[R-sig-ME] mcmcpvalue and contrasts
HStevens at MUOhio.edu
Wed Feb 27 18:42:38 CET 2008
On Feb 26, 2008, at 2:21 PM, Steven McKinney wrote:
>> -----Original Message-----
>> From: Ken Beath [mailto:kjbeath at kagi.com]
>> Sent: Mon 2/25/2008 8:46 PM
>> To: Steven McKinney
>> Cc: Hank Stevens; Help Mixed Models
>> Subject: Re: [R-sig-ME] mcmcpvalue and contrasts
>> On 26/02/2008, at 1:22 PM, Steven McKinney wrote:
>>> Hi Hank,
>>>> -----Original Message-----
>>>> From: r-sig-mixed-models-bounces at r-project.org on behalf of Ken
>>>> Sent: Mon 2/25/2008 4:05 PM
>>>> To: Hank Stevens
>>>> Cc: Help Mixed Models
>>>> Subject: Re: [R-sig-ME] mcmcpvalue and contrasts
>>>> On 26/02/2008, at 9:42 AM, Hank Stevens wrote:
>>>>> Hi Folks,
>>>>> I wanted to double check that my intuition makes sense.
>>>>> Examples of mcmcpvalue that I have seen use treatment "contrast"
>>>>> However, in more complex designs, testing overall effects of a
>>>>> might be better done with other contrasts, such as sum or Helmert
>>>>> My Contention:
>>>>> Different contrasts test different hypothesis, and therefore
>>>>> result in
>>>>> different P-values. This consequence of contrasts differs from
>>>>> analysis of variance, as in anova( lm(Y ~ X1*X2) ).
>>>>> *** This is right, isn't it? ***
>>>> The main problem is testing for a main effect in the presence of
>>>> interaction. While it looks like it gives sensible results in some
>>>> cases like balanced ANOVA, they really aren't sensible and the
>>>> of parameterisation in other cases makes that clear.
>>>> The difference for the interaction is probably just sampling
>>>> variation, increasing samples fixes this.
>>> Ken is correct - testing some of the main effect terms resulting
>>> different parameterizations due to the differing contrast structures
>>> will yield different results (though they in general will be
>>> meaningless if the corresponding interaction term is in the model
>>> and you do not have a balanced orthogonal design).
>> Even with orthogonal designs there is still a problem with
>> interpretation. If we have a model with A*B and the interaction and B
>> are significant, then it seems that the conclusion about B is limited
>> to the choice of A in the experiment. An assumption that the effect
>> of B will be the same with a different set of A seems rather risky,
>> although it seems to be what the FDA expect for multi-centre trials.
>> If there is some need to generalise then a model allowing for a
>> random effect for B seems more sensible.
> Yes, in general if an interaction A*B is significant, then both
> main effects that comprise the interaction are 'significant' in that
> they are the variables that define the significant interaction. The
> interaction is significant because the relationship between the
> reponse and one of the main effect terms depends on the level of the
> other main effect term, so it is important that both main effects
> remain in the model to allow the model to properly characterize this
> complex relationship among the three variables involved.
> Deleting either main effect from a model containing the interaction is
> rarely advisable as doing so can yield biased estimates of the
> interaction terms. If the interaction term is significant, no more
> testing need be done - both the main effects that comprise the
> interaction are important and necessary. Testing the main effects
> that comprise a significant interaction using models that contain the
> interaction seldom makes sense.
I have found, however, that it is often, yea, even more often, the
case that one factor, A, has a large independent effect, and that
another factor, B, moderates the effect of A to a small, albeit
detectable, degree. In these cases, it makes biological sense to
discuss the "independent" effect of A. Whether one cloaks this in an
"average" effect of A, or states that the effect of A is "at least b0,
and as high as b0+b1, given some value of B." I understand the
caution you express above -- I just did't want to see the baby go
along with the bath water.
More importantly, My own ignorance typically leaves me uncertain
regarding the best approaches for estimating the independent
contributions of A, B, and A:B, and inferring statistical significance
using mcmcpvalue. Using dummy coding (treatment 'contrasts') is
frequently a useful approach for me with very simple models (e.g. A
and B, each with two levels, plus only one random effect). However,
my informal trial-and-error suggests that Helmert contrasts, and to a
lesser extent sum-to-zero contrasts, provide more stable (and maybe
reliable) inference when trying to test whether factors and their
interactions have detectable effects under various selected models.
For instance, given nested models
m3 <- lmer(y ~ (A + B + C)^3 + (1|D) )
m2 <- lmer(y ~ (A + B + C)^2 + (1|D) )
m1 <- lmer(y ~ A + B + C + (1|D) )
Helmert contrasts seem to more precisely estimate the same beta's and
the same P values in mcmcpvalue than sum contrasts, and these are both
less variable across models than treatment contrasts. Perhaps this is
a function of my particular selection of data sets (see previous
posts), but I didn't think so, based on the different interpretations
of the different (non)orthogonal contrasts.
> The second issue you raise involves extrapolating beyond the range of
> the available data. Conclusions about A and B are indeed limited to
> the range of values covered by variables A and B. An assumption that
> the effect of B will be the same with a different set of A is indeed
> rather risky. Only if one can soundly argue that the set of
> institutions in a multicentre trial truly reflects the full range of
> populations that will be offered the treatment under study can one
> make such generalizations.
Dr. Hank Stevens, Assoicate Professor
338 Pearson Hall
Oxford, OH 45056
Office: (513) 529-4206
Lab: (513) 529-4262
FAX: (513) 529-4243
"If the stars should appear one night in a thousand years, how would men
believe and adore." -Ralph Waldo Emerson, writer and philosopher
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