# MVPA Meanderings

musings on fMRI multivariate pattern analyses

## Tuesday, August 16, 2016

### that's motion? respiration

In the previous post I showed some motion regressors with very regular oscillations. Several of you pointed towards respiration, and I was able today to extract the signal from a respiration belt for a couple of runs. The respiration signal (black line plots) is not perfectly temporally aligned to the movement regressors, but close enough to convince me that respiration is driving the oscillation. We're still looking into various acquisition details for why it is so prominent in this dataset; I am certainly not an MR physicist, but will summarize when we figure something out.

## Friday, August 12, 2016

### that's motion?

While my blogging has unfortunately been sparse lately, I've still been doing lots of fMRI analysis and MVPA! One project I'm currently involved with is just starting to collect high spatial (voxels acquired at 2x2x2 mm) and temporal (TR=800 msec) resolution task fMRI data using a simultaneous multi-slice (SMS) EPI on a Siemens Prisma 3T scanner (details below the fold). We've been looking closely at participant motion and signal quality, and trying various control analyses (button pushes detected in motor areas, task vs. rest, etc.).

UPDATE: This pattern is related to respiration.

Some of the participants have an oscillation in the movement regressors, and I would love to get your impressions of the pattern. Below are two runs (encoding directions AP and PA) of a task for the participant with the most striking oscillation. Plotted are the six columns (translation in blue, rotation in pink) generated by our implementation of the HCP processing pipelines (the Movement_Regressors.txt file, to be precise; MCFLIRT produces a nearly identical set of values). Acquisition frames are along the x-axis, with vertical lines marking 1 minute intervals (these runs are a bit more than 12 minutes long), and short tick marks indicating event onsets (the events are in three blocks).

The overall motion is quite small: less than a mm over each run, well under the 2 mm isotropic voxel size. But the second column (blue below) has a very clear oscillation, that strikes me as too regular to be physiological in origin. Below are the same values again, but just the translation columns, zoomed-in.

This movement is not a simple bug in the preprocessing, but is visible in the raw (converted to NIfTI and defaced, but not motion-corrected, spatially normalized, or anything else) image (click here to see a movie of 08's Pro1 run). It's also in the voxel intensities. The graph below has the same column 2 translation values as the Pro1 graph above, with the average frame-to-frame intensity of a 1900-voxel box-shaped ROI I put in the frontal lobe superimposed in pink. The two curves clearly track pretty well.

I've never seen movement like this in non-SMS EPI datasets, and its regularity makes me suspect that it's related to the acquisition somehow. I'm certainly not a physicist, so very much would appreciate any insights, or if you've encountered similar movement.

The person whose images are shown in this post has the largest and most regular oscillation of any person we've scanned yet (around 8 people); check below the fold for a few more examples, along with details of the acquisition sequence.

UPDATE: This pattern is related to respiration.

Some of the participants have an oscillation in the movement regressors, and I would love to get your impressions of the pattern. Below are two runs (encoding directions AP and PA) of a task for the participant with the most striking oscillation. Plotted are the six columns (translation in blue, rotation in pink) generated by our implementation of the HCP processing pipelines (the Movement_Regressors.txt file, to be precise; MCFLIRT produces a nearly identical set of values). Acquisition frames are along the x-axis, with vertical lines marking 1 minute intervals (these runs are a bit more than 12 minutes long), and short tick marks indicating event onsets (the events are in three blocks).

The overall motion is quite small: less than a mm over each run, well under the 2 mm isotropic voxel size. But the second column (blue below) has a very clear oscillation, that strikes me as too regular to be physiological in origin. Below are the same values again, but just the translation columns, zoomed-in.

This movement is not a simple bug in the preprocessing, but is visible in the raw (converted to NIfTI and defaced, but not motion-corrected, spatially normalized, or anything else) image (click here to see a movie of 08's Pro1 run). It's also in the voxel intensities. The graph below has the same column 2 translation values as the Pro1 graph above, with the average frame-to-frame intensity of a 1900-voxel box-shaped ROI I put in the frontal lobe superimposed in pink. The two curves clearly track pretty well.

I've never seen movement like this in non-SMS EPI datasets, and its regularity makes me suspect that it's related to the acquisition somehow. I'm certainly not a physicist, so very much would appreciate any insights, or if you've encountered similar movement.

The person whose images are shown in this post has the largest and most regular oscillation of any person we've scanned yet (around 8 people); check below the fold for a few more examples, along with details of the acquisition sequence.

## Tuesday, May 24, 2016

### resampling images with afni 3dresample

This is the third post showing how to resample an image: I first covered SPM, then wb_command. afni's 3dresample command is the shortest version yet. I highly suggest you verify that the resampling worked regardless of the method you choose; the best way I know of is simply visually checking landmarks, as described at the end of the SPM post.

The setup is the same as the previous examples:

The command just lists those three files, with the proper flags:

Not being especially linux-savvy (afni does not play nice with Windows, so I run it in NeuroDebian), I sometimes get stuck with path issues when running afni commands. When in doubt, navigate to the directory in which the afni command programs (3dresample, in this case) are located, and execute the commands from that directory, typing./ at the start of the command. You can specify the full paths to images if needed; the example command above assumes 3dresample is on the path and the images are in the directory from which the command is typed. If you're using NeuroDebian, you can add afni to the session's path by typing . /etc/afni/afni.sh at the command prompt before trying any afni commands.

The setup is the same as the previous examples:

- inImage.nii.gz is the image you want to resample (for example, the 1x1x1 mm anatomical image)
- matchImage.nii.gz is the image with the dimensions you want the output image to have - what inImage should be transformed to match (for example, the 3x3x3 mm functional image)
- outImage.nii.gz is the new image that will be written: inImage resampled to match matchImage.

The command just lists those three files, with the proper flags:

```
3dresample -master matchImage.nii.gz -prefix outImage.nii.gz -inset inImage.nii.gz
```

Not being especially linux-savvy (afni does not play nice with Windows, so I run it in NeuroDebian), I sometimes get stuck with path issues when running afni commands. When in doubt, navigate to the directory in which the afni command programs (3dresample, in this case) are located, and execute the commands from that directory, typing./ at the start of the command. You can specify the full paths to images if needed; the example command above assumes 3dresample is on the path and the images are in the directory from which the command is typed. If you're using NeuroDebian, you can add afni to the session's path by typing . /etc/afni/afni.sh at the command prompt before trying any afni commands.

## Friday, May 6, 2016

### "Classification Based Hypothesis Testing in Neuroscience", permuting

My previous post described the below-chance classification part of a recent paper by Jamalabadi et. al; this post will get into the parts on statistical inference and permutation testing.

First, I fully agree with Jamalabadi et. al that MVPA classification accuracy (or CCR, "correct classification rate", as they call it) alone is not sufficient for estimating effect size or establishing significance. As they point out, higher accuracy is better, but it can only be directly compared

The classification accuracy is not totally meaningless, but you need something to compare it to for statistical inference. As Jamalabadi et. al put it (and I've also long advocated), "We propose that MVPA results should be reported in terms of P values, which are estimated using randomization tests."{Aside: I think it's ok to use parametric tests for group-level inference in particular cases and after checking their assumptions, but prefer permutation tests and think they can provide stronger evidence.}

But there's one part of the paper I do not agree with, and that's their discussion of the prevalence of highly non-normal null distributions. The figure at left is Figure 5 from the paper, and are very skewed and non-normal null distributions resulting from classifying simulated datasets in different ways (chance should be 0.5). They show quite a few skewed null distributions from different datasets in the paper, and in the Discussion state that, "For classification with cross-validation in typical life-science data, i.e., small sample size data holding small effects, the distribution of classification rates is neither normal nor binomial."

However, I am accustomed to seeing approximately normal null distributions with MVPA, even in situations with very small effects and sample sizes. For example, below are null distributions (light blue) from eight simulated datasets. Each dataset was created to have 20 people, each with 4 runs of imaging data, each of which has 10 examples of each of 2 classes, and a single 50-voxel ROI. I generated the "voxel" values from a standard normal, with varying amounts of bias added to the examples of one class to allow classification. Classification was with leave-one-run-out cross-validation within each person, then averaging across the runs for the group-level accuracy; 1000 label rearrangements for the permutation test, following a dataset-wise scheme, averaging across subjects like in this demo.

The reddish line in each plot is the accuracy of the true-labeled dataset, which you can see increases from left to right across the simulated datasets, from 0.51 (barely above chance) to 0.83 (well above chance). The permutation test (perm. p) becomes more significant as the accuracy increases, since the true-labeled accuracy shifts to the right of the null distribution.

Note however, that the null distributions are nearly the same and approximately normal for all eight datasets. This is sensible: while the amount of signal in the simulated datasets increases, they all have the same number of examples, participants, classification algorithm (linear SVM, c=1), and cross-validation scheme. The different amounts of signal don't affect the permutation datasets: since the labels were randomized (within each subject and run), all permutation datasets are non-informative, and so produce similar null distributions. The null distributions above are for the group level (with the same dataset-wise permutation relabelings used within each person); I typically see more variability in individual null distributions, but with still approximate normality.

I suspect that the skewed null distributions obtained by Jamalabadi et. al are due either to the way in which the labels were permuted (particularly, that they might not have followed a dataset-wise scheme), or to the way the datasets were generated (which can have a big impact). Regardless, I have never seen as highly-skewed null distributions in real data as those reported by Jamalabadi et. al.

Jamalabadi H, Alizadeh S, SchÃ¶nauer M, Leibold C, & Gais S (2016). Classification based hypothesis testing in neuroscience: Below-chance level classification rates and overlooked statistical properties of linear parametric classifiers. Human brain mapping, 37 (5), 1842-55 PMID: 27015748

First, I fully agree with Jamalabadi et. al that MVPA classification accuracy (or CCR, "correct classification rate", as they call it) alone is not sufficient for estimating effect size or establishing significance. As they point out, higher accuracy is better, but it can only be directly compared

**within a dataset**: the number of examples, classifier, cross-validation scheme, etc. all influence whether or not a particular accuracy is "good". Concretely, it is very shaky to interpret a study as "better" if it classified at 84% while a different dataset in a different study classified at 76%; if, however, you find that changing the scaling of a dataset improves classification (of a single dataset) from 76 to 84%, you'd be more justified in calling it an improvement.The classification accuracy is not totally meaningless, but you need something to compare it to for statistical inference. As Jamalabadi et. al put it (and I've also long advocated), "We propose that MVPA results should be reported in terms of P values, which are estimated using randomization tests."{Aside: I think it's ok to use parametric tests for group-level inference in particular cases and after checking their assumptions, but prefer permutation tests and think they can provide stronger evidence.}

But there's one part of the paper I do not agree with, and that's their discussion of the prevalence of highly non-normal null distributions. The figure at left is Figure 5 from the paper, and are very skewed and non-normal null distributions resulting from classifying simulated datasets in different ways (chance should be 0.5). They show quite a few skewed null distributions from different datasets in the paper, and in the Discussion state that, "For classification with cross-validation in typical life-science data, i.e., small sample size data holding small effects, the distribution of classification rates is neither normal nor binomial."

However, I am accustomed to seeing approximately normal null distributions with MVPA, even in situations with very small effects and sample sizes. For example, below are null distributions (light blue) from eight simulated datasets. Each dataset was created to have 20 people, each with 4 runs of imaging data, each of which has 10 examples of each of 2 classes, and a single 50-voxel ROI. I generated the "voxel" values from a standard normal, with varying amounts of bias added to the examples of one class to allow classification. Classification was with leave-one-run-out cross-validation within each person, then averaging across the runs for the group-level accuracy; 1000 label rearrangements for the permutation test, following a dataset-wise scheme, averaging across subjects like in this demo.

The reddish line in each plot is the accuracy of the true-labeled dataset, which you can see increases from left to right across the simulated datasets, from 0.51 (barely above chance) to 0.83 (well above chance). The permutation test (perm. p) becomes more significant as the accuracy increases, since the true-labeled accuracy shifts to the right of the null distribution.

Note however, that the null distributions are nearly the same and approximately normal for all eight datasets. This is sensible: while the amount of signal in the simulated datasets increases, they all have the same number of examples, participants, classification algorithm (linear SVM, c=1), and cross-validation scheme. The different amounts of signal don't affect the permutation datasets: since the labels were randomized (within each subject and run), all permutation datasets are non-informative, and so produce similar null distributions. The null distributions above are for the group level (with the same dataset-wise permutation relabelings used within each person); I typically see more variability in individual null distributions, but with still approximate normality.

I suspect that the skewed null distributions obtained by Jamalabadi et. al are due either to the way in which the labels were permuted (particularly, that they might not have followed a dataset-wise scheme), or to the way the datasets were generated (which can have a big impact). Regardless, I have never seen as highly-skewed null distributions in real data as those reported by Jamalabadi et. al.

Jamalabadi H, Alizadeh S, SchÃ¶nauer M, Leibold C, & Gais S (2016). Classification based hypothesis testing in neuroscience: Below-chance level classification rates and overlooked statistical properties of linear parametric classifiers. Human brain mapping, 37 (5), 1842-55 PMID: 27015748

## Monday, April 25, 2016

### "Classification Based Hypothesis Testing in Neuroscience"

There's a lot of interesting MVPA methodology in a recent paper by Jamalabadi et. al, with the long (but descriptive) title "Classification Based Hypothesis Testing in Neuroscience: Below-Chance Level Classification Rates and Overlooked Statistical Properties of Linear Parametric Classifiers". I'll focus on the below-chance classification part here, and hopefully get to the permutation testing parts in detail in another post; for a very short version, I have no problem at all with their advice to report p-values and null distributions from permutation tests to evaluate significance, and agree that accuracy alone is not sufficient, but they have some very oddly-shaped null distributions, which make me wonder about their permutation scheme.

Anyway, the below-chance discussion is mostly in the section "Classification Rates Below the Level Expected for Chance" and Figure 3, with proofs in the appendices. Jamalabadi et. al set up a series of artificial datasets, designed to have differing amounts of signal and number of examples. They get many below-chance accuracies when "sample size and estimated effect size is low", which they attribute to "dependence on the subsample means":

This is a toy dataset with two classes (red and blue), 12 examples of each class. The red class is from a normal distribution with mean 0.1, the blue, a normal distribution with mean -0.1. The full dataset (at left) shows a very small difference between the classes: the mean of the the blue class is a bit to the left of the mean of the red class (top row triangles); the line separates the two means.

Following Jamalabadi et. al's Figure 3, I then did a three-fold cross-validation, leaving out four examples each time. One of the folds is shown in the right image above; the four left-out examples in each class are crossed out with black x. The diamonds are the mean of the training set (the eight not-crossed-out examples in each class). The crossed diamonds are the means of the test set (the four crossed-out examples in each class): and they are

This is the "dependence on subsample means": pulling out the test set shifts the means of the remaining examples (training set) in the other direction, making performance worse (in the example above, the training set means are further from zero than the full dataset). This won't matter much if the two classes are very distinct, but can have a strong impact when they're similar (small effect size), like in the example (and many neuroimaging datasets).

Is this an explanation for below-chance classification? Yes, I think it could be. It certainly fits well with my observations that below-chance results tend to occur when power is low, and should not be interpreted as anti-learning, but rather of poor performance. My advice for now remains the same: if you see below-chance classification, troubleshoot and try to boost power, but I think we now have more understanding of how below-chance performance

Jamalabadi H, Alizadeh S, SchÃ¶nauer M, Leibold C, & Gais S (2016). Classification based hypothesis testing in neuroscience: Below-chance level classification rates and overlooked statistical properties of linear parametric classifiers. Human brain mapping, 37 (5), 1842-55 PMID: 27015748

follow the jump for the R code to create the image above

Anyway, the below-chance discussion is mostly in the section "Classification Rates Below the Level Expected for Chance" and Figure 3, with proofs in the appendices. Jamalabadi et. al set up a series of artificial datasets, designed to have differing amounts of signal and number of examples. They get many below-chance accuracies when "sample size and estimated effect size is low", which they attribute to "dependence on the subsample means":

"Thus, if the test mean is a little above the sample mean, the training mean must be a little below and vice versa. If the means of both classes are very similar, the difference of the training means must necessarily have a different sign than the difference of the test means. This effect does not average out across folds, ....."They use Figure 3 to illustrate this dependence in a toy dataset. That figure is really too small to see online, so here's a version I made (R code after the jump if you want to experiment).

This is a toy dataset with two classes (red and blue), 12 examples of each class. The red class is from a normal distribution with mean 0.1, the blue, a normal distribution with mean -0.1. The full dataset (at left) shows a very small difference between the classes: the mean of the the blue class is a bit to the left of the mean of the red class (top row triangles); the line separates the two means.

Following Jamalabadi et. al's Figure 3, I then did a three-fold cross-validation, leaving out four examples each time. One of the folds is shown in the right image above; the four left-out examples in each class are crossed out with black x. The diamonds are the mean of the training set (the eight not-crossed-out examples in each class). The crossed diamonds are the means of the test set (the four crossed-out examples in each class): and they are

**flipped**: the blue mean is on the red side, and the red mean on the blue side. Looking at the position of the examples, all of the examples in the blue test set will be classified wrong, and all but one of the red: accuracy of 1/8, which is well below chance.This is the "dependence on subsample means": pulling out the test set shifts the means of the remaining examples (training set) in the other direction, making performance worse (in the example above, the training set means are further from zero than the full dataset). This won't matter much if the two classes are very distinct, but can have a strong impact when they're similar (small effect size), like in the example (and many neuroimaging datasets).

Is this an explanation for below-chance classification? Yes, I think it could be. It certainly fits well with my observations that below-chance results tend to occur when power is low, and should not be interpreted as anti-learning, but rather of poor performance. My advice for now remains the same: if you see below-chance classification, troubleshoot and try to boost power, but I think we now have more understanding of how below-chance performance

*can*happen.Jamalabadi H, Alizadeh S, SchÃ¶nauer M, Leibold C, & Gais S (2016). Classification based hypothesis testing in neuroscience: Below-chance level classification rates and overlooked statistical properties of linear parametric classifiers. Human brain mapping, 37 (5), 1842-55 PMID: 27015748

follow the jump for the R code to create the image above

## Tuesday, March 15, 2016

### pointer: PRNI 2016 paper submission deadline next week

The paper submission deadline for Pattern Recognition in Neuroimaging (PRNI) 2016 has been extended to 24 March, so be sure to get your manuscript in! For those of you with a psychology-type background, note that papers accepted to PRNI are cite-able, peer-reviewed publications, and will be published by IEEE.

This workshop is a great way to meet people interested in MVPA methods; not just SVMs and fMRI (though that's present), but also MEG, EEG, structural MRI, Bayesian methods, model interpretation, etc, etc. PRNI is in Trento, Italy this year, with a shuttle bus to Geneva, Switzerland for those attending OHBM as well (PRNI is held immediately prior to OHBM).

This workshop is a great way to meet people interested in MVPA methods; not just SVMs and fMRI (though that's present), but also MEG, EEG, structural MRI, Bayesian methods, model interpretation, etc, etc. PRNI is in Trento, Italy this year, with a shuttle bus to Geneva, Switzerland for those attending OHBM as well (PRNI is held immediately prior to OHBM).

## Tuesday, February 23, 2016

### distance metrics: what do we mean by "similar"?

There are many ways of quantifying the distance (aka similarity) between timecourses (or any numerical vector), and distance metrics sometimes vary quite a bit in which properties they use to quantify similarity. As usual, it's not that one metric is "better" than another, it's that you need to think about what constitutes "similar" and "different" for a particular project, and pick a metric that captures those characteristics.

I find it easiest to understand the properties of different metrics by seeing how they sort simple timecourses. This example is adapted from Chapter 8 (Figure 8.1 and Table 8.1) of H. Charles Romesburg's Cluster Analysis for Researchers. This is a highly readable book, and I highly recommend it as a reference for distance metrics (he covers many more than I do here), clustering, tree methods, etc. The computer program sections are dated, but such a minor part of the text that it's not a problem.

Here are the examples we'll be measuring the distance between (similarity of). To make it concrete, you could imagine these are the timecourses of five voxels, each measured at four timepoints. The first four timeseries are the examples from Romesburg's Figure 8.1. Timeseries 1 (black line) is the "baseline"; 2 (blue line) is the same shape as 1, but shifted up 15 units; 3 (red line) is baseline * 2; and 4 (green line) is the mirror image of the baseline (line 1, reflected across y = 20). I added line 5 (grey), to have a similar mean y as baseline, but closer in shape to line 4.

Here are the values for the same five lines:

Euclidean distance pretty much sorts the timecourses by their mean y: 1 is most similar (smallest distance) to 5, next-closest to 2, then 4, then 3 (read these distances from the first column in the table at right).

Thinking of these as fMRI timecourses, Euclidean distance pretty much ignores the "shape" of the lines (voxels): 1 and 5 are closest, even though voxel 1 has "more BOLD" at timepoint 2 and voxel 5 has "less BOLD" at timepoint 2. Likewise, voxel 1 is closer to voxel 4 (its mirror image) than to voxel 3, though I think most people would consider timecourses 1 and 3 more "similar" than 1 and 4.

Here's the tree and table for the same five timecourses, using 1-Pearson correlation as the distance metric. Now, lines 2 and 3 are considered exactly the same (correlation 1, distance 0) as line 1; in Romesburg's phrasing, Pearson correlation is "wholly insensitive" to additive and proportional translations. Consistently, lines 4 and 5 (the "downward pointing" shapes) are grouped together, while line 4 (the mirror image) is maximally dissimilar to line 1.

So, Pearson correlation may be suitable if you're more interested in shape than magnitude. In the fMRI context, we could say that correlation considers timecourses that go up and down together as similar, ignoring overall BOLD. If you care that one voxel's timecourse has higher BOLD than another (here, like 2 or 3 being higher than 1), you don't want to use Pearson correlation.

The

Euclidean distance and Pearson correlation: it ignores additive translations, but is sensitive to proportional translations.

As seen here, like correlation, the coefficient of shape difference considers lines 1 and 2 identical (maximally similar), but unlike correlation, line 3 is

I didn't find the coefficient in a built-in R function, but its equation (8.3 in Romesburg) is very simple to implement, as in the code below.

I've tried using the coefficient of shape difference in a few analyses, as its property of being sensitive to proportional translations more closely matches my intuitive understanding of "similar" timecourses. I haven't used it in any published analyses yet, as Pearson correlation has done better. But it certainly seems worth considering.

These three ways of measuring the similarity (distance) between timecourses are certainly not the only metrics, but I hope it's clear from just these three that the metric matters; they're not interchangeable.

I find it easiest to understand the properties of different metrics by seeing how they sort simple timecourses. This example is adapted from Chapter 8 (Figure 8.1 and Table 8.1) of H. Charles Romesburg's Cluster Analysis for Researchers. This is a highly readable book, and I highly recommend it as a reference for distance metrics (he covers many more than I do here), clustering, tree methods, etc. The computer program sections are dated, but such a minor part of the text that it's not a problem.

Here are the examples we'll be measuring the distance between (similarity of). To make it concrete, you could imagine these are the timecourses of five voxels, each measured at four timepoints. The first four timeseries are the examples from Romesburg's Figure 8.1. Timeseries 1 (black line) is the "baseline"; 2 (blue line) is the same shape as 1, but shifted up 15 units; 3 (red line) is baseline * 2; and 4 (green line) is the mirror image of the baseline (line 1, reflected across y = 20). I added line 5 (grey), to have a similar mean y as baseline, but closer in shape to line 4.

Here are the values for the same five lines:

```
data1 <- c(20,40,25,30);
data2 <- c(35,55,40,45);
data3 <- c(40,80,50,60);
data4 <- c(20, 0,15,10); # first four from Romesburg Table 8.1
data5 <- c(30,20,26,20); # and another line
```

### Which lines are most similar? Three metrics.

If we measure with**Euclidean distance**, lines 1 and 5 are closest. The little tree at right is built from the distance matrix printed below, using the R code that follows. I used R's built-in function to calculate the Euclidean distance between each pair of lines, putting the results into tbl in the format needed by hclust.Euclidean distance pretty much sorts the timecourses by their mean y: 1 is most similar (smallest distance) to 5, next-closest to 2, then 4, then 3 (read these distances from the first column in the table at right).

Thinking of these as fMRI timecourses, Euclidean distance pretty much ignores the "shape" of the lines (voxels): 1 and 5 are closest, even though voxel 1 has "more BOLD" at timepoint 2 and voxel 5 has "less BOLD" at timepoint 2. Likewise, voxel 1 is closer to voxel 4 (its mirror image) than to voxel 3, though I think most people would consider timecourses 1 and 3 more "similar" than 1 and 4.

```
tbl <- array(NA, c(5,5));
tbl[1,1] <- dist(rbind(data1, data1), method='euclidean');
tbl[2,1] <- dist(rbind(data1, data2), method='euclidean');
.... the other table cells ....
tbl[5,5] <- dist(rbind(data5, data5), method='euclidean');
plot(hclust(as.dist(tbl)), xlab="", ylab="", sub="", main="euclidean distance"); # simple tree
```

**Pearson correlation**sorts the timecourses very differently than Euclidean distance.Here's the tree and table for the same five timecourses, using 1-Pearson correlation as the distance metric. Now, lines 2 and 3 are considered exactly the same (correlation 1, distance 0) as line 1; in Romesburg's phrasing, Pearson correlation is "wholly insensitive" to additive and proportional translations. Consistently, lines 4 and 5 (the "downward pointing" shapes) are grouped together, while line 4 (the mirror image) is maximally dissimilar to line 1.

So, Pearson correlation may be suitable if you're more interested in shape than magnitude. In the fMRI context, we could say that correlation considers timecourses that go up and down together as similar, ignoring overall BOLD. If you care that one voxel's timecourse has higher BOLD than another (here, like 2 or 3 being higher than 1), you don't want to use Pearson correlation.

```
tbl <- array(NA, c(5,5));
tbl[1,1] <- cor(data1, data1); # method="pearson" is default
tbl[2,1] <- cor(data1, data2);
tbl[3,1] <- cor(data1, data3);
.... the other table cells ....
tbl[5,5] <- cor(data5, data5);
plot(hclust(as.dist(1-tbl)), xlab="", ylab="", sub="", main="1 - Pearson correlation");
```

The

**coefficient of shape difference**metric (page 99 in Romesburg) mixes a bit of the properties ofEuclidean distance and Pearson correlation: it ignores additive translations, but is sensitive to proportional translations.

As seen here, like correlation, the coefficient of shape difference considers lines 1 and 2 identical (maximally similar), but unlike correlation, line 3 is

*not*considered identical to line 1. Like Euclidean distance, the coefficient of shape difference considers lines 3 and 4 farther apart than any other pair of lines (correlation listed 1, 2, and 3 as all equally far from line 4).I didn't find the coefficient in a built-in R function, but its equation (8.3 in Romesburg) is very simple to implement, as in the code below.

I've tried using the coefficient of shape difference in a few analyses, as its property of being sensitive to proportional translations more closely matches my intuitive understanding of "similar" timecourses. I haven't used it in any published analyses yet, as Pearson correlation has done better. But it certainly seems worth considering.

```
# coefficient of shape difference, page 99 of Romesburg
get.dist <- function(dataA, dataB) {
if (length(dataA) != length(dataB)) { stop("length(dataA) != length(dataB)"); }
n <- length(dataA); # number of dimensions
d <- sqrt((n/(n-1))*(sum((dataA-dataB)^2)/n - ((1/(n^2))*(sum(dataA) - sum(dataB))^2)));
return(d);
}
tbl <- array(NA, c(5,5)); # tbl <- array(NA, c(4,4)); #
tbl[1,1] <- get.dist(data1, data1);
.... the other table cells ....
tbl[5,5] <- get.dist(data5, data5);
plot(hclust(as.dist(tbl)), xlab="", ylab="", sub="", main="coeff of shape diff");
```

These three ways of measuring the similarity (distance) between timecourses are certainly not the only metrics, but I hope it's clear from just these three that the metric matters; they're not interchangeable.

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