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THE DESIGN AND ANALYSIS OF SPLITPLOT 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 everytliii 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 SplitPlot Designs ................................................... 3 1.3 Dissertation Goals .................................................. 13 1.4 O verview ........................................................... 16 2 LITERATURE REVIEW ................................................. 17 2.1 SplitPlot Confounding ........................................ .... .. 17 2.2 SplitPlots in Robust Parameter Designs ............................ 19 2.3 BiRandomization Designs .......................................... 27 2.4 SplitPlots in Industrial Experiments ............................... 31 3 INCOMPLETE SPLITPLOT 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 SplitPlot Experim ents ....................................................... 47 3.5 Discussion of MinimumAberration in SplitPlot 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 ComponentProcess 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 SPLITPLOT SETTING .............................................. 119 5.1 FirstOrder Model for the Process Variables ....................... 120 5.2 SecondOrder 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 SPLITPLOT EXPERIMENTS IN INDUSTRY By Scott M. Kowalski December, 1999 Chairman: G. Geoffrey Vining Major Department: Statistics Splitplot experiments where the whole plot treatments and the subplot treatments are made up of combinations of twolevel 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 twentyfour 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 splitplot structure. When the structure is that of a splitplot 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 splitplot 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 SplitPlot Designs A splitplot design often refers to a design with qualitative factors but can easily handle quantitative factors. Also, a splitplot 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 "splitplot" design. Therefore, in this dissertation, we will use the term splitplot 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 subunits. In these situations, the splitplot experiment can be utilized. The experimental unit is referred to as the whole plot while the subunits are referred to as the subplots. For every splitplot 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. Splitplot experiments have been used extensively in agricultural settings. Even so, the following example from Montgomery (1997) shows that there are applications for splitplot 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 splitplot 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 splitplot 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 splitplot 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 splitplot 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 splitplot 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 + (T7)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 ariiilyt. 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 + (7r)'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, (TO3y)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 b1 (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)()(sk1) 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 SplitPlot 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 splitplot 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 splitsplitplot design. For a more detailed discussion of splitplot 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 splitplot 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 splitplot 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 heatandserve pastries, along with shelfstable readytoeat 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 doughbased products move through on a belt. The oven has two zones, which are controlled independently. In each zone you can atjut 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 splitplot 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 hardtochange 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 splitplot 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 splitplot 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 indepth look at confounding in splitplot 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 splitplot structure for the mixture experiments with process variables described in Chapter 4. CHAPTER 2 LITERATURE REVIEW The splitplot 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 SplitPlot 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, splitplot confounding was studied by Addelman (1964). He provided a table containing factorial and fractionalfactorial 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 splitplot confounding with the use of their noncrossed birandomization designs. Box and Jones (1992) illustrate splitplot 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, twolevel splitplot designs at both the whole plots and the subplots. They consider 2(n"l+2)(kl+k2) splitplot designs which are associated with a subset of the 2nk fractional factorial designs where n = n7 + n2 and k = k, + k2. The criterion used to select the optimal design is that of minimumaberration which is the design that has smallest number of words in the defining contrast with the fewest letters. Two methods are presented for constructing minimumaberration splitplot designs. The first method decomposes the 2 "k design into the 2(n+n2)(kl+k2) splitplot 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. Minimumaberration twolevel splitplot designs are also discussed in Binghamn and Sitter (1999). A combined search and sequential algorithm is presented for con structing all nonisomorphic minimumaberration splitplot 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 minimumaberration designs since sometimes it may be desirable to use these designs. 2.2 SplitPlots 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 splitplot 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 2kp x 2q, splitplot designs. In addition to splitplot 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 splitplot confounding are also given. Box and Jones (1992) investigate the use of splitplot designs as an alternative to the crossed array. They consider three experimental arrangements where the robust parameter design is set up as a splitplot 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 stripblock 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 crossproduct array would require 32 cake mix batches and 32 operations of the oven. Thus, the splitplot 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 crossproduct array would use 32 cake mix batches and 32 operations of the oven. Here, the savings of the splitplot 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 stripblock experiment is easier to run than the completely randomized crossproduct design, as well as both arrangements (a) and (b). Table 6: StripBlock 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 stripblock 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 hotwall, reduced pressure reactor. The reactant gases are introduced into one end of a threezone furnace tube and are pumped into the other end. The wafers enter the lowpressure 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 splitsplitplot design because there are three sizes of experimental units with different sources of variation. The design factors are applied to the tube (runtorun variability); the location in the tube affects the wafer (wafertowafer variability), whereas location in the wafer affects the die (dietodie 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 splitsplitplot 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 splitsplitplot 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 splitplot designs compared to the CRD and RCB. A summary of their conclusions is provided here. Consider the splitplot 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 stripblock 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 stripblock design and the splitplot design with the design factors applied to the subplots can be extremely useful in robust parameter design. 2.3 BiRandomization Designs Letsinger, Myers, and Lentner (1996) introduced birandomization designs (BRD's). BRD's refer to designs with two randomizations similar to that of a splitplot design. The whole plot variables are denoted by z = (z1, z2,..., zZ) while the subplot 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 noncrossed. 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 splitplot 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 noncrossed 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 subplots and need not have the same number of levels. Noncrossed 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 subplot factors. The crossed BRD might be represented by a 2k factorial in the subplot factors while the noncrossed BRD might use a 2kp fractionalfactorial in the subplot factors but not the same 2kp set of treatments. For both crossed and noncrossed 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 subplot 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 subplots 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' XV1y (2) with Var() (X'V1X)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 subplot terms as y = Z, + X*f3* + Z'AX*, where A is a matrix of whole plot x subplot 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 subplots. Then approximate ttests can be formed by substituting the estimated error variances into Equation (3). Noncrossed BRD's present a more complicated situation. The equivalency of OLS and GLS is only true in the case of a firstorder model. Although more complex, the above method can be adapted for the firstorder case. Letsinger, Myers, and Lentner (1996) compare three methods for the secondorder case. They are OLS, iterative reweighted least squares (IRLS), and restricted maximum likelihood (REML). Though IRLS and REML appear to be better methods, the "bt." method depends on the design, model, and any prior information. Birandomization 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 Doptimality 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 secondorder designs. For the secondorder de. central composite design (CCD) proves to be a good design. 2.4 SplitPlots in Industrial Experiments Lucas and Ju (1992) investigated the use of splitplot 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 facecentered cube design with four center points. They let x, correspond to the hardtochange 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 hardtochange 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 hardtochange factor, 031 and I11. These results correspond with the general result that splitplot 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 twolevel factorials (see Lucas and Ju (1992)). They considered a 24 factorial with x, as the hardtochange 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 hardtochange 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 easytovary 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 splitplot 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 deepfrying 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 splitplot design. Cornell (1988) considers factorlevel 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 regressiontype 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 workedout numerical examples. Santer and Pan (1997) discuss subset selection procedures for screening in two factor treatment designs. The paper deals mainly with splitplot designs run in com plete blocks; however, the stripplot 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 HardToChange Factor (from Lucas and Ju (1992)) Var(b) = A, + Ba, Hard To Change Variable Other Terms A B A B 1P P I1P i pi P = 1/(2k2 + 1) for the completely randomized design. P = 1 for the completely restricted design. P = (2kl 2)/[2(2kl 1)] for the partially restricted design. procedures depend onl the block variance. Miller (1997) considers various fractionalfactorial structures in stripplot experi ments. These stripplot experiments are identical in nature to the stripblock experi ments, arrangement (c), discussed in Box and Jones (1992). Stripplot 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 firststage 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 stripplot 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 stripplot configurations for fractionalfactorial 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 twolevel designs and then extended to mlevel and mixed level designs. The procedure for twolevel designs is presented here; for details on the extended cases, see Miller (1997). Consider the situation in which a proper fraction of a twolevel factorial design is to be run in a stripplot 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: Stripplot 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 WWasher 3 a2 + 4aR + (8/3) E W? j=1 Row Residual 3 a2 + 4aR 4 Column DDryer 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 2KQ design in b blocks; 2. Select a column design that consists of a 2kq design in b blocks; 3. Consider the product of the designs in steps 1 and 2 and select a LatinSquare 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 LatinSquare fraction is selected so that the confounding array effects in the unit stratum have desirable properties. Mee and Bates (1998) consider splitlot 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 splitlot 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 64wafer experiments (see .r.v and Bates (1998)). Splitlot designs for threelevel 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 SPLITPLOT 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 64fold 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 twofactor 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 2p will be called a 2kp 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 followup 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 231 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 2kP, 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 twofactor interactions; 2. Resolution IV in which main effects are aliased with threefactor interactions and twofactor interactions are aliased with other twofactor intera;i tioii: 3. Resolution V where twofactor interactions are aliased with threefactor in teractions. Of course, if all threefactor and higher interactions are negligible, a design with Resolution V is desired because it will allow the estimation of all main effects and twofactor 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 smallersized 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 higherorder 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 threefactor interactions or higher so that all main effects and twofactor interactions can be estimated. When the block size of 2k is reduced by 2p, each block will contain 2kp 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 2kp 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 2CkP 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 halfreplicate, 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 halffraction, it would appear logical to select a fivefactor 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 threefactor interaction since its alias will also be a threefactor 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 twofactor 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 SplitPlot 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; twofactor interactions between the whole plot and subplot factors; and if possible, twofactor 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 splitplot experi ments. Addelman (1964) also discusses ways of accomplishing this. Recently, the use of splitplot 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 twolevels. 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 twolevels, 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 splitplot exper iment. Consider a splitplot 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 twofactor interactions between the whole plot and subplot factors as is possible, although it is believed that some twofactor 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 splitplot structure by consid ering the factors as a 26 factorial in a completely randomized design. Actually, the experimenter would use a 262 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 twofactor interactions are aliased with each other. Even if we assume that all twofactor interactions among A, B, and C and all twofactor 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 262 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 262 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 231 x 231 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 splitplot nature and using four whole plots, is to consider reducing the whole plot factors and subplot factors separately using fractional factorials. A 231 fractional factorial with defining contrast I = ABC will be used for selecting the whole plot treatments and combined with a 231 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 splitplot 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 twofactor interactions between the whole plot and subplot factors. However, we must assume that the twofactor interactions among the subplot factors are negligible in order to estimate the main effects for the subplot factors. Method three uses splitplot confounding and four whole plots. At the whole plot level, a 231 fractional factorial with defining contrast I = ABC is used. Then, the threefactor interaction, PQR, is confounded with factor C to reduce the eight Table 15: Alias Structure for 231 x 231 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 SplitPlot 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 splitplot 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 splitplot 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 SplitPlot 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 SplitPlot 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 SplitPlot 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 MinimumAberration SplitPlot Designs In splitplot 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 minimumaberration 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 minimumaberration (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 twofactor 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 twofactor 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 hardtochange or costlytochange 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 splitplot experiments they are based purely on the overall resolution of the design instead of partial resolution. Also, they only use splitplot 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 splitplot 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 "mininmumaberration" (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 splitplot 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 factorseach factor has the same number of high and low levels presentwhich 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 twofactor 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 splitplot 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 twofactor interactions between whole plot and subplot factors, the main effects of the subplot factors, and if possible twofactor 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 splitplot 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 twofactor 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 twofactor interactions among the subplot factors are aliased with each other. However, with the 24 point design we can estimate three of the twofactor 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 SplitPlot 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 twofactor 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 [HPdenotes high P and LPdenotes 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 splitplot confounding. The defining contrast is I = ABC = ABPQR = CPQR which is also resolution III. The twofactor 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 twofactor 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 SplitPlot Confounding [HPdenotes 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 LPdenotes 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 twofactor 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 splitplot 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 twofactor 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 twofactor 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 SplitPlot 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 splitplot 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 SplitPlot 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 twofactor 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 splitplot 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 twofactor interactions among the subplot factors are aliased with each other. Also, four of the sixteen twofactor 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 twofactor 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 2139 x 231 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 SplitPlot 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 18term model involving the main effects of the whole plot factors, the main effects of the subplot factors, the twofactor interactions among subplot factors, and twofactor 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 ttests. 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 tvalue 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 Pvalue 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 splitplot 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 hardtochange 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 splitplot 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 SplitPlot Confounding Condition Number, K 4.05 3.36 3 3 Same Fraction 2.00 3 3 SplitPlot Confounding 2.00 3 4 Same Fraction 4.05 3 4 SplitPlot Confounding 3.36 4 Neither 2.00 4 3 Same Fraction 5.83 4 3 SplitPlot Confounding 2.00 4 4 Same Fraction 5.83 4 4 SplitPlot 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 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 singlecomponent 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 componentprocess 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 simplexcentroid by full 23 factorial, to only 16, which relied on running the onequarter 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 Doptimal 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 Doptimality is also given. While the reduction in the number of observations required can be great, obtaining Doptimality comes with a price. The Doptimal 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 mixtureprocess 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 Dcriterion 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 mixtureprocess variable models ordinarily used is presented. The method for constructing the design and comparing it's Dcriterion 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 startup 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 secondorder 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 secondorder model. Furthermore, in our polymer example, all secondorder 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 ComponentProcess 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 secondorder models that allow for pure quadratic and twofactor interaction terms. The general secondorder 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 (. Xi3i ) + iE i + (Of3iiXi q q i=1 i=1 i=1 j96i i = E(Ao + 0i + 3i) x E ixi ELx + E1E ijxxj i=1 i=1 j'i i = E x+ EE o >xx (5) i=1 i 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 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 + E E E ^ikXXjZk + E E E E ^>3j3kXiXZkZ (7) i 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 + Eokzk+ EE akizkkZ. (8) k=1 k on the response as well as up to twofactor 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 factorlevel 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 secondorder 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 secondorder 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 secondorder model is q q n (xz) = Z)+ E+ 'z i=l i + E E kZkZ E E YikXiZk (10) k which includes the mixture model, plus pure quadratic as well as twofactor inter action effects among the process variables, and twofactor 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 secondorder 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 simplexcentroid. 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 onehalf 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 simplexcentroid 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 simplexcentroid 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 Lpseudocomponents, 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 Lpseudocomponents 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 32 Case With Full Simplex z2 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 32 Case With Just the Centroid 4\ 
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