Monday, April 13, 2015

format conversion: 4dfp to NIfTI, plus setting handedness and headers

This post is a tutorial explaining how to convert fMRI datasets from 4dfp to NIfTI format. Most people not at Washington University in St Louis probably won't encounter a 4dfp dataset, since the format isn't in wide use. But much of the post isn't 4dfp-specific, and goes over ways to check (and correct) the orientation and handedness of voxel arrays. The general steps and alignment tests here should apply, regardless of which image format is being converted to NIfTI.

Converting images between formats (and software programs) is relatively easy ... ensuring that the orientation is set properly in the converted images is sometimes not, and often irritating. But it is very, very worth your time to make sure that the initial image conversion is done properly; sorting out orientation at the end of an analysis is much harder than doing it right from the start.

To understand the issues, remember that NIfTI (and 4dfp, and most other image formats) have two types of information: the 3d or 4d array of voxel values, and how to interpret those values (such as how to align the voxel array to anatomical space, the size of the voxels in mm, etc.), which is stored in a header. This post gives has more background information, as does this one. The NIfTI file specification allows several different ways of specifying alignment, and both left and right-handed voxel arrays. Flexibility is good, I guess, but can lead to great confusion, because different programs have different strategies for interpreting the header fields. Thus, the exact same NIfTI image can look different (e.g. left/right flipped, shifted off center) when opened in different programs. That's what we want to avoid: we want to create NIfTI images that will be read with proper alignment into most programs.

Step 1:  Read the image into R as a plain voxel array

I use the R4dfp R package to read 4dfp images into R, and the oro.nifti package to (read or) write NIfTI images out of R. The R4dfp package won't run in Windows, so needs to be run on a linux box, mac, or within NeuroDebian (oro.nifti runs on all platforms).

 in.4dfp <- R4dfp.Load(paste0(in.path, img.name));  
 vol <- in.4dfp[,,,];  

The 4dfp image fname at location in.path is read into R with the first command, and the voxel matrix extracted with the second. You can check properties of the 4dfp image by checking its fields, such as in.4dfp$dims and in.4dfp$center. The dimension of the extracted voxel array should match the input 4dfp fields (in.4dfp$dims == dim(vol)).

Step 2:  Determine the handedness of the input image and its alignment

Now, look at the extracted voxel array: how is it orientated? My strategy is to open the original image in the program whose display I consider to be the ground truth, then ensure the matrix in R matches that orientation. For 4dfp images, the "ground truth" program is fidl; often it's the program which created the input image. I then look at the original image and find a slice with a clear asymmetry, and display that slice in R with image.



Here's slice k=23 (green arrow) of the first timepoint in the image (blue arrow). The greyscale image is the view in fidl which we consider true: the left anterior structure (white arrow) is "pointy". The R code image(vol[,,23,1])) displays this same slice, using hot colors (bottom right). We can see that it's the correct slice (I truncated the side a bit in the screen shot), but the "pointy" section is at the bottom right of the image instead of the top left. So, the voxel array needs flipped left/right and anterior/posterior.

Step 3:  Convert and flip the array as needed

This doFlip R function reorders the voxel array. It takes and returns a 3d array, so should be run on each timepoint individually. This takes a minute or so to run, but I haven't bothered speeding it up, since it only needs to be run once per input image. If you have a faster version, please share!

 # flip the data matrix in the specified axis direction(s). Be very careful!!!  
 doFlip <- function(inArray, antPost=FALSE, leftRight=FALSE) {  
   if (antPost == FALSE & leftRight == FALSE) { stop("no flips specified"); }  
   if (length(dim(inArray)) != 3) { stop(print("not three dimensions in the array")); }  
   outvol <- array(NA, dim(inArray));  
   IMAX <- dim(inArray)[1];  
   JMAX <- dim(inArray)[2];  
   KMAX <- dim(inArray)[3];  
   for (k in 1:KMAX) {  
     for (j in 1:JMAX) { # i <- 1; j <- 1; k <- 1;  
       for (i in 1:IMAX) {  
         if (antPost == TRUE & leftRight == FALSE) { outvol[i,j,k] <- inArray[i,(JMAX-j+1), k]; }  
         if (antPost == TRUE & leftRight == TRUE) { outvol[i,j,k] <- inArray[(IMAX-i+1),(JMAX-j+1), k]; }  
         if (antPost == FALSE & leftRight == TRUE) { outvol[i,j,k] <- inArray[(IMAX-i+1), j, k]; }  
       }  
     }  
   }  
   return(outvol);  
 }  
  # put the array to right-handed coordinate system, timepoint-by-timepoint.  
  outvox <- array(NA, dim(vol));  
  for (sl in 1:dim(vol)[4]) { outvox[,,,sl] <- doFlip(vol[,,,sl], TRUE, TRUE); }  
  image(outvox[,,23,1])  

The last three code call the function  (TRUE, TRUE specifies flipping both left-right and anterior-posterior), putting the flipped timepoint images into the new array outvox. Now, when we look at the same slice and timepoint with the image command (image(outvox[,,23,1]))), it is orientated correctly.

Step 4:  Write out as a NIfTI image, confirming header information

A 3 or 4d array can be written out as a NIfTI image without specifying the header information (e.g. with writeNIfTI(nifti(outvox), fname), which uses the oro.nifti defaults). Such a "minimal header" image can be read in and out of R just fine, but will almost certainly not be displayed properly when used as an overlay image in standard programs (e.g., on a template anatomy in MRIcroN) - it will probably be out of alignment. The values in the NIfTI header fields are interpreted by programs like MRIcroN and the Workbench to ensure correct registration.

Some of the NIfTI header fields are still mysterious to me, so I usually work out the correct values for a particular dataset iteratively: writing a NIfTI with my best guess for the correct values, then checking the registration, then adjusting header fields if needed.

  out.nii <- nifti(outvox, datatype=64, dim=dim(outvox), srow_x=c(3,0,0,in.4dfp$center[1]),   
      srow_y=c(0,3,0,in.4dfp$center[2]), srow_z=c(0,0,3,in.4dfp$center[3]))   
  out.nii@sform_code <- 1    
  out.nii@xyzt_units <- 2; # for voxels in mm    
  pixdim(out.nii)[1:8] <- c(1, 3,3,3, dim(outvox)[4], 1,1,1);   
   # 1st slot is qfactor, then mm, then size of 4th dimension.   
  writeNIfTI(out.nii, paste0(out.path, img.name))    

These lines of code write out a 4d NIfTI with header values for my example image. The input image has 3x3x3 mm voxels, which is directly entered in the code, and the origin is read out of the input fields (you can also type the numbers in directly, such as srow_x=c(3,0,0,72.3)). The image below shows how to confirm that the output NIfTI image is orientated properly: the value of the voxel under the crosshairs is the same (blue arrows) in the original 4dfp image in fidl, the NIfTI in R, and the NIfTI in MRIcroN. The red arrows point out that the voxel's i,j,k coordinates are the same in MRIcroN and R, and the left-right flipping matches (yellow arrow).



Here's another example of what a correctly-aligned file looks like: the NIfTI output image is displayed here as an overlay on a template anatomy in MRIcroN (overlay is red) and the Workbench (overlay is yellow). Note that the voxel value is correct (blue), and that the voxel's x,y,z coordinates (purple) match between the two programs. If you look closely, the voxel's i,j,k coordinates (blue) are 19,4,23 in MRIcroN (like they were in R), but 18,3,22 in the Workbench. This is ok: Workbench starts counting from 0, R and MRIcroN from 1.



concluding remarks

It's straightforward to combine the R code snippets above into loops that convert an entire dataset. My strategy is usually to step through the first image carefully - like in this post - then convert the images for the rest of the runs and participants in a loop (i.e., everyone with the same scanning parameters). I'll then open several other images, confirming they are aligned properly.

This last image is a concrete example of what you don't want to see: the functional data (colored overlay) is offset from the anatomical template (greyscale). Don't panic if you see this: dive back into the headers.

Friday, April 3, 2015

below-chance classification accuracy: meaningful here?

Below-chance accuracy ... always exciting. It showed up today in an interesting way in a set of control analyses. For framing, this is a bit of the working memory task data from the HCP: 0-back and 2-back task blocks, using pictures of faces or places as the stimuli. This gives four examples (volumetric parameter estimate images) per person: 0-back with faces, 0-back with places, 2-back with faces, and 2-back with places.

The classification shown here was with linear SVM, two classes (all balanced, so chance is 0.5), with leave-16-subjects-out cross-validation. The cross-validation is a bit unusual since we're aiming for generalizability across people: I trained the classifiers on a pair of stimuli in the training people, then tested on a different pair of stimuli in the testing people. For example, one cross-validation fold is training on 0-back vs 2-back face in 144 people, then testing 0-back vs 2-back place with the 16 left-out people.

Anyway, a ROI-based classification analysis was performed, on 6 anatomic clusters (C1:C6), which are along the x-axis in the graphs. The left side graph shows a positive control-type analysis: as we expected, face vs. place is classified extremely well with these ROIs, but 0-back vs. 2-back is classified at chance. The right side graph shows some non-sensical, negative control-type analyses, all of which we expected to classify around chance. These are nonsense because we're training and testing on different classifications: for example, training a classifier to distinguish face vs place, then testing with all face stimuli, some of which were from 0-back blocks, others of which were from 2-back blocks.


The striking pattern is that the blue and green lines are quite far below chance, particularly in clusters C1 and C2, which classified face vs place nearly perfectly (ie in the left-side graph).

These ROIs classify face vs place very well. When trained on face vs place, but tested with 0-back vs. 2-back (red and purple lines), they classified basically at chance. This makes sense, because the classifiers learned meaningful ways to distinguish face and place during training, but then were tested with all face or all place stimuli, which they presumably would have classified according to picture type, not n-back. This gives a confusion matrix like the one shown here: all face test examples properly classified as face, for 10/20 = 0.5 accuracy.

Now, the classifiers did not learn to classify 0-back vs 2-back in these ROIs (left-side graph above). To get the observed below-chance accuracies, the confusion matrices would need to be something like this. Why? It is sort of plausible that the classifier could "know" that the place test examples are not face, and so split them equally between the two classes. But if the classifier properly classifies all the 2-back face examples here (as needed to get the below-chance accuracy), why wasn't 0-back vs 2-back properly classified before?

I'll keep looking at this, and save some of the actual confusion matrices to see how exactly the below-chance accuracies are being generated. It's not quite clear to me yet, but the striking pattern in the below-chance here makes me think that they actually might carry some meaning in this case, and perhaps give some more general insights. Any thoughts?

Tuesday, March 24, 2015

some thoughts on "Generation and Evaluation of a Cortical Area Parcellation from Resting-State Correlations"

Lately I've been working a bit with the brain parcellation map described in Gordon, et al. (2014), "Generation and Evaluation of a Cortical Area Parcellation from Resting-State Correlations" (citation below), which is available from the authors (thanks!) in both surface and volumetric formats.

As the title of the paper states, their brain parcellation was derived from resting state functional connectivity analyses. Briefly, the paper describes defining a set of ROIs ("parcels") which divide the cortical surface into meaningful (structurally and functionally) units. The parcel boundaries were defined from functional connectivity analyses, following the (reasonable) assumption that functional connectivity statistics should be homogenous within a parcel, but shift abruptly at parcel boundaries.

This is not the first functional connectivity-derived brain parcellation (Table 1 of the paper lists others), but I think is probably the most methodologically rigorous to date. I like that they used two datasets, each with more than 100 people, and serious quality control checks (motion, etc). I also like their reliability/stability/validity analyses: both between the two datasets, in individuals, and against the most robust and best understood atlases (including cytoarchitechtonic).

We'd like to use the parcellation for defining ROIs, particularly for frontal and parietal areas that aren't definitively divided in existing atlases. Gordon et al. did their analyses on the surface, but provide both surface (CIFTI) and volumetric (NIfTI) versions of the parcellation.

Here's an image I made (using a version of my knitr plotting code) showing a few slices the volumetric parcels (plotted on a conte MNI anatomy I resampled to 2x2x2 mm voxels to match the parcellation's resolution). As is apparent, while in volumetric space, the parcels closely follow the cortical surface (grey matter ribbon).

I see the logic of constraining analyses to the surface, particularly when fMRI images are acquired with high-resolution imaging and then subjected to precise, surface-optimized preprocessing (such as in the HCP). But I'm less convinced these narrow ROIs are advantageous for datasets collected with larger voxels (say 3x3x3 mm or larger) and "standard" preprocessing (such as SPM and spatial normalization).

For example, here are a few slices showing some of the validated ROIs from my recent paper overlayed on a few greyscale slices from the Gordon et al. parcellation. My dataset was acquired with 4x4x4 mm voxels, and all preprocessing was volumetric. The red ROI in the image at left was defined using a volumetric searchlight analysis, and, unsurprisingly, is rather "blobby:" it's not constrained to the cortical ribbon. The red ROI contains 416 voxels, of which 181 (.43) are in one of the parcels. Does that mean the 235 non-parcel voxels are uninformative? No. With 4x4x4 mm voxels, typical amounts of movement, and preprocessing which included spatial normalization, some of the BOLD, even if it all actually came from the grey matter, will appear to come from outside the cortical ribbon.

To summarize, my take is that this parcellation is the result of a methodological tour de force and worth careful consideration, especially for a high-resolution dataset preprocessed with surface analysis in mind (e.g. with freesurfer), even if doing a volumetric analysis. It may be less suitable for datasets with larger voxels and more standard preprocessing.


ResearchBlogging.orgGordon EM, Laumann TO, Adeyemo B, Huckins JF, Kelley WM, & Petersen SE (2014). Generation and Evaluation of a Cortical Area Parcellation from Resting-State Correlations. Cerebral cortex. PMID: 25316338 doi:10.1093/cercor/bhu239

Tuesday, February 17, 2015

research blogging: concatenating vs. averaging timepoints

A little bit of the (nicely described) methods in Shen et al. 2014 ("Decoding the individual finger movements ..." citation below) caught my eye: they report better results when concatenating the images from adjacent time points instead of averaging (or analyzing each independently). The study was straightforward: classifying which finger (or thumb) did a button press. They got good accuracies classifying single trials, with both searchlights and anatomical ROIs. There's a lot of nice methodological detail, including how they defined the ROIs in individual participants, and enough description of the permutation testing to tell that they followed what I'd call a dataset-wise scheme (nice to see!).

But what I want to highlight here is a pretty minor part of the paper: during preliminary analyses they classified the button presses in individual images (i.e., single timepoints; the image acquired during 1 TR), the average of two adjacent images (e.g., averaging the images collected 3 and 4 TR after a button press), and by concatenating adjacent images (e.g., concatenating the images collected 3 and 4 TR after the button press), and found the best results for concatenation (they don't specify how much better).

Concretely, concatenation sends more voxels to the classifier each time: if a ROI has 100 voxels, concatenating two adjacent images means that each example has 200 voxels (the 100 ROI voxels at timepoint 1 and the 100 ROI voxels at timepoint 2). The classifier doesn't "know" that this is actually 100 voxels at two timepoints; it "sees" 200 unique voxels. Shen et al.used linear SVM (c=1), which generally handles large numbers of voxels well; doubling ROI sizes might hurt the performance of other classifiers.

I haven't tried concatenating timepoints; my usual procedure is averaging (or fitting a HRF-type model). But I know others have also had success with concatenation; feel free to comment if you have any experience (good or bad).


ResearchBlogging.orgShen, G., Zhang, J., Wang, M., Lei, D., Yang, G., Zhang, S., & Du, X. (2014). Decoding the individual finger movements from single-trial functional magnetic resonance imaging recordings of human brain activity European Journal of Neuroscience, 39 (12), 2071-2082 DOI: 10.1111/ejn.12547

Saturday, February 14, 2015

hyperacuity with MVPA: a verdict yet?

A few years ago a debate started about whether MVPA hyperacuity is possible: can we pick up signals from sources smaller than an individual voxel? This topic popped up for me again recently, so this post organizes my notes, gives some impressions, and points out some of the key papers.

beginnings: V1 and grating orientations

In 2005 Kamitani & Tong and Haynes & Rees reported being able to use MVPA methods with fMRI data to detect the orientation of gratings in V1. The anatomy and function of early visual areas is better understood than most parts of the brain; we know that they are organized into columns, each sensitive to particular visual attributes. In V1, the orientation columns are known to be much smaller than (typical) fMRI voxels, so how could classification be possible?

Multiple groups, including Kamitani & Tong in their 2005 paper, suggest that this "hyperacuity" could be due to a voxel-level bias in the underlying architecture, whether in the distribution of orientation columns, the vasculature, or some combination of the two. The idea here is that, since columns are not perfectly evenly spatially distributed, each voxel will end up with more columns of one orientation than another, and this subtle population-level bias  is what's being detected in the MVPA.

does degrading the signal reduce hyperacuity?

From the beginning, the idea that hyperacuity was behind the detection of orientation was met with both excitement and skepticism. In 2010 Hans op de Beeck wrote a NeuroImage Comments and Controversy article which kicked off a series of papers trying to confirm (or not) hyperacuity by means of degrading the fMRI images. The logic is straightforward: if subtle biases within individual voxels are making the classification possible, degrading the images (blurring, adding noise, filtering), should dramatically reduce the classification accuracy.

op de Beeck (2010) smoothed images with information at varying spatial scales at different FWHM to change their signal, interpreting the results as suggesting that the apparent hyperacuity might actually be due to larger-scale patterns (spanning multiple voxels). Objections to this technique were raised, however, partly because smoothing's affect on information content is complex and difficult to interpret. Swisher et al. (2010) used spatial filters, rather than smoothing, to degrade the signal in very high-resolution images, and found that small (< 1 mm) scale information was present, and critical for classification accuracy. But, the presence of small-scale signal in high-resolution images doesn't preclude the presence of larger (> 2 mm) scale information; indeed, larger-scale information was also found by Swisher et al. (2010). Filtering was also used by Freeman et al. (2011), who identified larger ("coarser") scale information about orientation in V1. Alink et al. (2013) also used filtering, along with more complex stimuli, finding information in a range of scales, but also cautioning that the numerous interactions and complications mean that filtering is not a perfect approach.

spiraling around

Recently, a set of studies have tried another approach: changing the stimuli (such as to spirals) to try to avoid potential confounds related to the visual properties of the stimuli. These debates (e.g., Freeman et al. 2013, Carlson 2014)  get too much into details of visual processing for me to summarize here, but a new set of Comments and Controversy NeuroImage articles (Carlson & Wardle, Clifford & Mannion 2015) suggests that using spiral stimuli won't be definitive, either.

my musings, and does this imply anything about MVPA?

Overall, I'm landing in the "bigger patterns, not hyperacuity" camp. I find the demonstrations of larger-scale patterns convincing, and a more plausible explanation of the signal, at least for human fMRI with ~ 3 mm voxels; it strikes me as equally reasonable that very small-scale patterns could dominate for high-resolution scanning in anesthetized animals (e.g., Swisher et al. 2010).

But do these debates imply anything for the usefulness of MVPA as a whole? Carlson and Wardle (2015) suggest that it does, pointing out that at this 10-year anniversary of the first papers suggesting the possibility of hyperacuity, we still haven't "determined the underlying source of information, despite our strong understanding of the physiology of early visual cortex." I wonder if this is because the best understanding of the physiology of early visual cortex is at the fine scale (neurons and columns), not the coarse scale ( > 5 mm maps). I agree that interpreting the properties of individual voxels from MVPA is fraught with difficulty; interpreting the properties of groups of voxels is much more robust.

papers mentioned here, plus some other relevant papers

Wednesday, January 28, 2015

pointer: "Reward Motivation Enhances Task Coding in Frontoparietal Cortex"

I'm pleased to announce that a long-in-the-works paper of mine is now online: "Reward Motivation Enhances Task Coding in Frontoparietal Cortex". It doesn't look like the supplemental is online at the publisher's yet; The supplement is online now, or you can download it here. This is the work I spoke about at ICON last summer (July 2014). As the title indicates, this is not a straight methodology paper, though it has some neat methodological aspects, which I'll highlight here.

Briefly, the dataset is from a cognitive control task-switching paradigm: during fMRI scanning, people saw images of a human face with a word superimposed. But their response to the stimuli varied according to the preceding cue: in the Word task they responded whether the word part of the stimulus had two syllables or not; in the Face task they responded whether the image was of a man or woman. Figure 1 from the paper (below) schematically shows the timing and trial parts. The MVPA tried to isolate the activity associated with the cue part of the trial.


The people did this task on two separate scanning days: first the Baseline session, then the Incentive session. During the Incentive session incentives were introduced: people had a chance to earn extra money on some trials for responding quickly and accurately.

The analyses in the paper are aimed at understanding the effects of incentive: people perform a bit better when given an incentive (are more motivated) to perform better. We tested the idea that this improvement in performance is because the (voxel level) brain activity patterns encoding the task are better formed with incentive: sharper, more distinct, less noisy task-related patterns on trials with an incentive than trials without an incentive.

How to quantify "better formed"? There's no simple test, so we got at it three ways:

First, cross-session task classification accuracy (train on baseline session, test on incentive session) was higher on incentive trials, suggesting that the Incentive trials are "cleaner" (less noisy, so easier to classify). Further, the MVPA classification accuracy is a statistical mediator of performance accuracy (how many trials each person responded to correctly): people with a larger incentive-related increase in MVPA classification accuracy also tended to have a larger incentive-related increase in behavioral performance accuracy.

At left is Figure 4 from the paper, showing the correlation between classification and performance accuracy differences; each circle is a participant. It's nice to see this correlation between MVPA accuracy and behavior; there are still relatively few studies tying them together.

Second, we found that the Incentive test set examples tended to be further from the SVM hyperplane than the No-Incentive test set examples, which suggests that the classifier was more "confident" when classifying the Incentive examples. Since we used cross-session classification there was only one hyperplane for each person (the (linear) SVM trained on all baseline session examples), so it's possible to directly compare the distance of the test set examples to the hyperplane.

Third, we found a higher likelihood of distance concentration in the No-Incentive examples, suggesting that this dataset is less structured (higher intrinsic dimensionality) than the Incentive examples. The distance concentration calculation doesn't rely on the SVM hyperplane, and so gives another line of evidence.

There's (of course!) lots more detail and cool methods in the main paper; hope you enjoy! As always, please let me know what you think of this (and any questions), in comments, email, or in person.

UPDATE (24 March 2015): I have put some of the code and input images for this project online at the Open Science Foundation.


 ResearchBlogging.orgEtzel JA, Cole MW, Zacks JM, Kay KN, & Braver TS (2015). Reward Motivation Enhances Task Coding in Frontoparietal Cortex. Cerebral Cortex PMID: 25601237

Wednesday, January 21, 2015

research blogging: "Exceeding chance level by chance"

Neuroskeptic made me aware of a new paper by Combrisson & Jerbi entitled "Exceeding chance level by chance: The caveat of theoretical chance levels in brain signal classification and statistical assessment of decoding accuracy"; full citation below. Neuroskeptic's post has comments and a summary of the article, which I suggest you check out, along with its comment thread. 

My first reaction reading the article was confusion: are they suggesting we shouldn't test against chance (0.5 for two classes), but some other value? But no, they are arguing that it is necessary to do a test against chance ... to which I say, yes, of course it is necessary to do a statistical test to see if the accuracy you obtained is significantly above chance. The authors are arguing against a claim ("the accuracy is 0.6! 0.6 is higher than 0.5, so it's significant!") that I don't think I've seen in an MVPA paper, and would certainly question if I did. Those of us doing MVPA debate about how exactly to best do a permutation test (a favorite topic of mine!), and if the binomial or t-test is appropriate in particular situations, but everyone agrees that a statistical test is needed to support a claim that an accuracy is significant. In short, I agree with

What about the results of the paper's analyses? Basically, they strike me as unsurprising. For example, the authors note that smaller datasets are less stable (eg quite easy to get accuracies above 0.7 in noise data when only 5 examples of each class), and that smaller test set sizes (eg leave-1-out vs. leave-20-out cross validation when 100 examples) tend to have higher variance across the cross-validation folds (and so harder to reach significance). At right is Figure 1e, showing the accuracies they obtained from classifying many (Gaussian random) noise datasets of different sizes. What I immediately noticed is how nice and symmetrical around chance the spread of dots appears: this is the sort of figure we expect to see when doing a permutation test. Eyeballing the graph (and assuming the permutation test was done properly), we'd probably end up with accuracies above 0.7 being significant at small sample sizes, and around 0.6 for larger datasets, which strikes me as reasonable.

I'm not a particular fan of using the binomial for significance in neuroimaging datasets, especially when the datasets have any sort of complex structure (eg multiple fMRI scanning runs, cross-validation, more than one person), which they almost always have. Unless your data is structured exactly like Combrisson & Jerbi's (and they did the permutation test properly, which they might not have, see Martin Hebart's comments), Table 1 strikes me as inadequate for establishing significance: I'd want to see a test taking into account the variance in your actual dataset (and claims being made).

Perhaps my concluding comment should be that proper statistical testing can be hard, and is usually time consuming, but is absolutely necessary. Neuroimaging datasets are nearly always structured (eg sources of variance and patterns of dependency and interaction) far differently from the assumptions of quick statistical tests, and we are asking questions of them not covered by one-line descriptions. Don't look for a quick fix, but rather focus on your dataset and claims, and a method for establishing significance levels is nearly always possible.


ResearchBlogging.orgCombrisson, E., & Jerbi, K. (2015). Exceeding chance level by chance: The caveat of theoretical chance levels in brain signal classification and statistical assessment of decoding accuracy Journal of Neuroscience Methods DOI: 10.1016/j.jneumeth.2015.01.010