> Our concern with this approach is related with using the contrast images at
> the second level. We have realized that if we use a certain measure A, and
> subtract a control task B from it, we end up with a measure that usually
> correlates positively with A, but *correlates negatively* with B. Therefore,
> when we use the contrast resulting from a subtraction of parameter estimates
> at the first level, the values at each voxel are negatively correlated with
> our control measure. We would like, however, to be able to use a measure
> that is *independent* of B.
Under the null, the [A-B] constrast is uncorrelated with your
individual variable; A and B in isolation are also uncorrelated, if
they are centered. This can be shown agebraically. What you mean is
that if the null is rejected at the regression of the individual
variable on the contrast image, then you do not know if you have a
positive association with A or a negative association with B.
> Ideally, we would like to be able to look for the relationship of brain
> response A to certain behavior while *regressing out* the brain responses to
> B, and not subtracting those responses. It seems that only by doing this, we
> would be able to effectively remove the influence of measure B. Would it be
> possible to do this in SPM?
Treating A and B quantitatively, as you are proposing to do here, is
difficult due to the non-quantitative nature of the BOLD-EPI signal.
In other words, you cannot view A and B as separate measures of
activity; only the difference is valid. Furthermore, it breaks the SPM
approach (because the regressor now including B differs at each voxel
-- so no, you can't do it with SPM). You could adjust for B, however,
in a ROI-averaged signal where the ROI is selected by a contrast
orthogonal to the factor with levels A B.
Apart from the limitations of BOLD-EPI, the issue you are raising
bears some relation to interventional studies, where for example you
test the effect of therapy (the 'control variable') on a pre- and
post-therapy measurement (A and B). In this case, it is indeed common
to adjust for pre- instead of regressing on [post - pre]. The reason
is that the contrast [post - pre] is like having pre in the regression
model with a fixed coefficient of one; if you adjust, instead, you
estimate this coefficient from the data, i.e. the model is more
general. The issue, however, is far from clearcut; much depends on the
existence of a causal association between pre levels and your 'control
variable'. If this is the case, then contrary to your reasoning you do
introduce bias in the estimate of the control variable. See basic
background in S. Greenland, J. Pearl, J. M. Robins 1999, ‘Causal
diagrams for epidemiologic research’. Epidemiology, 1:37-48, and more
M. M. Glymour, J. Weuve, L. F. Berkman, I. Kawachi, J. M. Robins 2005,
When is baseline adjustment useful in analyses of change? An example
with education and cognitive change’. American Journal of
A discussion of the generality of adjusting vs. regressing on the
contrast is in the book by Hill & Gelman, Data Analysis Using
Regression and Multilevel/Hierarchical Models. Cambridge (UK):
Cambridge University Press
The algebra of individual testing at the 2nd level is in
Dept. of Psychiatry
University of Ulm, Germany
> I'm writing to ask if this problem has been considered before, and whether
> you have any suggestion about how we can deal with it?
> I'd be very grateful for any thoughts that you have about these issues.
> With many thanks and kind regards,
> Lucia Garrido