REMARKS ABOUT EXERCISE 4
This exercise is designed to help you see the relationships among two-way anova and one-way
anova in which the one-way analysis is based on “stringing out” the two-way design. By “stringing out” I
mean the kind of operation described in the exercise in which you re-name the treatment combinations in
the two-way anova and then use a priori contrasts to test the two-way main effects and interactions.
Now, it must be admitted that this exercise works well because the two-way design in question is
indeed a 2 x 2 factorial. If the design had been larger, the “prior contrast” approach in the “strung out”
one-way anova equivalent would have been more complicated, particularly when the sample sizes were
unequal across “cells.” But the point to made here was pedagogic and the level was set at the beginning
one; if you’re interested in the nuances and complications of what actually happens in your favorite
software when it encounters a larger design, let me know and I’ll point you toward that material.
That stated, the statistical parts of the exercise are straightforward. If executed correctly, the
exercise reveals these points:
1. When sample sizes are equal in all treatment combinations, Type I and Type III SS extracted from the
two-way design are identical AND the a priori contrasts from the “strung out” one-way anovas recreate
the SS for each main effect and the interaction.
2. When sample sizes are unequal, Type I and Type III SS are not the same. Moreover, the residual
variance in the two-way design will differ when you extract the different types of SS. And one more
thing: if one does not extract the interaction but extracts only the main effects, the Type III SS for main
effects will not be the same as when you extract those same main effects along with the interaction.
NOTE. When sample sizes are unequal, some software packages are set up such that the default SS are
Type III. It might be the case that if you write the model statement explictly, as in Y = constant + effect
A + effect B + Interaction AB, that Type I SS are extracted for the effect that comes first, that Type III SS
are extracted for the effect that comes next, but adjusted only for the preceding effects (as in a step-wise
multiple regression), and that only the interaction is a “true” Type III (as if all other effects existed and
had been extracted). You have to really know what your software is doing.
3. When sample sizes are unequal, the a priori contrast approach from the “strung out” one-way anova
yields true Type III SS for each effect and the proper residual from a Type III analysis.
4. When sample sizes are unequal, if one treats each main effect as if it were the sole factor in the
analysis such that one performs a one-way anova FOR THAT EFFECT (NOT a one-way anova on the
entire “strung-out” design), one gets the Type I SS for that effect and a residual variance corresponding to
the “Type I” analysis. Obviously this residual variance is larger than the residual that you can obtain
from a two-way anova Type III analysis because, in the case of the one-way anova for the main effect, the
residual includes the effects of the other main effect and the interaction. That is, this analysis may
overestimate the SS for the effect (because it assumes the other effect doesn’t exist) but it also
overestimates the residual, so whether it is indeed “too liberal” an analysis is not so clear.
The biological aspects of the assignment require some thought. First, let’s not even consider any
density-dependent aspects of our situation because that would suggest yet a different measure of fitness
and require some knowledge of the equilibrium population numbers. Moving on, if the major force of
selection were acting purely through viability, that is, survival from birth to maturity, and not through any
differential fecundity, then it makes sense to count adults in the measure of fitness. Surviving adults are
the currency of fitness and immature numbers might dilute the signal of local adaptation, especially if
there is substantial mortality between birth and maturity. If sperm are not limiting in any way such that
reproduction is purely a function of female numbers (and no inbreeding effects are manifested in any
serious manner), one could argue that only females should be counted because, again, male numbers
really dilute the signal.
If selection occurs not through viability but only through differential fecundity, the problem is
more complicated because the it is the number of newborns that reflects the fitness differences among the
groups. Here we should count newborns, which of course were not distinguished in the data you
received. When selection occurs through both viability and fertility effects, well, one must count
everything and analyze adults and newborns separately in each generation (these methods were worked
out by, among others, the legendary Tim Prout and I can point you toward the relevant papers if you’re
interested). Of course, you were given data after some unknown number of generations so you could not
do this even if you had wanted, and so one might argue that separate analyses of female adults and
immatures are warranted at least to approximate what might be the right analysis.
Well, these are advanced issues that are beyond the immediate scope of the assignment but it is
useful to keep them in mind because a knowledge of the theoretical issues would have been imperative in
the design of the data collection for this experiment (indeed, data were collected in every generation
precisely because of the theoretical papers on this issue).
Local adaptation, as we described it, clearly requires a significant interaction between origin and
treatment in this design with the direction of the inequalities following the theory as the exercise
presented it. If indeed the situation described in part a) of the last section obtained, this would suggest
genuine, strong trade-offs in both genetic stocks (i.e. fish from both origins) between fitness in each
environment. That is, adaptation to the home condition seems to have produced a compromise in the
absolute ability to handle the other condition. The situation described in part b) of the exercise’s latter
part relaxes that requirement; in other words, one stock does not encounter this tradeoff but the other one
does (otherwise it would be the better stock in each environment). We might still have local adaptation
however we define it, but without the evidence for trade-offs in adaptation across environments.
Two treatments/factors are not included in this experiment, at least not in these data, and are
generally not included in any field or quasi-field (i.e. artificial ponds, greenhouse environment) study of
local adaptation with which I’m familiar (and I’ll buy lunch for anyone who proves me wrong). First,
experimental populations do not reach any sort of density equilibrium so the potential role of densitydependent selection cannot be evaluated. Obviously this means if the stocks are locally adapted to
different levels of crowding, one will never be able to tell with the design as presented. Second,
individuals from different stocks do not mix in a single environment. That is, the classic design places
each stock in each environment and usually does not allow interactions among individuals from different
stocks in a single environment. More pointedly, individuals from different stocks are never in
competition (here’s that density-dependent thing again). For all we know, individuals from different
stocks might have different competitive abilities to each other and this aspect of potential fitness is not
revealed by the classic design. This is odd, inasmuch as, in nature, gene flow might bring individuals
from different stocks into contact and potential competition with each other and the ultimate genetic
outcome might depend upon this competition. Again, these ideas were not part of the design and not part
of the exercise, but if one wants to think about local adaptation and what we do and do not know about it,
these are issues that one ought to confront.