed to be independent and identically (i.i.d.) distributed as

N(0, a2).


For a more detailed discussion on RSM see Khuri and Cornell (1996), Box and Draper

(1987), and Myers and Montgomery (1995).












1.2 Split-Plot Designs

A split-plot design often refers to a design with qualitative factors but can easily

handle quantitative factors. Also, a split-plot design usually has replication. However,

in the literature it has been common practice to refer to any design that uses one

level of restricted randomization regardless of replication as a "split-plot" design.

Therefore, in this dissertation, we will use the term split-plot design throughout.

When performing minultifactor experiments, there may be situations where com-

plete randomization might not be feasible. A common situation is when the nature

of the experiment or factor levels preclude the use of small experimental units. Often

a second factor can be studied by dividing the experimental units into sub-units. In

these situations, the split-plot experiment can be utilized. The experimental unit

is referred to as the whole plot while the sub-units are referred to as the subplots.

For every split-plot experiment there are two randomizations. Whole plot treatments

are randomly assigned to whole plots based on the whole plot design. Within each

whole plot, subplot treatments are randomly assigned to subplots with a separate

randomization for each whole plot. This leads to two error terms, one for the whole

plot treatments and one for subplot treatments as well as the interaction between

whole plot treatments and subplot treatments. Split-plot experiments have been used

extensively in agricultural settings. Even so, the following example from Montgomery

(1997) shows that there are applications for split-plot experiments in industrial set-

tings.

A paper manufacturer is interested in studying the tensile strength of paper based

on three different pulp preparation methods and four cooking temperatures for the












pulp. Each replicate of the full factorial experiment requires 12 observations, and the

experimenter will run three replicates. However, the pilot plant is only capable of

making 12 runs per day, so the experimenter decides to run one replicate on each of

three days. The days are considered blocks. On any day, he conducts the experiment

as follows. A batch of pulp is produced by one of the three methods. Then this

batch is divided into four samples, and each sample is cooked at one of the four

temperatures. Then a second batch of pulp is made using one of the remaining two

methods. This second batch is also divided into four samples that are tested at the

four temperatures. This is repeated for the remaining method. The data are given in

Table 1. This experiment differs from a factorial experiment because of the restriction

on the randomization. For the experiment to be considered a factorial experiment,

the 12 treatment combinations should be randomly run within each block or day. This

is not the case here. In each block a pulp preparation method is randomly chosen,

but then all four temperatures are run using this method. For example, suppose

method 2 is selected as the first method to be used, then it is impossible for any of

the first four runs of the experiment to be, say, method 1, temperature 200. This

restriction on the randomization leads to a split-plot experiment with the three pulp

preparation methods as the whole plot treatments and the four temperatures as the

subplot treatments. It should be noted that conducting a split-plot experiment, as

opposed to a completely randomized experiment, can be easier because it reduces

the number of times the whole plot treatment is changed. This usually will result

in a time savings which will lead to reduced costs. For example, suppose one is

interested in six subplot treatments and four whole plot treatments. Let the whole













Table 1: Data for Tensile Strength of Paper (from Montgomery (1997))


Block 1 Block 2 Block 3


Pulp Preparation Method 1 2 3 1 2 3 1 2 3
Temperature
200 30 34 29 28 31 31 31 35 32
225 35 41 26 32 36 30 37 40 34
250 37 38 33 40 42 32 41 39 39
275 36 42 36 41 40 40 40 44 45



plot treatments be comprised of a 22 factorial in time and temperature of a kiln. A

completely randomized experiment would require the kiln to be fired up quite possibly

24 times. With a split-plot experiment, the kiln only needs to be brought up to the

correct temperature 4 times per replicate. This leads to a savings of time and possibly

money.

A split-plot experiment can be run inside of many standard designs, such as the

completely randomized design (CRD) and the randomized complete block (RCB) de-

sign. As in the example from Montgomery (1997), suppose the split-plot experiment

is performed using a RCB design. Let Yijk denote the observation for subplot treat-

ment k receiving whole plot treatment i in block j. Kemnipthorne (1952) uses as his

model


Yijk = / + Ti + f3j + 6ij + 7Yk + (T-7)ik + Cijk for i= 1,2,...,t

j = 1,2,..., b













where


t is the number of levels for the whole plot treatment,

b is the number of blocks or replicates of the basic whole plot experiment,

s is the number of levels for the subplot treatment,

yi is the overall mean,

T, is the effect of the ith whole plot treatment,

Oj is the effect of the jh block,


8ij is the whole plot error term,


Yk is the effect of the kth subplot treatment,

(TY)ik is the whole plot treatment by subplot treatment interaction, and

Eijk is the subplot error.


He uses randomization theory to derive the expected mean squares summarized in

Table 2. In this table, ,6 is the experimental error variance for the whole plot treat-

ments, and a2 is the experimental error variance for the subplot treatments.

Many ariiily-t-. assume that the blocks are random and use an unrestricted mixed

model to derive the appropriate mean squares. The most common model for this

approach is














Yijk = P + T, + 3j + (Tf),i + Yk + (TY)ik + 6tjk (1)

: = 1,2, j = 1,2,.. b k = 1,2,...,s,

where


it is the overall mean,

T-: is the effect of whole plot treatment i,

Oj is the effect of block j,

(TOf3)ij is the block x whole plot treatment interaction,

-Yk is the effect of subplot treatment k,

(T77)ik is the whole plot treatment x subplot treatment interaction, and

Eijk is the subplot error.

The (T/3)ij term will be the whole plot error term for the case of an RCB design under

the usual assumption of no block x whole plot treatment interaction. The analysis

of variance table associated with the model in Equation (1), assuming whole plot

treatments and subplot treatments are fixed and blocks are random, is given in Table

3. If the block by whole plot interaction is called the whole plot error, then Tables 2

and 3 suggest the same basic testing procedures. The following additional constraints

and assumptions are needed for hypothesis testing:


T= 0, >k= 0,
i k












0, N(0 2) V(0, Or2) 6^~N(0, ar2)
N (0,Oo ),bi N (o), N

and where bij and Cijk are independent.
Montgomery (1997) uses a restricted mixed model as the basis for his analysis of

the following form


Yijkh = A1 + Ti + O3j + (TfO)i + fYk + (7-r)'4k + (0),)j, + (T[3-)i3k + iikh,

where

h = 1, 2,. ., r is the number of replicates,

(TOf)j is the random block by whole plot treatment interaction,

is the whole plot treatment x subplot treatment interaction,

(/30Y)jk is the random block by subplot treatment interaction,

(TO3-y)ijk is the random block by whole plot treatment by subplot treatment
interaction.

Under this restricted mixed model, the random interactions involving a fixed factor
are assumed subject to the constraint that the sum of that interaction's effects over
the levels of the fixed factor is zero. Table 4 gives the resulting expected mean squares,
which suggests that there are three distinct error terms. The block by whole plot by
subplot interaction is used to test the whole plot by subplot interaction; the block
by subplot interaction is used to test the main effect of the subplot treatment; and
the block by whole plot interaction is used to test the main effect of the whole plot.













Table 2: Expected Mean Squares Table Under Randomization Theory

Source df Expected Mean Square
Whole Plot Treatment t 1 ao, + I_ # T2


Blocks
Whole Plot Error


b-1
(t- 1)(b- 1)


8
Subplot Treatment s 1 a2 + b E 7y
ck=l

Whole Plot x Subplot (t 1)(s 1) a2 + (tb b E- i E=l (T)ik
(t1)(S 1) i Ek i(FYi

Subplot Error t(b 1)(s 1) a2



Note, if h = 1, the variance of Eijkh is not estimable. This restricted ailiuil.-is reduces

to the other two analyses only if the block by subplot interaction is unimportant. In

such a case, its contribution can be pooled with the block by whole plot by subplot

interaction to form the same error term as the randomization and unrestricted mixed

model analyses.

Whole plot treatments are applied to blocks of t units which can be divided

further into s subunits, where s is the number of levels of the subplot treatment. Any

differences among these blocks must be confounded with the whole plot treatment

comparisons. Consequently, comparisons among the subplot treatments are made

with greater precision, and this leads to the more important factor usually being

assigned to the subplot. Using the unrestricted model and Table 3, it is seen that the

null hypothesis of no whole plot treatment effect, H0 : rl = T2 .= Trt, versus at

least one not equal, is tested using the Block x Whole Plot Treatment interaction as


a2 + staj
2
or,













Table 3: Expected Mean Squares Table Under the Most Common Unrestricted Mixed
Model

Source df Expected Mean Square
Whole Plot Treatment t 1 a2 + saj + E ri2
'- =1

Blocks b 1 a2 + sa + sta

Block x Whole Plot Treatment (t 1)(b 1) a2 + sa6
Subplot Treatment s 1 a2 + k= k "
k=l
t s
(tC2+ b TY2
Whole Plot x Subplot (t- 1)(s- 1) a2 + b- E E (r')ik
i=1 k=1

Error t(b- 1)(s- 1) a2
N,,t.-: Whole Plot and Subplot Treatments are assumed fixed while Blocks
are assumed to be random.



Table 4: Expected Mean Squares Table Under the Restricted Mix:-. Mohdel


Source df Expected Mean Square
Whole Plot Treatment t -1 r2 + sr + Zi l T2

Blocks b -1 a2 + sa2 + sta
Block x Whole (t 1)(b 1) a2 + saU_
Subplot Treatment s- 1 ar2 + ta2 + ELI -Y

Block x Sub (b- 1)(s- 1) a2 + ta2

Whole Plot x Subplot (t 1)(s 1) a2 + or + b i l(T)2
0Block x Whole x Sub (-1)(-)(s-k1) a2+
Block x Whole x Sub (t 1)(b 1)(s 1) ar2 +F Or2.












the error term. The hypothesis of no subplot treatment effect, H0 : Y1 = 72 .. 'Y,

versus at least one not equal, is tested using Error which is also used to test the

significance of the whole plot x subplot treatment interaction.

Suppose the whole plot and subplot treatments are a factorial structure. In this

case, after the hypothesis tests above are performed, a more detailed investigation of

the individual factors and their interactions can be carried out. For example, consider

the situation discussed above with t = 4 whole plot treatments consisting of a 22

factorial in zl and z2 and s = 4 subplot treatments also consisting of a 22 factorial

in x, and x2. The t 1 = 3 degrees of freedom (df) for the whole plot treatments

can be partitioned into single df contrasts z1, z2, and z12z2. Likewise, the s 1 = 3

df for the subplot treatments can be partitioned into a single df contrasts X1, x2,

and xIx2. Also, the (t 1)(s 1) = 9 df for the whole plot x subplot treatment

interaction can be broken down into 9 single df effects involving z1, z2, xi, and x2

(see Table 5). Orthogonal contrasts should be calculated and tested for each factor

and the interactions using the appropriate error term from the original analysis. This

can be accomplished in SAS by using PROC GLM and the CONTRAST statement along

with the option E = error term after the model statement for the whole factors and

interactions. For the subplot factors, interactions among subplot factors, and whole

plot x subplot factor interactions, the aiialdy.is can be run a second time. In this

second imiilv'ik. the treatments in the model statement can be entered as factors and

interactions, similar to a regression model. The correct tests for the subplot factors

and whole plot x subplot factor interactions are given by SAS.

















Table 5: Analysis of Variance Table for a Split-Plot Experiment Run Using a RCB
Design With Factorial Structure and the Most Common Unrestricted Model

Source df
Whole Plot Treatment t 1 = 3
ZI 1
z2 1
ZlZ2 1

Blocks b- 1

Block x Whole Plot Treatment (t 1)(b- 1)
Subplot Treatment s 1 = 3
xl l+ 1
x2 1
XlX2 1

Whole Plot x Subplot (t 1)(s 1) = 9
zlxl 1t
z1X2 1
Z2X1 tt 1
Z2X2 i 1
zIx1x2 t 1
Z2XlX2 1
Z1Z2X1 1
Zl Z2X2 1t
Z1Z2X1X2 1

Error t(b- 1)(s- 1)


t These terms are tested using the Block x Whole Plot Treatment interaction.
tt These terms are tested using Error.












The concept of the split-plot design can be extended if further randomization

restrictions exist. For example, suppose there are two levels of randomization restric-

tions within a block in which case we might have a split-split-plot design. For a more

detailed discussion of split-plot designs and their extensions see Yates (1937), Cox

(1958), Wooding (1973) and .Mrito iiiery (1997).


1.3 Dissertation Goals


The focus of this dissertation is to enhance our understanding of the design and

anilyi, of split-plot experiments. The experiments considered will be industrial in

nature. As much as possible, the dissertation will focus on or discuss the types

of experiments that would be run in industry in terms of size and resources. An

important goal is to come up with methods that are clear, practical, and easy to

implement. In other words, this dissertation will address issues of real concern to

applied statisticians working in industry mand provide them some tools that can be

used with split-plot experiments. Below two industrial statisticians have been kind

enough to share real situations that help to show the relevance of the work in this

dissertation.

A Food Industry Example

Frozen heat-and-serve pastries, along with shelf-stable ready-to-eat pastries, rep-

resent a large segment of the convenience foods that today's consumers crave. Op-

timized proofing and baking operations are critical to the successful manufacture of

high quality baked goods such as these. However, as this market segment has grown,













so has the manufacturing capacity, which has necessitated the installation of new

proofers and ovens. Given the complexity of these operations, qualifying a new piece

of proofing or baking equipment poses a challenging experimental design problem:

how do you design an experiment to explore the operating profile for a new proofer

or oven?

As an example, consider a continuous oven, in which dough-based products move

through on a belt. The oven has two zones, which are controlled independently. In

each zone you can atju-t the Temperature, the Relative Humidity (RH), the Air Flow

Speed (AF), and the Residence Time. In general, the conditions in each zone will be

different, as each zone is used to impart different characteristics to the product. All

of these variables will impact the quality of the finished product.

Experimenting with this type of oven requires a restricted randomization. You

can easily reset the air flow and residence time in each zone on the fly, but changes in

the temperature and relative humidity require a waiting period to allow the oven to

return to steady state. Thus, oven experiments are typically conducted as a split-plot

design with four whole plot treatments, namely


Zone 1 Temp, Zone 1 RH, Zone 2 Temp, and Zone 2 RH,


and four split plot treatments, namely


Zone 1 AF, Zone 1 Res Time, Zone 2 AF, and Zone 2 Res Time.


In addition, we typically want to evaluate the effect of the oven on at least two prod-

ucts (,











product that is baked is evaluated in a variety of ways, including sensory characteri-

zations and analytical and physical testing.

What makes this experimental setup so difficult, is that exploring the profile of

a new oven must typically occur on prototype equipment at the oven manufacturer.

This means the experiment must be conducted in a very short period of time, often

two days or less. This makes it imperative that the experiment have as few runs

as possible usually between 12 and 20 runs. The research described in this thesis is

directly applicable to problems like this, and will be very useful for teams of process

engineers charged with gathering the data they need to fully evaluate candidate ovens

and proofers.


An Integrated Circuits Example


Integrated microflex circuits are manufactured over several, very complicated pro-

cess steps. Circuit plating is a key step in this process. It involves depositing a

uniform layer of copper on the microflex circuits. Copper thickness is a key quality

characteristic due to functionality issues. High variability in copper thickness results

in poor bonding of chips to these circuits. Some of the variables that effects circuit

thickness are the circuit geometry, the line speed, the current in amperes, the copper

concentration in the chemistry bath, and the concentration of both sulfuric acid and

hydrogen peroxide.

Designing experiments to optimize copper thickness is a challenge because of the

presence of hard-to-change variables. In particular, restricted randomization occurs

with circuit geometry, line speed, and current. Randomization is not restricted for












the remaining variables. Data from such experiments are analyzed by assuming that

it arose from a completely randomized experiment. Research in the area of split-plot

experiments with multiple whole plot and subplot factors is lacking and the work in

this dissertation should be of real help to industrial statisticians.


1.4 Overview


The literature review that follows in Chapter 2 is intended to familiarize the reader

with other work that discusses split-plot designs in RSI. Chapter 3 begins with some

background information onl 2k factorial experiments and the remainder of Chapter

3 is devoted to a more in-depth look at confounding in split-plot experiments. In

Chapter 4, a new model and class of designs for mixture experiments with process

variables will be developed in a completely randomized setting. Finally, the last

chapter will assume a split-plot structure for the mixture experiments with process

variables described in Chapter 4.
















CHAPTER 2
LITERATURE REVIEW


The split-plot error structure has been underutilized in RSM. Most RSM ex-

periments assume a completely randomized error structure. Letsinger, Myers, and

Lentner (1996, pg. 382) point out, "Unfortunately, while this completely randomized

assumption simplifies analysis and research, independent resetting of variable levels

for each design run may not be feasible due not only to equipment and resource con-

straints, but also budget restrictions." This chapter focuses on the literature involving

restricted randomization within RSM.


2.1 Split-Plot Confounding

When the whole plot and/or subplot treatments are of a factorial nature, it is

possible to reduce the number of whole plots and/or subplots needed through frac-

tionating. This is important in industrial experiments where constraints limit the size

of the experiment. Bartlett (1935) suggested the possibility of confounding higher-

order subplot interactions to reduce the number of subplots needed within each whole

plot. Later, split-plot confounding was studied by Addelman (1964). He provided

a table containing factorial and fractional-factorial arrangements that involve split-

plot confounding. However, he did not consider confounding within the whole plots.

Letsinger, Myers, and Lentner (1996) discuss the possibility of split-plot confounding












with the use of their noncrossed bi-randomization designs. Box and Jones (1992)

illustrate split-plot confounding using a cake mix example.

In some experiments, there are constraints on the number of subplots within each

whole plot. When the whole plots are arranged in a CRD, Robinson (1967) discussed

situations where the number of subplots per whole plot is less than the number

of subplot treatments. The whole plots are treated as blocks and then a balanced

incomplete block (BIB) design is used to allocate the subplot treatments to the whole

plots. If the whole plots are arranged in an RCB design, the same procedure can be

applied. If the number of whole plots per block is less than the number of whole plot

treatments, then an incomplete block design can be used there as well. Robinson

(1970) gave details on the case when both whole plot and subplot treatments are

arranged in incomplete block designs. Essentially, the procedure amounts to arranging

the whole plot treatments in blocks using a BIB design and then considering the whole

plots as blocks and arranging the subplot treatments in another BIB design. Robinson

(1970) provided formulas for the estimates of the main effects and interactions for

three cases: within whole plot, between whole plot within block, and between blocks.

Formulas are also given for the variance of the differences of these estimates for each

case.

Huang, Chen and Voelkel (1998) also investigate frictiiiiiitliiig, two-level split-plot

designs at both the whole plots and the subplots. They consider 2(n"l+2)-(kl+k2)

split-plot designs which are associated with a subset of the 2n-k fractional factorial

designs where n = n7 + n2 and k = k, + k2. The criterion used to select the optimal

design is that of minimum-aberration which is the design that has smallest number of












words in the defining contrast with the fewest letters. Two methods are presented for

constructing minimum-aberration split-plot designs. The first method decomposes

the 2 "-k design into the 2(n-+n2)-(kl+k2) split-plot design. This method is used to

derive extensive, though incomplete, tables of the designs. The second and more

complicated method which involves linear integer programming is used when the first

method fails.

Minimum-aberration two-level split-plot designs are also discussed in Binghamn

and Sitter (1999). A combined search and sequential algorithm is presented for con-

structing all non-isomorphic minimum-aberration split-plot designs which include the

tables of Huang, Chen and Voelkel (1998). Bingham and Sitter (1999) catalog designs

for 16 and 32 runs containing up to 10 factors. Included in this catalog are the second

and third best minimum-aberration designs since sometimes it may be desirable to

use these designs.


2.2 Split-Plots in Robust Parameter Designs


Genichi Taguchi proposed methods for designing experiments for product design

that are robust to environmental variables. The goal of robust design is to design an

experiment that identifies the settings of the design factors that make the product

robust to the effects of the noise variables. The design factors, which are factors

controlled during manufacturing, make up the inner array while the environmental

factors, or noise factors, make up the outer array. Environmental factors are fac-

tors that are difficult to control and can cause variation in the use or performance

of products. The experimental design or "crossed arrive" consists of crossing each












experimental design setting of the inner array with each experimental design setting

of the outer array. Unless the number of factors in these arrays is small, Taguchi's

designs become large and expensive.

An alternative to Taguchi's crossed array is the "combined" array. The combined

array utilizes a single experimental design in both the design and environmental fac-

tors. Therefore, the response is modeled directly as a function of the design factors

and the environmental factors using a single linear model. More details on the com-

bined array can be found in Welch, Kang, and Sacks (1990); Shoemaker, Tsui, and

Wu (1991); and O'Donnell and Vining (1997).

Bisgaard (1999) discusses split-plot designs in association with inner and outer

array designs. He focuses on screening experiments that use restricted randomization.

The paper gives a nice overview of defining relations and confounding structures for

the 2k-p x 2q-, split-plot designs. In addition to split-plot confounding, Bisgaard

(1999) points out that the same fraction of the subplot factors can be run in each

whole plot. The appropriate standard errors for testing effects when using split-plot

confounding are also given.

Box and Jones (1992) investigate the use of split-plot designs as an alternative to

the crossed array. They consider three experimental arrangements where the robust

parameter design is set up as a split-plot design:


1. arrangement (a) thle whole plots contain the environmental factors and the

subplots contain the design factors;












2. arrangement (b) the whole plots contain the design factors and the subplots

contain the environmental factors;


3. arrangement (c) the subplot factors are assigned in "strips" across the whole

plot factors (commonly called a strip-block experiment).


These three arrangements are illustrated through an example seeking the best recipe

for a cake mix. Three design factors have been identified as affecting taste. They are

flour, shortening, and egg powder and are studied using a 23 factorial design. The

consumer may have an oven in which the temperature is biased up or down. Also,

the consumer may overcook or undercook the cake. Therefore, the recipe is to be

robust to two environmental factors, oven temperature and baking time, whose levels

are combined using a 22 factorial design.


Arrangement (a)


Under this arrangement, the whole plots contain the environmental factors and

the subplots contain the design factors. Suppose there are m levels of the envi-

ronmental factors, E1, E2,..., Ej,... I E,, applied to the whole plots, n levels of

the design factors, D1, D2,..., Di,..., Dn, applied to the subplots, and I replicates,

rl, r2,..., ru,... ,ri, with the whole plots in I randomized blocks. For the cake mix

example, mn = 4, n = 8, and 1 = 1. Arrangement (a) requires m x n x I subplots

and m x I whole plots. Thus for the cake mix example, 4 x 8 x 1 = 32 cake mix

batches are required, but only 4 x 1 =4 operations of the oven are necessary. By

comparison, a completely randomized cross-product array would require 32 cake mix












batches and 32 operations of the oven. Thus, the split-plot arrangement has saved
time by reducing the number of operations of the oven.

The model for arrangement (a) is


Yijk = IL + 'Yk + aj + 71jk + i + (a6)ij + Eijk ,

where Yijk is the response of the kth replicate of the ith level of factor D and the jth

level of factor E, p is the overall mean, yk is the random effect of the kth replicate

with -7k N( 0, o2), aj is the fixed effect of the jth level of factor E, 6i is the fixed

effect of the ith level of factor D, (a6)j is the interaction effect of the ith level of D

and the jth level of E, Tjk N(O, a2,,) is the whole plot error, jk N(0, ar') is the

subplot error, and qgk and fijk are independent.

Arrangement (b)

With this arrangement, the whole plots contain the design factors while the sub-

plots contain the environmental factors. Arrangement (b) requires only 8 x 1 = 8 cake

mix batches but requires 4 x 8 x 1 = 32 operations of the oven. Again, a completely

randomized cross-product array would use 32 cake mix batches and 32 operations

of the oven. Here, the savings of the split-plot design is not as great since only the

number of cake mix batches is reduced. This is not an ideal situation for indus-

trial experiments. First of all, the design factors are of greater interest. Therefore,

applying the design factors to the whole plots results in a loss of precision for the

design factors. Hence, it is possible to have large differences between the levels of

the design factors that are insignificant when tested. Also, from an economic point












of view, arrangement (b) is costly. It requires an inefficient use of the environmen-

tal factors which in industrial experiments are typically the difficult or expensive to

change factors.

The model for arrangement (b) is


Yijk "= :+ 7 k + bi + Trik + Cj + (a6)i + ijk ,

where yijk is the response of the kth replicate of the ith level of factor D and the jth

level of factor E, p is the overall mean, -y is the random effect of the kth replicate

with 7Yk N(O, a'), aj is the fixed effect of the jth level of factor E, 6i is the fixed

effect of the ith level of factor D, (a6b)ij is the interaction effect of the ith level of D

and the jth level of E, Oik N(O, o,,) is the whole plot error, fijk N(O, a) is the

subplot error, and Oik and Eijk are independent.

Arrangement (c)

Now, consider the arrangement where the subplot treatments are randomly as-

signed in strips across each block of whole plot treatments (see Table 6). For the

cake mix example, suppose each of the n = 8 batches of cake mix is subdivided into

m = 4 subgroups. One subgroup from each batch is then selected, and these eight

are baked in the same oven at the appropriate temperature for the appropriate time.

This arrangement requires only 8 cake mix batches and only 4 operations of the oven.

Therefore, the strip-block experiment is easier to run than the completely randomized

cross-product design, as well as both arrangements (a) and (b).













Table 6: Strip-Block Arrangement (Box and Jones (1992))

Block 1 Block 2 Block 3
a,1 a2 a3 a3 a2 a1 al a3 a2
bl b2 b1
b2 bi b2




The model for the strip-block arrangement is


Yijk = p + k + aj -+ '1jk + bi + Oik + (O)ij + Cijk ,

where Yijk is the response of the kth replicate of the ith level of factor D and the jth

level of factor E, it is the overall mean, Yk is the random effect of the kth replicate with

Yk N(O, a2), aj is the fixed effect of the jth level of factor E, 6i is the fixed effect
of the ith level of factor D, (a6)iy is the interaction effect of the ith level of D and the
jth level of E. In arrangement (c), rqjk N(O, ao), Oik N(O, aD), 'ijk N(Oa2)

and 'tljk, Oik and Eijk are independent.

ANOVA tables for all three arrangements are given in Box and Jones (1992).

These tables indicate the appropriate denominators for tests involving the design

factors, the environmental factors, and their interactions assuming replication. When

there is no replication, normal probability plots, one for the whole plot factors and

one for the subplot factors and whole plot x subplot interactions, can be used to

select significant effects. Also, if the design and environmental factors are factorial

combinations, it may be possible to pool negligible higher order interactions to get

estimates of the whole plot and subplot errors.












It is of great interest to the researcher to learn how and which environmental

factors influence the design variables. This information is contained in the subplot

x whole plot interactions. However, Taguchi's anih.lyni is commonly conducted in

terms of a performance statistic, such as the signal to noise ratio (SNR). The SNR

is calculated for each point in the inner array using data obtained from the outer

array about that point. Therefore, Taguchi ignores any information contained in the

interactions of the design and environmental factors. This is generally considered to

be a serious drawback to the Taguchi analysis.

Phadke (1989) presented an example involving a polysilicon deposition process

which he analyzed using Taguchi's SNR's. Polysilicon film is typically deposited

on top of the oxide layer of the wafers using a hot-wall, reduced pressure reactor.

The reactant gases are introduced into one end of a three-zone furnace tube and are

pumped into the other end. The wafers enter the low-pressure chemical vapor depo-

sition furnace in two quartz boats, each with 25 wafers, and polysilicon is deposited

simultaneously onil all 50 wafers. The desired output of this process is a wafer which

has a uniform layer of film of a specified thickness. Six design factors each at three

levels were identified: temperature, pressure, nitrogen flow, silane flow, setting time,

and cleaning method. Tube location and die location were considered noise factors.

Three responses, film thickness, particle counts, and deposition rate, were of interest.

The smaller the better SNR was used in the analysis for particles, the target is best

SNR was used for thickness, and a 20 logo10 transformation was used for deposition

rate. The data were analyzed using ANOVA techniques to determine the effect of












each design factor on the responses. A more detailed discussion of the selection of

fict.,r.,, design, and analysis of the SNR's is contained in Chapter 4 of Phadke (1989).

The actual structure of this experiment was a split-split-plot design because there

are three sizes of experimental units with different sources of variation. The design

factors are applied to the tube (run-to-run variability); the location in the tube affects

the wafer (wafer-to-wafer variability), whereas location in the wafer affects the die

(die-to-die variability). Therefore, using Taguchi's SNR's to analyze this experiment

will result in a complete loss of information in the design x noise factor interactions.

Cantell and Ramirez (1994) reanalyzed the data as if it were a split-split-plot design.

They pooled higher order interactions to get the necessary error terms in order to

perform hypothesis tests on the design factors and the design x noise factor inter-

actions. Interaction plots were used to determine the level of the design factor that

minimized the variation across the levels of the noise factors. Although the final

recommendations on the design factor levels by Cantell and Ramirez (1994) differed

from Phadke (1989) on only one of the six design factors, the use of the split-split-plot

design has allowed the process engineer to have a better understanding of the sources

of variation. This added information may lead to process improvement in the future.

Kempthorne (1952) and Box and Jones (1992) provide details on the relative

efficiency of these split-plot designs compared to the CRD and RCB. A summary of

their conclusions is provided here. Consider the split-plot experiment as a uniformity

trial. If the uniformity trial was run as a CRD or a RCB experiment, then, for

arrangements (a) and (b), the subplot factor effects and the subplot x whole plot

interactions are estimated more precisely than the whole plot factor effects. Compared












with arrangements (a) and (b), the strip-block design estimates the subplot x whole

plot interactions more precisely but the subplot factor effects with less precision.

However, the whole plot factor effects are estimated with equal precision. Based on

these results, arrangement (a) with the environmental factors applied to the whole

plots is generally preferred over arrangement (b). Both the strip-block design and

the split-plot design with the design factors applied to the subplots can be extremely

useful in robust parameter design.

2.3 Bi-Randomization Designs


Letsinger, Myers, and Lentner (1996) introduced bi-randomization designs (BRD's).

BRD's refer to designs with two randomizations similar to that of a split-plot design.

The whole plot variables are denoted by z = (z1, z2,..., zZ) while the sub-plot vari-

ables are denoted by x = (Xl, X2,..., xx). Hence, the ith design run is (zi, xi). BRD's

are broken into two classes, crossed and non-crossed. Crossed BRD's are constructed

as follows:


1. randomize the a unique combinations of z to the whole plot experimental units

(EU's), then


2. randomize the b levels of x to the smaller EU's within each whole plot (see

Table 7).


Thus every level of x is "crossed" with every level of z. These designs are the usual

split-plot designs.














Table 7: Crossed BRD From Letsinger,
Myers, and Lentner (1996)

ZI X1 ... Xb
Z2 XI ... Xb


Za X1 Xb



Table 8: Noncrossed BRD From Letsinger,
Myers, and Lentner (1996)

Zi X1 Xibj
Z2 X21 X2b2


Za Xal ... Xab,



The non-crossed BRD's differ from the crossed BRD's in that not all levels of x

are associated with zi. The whole plots have different levels of the sub-plots and need

not have the same number of levels. Non-crossed BRD's are constructed as follows:


1. randomize the a unique combinations of z to the whole plot EU's, then


2. randomize the bi levels of x to the smaller EU's within each whole plot (see

Table 8).


The distinction between these two can be thought of in terms of the sub-plot factors.

The crossed BRD might be represented by a 2k factorial in the sub-plot factors while

the non-crossed BRD might use a 2k-p fractional-factorial in the sub-plot factors but

not the same 2k-p set of treatments.












For both crossed and non-crossed BRD's, the two randomizations complicate the
error structure. The first randomization leads to the whole plot error variance, a,
while the second randomization leads to the sub-plot variance, ao. It is assumed that

the covariance between any two observations on the same whole plot is constant over
all whole plots and that observations on two sub-plots from different whole plots are
uncorrelated. The response surface model is

y=X/3 + 6 +E,

where 6 + E N(0, V) with V = aOJ + o2I, where J is a block diagonal matrix of

lb x 1' and where b, is the number of observations within the ith whole plot. Now
using generalized least squares (GLS), the maximum likelihood estimate (MILE) of
the response surface model is

(x'V' X' XV-1y (2)

with
Var() (X'V-1X)1. (3)

From Equation (2), it is seen that the model estimation depends on the matrix V
and thus both a2 and ao.
Suppose that the response surface model is partitioned into the whole plot and
sub-plot terms as
y = Z, + X*f3* + Z'AX*,

where A is a matrix of whole plot x sub-plot interaction parameters. The response
surface design should be large enough to test for general lack of fit as well as lack of












fit from the whole plots. Therefore, the number of whole plots available must exceed

the number of parameters in -f.

For the crossed BRD, there is an equivalence between ordinary least squares (OLS)

and GLS. This equivalence means that Equation (2) becomes


S= (X'X X'y

and the model estimation no longer depends on the error variance. However, for

testing purposes, the error variance must be estimated. Letsinger, Myers, and Lentner

(1996) suggest augmenting the response surface model with insignificant whole plot

terms, Z*p, to saturate the a 1 whole plot degrees of freedom. The whole plot

saturated model can be used to calculate lack of fit sums of squares for both the whole

plots and the sub-plots. Then approximate t-tests can be formed by substituting the

estimated error variances into Equation (3).

Non-crossed BRD's present a more complicated situation. The equivalency of OLS

and GLS is only true in the case of a first-order model. Although more complex, the

above method can be adapted for the first-order case. Letsinger, Myers, and Lentner

(1996) compare three methods for the second-order case. They are OLS, iterative

reweighted least squares (IRLS), and restricted maximum likelihood (REML). Though

IRLS and REML appear to be better methods, the "b-t." method depends on the

design, model, and any prior information.
Bi-randomization introduces the need for new definitions for design efficiency be-

cause efficient designs in the literature are based on a completely randomized error

structure. For example, for the BRD the D-optimality criterion (see, eg., Kiefer and












Wolfowitz (1959)) becomes

min N (X'V-'X)1

over all designs D. Letsinger, Myers, and Lentner (1996) provide comparisons of

several first- and second-order designs. For the second-order de.
central composite design (CCD) proves to be a good design.

2.4 Split-Plots in Industrial Experiments

Lucas and Ju (1992) investigated the use of split-plot designs in industrial experi-

ments where one factor was difficult to change and its levels served as the whole plot

treatments. They began their study with a simulation exercise using a four factor

face-centered cube design with four center points. They let x, correspond to the

hard-to-change factor, while x2, x3, and x4 were easy to vary. This design allowed for

the fitting of the quadratic model
4 4 3 4
Y +00 + x + iX2 + O3ijXiXj +.
i=1 i=1 i=1 j=i+l
However, since the error was the only term of interest, all the regression coefficients

can be zero. Therefore, data was generated using

Y = e = EU, + es ,

where ,, N(0, (,2,,) was the error term associated with changing the level of x, and

c, N(0, 0,) was the error associated with any new experimental run. Twentyeight

runs were generated using the following steps:


1. Generate E,,, N(O,a ,) and E, N(O, o).













2. Y = Ew+CS.


3. If the level of x, of the current run is different from that of the previous run, a

new value of both E,, and F, is generated. Otherwise, generate a new value for

E, only.


4. Go to step 2 until all 28 runs are completed.


The data were generated for completely randomized, completely restricted, and

partially restricted run orders. For a partially restricted run order, each level of

the hard-to-change factor was visited exactly twice and the runs at each level were

randomly divided into two equal groups. Each time a data set was generated, the

least squares estimates of the 13's were computed and the residual error was estimated.

The simulation procedure was repeated 1,000 times.

Lucas and Ju (1992) summarized their simulation results in a table with a listing

of the standard deviations of the regression coefficients for the three different ways

of running the experiment. The restricted randomization case has a much smaller

residual standard deviation and much smaller standard deviations for all the regres-

sion coefficients except those associated with the hard-to-change factor, 031 and I11.

These results correspond with the general result that split-plot designs will produce

increased precision on the subplot factors while sacrificing precision on the whole plot

factors. The magnitudes of the coefficients of the estimated standard deviations for

the partially restricted case were greater than those with the completely randomized

case but less than the corresponding estimates for the completely restricted case.












A similar simulation was conducted for two-level factorials (see Lucas and Ju

(1992)). They considered a 24 factorial with x, as the hard-to-change factor. This

allows the fitting of a regression model that includes the linear and interaction terms.

Again, a summary table is provided by Lucas and Ju (1992) showing s similar results to

the other experimental scenarios. The completely restricted experiment had smaller

standard deviations for all the regression coefficients except 01. Table 9 gives the

formula for the variance of the regression coefficients for a 2k factorial experiment

with one hard-to-change factor. Recall that in the partial restricted case, the blocking

was done at random. This can be improved on by blocking orthogonally. The 24

factorial can easily be blocked orthogonally in 4 blocks of size 4 or 8 blocks of size 2.

Both of these blocking schemes are an improvement over the partially restricted case

in that they have smaller standard deviations on the easy-to-vary factors.

Cornell (1988) discusses the analysis of data from mixture experiments with pro-

cess variables where the mixture blends are embedded in the process variable com-

binations as in "a split-plot design". The mixture process variables are factors that

are not mixture ingredients but whose levels could affect the blending properties of

the mixture components. To illustrate this situation, Cornell uses an example from

Cornell and Gorman (1984) involving fish patties. The mixture experiment involves

making fish patties from different blends of three fish species (mullet, sheepshead,

and croaker). The patties were subjected to factor level combinations of three process

variables (cooking temperature, cooking time, and deep-frying time). Each process

variable was studied at two levels. When process variables are included in a mixture












experiment, complete randomization tends to be impractical. This leads to a restric-

tion on randomization and lends itself to the split-plot design.

Cornell (1988) considers factor-level combinations of the process variables as the

whole plot treatments and the mixture component blends as the subplot treatments,

but points out that their roles can be switched. Hence, a combination of the levels

of the process variables is selected and all blends are run at this combination. An-

other combination of the process variable levels is chosen and all blends are run at

this combination. This procedure is continued until all combinations of the process

variables are performed. Following a replication of the complete design, the split-

plot nature of the experiment leads to two error terms which are used to assess the

significance of the effects of the whole plot treatments, the subplot treatments, and

their interaction. Several regression-type models are considered for estimating the

effects of the process variables, the blending properties of the mixture components,

and interactions between the two. The paper explains how to estimate the regression

coefficients as well as how to obtain variances and perform hypotheses tests. Both

balanced and unbalanced cases are considered. The hypothesis testing procedures are

illustrated with two completely worked-out numerical examples.

Santer and Pan (1997) discuss subset selection procedures for screening in two-

factor treatment designs. The paper deals mainly with split-plot designs run in com-

plete blocks; however, the strip-plot design is also discussed. One factor serves as the

whole plot factor while the other is the subplot factor. The goal is to select a subset

of the treatment combinations associated with the largest mean. Subset selection

procedures are given for additive and nonadditive factor cis,. where neither of the













Table 9: Variance of the Regression Coefficients For a 2k With
One Hard-To-Change Factor (from Lucas and Ju (1992))

Var(b) =- A, + Ba,

Hard To Change Variable Other Terms
A B A B

1-P P I1-P
i- -p-i

P = 1/(2k-2 + 1) for the completely randomized
design.
P = 1 for the completely restricted design.
P = (2k-l 2)/[2(2k-l 1)] for the partially
restricted design.


procedures depend onl the block variance.

Miller (1997) considers various fractional-factorial structures in strip-plot experi-

ments. These strip-plot experiments are identical in nature to the strip-block experi-

ments, arrangement (c), discussed in Box and Jones (1992). Strip-plot configurations

can be applied when the process being investigated is separated into two distinct

stages and it is possible to apply the second stage simultaneously to groups of the

first-stage product. Miller uses an example involving four washing machines and four

dryers in two blocks. Sets of cloth samples are run through the washing machines,

and then the samples are divided into groups such that each group contained exactly

one sample from each washer. Each group of samples would then be assigned to one

of the dryers. The response of interest was the extent of wrinkling.

It is convenient to represent strip-plot structures as rectangular arrays of experi-

mental units in which the levels of one treatment factor (or set of factors) are assigned












to the rows and the levels of a second treatment factor (or set of factors) are assigned

to the columns. Table 10 represents the laundry experiment in which each square

represents a cloth sample, rows represent sets of samples that were washed together,

and columns represent sets of samples that were dried together. The ANOVA table

for the laundry example, which is divided into "strata" corresponding to blocks, rows,

columns, and units, is given in Table 11. When making inferences about the effects

in a particular stratum, the estimate of variation must be based on the residual term

for that stratum.

Miller (1997) proposes a method for constructing strip-plot configurations for

fractional-factorial designs which consists of three steps:

1. Identify a suitable design for applying row treatments to rows ignoring columns;

2. Identify a suitable design for applying column treatments to columns ignoring

rows;

3. Select a suitable fraction of the product of the row and column designs.

The method is applied for two-level designs and then extended to m-level and mixed-

level designs. The procedure for two-level designs is presented here; for details on the

extended cases, see Miller (1997).

Consider the situation in which a proper fraction of a two-level factorial design is

to be run in a strip-plot arrangement using b = 2 blocks. Each block has r = 2M

rows and c = 2" columns. Let K and k represent the number of row and column

factors, respectively, and define Q = K (w + M) and q = k (w + mn). Then, the

procedure is as follows:


















Table 10: Strip-plot Configuration of the
Laundry Experiment (from Miller (1997))

Dryer Dryer
Washer 1 2 3 4 Washer 1 2 3 4
1 1
2 2
3 3
4 4
Block 1 Block 2


Table 11: ANOVA Table for the Laundry Example (from Miller (1997))

Strata Source df E(MS)
Block Blocks 1 a2 + 4a0 + 4a0, + 16a2
4
Row W-Washer 3 a2 + 4aR + (8/3) E W?
j=1
Row Residual 3 a2 + 4aR
4
Column D-Dryer 3 a2 + 474 + (8/3) Z Dk
j=l
Column Residual 3 a2 + 47C
4 4
Unit W x D 9 a2 + (1/9) E E [WD]?k
j=1 k=i
Unit Residual 9 a2












1. Select a row design that consists of a 2K-Q design in b blocks;

2. Select a column design that consists of a 2k-q design in b blocks;

3. Consider the product of the designs in steps 1 and 2 and select a Latin-Square

fraction of this product.

The selection of the design in steps 1 and 2 can be made on the basis that the analyses

for the row stratum and the column stratum will essentially be the analyses of these

designs. The Latin-Square fraction is selected so that the confounding array effects

in the unit stratum have desirable properties.

Mee and Bates (1998) consider split-lot experiments involving the etching of silicon

wafers. These experiments are performed in steps where a different factor is applied

at each step. Thus, there are an equal number of steps and factors. Specifying a

split-lot design involves determining the following:


1. the number of process steps with experimentation;

2. the number of factors and their levels at each processing step with experimen-

tation;

3. the subplot size at each processing step;

4. the number of wafers (experimental units) in the entire experiment;

5. a plan that details for each experimental wafer the process subplot at each step.

Mee and Bates emphasize symmetric designs, which are designs having the same

subplot size at each experimentation step.












The experimental plan in item 5 above will be determined as follows. First, to

define b subplots at each step, obtain b 1 contrasts for each experimental step. Then

assign factors to contrasts within the group intended for their respective processing

step. This is done in a way that gives the most information on the interaction effects

of interest. The approach is to determine a set of independent contrasts that can

be cycled to produce additional sets. The initial set of independent contrasts must

be chosen so that the groups of effects remain disjoint. This process and the result-

ing designs are illustrated for a variety of 64-wafer experiments (see .r.v and Bates

(1998)). Split-lot designs for three-level factors are also discussed. It should be noted

that if there are only two steps, the procedures by Miller (1997) can be applied with

one or with many factors at each step.
















CHAPTER 3
INCOMPLETE SPLIT-PLOT EXPERIMENTS


The focus of attention in factorial experiments centers on the effects of numerous

factors and their interactions. An important class of factorial experiments is the 2k

factorials where each of the k factors is assigned two levels. These experiments are

very useful in exploratory investigations as well as optimization problems because

they allow a large number of factors and their interactions to be examined.

Since there are only two levels of each factor, they will be denoted as low and high

for ease of reference. A treatment combination pertains to a level of each and every

factor and will be designated by lower case letters using the following conventions:

If a factor is at its low level, the corresponding letter is omitted from the treat-

ment designation. Conversely, if a factor is at its high level, the corresponding

letter is included.

When all factors are at their low levels, the treatment will be designated by the

symbol (1).


Under this notation, the treatments for a 22 factorial experiment in factors P and Q

are designated as (1), p, q, and pq. Factors and their effects will be designated by

capital letters.

Factorial experiments become large very rapidly so that often a single replicate

of the N = 2k runs requires more resources than are available, even with a moderate













number of factors, k. Even when resources are available, we may not want to estimate

all of the 2k 1 factorial effects. As an example, with k > 3, interactions involving

3 or more factors are generally considered to be negligible or of little importance.

Thus, a single replicate of a 2' requires 128 experimental units and provides a 64-fold

replication of each main effect. Of the 127 effects that can be estimated, only 28 may

be of major interest (seven main effects and 21 two-factor interactions).


3.1 Fractional Factorials


Finney (1945) proposed reducing the size of the experiment by using only a frac-

tion of the total number of possible treatment combinations. Such experiments are

called fractional factorials. He outlined methods of constructing fractions for 2k and
3k experiments. For screening purposes, Plackett and Burman (1946) gave designs

for the minimum possible number of experimental units, N = k + 1 where N is a

multiple of 4, and pointed out their utility in physical and industrial research. Since

then, these designs have found many applications, particularly in industrial research

and development. Their chief appeal is that they enable a large number of factors,

generally 5 or more, to be included in an experiment of practical size so that the

investigator can discover quickly which factors have an effect on the response. In this

chapter, the discussion will be limited to the case where every factor has only two

levels.

A 2k experiment that is reduced by a factor of 2-p will be called a 2k-p fractional

factorial experiment. These experiments have two major problems which can limit

their usefulness:












1. Every linear contrast of the treatments estimates more than one effect; hence,

each effect is aliased with one or more other effects. This can lead to the

misinterpretation of an effect which is not likely to happen with a complete

factorial experiment.

2. There is no independent estimate of experimental error.


Despite these limitations, fractional factorial experiments are used in exploratory

research and in situations that permit follow-up experiments to be performed. They

have been especially useful in industrial research and development where experimen-

tal errors tend to be small, the number of factors being investigated is large, and

experimentation is sequential. As a tool for exploratory research, fractional factorials

provide a means to efficiently evaluate a large number of factors using a relatively

small number of experimental units. This allows important factors to be detected

and unimportant factors to be screened or discarded rather than committing a large

amount of experimental resources on all of the factors.

Effects that are estimated by the same linear combination of treatments are called

aliases. Which effects are aliased depends on the factorial effects used to select the

treatments. The defining contrast is the effects) that is confounded with the constant

effect, I. It can be represented as an equation by setting the confounded effect equal

to I. The alias chain for an effect is found by forming the generalized interaction of

the effect with all terms in the defining contrast. For example, if a 23-1 fraction in

factors A, B, and C is run with defining contrast I = ABC, then the alias of the

main effect A is A(I) = A2BC which gives A = BC since A2 = I. Therefore, the













alias chains for the main effects, A, B and C are as follows:

A =BC
B = AC
C =AB.

For a 2k-P, there are 2P 1 effects in the defining contrast. The experimenter can

select any p factorial effects to be the defining contrast. The remaining 2P p 1

factorial effects are automatically determined as being the generalized interactions

among the p effects.

Box and Hunter (1961a, 1961b) classified fractional factorial plans by their degree

of aliasing of effects. This measure is called the resolution of the plan. The number

of letters in the shortest member of a set of defining contrasts determines the design's

resolution. Three important resolutions are


1. Resolution III- in which main effects are aliased with two-factor interactions;

2. Resolution IV in which main effects are aliased with three-factor interactions

and two-factor interactions are aliased with other two-factor intera;i tioii-:

3. Resolution V where two-factor interactions are aliased with three-factor in-

teractions.


Of course, if all three-factor and higher interactions are negligible, a design with

Resolution V is desired because it will allow the estimation of all main effects and

two-factor interactions since they are aliased with negligible effects.












3.2 Confounding

Suppose that a 2k factorial experiment is to be run in blocks. As noted earlier, the

main disadvantage of 2k factorial experiments is their size. Consequently, even for a

moderate number of factors, it may not be possible to find blocks with the required

number of homogeneous experimental units. When this occurs, it is necessary to use

smaller-sized blocks or incomplete block designs.

With an incomplete block design, there must be some loss of information. A

balanced incomplete block design, if it exists, distributes this loss equally to all treat-

ments. However, in factorial experiments, it is the main effects and interactions that

are important. For most factorial experiments with more than three factors, it is

highly unlikely that all effects, especially the higher-order interactions, are important.

If some effects can be assumed negligible prior to performing the experiment, then

a better procedure for constructing incomplete blocks, originally suggested by Fisher

(1926), would be finding arrangements which completely or partially sacrifice the in-

formation on these effects so that full information can be obtained on the rest. This

is done by forcing the comparisons among the blocks to be identical to the contrasts

for the negligible effects. Effects that are estimated by the same linear combination

of the treatments are said to be confounded. As a result, it is impossible to determine

if the observed difference is due to differences in blocks or due to the factorial effects

that are aliased woth the blocks.

Effects selected to be confounded with blocks are called the defining contrasts

since they determine which treatments will occur together in a block. These effects

are selected by the experimenter and should be effects thought to be negligible since












they are no longer separately estimable. Generally, these effects will be three-factor

interactions or higher so that all main effects and two-factor interactions can be

estimated.

When the block size of 2k is reduced by 2-p, each block will contain 2k-p experi-

mental units and each complete replicate will contain 2P blocks. In this case, it will

be necessary to confound 2P 1 effects in each replicate. The experimenter chooses p

of these effects with the remaining 2p p 1 effects being the generalized interactions

of the original p effects. When more than one replicate of the 2k-p fractional factorial

is performed, two types of confounding are possible:


1. Complete the same set of effects is confounded in each replicate;

2. Partial different sets of effects are confounded in different replicates.


Complete confounding is used whenever all information on the confounded effects

can be sacrificed. This should only be used when all confounded effects are believed

to be negligible. Complete confounding creates no problems with the analysis. It is

only necessary to find the effect totals for all unconfounded effects.

There are situations where effects believed to be important must be confounded,

for example, when available resources force the use of small block sizes. In these cases,

partial confounding is used. Partial confounding means confounding different effects

in different replicates so as to allow estimation of all effects. These estimates use only

the data from the replicates in which the effect is unconfounded. Thus, there will be

greater precision on effects that are unconfounded than on effects that are partially












confounded. While the amount of information is reduced, statistical significance of

each effect can be ascertained.


3.3 Confounding in Fractional Factorials


Although only a fraction of the treatments are included in a 2Ck-P experiment, this

number may still be too large for available blocks. As in any factorial experiment,

confounding is used to reduce the block size. Confounding an effect in a fractional

factorial experiment also confounds all of its aliases.

Consider a 26`1 fractional factorial experiment using the "be.r" defining contrast

for a half-replicate, I = ABCDEF. This requires 32 homogeneous experimental

units. If these are not available, then blocks of smaller size can be created by con-

founding additional effects. Suppose blocks of size 16 experimental units are available.

To create two blocks of size 16 for the 32 treatments it is necessary to confound one

effect. Since ABCDEF was used to define the half-fraction, it would appear logical

to select a five-factor interaction, say, ABODE. However, the alias of this interac-

tion or generalized interaction of the effect with ABCDEF is F and will also be

confounded with blocks. A better choice is to confound any three-factor interaction

since its alias will also be a three-factor interaction. As a result, no information is

lost on potentially important effects.

The word '"b(-,t." should be clarified. It is referring to the design which has the

least amount of aliasing among important effects which are usually thought to be

main effects and two-factor interactions. If important effects are not aliased with each

other, then 'Ljvt" refers to the design with highest Resolution. Therefore, "best" is













a criterion based onil estiinability. Throughout this chapter, wherever the phase 'best

design" is used it will be under the above setting.

3.4 Combining Fractional Factorials and
Confounding in Split-Plot Experiments

Splitting the plots or experimental units is possible with any experimental design.

The design refers to the assignment of the whole plot and subplot treatments and is

selected in order to control the known sources of extraneous variation. Regardless of

the choice of design, the subplot treatments can be thought of as being arranged in

blocks where the whole plots are the blocks. In each whole plot, if all the subplot

treatments can be run, then the situation resembles that of a complete block design

as far as the subplot treatments are concerned. However, there are situations where

in each whole plot not all of the subplot treatments can be performed so that some

form of an incomplete block design must be used. If the subplot treatments result

from a 2k factorial structure, then the methods discussed in the previous sections of

this chapter can be applied to reduce the number of subplot treatments in a whole

plot.

Consider the situation where both the whole plot treatments and the subplot

treatments have a 2k factorial structure. Assume that the design for the whole plot

treatments is a CRD. Suppose, only a fraction of the whole plot treatments are of

interest and only a fraction of the subplot treatments can be run for each whole plot.

We will consider the situation involving noise factors and design factors. The noise

factors will be the whole plot factors. Therefore, the goal of the experiment is to

estimate the following:












main effects for the whole plot factors;

main effects for the subplot factors;

two-factor interactions between the whole plot and subplot factors;

and if possible, two-factor interactions among the subplot factors.

Note that if there were sufficient resources to run all whole plot treatments and

subplot treatments, then all four goals would be automatically satisfied. However, in

most situations, this is not economically possible. Therefore, we shall try to estimate

as many effects as is possible within the restrictions on the resources available.

The idea of confounding effects in order to reduce the number of subplot treat-

ments per whole plot treatment and achieve the second goal has been around for some

time. Kempthorne (1952) has a section devoted to confounding in split-plot experi-

ments. Addelman (1964) also discusses ways of accomplishing this. Recently, the use

of split-plot experiments in industry has generated renewed interest in confounding.

Huang, Chen, and Voelkel (1998) and Bingham and Sitter (1999) discuss minimum-

aberration designs for factors with two-levels. This technique helps to improve the

estimation problem by raising the resolution concerning the subplot factors, but one

must be careful with the whole plot x subplot interactions. Bisgaard (1999) uses

inner and outer arrays, with factors at two-levels, as in robust parameter design and

provides the standard errors for various contrasts among the whole plot and subplot

factors.

We will use an example to compare the use of confounding in a split-plot exper-

iment. Consider a split-plot experiment with three whole plot factors, A, B, and C,












and three subplot factors, P, Q, and R where all factors have two levels. Suppose

only 16 runs are possible among the 64 total number of combinations. There are two

ways to allocate the whole plots and subplots for this experiment. We can use four

whole plots with each whole plot containing four subplots or we can use eight whole

plots with each whole plot containing two subplots. The goal of the experiment is to

estimate all six main effects and as many of the nine two-factor interactions between

the whole plot and subplot factors as is possible, although it is believed that some

two-factor interactions among the subplot factors might be significant. To conserve

space in the tables, the confounding structure or alias chains will be given only up to

order two. Therefore, if there is a blank space in the alias table, it means that the

effect is aliased with interactions of order higher than two.

First, suppose that the experimenter ignores the split-plot structure by consid-

ering the factors as a 26 factorial in a completely randomized design. Actually, the

experimenter would use a 26-2 fractional factorial design to obtain the 16 runs. The

best defining contrast is


I = ABCP = CPQR = ABQR,

which has Resolution IV. The layout is given in Table 12 and the alias chains are

given in Table 13. All main effects can be estimated, but two-factor interactions are

aliased with each other. Even if we assume that all two-factor interactions among A,

B, and C and all two-factor interactions among P, Q, and R are negligible, there is

still a problem since AQ is aliased with BR and AR is aliased with BQ. In other

words, some of the interactions we are interested in are aliased with each other.

















Table 12: Design Layout for 26-2 With Defining
Contrast I = ABCP = CPQR = ABQR


abcp ab cp
acr acq cpqr
bcq bcr bpr
apq qr apr


abcpqr
abqr
bpq
(1)


Table 13: Alias Structure for 26-2


A
B
C
P
Q
R
AB
AC
AP
AQ
AR
CQ
CR


CP+QR
BP
BC
BR
BQ
PR
PQ












Table 14: Design Layout for the Combined 23-1 x 23-1
With Defining Contrast I = ABC = PQR = ABCPQR

a b c abc
P P P P
pqr pqr pq pqr

q q q q
r r r r
pqr pqr pqr pqr


A second method, incorporating the split-plot nature and using four whole plots,
is to consider reducing the whole plot factors and subplot factors separately using
fractional factorials. A 23-1 fractional factorial with defining contrast I = ABC
will be used for selecting the whole plot treatments and combined with a 23-1 with
defining contrast I = PQR in selecting the subplot treatments (see Table 14). The
overall defining contrast for the experiment is

I = ABC = PQR = ABCPQR,

and the alias structure is shown in Table 15. Once we consider the split-plot structure,
the best we can do at the whole plot level is a Resolution III design. This method
provides a good design for estimating the two-factor interactions between the whole
plot and subplot factors. However, we must assume that the two-factor interactions
among the subplot factors are negligible in order to estimate the main effects for the
subplot factors.
Method three uses split-plot confounding and four whole plots. At the whole
plot level, a 23-1 fractional factorial with defining contrast I = ABC is used. Then,
the three-factor interaction, PQR, is confounded with factor C to reduce the eight













Table 15: Alias Structure for 23-1 x 23-1

A = BC
B = AC
C = AB
P = QR
Q = PR
R = PQ
AP =
AQ =
AR =
BP =
BQ =
BR =
CP =
CQ =
CR =



subplot treatments to four per whole plot (see Table 16). The idea is to put the

positive fraction of PQR wherever C is positive and the negative fraction wherever

C is negative. The overall defining contrast is given by


I = ABC = CPQR = ABPQR


with the alias structure provided in Table 17. This design is better than the second

design in terms of aliasing of the main effects for the subplot factors, but cannot

estimate all nine whole plot by subplot factor interactions without assuming that PQ,

PR, and QR are negligible. If, on the other hand, it is reasonable to assume that the

whole plot factor C will not interact with any of the subplot factors, then PQ, PR,

QR, the main effects for subplot factors and the remaining six whole plot by subplot













Table 16: Design Layout for Split-Plot Confounding
With Defining Contrast I = ABC = CPQR = ABPQR

a b c abc
(1) (1) p p
pq pq q q
pr pr r r
qr qr pqr pqr


factor interactions can be estimated using this design. Also, on a iiii.,iltini level,

some experimenters would feel more comfortable with this design since it uses all 8

subplot treatments.

The fourth method uses eight whole plots and split-plot confounding. Since there

are eight whole plots, the complete 23 factorial can be used for the whole plot fac-

tors. However, we must now reduce the number of subplots to two per whole plot.

This implies that we must confound two members in the defining contrast and their

generalized interaction completes the defining contrast. Using split-plot confounding,

the defining contrast is


I = ABPQ = ACQR = BCPR,


with the layout given in Table 18 and the alias structure given in Table 19. This design

is good for estimating main effects but has some serious deficiencies with interactions.

One possible problem with designs that use eight whole plots is cost. If the whole

plot factors are costly to change, then using eight whole plots as opposed to four

might be impractical. Another problem with designs using eight whole plots is the

breakdown of the degrees of freedom. There are 7 df for the whole plot design and














Table 17: Alias Structure for Split-Plot Confounding

A = BC
B = AC
C = AB
P=
Q =
R =
AP =
AQ=
AR=
BP=
BQ=
BR=
CP = QR
CQ = PR
CR = PQ


Table 18: Design Layout for Split-Plot Confounding
in 8 Whole plots With I = ABPQ = ACQR = BCPR

(1) a b ab c ac bc abc
AB+ AB- AB- AB+ AB+ AB- AB- AB+
AC+ AC- AC+ AC- AC- AC+ AC- AC+

PQ+ PQ- PQ- PQ+ PQ+ PQ- PQ- PQ+
QR+ QR- QR+ QR- QR- QR+ QR- QR+

pqr pr qr pq pq qr pr pqr
(1) q p r r p q (1)













Table 19: Alias Structure for Split-Plot Confounding
For 8 Whole Plots With I = ABPQ = ACQR = BCPR


A
B =
C
AB = PQ
AC = QR
BC = PR
P =
Q =
R=
AP = BQ
AQ = BP+ CR
AR = CQ
BR = CP


only 8 df left for the subplot factors and whole plot x subplot factor interactions.

Therefore, at the subplot level there are only enough df to estimate either three

main effects and five interactions or eight interactions. This may not be sufficient to

estimate all the effects of interest.


3.5 Discussion of Minimum-Aberration Split-Plot Designs


In split-plot designs using some sort of confounding, there is a concept of partial

resolution. The partial resolution of the whole plots refers to the resolution of terms

in the defining contrast involving only whole plot factors. The partial resolution of

the subplot factors refers to the resolution of terms in the defining contrast involving

either only subplot factors or both whole plot and subplot factors. Recall that the

definition of minimum-aberration is the design that has smallest number of words in













the defining contrast with the fewest letters. Therefore, it is looking at the overall

resolution of the design and not the partial resolution.

Huang, Chen and Voelkel (1998) and Bingham and Sitter (1999) have tabled

minimum-aberration (MA) designs for 16 and 32 runs for up to 10 factors. When a

design is needed that fits in these restrictions, one can simply look up the appropriate

design in these tables. However, the MA designs in these tables do not take into

account other design issues such as which effects are the most important to estimate.

This concept seems to be overlooked in the literature. For example, suppose the whole

plot factors are noise factors and only their main effects are of interest. Now, further

suppose that the two-factor whole plot by subplot interactions are the most important

effects to estimate (which is the case in many experiments). Then, it is better to

fractionate the whole plot treatments and subplot treatments separately since this

would alias the two-factor interactions of interest with higher order interactions. Note,

this design would not be the MA design since the partial resolution of the whole plot

factors would be too low.

Another concern with MA designs is the allocation of the runs. Consider the

MA designs for 16 runs involving combinations of 2, 3, and 4 whole plot and subplot

factors. With the exception of the cases involving 2 whole plot factors with 3 or 4

subplot factors, all the other MA designs use eight whole plots with two subplots per

whole plot. This raises several concerns.

1. Typically in industrial experiments, the whole plot factors are hard-to-change

or costly-to-change factors. If they are hard to change, then it would make more

sense to only change them four times as opposed to eight. Also, if changing













these factors is expensive, then again changing them four times seems more

reasonable.

2. It is not an efficient allocation of the degrees of freedom. Using eight whole

plots with two subplots per whole plot gives 7 df for whole plot factors and 8 df

for subplot factors and whole plot x subplot factor interactions. This allocates

a disproportionate number of degrees of freedom to the whole plot factors. In

contrast, using four whole plots with four subplots per whole plot gives 3 df for

whole plot factors and 12 df for terms involving subplot factors.

3. Using two subplots per whole plot is similar to using blocks of size two in a

block design which is not generally recommended.

MA designs are in general "good" designs, however, for split-plot experiments they

are based purely on the overall resolution of the design instead of partial resolution.

Also, they only use split-plot confounding to reduce the size of the experiment and

are not motivated by any other concerns such as those mentioned above.


3.6 Adding Runs to Improve Estimation


With the concerns of the previous section in mind, mainly the allocation of degrees

of freedom, we will focus our attention on 16 run designs that use four whole plots

with four subplots per whole plot. Within this allocation of the resources, the best

design is found for the two types of confounding discussed in the example in section

3.4. These are split-plot confounding and fractionating of the whole plot and subplot

factors separately (called the Cartesian product design in Bisgaard (1999)). The best













design is found using the "mininmum-aberration" (MA) criterion, but this differs from

just using MA because we are restricted to using four whole plot treatments with four

subplot treatments per whole plot. Therefore, the best resolution is desired within

this restricted setting. With the exception of the cases involving 2 whole plot factors

with 3 or 4 subplot factors, these designs will not be the overall MA design.

Once the sixteen run design is found, eight additional runs are considered in order

to break some of the alias chains. Along with breaking some of the alias chains, extra

degrees of freedom are now available in order to estimate additional effects. The

result is a 24 run design which we feel is a nice compromise between the 16 and 32

run designs presented in Huang, Chen and Voelkel (1998) and Bingham and Sitter

(1999). Which eight treatments should be added is the question to be answered next,

but first we briefly discuss foldover designs.

The concept of a foldover design was introduced in Box and Hunter (1961b).

Suppose an experiment involving k factors each at two levels is to be performed and

an initial Resolution III fractional factorial design is used. One way to do a the

foldover is to repeat the initial design and change the levels of one of the factors while

leaving the levels of the other factors unchanged. This allows the estimation of all

the interactions that contain the folded factor but doubles the size of the experiment.

A related idea is that of semifolding which folds only the points that are at the high

level of a factor (or the low level). The addition of the new points breaks certain alias

chains and allows estimates of interactions involving the factor that is semifolded to

be calculated while adding only half as many points as a complete foldover design.

In the rest of this chapter, we apply seminifolding to split-plot experiments.













In most of the cases studied here, the eight additional points are added to the

initial 16 run design by semifolding on either one or two subplot factors which results

in a 24 point design consisting of four whole plots with six subplots per whole plot.

he .,e designs will have 3 df for the whole plot treatments and 20 df for the subplot

treatments. The initial 16 point design is balanced over the subplot factors-each

factor has the same number of high and low levels present-which allows for the

effects to estimated with equal precision. It is desired to preserve this balance of the

subplot factors in the 24 point design as well as maintain the same number of subplot

treatments per whole plot. Therefore, in half of the whole plots the semifolding is on

the high level of a subplot factor while in the other half the semifolding is on the low

level of that factor.

In some cases, it is necessary to fold on a whole plot factor in order to estimate

the main effects of the whole plot factors. In these cases, two whole plots are added so

that the 24 point design consists of six whole plots with four subplots per whole plot.

These designs will have 5 df for the whole plot treatments and 18 df for the subplot

treatments. All nine cases involving 2, 3, and 4 whole plot and subplot factors are

considered. However, two cases do not need to be improved upon.


1. Two whole plot factors and two subplot factors: the 16 points represent the full

factorial. Since no fractionating or confounding is needed, there is nothing to

improve upon.

2. Two whole plot factors and three subplot factors: in this case, the MA design

presented in Huang, Chen and Voelkel (1998) is the best design possible and












allows estimates all of the main effects and all of the two-factor interactions.

For all situations involving less than four whole plot factors, a general method can

be used to construct 24 run designs. First, construct a 16 run design that uses four

whole plots with four subplots in each whole plot.


If there are two whole plot factors, then use the complete factorial in the whole

plot factors.

If there are three whole plot factors, then use one of the two half fractions found

using the defining contrast I = ABC.


To complete the 16 run design use either split-plot confounding or a separate fractional

factorial in the subplot factors to decide which subplot treatments will appear in each

whole plot. After the 16 run design is selected on, use semifolding to obtain two extra

subplot treatments for each whole plot treatment. The semifolding is, for the most

part, done on two subplot factors. In two of the whole plots, the subplot treatments

are folded on one factor (the high level of the factor in one whole plot and the low

level of the factor in the other whole plot). In the remaining two whole plots, the

subplot treatments are folded on a different subplot factor (again, on the high level

in one whole plot and the low level in the other whole plot). In the special case of

three subplot factors, the semifolding is done on just one factor since there is only

one alias chain in the defining contrast.

When there are four or more whole plot factors, using 4 whole plots results in

insufficient degrees of freedom to estimate the main effects of the whole plot factors.












Therefore, the additional eight runs will be added in the form of two extra whole

plots. This leads to a 24 run design with 6 whole plots with 4 subplots per whole

plot. The whole plot treatments used in the two additional whole plots are found

by semifolding on a whole plot factor. However, which subplot treatments should be

used in the two additional whole plots is case specific. To illustrate how to apply

these methods, the seven remaining cases involving 2, 3 and 4 whole plot and subplot

factors will be presented. For all the cases, tables which show the designs in highs

and lows for each factor are given in Appendix A.

For these designs, the aiily.-i.n could use one normal probability plot for the whole

plot effects and a separate plot for the effects involving the subplot factors and the

interactions between whole plot and subplot factors. One assumption of a normal

probability plot is that the effects are independent. This is not the case here. However,

it will be shown later in this chapter that the correlations are low (near zero) and

that a normal probability plot is therefore valid. In some cases there are degrees

of freedom left at the subplot level so that if desired they can be used to estimate

the an error variance. It should be reiterated that the goal of the experiment is to

estimate as well as test for significance the main effects for the whole plot factors, the

two-factor interactions between whole plot and subplot factors, the main effects of

the subplot factors, and if possible two-factor interactions among the subplot factors.

2 WP Factors (A, B) and 4 SP Factors (P, Q, R, S)

To obtain a 16 point design under this situation, only the subplot treatments need

to be fractionated or confounded. First, consider fractionating the subplot treatments.













The defining contrast is I = PQR = QRS = PS which is resolution II. Alias chains

involving both P and S need to be broken. Therefore, the additional eight points

are obtained by semifolding on high and low P in two whole plots and on high and

low S in the other two. The 24 point design is shown in Table 20. The chains are

almost completely broken. Only two of the three interactions. BP, BS, and PS

are estimable. If it can be assumed that PS is negligible, then everything else is

estimable. It is not unreasonable to believe that with four factors one of the two-

factor interactions is negligible and the experimenter should be able to help determine

which interaction is most likely to be negligible.

Next, consider split-plot confounding. The defining contrast is I = APQR =

BQRS = ABPS which is resolution IV. This design is the MA design given in Huang,

Chen and Voelkel (1998). Again, alias chains involving both P and S need to be

broken. Therefore, the additional eight points are obtained by semifolding on high

and low P in two whole plots and on high and low S in the other two. The 24

point design is shown in Table 21. All of the two-factor interactions between whole

plot and subplot factors can be estimated except BS which is aliased with QR. If

QR is assumed to be negligible, then BS can be estimated. Most of the two-factor

interactions among the subplot factors are aliased with each other. However, with

the 24 point design we can estimate three of the two-factor interactions between

the subplot factors without making any assumptions about negligibility, which is an

improvement over the MA design.
















Table 20: 24 Point Design for the Case of 2 WP Factors and 4 SP Factors Using
the Same Fraction [HP(HS)-denotes high P(S) and LP(LS)-denotes low P(S)]


a b ab (1)
q q q q
r r r r
ps ps ps ps
pqrs pqrs pqrs pqrs
Fold on
HP LP HS LS
s pq p qs
qrs pr pqr rs


Table 21: 24 Point Design for the Case of 2 WP Factors and 4 SP Factors Using
Split-Plot Confounding [HP(HS)-denotes high P(S) and LP(LS)-denotes low P(S)]


a b ab (1)
p s q qr
pqr pq r pqs
qs pr ps prs
rs qrs pqrs (1)
Fold on
HP LP HS LS
(1) ps p qrs
qr pqrs pqr s













Table 22: 16 Point Design for the Case of 3 WP Factors and 2 SP Factors
Using a Fraction Factorial of the Whole Plot Factors

a b c abc
P P P P
q q q q
pq pq pq pq
(1) (1) (1) (1)


3 WP Factors (A, B, C) and 2 SP Factors (P, Q)

In this case, only the whole plot factors need to be fractionated. Since nothing

needs to be done to the subplot factors, there is only one 16 point design. The defining

contrast is I = ABC which is Resolution III. Since the design estimates everything

set out in the goal of the experiment, no points need to be added to this design.

However, note that this is not the MA design which is run using eight whole plots

with 2 subplots per whole plot. The 16 point design in four whole plots with four

subplots per whole plot is shown in Table 22.

3 WP Factors (A, B, C) and 3 SP Factors (P, Q, R)

To obtain a 16 point design in this situation, both the whole plot and subplot

treatments need to be fractionated or confounded. First, consider fractionating the

whole plot and subplot treatments separately. The defining contrast is I = ABC =

PQR = ABCPQR which is resolution III. The two-factor interactions between whole

plot and subplot factors are already estimable. Therefore, there is only one alias

chain that needs to be broken, and that is associated with PQR. The additional













Table 23: 24 Point Design for the Case of 3 WP Factors and 3 SP Factors
Using the Same Fraction [HP-denotes high P and LP-denotes low P]

a b c abc
P P P P
q q q q
r r r r
pqr pqr pqr pqr
Fold on
HP LP LP HP
(1) pq pq (1)
qr pr pr qr


eight points are obtained by semifolding on factor P. The 24 points design is shown

in Table 23. The chain has been broken and now P, Q, R, PQ, PR, and QR are all

estimable. There are 5 df left over for a subplot error term.

Next, consider split-plot confounding. The defining contrast is I = ABC =

ABPQR = CPQR which is also resolution III. The two-factor interactions between

whole plot factors A and B and the subplot factors are already estimable. Therefore,

the only alias chain that needs to be broken is CPQR. The additional eight points

are obtained by semifolding on factor P while being careful to fold both high and low

P where C is high and where C is low. The 24 point design is shown in Table 24. The

chain has been broken and now all of the effects of interest including the two-factor

interactions among the subplot factors are estimable. There are 5 df left over for a

subplot error term.













Table 24: 24 Point Design for the Case of 3 WP
Using Split-Plot Confounding [HP-denotes high

a b c abc
Pq Pq P P
pr pr q q
qr qr r r
(1) (1) pqr pqr
Fold on
HP LP LP HP
q pqr pq (1)
r p pr qr


Factors and 3 SP Factors
P and LP-denotes low P]


3 WP Factors (A, B, C) and 4 SP Factors (P, Q, R, S)

To obtain a 16 point design in this situation, both the whole plot and subplot

treatments need to be fractionated or confounded. First, consider fractionating the

whole plot and subplot treatments separately. The defining contrast is I = ABC =

PQR = QRS = PS = ABCPQR = ABCQRS = ABCPS which is Resolution

II. In order to estimate the subplot factor main effects and possibly the two-factor

interactions among the subplot factors, the two chains PQR and QRS with resulting

chain PS need to be broken. The additional eight points are obtained by semnifolding

on both factors P and S. The 24 points design is shown in Table 25. The chains

are almost completely broken. Two resulting chains AP = PS and AS = PS are

left. The aliasing here means that the sum of AP and AS equals PS. Therefore, the

model can accommodate the fitting of any two of the three factors. So for example, if

PS is assumed negligible, then the effects of AS and AP are estimable. There are 4

df left that can be used as an error term or used to estimate PQ, PR, QS and RS.













Table 25: 24 Point Design for the Case of 3 WP Factors and 4 SP Factors Using
the Same Fraction [HP(HS)-denotes high P(S) and LP(LS)-denotes low P(S)]

a b c abc
q q q q
r7 r r r
ps ps ps ps
pqrs pqrs pqrs pqrs
Fold on
HP LP HS LS
s pq p qs
qrs pr pqr rs


Next, consider split-plot confounding. The defining contrast is I = ABC =

BCPQR = ACQRS = ABPS = APQR = BQRS = CPS which is resolution

III. Not much of anything is estimable free of two-factor interactions. Again, the

additional eight points are obtained by semifolding on factors P and S. The 24 point

design is shown in Table 26. Again, the chains are almost completely broken. Three

resulting chains C = PS, AP = PS and BS = PS are left. The aliasing here means

that the sum of C, AP, and BS equals PS. Therefore, the model can accommodate

the fitting of any three of the four factors. So for example, assuming PS is negligible

allows for C, AP and BS to be estimated. Also, any two of the remaining five

two-factor interactions among the subplot factors can be estimated.


4 WP Factors (A, B, C, D) and 2 SP Factors (P, Q)


In this case, only the whole plot treatments need to be fractionated. Note, with

four whole plot factors there are only 3 df for whole plot factor effects. Hence, whole













Table 26: 24 Point Design for the Case of 3 WP Factors and 4 SP Factors Using
Split-Plot Confounding [HP(HS)-denotes high P(S) and LP(LS)-denotes low P(S)]


a b c abc
p s qr q
pqr pq pqs r
qs pr prs ps
rs qrs (1) pqrs
Fold on
HP LP LS HS
(1) ps qrs p
qr pqrs s pqr


Table 27: 24 Point Design for the Case of 4 WP Factors and 2 SP
Factors Using a Fractional Factorial of the Whole Plot Factors

Fold on A
b c ad abcd d bcd
P P P P P P
q q q q q q
pq pq pq pq pq pq
(1) (1) (1) (1) (1) (1)


plots will need to be added for all cases involving four whole plot factors. Since

nothing needs to be done to the subplot factors, there is only one 16 point design. The

defining contrast is I = ABC = BCD = AD which is resolution II. The additional

whole plots are obtained by semifolding on factor A. The 24 point design is shown in

Table 27. The chains are broken and everything is estimable.












4 WP Factors (A, B, C, D) and 3 SP Factors (P, Q, R)

To obtain a 16 point design in this situation, both the whole plot and subplot

treatments need to be fractionated or confounded. First, consider fractionating the

whole plot and subplot treatments separately. The defining contrast is I = ABC =

BCD = AD = PQR = ABCPQR = BCDPQR = ADPQR which is resolution

II. The additional whole plot treatments are obtained by semifolding on factor A.

The positive fraction, I = PQR, is run in one whole plot while the negative fraction,
I = -PQR, is run in the other whole plot. The negative fraction can be thought of

as semifolding on any subplot factor and placing all of the points in one whole plot

instead of two as was done in all the cases up until now. The 24 point design is shown

in Table 28. The chains are broken and everything is estimable.

Next, consider split-plot confounding. The defining contrast is I = ABC =

BCD = AD = CPQR = ABPQR = BDPQR = ACDPQR which is resolution II.

Besides breaking chains among the whole plot factors, the chain, CPQR needs to be

broken. The additional whole plot treatments are obtained by semifolding on factor

A. Again, the positive fraction, I = PQR, is run in one whole plot with the negative

fraction, I = -PQR, is run in the other whole plot. Again, this can be thought of

as semifolding each fraction on any subplot factor and placing all four points in the

same whole plot. The 24 point design is shown in Table 29. The chains are broken

and everything is estimable.



















Table 28: 24 Point Design for the Case of 4 WP Factors
and 3 SP Factors Using the Same Fraction
Fold on A
b c ad abcd d bcd
P P P P P Pq
q q q q q pr
r r r r r qr
pqr pqr pqr pqr pqr (1)












Table 29: 24 Point Design for the Case of 4 WP Factors
and 3 SP Factors Using Split-Plot Confounding
Fold on A
b c ad abcd d bcd
Pq P pq P P Pq
pr q pr q q pr
qr r qr r r qr
(1) pqr (1) pqr pqr (1)












4 WP Factors (A, B, C, D) and 4 SP Factors (P, Q, R, S)

As the number of both whole plot factors and subplot factors increases, it becomes

impossible to break all of the relationships and estimate all of the important effects.

Therefore, some effects will need to be assumed negligible. Also, in the case of four

whole plot factors and four subplot factors, there is insufficient degrees of freedom to

estimate the four subplot factor main effects and the sixteen two-factor whole plot

by subplot interactions. Thus, some effects cannot be estimated anyway. Assuming

these effects to be negligible enables the estimation of the remaining effects.

To obtain a 16 point design in this situation, both the whole plot and subplot

treatments need to be fractionated. First, consider fractionating the whole plot and

subplot treatments separately. The defining contrast is I = ABC = BCD = AD =

PQR = QRS = PS = ABCPQR = ABCQRS = ABCPS = BCDPQR =

BCDQRS = BCDPS = ADPQR = ADQRS = ADPS which is resolution II. Be-

sides breaking chains among the whole plot factors, the chains, ADPS and PS need

to be broken. The additional whole plot treatments are obtained by semifolding on

factor A. The subplots are semifolded on factor P in one whole plot and factor S in

another whole plot. The 24 point design is shown in Table 30.

Next, consider split-plot confounding. The defining contrast is I = ABC =

BCD = AD = ACPQR = BDQRS = ABCDPS = BPQR = ABDPQR =

CDPQR = ACDQRS = CQRS = ABQRS = DPS = APS = BCPS which is

resolution II. The additional whole plot treatments are obtained by semifolding on

factor A. Again, the subplot factors are semifolded on P and S. Care must be taken












when choosing which whole plots the subplot factors are semifolded. Otherwise, the

same treatment combinations will occur in both additional whole plots. This occurs

when the semifolding uses the whole plots containing the subplot treatments defined

by PQR+, QRS+ and PQR-, QRS- or PQR+, QRS- and PQR-, QRS+. Any other

combination is fine. In this section, P is semnifolded in the whole plot containing

whole treatment c (PQR-, QRS+) and S is semifolded in the whole plot containing

whole plot treatment abcd (PQR+, QRS+). The 24 points design is shown in Table

31.

Most of the chains are broken but some of the two-factor interactions among the

subplot factors are aliased with each other. Also, four of the sixteen two-factor inter-

actions between whole plot and subplot factors must be assumed negligible. These

terms are AS, CS, DS, and DP. This is fairly nice since three of these terms involve

subplot factor S. Therefore, if it is believed that one of the subplot factors is unlikely

to interact with the whole plot factors, these terms or effects could be assumed negli-

gible. This does not seem unreasonable. Now the 18 subplot df are partitioned into 4

df for the subplot factor main effects, 12 df for the whole plot by subplot interactions,

and 2 for two-factor interactions among subplot factors (these two effects can be any

pair except PQ and QS or PR and RS).


3.7 An Example

To illustrate how an experiment could be carried out and analyzed, an example is

presented. The example, from Taguchi (1987), involves the study of a wool washing

and carding process. The original experiment used a 213-9 x 23-1 inner and outer





















Table 30: 24 Point Design for the Case of 4 WP Factors and
4 SP Factors Using the Same Fraction


b
q
r
I'
ps
prs
pqrs


4


C
q
r
PS
ps
pqrs


+


ad abed
q q
r r
ps ps
pqrs pqrs


Fold on A
d bed
pq qs
pr rs
s p
qrs pqr


Table 31: 24 Point Design for the Case of 4 WP Factors and
4 SP Factors Using Split-Plot Confounding


b c ad abed
p qrs (1) q
pqr s qr r
qs pq pqs ps
rs pr prs pqrs


Fold on A
d bcd
pqrs qs
ps rs
q P
r pqr












array. For our purposes, we shall only consider the first three factors in the inner

array along with the three factors in the outer array. The outer array will make up

the whole plot factors while the inner array will have the subplot factors. The original

experiment was not run using restricted randomization, but it will be assumed that

it was in order to present the analysis.

The 24 run designs discussed earlier can be utilized. For this example, the design

given in Table 23 with separate fractions at the whole plot and subplot levels is used.

The only difference is that the Taguchi example uses the negative fraction of the whole

plot factors instead of the positive fraction. To correspond with the factor names in

the Taguchi example, let X, Y and Z be the whole plot factors and A, B and C be

the subplot factors. The design along with the responses is shown in Table 32.

The analysis involves fitting the 18-term model involving the main effects of the

whole plot factors, the main effects of the subplot factors, the two-factor interactions

among subplot factors, and two-factor interactions between whole plot and subplot

factors. This leaves five degrees of freedom for a subplot error term. Table 33 gives

the estimated effects and t-tests. The tests for the three whole plot factor main effects

are not correct and should be ignored. From Table 33, there appears to be an effect

due to the interaction of factors B and C. Since there are only 5 df for error, one

might choose to use a normal probability plot to investigate at the subplot level. The

design is not completely balanced or orthogonal which leads to some effects having

one standard error and others having a different standard error. Therefore, instead

of just plotting the effects, the effects are divided by their standard error and then

plotted. The plot is shown in Figure 1 and gives BC and ZC as significant effects.




















Table 32: 24 Point Design for the Example

X Y Z A B C Response
+ 19.0
+ 22.5
+ 26.0
+ + + 21.5
20.0
+ + 18.5
+ + + 16.0
+ 21.0
+ 20.0
+ + + 16.0
+ + 24.0
+ -____ + 23.0
+ + + 17.5
+ 21.0
+ 22.0
+ + + 22.0
+ + 21.0
____ + + 19.0
+ + + 19.0
+ 22.5
+ 26.5
+ + + 23.0
23.0
+ + 26.5






















Table 33: Effects Table for the Example


Effect Coeff
21.266
-0.937 -0.469
1.406 0.703
-2.156 -1.078
1.000 0.500
-0.812 -0.406
0.937 0.469
0.031 0.016
-0.187 -0.094
-0.563 -0.281
-0.094 -0.047
0.312 0.156
0.875 0.438
0.344 0.172
0.500 0.250
-1.312 -0.656
1.375 0.687
1.250 0.625
-4.438 -2.219
d Tests


nt





















Vali


Term
Constai
X
Y
Z
y
z
A
B
C
X*A
X*B
X*C
Y*A
Y*B
Y*C
Z*A
Z*B
Z*C
A*B
A*C
B*C
t Not


Std Error
0.4288
0.4951
0.4288
0.4288
0.4951
0.4951
0.4951
0.4288
0.4951
0.4951
0.4288
0.4288
0.4288
0.4288
0.4288
0.4288
0.4951
0.4951
0.4951


t-value
49.60
-0.95
1.64
-2.51
1.01
-0.82
0.95
0.04
-0.19
-0.57
-0.11
0.36
1.02
0.40
0.58
-1.53
1.39
1.26
-4.48


P-value
0.000
0.3871
0.162t
0.054t
0.359
0.449
0.387
0.972
0.857
0.595
0.917
0.730
0.354
0.705
0.585
0.186
0.224
0.262
0.007

























1.0 ______
*
0.9 S

0.8
0.7 5
0
8 0.6
.X 0.5
' 0.4 -
0.3

0.2 -
0.1 ZC
0.0 BC
SI I I I
-5 -4 -3 -2 -1 0 1 2
Effect/Standard Error


Figure 1: Normal Probability Plot for the Example













3.8 Summary

The main goal of this chapter is to understand some of the complications involved

with using the two types of confounding in split-plot experiments. If the design is

chosen using the MA criterion, then designs constructed by combining the fractional

factorial of the whole plot treatments with a fractional factorial of the subplot treat-

ments are not considered. This is because their partial resolution is too low. However,

it has been shown that depending on what is to be estimated, it may not be wise

to eliminate such designs. Also, for 16 run designs the MA criterion tends to select

designs with eight whole plots and two subplots per whole plot. These designs do

not take into consideration the possible increase in the cost of experimentation or of

factors whose levels are hard to change.

We have presented a 24 run design which is a compromise between the 16 run

and 32 run designs. We begin with a 16 run design using four whole plots with four

subplots per whole plot. Such a strategy accommodates hard-to-change factors as

well as cost considerations involving the experiment. Then, eight additional runs are

added using semifolding of one or two factors. These runs preserve the balance of

high and low levels of each subplot factor as well as maintain the same number of

subplots for each whole plot. Except for the cases involving four whole plot factors,

the additional runs are at the subplot level. Thus, as long as adding the runs is

feasible, it should not be too costly. Also, the extra runs allow for additional effects to

be estimated and/or add degrees of freedom for estimating the subplot error variance.

Though designs using split-plot confounding and separate fractions differ in what

they can estimate in 16 runs, there is not much difference in estimability when using













Table 34: Condition Numbers for the Various Cases


# of WP Factors # of SP Factors
2 4
2 4


Type of Confounding
Same Fraction
Split-Plot Confounding


Condition Number, K
4.05
3.36


3 3 Same Fraction 2.00
3 3 Split-Plot Confounding 2.00

3 4 Same Fraction 4.05
3 4 Split-Plot Confounding 3.36
4 Neither 2.00

4 3 Same Fraction 5.83
4 3 Split-Plot Confounding 2.00

4 4 Same Fraction 5.83
4 4 Split-Plot Confounding 3.36



the 24 run designs.

The phrase "the chains are broken" used throughout this chapter does not mean

that all of the effects are no longer aliased. Sometimes the effects are aliased at

a lower degree than unity (completely aliased). Therefore, there is some degree of

collinearity between the effects. To measure the magnitude of this collinearity, the

condition number

Largest Eigenvalue of (X'X)
SSmallest Eigenvalue of (X'X)

is calculated for each case (see Table 34). Many textbooks declare collinearity to be

a problem if K > 30. It is seen from Table 34 that collinearity does not seem to be a

problem for the cases considered in this chapter. The variance inflation factors (VIF)













are also calculated. They are not reported here, but none of the VIF's exceeds 3.

This confirms that the collinearity is mild.

The cases used in this chapter are chosen because they cover a wide range of

industrial applications. The methods described in this chapter can be applied to

experiments involving even more than four factors at either or both the whole plot

and subplot level. However, as is seen with the case involving four whole plot factors

and four subplot factors, not all chains can be broken. However, the additional

points should result in a design which estimates more effects with less assumptions on

negligibility than a 16 point design. If the cost and time of adding the eight points is

acceptable and the goals of the experiment are those discussed in this chapter, then

the 24 run designs can improve the estimability of important effects.

















CHAPTER 4
A NEW MODEL AND CLASS OF DESIGNS FOR
MIXTURE EXPERIMENTS WITH PROCESS VARIABLES


Experiments that involve the blending of two or more components to produce high

quality products are known as mixture experiments. The quality of the end product

depends on the relative proportions of the components in the mixture. For example,

suppose we wish to study the flavor of a fruit punch consisting of juices from apples,

pineapples, and oranges. The flavor of the punch depends on the relative proportion

of the juices in the blend.

Consider a mixture experiment consisting of q components. Let xi, for i =

1, 2,..., q, represent the fractional proportion contributed by component i. Then the

proportions must satisfy the following constraints
q
0 i=1
and the experimental region is a (q 1)-dimensional simplex, Sq. For q =3, S3 is an

equilateral triangle and for q = 4, 54 is a tetrahedron. Typically, the blends used in

a mixture experiment are the vertices or single-component blends, the midpoints of

the edges, centroids of faces, etc., and the centroid of the simplex.

In some mixture experiments, the quality of the product depends not only on the

proportions of the components in the blend, but also on the processing conditions.

Process variables are factors that do not form any portion of the mixture but whose

levels, when changed, could affect the blending properties of the components. Cornell













(1990) discusses an experiment involving fish patties. The texture of the fish patties

depends not only on the proportions of three fish species that are blended but also

on three process variables which are cooking temperature, cooking time and deep fat

frying time.

A concern with mixture experiments involving process variables is that the size

of the experiment increases rapidly as the number of process variables, n increases.

In the fruit punch or fish patty examples above, it may not be necessary to limit the

size of the experiment. However, in most industrial experiments, cost and time do

impose restrictions on the number of runs permitted. Therefore, a design strategy

that uses fewer observations is preferred over a design that does not.

Cornell and Gorman (1984) presented combined mixture component-process vari-

able designs for n > 3 process variables that use only a fraction of the total number

of possible design points. They considered process variables each at two levels and

suggest fractions of the 2' factorial be considered. Two plans involving the frac-

tional factorial design in the process variables were discussed. The first plan, called

a matched fraction, places the same 23'-1 fractional replicate design at each mixture

composition point. The other plan, called a mixed fraction, uses different fractions at

the composition points. Each plan was applied to the situation involving three mnix-

ture components and three process variables with the total number of design points

ranging from 56 for the combined simplex-centroid by full 23 factorial, to only 16,

which relied on running the one-quarter fraction. It should be noted that if inter-

actions among the process variables are likely to be pre.-int. the use of a fractional

factorial will result in bias being present in the coefficient estimates. Cornell and












Gorman give recommendations regarding the choice of design which depend on the
form of the model to be fitted and whether or not there is prior knowledge on the

magnitude of the experimental error variance.

Czitrom (1988, 1989) considered the blocking of mixture experiments consisting

of three and four mixture components. She used two orthogonal blocks to construct

D-optimal designs. Draper et al. (1993) consider mixture experiments with four

mixture components. They treat a combination of the levels of the process variables

as defining blocks. Orthogonally blocked mixture designs constructed from Latin

Squares are presented. The optimal choice of a design using D-optimality is also given.

While the reduction in the number of observations required can be great, obtaining

D-optimality comes with a price. The D-optimal designs require very nonstandard

values for the component proportions.

We propose an alternative approach to reducing the size of the experiment which

borrows ideas from the above references. The concept of running only a subset of the

total number of mixture-process variable combinations is borrowed from Cornell and

Gorman (1984), although our fraction will involve the mixture component blends as

well. To evaluate the fraction, we shall make use of the D-criterion criterion (Czitrom

(1988, 1989)). The next section provides a type of experimental situation which led

to this research. In the section that follows, a combined model which is slightly

different in form from the combined mixture-process variable models ordinarily used

is presented. The method for constructing the design and comparing it's D-criterion

is discussed in the fourth section. The final section of this paper contains details on

the analysis of the experiments using the proposed designs and model forms.













4.1 Experimental Situation

Historically in the mixture literature, the interest in the blending properties of the

mixture components has been higher than that of studying the effects of the process

variables. Generally, the process variables have been treated as "'noike" factors. The

primary focus on the mixture by process variable interactions has been on the effects

of the process variables on the blending properties of the mixture components.

In many industrial situations, the interest in the process variables is at least equal

to that in the mixture components. Consider the production of a polymer which is

produced by reacting together three specific components. The research laboratory

proposes a specific formulation which is the result of a highly controlled environment

with reagent grade chemicals and laboratory glassware. The plant personnel use this

formulation during the pilot plant and initial start-up of the full production pro-

cess. During this period, the plant personnel are trying to find the proper processing

conditions to produce a useable product profitably.

At some point, plant personnel need to reevaluate the polymer's formulation in

light of the actual raw materials and the plant's full scale production capabilities.

Plant personnel need to find the "optimal" combination of the formulation and pro-

cessing conditions.

Traditionally, in response surface applications, the model assumed for process op-

timization is a second-order Taylor series. Such an assumption is based on background

knowledge in knowing the true surface over the experimental region can be approx-

imated by fitting a second-order model. Furthermore, in our polymer example, all

second-order terms involving mixture components, process variables, and the mixture













by process variable interactions are of equal importance. In fact, the specific mixture

component by process variable interaction terms may provide a significant amount of

insight into which operating conditions are optimal. For instance, the engineer truly

needs to know if a specific mixture component makes the reaction especially sensitive

to the reaction temperature.

This type of experimental situation leads us to propose a new model for extracting

information from a mixture experiment with process variables. The time and cost

constraints faced by plant personnel leads us to propose a new class of designs based

upon this model.


4.2 The Combined Mixture Component-Process Variable Model


In mixture experiments involving process variables, the form of the combined

model consisting of terms in the mixture proportions as well as in the process vari-

ables depends on the blending properties of the mixture components, the effects of

the process variables, and any interactions between the mixture components and pro-

cess variables. These models are typically second-order models that allow for pure

quadratic and two-factor interaction terms.

The general second-order polynomial in q mixture components is

q q q
71 = Ao + E Ox + E O.ix + E E Axxj (4)
i= i=1 i
Now using the constraints


xi = 1 and x. = xi 1- xj ,
i=1 j=1













Equation (4) becomes


(. Xi3-i ) + iE i + (Of3iiXi q q
i=1 i=1 i=1 j96i i q q q q
= E(Ao + 0i + 3i) x E ixi ELx + E1E ijxxj
i=1 i=1 j'i i q q
= E- x+ EE o >xx (5)
i=1 i where = /3o + A + Oij and /3 = Aj O3i ij for i, j = 1, 2,..., q, i < j.

Suppose that an experiment is to be performed with q mixture components,

x1, x2, ... Xq, and n process variables, z1, z2, ..., z,. In the process variables, let us

consider the model
n n
71pV = ao + E CkZk + E E CakZkZ (6)
k=l k Then there are two main types of combined models (see Cornell (1990)) that can be

used in this situation. The first type is a model which crosses the mixture model

terms in Equation (5) with each and every term of Equation (6). This produces the

combined model
q q q n q n
q(x, z) = 3,xi +E E3jXiXj + E E^xiZk + EEEYiklXiZkZ,
i=1 i q n q n
+ E E E ^ikXXjZk + E E E E ^>3j3kXiXZkZ (7)
i which includes parameters for three and four factor interactions. Depending on the

design, the model of Equation (7) provides a measure of the linear and nonlinear

blending properties of the mixture components averaged across the settings of the

process variables as well as the effects of the process variables on the linear and

nonlinear blending properties.













The second type of combined model is the additive model which combines the

models in Equations (5) and (6) without crossing any of the xi and zj terms. This

produces the model
q q
m/(x,z) + E
i=1 i n n
+ Eokzk+ EE akizkkZ. (8)
k=1 k Equation(8) provides a measure of the quadratic blending of the mixture components

on the response as well as up to two-factor interactions between the process variables

on the response. Since the model does not contain any crossproduct terms between

the mixture components and the process variables, when fitting Equation (8) the

user assumes the blending of the mixture components is the same at all factor-level

combinations of the process variables. This assumption is probably unrealistic in most

situations. Also, in some experiments like the one described in the previous section,

the mixture component by process variable interactions may be the most important

terms in the model.

A major concern with mixture experiments involving process variables is their

size. Many industrial situations require the use of small experiments due to time

and/or cost constraints. As the number of mixture components and/or process vari-

ables increases, the model in Equation (7) will require a design with a large number

of points. While the fitting of the model in Equation (8) permits the use of a smaller

design than the fitting of the model in Equation (7), it does not, as pointed out

earlier, address the estimation of the mixture components by process variable inter-

actions. If cost constraints limit the size of the experiment yet interactions between













mixture components and process variables are believed to be important, some sort of

compromise between these two models is needed.

Most of the model forms that have been proposed for response surface investi-

gations are based on a Taylor series approximation. In keeping with this tradition,

suppose that the true model for the n process variables is a second-order model.

Instead of Equation (6), such a model would be

71 n n
22
17Pv = ao + E Z kZk + E Z kkzk + E E klZkZ. (9)
k=l k=l k
Equation (9) is Equation (6) plus the n pure quadratic terms. Also, a Taylor series

approximation for a combined second-order model would include only up to two factor

interactions and would not be the model in Equation (7). Combining Equation (5)

with Equation (9), our proposed combined second-order model is

q q n
(xz) = Z)+ E+ 'z
i=l i n q n
+ E E kZkZ E E YikXiZk (10)
k
which includes the mixture model, plus pure quadratic as well as two-factor inter-

action effects among the process variables, and two-factor interactions between the

linear blending terms in the mixture components and the main effect terms in the

process variables. The minimum number of design points needed for the proposed

model (10) is less than what is needed for the completely crossed model (7) but is

more than is needed for the additive model (8). Also, the proposed model can be used

even if one does not feel the need for pure quadratic terms in the process variables

by simply omitting those n terms.












To support the fitting of Equation (10) we shall require a design that will support

nonlinear blending of the mixture components as well as the fitting of the full second

order model in the process variables. In the next section, we discuss a design approach

that will accommodate these terms.


4.3 Design Approach

In mixture experiments as in most response surface investigations, the design and

the form of the model to be fitted go hand in hand. For example, if a second order

model is suspected, it is necessary to select a design that will support the fit of this

model. The design chosen must have at least as many points as there are parameters

in the model. Therefore, a (q + n)(q + n + 1)/2 point design is needed to support the

fitting of the model in Equation (10).

A popular response surface design for fitting a second-order model of the form in

Equation (9) is the central composite design (ccd) which consists of a complete 2' (or

a Resolution V fraction of a 2n) factorial design, 2n axial points with levels a for

one factor and zero for the rest, and at least one center point. If a = 1 is selected,

the design region is a hypercube.

The approach to reducing the number of observations needed in a mixture exper-

iment begins with a ccd in the process variables. A simplex is then placed at each

point in the ccd with only a fraction of the mixture blends at each point. The mixture

blends at each design point are selected from the full simplex-centroid. A general

notion of balance among the mixture components across the process variables is de-

sired. First of all, let us insist on the same number of mixture blends to be present













at both the high and low levels of each process variable. Secondly, let us insist on all

of the mixture blends be present at each 1 factorial level for each process variable.

These ideas seem very intuitive and lead us to select some of the mixture blends to be

used at certain design points and different mixture blends to be used at other design

points.

Two designs are considered for the fitting of the model in Equation (10). With

both designs, the vertices of the simplex are run at one-half of the 2' factorial points

in the process variables with the midedge points of the simplex being run at the other

half. This is done in a such a way, that if the design is collapsed across the levels

of each process variable then one gets a simplex with vertices and midpoints at both

the low and high level of the remaining process variables. Hence, the information in

the mixture blends is spread evenly among the process variables. This is intuitively

appealing since if a process variable is deemed negligible then there is still complete

information on the mixture blends for the other process variables. Ntxt,. the axial

points in the process variables are paired with just the centroid of the simplex. This

allows for the centroid to also be present if the design is collapsed. The two designs

differ only in the number of points placed at the center of the process variables. With

one design the entire simplex-centroid is performed at the center while with the other

only the centroid mixture blend is performed at the center of the process variables.

Consider an example involving three mixture components and two process vari-

ables. The model for this example, using Equation (10), contains 15 terms. The two

designs are shown in Figures 2 and 3. For three mixture components, the design with

the full simplex-centroid at the center of the process variables consists of 23 points













while the second design with just the centroid consists of 17 points. Either could be

used to estimate the 15 terms in the model.

The designs in Figures 2 and 3 can be extended to experiments involving more

than 3 mixture components (MC) and/or more than 2 process variables (PV). The

extension is straightforward. Following the same general notion of balance described

earlier, one can generate the needed designs. In this paper, a total of five cases are

discussed: 3 MC, 2 PV; 3 MC, 3 PV; 4 MC, 2 PV; 4 MC, 3 PV; and 3 MC, 2 PV with

upper and lower bound constraints on the mixture component proportions. For four

mixture components, there are four vertices and six edge midpoints of the tetrahedron.

For three process variables, the layout is a cube with 23 = 8 factorial points, six axial

points, and a center point. Placing upper and lower bound constraints on the mixture

component proportions creates a more complicated mixture region than the simplex.

The constrained region is typically an irregular polygon. The example in this paper

(3 MC, 2 PV) uses the following constraints:

0.25 < x, < 0.40 0.25 < x2 < 0.40 0.25 < x3 < 0.40.

The resulting mixture region is a hexagon. Generally, the original components are
transformed to L-pseudocomponents, x (- )/(- =L) i = 1,2,...,, to

make the construction of the design and the fitting of the model easier. For the exam-

ple in this paper, the mixture components can be transformed to L-pseudocomponents

using
xi 0.25 =x 0.25
1 (0.25 + 0.25 + 0.25) 0.25 1,2,3.

Candidate points for the two designs in this case consist of the six vertices and







x_1 =1


x_2 = 1 xj


Figure 2: Proposed Design for the 3-2 Case With Full Simplex


z-2
A-


/


4 z1


=
]-=1


I ,'


A






x_1 =1

x_2 =1 x _3 = 1


z_2
A-


I z-


Figure 3: Proposed Design for the 3-2 Case With Just the Centroid


4\




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