interpreting blocks and random factors: comment

Interpreting Blocks and Random Factors: CommentAuthor(s): David A. HarvilleSource: Journal of the American Statistical Association, Vol. 86, No. 415 (Sep., 1991), pp. 812-815Published by: American Statistical AssociationStable URL: http://www.jstor.org/stable/2290418 .

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812 Journal of the American Statistical Association

Comment DAVID A. HARVILLE*

1. INTRODUCTION

The existence of several alternative approaches to the formulation of mixed models has led to much confusion and some controversy. The authors have attempted to re- solve this confusion and controversy, which persist despite previous attempts at resolution by, for example, Hocking (1973) and Harville (1978). In my opinion, they persist because some of the underlying issues are rather subtle and (to a lesser extent) because many users of mixed-model methodology lack familiarity with the relevant mathematics.

The authors have chosen to use "population" models, rather than randomization models, in their presentation. For consistency-and because of my own preference for population models (Harville 1975)-I shall do likewise in my discussion.

My discussion is organized into three sections, corresponding to three topics: the efficiency of blocking, choosing between alternative formulations of the model, and the distinction (made by the authors) between independent contributions and random interaction effects.

2. EFFICIENCY OF BLOCKING

In their Section 3.1, the authors define the efficiency of blocking to be varN(l cjYj)/varB(2 cjY1), where the subscripts N and B identify the design as nonblocked or blocked. It is unclear from the authors' discussion whether they in- tend for the experimental units for the nonblocked design to be the same as those for the blocked design. It is cus- tomary (for purposes of defining the efficiency of blocking) to take the experimental units for both designs to be the same.

If the units for both designs were taken to be the same, the authors' formula (3.2) for the efficiency of blocking would be incorrect. It would be incorrect because the authors implicitly assume that the variance of a treatment average is the same for a nonblocked design as for a blocked design. In reality, the "effective" variance of a treatment average for a nonblocked design would either be smaller or larger than the variance 02 /J of a treatment average for a blocked design, depending on whether p > 0 or p < 0 (since, for a nonblocked design, two or more units from one block could be allocated to the same treatment). The authors' formula for the efficiency of blocking would be correct only if each of the IJ experimental units included in the nonblocked design were assumed to come from a different block.

Let us now suppose that the experimental units for the nonblocked design are the same as those for the blocked design and consider the effect of this supposition on the

* David A. Harville is Professor, Department of Statistics, Iowa State University, Ames, IA 50011.

efficiency of blocking. In doing so, let us restrict attention to designs for which each of the I treatments is assigned to exactly J of the IJ experimental units and assume that K = 1 (i.e., that only one observation is to be taken on each experimental unit).

For i, p = 1, ...,I, and j = 1, J, let Y!p represent the observation that would be obtained if the ith treatment were assigned to the pth of those experimental units in the jth block. Further, define Sijp = 1 if the ith treatment is assigned to the pth unit in the jth block; define 8ijp = 0, otherwise. Take 8 to be the I2J-dimensional vector whose ijpth element is 6ijp. The assignment of treatments to experimental units may be by restricted randomization (as in the case of a randomized complete block design) or by unrestricted randomization (as in the case of a completely randomized design); in either case the effect is to in- duce a distribution on 8 (Kempthorne 1952). Take Yi = J-1 ljlp 8ijpY*p to be the average of the J observations on the ith treatment.

Assume that (conditional on 8) the Y*jp's follow a population model with E(Y*p) = gi (for i, p = 1, ..., I, and j = 1, ..., J) and

cov(Y!p,Y Fj,r,) = o2y if i' = i, j' = j, and p' = p,

=pr2y ifj'=j, and p'=p,

=0 ifj'#j. These assumptions are consistent with those of the authors' population model.

It can be shown (via a straightforward, though somewhat tedious exercise) that E(li ciYi I 8) = 2 cigi and that

var( cgi|i = (o2/J)( -p) c2

2

+ (po2/J2) E (E cjnij)

where (for i = 1, ..., I and j = 1, ..., J) nij = Ep Sijp represents the number of appearances of the ith treatment in the jth block. For a (balanced) block arrangement, nij = 1 (for i = 1, . .., I and j = 1, ... ., J) and (since Yj ci = O)

var( ciY | (U21j)(l-p _

c2 (1

in agreement with the authors' results. For a completely randomized design, it can be shown that

? 1991 American Statistical Association Joumal of the American Statistical Association

September 1991, Vol. 86, No. 415, Review Paper



Harville: Comment 813

E[var( cii T1

=((T21j[I _ (I _1 )(IJ-1 I) lp] Ec2i (2)

(where the expectation is with respect to the distribution induced on { by the randomization).

Forming the ratio of expressions (2) and (1) gives

1- [(I- )/(IJ- l)]p

i-p~~~~~~~3 1 - p

as a measure of the efficiency of blocking. This measure gives a smaller value for the efficiency of blocking than the authors' measure (3.2) if p > 0, and a larger value if p < 0. It is similar to the authors' measure in that it is a strictly increasing function of p and leads to the same test of the null hypothesis that "blocking has no effect on the efficiency of treatment comparisons."

By replacing the parameter p in formula (3) with the estimator f (discussed by the authors in their Section 3.3), we obtain (after some simplification)

(J - I)MS(Blocks) + J(I - 1)MS(T*B)

(IJ - 1)MS(T*B)

as an estimator of the efficiency of blocking. This estimator is identical to the estimator derived by Kempthorne (1952) on the basis of a randomization model.

Note that measure (3) is based on the implicit assumption that the existence of blocks is to be ignored in the analysis of the data from the completely randomized design. Alter- native measures of efficiency could be devised that would be more appropriate than (3) if the existence of the blocks were to be taken into account in that analysis.

3. MODEL 1 VERSUS MODEL 2

For purposes of evaluating or comparing linear models- like the authors' Models 1 and 2-that might be applied to a vector, say y, of observations, it seems desirable to es- tablish some criteria. I suggest the following three.

Criterion 1. Associated with any linear model are the collections, say At and t, of the values of E(y) and var(y) that can be generated by allowing the parameters of the model (e.g., fixed effects and variance components) to range over their possible values (i.e., over the parameter space). The model should be sufficiently flexible that At and v include all vectors and matrices that can be regarded as "reasonable candidates" for E(y) and var(y), but not so flexible that they include vectors or matrices that can be "ruled out" a priori.

Criterion 2. Typically the quantities about which inferences or predictions are to be made are most easily expressed in nonstatistical terms associated with a particular application or type of application. The model should be such that it is relatively easy to reexpress the quantities of interest in terms of the model's parameters or in terms of random variables associated with the model (e.g., random effects).

Criterion 3. The model should be such that, once the quantities of interest have been reexpressed as in Criterion 2, it is clear what statistical procedures should be adopted and how (from a computational standpoint) those procedures should be implemented.

In comparing Models 1 and 2, the authors implicitly adopt criteria similar to Criteria 1-3. The primary difference between the two sets of criteria is that the authors seem to prefer a more restrictive version of Criterion 2; they seem to favor models whose individual parameters correspond to quantities of interest and-in the case of models like Models 1 and 2-whose individual random effects correspond to quantities of interest. They may feel that models that satisfy their more restrictive version of Criterion 2 are more likely to satisfy Criterion 3.

It seems desirable to introduce into the comparison of Models 1 and 2 a modified version of Model 1, say Model 1', in which the restriction o-2 ? o-2/I is imposed on the parameter space. Models 1 and 2 differ with regard to Cri- terion 1, and the choice between them should be based solely on that criterion; if the data can reasonably be envisioned as having been generated from uncorrelated random effects and errors in accordance with the authors' Equation (4.5) [and their Equation (4.1) or (5.1)], then Model 2 should be preferred to Model 1. Models 1' and 2 are equivalent with regard to Criterion 1, and the choice between them should be based on Criteria 2 and 3.

It might seem from the authors' discussion that, in mak- ing inferences about the efficiency of blocking, Model 2 has an advantage over Model 1' (or 1) with respect to Cri- teria 2 and 3. However, it is nearly as easy to express p (the correlation between units in the same block), and hence the efficiency of blocking, in terms of the parameters of Model 1' (or 1) as in terms of the parameters of Model 2. We find that p = (o- b-Ilor)/[or + 1-1(1-1)or]. More- over, in light of this expression, it is readily apparent from the (Version 1) EMS's in the authors' Table 2 that the ratio MS(Blocks)/MS(T*B) is an appropriate test statistic for testing the null hypothesis that p = 0-or equivalently the null hypothesis that "blocking has no effect on efficiency of treatment comparisons" (Sec. 4.3, final paragraph).

According to the authors, the random variables bl, ... bj (from Model 1 or 1') can be more "naturally" regarded as the main effects of blocks than the random variables bl,

bj (from Model 2), and hence the hypothesis H1: - o2= O is more naturally interpretable as a hypothesis that "block main effect is zero" than the hypothesis H2: 0ob = 0. I can tnink of exceptions. Consider, for example, the animal- breeding application (mentioned by the authors in their Sec- tion 7.1), in which the treatments correspond to "environments" and the blocks to "genotypes." There may be I* environments that are of interest, only I of which are rep- resented in the data. Then the quantities I" E,i= Wil -,u

*--,*- =1 Wij - , which (under Model 2) converge (as I* o- o) to b1, . .., bJ, may be of more interest than b1

I* is sufficiently large, it may be "natural" to regard b1, ..,bJ as the main effects of blocks. Moreover, in con-



814 Journal of the American Statistical Association

nection with the authors' study of the limiting behavior of the BLUP's of bl, ..., bj, note that, in the context of this example, it is natural to let I -> oo as well as J, K o-> o, in which case the BLUP's converge to bl, ..., bj.

Under Model 2,

COV(Yijk, Yi'j'k') = 0b + e+ o

if i'=i, j'=j, and k'=k, - LT2 + LT2

if i' = i, j' = j, and k' # k,

=(- if i' = i and j'j,

-O if j'$j.

Thus each of the variance components is interpretable as a difference in covariation. A more flexible model is obtained by relaxing the assumption (implicit in Model 2) that these differences in covariation are nonnegative. When this is done, it may be desirable (to avoid confusion) to replace 'b, (J2, and 0-2 with symbols not tied to Model 2 and-

following Nelder (1977)-to refer to these parameters as canonical components rather than variance components.

In principle there is no need to introduce a model like Model 1 or 2 in which the observations are expressed in terms of random effects and errors; the variance-covariance matrix of the observations can be expressed directly in terms of canonical components. In practice, however, the introduction of such a model may make it easier to write out the variance-covariance matrix and may also be helpful in satisfying Criteria 2 and 3.

4. INTERACTIONS VERSUS INDEPENDENT CONTRIBUTIONS

In their Sections 6.3 and 7.3 the authors attempt to dif- ferentiate between random interaction effects and random effects that they call independent contributions. Among the authors' criteria for distinguishing independent contributions from random interaction effects are the following.

Criterion 1'. If blocks (as well as treatments) were regarded as fixed, then the treatment-by-block interaction effects would necessarily be fixed. In contrast, the randomness of independent contributions is inherent; it is not a consequence of the randomness of other terms in the model.

Criterion 2'. Random effects are independent contributions if they cannot be deleted from the model even when the factors whose levels index the random effects behave additively. For example, the whole-plot errors (the G1 's) cannot be deleted from the authors' model (6.6) even when treatments and blocks behave additively.

Criterion 1' is based on a long-standing convention. Ac- cording to this convention, the way to determine whether effects are random or fixed is to first classify each factor as random or fixed depending on whether or not the levels of that factor can be regarded as a random sample from an "infinite" population of levels. If the factor is determined to be random, then all effects indexed by (i.e., including a subscript for) the levels of that factor are taken to be ran-

dom. The motivation for this convention comes from re- garding the distribution of the random effects as being that induced by the sampling of the levels of the random factors.

In my opinion this convention is much too restrictive. It rules out many potentially useful models, and, by doing so, tends to promote the use of inappropriate models.

In deciding whether the main effects associated with any particular factor-or the interaction effects associated with any particular combination of factors-are to be regarded as fixed or random, the relevant distribution is the conditional distribution of the effects given the levels. Is it reasonable, in light of any prior information that is to be taken into account, to suppose that, conditional on the levels, the effects have mean zero and common variance and, for example, that they are uncorrelated? If so, then it may be appropriate to regard the effects as random. The final de- cision should be made by thinking in terms of which assumption is likely to lead to the more sensible analysis.

Suppose, for example, that the only two factors of import are treatments and blocks and that it has been determined that the main effects of both factors should be regarded as fixed. Then, according to the conventional wisdom, treatment-by-block interaction effects should also be regarded as fixed, which-unless there is some replication of treatments within blocks or unless treatment-by-block interactions are thought to be negligible-precludes a sensible (frequentist) analysis. In many instances, however, it may be reasonable to ignore the conventional wisdom by re- garding the treatment-by-block interaction effects as random and analyzing the data accordingly. In fact, even if there is replication of treatments within blocks, taking the interaction effects to be random may, in many instances, lead to a more sensible analysis than taking them to be fixed (or assuming that they are negligible).

Criterion 2' for distinguishing independent contributions from random interaction effects is needed only because of the confusing custom (implicitly followed by the authors) of using a single random term to represent a sum of confounded random effects. Let us consider this custom in the context of a two-way classification by treatments and blocks, taking care to distinguish between two types of replication within blocks: (1) replication that results from assigning the same treatment to more than one unit in the same block, and (2) repeated measurements on the same unit.

Denote by pijl, ..., pijR,, those of the experimental units in the jth block that were allocated to the ith treatment, and let Yijrk represent the kth of K measurements on the rth of these Rij units. Decompose Yijrk as

Yijrk - WijPr + eijrk ,

where eijrk is a measurement error. Here W1jp represents the mean of an "infinite" number of measurements on the pth unit in the jth block when that unit is subjected to the ith treatment.

Notice that my notation differs from that of the authors in that, for purposes of distinguishing between the two types of within-block replication, I have introduced an additional subscript. More significantly, notice that W1jp is a concep- tually well-defined quantity, whereas the authors' W1, is not.



Bremer: Comment 815

Their definition is in terms of "a large number of observations of treatment i in block j." Presumably, large means a large number of measurements on the same unit, in which case it is implicit in the authors' notation that there is no unit-to-unit variation within a block-large with respect to the number of units would not be meaningful in any of the authors' Examples 1.1-1.4.

Corresponding to the authors' Models 1 and 2 for their Wij are models for Wijp of the general form

Wijp = p + r, + bj + gj + up + n ijp (4)

where ,u and -i are unknown parameters (Wilk and Kemp- thorne 1956, WADC Technical Report). We could take the b1's, g11's, ujp's, and nijp's to be uncorrelated random variables having mean zero and common variances b-2, J2

.2, and (T2, respectively, corresponding to the assumptions in the authors' Model 2. Alternatively, we could assume a correlation structure consistent with the restrictions 1i gij = Ep ujp = Yi nijp = Yp nijp = 0, corresponding to the assumptions in the authors' Model 1. In either case, the pres- ence in Model (4) of the sum Ujp + n1jp allows for the pos- sibility of within-block unit differences and within-block treatment-by-unit interactions.

Note that (since each unit receives only one treatment) UJPiJr and nijp,, are inherently confounded. Moreover, if Rij = 1 for all i and j (as in the case of a randomized complete block design), then gi is confounded with Ujpif and nijp,,, It is common practice to represent a sum of confounded effects or errors by a single symbol, which may lead to confusion. For example, when Ri = 1 for all i and j and K =

1 (the case considered by the authors in their Section 4), it is common practice to suppress the last two subscripts of Yijrk and eijrk and to write

Yij = g + ri + bj + eij, in which case eij implicitly represents the sum of four confounded effects or errors.

Let us now turn to the more complex model considered by the authors in their Section 6.3. As indicated by the authors, it is natural to think of the Gi term in their model (6.6) as representing the contribution of the ijth whole plot. Confusion arises because Gij actually represents the sum of three confounded effects, consisting, in addition to a whole- plot effect, of a whole-plot-treatment by block interaction effect and a within-block whole-plot-treatment by whole- plot interaction effect.

In conclusion, the authors' distinction between independent contributions and random interaction effects seems su- perfluous and ill-defined. The need for any such distinction can be eliminated by relaxing an overly restrictive convention and by recognizing that some of the terms in a linear model may represent the sum of two or more confounded effects or errors.

REFERENCES

Harville, D. A. (1975), "Experimental Randomization: Who Needs It?" The American Statistician, 29, 27-31.

Nelder, J. A. (1977), "A Reformulation of Linear Models," Journal of the Royal Statistical Society, Ser. A, 140, 48-63.

Wilk, M. B., and Kempthorne, 0. (1956), "Analysis of Variance: Pre- liminary Tests, Pooling, and Linear Models," WADC Technical Re- port 55-244, Wright-Patterson Air Force Base, Ohio.

Comment RONALD H. BREMER*

1. INTRODUCTION

The authors have presented many considerations needed to fully understand the two-way mixed model. The argu- ments supporting the conclusion that Model 1 is "the" two- way mixed model are not convincing. The implication of the authors that choosing Model 1 implies Version 1 of the EMS table is where I differ in opinion the most. In more complex mixed models, the relationship between the covariance structure implied by the generalization of Model 1 must be used to relate the Version 2 EMS table to Model 1. I agree with the authors that Model 1 is preferable to Model 2, but I feel that EMS's of SAS are more versatile when examining this model. Not recognizing the usefulness of the Version 2 EMS table with regard to Model 1 has the following consequences.

* Ronald H. Bremer is Assistant Professor, Information Systems and Quantitative Sciences, Texas Tech University, Lubbock, TX 79409-2101.

1. The covariance component (variance component) interpretation available in Model 1 is ignored. This interpretation is useful in formulating, unifying, and under- standing complex models.

2. The interpretation of the random variables in Model 1 with respect to the covariance components can be used to unify the ideas and problems with those of MANOVA, multiple regression, and time series.

3. Obtaining the Version 2 EMS table is simple in comparison to the Version 1 EMS algorithm. Moreover, con- verting from the Version 2 EMS table to the Version 1 EMS table is straightforward.

4. The variances of the random variables in Model 1 are composite in nature. This can lead to less efficient infer-

? 1991 American Statistical Association Journal of the American Statistical Association

September 1991, Vol. 86, No. 415, Review Paper



interpreting blocks and random factors: comment

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