Experiments in Science and Industry
Experimental methods are widely used in research as well as in industrial settings, however, sometimes for very different purposes. The primary goal in scientific research is usually to show the statistical significance of an effect that a particular factor exerts on the dependent variable of interest (for details concerning the concept of statistical significance see Elementary Concepts).
In industrial settings, the primary goal is usually to extract the maximum amount of unbiased information regarding the factors affecting a production process from as few (costly) observations as possible. While in the former application (in science) analysis of variance (ANOVA) techniques are used to uncover the interactive nature of reality, as manifested in higher-order interactions of factors, in industrial settings interaction effects are often regarded as a "nuisance" (they are often of no interest; they only complicate the process of identifying important factors).
Differences in techniques
These differences in purpose have a profound effect on the techniques that are used in the two settings. If you review a standard ANOVA text for the sciences, for example the classic texts by Winer (1962) or Keppel (1982), you will find that they will primarily discuss designs with up to, perhaps, five factors (designs with more than six factors are usually impractical; see the ANOVA/MANOVA chapter). The focus of these discussions is how to derive valid and robust statistical significance tests. However, if you review standard texts on experimentation in industry (Box, Hunter, and Hunter, 1978; Box and Draper, 1987; Mason, Gunst, and Hess, 1989; Taguchi, 1987) you will find that they will primarily discuss designs with many factors (e.g., 16 or 32) in which interaction effects cannot be evaluated, and the primary focus of the discussion is how to derive unbiased main effect (and, perhaps, two-way interaction) estimates with a minimum number of observations.
This comparison can be expanded further, however, a more detailed description of experimental design in industry will now be discussed and other differences will become clear. Note that the General Linear Models and ANOVA/MANOVA chapters contain detailed discussions of typical design issues in scientific research; the General Linear Model procedure is a very comprehensive implementation of the general linear model approach to ANOVA/MANOVA (univariate and multivariate ANOVA). There are of course applications in industry where general ANOVA designs, as used in scientific research, can be immensely useful. You may want to read the General Linear Models and ANOVA/MANOVA chapters to gain a more general appreciation of the range of methods encompassed by the term Experimental Design.
Overview
The general ideas and principles on which experimentation in industry is based, and the types of designs used will be discussed in the following paragraphs. The following paragraphs are meant to be introductory in nature. However, it is assumed that you are familiar with the basic ideas of analysis of variance and the interpretation of main effects and interactions in ANOVA. Otherwise, it is strongly recommend that you read the Introductory Overview section for ANOVA/MANOVA and the General Linear Models chapter.
General Ideas
In general, every machine used in a production process allows its operators to adjust various settings, affecting the resultant quality of the product manufactured by the machine. Experimentation allows the production engineer to adjust the settings of the machine in a systematic manner and to learn which factors have the greatest impact on the resultant quality. Using this information, the settings can be constantly improved until optimum quality is obtained. To illustrate this reasoning, here are a few examples:
Example 1: Dyestuff manufacture. Box and Draper (1987, page 115) report an experiment concerned with the manufacture of certain dyestuff. Quality in this context can be described in terms of a desired (specified) hue and brightness and maximum fabric strength. Moreover, it is important to know what to change in order to produce a different hue and brightness should the consumers' taste change. Put another way, the experimenter would like to identify the factors that affect the brightness, hue, and strength of the final product. In the example described by Box and Draper, there are 6 different factors that are evaluated in a 2**(6-0) design (the 2**(k-p) notation is explained below). The results of the experiment show that the three most important factors determining fabric strength are the Polysulfide index, Time, and Temperature (see Box and Draper, 1987, page 116). One can summarize the expected effect (predicted means) for the variable of interest (i.e., fabric strength in this case) in a so- called cube-plot. This plot shows the expected (predicted) mean fabric strength for the respective low and high settings for each of the three variables (factors).
Example 1.1: Screening designs. In the previous example, 6 different factors were simultaneously evaluated. It is not uncommon, that there are very many (e.g., 100) different factors that may potentially be important. Special designs (e.g., Plackett-Burman designs, see Plackett and Burman, 1946) have been developed to screen such large numbers of factors in an efficient manner, that is, with the least number of observations necessary. For example, you can design and analyze an experiment with 127 factors and only 128 runs (observations); still, you will be able to estimate the main effects for each factor, and thus, you can quickly identify which ones are important and most likely to yield improvements in the process under study.
Example 2: 3**3 design. Montgomery (1976, page 204) describes an experiment conducted in order identify the factors that contribute to the loss of soft drink syrup due to frothing during the filling of five- gallon metal containers. Three factors where considered: (a) the nozzle configuration, (b) the operator of the machine, and (c) the operating pressure. Each factor was set at three different levels, resulting in a complete 3**(3-0) experimental design (the 3**(k-p) notation is explained below).
Moreover, two measurements were taken for each combination of factor settings, that is, the 3**(3-0) design was completely replicated once.
Example 3: Maximizing yield of a chemical reaction. The yield of many chemical reactions is a function of time and temperature. Unfortunately, these two variables often do not affect the resultant yield in a linear fashion. In other words, it is not so that "the longer the time, the greater the yield" and "the higher the temperature, the greater the yield." Rather, both of these variables are usually related in a curvilinear fashion to the resultant yield.
Thus, in this example your goal as experimenter would be to optimize the yield surface that is created by the two variables: time and temperature.
Example 4: Testing the effectiveness of four fuel additives. Latin square designs are useful when the factors of interest are measured at more than two levels, and the nature of the problem suggests some blocking. For example, imagine a study of 4 fuel additives on the reduction in oxides of nitrogen (see Box, Hunter, and Hunter, 1978, page 263). You may have 4 drivers and 4 cars at your disposal. You are not particularly interested in any effects of particular cars or drivers on the resultant oxide reduction; however, you do not want the results for the fuel additives to be biased by the particular driver or car. Latin square designs allow you to estimate the main effects of all factors in the design in an unbiased manner. With regard to the example, the arrangement of treatment levels in a Latin square design assures that the variability among drivers or cars does not affect the estimation of the effect due to different fuel additives.
Example 5: Improving surface uniformity in the manufacture of polysilicon wafers. The manufacture of reliable microprocessors requires very high consistency in the manufacturing process. Note that in this instance, it is equally, if not more important to control the variability of certain product characteristics than it is to control the average for a characteristic. For example, with regard to the average surface thickness of the polysilicon layer, the manufacturing process may be perfectly under control; yet, if the variability of the surface thickness on a wafer fluctuates widely, the resultant microchips will not be reliable. Phadke (1989) describes how different characteristics of the manufacturing process (such as deposition temperature, deposition pressure, nitrogen flow, etc.) affect the variability of the polysilicon surface thickness on wafers. However, no theoretical model exists that would allow the engineer to predict how these factors affect the uniformness of wafers. Therefore, systematic experimentation with the factors is required to optimize the process. This is a typical example where Taguchi robust design methods would be applied.
Example 6: Mixture designs. Cornell (1990, page 9) reports an example of a typical (simple) mixture problem. Specifically, a study was conducted to determine the optimum texture of fish patties as a result of the relative proportions of different types of fish (Mullet, Sheepshead, and Croaker) that made up the patties. Unlike in non-mixture experiments, the total sum of the proportions must be equal to a constant, for example, to 100%. The results of such experiments are usually graphically represented in so-called triangular (or ternary) graphs.
In general, the overall constraint -- that the three components must sum to a constant -- is reflected in the triangular shape of the graph (see above).
Example 6.1: Constrained mixture designs. It is particularly common in mixture designs that the relative amounts of components are further constrained (in addition to the constraint that they must sum to, for example, 100%). For example, suppose we wanted to design the best-tasting fruit punch consisting of a mixture of juices from five fruits. Since the resulting mixture is supposed to be a fruit punch, pure blends consisting of the pure juice of only one fruit are necessarily excluded. Additional constraints may be placed on the "universe" of mixtures due to cost constraints or other considerations, so that one particular fruit cannot, for example, account for more than 30% of the mixtures (otherwise the fruit punch would be too expensive, the shelf-life would be compromised, the punch could not be produced in large enough quantities, etc.). Such so-called constrained experimental regions present numerous problems, which, however, can be addressed.
In general, under those conditions, one seeks to design an experiment that can potentially extract the maximum amount of information about the respective response function (e.g., taste of the fruit punch) in the experimental region of interest.
Computational Problems
There are basically two general issues to which Experimental Design is addressed:
Components of Variance, Denominator Synthesis
There are several statistical methods for analyzing designs with random effects (see Methods for Analysis of Variance). The Variance Components and Mixed Model ANOVA/ANCOVA chapter discusses numerous options for estimating variance components for random effects, and for performing approximate F tests based on synthesized error terms.
Summary
Experimental methods are finding increasing use in manufacturing to optimize the production process. Specifically, the goal of these methods is to identify the optimum settings for the different factors that affect the production process. In the discussion so far, the major classes of designs that are typically used in industrial experimentation have been introduced: 2**(k-p) (two-level, multi-factor) designs, screening designs for large numbers of factors, 3**(k-p) (three-level, multi-factor) designs (mixed designs with 2 and 3 level factors are also supported), central composite (or response surface) designs, Latin square designs, Taguchi robust design analysis, mixture designs, and special procedures for constructing experiments in constrained experimental regions. Interestingly, many of these experimental techniques have "made their way" from the production plant into management, and successful implementations have been reported in profit planning in business, cash-flow optimization in banking, etc. (e.g., see Yokyama and Taguchi, 1975).
These techniques will now be described in greater detail in the following sections:
In many cases, it is sufficient to consider the factors affecting the production process at two levels. For example, the temperature for a chemical process may either be set a little higher or a little lower, the amount of solvent in a dyestuff manufacturing process can either be slightly increased or decreased, etc. The experimenter would like to determine whether any of these changes affect the results of the production process. The most intuitive approach to study those factors would be to vary the factors of interest in a full factorial design, that is, to try all possible combinations of settings. This would work fine, except that the number of necessary runs in the experiment (observations) will increase geometrically. For example, if you want to study 7 factors, the necessary number of runs in the experiment would be 2**7 = 128. To study 10 factors you would need 2**10 = 1,024 runs in the experiment. Because each run may require time-consuming and costly setting and resetting of machinery, it is often not feasible to require that many different production runs for the experiment. In these conditions, fractional factorials are used that "sacrifice" interaction effects so that main effects may still be computed correctly.
Generating the Design
A technical description of how fractional factorial designs are constructed is beyond the scope of this introduction. Detailed accounts of how to design 2**(k-p) experiments can be found, for example, in Bayne and Rubin (1986), Box and Draper (1987), Box, Hunter, and Hunter (1978), Montgomery (1991), Daniel (1976), Deming and Morgan (1993), Mason, Gunst, and Hess (1989), or Ryan (1989), to name only a few of the many text books on this subject. In general, it will successively "use" the highest-order interactions to generate new factors. For example, consider the following design that includes 11 factors but requires only 16 runs (observations).
| Design: 2**(11-7), Resolution III | |||||||||||
|---|---|---|---|---|---|---|---|---|---|---|---|
| Run | A | B | C | D | E | F | G | H | I | J | K |
| 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 |
1 1 1 1 1 1 1 1 -1 -1 -1 -1 -1 -1 -1 -1 |
1 1 1 1 -1 -1 -1 -1 1 1 1 1 -1 -1 -1 -1 |
1 1 -1 -1 1 1 -1 -1 1 1 -1 -1 1 1 -1 -1 |
1 -1 1 -1 1 -1 1 -1 1 -1 1 -1 1 -1 1 -1 |
1 1 -1 -1 -1 -1 1 1 -1 -1 1 1 1 1 -1 -1 |
1 -1 -1 1 -1 1 1 -1 1 -1 -1 1 -1 1 1 -1 |
1 -1 -1 1 1 -1 -1 1 -1 1 1 -1 -1 1 1 -1 |
1 -1 1 -1 -1 1 -1 1 -1 1 -1 1 1 -1 1 -1 |
1 -1 -1 1 -1 1 1 -1 -1 1 1 -1 1 -1 -1 1 |
1 1 1 1 -1 -1 -1 -1 -1 -1 -1 -1 1 1 1 1 |
1 1 -1 -1 1 1 -1 -1 -1 -1 1 1 -1 -1 1 1 |
Reading the design. The design displayed above should be interpreted as follows. Each column contains +1's or -1's to indicate the setting of the respective factor (high or low, respectively). So for example, in the first run of the experiment, set all factors A through K to the plus setting (e.g., a little higher than before); in the second run, set factors A, B, and C to the positive setting, factor D to the negative setting, and so on. Note that there are numerous options provided to display (and save) the design using notation other than ±1 to denote factor settings. For example, you may use actual values of factors (e.g., 90 degrees Celsius and 100 degrees Celsius) or text labels (Low temperature, High temperature).
Randomizing the runs. Because many other things may change from production run to production run, it is always a good practice to randomize the order in which the systematic runs of the designs are performed.
The Concept of Design Resolution
The design above is described as a 2**(11-7) design of resolution III (three). This means that you study overall k = 11 factors (the first number in parentheses); however, p = 7 of those factors (the second number in parentheses) were generated from the interactions of a full 2**[(11-7) = 4] factorial design. As a result, the design does not give full resolution; that is, there are certain interaction effects that are confounded with (identical to) other effects. In general, a design of resolution R is one where no l-way interactions are confounded with any other interaction of order less than R-l. In the current example, R is equal to 3. Here, no l = 1 level interactions (i.e., main effects) are confounded with any other interaction of order less than R-l = 3-1 = 2. Thus, main effects in this design are confounded with two- way interactions; and consequently, all higher-order interactions are equally confounded. If you had included 64 runs, and generated a 2**(11-5) design, the resultant resolution would have been R = IV (four). You would have concluded that no l=1-way interaction (main effect) is confounded with any other interaction of order less than R-l = 4-1 = 3. In this design then, main effects are not confounded with two-way interactions, but only with three-way interactions. What about the two-way interactions? No l=2-way interaction is confounded with any other interaction of order less than R-l = 4-2 = 2. Thus, the two-way interactions in that design are confounded with each other.
Plackett-Burman (Hadamard Matrix) Designs for Screening
When one needs to screen a large number of factors to identify those that may be important (i.e., those that are related to the dependent variable of interest), one would like to employ a design that allows one to test the largest number of factor main effects with the least number of observations, that is to construct a resolution III design with as few runs as possible. One way to design such experiments is to confound all interactions with "new" main effects. Such designs are also sometimes called saturated designs, because all information in those designs is used to estimate the parameters, leaving no degrees of freedom to estimate the error term for the ANOVA. Because the added factors are created by equating (aliasing, see below), the "new" factors with the interactions of a full factorial design, these designs always will have 2**k runs (e.g., 4, 8, 16, 32, and so on). Plackett and Burman (1946) showed how full factorial design can be fractionalized in a different manner, to yield saturated designs where the number of runs is a multiple of 4, rather than a power of 2. These designs are also sometimes called Hadamard matrix designs. Of course, you do not have to use all available factors in those designs, and, in fact, sometimes you want to generate a saturated design for one more factor than you are expecting to test. This will allow you to estimate the random error variability, and test for the statistical significance of the parameter estimates.
Enhancing Design Resolution via Foldover
One way in which a resolution III design can be enhanced and turned into a resolution IV design is via foldover (e.g., see Box and Draper, 1987, Deming and Morgan, 1993): Suppose you have a 7-factor design in 8 runs:
| Design: 2**(7-4) design | |||||||
|---|---|---|---|---|---|---|---|
| Run | A | B | C | D | E | F | G |
| 1 2 3 4 5 6 7 8 |
1 1 1 1 -1 -1 -1 -1 |
1 1 -1 -1 1 1 -1 -1 |
1 -1 1 -1 1 -1 1 -1 |
1 1 -1 -1 -1 -1 1 1 |
1 -1 1 -1 -1 1 -1 1 |
1 -1 -1 1 1 -1 -1 1 |
1 -1 -1 1 -1 1 1 -1 |
This is a resolution III design, that is, the two-way interactions will be confounded with the main effects. You can turn this design into a resolution IV design via the Foldover (enhance resolution) option. The foldover method copies the entire design and appends it to the end, reversing all signs:
| Design: 2**(7-4) design (+Foldover) | ||||||||
|---|---|---|---|---|---|---|---|---|
| Run |
A |
B |
C |
D |
E |
F |
G |
New: H |
| 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 |
1 1 1 1 -1 -1 -1 -1 -1 -1 -1 -1 1 1 1 1 |
1 1 -1 -1 1 1 -1 -1 -1 -1 1 1 -1 -1 1 1 |
1 -1 1 -1 1 -1 1 -1 -1 1 -1 1 -1 1 -1 1 |
1 1 -1 -1 -1 -1 1 1 -1 -1 1 1 1 1 -1 -1 |
1 -1 1 -1 -1 1 -1 1 -1 1 -1 1 1 -1 1 -1 |
1 -1 -1 1 1 -1 -1 1 -1 1 1 -1 -1 1 1 -1 |
1 -1 -1 1 -1 1 1 -1 -1 1 1 -1 1 -1 -1 1 |
1 1 1 1 1 1 1 1 -1 -1 -1 -1 -1 -1 -1 -1 |
Thus, the standard run number 1 was -1, -1, -1, 1, 1, 1, -1; the new run number 9 (the first run of the "folded-over" portion) has all signs reversed: 1, 1, 1, -1, -1, -1, 1. In addition to enhancing the resolution of the design, we also have gained an 8'th factor (factor H), which contains all +1's for the first eight runs, and -1's for the folded-over portion of the new design. Note that the resultant design is actually a 2**(8-4) design of resolution IV (see also Box and Draper, 1987, page 160).
Aliases of Interactions: Design Generators
To return to the example of the resolution R = III design, now that you know that main effects are confounded with two-way interactions, you may ask the question, "Which interaction is confounded with which main effect?"
| Factor |
Fractional Design Generators 2**(11-7) design (Factors are denoted by numbers) Alias |
|---|---|
| 5 6 7 8 9 10 11 |
123 234 134 124 1234 12 13 |
Design generators. The design generators shown above are the "key" to how factors 5 through 11 were generated by assigning them to particular interactions of the first 4 factors of the full factorial 2**4 design. Specifically, factor 5 is identical to the 123 (factor 1 by factor 2 by factor 3) interaction. Factor 6 is identical to the 234 interaction, and so on. Remember that the design is of resolution III (three), and you expect some main effects to be confounded with some two-way interactions; indeed, factor 10 (ten) is identical to the 12 (factor 1 by factor 2) interaction, and factor 11 (eleven) is identical to the 13 (factor 1 by factor 3) interaction. Another way in which these equivalencies are often expressed is by saying that the main effect for factor 10 (ten) is an alias for the interaction of 1 by 2. (The term alias was first used by Finney, 1945).
To summarize, whenever you want to include fewer observations (runs) in your experiment than would be required by the full factorial 2**k design, you "sacrifice" interaction effects and assign them to the levels of factors. The resulting design is no longer a full factorial but a fractional factorial.
The fundamental identity. Another way to summarize the design generators is in a simple equation. Namely, if, for example, factor 5 in a fractional factorial design is identical to the 123 (factor 1 by factor 2 by factor 3) interaction, then it follows that multiplying the coded values for the 123 interaction by the coded values for factor 5 will always result in +1 (if all factor levels are coded ±1); or:
I = 1235
where I stands for +1 (using the standard notation as, for example, found in Box and Draper, 1987). Thus, we also know that factor 1 is confounded with the 235 interaction, factor 2 with the 135, interaction, and factor 3 with the 125 interaction, because, in each instance their product must be equal to 1. The confounding of two-way interactions is also defined by this equation, because the 12 interaction multiplied by the 35 interaction must yield 1, and hence, they are identical or confounded. Therefore, one can summarize all confounding in a design with such a fundamental identity equation.
Blocking
In some production processes, units are produced in natural "chunks" or blocks. You want to make sure that these blocks do not bias your estimates of main effects. For example, you may have a kiln to produce special ceramics, but the size of the kiln is limited so that you cannot produce all runs of your experiment at once. In that case you need to break up the experiment into blocks. However, you do not want to run positive settings of all factors in one block, and all negative settings in the other. Otherwise, any incidental differences between blocks would systematically affect all estimates of the main effects of the factors of interest. Rather, you want to distribute the runs over the blocks so that any differences between blocks (i.e., the blocking factor) do not bias your results for the factor effects of interest. This is accomplished by treating the blocking factor as another factor in the design. Consequently, you "lose" another interaction effect to the blocking factor, and the resultant design will be of lower resolution. However, these designs often have the advantage of being statistically more powerful, because they allow you to estimate and control the variability in the production process that is due to differences between blocks.
Replicating the Design
It is sometimes desirable to replicate the design, that is, to run each combination of factor levels in the design more than once. This will allow you to later estimate the so-called pure error in the experiment. The analysis of experiments is further discussed below; however, it should be clear that, when replicating the design, one can compute the variability of measurements within each unique combination of factor levels. This variability will give an indication of the random error in the measurements (e.g., due to uncontrolled factors, unreliability of the measurement instrument, etc.), because the replicated observations are taken under identical conditions (settings of factor levels). Such an estimate of the pure error can be used to evaluate the size and statistical significance of the variability that can be attributed to the manipulated factors.
Partial replications. When it is not possible or feasible to replicate each unique combination of factor levels (i.e., the full design), one can still gain an estimate of pure error by replicating only some of the runs in the experiment. However, one must be careful to consider the possible bias that may be introduced by selectively replicating only some runs. If one only replicates those runs that are most easily repeated (e.g., gathers information at the points where it is "cheapest"), one may inadvertently only choose those combinations of factor levels that happen to produce very little (or very much) random variability -- causing one to underestimate (or overestimate) the true amount of pure error. Thus, one should carefully consider, typically based on your knowledge about the process that is being studied, which runs should be replicated, that is, which runs will yield a good (unbiased) estimate of pure error.
Adding Center Points
Designs with factors that are set at two levels implicitly assume that the effect of the factors on the dependent variable of interest (e.g., fabric Strength) is linear. It is impossible to test whether or not there is a non-linear (e.g., quadratic) component in the relationship between a factor A and a dependent variable, if A is only evaluated at two points (.i.e., at the low and high settings). If one suspects that the relationship between the factors in the design and the dependent variable is rather curve-linear, then one should include one or more runs where all (continuous) factors are set at their midpoint. Such runs are called center-point runs (or center points), since they are, in a sense, in the center of the design (see graph).
Later in the analysis (see below), one can compare the measurements for the dependent variable at the center point with the average for the rest of the design. This provides a check for curvature (see Box and Draper, 1987): If the mean for the dependent variable at the center of the design is significantly different from the overall mean at all other points of the design, then one has good reason to believe that the simple assumption that the factors are linearly related to the dependent variable, does not hold.
Analyzing the Results of a 2**(k-p) Experiment
Analysis of variance. Next, one needs to determine exactly which of the factors significantly affected the dependent variable of interest. For example, in the study reported by Box and Draper (1987, page 115), it is desired to learn which of the factors involved in the manufacture of dyestuffs affected the strength of the fabric. In this example, factors 1 (Polysulfide), 4 (Time), and 6 (Temperature) significantly affected the strength of the fabric. Note that to simplify matters, only main effects are shown below.
| ANOVA; Var.:STRENGTH; R-sqr = .60614; Adj:.56469 (fabrico.sta) | |||||
|---|---|---|---|---|---|
| 2**(6-0) design; MS Residual = 3.62509 DV: STRENGTH |
|||||
| SS | df | MS | F | p | |
| (1)POLYSUFD (2)REFLUX (3)MOLES (4)TIME (5)SOLVENT (6)TEMPERTR Error Total SS |
48.8252 7.9102 .1702 142.5039 2.7639 115.8314 206.6302 524.6348 |
1 1 1 1 1 1 57 63 |
48.8252 7.9102 .1702 142.5039 2.7639 115.8314 3.6251 |
13.46867 2.18206 .04694 39.31044 .76244 31.95269 |
.000536 .145132 .829252 .000000 .386230 .000001 |
Pure error and lack of fit. If the experimental design is at least partially replicated, then one can estimate the error variability for the experiment from the variability of the replicated runs. Since those measurements were taken under identical conditions, that is, at identical settings of the factor levels, the estimate of the error variability from those runs is independent of whether or not the "true" model is linear or non-linear in nature, or includes higher-order interactions. The error variability so estimated represents pure error, that is, it is entirely due to unreliabilities in the measurement of the dependent variable. If available, one can use the estimate of pure error to test the significance of the residual variance, that is, all remaining variability that cannot be accounted for by the factors and their interactions that are currently in the model. If, in fact, the residual variability is significantly larger than the pure error variability, then one can conclude that there is still some statistically significant variability left that is attributable to differences between the groups, and hence, that there is an overall lack of fit of the current model.
| ANOVA; Var.:STRENGTH; R-sqr = .58547; Adj:.56475 (fabrico.sta) | |||||
|---|---|---|---|---|---|
| 2**(3-0) design; MS Pure Error = 3.594844 DV: STRENGTH |
|||||
| SS | df | MS | F | p | |
| (1)POLYSUFD (2)TIME (3)TEMPERTR Lack of Fit Pure Error Total SS |
48.8252 142.5039 115.8314 16.1631 201.3113 524.6348 |
1 1 1 4 56 63 |
48.8252 142.5039 115.8314 4.0408 3.5948 |
13.58200 39.64120 32.22154 1.12405 |
.000517 .000000 .000001 .354464 |
For example, the table above shows the results for the three factors that were previously identified as most important in their effect on fabric strength; all other factors where ignored in the analysis. As you can see in the row with the label Lack of Fit, when the residual variability for this model (i.e., after removing the three main effects) is compared against the pure error estimated from the within-group variability, the resulting F test is not statistically significant. Therefore, this result additionally supports the conclusion that, indeed, factors Polysulfide, Time, and Temperature significantly affected resultant fabric strength in an additive manner (i.e., there are no interactions). Or, put another way, all differences between the means obtained in the different experimental conditions can be sufficiently explained by the simple additive model for those three variables.
Parameter or effect estimates. Now, look at how these factors affected the strength of the fabrics.
| Effect | Std.Err. | t (57) | p | |
|---|---|---|---|---|
| Mean/Interc. (1)POLYSUFD (2)REFLUX (3)MOLES (4)TIME (5)SOLVENT (6)TEMPERTR |
11.12344 1.74688 .70313 .10313 2.98438 -.41562 2.69062 |
.237996 .475992 .475992 .475992 .475992 .475992 .475992 |
46.73794 3.66997 1.47718 .21665 6.26980 -.87318 5.65267 |
.000000 .000536 .145132 .829252 .000000 .386230 .000001 |
The numbers above are the effect or parameter estimates. With the exception of the overall Mean/Intercept, these estimates are the deviations of the mean of the negative settings from the mean of the positive settings for the respective factor. For example, if you change the setting of factor Time from low to high, then you can expect an improvement in Strength by 2.98; if you set the value for factor Polysulfd to its high setting, you can expect a further improvement by 1.75, and so on.
As you can see, the same three factors that were statistically significant show the largest parameter estimates; thus the settings of these three factors were most important for the resultant strength of the fabric.
For analyses including interactions, the interpretation of the effect parameters is a bit more complicated. Specifically, the two-way interaction parameters are defined as half the difference between the main effects of one factor at the two levels of a second factor (see Mason, Gunst, and Hess, 1989, page 127); likewise, the three-way interaction parameters are defined as half the difference between the two-factor interaction effects at the two levels of a third factor, and so on.
Regression coefficients. One can also look at the parameters in the multiple regression model (see Multiple Regression). To continue this example, consider the following prediction equation:
Strength = const + b1 *x1 +... + b6 *x6
Here x1 through x6 stand for the 6 factors in the analysis. The Effect Estimates shown earlier also contains these parameter estimates:
| Coeff. |
Std.Err. Coeff. |
-95.% Cnf.Limt |
+95.% Cnf.Limt |
|
|---|---|---|---|---|
| Mean/Interc. (1)POLYSUFD (2)REFLUX (3)MOLES (4)TIME (5)SOLVENT (6)TEMPERTR |
11.12344 .87344 .35156 .05156 1.49219 -.20781 1.34531 |
.237996 .237996 .237996 .237996 .237996 .237996 .237996 |
10.64686 .39686 -.12502 -.42502 1.01561 -.68439 .86873 |
11.60002 1.35002 .82814 .52814 1.96877 .26877 1.82189 |
Actually, these parameters contain little "new" information, as they simply are one-half of the parameter values (except for the Mean/Intercept) shown earlier. This makes sense since now, the coefficient can be interpreted as the deviation of the high-setting for the respective factors from the center. However, note that this is only the case if the factor values (i.e., their levels) are coded as -1 and +1, respectively. Otherwise, the scaling of the factor values will affect the magnitude of the parameter estimates. In the example data reported by Box and Draper (1987, page 115), the settings or values for the different factors were recorded on very different scales:
| data file: FABRICO.STA [ 64 cases with 9 variables ] 2**(6-0) Design, Box & Draper, p. 117 |
|||||||||
|---|---|---|---|---|---|---|---|---|---|
| POLYSUFD | REFLUX | MOLES | TIME | SOLVENT | TEMPERTR | STRENGTH | HUE | BRIGTHNS | |
| 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 . . . |
6 7 6 7 6 7 6 7 6 7 6 7 6 7 6 . . . |
150 150 170 170 150 150 170 170 150 150 170 170 150 150 170 . . . |
1.8 1.8 1.8 1.8 2.4 2.4 2.4 2.4 1.8 1.8 1.8 1.8 2.4 2.4 2.4 . . . |
24 24 24 24 24 24 24 24 36 36 36 36 36 36 36 . . . |
30 30 30 30 30 30 30 30 30 30 30 30 30 30 30 . . . |
120 120 120 120 120 120 120 120 120 120 120 120 120 120 120 . . . |
3.4 9.7 7.4 10.6 6.5 7.9 10.3 9.5 14.3 10.5 7.8 17.2 9.4 12.1 9.5 . . . |
15.0 5.0 23.0 8.0 20.0 9.0 13.0 5.0 23.0 1.0 11.0 5.0 15.0 8.0 15.0 . . . |
36.0 35.0 37.0 34.0 30.0 32.0 28.0 38.0 40.0 32.0 32.0 28.0 34.0 26.0 30.0 . . . |
Shown below are the regression coefficient estimates based on the uncoded original factor values:
| Regressn Coeff. |
Std.Err. |
t (57) |
p |
|
|---|---|---|---|---|
| Mean/Interc. (1)POLYSUFD (2)REFLUX (3)MOLES (4)TIME (5)SOLVENT (6)TEMPERTR |
-46.0641 1.7469 .0352 .1719 .2487 -.0346 .2691 |
8.109341 .475992 .023800 .793320 .039666 .039666 .047599 |
-5.68037 3.66997 1.47718 .21665 6.26980 -.87318 5.65267 |
.000000 .000536 .145132 .829252 .000000 .386230 .000001 |
Because the metric for the different factors is no longer compatible, the magnitudes of the regression coefficients are not compatible either. This is why it is usually more informative to look at the ANOVA parameter estimates (for the coded values of the factor levels), as shown before. However, the regression coefficients can be useful when one wants to make predictions for the dependent variable, based on the original metric of the factors.
Graph Options
Diagnostic plots of residuals. To start with, before accepting a particular "model" that includes a particular number of effects (e.g., main effects for Polysulfide, Time, and Temperature in the current example), one should always examine the distribution of the residual values. These are computed as the difference between the predicted values (as predicted by the current model) and the observed values. You can compute the histogram for these residual values, as well as probability plots (as shown below).
The parameter estimates and ANOVA table are based on the assumption that the residuals are normally distributed (see also Elementary Concepts). The histogram provides one way to check (visually) whether this assumption holds. The so-called normal probability plot is another common tool to assess how closely a set of observed values (residuals in this case) follows a theoretical distribution. In this plot the actual residual values are plotted along the horizontal X-axis; the vertical Y-axis shows the expected normal values for the respective values, after they were rank-ordered. If all values fall onto a straight line, then one can be satisfied that the residuals follow the normal distribution.
Pareto chart of effects. The Pareto chart of effects is often an effective tool for communicating the results of an experiment, in particular to laymen.
In this graph, the ANOVA effect estimates are sorted from the largest absolute value to the smallest absolute value. The magnitude of each effect is represented by a column, and often, a line going across the columns indicates how large an effect has to be (i.e., how long a column must be) to be statistically significant.
Normal probability plot of effects. Another useful, albeit more technical summary graph, is the normal probability plot of the estimates. As in the normal probability plot of the residuals, first the effect estimates are rank ordered, and then a normal z score is computed based on the assumption that the estimates are normally distributed. This z score is plotted on the Y-axis; the observed estimates are plotted on the X-axis (as shown below).
Square and cube plots. These plots are often used to summarize predicted values for the dependent variable, given the respective high and low setting of the factors. The square plot (see below) will show the predicted values (and, optionally, their confidence intervals) for two factors at a time. The cube plot will show the predicted values (and, optionally, confidence intervals) for three factors at a time.
Interaction plots. A general graph for showing the means is the standard interaction plot, where the means are indicated by points connected by lines. This plot (see below) is particularly useful when there are significant interaction effects in the model.
Surface and contour plots. When the factors in the design are continuous in nature, it is often also useful to look at surface and contour plots of the dependent variable as a function of the factors.
These types of plots will further be discussed later in this section, in the context of 3**(k-p), and central composite and response surface designs.
Summary
2**(k-p) designs are the "workhorse" of industrial experiments. The impact of a large number of factors on the production process can simultaneously be assessed with relative efficiency (i.e., with few experimental runs). The logic of these types of experiments is straightforward (each factor has only two settings).
Disadvantages. The simplicity of these designs is also their major flaw. As mentioned before, underlying the use of two-level factors is the belief that the resultant changes in the dependent variable (e.g., fabric strength) are basically linear in nature. This is often not the case, and many variables are related to quality characteristics in a non-linear fashion. In the example above, if you were to continuously increase the temperature factor (which was significantly related to fabric strength), you would of course eventually hit a "peak," and from there on the fabric strength would decrease as the temperature increases. While this types of curvature in the relationship between the factors in the design and the dependent variable can be detected if the design included center point runs, one cannot fit explicit nonlinear (e.g., quadratic) models with 2**(k-p) designs (however, central composite designs will do exactly that).
Another problem of fractional designs is the implicit assumption that higher-order interactions do not matter; but sometimes they do, for example, when some other factors are set to a particular level, temperature may be negatively related to fabric strength. Again, in fractional factorial designs, higher-order interactions (greater than two-way) particularly will escape detection.
| To index |
2**(k-p) fractional factorial designs are often used in industrial experimentation because of the economy of data collection that they provide. For example, suppose an engineer needed to investigate the effects of varying 11 factors, each with 2 levels, on a manufacturing process. Let us call the number of factors k, which would be 11 for this example. An experiment using a full factorial design, where the effects of every combination of levels of each factor are studied, would require 2**(k) experimental runs, or 2048 runs for this example. To minimize the data collection effort, the engineer might decide to forego investigation of higher-order interaction effects of the 11 factors, and focus instead on identifying the main effects of the 11 factors and any low-order interaction effects that could be estimated from an experiment using a smaller, more reasonable number of experimental runs. There is another, more theoretical reason for not conducting huge, full factorial 2 level experiments. In general, it is not logical to be concerned with identifying higher-order interaction effects of the experimental factors, while ignoring lower-order nonlinear effects, such as quadratic or cubic effects, which cannot be estimated if only 2 levels of each factor are employed. So althrough practical considerations often lead to the need to design experiments with a reasonably small number of experimental runs, there is a logical justification for such experiments.
The alternative to the 2**(k) full factorial design is the 2**(k-p) fractional factorial design, which requires only a "fraction" of the data collection effort required for full factorial designs. For our example with k=11 factors, if only 64 experimental runs can be conducted, a 2**(11-5) fractional factorial experiment would be designed with 2**6 = 64 experimental runs. In essence, a k-p = 6 way full factorial experiment is designed, with the levels of the p factors being "generated" by the levels of selected higher order interactions of the other 6 factors. Fractional factorials "sacrifice" higher order interaction effects so that lower order effects may still be computed correctly. However, different criteria can be used in choosing the higher order interactions to be used as generators, with different criteria sometimes leading to different "best" designs.
2**(k-p) fractional factorial designs can also include blocking factors. In some production processes, units are produced in natural "chunks" or blocks. To make sure that these blocks do not bias your estimates of the effects for the k factors, blocking factors can be added as additional factors in the design. Consequently, you may "sacrifice" additional interaction effects to generate the blocking factors, but these designs often have the advantage of being statistically more powerful, because they allow you to estimate and control the variability in the production process that is due to differences between blocks.
Design Criteria
Many of the concepts discussed in this overview are also addressed in the Overview of 2**(k-p) Fractional factorial designs. However, a technical description of how fractional factorial designs are constructed is beyond the scope of either introductory overview. Detailed accounts of how to design 2**(k-p) experiments can be found, for example, in Bayne and Rubin (1986), Box and Draper (1987), Box, Hunter, and Hunter (1978), Montgomery (1991), Daniel (1976), Deming and Morgan (1993), Mason, Gunst, and Hess (1989), or Ryan (1989), to name only a few of the many text books on this subject.
In general, the 2**(k-p) maximally unconfounded and minimum aberration designs techniques will successively select which higher-order interactions to use as generators for the p factors. For example, consider the following design that includes 11 factors but requires only 16 runs (observations).
| Design: 2**(11-7), Resolution III | |||||||||||
|---|---|---|---|---|---|---|---|---|---|---|---|
| Run | A | B | C | D | E | F | G | H | I | J | K |
| 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 |
1 1 1 1 1 1 1 1 -1 -1 -1 -1 -1 -1 -1 -1 |
1 1 1 1 -1 -1 -1 -1 1 1 1 1 -1 -1 -1 -1 |
1 1 -1 -1 1 1 -1 -1 1 1 -1 -1 1 1 -1 -1 |
1 -1 1 -1 1 -1 1 -1 1 -1 1 -1 1 -1 1 -1 |
1 1 -1 -1 -1 -1 1 1 -1 -1 1 1 1 1 -1 -1 |
1 -1 -1 1 -1 1 1 -1 1 -1 -1 1 -1 1 1 -1 |
1 -1 -1 1 1 -1 -1 1 -1 1 1 -1 -1 1 1 -1 |
1 -1 1 -1 -1 1 -1 1 -1 1 -1 1 1 -1 1 -1 |
1 -1 -1 1 -1 1 1 -1 -1 1 1 -1 1 -1 -1 1 |
1 1 1 1 -1 -1 -1 -1 -1 -1 -1 -1 1 1 1 1 |
1 1 -1 -1 1 1 -1 -1 -1 -1 1 1 -1 -1 1 1 |
Interpreting the design. The design displayed in the Scrollsheet above should be interpreted as follows. Each column contains +1's or -1's to indicate the setting of the respective factor (high or low, respectively). So for example, in the first run of the experiment, all factors A through K are set to the higher level, and in the second run, factors A, B, and C are set to the higher level, but factor D is set to the lower level, and so on. Notice that the settings for each experimental run for factor E can be produced by multiplying the respective settings for factors A, B, and C. The A x B x C interaction effect therefore cannot be estimated independently of the factor E effect in this design because these two effects are confounded. Likewise, the settings for factor F can be produced by multiplying the respective settings for factors B, C, and D. We say that ABC and BCD are the generators for factors E and F, respectively.
The maximum resolution design criterion. In the Scrollsheet shown above, the design is described as a 2**(11-7) design of resolution III (three). This means that you study overall k = 11 factors, but p = 7 of those factors were generated from the interactions of a full 2**[(11-7) = 4] factorial design. As a result, the design does not give full resolution; that is, there are certain interaction effects that are confounded with (identical to) other effects. In general, a design of resolution R is one where no l-way interactions are confounded with any other interaction of order less than R - l. In the current example, R is equal to 3. Here, no l = 1-way interactions (i.e., main effects) are confounded with any other interaction of order less than R - l = 3 -1 = 2. Thus, main effects in this design are unconfounded with each other, but are confounded with two-factor interactions; and consequently, with other higher-order interactions. One obvious, but nevertheless very important overall design criterion is that the higher-order interactions to be used as generators should be chosen such that the resolution of the design is as high as possible.
The maximum unconfounding design criterion. Maximizing the resolution of a design, however, does not by itself ensure that the selected generators produce the "best" design. Consider, for example, two different resolution IV designs. In both designs, main effects would be unconfounded with each other and 2-factor interactions would be unconfounded with main effects, i.e, no l = 2-way interactions are confounded with any other interaction of order less than R - l = 4 - 2 = 2. The two designs might be different, however, with regard to the degree of confounding for the 2-factor interactions. For resolution IV designs, the "crucial order," in which confounding of effects first appears, is for 2-factor interactions. In one design, none of the "crucial order," 2-factor interactions might be unconfounded with all other 2-factor interactions, while in the other design, virtually all of the 2-factor interactions might be unconfounded with all of the other 2-factor interactions. The second "almost resolution V" design would be preferable to the first "just barely resolution IV" design. This suggests that even though the maximum resolution design criterion should be the primary criterion, a subsidiary criterion might be that generators should be chosen such that the maximum number of interactions of less than or equal to the crucial order, given the resolution, are unconfounded with all other interactions of the crucial order. This is called the maximum unconfounding design criterion, and is one of the optional, subsidiary design criterion to use in a search for a 2**(k-p) design.
The minimum aberration design criterion. The miniminum aberration design criterion is another optional, subsidiary criterion to use in a search for a 2**(k-p) design. In some respects, this criterion is similar to the maximum unconfounding design criterion. Technically, the minimum aberration design is defined as the design of maximum resolution "which minimizes the number of words in the defining relation that are of minimum length" (Fries & Hunter, 1980). Less technically, the criterion apparently operates by choosing generators that produce the smallest number of pairs of confounded interactions of the crucial order. For example, the minimum aberration resolution IV design would have the minimum number of pairs of confounded 2-factor interactions.
To illustrate the difference between the maximum unconfounding and minimum aberration criteria, consider the maximally unconfounded 2**(9-4) design and the minimum aberration 2**(9-4) design, as for example, listed in Box, Hunter, and Hunter (1978). If you compare these two designs, you will find that in the maximally unconfounded design, 15 of the 36 2-factor interactions are unconfounded with any other 2-factor interactions, while in the minimum aberration design, only 8 of the 36 2-factor interactions are unconfounded with any other 2-factor interactions. The minimum aberration design, however, produces 18 pairs of confounded interactions, while the maximally unconfounded design produces 21 pairs of confounded interactions. So, the two criteria lead to the selection of generators producing different "best" designs.
Fortunately, the choice of whether to use the maximum unconfounding criterion or the minimum aberration criterion makes no difference in the design which is selected (except for, perhaps, relabeling of the factors) when there are 11 or fewer factors, with the single exception of the 2**(9-4) design described above (see Chen, Sun, & Wu, 1993). For designs with more than 11 factors, the two criteria can lead to the selection of very different designs, and for lack of better advice, we suggest using both criteria, comparing the designs that are produced, and choosing the design that best suits your needs. We will add, editorially, that maximizing the number of totally unconfounded effects often makes more sense than minimizing the number of pairs of confounded effects.
Summary
2**(k-p) fractional factorial designs are probably the most frequently used type of design in industrial experimentation. Things to consider in designing any 2**(k-p) fractional factorial experiment include the number of factors to be investigated, the number of experimental runs, and whether there will be blocks of experimental runs. Beyond these basic considerations, one should also take into account whether the number of runs will allow a design of the required resolution and degree of confounding for the crucial order of interactions, given the resolution.
| To index |
In some cases, factors that have more than 2 levels have to be examined. For example, if one suspects that the effect of the factors on the dependent variable of interest is not simply linear, then, as discussed earlier (see 2**(k-p) designs), one needs at least 3 levels in order to test for the linear and quadratic effects (and interactions) for those factors. Also, sometimes some factors may be categorical in nature, with more than 2 categories. For example, you may have three different machines that produce a particular part.
Designing 3**(k-p) Experiments
The general mechanism of generating fractional factorial designs at 3 levels (3**(k-p) designs) is very similar to that described in the context of 2**(k-p) designs. Specifically, one starts with a full factorial design, and then uses the interactions of the full design to construct "new" factors (or blocks) by making their factor levels identical to those for the respective interaction terms (i.e., by making the new factors aliases of the respective interactions).
For example, consider the following simple 3**(3-1) factorial design:
| 3**(3-1) fractional factorial design, 1 block , 9 runs |
|||
|---|---|---|---|
| Standard Run |
A |
B |
C |
| 1 2 3 4 5 6 7 8 9 |
0 0 0 1 1 1 2 2 2 |
0 1 2 0 1 2 0 1 2 |
0 2 1 2 1 0 1 0 2 |
As in the case of 2**(k-p) designs, the design is constructed by starting with the full 3-1=2 factorial design; those factors are listed in the first two columns (factors A and B). Factor C is constructed from the interaction AB of the first two factors. Specifically, the values for factor C are computed as
C = 3 - mod3 (A+B)
Here, mod3(x) stands for the so-called modulo-3 operator, which will first find a number y that is less than or equal to x, and that is evenly divisible by 3, and then compute the difference (remainder) between number y and x. For example, mod3(0) is equal to 0, mod3(1) is equal to 1, mod3(3) is equal to 0, mod3(5) is equal to 2 (3 is the largest number that is less than or equal to 5, and that is evenly divisible by 3; finally, 5-3=2), and so on.
Fundamental identity. If you apply this function to the sum of columns A and B shown above, you will obtain the third column C. Similar to the case of 2**(k-p) designs (see 2**(k-p) designs for a discussion of the fundamental identity in the context of 2**(k-p) designs), this confounding of interactions with "new" main effects can be summarized in an expression:
0 = mod3 (A+B+C)
If you look back at the 3**(3-1) design shown earlier, you will see that, indeed, if you add the numbers in the three columns they will all sum to either 0, 3, or 6, that is, values that are evenly divisible by 3 (and hence: mod3(A+B+C)=0). Thus, one could write as a shortcut notation ABC=0, in order to summarize the confounding of factors in the fractional 3**(k-p) design.
Some of the designs will have fundamental identities that contain the number 2 as a multiplier; e.g.,
0 = mod3 (B+C*2+D+E*2+F)
This notation can be interpreted exactly as before, that is, the modulo3 of the sum B+2*C+D+2*E+F must be equal to 0. The next example shows such an identity.
An Example 3**(4-1) Design in 9 Blocks
Here is the summary for a 4-factor 3-level fractional factorial design in 9 blocks, that requires only 27 runs.
SUMMARY: 3**(4-1) fractional factorial
Design generators: ABCD
Block generators: AB,AC2
Number of factors (independent variables): 4
Number of runs (cases, experiments): 27
Number of blocks: 9
This design will allow you to test for linear and quadratic main effects for 4 factors in 27 observations, which can be gathered in 9 blocks of 3 observations each. The fundamental identity or design generator for the design is ABCD, thus the modulo3 of the sum of the factor levels across the four factors is equal to 0. The fundamental identity also allows you to determine the confounding of factors and interactions in the design (see McLean and Anderson, 1984, for details).
| Unconfounded Effects (experi3.sta) | ||
|---|---|---|
| EXPERIM. DESIGN |
List of uncorrelated factors and interactions 3**(4-1) fractional factorial design, 9 blocks, 27 runs |
|
| Unconf. Effects (excl. blocks) |
Unconfounded if blocks included? |
|
| 1 2 3 4 5 6 7 8 |
(1)A (L) A (Q) (2)B (L) B (Q) (3)C (L) C (Q) (4)D (L) D (Q) |
Yes Yes Yes Yes Yes Yes Yes Yes |
As you can see, in this 3**(4-1) design the main effects are not confounded with each other, even when the experiment is run in 9 blocks.
Box-Behnken Designs
In the case of 2**(k-p) designs, Plackett and Burman (1946) developed highly fractionalized designs to screen the maximum number of (main) effects in the least number of experimental runs. The equivalent in the case of 3**(k-p) designs are the so-called Box-Behnken designs (Box and Behnken, 1960; see also Box and Draper, 1984). These designs do not have simple design generators (they are constructed by combining two-level factorial designs with incomplete block designs), and have complex confounding of interaction. However, the designs are economical and therefore particularly useful when it is expensive to perform the necessary experimental runs.
Analyzing the 3**(k-p) Design
The analysis of these types of designs proceeds basically in the same way as was described in the context of 2**(k-p) designs. However, for each effect, one can now test for the linear effect and the quadratic (non-linear effect). For example, when studying the yield of chemical process, then temperature may be related in a non-linear fashion, that is, the maximum yield may be attained when the temperature is set at the medium level. Thus, non-linearity often occurs when a process performs near its optimum.
ANOVA Parameter Estimates
To estimate the ANOVA parameters, the factors levels for the factors in the analysis are internally recoded so that one can test the linear and quadratic components in the relationship between the factors and the dependent variable. Thus, regardless of the original metric of factor settings (e.g., 100 degrees C, 110 degrees C, 120 degrees C), you can always recode those values to -1, 0, and +1 to perform the computations. The resultant ANOVA parameter estimates can be interpreted analogously to the parameter estimates for 2**(k-p) designs.
For example, consider the following ANOVA results:
| Factor | Effect | Std.Err. | t (69) | p |
|---|---|---|---|---|
| Mean/Interc. BLOCKS(1) BLOCKS(2) (1)TEMPERAT (L) TEMPERAT (Q) (2)TIME (L) TIME (Q) (3)SPEED (L) SPEED (Q) 1L by 2L 1L by 2Q 1Q by 2L 1Q by 2Q |
103.6942 .8028 -1.2307 -.3245 -.5111 .0017 .0045 -10.3073 -3.7915 3.9256 .4384 .4747 -2.7499 |
.390591 1.360542 1.291511 .977778 .809946 .977778 .809946 .977778 .809946 1.540235 1.371941 1.371941 .995575 |
265.4805 .5901 -.9529 -.3319 -.6311 .0018 .0056 -10.5415 -4.6812 2.5487 .3195 .3460 -2.7621 |
0.000000 .557055 .343952 .740991 .530091 .998589 .995541 .000000 .000014 .013041 .750297 .730403 .007353 |
Main-effect estimates. By default, the Effect estimate for the linear effects (marked by the L next to the factor name) can be interpreted as the difference between the average response at the low and high settings for the respective factors. The estimate for the quadratic (non-linear) effect (marked by the Q next to the factor name) can be interpreted as the difference between the average response at the center (medium) settings and the combined high and low settings for the respective factors.
Interaction effect estimates. As in the case of 2**(k-p) designs, the linear-by-linear interaction effect can be interpreted as half the difference between the linear main effect of one factor at the high and low settings of another. Analogously, the interactions by the quadratic components can be interpreted as half the difference between the quadratic main effect of one factor at the respective settings of another; that is, either the high or low setting (quadratic by linear interaction), or the medium or high and low settings combined (quadratic by quadratic interaction).
In practice, and from the standpoint of "interpretability of results," one would usually try to avoid quadratic interactions. For example, a quadratic-by-quadratic A-by-B interaction indicates that the non- linear effect of factor A is modified in a nonlinear fashion by the setting of B. This means that there is a fairly complex interaction between factors present in the data that will make it difficult to understand and optimize the respective process. Sometimes, performing nonlinear transformations (e.g., performing a log transformation) of the dependent variable values can remedy the problem.
Centered and non-centered polynomials. As mentioned above, the interpretation of the effect estimates applies only when you use the default parameterization of the model. In that case, you would code the quadratic factor interactions so that they become maximally "untangled" from the linear main effects.
Graphical Presentation of Results
The same diagnostic plots (e.g., of residuals) are available for 3**(k-p) designs as were described in the context of 2**(k-p) designs. Thus, before interpreting the final results, one should always first look at the distribution of the residuals for the final fitted model. The ANOVA assumes that the residuals (errors) are normally distributed.
Plot of means. When an interaction involves categorical factors (e.g., type of machine, specific operator of machine, and some distinct setting of the machine), then the best way to understand interactions is to look at the respective interaction plot of means.
Surface plot. When the factors in an interaction are continuous in nature, you may want to look at the surface plot that shows the response surface applied by the fitted model. Note that this graph also contains the prediction equation (in terms of the original metric of factors), that produces the respective response surface.
Designs for Factors at 2 and 3 Levels
You can also generate standard designs with 2 and 3 level factors. Specifically, you can generate the standard designs as enumerated by Connor and Young for the US National Bureau of Standards (see McLean and Anderson, 1984). The technical details of the method used to generate these designs are beyond the scope of this introduction. However, in general the technique is, in a sense, a combination of the procedures described in the context of 2**(k-p) and 3**(k-p) designs. It should be noted however, that, while all of these designs are very efficient, they are not necessarily orthogonal with respect to all main effects. This is, however, not a problem, if one uses a general algorithm for estimating the ANOVA parameters and sums of squares, that does not require orthogonality of the design.
The design and analysis of these experiments proceeds along the same lines as discussed in the context of 2**(k-p) and 3**(k-p) experiments.
| To index |
The 2**(k-p) and 3**(k-p) designs all require that the levels of the factors are set at, for example, 2 or 3 levels. In many instances, such designs are not feasible, because, for example, some factor combinations are constrained in some way (e.g., factors A and B cannot be set at their high levels simultaneously). Also, for reasons related to efficiency, which will be discussed shortly, it is often desirable to explore the experimental region of interest at particular points that cannot be represented by a factorial design.
The designs (and how to analyze them) discussed in this section all pertain to the estimation (fitting) of response surfaces, following the general model equation:
y = b0 +b1 *x1 +...+bk *xk + b12 *x1 *x2 +b13 *x1 *x3 +...+bk-1,k *xk-1 *xk + b11 *x1² +...+bkk *xk²
Put into words, one is fitting a model to the observed values of the dependent variable y, that include (1) main effects for factors x1 , ..., xk, (2) their interactions (x1*x2, x1*x3, ... ,xk-1*xk), and (3) their quadratic components (x1**2, ..., xk**2). No assumptions are made concerning the "levels" of the factors, and you can analyze any set of continuous values for the factors.
There are some considerations concerning design efficiency and biases, which have led to standard designs that are ordinarily used when attempting to fit these response surfaces, and those standard designs will be discussed shortly (e.g., see Box, Hunter, and Hunter, 1978; Box and Draper, 1987; Khuri and Cornell, 1987; Mason, Gunst, and Hess, 1989; Montgomery, 1991). But, as will be discussed later, in the context of constrained surface designs and D- and A-optimal designs, these standard designs can sometimes not be used for practical reasons. However, the central composite design analysis options do not make any assumptions about the structure of your data file, that is, the number of distinct factor values, or their combinations across the runs of the experiment, and, hence, these options can be used to analyze any type of design, to fit to the data the general model described above.
Design Considerations
Orthogonal designs. One desirable characteristic of any design is that the main effect and interaction estimates of interest are independent of each other. For example, suppose you had a two- factor experiments, with both factors at two levels. Your design consists of four runs:
| A | B | |
|---|---|---|
| Run 1 Run 2 Run 3 Run 4 |
1 1 -1 -1 |
1 1 -1 -1 |
For the first two runs, both factors A and B are set at their high levels (+1). In the last two runs, both are set at their low levels (-1). Suppose you wanted to estimate the independent contributions of factors A and B to the prediction of the dependent variable of interest. Clearly this is a silly design, because there is no way to estimate the A main effect and the B main effect. One can only estimate one effect -- the difference between Runs 1+2 vs. Runs 3+4 -- which represents the combined effect of A and B.
The point here is that, in order to assess the independent contributions of the two factors, the factor levels in the four runs must be set so that the "columns" in the design (under A and B in the illustration above) are independent of each other. Another way to express this requirement is to say that the columns of the design matrix (with as many columns as there are main effect and interaction parameters that one wants to estimate) should be orthogonal (this term was first used by Yates, 1933). For example, if the four runs in the design are arranged as follows:
| A | B | |
|---|---|---|
| Run 1 Run 2 Run 3 Run 4 |
1 1 -1 -1 |
1 -1 1 -1 |
then the A and B columns are orthogonal. Now you can estimate the A main effect by comparing the high level for A within each level of B, with the low level for A within each level of B; the B main effect can be estimated in the same way.
Technically, two columns in a design matrix are orthogonal if the sum of the products of their elements within each row is equal to zero. In practice, one often encounters situations, for example due to loss of some data in some runs or other constraints, where the columns of the design matrix are not completely orthogonal. In general, the rule here is that the more orthogonal the columns are, the better the design, that is, the more independent information can be extracted from the design regarding the respective effects of interest. Therefore, one consideration for choosing standard central composite designs is to find designs that are orthogonal or near-orthogonal.
Rotatable designs. The second consideration is related to the first requirement, in that it also has to do with how best to extract the maximum amount of (unbiased) information from the design, or specifically, from the experimental region of interest. Without going into details (see Box, Hunter, and Hunter, 1978; Box and Draper, 1987, Chapters 14; see also Deming and Morgan, 1993, Chapter 13), it can be shown that the standard error for the prediction of dependent variable values is proportional to:
(1 + f(x)' * (X'X)¨¹ * f(x))**½
where f(x) stands for the (coded) factor effects for the respective model (f(x) is a vector, f(x)' is the transpose of that vector), and X is the design matrix for the experiment, that is, the matrix of coded factor effects for all runs; X'X**-1 is the inverse of the crossproduct matrix. Deming and Morgan (1993) refer to this expression as the normalized uncertainty; this function is also related to the variance function as defined by Box and Draper (1987). The amount of uncertainty in the prediction of dependent variable values depends on the variability of the design points, and their covariance over the runs. (Note that it is inversely proportional to the determinant of X'X; this issue is further discussed in the section on D- and A-optimal designs).
The point here is that, again, one would like to choose a design that extracts the most information regarding the dependent variable, and leaves the least amount of uncertainty for the prediction of future values. It follows, that the amount of information (or normalized information according to Deming and Morgan, 1993) is the inverse of the normalized uncertainty.
For the simple 4-run orthogonal experiment shown earlier, the information function is equal to
Ix = 4/(1 + x1² + x2²)
where x1 and x2 stand for the factor settings for factors A and B, respectively (see Box and Draper, 1987).
Inspection of this function in a plot (see above) shows that it is constant on circles centered at the origin. Thus any kind of rotation of the original design points will generate the same amount of information, that is, generate the same information function. Therefore, the 2-by-2 orthogonal design in 4 runs shown earlier is said to be rotatable.
As pointed out before, in order to estimate the second order, quadratic, or non-linear component of the relationship between a factor and the dependent variable, one needs at least 3 levels for the respective factors. What does the information function look like for a simple 3-by-3 factorial design, for the second-order quadratic model as shown at the beginning of this section?
As it turns out (see Box and Draper, 1987 and Montgomery, 1991; refer also to the manual), this function looks more complex, contains "pockets" of high-density information at the edges (which are probably of little particular interest to the experimenter), and clearly it is not constant on circles around the origin. Therefore, it is not rotatable, meaning different rotations of the design points will extract different amounts of information from the experimental region.
Star-points and rotatable second-order designs. It can be shown that by adding so-called star- points to the simple (square or cube) 2-level factorial design points, one can achieve rotatable, and often orthogonal or nearly orthogonal designs. For example, adding to the simple 2-by-2 orthogonal design shown earlier the following points, will produce a rotatable design.
| A | B | |
|---|---|---|
| Run 1 Run 2 Run 3 Run 4 Run 5 Run 6 Run 7 Run 8 Run 9 Run 10 |
1 1 -1 -1 -1.414 1.414 0 0 0 0 |
1 -1 1 -1 0 0 -1.414 1.414 0 0 |
The first four runs in this design are the previous 2-by-2 factorial design points (or square points or cube points); runs 5 through 8 are the so-called star points or axial points, and runs 9 and 10 are center points.
The information function for this design for the second-order (quadratic) model is rotatable, that is, it is constant on the circles around the origin.
Alpha for Rotatability and Orthogonality
The two design characteristics discussed so far -- orthogonality and rotatability -- depend on the number of center points in the design and on the so-called axial distance
(alpha), which is the distance of the star points from the center of the design (i.e., 1.414 in the design shown above). It can be shown (e.g., see Box, Hunter, and Hunter, 1978; Box and Draper, 1987, Khuri and Cornell, 1987; Montgomery, 1991) that a design is rotatable if:
= ( nc )¼
where nc stands for the number of cube points in the design (i.e., points in the factorial portion of the design).
A central composite design is orthogonal, if one chooses the axial distance so that:
= {[( nc + ns + n0 )½ - nc½]² * nc/4}¼
where
nc is the number of cube points in the design
ns is the number of star points in the design
n0 is the number of center points in the design
To make a design both (approximately) orthogonal and rotatable, one would first choose the axial distance for rotatability, and then add center points (see Kkuri and Cornell, 1987), so that:
n0 
4*nc½ + 4 - 2k
where k stands for the number of factors in the design.
Finally, if blocking is involved, Box and Draper (1987) give the following formula for computing the axial distance to achieve orthogonal blocking, and in most cases also reasonable information function contours, that is, contours that are close to spherical:
= [k*(l+ns0/ns)/(1+nc0/nc)]½
where
ns0 is the number of center points in the star portion of the design
ns is the number of non-center star points in the design
nc0 is the number of center points in the cube portion of the design
nc is the number of non-center cube points in the design
Available Standard Designs
The standard central composite designs are usually constructed from a 2**(k-p) design for the cube portion of the design, which is augmented with center points and star points. Box and Draper (1987) list a number of such designs.
Small composite designs. In the standard designs, the cube portion of the design is typically of resolution V (or higher). This is, however, not necessary, and in cases when the experimental runs are expensive, or when it is not necessary to perform a statistically powerful test of model adequacy, then one could choose for the cube portion designs of resolution III. For example, it could be constructed from highly fractionalized Plackett-Burman designs. Hartley (1959) described such designs.
Analyzing Central Composite Designs
The analysis of central composite designs proceeds in much the same way as for the analysis of 3**(k-p) designs. You fit to the data the general model described above; for example, for two variables you would fit the model:
y = b0 + b1*x1 + b2*x2 + b12*x1*x2 + b11*x12 + b22*x22
The Fitted Response Surface
The shape of the fitted overall response can best be summarized in graphs and you can generate both contour plots and response surface plots (see examples below) for the fitted model.
Categorized Response Surfaces
You can fit 3D surfaces to your data, categorized by some other variable. For example, if you replicated a standard central composite design 4 times, it may be very informative to see how similar the surfaces are when fitted to each replication.
This would give you a graphical indication of the reliability of the results and where (e.g., in which region of the surface) deviations occur.
Clearly, the third replication produced a different surface. In replications 1, 2, and 4, the fitted surfaces are very similar to each other. Thus, one should investigate what could have caused this noticeable difference in the third replication of the design.
| To index |
Latin square designs (the term Latin square was first used by Euler, 1782) are used when the factors of interest have more than two levels and you know ahead of time that there are no (or only negligible) interactions between factors. For example, if you wanted to examine the effect of 4 fuel additives on reduction in oxides of nitrogen and had 4 cars and 4 drivers at your disposal, then you could of course run a full 4 x 4 x 4 factorial design, resulting in 64 experimental runs. However, you are not really interested in any (minor) interactions between the fuel additives and drivers, fuel additives and cars, or cars and drivers. You are mostly interested in estimating main effects, in particular the one for the fuel additives factor. At the same time, you want to make sure that the main effects for drivers and cars do not affect (bias) your estimate of the main effect for the fuel additive.
If you labeled the additives with the letters A, B, C, and D, the Latin square design that would allow you to derive unconfounded main effects estimates could be summarized as follows (see also Box, Hunter, and Hunter, 1978, page 263):
| Car | ||||
|---|---|---|---|---|
| Driver | 1 | 2 | 3 | 4 |
| 1 2 3 4 |
A D B C |
B C D A |
D A C B |
C B A D |
The example shown above is actually only one of the three possible arrangements in effect estimates. These "arrangements" are also called Latin square. The example above constitutes a 4 x 4 Latin square; and rather than requiring the 64 runs of the complete factorial, you can complete the study in only 16 runs.
Greco-Latin square. A nice feature of Latin Squares is that they can be superimposed to form what are called Greco-Latin squares (this term was first used by Fisher and Yates, 1934). For example, the following two 3 x 3 Latin squares can be superimposed to form a Greco-Latin square:
In the resultant Greco-Latin square design, you can evaluate the main effects of four 3-level factors (row factor, column factor, Roman letters, Greek letters) in only 9 runs.
Hyper-Greco Latin square. For some numbers of levels, there are more than two possible Latin square arrangements. For example, there are three possible arrangements for 4-level Latin squares. If all three of them are superimposed, you get a Hyper-Greco Latin square design. In that design you can estimate the main effects of all five 4-level factors with only 16 runs in the experiment.
Analyzing the Design
Analyzing Latin square designs is straightforward. Also, plots of means can be produced to aid in the interpretation of results.
Very Large Designs, Random Effects, Unbalanced Nesting
Note that there are several other statistical methods that can also analyze these types of designs; see the section on Methods for Analysis of Variance for details. In particular the Variance Components and Mixed Model ANOVA/ANCOVA chapter discusses very efficient methods for analyzing designs with unbalanced nesting (when the nested factors have different numbers of levels within the levels of the factors in which they are nested), very large nested designs (e.g., with more than 200 levels overall), or hierarchically nested designs (with or without random factors).
| To index |
Applications. Taguchi methods have become increasingly popular in recent years. The documented examples of sizable quality improvements that resulted from implementations of these methods (see, for example, Phadke, 1989; Noori, 1989) have added to the curiosity among American manufacturers. In fact, some of the leading manufacturers in this country have begun to use these methods with usually great success. For example, AT&T is using these methods in the manufacture of very large scale integrated (VLSI) circuits; also, Ford Motor Company has gained significant quality improvements due to these methods (American Supplier Institute, 1984 to 1988). However, as the details of these methods are becoming more widely known, critical appraisals are also beginning to appear (for example, Bhote, 1988; Tribus and Szonyi, 1989).
Overview. Taguchi robust design methods are set apart from traditional quality control procedures (see Quality Control and Process Analysis) and industrial experimentation in various respects. Of particular importance are:
Quality and Loss Functions
What is quality. Taguchi's analysis begins with the question of how to define quality. It is not easy to formulate a simple definition of what constitutes quality; however, when your new car stalls in the middle of a busy intersection -- putting yourself and other motorists at risk -- you know that your car is not of high quality. Put another way, the definition of the inverse of quality is rather straightforward: it is the total loss to you and society due to functional variations and harmful side effects associated with the respective product. Thus, as an operational definition, you can measure quality in terms of this loss, and the greater the quality loss the lower the quality.
Discontinuous (step-shaped) loss function. You can formulate hypotheses about the general nature and shape of the loss function. Assume a specific ideal point of highest quality; for example, a perfect car with no quality problems. It is customary in statistical process control (SPC; see also Process Analysis) to define tolerances around the nominal ideal point of the production process. According to the traditional view implied by common SPC methods, as long as you are within the manufacturing tolerances you do not have a problem. Put another way, within the tolerance limits the quality loss is zero; once you move outside the tolerances, the quality loss is declared to be unacceptable. Thus, according to traditional views, the quality loss function is a discontinuous step function: as long as you are within the tolerance limits, quality loss is negligible; when you step outside those tolerances, quality loss becomes unacceptable.
Quadratic loss function. Is the step function implied by common SPC methods a good model of quality loss? Return to the "perfect automobile" example. Is there a difference between a car that, within one year after purchase, has nothing wrong with it, and a car where minor rattles develop, a few fixtures fall off, and the clock in the dashboard breaks (all in-warranty repairs, mind you...)? If you ever bought a new car of the latter kind, you know very well how annoying those admittedly minor quality problems can be. The point here is that it is not realistic to assume that, as you move away from the nominal specification in your production process, the quality loss is zero as long as you stay within the set tolerance limits. Rather, if you are not exactly "on target," then loss will result, for example in terms of customer satisfaction. Moreover, this loss is probably not a linear function of the deviation from nominal specifications, but rather a quadratic function (inverted U). A rattle in one place in your new car is annoying, but you would probably not get too upset about it; add two more rattles, and you might declare the car "junk." Gradual deviations from the nominal specifications do not produce proportional increments in loss, but rather squared increments.
Conclusion: Controlling variability. If, in fact, quality loss is a quadratic function of the deviation from a nominal value, then the goal of your quality improvement efforts should be to minimize the squared deviations or variance of the product around nominal (ideal) specifications, rather than the number of units within specification limits (as is done in traditional SPC procedures).
Signal-to-Noise (S/N) Ratios
Measuring quality loss. Even though you have concluded that the quality loss function is probably quadratic in nature, you still do not know precisely how to measure quality loss. However, you know that whatever measure you decide upon should reflect the quadratic nature of the function.
Signal, noise, and control factors. The product of ideal quality should always respond in exactly the same manner to the signals provided by the user. When you turn the key in the ignition of your car you expect that the starter motor turns and the engine starts. In the ideal-quality car, the starting process would always proceed in exactly the same manner -- for example, after three turns of the starter motor the engine comes to life. If, in response to the same signal (turning the ignition key) there is random variability in this process, then you have less than ideal quality. For example, due to such uncontrollable factors as extreme cold, humidity, engine wear, etc. the engine may sometimes start only after turning over 20 times and finally not start at all. This example illustrates the key principle in measuring quality according to Taguchi: You want to minimize the variability in the product's performance in response to noise factors while maximizing the variability in response to signal factors.
Noise factors are those that are not under the control of the operator of a product. In the car example, those factors include temperature changes, different qualities of gasoline, engine wear, etc. Signal factors are those factors that are set or controlled by the operator of the product to make use of its intended functions (turning the ignition key to start the car).
Finally, the goal of your quality improvement effort is to find the best settings of factors under your control that are involved in the production process, in order to maximize the S/N ratio; thus, the factors in the experiment represent control factors.
S/N ratios. The conclusion of the previous paragraph is that quality can be quantified in terms of the respective product's response to noise factors and signal factors. The ideal product will only respond to the operator's signals and will be unaffected by random noise factors (weather, temperature, humidity, etc.). Therefore, the goal of your quality improvement effort can be stated as attempting to maximize the signal-to-noise (S/N) ratio for the respective product. The S/N ratios described in the following paragraphs have been proposed by Taguchi (1987).
Smaller-the-better. In cases where you want to minimize the occurrences of some undesirable product characteristics, you would compute the following S/N ratio:
Eta = -10 * log10 [(1/n) * 
(yi2)] for i = 1 to no. vars
see outer arrays
Here, Eta is the resultant S/N ratio; n is the number of observations on the particular product, and y is the respective characteristic. For example, the number of flaws in the paint on an automobile could be measured as the y variable and analyzed via this S/N ratio. The effect of the signal factors is zero, since zero flaws is the only intended or desired state of the paint on the car. Note how this S/N ratio is an expression of the assumed quadratic nature of the loss function. The factor 10 ensures that this ratio measures the inverse of "bad quality;" the more flaws in the paint, the greater is the sum of the squared number of flaws, and the smaller (i.e., more negative) the S/N ratio. Thus, maximizing this ratio will increase quality.
Nominal-the-best. Here, you have a fixed signal value (nominal value), and the variance around this value can be considered the result of noise factors:
Eta = 10 * log10 (Mean2/Variance)
This signal-to-noise ratio could be used whenever ideal quality is equated with a particular nominal value. For example, the size of piston rings for an automobile engine must be as close to specification as possible to ensure high quality.
Larger-the-better. Examples of this type of engineering problem are fuel economy (miles per gallon) of an automobile, strength of concrete, resistance of shielding materials, etc. The following S/N ratio should be used:
Eta = -10 * log10 [(1/n) * (1/yi2)] for i = 1 to no. vars
see outer arrays
Signed target. This type of S/N ratio is appropriate when the quality characteristic of interest has an ideal value of 0 (zero), and both positive and negative values of the quality characteristic may occur. For example, the dc offset voltage of a differential operational amplifier may be positive or negative (see Phadke, 1989). The following S/N ratio should be used for these types of problems:
Eta = -10 * log10(s2) for i = 1 to no. vars see outer arrays
where s2 stands for the variance of the quality characteristic across the measurements (variables).Fraction defective. This S/N ratio is useful for minimizing scrap, minimizing the percent of patients who develop side-effects to a drug, etc. Taguchi also refers to the resultant Eta values as Omegas; note that this S/N ratio is identical to the familiar logit transformation (see also Nonlinear Estimation):
Eta = -10 * log10[p/(1-p)]
where
p is the proportion defective
Ordered categories (the accumulation analysis). In some cases, measurements on a quality characteristic can only be obtained in terms of categorical judgments. For example, consumers may rate a product as excellent, good, average, or below average. In that case, you would attempt to maximize the number of excellent or good ratings. Typically, the results of an accumulation analysis are summarized graphically in a stacked bar plot.
Orthogonal Arrays
The third aspect of Taguchi robust design methods is the one most similar to traditional techniques. Taguchi has developed a system of tabulated designs (arrays) that allow for the maximum number of main effects to be estimated in an unbiased (orthogonal) manner, with a minimum number of runs in the experiment. Latin square designs, 2**(k-p) designs (Plackett-Burman designs, in particular), and Box-Behnken designs main are also aimed at accomplishing this goal. In fact, many of the standard orthogonal arrays tabulated by Taguchi are identical to fractional two-level factorials, Plackett-Burman designs, Box-Behnken designs, Latin square, Greco-Latin squares, etc.
Analyzing Designs
Most analyses of robust design experiments amount to a standard ANOVA of the respective S/N ratios, ignoring two-way or higher-order interactions. However, when estimating error variances, one customarily pools together main effects of negligible size.
Analyzing S/N ratios in standard designs. It should be noted at this point that, of course, all of the designs discussed up to this point (e.g., 2**(k-p), 3**(k-p), mixed 2 and 3 level factorials, Latin squares, central composite designs) can be used to analyze S/N ratios that you computed. In fact, the many additional diagnostic plots and other options available for those designs (e.g., estimation of quadratic components, etc.) may prove very useful when analyzing the variability (S/N ratios) in the production process.
Plot of means. A visual summary of the experiment is the plot of the average Eta (S/N ratio) by factor levels. In this plot, the optimum setting (i.e., lar
