How will the neurosciences be transformed by machine learning and big data?

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Machine learning and statistics have been rapidly advancing in the past decade. Boosted by big data sets, new methods for inference and prediction are transforming many fields of science and technology. How will these developments affect the neurosciences? Bzdok & Yeo (pp2016) take a stab at this question in a wide-ranging review of recent analyses of brain data with modern methods.

Their review paper is organised around four key dichotomies among approaches to data analysis. I will start by describing these dichotomies from my own perspective, which is broadly – though not exactly – consistent with Bzdok & Yeo’s.

Generative versus discriminative models: A generative model is a model of the process that generated the data (mapping from latent variables to data), whereas a discriminative model maps from the data to selected variables of interest.
Nonparametric versus parametric models: Parametric models are specified using a finite number of parameters and thus their flexibility is limited and cannot grow with the amount of data available. Nonparametric models can grow in complexity with the data: The set of numbers identifying a nonparametric model (which may still be called “parameters”) can grow without a predefined limit.
Bayesian versus frequentist inference: Bayesian inference starts by defining a prior over all models believed possible and then infers the posterior probability distribution over the models and their parameters on the basis of the data. Frequentist inference identifies variables of interest that can be computed from data and constructs confidence intervals and decision rules that are guaranteed to control the rate of errors across many hypothetical experimental analyses.
Out-of-sample prediction and generalisation versus within-sample explanation of variance: Within-sample explanation of variance attempts to best explain a given data set (relying on assumptions to account for the noise in the data and control overfitting). Out-of-sample prediction integrates empirical testing of the generalisation of the model to new data (and optionally to different experimental conditions) into the analysis, thus testing the model, including all assumptions that define it, more rigorously.

Generative models are more ambitious than discriminative models in that they attempt to account for the process that generated the data. Discriminative models are often leaner – designed to map directly from data to variables of interest, without engaging all the complexities of the data-generating process.

Nonparametric models are more flexible than parametric models and can adapt their complexity to the amount of information contained in the data. Parametric models can be more stable when estimated with limited data and can sometimes support more sensitive inference when their strong assumptions hold.

Philosophically, Bayesian inference is more attractive than frequentist inference because it computes the probability of models (and model parameters) given the givens (or in Latin: the data). In real life, also, Bayesian inference is what I would aim to roughly approximate to make important decisions, combining my prior beliefs with current evidence. Full Bayesian inference on a comprehensive generative model is the most rigorous (and glamorous) way of making inferences. Explicate all your prior knowledge and uncertainties in the model, then infer the probability distribution over all states of the world deemed possible given what you’ve been given: the data. I am totally in favour of Bayesian analysis for scientific data analysis from the armchair in front of the fireplace. It is only when I actually have to analyse data, at the very last moment, that I revert to frequentist methods.

My only problem with Bayesian inference is my lack of skill. I never finish enumerating the possible processes that might have given rise to the data. When I force myself to stop enumerating, I don’t know how to implement the (incomplete) list of possible processes in models. And if I forced myself to make the painful compromises to implement some of these processes in models, I wouldn’t know how to do approximate inference on the incomplete list of badly implemented models. I would know that many of the decisions I made along the way were haphazard and inevitably subjective, that all them constrain and shape the posterior, and that few of them will be transparent to other researchers. At that point frequentist inference with discriminative models starts looking attractive. Just define easy-to-understand statistics of interest that can efficiently be computed from the data and estimate them with confidence intervals, controlling error probability without relying on subjective priors. Generative-model comparisons, as well, are often easier to implement in the frequentist framework.

Regarding the final dichotomy, out-of-sample prediction using fitted models provides a simple empirical test of generalisation. It can be used to test for generalisation to new measurements (e.g. responses to the same stimuli as in decoding) or to new conditions (as in cross-decoding and in encoding models, e.g. Kay et al. 2008; Naselaris et al. 2009). Out-of-sample prediction can be applied in crossvalidation, where the data are repeatedly split to maximise statistical efficiency (trading off computational efficiency).

Out-of-sample prediction tests are useful because they put assumptions to the test, erring on the safe side. Let’s say we want to test if two patterns are distinct and we believe the noise is multinormal and equal for both conditions. We could use a within-sample method like multivariate analysis of variance (MANOVA) to perform this test, relying on the assumption of multinormal noise. Alternatively, we could use out-of-sample prediction. Since we believe that the noise is multinormal, we might fit a Fisher linear discriminant, which is the Bayes-optimal classifier in this scenario. This enables us to project held-out data onto a single dimension, the discriminant, and use simpler inference statistics and fewer assumptions to perform the test. If multinormality were violated, the classifier would no longer be optimal, making prediction of the labels for held-out data work worse. We would more frequently err on the safe side of concluding that there is no difference, and the false-positives rate would still be controlled. MANOVA, by contrast, relies on multinormality for the validity of the test and violations might inflate the false-positives rate.

More generally, using separate training and test sets is a great way to integrate the cycle of exploration (hypothesis generation, fitting) and confirmation (testing) into the analysis of a single data set. The training set is used to select or fit, thus restricting the space of hypotheses to be tested. We can think of this as generating testable hypotheses. The training set helps us go from a vague hypothesis we don’t know how to test to a specifically defined hypothesis that is easy to test. The reason separate training and test sets are standard practice in machine learning and less widely used in statistics is that machine learning has more aggressively explored complex models that cannot be tested rigorously any other way. More on this here.

Out-of-sample prediction is not the alternative to p values

One thing I found uncompelling (though I’ve encountered it before, see Fig. 1) is the authors’ suggestion that out-of-sample prediction provides an alternative to null-hypothesis significance testing (NHST). Perhaps I’m missing something. In my view, as outlined above, out-of-sample prediction (the use of independent test sets) enables us to use one data set to restrict the hypothesis space (training) and another data set to do inference on the more specific hypotheses, which are easier to test with fewer assumptions. The prediction is the restricted hypothesis space. Just like within-sample analyses, out-of-sample prediction requires a framework for performing inference on the hypothesis space. This framework can be either frequentist (e.g. NHST) or Bayesian.

For example, after fitting encoding models to a training data set, we can measure the accuracy with which they predict the test set. The fitted models have all their parameters fixed, so are easy to test. However, we still need to assess whether the accuracy is greater than 0 for each model and whether one model has greater accuracy than another.

Using up one part of the data to restrict the hypothesis space (fitting) and then using another to perform inference on the restricted hypothesis space (so as to avoid the bias of training set accuracy that results from overfitting) could be viewed as a crude approximation (vacillating between overfitting on one set and using another to correct) to the rigorous thing to do: updating the current probability distribution over all possibilities as each data point is encountered.

Figure 1: I don’t understand why some people think of out-of-sample prediction as an alternative to p values.

Bzdok & Yeo do a good job of appreciating the strengths and weaknesses of either choice of each of these dichotomies and considering ways to combine the strengths even of apparently opposed choices. Four boxes help introduce the key dichotomies to the uninitiated neuroscientist.

The paper provides a useful tour through recent neuroscience research using advanced analysis methods, with a particular focus on neuroimaging. The authors make several reasonable suggestions about where things might be going, suggesting that future data analyses will…

leverage big data sets and be more adaptive (using nonparametric models)
incorporate biological structure
combine the strengths of Bayesian and frequentist techniques
integrate out-of-sample generalisation (e.g. implemented in crossvalidation)

Weaknesses of the paper in its current form

The main text moves over many example studies and adds remarks on analysis methodology that will not be entirely comprehensible to a broad audience, because they presuppose very specialised knowledge.

Too dense: The paper covers a lot of ground, making it dense in parts. Some of the points made are not sufficiently developed to be fully compelling. It would also be good to reflect on the audience. If the audience is supposed to be neuroscientists, then many of the technical concepts would require substantial unpacking. If the audience were mainly experts in machine learning, then the neuroscientific concepts would need to be more fully explained. This is not easy to get right. I will try to illustrate these concerns further below in the “particular comments” section.

Too uncritical: A positive tone is a good thing, but I feel that the paper is a little too uncritical of claims in the literature. Many of the results cited, while exciting for the sophisticated models that are being used, stand and fall with the model assumptions they are based on. Model checking and comparison of many alternative models are not standard practice yet. It would be good to carefully revise the language, so as not to make highly speculative results sound definitive.

No discussion of task-performing models: The paper doesn’t explain what from my perspective is the most important distinction among neuroscience models: Do they perform cognitive tasks? That this distinction is not discussed in detail reflects the fact that such models are still rare in neuroscience. We use a lot of different kinds of model, but even when they are generative and causal and constrained by biological knowledge, they are still just data-descriptive models in the sense that they do not perform any interesting brain information processing. Although they may be stepping stones toward computational theory, such models do not really explain brain computation at any level of abstraction. Task-performing computational models, as introduced by cognitive science, are first evaluated by their ability to perform an information-processing function. Recently, deep neural networks that can perform feats of intelligence such as object recognition have been used to explain brain and behavioural data (Yamins et al. 2013; 2014: Khaligh-Razavi et al. 2014; Cadieu et al. 2014; Guclu & van Gerven 2015). For all their abstractions, many of their architectural features are biologically plausible and at least they pass the most basic test for a computational model of brain function: explaining a computational function (for reviews, see Kriegeskorte 2015; Yamins & DiCarlo 2015).

screenshot1271 Figure 2: Shades of Bayes. The authors follow Kevin Murphy’s textbook in defining degrees of Bayesianity of inference, ranging from maximum likelihood estimation (top) to full Bayesian inference on parameters and hyperparameters (bottom). Above is my slightly modified version.

Comments on specific statements

“Following many new opportunities to generate digitized brain data, uncertainties about neurobiological phenomena henceforth required assessment in the statistical arena.”

Noise in the measurements, not uncertainties about neurobiological phenomena, created the need for statistical inference.

“Finally, it is currently debated whether increasingly used “deep” neural network algorithms with many non-linear hidden layers are more accurately viewed as parametric or non-parametric.”

This is an interesting point. Perhaps the distinction between nonparametric and parametric becomes unhelpful when a model with a finite, fixed, but huge number of parameters is tempered by flexible regularisation. It would be good to add a reference on where this is “debated”.

“neuroscientists often conceptualize behavioral tasks as recruiting multiple neural processes supported by multiple brain regions. This century-old notion (Walton and Paul, 1901) was lacking a formal mathematical model. The conceptual premise was recently encoded with a generative model (Yeo et al., 2015). Applying the model to 10,449 experiments across 83 behavioral tasks revealed heterogeneity in the degree of functional specialization within association cortices to execute diverse tasks by flexible brain regions integration across specialized networks (Bertolero et al., 2015a; Yeo et al., 2015).”

This is an example of a passage that is too dense and lacks the information required for a functional understanding of what was achieved here. The model somehow captures recruitment of multiple regions, but how? “Heterogeneity in the degree of functional specialisation”, i.e. not every region is functionally specialised to exactly the same degree, sounds both plausible and vacuous. I’m not coming away with any insight here.

“Moreover, generative approaches to fitting biological data have successfully reverse engineered i) human facial variation related to gender and ethnicity based on genetic information alone (Claes et al., 2014)”

Fitting a model doesn’t amount to reverse engineering.

“Finally, discriminative models may be less potent to characterize the neural mechanisms of information processing up to the ultimate goal of recovering subjective mental experience from brain recordings (Brodersen et al., 2011; Bzdok et al., 2016; Lake et al., 2015; Yanga et al., 2014).”

Is the ultimate goal to “recover mental experience”? What does that even mean? Do any of the cited studies attempt this?

“Bayesian inference is an appealing framework by its intimate relationship to properties of firing in neuronal populations (Ma et al., 2006) and the learning human mind (Lake et al., 2015).”

Uncompelling. If the brain and mind did not rely on Bayesian inference, Bayesian inference would be no less attractive for analysing data from the brain and mind.

“Parametric linear regression cannot grow more complex than a stiff plane (or hyperplane when more input dimensions Xn) as decision boundary, which entails big regions with identical predictions Y.”

The concept of decision boundary does not make sense in a regression setting.

“Typical discriminative models include linear regression, support vector machines, decision-tree algorithms, and logistic regression, while generative models include hidden Markov models, modern neural network algorithms, dictionary learning methods, and many non-parametric statistical models (Teh and Jordan, 2010).”

Linear regression is not inherently either discriminative or generative, nor are neural networks. A linear regression model is generative when it predicts the data (either in a within-sample framework, such as classical univariate activation-based brain mapping, or in an out-of-sample predictive framework, such as encoding models). It is discriminative when it takes the data as input to predict other variables of interest (e.g. stimulus properties in decoding, or subject covariates).

“Box 4: Null-hypothesis testing and out-of-sample prediction”

As discussed above, this seems to me a false dichotomy. We can perform out-of-sample predictions and test them with null-hypothesis significance testing (NHST). Moreover, Bayesian inference (the counterpart to NHST) can operate on a single data set. It makes more sense to me to contrast out-of-sample prediction versus within-sample explanation of variance.

Brain representations of animal videos are surprisingly stable across tasks and only subtly modulated by attention

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Nastase et al. (pp2016) presented video clips (duration: 2 s) to 12 human subjects during fMRI. In a given run, a subject performed one of two tasks: detecting repetitions of either the animal’s behaviour (eating, fighting, running, swimming) or the category of animal (primate, ungulate, bird, reptile, insect). They performed region-of-interest and searchlight-based pattern analyses. Results suggest that:

The animal behaviours are associated with clearly distinct patterns of activity in many regions, whereas different animal taxa are less discriminable overall. Within-animal-category representational dissimilarities (correlation distances) are similarly large as between-animal-category representational dissimilarities, indicating little clustering by these (very high-level) animal categories. However, animal-category decoding is above chance in a number of visual regions and generalises across behaviours, indicating some degree of linear separability. For the behaviours, there is strong evidence for both category clustering and linear separability (decodability generalising across animal taxa).

Representations are remarkably stable across attentional tasks, but subtly modulated by attention in higher regions. There is some evidence for subtle attentional modulations, which (as expected) appear to enhance task-relevant sensory signals.

Overall, this is a beautifully designed experiment and the analyses are comprehensive and sophisticated. The interpretation in the paper focusses on the portion of the results that confirms the widely accepted idea that task-relevant signals are enhanced by attention. However, the stability of the representations across attentional tasks is substantial and deserves deeper analyses and interpretation.

screenshot1195

Spearman correlations between regional RDMs and behaviour-category RDM (top) and a animal-category RDM (bottom). These correlations measure category clustering in the representation. Note (1) that clustering is strong for behaviours but weak for animal taxa, and (2) that modulations of category clustering are subtly, but significant in several regions, notably in the left postcentral sulcus (PCS) and ventral temporal (VT) cortex.

Strengths

The experiment is well motivated and well designed. The movie stimuli are naturalistic and likely to elicit vivid impressions and strong responses. The two attentional tasks are well chosen as both are quite natural. There are 80 stimuli in total: 5 taxa * 4 behaviours * 2 particular clips * 2 horizontally flipped versions. It’s impossible to control confounds perfectly with natural video clips, but this seems to strike quite a good balance between naturalism and richness of sampling and experimental control.

The analyses are well motivated, sophisticated, well designed, systematic and comprehensive. Analyses include both a priori ROIs (providing greater power through fewer tests) and continuous whole-brain maps of searchlight information (giving rich information about the distribution of information across the brain). Surface-based searchlight hyperalignment based on a separate functional dataset ensures good coarse-scale alignment between subjects (although detailed voxel pattern alignment is not required for RSA). The cortical parcellation based on RDM clustering is also an interesting feature. The combination of threshold-free cluster enhancement and searchlight RSA is novel, as far as I know, and a good idea.

Weaknesses

The current interpretation mainly confirms prevailing bias. The paper follows the widespread practice in cognitive neuroscience of looking to confirm expected effects. The abstract tells us what we already want to believe: that the representations are not purely stimulus driven, but modulated by attention and in a way that enhances the task-relevant distinctions. There is evidence for this in previous studies, for simple controlled stimuli, and in the present study, for more naturalistic stimuli. However, the stimulus, and not the task, explains the bulk of the variance. It would be good to engage the interesting wrinkles and novel information that this experiment could contribute, and to describe the overall stability and subtle task-flexibility in a balanced way.

Behavioural effects confounded with species: Subjects saw a chimpanzee eating a fruit, but they never saw that chimpanzee, or in fact any chimpanzee fighting. The videos showed different animal species in the primate category. Effects of the animal’s behaviour, thus, are confounded with species effects. There is no pure comparison between behaviours within the same species and/or individual animal. It’s impossible to control for everything, but the interpretation requires consideration of this confound, which might help explain the pronounced distinctness of clips showing different behaviours.

Asymmetry of specificity between behaviours and taxa: The behaviours were specific actions, which correspond to linguistically frequent action concepts (eating, fighting, running, swimming). However, the animal categories were very general (primate, ungulate, bird, reptile, insect), and within each animal category, there were different species (corresponding roughly to linguistically frequent basic-level noun concepts). The fact that the behavioural but not the animal categories corresponded to linguistically frequent concepts may help explain the lack of animal-category clustering.

Representational distances were measured with the correlation distance, creating ambiguity. Correlation distances are ambiguous. If they increase (e.g. for one task as compared to another) this could mean (1) the patterns are more discriminable (the desired interpretation), (2) the overall regional response (signal) was weaker, or (3) the noise was greater; or any combination of these. To avoid this ambiguity, a crossvalidated pattern dissimilarity estimator could be used, such as the LD-t (Kriegeskorte et al. 2007; Nili et al. 2014) or the crossnobis estimator (Walther et al. 2015; Diedrichsen et al. pp2016; Kriegeskorte & Diedrichsen 2016). These estimators are also more sensitive (Walther et al. 2015) because, like the Fisher linear discriminant, they benefit from optimal weighting of the evidence distributed across voxels and from noise cancellation between voxels. Like decoding accuracies, these estimators are crossvalidated, and therefore unbiased (in particular, the expected value of the distance estimate is zero under the null hypothesis that the patterns for two conditions are drawn from the same distribution). Unlike decoding accuracies, these distance estimators are continuous and nonsaturating, providing a more sensitive and undistorted characterisation of the representational geometry.

Some statistical analysis details are missing or unclear. The analyses are complicated and not everything is fully and clearly described. In several places the paper states that permutation tests were used. This is often a good choice, but not a sufficient description of the procedure. What was the null hypothesis? What entities are exchangeable under that null hypothesis? What was permuted? What exactly was the test statistic? The contrasts and inferential thresholds could be more clearly indicated in the figures. I did not understand in detail how searchlight RSA and threshold-free cluster enhancement were combined and how map-level inference was implemented. A more detailed description should be added.

Spearman RDM correlation is not optimally interpretable. Spearman RDM correlation is used to compare the regional RDMs with categorical RDMs for either behavioural categories or animal taxa. Spearman correlation is not a good choice for model comparisons involving categorical models, because of the way it deals with ties, of which there are many in categorical model RDMs (Nili et al. 2014). This may not be an issue for comparing Spearman RDM correlations for a single category-model RDM between the two tasks. However, it is still a source of confusion. Since these model RDMs are binary, I suspect that Spearman and Pearson correlation are equivalent here. However, for either type of correlation coefficient, the resulting effect size depends on the proportion of large distances in the model matrix (30 of 190 for the taxonomy and 40 of 190 for the behavioural model). Although I think it is equivalent for the key statistical inferences here, analyses would be easier to understand and effect sizes more interpretable if differences between averages of dissimilarities were used.

Suggestions

In general, the paper is already at a high level, but the authors may consider making improvements addressing some of the weaknesses listed above in a revision. I have a few additional suggestions.

Open data: This is a very rich data set that cannot be fully analysed in a single paper. The positive impact on the field would be greatest if the data were made publicly available.

Structure and clarify the results section: The writing is good in general. However, the results section is a long list of complex analyses whose full motivation remains unclear in some places. Important details for basic interpretation of the results should be given before stating the results. It would be good to structure the results section according to clear claims. In each subsection, briefly state the hypothesis, how the analysis follows from the hypothesis, and what assumptions it depends on, before describing the results.

Compare regional RDMs between tasks without models: It would be useful to assess whether representational geometries change across tasks without relying on categorical model RDMs. To this end the regional RDMs (20×20 stimuli) could be compared between tasks. A good index to be computed for each subject would be the between-task RDM correlation minus the within-task RDM correlation (both across runs and matched to equalise the between run temporal separation). Inference could use across subject nonparametric methods (subject as random effect). This analysis would reveal the degree of stability of the representational geometry across tasks.

Linear decoding generalising across tasks: It would be good to train linear decoders for behaviours and taxa in one task and test for generalisation to the other task (and simultaneously across the other factor).

Independent definition of ROIs: Might the functionally driven parcellation of the cortex and ROI selection based on intersubject searchlight RDM reliability not bias the ROI analyses? It seems safer to use independently defined ROIs.

Task decoding: It would be interesting to see a searchlight maps of task decodability. Training and test sets should always consist of different runs. One could assess generalisation to new runs and ideally also generalisation across behaviours and taxa (leaving out one animal category or one behavioural category from the training set).

Further investigate the more prominent distinctions among behaviours than among taxa: Is this explained by a visual similarity confound? Cross-decoding of behaviour between taxa sheds some light on this. However, it would be good also to analyse the videos with motion-energy models and look at the representational geometries in such models.

Additional specific comments and questions

Enhancement and collapse have not been independently measured. The abstract states: “Attending to animal taxonomy while viewing the same stimuli increased the discriminability of distributed animal category representations in ventral temporal cortex and collapsed behavioural information.” Similarly, on page 12, it says: “… accentuating task-relevant distinctions and reducing unattended distinctions.”
This description is intuitive, but it incorrectly suggests that the enhancement and collapse have been independently measured. This is not the case: It would require a third, e.g. passive-viewing condition. Results are equally consistent with the interpretation that attention just enhances the task-relevant distinctions (without collapsing anything). Conversely, the reverse might also be consistent with the results shown: that attention just collapses the task-irrelevant distinctions (without enhancing anything).

You explain in the results that this motivates the use of the term categoricity, but then don’t use that term consistently. Instead you describe it as separate effects, e.g. in the abstract.

The term categoricity may be problematic for other reasons. A better description might be “relative enhancement of task-relevant representational distinctions”. Results would be more interpretable if crossvalidated distances were used, because this would enable assessment of changes in discriminability. By contrast, larger correlation distance can also result from reduced responses or nosier data.

Map-inferential thresholds are not discernable: In Fig. 2, all locations with positively model-correlated RDMs are marked in red. The locations exceeding the map-inferential threshold are not visible because the colour scale uses red for below- and above-threshold values. The legend (not just the methods section) should also clarify whether multiple testing was corrected for and if so how. The Fig. 2 title “Effect of attention on local representation of behaviour and taxonomy” is not really appropriate, since the inferential results on that effect are in Fig. S3. Fig. S3 might deserve to be in the main paper, given that the title claim is about task effects.

Videos on YouTube: To interpret these results, one really has to watch the 20 movies. How about putting them on YouTube?

Previous work: The work of Peelen and Kastner and of Sigala and Logothetis on attentional dependence of visual representations should be cited and discussed.

Colour scale: The jet colour scale is not optimal in general and particularly confusing for the model RDMs. The category model RDMs for behaviour and taxa seem to contain zeroes along the diagonal, ones for within-category comparisons and twos for between-category comparisons. Is the diagonal excluded from model? In that case the matrix is binary, but contains ones and twos instead of zeroes and ones. While this doesn’t matter for the correlations, it is a source of confusion for readers.

Show RDMs: To make results easier to understand, why not show RDMs? Could average certain sets of values for clarity.

Statistical details

“When considering all surviving searchlights for both attention tasks, the mean regression coefficient for the behavioural category target RDM increased significantly from 0.100 to 0.129 (p = .007, permutation test).”
Unclear: What procedure do these searchlights “survive”? Also: what is the null hypothesis? What is permuted? Are these subject RFX tests?

The linear mixed effects model of Spearman RDM correlations suggests differences between regions. However, given the different noise levels between regions, I’m not sure these results are conclusive (cf. Diedrichsen et al. 2011).

“To visualize attentional changes in representational geometry, we first computed 40 × 40 neural RDMs based on the 20 conditions for both attention tasks and averaged these across participants.”
Why is the 40×40 RDM (including, I understand, both tasks) ever considered? The between-task pattern comparisons are hard to interpret because they were measured in different runs (Henriksson et al. 2015; Alink et al. pp2015).

“Permutation tests revealed that attending to animal behaviour increased correlations between the observed neural RDM and the behavioural category target RDM in vPC/PM (p = .026), left PCS (p = .005), IPS (p = .011), and VT (p = .020).”
What was the null? What was permuted? Do these survive multiple testing correction? How many regions were analysed?

Fig. 3: Bootstrapped 95% confidence intervals. What was bootstrapped? Conditions?

page 14: Mean of searchlight regression coefficients – why only select those searchlights that survive TFCE in both attention conditions?

page 15: Parcellation of ROIs based on the behaviour attention data only. Why?

SI text: Might eye movements constitute a confound? (Free viewing during video clips)

“more unconfounded” -> “less confounded”

Acknowledgement
Thanks to Marieke Mur for discussing this paper with me and sharing her comments, which are included above.

— Nikolaus Kriegeskorte

Why should we invest in basic brain science?

I’ve been approached for comment on an in-press paper. Among the questions posed to me was this one:

How does this kind of research benefit society? Why do we need to understand the neuroscience behind perception, learning, and social interaction? Why should we continue to invest in this kind of research?

Good questions. In conversation, I tend to dodge these by saying “it’s just interesting”. I haven’t had to write many grant proposals so far. A little elaboration on “it’s just interesting” seemed appropriate here. All I could come up with was this:

This is basic science. It benefits a society that values knowledge and is interested in finding out how the human mind and brain work. It is also imaginable that one day this research, along with hundreds or thousands of other studies, will help us make progress in the treatment of brain disorders. However, this is speculative at present. Many important advances of technology and medicine are based on basic science. Insight is often useful. But to gain it we must pursue it for its own sake, rather than with a need to justify every step toward it by an application.

I wish I had a better answer. Any suggestions?

Different categorical divisions become prominent at different latencies in the human ventral visual representation

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[Below is my secret peer review of Cichy, Pantazis & Oliva (2014). The review below applies to the version as originally submitted, not to the published version that the link refers to. Several of the concrete suggestions for improvements below were implemented in revision. Some of the more general remarks on results and methodology remain relevant and will require further studies to completely resolve. For a brief summary of the methods and results of this paper, see Mur & Kriegeskorte (2014).]

This paper describes an excellent project, in which Cichy et al. analyse the representational dynamics of object vision using human MEG and fMRI on a set of 96 object images whose representation in cortex has previously been studied in monkeys and humans. The previous studies provide a useful starting point for this project. However, the use of MEG in humans and the combination of MEG and fMRI enables the authors to characterise the emergence of categorical divisions at a level of detail that has not previously been achieved. The general approaches of MEG-decoding and MEG-RSA pioneered by Thomas Carlson et al. (2013) are taken to new level here by using a richer set of stimuli (Kiani et al. 2007; Kriegeskorte et al. 2008). The experiment is well designed and executed, and the general approach to analysis is well-motivated and sound. The results are potentially of interest to a broad audience of neuroscientists. However, the current analyses lack some essential inferential components that are necessary to give us full confidence in the results, and I have some additional concerns that should be addressed in a major revision as detailed below.

MAJOR POINTS

(1) Confidence-intervals and inference for decoding-accuracy, RDM-correlation time courses and peak-latency effects

Several key inferences depend on comparing decoding accuracies or RDM correlations as a function of time, but the reliability of these estimates is not assessed. The paper also currently gives no indication of the reliability of the peak latency estimates. Latency comparisons are not supported by statistical inference. This makes it difficult to draw firm conclusions. While the descriptive analyses presented are very interesting and I suspect that most of the effects the authors highlight are real, it would be good to have statistical evidence for the claims. For example, I am not confident that the animate-inanimate category division peaks at 285 ms. This peak is quite small and on top of a plateau. Moreover, the time the category clustering index reaches the plateau (140 ms) appears more important. However, interpretation of this feature of the time course, as well, would require some indication of the reliability of the estimate.

I am also not confident that the RDM-correlation between the MEG and V1-fMRI data really has a significantly earlier peak than the RDM-correlation between the MEG and IT-fMRI data. This confirms our expectations, but it is not a key result. Things might be more complicated. I would rather see unexpected result of a solid analysis than an expected result of an unreliable analysis.

Ideally, adding 7 more subjects would allow random effects analyses. All time courses could then be presented with error margins (across subjects, supporting inference to the population by treating subjects as a random-effect dimension). This would also lend additional power to the fixed-effects inferential analyses.

However, if the cost of adding 7 subjects is considered too great, I suggest extending the approach of bootstrap resampling of the image set. This would provide reliability estimates (confidence intervals) for all accuracy estimates and peak latencies and support testing peak-latency differences. Importantly, the bootstrap resampling would simulate the variability of the estimates across different stimulus samples (from a hypothetical population of isolated object images of the categories used here). It would, thus, provide some confidence that the results are not dependent on the image set. Bootstrap resampling each category separately would ensure that all categories are equally represented in each resampling.

In addition, I suggest enlarging the temporal sliding window in order to stabilise the time courses, which look a little wiggly and might give unstable estimates of magnitudes and latencies across bootstrap samples otherwise – e.g. the 285 ms animate-inanimate discrimination peak. This will smooth the time courses appropriately and increase the power. A simple approach would be to use a bigger time steps as well, e.g. 10- or 20-ms bins. This would provide more power in Bonferroni correction across time. Alternatively, the false-discovery rate could be used to control false positives. This would work equally well for overlapping temporal windows (e.g. 20-ms window, 1 ms steps).

(2) Testing linear separability of categories

The present version of the analyses uses averages of pairwise stimulus decoding accuracies. The decoding accuracies serve as measures of representational discriminability (a particular representational distance measure). This is fine and interpretable. The average between minus the average within discriminability is a measure of clustering, which is a stronger result in a sense than linear decodability. However, it would be good to see is linear decoding of each category division reveals additional or earlier effects. While your clustering index essentially implies linear separability, the opposite is not true. For example, two category regions arranged like stacked pancakes could be perfectly linearly discriminable while having no significant clustering (i.e. difference between the within and between category discriminabilities of image pairs). Like this:

1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1
2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2 2

Each number indexes a category and each repetition represents an exemplar. The two lines illustrate the pancake situation. If the vertical separation of the pancakes is negligible, they are perfectly linearly discriminable, despite a negligible difference between the average within and the average between distance. It would be interesting to see these linear decoding analyses performed using either indendent response measurements for the same stimuli or an independent (held out) set of stimuli as the test set. This would more profoundly address different aspects of the representational geometry.

For the same images in the test set, pairwise discriminability in a high-dimensional space strongly suggests that any category dichotomy can be linearly decoded. Intuitively, we might expect the classifier to generalise well to the extent that the categories cluster (within distances < between distances) – but this need not be the case (e.g. the pancake scenario might also afford good generalization to new exemplars).

(3) Circularity of peak-categorical MDS arrangements

The peak MDS plots are circular in that they serve to illustrate exactly the effect (e.g. animate-inanimate separation) that the time point has been chosen to maximise. This circularity could easily be removed by selecting the time point for each subject based on the other subjects’ data. The accuracy matrices for the selected time points could then be averaged across subjects for MDS.

(4) Test individual-level match of MEG and fMRI

It is great that fMRI and MEG data was acquired in the same participants. This suggests an analysis of the consistent reflection of individual idiosyncrasies in object processing in fMRI and MEG. One way to investigate this would be to correlate single-subject RDMs between MEG and fMRI, within and between subjects. If the within-subject MEG-fMRI RDM correlation is greater (at any time point), then MEG and fMRI consistently reflect individual differences in object processing.

MINOR POINTS

Why average trials? Decoding accuracy means nothing then. Single-trial decoding accuracy and information in bits would be interesting to see and useful to compare to later studies.

The stimulus-label randomisation test for category clustering (avg(between)-avg(within)) is fine. However, the bootstrap test as currently implemented might be problematic.

“Under the null hypothesis, drawing samples with replacement from D0 and calculating their mean decoding accuracy daDo, daempirial should be comparable to daD0. Thus, assuming that D has N labels (e.g. 92 labels for the whole matrix, or 48 for animate objects), we draw N samples with replacement and compute the mean daD0 of the drawn samples.”

I understand the motivation for this procedure and my intuition is that this test is likely to work, so this is a minor point. However, subtracting the mean empirical decoding accuracy might not be a valid way of simulating the null hypothesis. Accuracy is a bounded measure and its distribution is likely to be wider under the null than under H1. The test is likely to be valid, because under H0 the simulation will be approximately correct. However, to test if some statistic significantly exceeds some fixed value by bootstrapping, you don’t need to simulate the null hypothesis. Instead, you simulate the variability of the estimate and obtain a 95%-confidence interval by bootstrapping. If the fixed value falls outside the interval (which is only going to happen in about 5% of the cases under H0), then the difference is significant. This seems to me a more straightforward and conventional test and thus preferable. (Note that this uses the opposite tail of the distribution and is not equivalent here because the distribution might not be symmetrical.)

Fig. 1: Could use two example images to illustrate the pairwise classification.

It might be good here to see real data in the RDM on the upper right (for one time point) to illustrate.

“non-metric scaling (MDS)”: add multidimensional

Why non-metric? Metric MDS might more accurately represent the relative representational distances.

“The results (Fig. 2a, middle) indicate that information about animacy arises early in the object processing chain, being significant at 140 ms, with a peak at 285 ms.”
I would call that late – relative to the rise of exemplar discriminability.

“We set the confidence interval at p=”
This is not the confidence interval, this is the p value.

“To our knowledge, we provide here the first multivariate (content-based) analysis of face- and body-specific information in EEG/MEG.”

The cited work by Carlson et al. (2012) shows very similar results – but for fewer images.

“Similarly, it has not been shown previously that a content-selective investigation of the modulation of visual EEG/MEG signals by cognitive factors beyond a few everyday categories is possible24,26.”
Carlson et al. (2011, 2012; refs 22,23) do show similar results.

I don’t understand what you mean by “cognitive factors” here.

Fig S3d
What are called “percentiles”, are not percentiles: multiply by 100.

“For example, a description of the temporal dynamics of face representation in humans might be possible with a large and rich parametrically modulated stimulus set as used in monkey electrophysiology 44.”
Should cite Freiwald (43), not Shepard (44) here.

LANGUAGE, LOGIC, STYLE, AND GRAMMAR

Although the overall argument is very compelling, there were a number of places in the manuscript where I came across weaknesses of logic, style, and grammar. The paper also had quite a lot of typos. I list some of these below, to illustrate, but I think the rest of the text could use more work as well to improve precision and style.

One stylistic issue is that the paper switches between present and past tense without proper motivation (general statement versus report of procedures used in this study).

Abstract: “individual image classification is resolved within 100ms”

Who’s doing the classification here? The brain or the researchers? Also: discriminating two exemplars is not classification (except in a pattern-classifier sense). So this is not a good way to state this. I’d say individual images are discriminated by visual representations within 100 ms.

“Thus, to gain a detailed picture of the brain’s [] in object recognition it is necessary to combine information about where and when in the human brain information is processed.”

Some phrase missing there.

“Characterizing both the spatial location and temporal dynamics of object processing

demands innovation in neuroimaging techniques”

A location doesn’t require characterisation, only specification. But object processing does not take place in one location. (Obviously, the reader may guess what you mean — but you’re not exactly rewarding him or her for reading closely here.)

“In this study, using a similarity space that is common to both MEG and fMRI,”
Style. I don’t know how a similarity space can be common to two modalities. (Again, the meaning is clear, but please state it clearly nevertheless.)

“…and show that human MEG responses to object correlate with the patterns of neuronal spiking in monkey IT”
grammar.

“1) What is the time course of object processing at different levels of categorization?”
Does object processing at a given level of categorisation have a single time course? If not, then this doesn’t make sense.

“2) What is the relation between spatially and temporally resolved brain responses in a content-selective manner?”
This is a bit vague.

“The results of the classification (% decoding accuracy, where 50% is chance) are stored in a 92 × 92 matrix, indexed by the 92 conditions/images images.”
images repeated

“Can we decode from MEG signals the time course at which the brain processes individual object images?”
Grammatically, you can say that the brain processes images “with” a time course, not “at” a time course. In terms of content, I don’t know what it means to say that the brain processes image X with time course Y. One neuron or region might respond to image X with time course Y. The information might rise and fall according to time course Y. Please say exactly what you mean.
“A third peek at ~592ms possibly indicates an offset-response”
Peek? Peak.

“Thus, multivariate analysis of MEG signals reveal the temporal dynamics of visual content processing in the brain even for single images.”
Grammar.

“This initial result allows to further investigate the time course at which information about membership of objects at different levels of categorization is decoded, i.e. when the subordinate, basic and superordinate category levels emerge.”
Unclear here what decoding means. Are you suggesting that the categories are encoded in the images and the brain decodes them? And you can tell when this happens by decoding? This is all very confusing. 😉

“Can we determine from MEG signals the time course at which information about membership of an image to superordinate-categories (animacy and naturalness) emerges in the brain?”
Should say “time course *with* which”. However, all the information is there in the retina. So it doesn’t really make sense to say that the information emerges with a time course. What is happening is that category membership becomes linearly decodable, and thus in a sense explicit, according to this time course.

“If there is information about animacy, it should be mirrored in more decoding accuracy for comparisons between the animate and inanimate division than within the average of the animate and inanimate division.”

more decoding accuracy -> greater decoding accuracy

“within the average” Bad phrasing.

“utilizing the same date set in monkey electrophysiology and human MRI”
–> stimulus set

“Boot-strapping labels tests significance against chance”
Determining significance is by definition a comparison of the effect estimate against what would be expected by chance. It therefore doesn’t make sense to “test significance against chance”.

“corresponding to a corresponding to a p=2.975e-5 for each tail”
Redundant repetition.

“Given thus [?] a fMRI dissimilarity matrices [grammar] for human V1 and IT each, we calculate their similarity (Spearman rank-order correlation) to the MEG decoding accuracy matrices over time, yielding 2nd order relations (Fig. 4b).”

“We recorded brain responses with fMRI to the same set of object images used in the MEG study *and the same participants*, adapting the stimulation paradigm to the specifics of fMRI (Supplementary Fig. 1b).”
Grammar

The effect is significant in IT (p<0.001), but not in V1 (p=0.04). Importantly, the effect is significantly larger in IT than in V1 (p<0.001).

p=0.04 is also significant, isn’t it? This is very similar to Kriegeskorte et al. (2008, Fig. 5A), where the animacy effect was also very small, but significant in V1.

“boarder” -> “border”

The selfish scientist’s guide to preprint posting

Preprint posting is the right thing to do for science and society. It enables us to share our results earlier, speeding up the pace of science. It also enables us to catch errors earlier, minimising the risk of alerting the world to our findings (through a high-impact publication) before the science is solid. Importantly, preprints ensure long-term open access to our results for scientists and for the public. Preprints can be rapidly posted for free on arXiv and bioRxiv, enabling instant open access.

Confusingly for any newcomer to science who is familiar with the internet, scientific journals don’t provide open access to papers in general. They restrict access with paywalls and only really publish (in the sense of to make publicly available) a subset of papers. The cost of access is so high that even institutions like Harvard and the UK’s Medical Research Council (MRC) cannot afford paying for general access to all the relevant scientific literature. For example, as MRC employees, members of my lab do not have access to the Journal of Neuroscience, because our MRC Unit, the Cognition and Brain Sciences Unit in Cambridge, cannot afford to subscribe to it. The University of Cambridge pays more than one million pounds in annual subscription fees to Elsevier alone, a single major publishing company, as do several other UK universities. Researchers who are not at well-funded institutions in rich countries are severely restricted in their access to the literature and cannot fully participate in science under the present system.

Journals administer peer review and provide pretty layouts and in some cases editing services. Preprints complement journals, enabling us to read about each other’s work as soon as it’s written up and without paywall restrictions. With the current revival of interest in preprints (check out ASAPbio), more and more scientists choose to post their papers as preprints.

All major journals including Nature, Science, and most high-impact field-specific journals support the posting of preprints. Preprint posting is in the interest of journals because they, too, would like to avoid publication of papers with errors and false claims. Moreover, the early availability of the results boosts early citations and thus the journal’s impact factor. Check out Wikipedia’s useful overview of journal preprint policies. For detailed information on each journal’s precise preprint policy, refer to the excellent ROMEO website at the University of Nottingham’s SHERPA project on the future of scholarly communication (thanks to Carsten Allefeld for pointing this out).

All the advantages of using preprints to science and society are good and well. However, we also need to think about ourselves. Does preprint posting mean that we give away our results to competitors, potentially suffering a personal cost for the common good? What is the selfish scientist’s best move to advance her personal impact and career? There is a risk of getting scooped. However, this risk can be reduced by not posting too early. It turns out that posting a preprint, in addition to publication in a journal, is advisable from a purely selfish perspective, because it brings the following benefits to the authors:

Open access: Preprints guarantee open access, enhancing the impact and ultimate citation success of our work. This is a win for the authors personally, as well as for science and society.
Errors caught: Preprints help us catch errors before wider reception of the work. Again this is a major benefit not only to science, society, and journals, but also to the authors, who may avoid having to correct or retract their work at a later stage.
Earlier citation: Preprints grant access to our work earlier, leading to earlier citation. This is beneficial to our near-term citation success, thus improving our bibliometrics and helping our careers — as well as boosting the impact factor of the journal, where the paper appears.
Preprint precedence: Finally, preprints can help establish the precedence of findings. A preprint is part of the scientific record and, though the paper still awaits peer review, it can help establish scientific precedence. This boosts the long-term citation count of the paper.

In computer science, math, and physics, reading preprints is already required to stay abreast of the literature. The life sciences will follow this trend. As brain scientists working with models from computer science, we read preprints and, if we judge them to be of high-quality and relevance, we cite them.

My lab came around to routine preprint posting for entirely selfish reasons. Our decision was triggered by an experience that drove home the power of preprints. A competing lab had posted a paper closely related to one of our projects as a preprint. We did not post preprints at the time, but we cited their preprint in the paper on our project. Our paper appeared before theirs in the same journal. Although we were first, by a few months, with a peer-reviewed journal paper, they were first with their preprint. Moreover, our competitors could not cite us, because we had not posted a preprint and their paper had already been finalised when ours appeared. Appropriately, they took precedence in the citation graph – with us citing them, but not vice versa.

Posting preprints doesn’t only have advantages. It is also risky. What if another group reads the preprint, steals the idea, and publishes it first in a high-impact journal? This could be a personal catastrophe for the first author, with the credit for years of original work diminished to a footnote in the scientific record. Dishonorable scooping of this kind is not unheard of. Even if we believe that our colleagues are all trustworthy and outright stealing is rare, there is a risk of being scooped by honorable competitors. Competing labs are likely to be independently working on related issues. Seeing our preprint might help them improve their ongoing work; and they may not feel the need to cite our preprint for the ideas it provided. Even if our competitors do not take any idea from our preprint, just knowing that our project is ready to enter the year-long (or multiple-year) publication fight might motivate them to accelerate progress with their competing project. This might enable them to publish first in a journal.

The risk of being scooped and the various benefits vary as a function of the time of preprint posting. If we post at the time of publication in a journal, the risk of being scooped is 0 and the benefit of OA remains. However, the other benefits grow with earlier posting. How do benefits and costs trade off and what is the optimal time for posting a preprint?

As illustrated in the figure below, this selfish scientist believes that the optimal posting time for his lab is around the time of the first submission of the paper. At this point, the risk of being scooped is small, while the benefits of preprint precedence and early citation are still substantial. I therefore encourage the first authors in my lab to post at the time of first submission. Conveniently, this also minimises the extra workload required for the posting of the preprint. The preprint is the version of the paper to be submitted to a journal, so no additional writing or formatting is required. Posting a preprint takes less than half an hour.

I expect that as preprints become more widely used, incentives will shift. Preprints will more often be cited, enhancing the preprint-precedence and early-citation benefits. This will shift the selfish scientist’s optimal time of preprint posting to an earlier point, where an initial round of responses can help improve the paper before a journal vets it for a place in its pages. For now, we post at the time of the first submission.

preprint benefits afo posting time

Benefits and costs to the authors of posting preprints as a function of the time of posting. This figure considers the benefits and costs of posting a preprint at a point in time ranging from a year before (-1) to a year after (1, around the time of appearance in a journal) initial submission (0). The OA benefit (green) of posting a preprint is independent of the time of posting. This benefit is also available by posting the preprint after publication of the paper in a journal. The preprint-precedence (blue) and early-citation (cyan) benefits grow by an equal amount with every month prior to journal publication that the paper is out as a preprint. This is based on the assumption that the rest of the scientific community, acting independently, is chipping away at the novelty and citations of the paper at a constant rate. When the paper is published in a journal (assumed at 1 year after initial submission), the preprint no longer accrues these benefits, so the lines reach 0 benefit at the time of the journal publication. Finally, the risk of being scooped (red) is large when the preprint is posted long before initial submission. At the time of submission, it is unlikely that a competitor starting from scratch can publish first in a journal. However, there is still the risk that competitors who were already working on related projects accelerate these and achieve precedence in terms of journal publication as a result. The sum total (black) of the benefits and the cost associated with the risk of being scooped peaks slightly before the time of the first submission to a journal. The figure serves to illustrate my own rationale for posting around the time of the first submission of a paper to a journal. It is not based on objective data, but on subjective estimation of the costs and benefits for a typical paper from my own lab.

Using performance-driven deep learning models to understand sensory cortex

In a new perspective piece in Nature Neuroscience, Yamins & Dicarlo (2016) discuss the emerging methodology and initial results in the literature of using deep neural nets with millions of parameters optimised for task performance to explain representations in sensory cortical areas. These are important developments. The authors explain the approach very well, also covering the historical progression toward it and its future potential. Here are the key features of the approach as outlined by the authors.

(1) Complex models with multiple stages of nonlinear transformation from stimulus to response are used to explain high-level brain representations. The models are “stimulus computable” in the sense of fully specifying the computations from a physical description of the stimulus to the brain responses (avoiding the use of labels or judgments provided by humans).

(2) The models are neurobiologically plausible and “mappable”, in the sense that their components are thought to be implemented in specific locations in the brain. However, the models abstract from many biological details (e.g. spiking, in the reviewed studies).

(3) The parameters defining a model are specified by optimising the model’s performance at a task (e.g. object recognition). This is essential because deep models have millions of parameters, orders of magnitude too many to be constrained by the amounts of brain-activity data that can be acquired in a typical current study.

(4) Brain-activity data may additionally be used to define affine transformations of the model representations, so as to (a) fine-tune the model to explain the brain representations and/or (b) define the relationship between model units and measured brain responses in a particular individual.

(5) The resulting model is tested by evaluating the accuracy with which it predicts the representation of a set of stimuli not used in fitting the model. Prediction accuracy can be assessed at different levels of description:

as the accuracy of prediction of a stimulus-response matrix,
as the accuracy of prediction of a representational dissimilarity matrix, or
as the accuracy of prediction of task-information decodability (i.e. are the decoding accuracies for a set of stimulus dichotomies correlated between model and neural population?).

A key insight is that the neural-predictive success of the models derives from combining constraints on architecture and function.

Architecture: Neuroanatomical and neurophysiological findings suggest (a) that units should minimally be able to compute linear combinations followed by static nonlinearities and (b) that their network architecture should be deep with rich multivariate representations at each stage.
Function: Biological recognition performance and informal characterisations of high-level neuronal response properties suggest that the network should perform a transformation that retains high-level sensory information, but also emphasises behaviourally relevant categories and semantic dimensions. Large sets of labelled stimuli provide a constraint on the function to be computed in the form of a lookup table.

Bringing these constraints together has turned out to enable the identification of models that predict neural responses throughout the visual hierarchies better than any other currently available models. The models, thus, generalise not just to novel stimuli (Yamins et al. 2014; Khaligh-Razavi & Kriegeskorte 2014; Cadieu et al. 2014), but also from the constraints imposed on the mapping (e.g. mapping images to high-level categories) to intermediate-level representational stages (Güçlü & van Gerven 2015; Seibert et al. PP2016). Similar results are beginning to emerge for auditory representations.

The paper contains a useful future outlook, which is organised into sections considering improvements to each of the three components of the approach:

model architecture: How deep, what filter sizes, what nonlinearities? What pooling and local normalisation operations?
goal definition: What task performance is optimised to determine the parameters?
learning algorithm: Can learning algorithms more biologically plausible than backpropagation and potentially combining unsupervised and supervised learning be used?

In exploring alternative architectures, goals, and learning algorithms, we need to be guided by the known neurobiology and by the computational goals of the system (ultimately the organism’s survival and reproduction). The recent progress with neural networks in engineering provides the toolbox for combining neurobiologically plausible components and setting their parameters in a way that supports task performance. Alternative architectures, goals, and learning algorithms will be judged by their ability to predict neural representations of novel stimuli and biological behaviour.

The final section reflects on the fact that the feedfoward deep convolutional models currently very successful in this area only explain the feedforward component of sensory processing. Recurrent neural net models, which are also rapidly conquering increasingly complex tasks in engineering applications, promise to address these limitations of the initial studies using deep nets to explain sensory brain representations.

This perspective paper will be of interest to a broad audience of neuroscientists not themselves working with complex computational models, who are looking for a big-picture motivation of the approach and review of the most important findings. It will also be of interest to practitioners of this new approach, who will value the historical review and the careful motivation of each of the components of the methodology.

Deep net representational geometries become more similar to the ventral stream as performance is optimised

[R6I7]

Seibert, Yamins, Ardila, Hong, DiCarlo, and Gardner compared a deep convolutional neural network for visual object recognition to human ventral-stream representations as measured with fMRI (PP). The network was similar to the one described in Krizhevsky et al. (2012), the network that won the ImageNet competition that year with a large increase in performance compared to previous computer vision systems. The representations in the layers of the Krizhevsky deep net and similar models have been compared to human and monkey brain representations at different stages of the ventral stream previously (Yamins et al. 2013, Yamins et al. 2014; Khaligh-Razavi & Kriegeskorte 2014; Cadieu et al. 2014; Güçlü & van Gerven 2015). The present study is consistent with the previous results, generalises this line work to an interesting new set of test images, and investigates how the representational similarity of the model layers to the brain areas evolves as model performance is optimised. Results suggest that the optimisation of recognition performance increases representational similarity to visual areas, even for early and mid-level visual areas.

Model architecture: The convolutional network was inspired by that of Krizhevsky et al. (2012), using similar convolutional filter sizes, rectified linear units, the same pooling and local normalisation procedures, and data from ImageNet for training on 1000-class categorisation. However, the input images were downsampled to a substantially smaller size (120 x 120 pixels, instead of 224 x 224 pixels). Another major modification was that two intermediate fully connected layers (which contain most of the parameters in Krizhevsky et al.’s net) were omitted. This is reported to have no significant effect on recognition performance on an independent ImageNet test set.

Training and test stimuli: Like Krizhevsky et al., Seibert et al. trained the network by backpropagation to classify objects into 1000 categories. They used the very large ImageNet set of labelled images for model training and then presented the network and two human subjects with a different set of more controlled images: 1,785 grayscale images of 3D renderings of objects in many positions and views, superimposed to random natural backgrounds.

Representational similarity analysis: The authors compared the representational dissimilarity matrices (RDMs) between model layers and brain areas. They first randomly selected 1000 model features from a given layer, then reweighted these features, stretching and squeezing the representational space along its original axes, so as to maximise the RDM correlation between the model layer and the brain region. The maximisation of the RDM correlation was performed on the basis of 15 of the images for each of the 64 objects (different positions, views, and backgrounds). Using the fitted weights, they then re-estimated the model RDMs on the basis of the other 12 position-view combinations for the same 64 objects and computed the RDM correlation (Spearman) between model layer and brain region.

ScreenShot741

Detail of Figure 1 from the paper: Grayscale stimulus images were created by superimposing 3D models to natural backgrounds. The set strikes an interesting balance between naturalness and control. There were 8 objects from each of 8 categories (animals, boats, cars, chairs, faces, fruits, planes, tables) and each object was presented in 27 or 28 different combinations of position (including entirely nonoverlapping positions), view, and natural background image. For each of the 8 x 8 = 64 objects, they averaged response patterns to all the images that contained it, so as to compute 64 x 64-entry representational dissimilarity matrices (RDMs) using 1-Pearson correlation as the distance measure.

Related previous work: This work is closely related to recent papers by Yamins et al. (2013; 2014), Khaligh-Razavi et al. (2014), Cadieu et al. (2014), and Güçlü & van Gerven (2015). Yamins et al. showed that performance-optimised convolutional network models explain primate-IT neuronal recordings, with models performing better at object recognition also better explaining IT. Khaligh-Razavi et al. compared 37 computational model representations, including the layers of the Krizhevsky et al. (2012) model and a range of popular computer vision features, to human fMRI and monkey recording data (Kiani et al. 2007) and found that only the deep convolutional net, which was extensively trained to emphasize categorical divisions, could fully explain the IT data. They also showed that early visual cortex is well accounted for by earlier layers of the deep convolutional network (and by Gabor representations and other computer vision features). Cadieu et al. (2014) showed that among 6 different models, only Krizhevsky et al. (2012) and an even more powerful deep convolutional network by Zeiler & Fergus (2013) separate the categories in the representational space to a degree comparable to IT cortex. Güçlü & van Gerven (2015) investigated to what extent each layer of the model could explain the representations in each visual area of the ventral stream, finding rough correspondences between lower, intermediate, and higher model representations and early, mid-level, and higher ventral-stream regions, respectively.

How does the present work go beyond previous studies? The most striking novel contribution of this study is the characterisation of how representational similarity to visual areas develops as the neural net’s performance is optimised from a random initialisation. Unlike Yamins et al. (2014) and Cadieu et al. (2014), this study compares a convolutional network to the human ventral stream and, unlike Khaligh-Razavi & Kriegeskorte (2014), each image was presented in many positions and views and with many different backgrounds. The data is from only two subjects, but each subject underwent 9 sessions, so the total data set is substantial. The human fMRI data set is exciting in that it systematically varies category, exemplar, and accidental properties (position, view, background). However, the authors averaged across different images of each of the objects. I wonder if this data set has further potential for future analyses that don’t average across responses to different images.

Comparing many model representations to each of the areas of the visual system is a challenge requiring multiple studies. It’s great to see another study comparing the layers (including pooling layers and intermediate convolutional stages) alongside several control models (V1-like, V2-like, HMAX), which hadn’t been compared to deep convolutional networks before.

ScreenShot756

Figure 2 from the paper: Successive stages of the human ventral stream (V1, V2, V4, LOC) are best explained by successive layers of a deep convolutional neural net model. The representational geometry in V1 most resembles that of a lower and an intermediate layer of the network. The representational geometry in V2 most resembles that of an intermediate layer. And the representational geometries of V4 and LOC most resemble that of a higher layer of the network. Categories are reflected in clusters of response patterns in V4 and even more strongly in LOC. The same holds for higher layers of the network model.

Strengths

Model predictions of brain representational geometries are analysed as a function of model performance. This nicely demonstrates that it is not just the architecture, but performance optimisation that drives successful predictions of representations across all levels of the ventral stream.
Adds to the evidence that deep convolutional neural networks can explain the feedforward component of the stagewise representational transformations in the ventral visual stream.
Rich stimulus set of 1785 images that strikes an interesting balance between naturalism and control, independently varying objects and accidental properties.
Multiple data sets in each subject. This fMRI data set could in the future support tests of a wide variety of models.

Weaknesses

Statistical procedures are not clearly described and not fully justified. What type of generalisation does the crossvalidation scheme test for? What is being bootstrapped? Why are normal and independence assumptions relied on for inference, when bootstrapping the objects would enable straightforward tests that don’t require these assumptions?
The analysis is based on average response patterns across many different images for each object. This renders results more difficult to interpret.
Only two subjects.

Overall, this is a very nice study and a substantial contribution to the literature. However, the averaging across responses elicited by different images complicates the interpretation of the results and the statistical analyses need to be improved, better described, and fully justified – as detailed below. Although the overall results described in this review appear likely to hold up, I am not confident that the inferential results for particular model comparisons are reliable. (If concerns detailed below were substantively addressed, I would consider adjusting the reliability rating.)

Issues to consider addressing in a revision

(1) Can averaged response patterns elicited by different individual images be interpreted?

If we knew a priori that a region represents the objects with perfect invariance to position, view and background, then averaging across many images of the same objects that differ in these variables would make sense. However, we know that none of the regions is really invariant to position, view, and background, and gradually achieving some tolerance is one of the central computational challenges. The averaging will have differential effects in different regions as tolerance increases along the ventral stream. I don’t understand how to interpret the RDM for V1 given that it is based on averaged patterns. The object positions and backgrounds vary widely. Presumably different images of the same object are represented totally differently in V1. The averages should then form a tighter cluster of patterns (by factor 4 after averaging 16 images). Isn’t it puzzling then that the resulting RDM is still significantly correlated with the model? To explain this, do we have to assume that V1 actually represents the objects somewhat tolerantly (perhaps through feedback)? In a high-level representation tolerant to variation of accidental properties and sensitive to categorical differences, we expect the representations of the different images for a given object to be much more similar, so the averaging would have a smaller effect. All this confusion could be avoided by analysing patterns evoked by individual images. In addition, the emergence of tolerance across stages of processing could then be characterised.

(2) What type of generalisation does the crossvalidation scheme support?

Ideally, the crossvalidation should estimate the generalisation performance of the RDM prediction from the model for new images showing different objects. This is not the case here.

First, it appears that the brain data used for training (model weight fitting) and test (estimation of RDM correlation) are responses to the same set of images (all images). The weighting of the model features is estimated using a subset of 15 of the images for each object, and the RDM correlation between model and brain data assessed using 12 different images (different poses and backgrounds) of the same objects. This would seem to fall short of a test of generalisation to new images (even of the same objects) because all images are used (on the side of the brain responses) in the training procedure. Please clarify this issue.
Second, even if there was no overlap in the images used in training and test (on the side of either the model fitting or the brain data), the models are overfitted to the object set. Ideally, nonoverlapping sets of images of different objects should be used for training and testing. How about using a random subset of 4 of the objects in each category (32 in total) for fitting the weights and the other 32 objects for estimating the RDM correlation?

Overall, it seems unclear what type of generalisation these analyses test for. Let’s consider the issue of overfitting to the object set more closely. Currently, the weights w are fitted to 15 of the 27 images for a given object. In an idealised high-level representation invariant to the accidental variation, the two image sets will be identically represented. We expect the object representations to be in general position (no two on a point, no three on a line, no four on a plane and so on). Even if the 64 object representations were not at all clustered by category, but instead distributed randomly, we could linearly read out any categorical distinction and the decoder would generalise to the other 12 images. This is just to illustrate the expected effect of overfitting to the object set. In the present study, weights were fitted to predict RDMs not to discriminate categories. Fitting the 1000 scaling parameters to explain an RDM with 64*(64-1)/2 = about 2K dissimilarities should enable us to fit any RDM quite precisely. I would not be surprised if a noncategorical representation could fit a clearly categorical representation (block-diagonal RDM) in this context. The test-set correlations would then really just be a measure of the replicability of the brain RDMs – rather than a measure of the fit of the model. Regularisation might help ensure that different models are still distinguishable, but it also further complicates interpretation (see below).

Since higher regions are more tolerant, the training and test images are more similarly represented in these regions, and so we would expect greater positive overfitting bias on the estimated RDM correlation for higher regions regardless of the model. It is reassuring that the models still perform differently in LOC. However, the overfitting to the object set complicates interpretation.

The category decoding performance measure is similarly compromised by averaging across different images. Decoding performance as well (if I understood correctly) was tested by averaging different images for each object and training and testing on the same set of objects with different particular images in the test set. So the test is not a test of generalisation to different objects but to different images of the same objects. Again any representation uniquely representing each object (and having at least as many dimensions as the number of objects in both classes combined minus one, which is the case here) will appear to support linear category decoding, even if the distributions in representational space corresponding to the two categories (including the entire populations of objects they comprise) were not at all linearly separable and across-object generalisation performance were at chance level.

(3) Clarify the bootstrapping procedure used in model comparison

The first 6 times the term bootstrap is used, it is entirely unclear what entities are being resampled with replacement. The sampling of 1000 model units is explained in this context, and suggests that this is the resampling with replacement referred to as bootstrapping. Only on page 15 it says: “Our approach bootstraps over independent stimulus samples”. I’m not sure what multiple independent stimulus samples are meant here. Are the objects (averaged across images) resampled? Or are the images resampled? (The latter would necessitate re-estimating the object-average voxel responses to each object for each bootstrap sample.)

(4) Clarify and justify the test used for model comparison

The methods section states:

“Using the bootstrapping above, we computed p-values testing if Layer A better explained visual area X’s RDM than Layer B”

This suggests that a bootstrap test was used to compare models with respect to their RDM prediction performance. But then the model comparison test is described as follows:

“We use Fisher’s r-to-z transformation using Steiger (1980)’s approach to compute p-values for difference in correlation values (Lee and Preacher, 2013). The approach tests for equality of two correlation values from the same sample where one variable is held in common between the two coefficients (in our case, an RDM of a given visual area).”

The Steiger (1980) method for comparing two dependent correlations assumes that the elements of the correlated vectors are sampled independently. As you acknowledge, this is violated for dissimilarities in an RDM. But why then is the Steiger method appropriate? You mention bootstrapping, but don’t explain how your bootstrapping procedure interacts with the Steiger method. Kriegeskorte et al. (2008) and Nili et al. (2014) describe a bootstrapping approach to RDM model comparison that takes the dependencies between dissimilarities into account and does not rely on the Steiger method. Ideally, the objects, not the images, should be resampled with replacement, to simulate variation across objects (not across images of the same objects) and to avoid re-estimation of object-average patterns. Finally, it would be good to use model-comparative inference to support the improvement the RDM explanation of ventral stream regions as performance is optimised by training with backpropagation.

(5) Reconsider the regularisation used in feature-weight fitting

The one-iteration optimisation (motivated as a variant of early stopping) is a very ad-hoc choice of regulariser. I have no idea what prior is implicit to this method. However, this implicit prior is part of the model you are testing and affects the model comparison results. It is even a key component of the model because you are fitting so many parameters that different models might not be distinguishable without this prior.

(6) Show full inferential results with correction for multiple testing

It would be great if the figures showed which RDM correlations are significant and which pairs are significantly different. In addition, it would be good to account for multiple testing. Nonparametric methods for testing and comparing RDM correlations are described in Nili et al. (2014).

(7) Show noise ceilings

It would be good to see whether the model layers fully or only partially explain the explainable component of the variance in the RDMs. This could yield the insight that the model does fall short given the present study’s data set. It would be interesting then to learn how it falls short and this would motivate future changes to the model. Alternatively, if the model reaches the noise ceiling, we would learn that we need to get better or more data to find out how the model still falls short. The methods section suggests that a noise ceiling was estimated for Figure 6, stating:

“To avoid the problem of finding linear re-weightings using smaller sub-sets of our data, we instead computed noise ceilings and percent explained variance values (Figure 6) without using the weighting procedure described above. Noise ceilings for each visual area were computed by splitting the runs of our data into two non-overlapping groups. With each group, we estimated stimulus responses (beta weights) using the procedure described above (see the Image responses section) and computed object-averaged RDMs for each visual area. We used the correlation between the RDM from each of the two groups as our noise ceiling for percent explained variance estimates (Figure 6).”

However, Figure 6 and its legend don’t mention a noise ceiling. What is the noise ceiling in these analyses? Figure 2 would also benefit from noise ceilings for each of the brain areas. In addition, the split-half correlation should underestimate the noise ceiling because half the data is used and both RDMs are affected by noise. The noise ceiling computation should instead give an estimate of the expected performance of a noiseless true model or upper and lower bounds on this performance (Nili et al. 2014, Khaligh-Razavi & Kriegeskorte 2015).

(8) What is the function of the two branches of the model?

Clarify the function of the two branches of the model in the legend of Figure 5 and in the methods section. A single GPU was used for training here. Did this serve to keep the architecture consistent with Krizhevsky et al. (2012)?

(9) Why are the ROIs so big?

As far as I remember, a normal size for LO or FFA is below 1 ml. LO1, LO2, and FFA have 234, 299, and 292 voxels (pooled across two subjects), corresponding to 3 to 4 ml on average across subjects (given that voxels were 3 mm isotropic).

(10) Add a colour legend to Figure 4

This would help the reader quickly understand the meaning of the lines without having to refer to the text description.

The four pillars of open science

An open review of Gorgolewski & Poldrack (PP2016)

the 4 pillars of open science.png

The four pillars of open science are open data, open code, open papers (open access), and open reviews (open evaluation). A practical guide to the first three of these is provided by Gorgolewski & Poldrack (PP2016). In this open review, I suggest a major revision in which the authors add treatment of the essential fourth pillar: open review. Image: The Porch of the Caryatids (Porch of the Maidens) of the ancient Greek temple Erechtheion on the north side of the Acropolis of Athens.

Open science is a major buzz word. Is all the talk about it just hype? Or is there a substantial vision that has a chance of becoming a reality? Many of us feel that science can be made more efficient, more reliable, and more creative through a more open flow of information within the scientific community and beyond. The internet provides the technological basis for implementing open science. However, making real progress with this positive vision requires us to reinvent much of our culture and technology. We should not expect this to be easy or quick. It might take a decade or two. However, the arguments for openness are compelling and open science will prevail eventually.

The major barriers to progress are not technological, but psychological, cultural, and political: individual habits, institutional inertia, unhealthy incentives, and vested interests. The biggest challenge is the fact that the present way of doing science does work (albeit suboptimally) and our vision for open science has not merely not yet been implemented, but has yet to be fully conceived. We will need to find ways to gradually evolve our individual workflows and our scientific culture.

Gorgolewski & Poldrack (PP2016) offer a brief practical guide to open science for researchers in brain imaging. I was expecting a commentary reiterating the arguments for open science most of us have heard before. However, the paper instead makes good on its promise to provide a practical guide for brain imaging and it contains many pointers that I will share with my lab and likely refer to in the future.

The paper discusses open data, open code, and open publications – describing tools and standards that can help make science more transparent and efficient. My main criticism is that it leaves out what I think of as a fourth essential pillar of open science: open peer review. Below I first summarise some of the main points and pointers to resources that I took from the paper. Along the way, I add some further points overlooked in the paper that I feel deserve consideration. In the final section, I address the fourth pillar: open review. In the spirit of a practical guide, I suggest what each of us can easily do now to help open up the review process.

1 Open data

Open-data papers more cited, more correct: If data for a paper are published, the community can reanalyse the data to confirm results and to address additional questions. Papers with open data are cited more (Piwowar et al. 2007, Piwowar & Vision 2013) and tend to make more correct use of statistics (Wicherts et al. 2011).
Participant consent: Deidentified data can be freely shared without consent from the participants in the US. However, rules differ in other countries. Ideally, participants should consent to their data being shared. Template text for consent forms is offered by the authors.
Data description: The Brain Imaging Data Structure (BIDS) (Gorgolewski et al. 2015) provides a standard (evolved from the authors’ OpenfMRI project; Poldrack et al. 2013) for file naming and folder organisation, using file formats such as NifTI, TSV and JSON.
Field-specific brain-imaging data repositories: Two repositories accept brain imaging data from any researcher: FCP/INDI (for resting state fMRI only) and OpenfMRI (for any datasets that includes MRI data).
Field-general repositories: Field-specific repositories like those mentioned help standardise sharing for particular types of data. If the formats offered are not appropriate for the data to be shared, field-general repositories, including FigShare, Dryad, or DataVerse can be used.
Data papers: A data paper is a paper that focusses on the description of a particular data set that is publicly accessible. This helps create incentives for ambitious data acquisitions and to enable researchers to specialise in data acquisition. Journals publishing data papers include: Scientific Data, Gigascience, Data in Brief, F1000Research, Neuroinformatics, and Frontiers in Neuroscience.
Processed-data sharing: It can be useful to share intermediate or final results of data analysis. With the initial (and often somewhat more standardised) steps of data processing out of the way, processed data are often much smaller in volume and more immediately amenable to further analyses by others. Statistical brain-imaging maps can be shared via the authors’ NeuroVault.org website.

2 Open code

Code sharing for transparency and reuse: Data-analysis details are complex in brain imaging, often specific to a particular study, and seldom fully defined in the methods section. Sharing code is the only realistic way of fully defining how the data have been analysed and enabling others to check the correctness of the code and effects of adjustments. In addition, the code can be used as a starting point for the development of further analyses.
Your code is good enough to share: A barrier to sharing is the perception among authors that their code might not be good enough. It might be incompletely documented, suboptimal, or even contain errors. Until the field finds ways to incentivise greater investment in code development and documentation for sharing, it is important to lower the barriers to sharing. Sharing imperfect code is preferable to not sharing code (Barnes 2010).
Sharing does not imply provision of user support: Sharing one’s code does not imply that one will be available to provide support to users. Websites like org can help users ask and answer questions independently (or with only occasional involvement) of the authors.
Version Control System (VCS) essential to code sharing: VCS software enables maintenance of complex code bases with multiple programmers and versions, including the ability to merge independent developments, revert to previous versions when a change causes errors, and to share code among collaborators or publicly. An excellent, freely accessible, widely used, web-based VCS platform is com, introduced in Blischak et al. (2016).
Literate programming combines code and results and text narrative: Scripted automatic analyses have the advantage of automaticity and reproducibility (Cusack et al. 2014), compared to point-and-click analysis in an application with a graphical user interface. However, the latter enables more interactive interrogation of the data. Literate programming (Knuth 1992) attempts to make coding more interactive and provides a full and integrated record of the code, results, and text explanations. This provides a fully computationally transparent presentation of results, makes the code accessible to oneself later in time, and to collaborators and third parties, with whom literate programs can be shared (e.g. via GitHub). Software supporting this includes: Jupyter (for R, Python and Julia), R Markdown (for R) and matlabweb (for MATLAB).

3 Open papers

Open notebook science: Open science is about enhancing the bandwidth and reducing the latency in our communication network. This means sharing more and at earlier stages, not only our data and code, but ultimately also our day-to-day incremental progress. This is called open notebook science and has been explored, by Cameron Neylon and Michael Nielson among others. Gorgolewski & Poldrack don’t comment on this beautiful vision for an entirely different workflow and culture at all. Perhaps open notebook science is too far in the future? However, some are already practicing it. Surely, we should start exploring it in theory and considering what aspects of open notebook science we can integrate into our workflow. It would be great to have some pointers to practices and tools that help us move in this direction.
The scientific paper remains a critical component of scientific communication: Data and code sharing are essential, but will not replace communication through permanently citable scientific papers that link (increasingly accessible) data through analyses to novel insights and relate these insights to the literature.
Papers should simultaneously achieve clarity and transparency: The conceptual clarity of the argument leading to an insight is often at a tension with the transparency of all the methodological details. Ideally, a paper will achieve both clarity and transparency, providing multiple levels of description: a main narrative that abstracts from the details, more detailed descriptions in the methods section, additional detail in the supplementary information, and full detail in the links to the open data and code, which together enable exact reproduction of the results in the figures. This is an ideal to aspire to. I wonder if any paper in our field has fully achieved it. If there is one, it should surely be cited.
Open access: Papers need to be openly accessible, so their insights can have the greatest positive impact on science and society. This is really a no brainer. The internet has greatly lowered the cost of publication, but the publishing industry has found ways to charge higher prices through a combination of paywalls and unreasonable open-access charges. I would add that every journal contains unique content, so the publishing industry runs hundreds of thousands of little monopolies – safe from competition. Many funding bodies require that studies they funded be published with open access. We need political initiatives that simply require all publicly funded research to be publicly accessible. In addition, we need publicly funded publication platforms that provide cost-effective alternatives to private publishing companies for editorial boards that run journals. Many journals are currently run by scientists whose salaries are funded by academic institutions and the public, but whose editorial work contributes to the profits of private publishers. In historical retrospect, future generations will marvel at the genius of an industry that managed for decades to employ a community without payment, take the fruits of their labour, and sell them back to that very community at exorbitant prices – or perhaps they will just note the idiocy of that community for playing along with this racket.
Preprint servers provide open access for free: Preprint servers like bioRxiv and arXiv host papers before and after peer review. Publishing each paper on a preprint server ensures immediate and permanent open access.
Preprints have digital object identifiers (DOIs) and are citable: Unlike blog posts and other more fleeting forms of publication, preprints can thus be cited with assurance of permanent accessibility. In my lab, we cite preprints we believe to be of high quality even before peer review.
Preprint posting enables community feedback and can help establish precedence: If a paper is accessible before it is finalised the community can respond to it and help catch errors and improve the final version. In addition, it can help the authors establish the precedence of their work. I would add that this potential advantage will be weighed against the risk of getting scooped by a competitor who benefits from the preprint and is first to publish a peer-reviewed journal version. Incentives are shifting and will encourage earlier and earlier posting. In my lab, we typically post at the time of initial submission. At this point getting scooped is unlikely, and the benefits of getting earlier feedback, catching errors, and bringing the work to the attention of the community outweighs any risks of early posting.
Almost all journals support the posting of preprints: Although this is not widely known in the brain imaging and neuroscience communities, almost all major journals (including Nature, Science, Nature Neuroscience and most others) have preprint policies supportive of posting preprints. Gorgolewski & Poldrack note that they “are not aware of any neuroscience journals that do not allow authors to deposit preprints before submission, although some journals such as Neuron and Current Biology consider each submission independently and thus one should contact the editor prior to submission.” I would add that this reflects the fact that preprints are also advantageous to journals: They help catch errors and get the reception process and citation of the paper going earlier, boosting citations in the two-year window that matters for a journal’s impact factor.

4 Open reviews

The fourth pillar of open science is the open evaluation (OE, i.e. open peer review and rating) of scientific papers. This pillar is entirely overlooked in the present version of the Gorgolewski & Poldrack’s commentary. However, peer review is an essential component of communication in science. Peer review is the process by which we prioritise the literature, guiding each field’s attention, and steering scientific progress. Like other components of science, peer review is currently compromised by a lack of transparency, by inefficiency of information flow, and by unhealthy incentives. The movement for opening the peer review process is growing.

In traditional peer review, we judge anonymously, making inherently subjective decisions that decide about the publication of our competitors’ work, under a cloak of secrecy and without ever having to answer for our judgments. It is easy to see that this does not provide ideal incentives for objectivity and constructive criticism. We’ve inherited secret peer review from the pre-internet age (when perhaps it made sense). Now we need to overcome this dysfunctional system. However, we’ve grown used to it and may be somewhat comfortable with it.

Transparent review means (1) that reviews are public communications and (2) that many of them are signed by their authors. Anonymous reviewing must remain an option, to enable scientists to avoid social consequences of negative judgments in certain scenarios. However, if our judgment is sound and constructively communicated, we should be able to stand by it. Just like in other domains, transparency is the antidote to corruption. Self-serving arguments won’t fly in open reviewing, and even less so when the review is signed. Signing adds weight to a review. The reviewer’s reputation is on the line, creating a strong incentive to be objective, to avoid any impression of self-serving judgment, and to attempt to be on the right side of history in one’s judgment of another scientist’s work. Signing also enables the reviewer to take credit for the hard work of reviewing.

The arguments for OE and a synopsis of 18 visions for how OE might be implemented are given in Kriegeskorte, Walther & Deca (2012). As for other components of open science, the primary obstacles to more open practices are not technological, but psychological, cultural, and political. Important journals like eLife and those of the PLoS family are experimenting with steps toward opening the review process. New journals including, the Winnower, ScienceOpen, and F1000 Research already rely on postpublication peer review.

We don’t have to wait for journals to lead us. We have all the tools to reinvent the culture of peer review. The question is whether we can handle the challenges this poses. Here, in the spirit of Gorgolewki & Poldrack’s practical guide, are some ways that we can make progress toward OE now by doing things a little differently.

Sign peer reviews you author: Signing our reviews is a major step out of the dark ages of peer review. It’s easier said than done. How can we be as critical as we sometimes have to be and stand by our judgment? We can focus first on the strengths of a paper, then communicate all our critical arguments in a constructive manner. Some people feel that we must sign either all or none of our reviews. I think that position is unwise. It discourages beginning to sign and thus de facto cements the status quo. In addition, there are cases where the option to remain anonymous is needed, and as long as this option exists we cannot enforce signing anyway. What we can do is take anonymous comments with a grain of salt and give greater credence to signed reviews. It is better to sign sometimes than never. When I started to sign my reviews, I initially reserved the right to anonymity for myself. After all this was a unilateral act of openness; most of my peers do not sign their reviews. However, after a while, I decided to sign all of my reviews, including negative ones.
Openly review papers that have preprints: When we read important papers as preprints, let’s consider reviewing them openly. This can simultaneously serve our own and our collective thought process: an open notebook distilling the meaning of a paper, why its claims might or might not be reliable, how it relates to the literature, and what future steps it suggests. I use a blog. Alternatively or additionally, we can use PubMed Commons or PubPeer.
Make the reviews you write for journals open: When we are invited to do a review, we can check if the paper has been posted as a preprint. If not, we can contact the authors, asking them to consider posting. At the time of initial submission, the benefits tend to outweigh the risks of posting, so many authors will be open to this. Preprint posting is essential to open review. If a preprint is available, we can openly review it immediately and make the same review available to the journal to contribute to their decision process.
Reinvent peer review: What is an open review? For example, what is this thing you’re reading? A blog post? A peer review? Open notes on the essential points I would like to remember from the paper with my own ideas interwoven? All of the above. Ideally, an open review helps the reviewer, the authors, and the community think – by explaining the meaning of a paper in the context of the literature, judging the reliability of its claims, and suggesting future improvements. As we begin to review openly, we are reinventing peer review and the evaluation of scientific papers.
Invent peer rating: Eventually we will need quantitative measures evaluating papers. These should not be based on buzz and usage statistics, but reflect the careful judgement of peers who are experts in the field, have considered the paper in detail, and ideally stand by their judgment. Quantitative judgments can be captured in ratings. Multidimensional peer ratings can be used to build a plurality of paper evaluation functions (Kriegeskorte 2012) that prioritise the literature from different perspectives. We need to invent suitable rating systems. For primary research papers, I use single-digit ratings on multiple scales including reliability, importance, and novelty, using capital letters to indicate the scale in the following format: [R7I5].

Errors are normal

As we open our science and share more of it with the community, we run the risk of revealing more of our errors. From an idealistic perspective that’s a good thing, enabling us learn more efficiently as individuals and as a community. However, in the current game of high-impact biomedical science there is an implicit pretense that major errors are unlikely. This is the reason why, in the rare case that a major error is revealed despite our lack of transparent practices, the current culture requires that everyone act surprised and the author be humiliated. Open science will teach us to drop these pretenses. We need to learn to own our mistakes (Marder 2015) and to be protective of others when errors are revealed. Opening science is an exciting creative challenge at many levels. It’s about reinventing our culture to optimise our collective cognitive process. What could be more important or glamorous?

Additional suggestions for improvements in revision

A major relevant development regarding open science in the brain imaging community is the OHBM’s Committee on Best Practices in Data Analysis and Sharing (COBIDAS), of which author Russ Poldrack and I are members. COBIDAS is attempting to define recommended practices for the neuroimaging community and has begun a broad dialogue with the community of researchers (see weblink above). It would be good to explain how COBIDAS fits in with the other developments.
About a third of the cited papers are by the authors. This illustrates their substantial contribution and expertise in this field. I found all these papers worthy of citation in this context. However, I wonder if other groups that have made important contributions to this field should be more broadly cited. I haven’t followed this literature closely enough to give specific suggestions, but perhaps it’s worth considering whether references should be added to important work by others.
As for the papers, the authors are directly involved in most of the cited web resources OpenfMRI, NeuroVault, NeuroStars.org. This is absolutely wonderful, and it might just be that there is not much else out there. Perhaps readers of this open review can leave pointers in the comments in case they are aware of other relevant resources. I would share these with the authors, so they can consider whether to include them in revision.
Can the practical pointers be distilled into a table or figure that summarises the essentials? This would be a useful thing to print out and post next to our screens.
“more than fair” -> “only fair”

Disclosures

I have the following relationships with the authors.

relationship	number of authors
acquainted	2
collaborated on committee	1
collaborated on scientific project	0

References

Barnes N (2010) Publish your computer code: it is good enough. Nature. 467: 753. doi: 10.1038/467753a

Blischak JD, Davenport ER, Wilson G. (2016) A Quick Introduction to Version Control with Git and GitHub. PLoS Comput Biol. 12: e1004668. doi: 10.1371/journal.pcbi.1004668

Cusack R, Vicente-Grabovetsky A, Mitchell DJ, Wild CJ, Auer T, Linke AC, et al. (2014) Automatic analysis (aa): efficient neuroimaging workflows and parallel processing using Matlab and XML. Front Neuroinform. 2014;8: 90. doi: 10.3389/fninf.2014.00090

Gorgolewski KJ, Auer T, Calhoun VD, Cameron Craddock R, Das S, Duff EP, et al. (2015) The Brain Imaging Data Structure: a standard for organizing and describing outputs of neuroimaging experiments [Internet]. bioRxiv. 2015. p. 034561. doi: 10.1101/034561

Gorgolewski KJ, Varoquaux G, Rivera G, Schwarz Y, Ghosh SS, Maumet C, et al. (2015) NeuroVault.org: a webbased repository for collecting and sharing unthresholded statistical maps of the human brain. Front Neuroinform. Frontiers. 9. doi: 10.3389/fninf.2015.00008

Knuth DE (1992) Literate programming. CSLI Lecture Notes, Stanford, CA: Center for the Study of Language and Information (CSLI).

Kriegeskorte N, Walther A, Deca D (2012) An emerging consensus for open evaluation: 18 visions for the future of scientific publishing Front. Comput. Neurosci http://dx.doi.org/10.3389/fncom.2012.00094

Kriegeskorte N (2012) Open evaluation: a vision for entirely transparent post-publication peer review and rating for science. Front. Comput. Neurosci., 17 http://dx.doi.org/10.3389/fncom.2012.00079

Marder E (2015) Living Science: Owning your mistakes DOI: http://dx.doi.org/10.7554/eLife.11628 eLife 2015;4:e11628

Piwowar HA, Day RS, Fridsma DB (2007) Sharing detailed research data is associated with increased citation rate. PLoS One. 2007;2: e308. doi: 10.1371/journal.pone.0000308

Piwowar HA, Vision TJ (2013) Data reuse and the open data citation advantage. PeerJ. 1: e175. doi: 10.7717/peerj.175

Poldrack RA, Barch DM, Mitchell JP, Wager TD, Wagner AD, Devlin JT, et al. (2013) Toward open sharing of taskbased fMRI data: the OpenfMRI project. Front Neuroinform. 2013;7: 1–12. doi: 10.3389/fninf.2013.00012

Wicherts JM, Bakker M, Molenaar D (2011) Willingness to Share Research Data Is Related to the Strength of the Evidence and the Quality of Reporting of Statistical Results. Tractenberg RE, editor. PLoS One. 6: e26828. doi: 10.1371/journal.pone.0026828

Do view-invariant brain representations of actions arise within 200 ms of viewing?

[R7I7]

Humans can rapidly visually recognise the actions people around them are engaged in and this ability is important for successful behaviour and social interaction. Isik et al. presented human subjects with 2-second video clips of humans performing actions while measuring brain activity with MEG. The clips comprised 5 actions (walk, run, jump, eat, drink) performed by each of five different actors and video-recorded from each of five different views (only frontal and profile used in MEG). Results show that action can be decoded from MEG signals arising about 200 ms after the onset of the video, with decoding accuracy peaking after about 500 ms and then decaying while the stimulus is still on, with a rebound after stimulus offset. Moreover, decoders generalise across actors and views. The authors conclude that the brain rapidly computes a representation that is invariant to view and actor.

ScreenShot738

Figure from the paper. Legend from the paper with my modifications in brackets: [Accuracy of action decoding (%) from MEG data as a function of time after video onset]. We can decode [which of five actions was being performed in the video clip] by training and testing on the same view (‘within-view’ condition), or, to test viewpoint invariance, training on one view (0 degrees [frontal, I think, but this should be clarified] or 90 degrees [profile]) and testing on the second view (‘across view’ condition). Results are each [sic] from the average of eight different subjects. Error bars represent standard deviation [across what?]. Horizontal line indicates chance decoding accuracy. […] Lines at the bottom of plot indicate significance with p<0.01 permutation test, with the thickness of the line indicating [for how many of the 8 subjects decoding was significant]. [Note the significant offset response after the 2-s video (whose duration should be indicated by a stimulus bar).]

The rapid view-invariant action decoding is really quite amazing. It would be good to see more detailed analyses to assess the nature of the signals enabling this decoding feat. Of course, 200 ms already allows for recurrent computations and the decodability peak is at 500 ms, so this is not strong evidence for a pure feedforward account.

The generalisation across actors is less surprising. This was a very controlled data set. Despite some variation in the appearance of the actors, it seems plausible that there would be some clustering of the vectors of pixels across space and time (or of features of a low-level visual representation) corresponding to different actors performing the same action seen from the same angle.

In separate experiments, the authors used static single frames taken from the videos and dynamic point-light figures as stimuli. These reduced form-only and motion-only stimuli were associated with diminished separation of actions in the human brain and in model representations, and with diminished human action recognition, suggesting that form and motion information are both essential to action recognition.

I’m wondering about the role of task-related priors. Subjects were performing an action recognition task on this controlled set of brief clips during MEG while freely viewing the clips (though this is not currently clearly stated). This task is likely to give rise to strong prior expectations about the stimulus (0 deg or 90 deg, one of five actions, known scale and positions of key features for action discrimination). Primed to attend to particular diagnostic features and to fixate in certain positions, the brain will configure itself for rapid dynamic discrimination among the five possible actions. The authors present a group-average analysis of eye movements, suggesting that these do not provide as much information about the actions as the MEG signal. However, the low-dimensional nature of the task space is in contrast to natural conditions, where a wider variety of actions can be observed and view, actor, size, and background vary more. The precise prior expectations might contribute to the rapid discriminability of the actions in the brain signals.

The authors model the results in the framework of feedforward processing in a Hubel-and-Wiesel/Poggio-style model that alternates convolution and max-pooling to simulate responses resembling simple and complex cells, respectively. This model is extended here to process video using spatiotemporal filter templates. The first layer uses Gabor filters, higher layers use templates in the first layer matching video clips in the stimulus set. The authors argue that this model supports invariant decoding and largely accounts for the MEG results.

Like the subjects, the model is set up to process the restricted stimulus space. The internal features of the model were constructed using representational fragments from samples from the same parametric space of videos. The exact videos used to test the models were not used for constructing the feature set. However, if I understood correctly, videos from the same restricted space (5 actions, 5 actors, 5 views) were used. Whether the model can be taken to explain (at a high level of abstraction) the computations performed by the brain depends critically on the degree to which the model is not specifically constructed for the (necessarily very limited) 5-action controlled stimulus space used in the study.

As the authors note, humans still outperform computer vision models at action recognition. How does the authors’ own model perform on less controlled action videos? If it the model cannot perform the task on real-world sensory input, can we be confident that it captures the way that the human brain performs the task? This is a concern in many studies and not trivial to address. However, the interpretation of the results should engage this issue.

Strengths

Controlled stimulus set: The set of video stimuli (5 actions x 5 actors x 5 views x 26 clips = 3250 2-sec clips) is impressive. Assembling this set is an important contribution to the field. The set is condition-rich (compared to typical stimulus sets used in cognitive neuroscience studies) and seems to strike a good balance between control and realism. This set could be a driver of progress if it were to be used in multiple modelling and empirical studies.
Combination of brain-activity measurements and a simple computational model, which provides a useful starting point for modelling the recognition of dynamic actions, as it is minimal and standard in many respects: a feedforward model in the HMAX framework, extended from spatial to spatiotemporal filters.

Weaknesses

Controlled stimulus set: The set of video stimuli is very restricted compared to real-world action recognition. For the brain data, this means that subjects might have rapidly formed priors about the stimuli, enabling them to configure their visual systems (e.g. attentional templates, fixation targets) for more rapid recognition of the 5 actions than is possible in real-world settings. This limitation is shared with many studies in our field and difficult to overcome without giving up control (which is a strength, see above). I therefore suggest addressing this problem in the discussion.
The model uses features based on spatiotemporal patterns sampled from the same restricted stimulus space. Although non-identical clips were used, the videos underlying the representational space appear to share a lot with the experimental stimuli (same 5 actions, same 5 views, same background?, same actors?). I would therefore not expect this model to work well on arbitrary real-world action video clips. This is in contrast to recent studies using deep convolutional neural nets (e.g. Khaligh-Razavi & Kriegeskorte 2014), where the models were trained without any information about the (necessarily restricted) brain-experimental stimulus set and can perform recognition under real-world conditions.
Only one model (in two variants) is tested. In order to learn about computational mechanism, it would be good to test more models.
MEG data were acquired during viewing of only 50 of the clips (5 actions x 5 actors x 2 views).
Missing inferential analyses: While the authors employ inferential analyses in single subjects and report number of significant subjects, few hypotheses of interest are formally statistically tested. The effects interpreted appear quite strong, so the results described above appear solid nevertheless (interpretational caveats notwithstanding).

Overall evaluation

This is an ambitious study describing results of a well-designed experiment using a stimulus set that is a major step forward. The results are an interesting and substantial contribution to the literature. However, the analyses could be much richer than they currently are and the interpretation of the results is not straightforward. Stimulus-set-induced priors may have affected both the neural processing measured and the model (which used templates from stimuli within the controlled video set). Results should be interpreted more cautiously in this context.

Although feedforward processing is an important part of the story, it is not the whole story. Recurrent signal flow is ubiquitous in the brain and essential to brain function. In engineering, similarly, recurrent neural networks are beginning to dominate spatiotemporal processing challenges such as speech and video recognition. The fact that the MEG data are presented as time courses, revealing a rich temporal structure, and the model analyses are bar graphs illustrates the key limitation of the model.

It would be great to extend the analyses to reveal a richer picture of the temporal dynamics. This should include an analysis of the extent to which each model layer can explain the representational geometry at each latency from stimulus onset.

Future directions

In revision or future studies, this line of work could be extended in a number of ways:

Use multiple models that can handle real-world action videos. The authors’ controlled video set is extremely useful for testing human and model representations, and for comparing humans to models. However, to be able to draw strong conclusions, the models, like the humans, would have to be trained to recognise human actions under real-world conditions (unrestricted natural video). In addition, it would be good to compare the biological representational dynamics to both feedforward and recurrent computational models.
To overcome the problem of stimulus-set related priors, which make it difficult to compare representational dynamics measured for restricted stimulus sets to real-world recognition in biological brains, one could present a large set of stimuli without ever presenting a stimulus twice to the same subject. Would the action category still be decodable at 150 ms with generalisation across views? Would a feedforward computer vision model trained on real-world action videos be able to predict the representational dynamics?
The MEG analyses could use source reconstruction to enable separate analyses of the representational dynamics in different brain regions.
It would be useful to have MEG data for the full stimulus set of 5 actions x 5 actors x 5 viewpoints = 125 conditions. The representational geometries could be analysed in detail to reveal which particular action pairs become discriminable when with what level of invariance.

Particular suggestions for improvements of this paper

(1) Present more detailed results

It would be good to see results separately for each pair of actions and each direction of crossdecoding (0 deg training -> 90 deg testing, and 90 deg training -> 0 deg testing). Regarding the former, eating and drinking involve very similar body postures and motions. Is this reflected in the discriminability of these actions?

Regarding, the decoding generalisation across views, you state:

“We decoded by training only on one view (0 degrees or 90 degrees), and testing on a second view (0 degrees or 90 degrees).”

Was the training set exclusively composed on 0 degree (frontal?) and the test set exclusively of 90 degree (side view?), and vice versa? In case the test set contained instances of both views (though of course, not for the same actor and action), results are more difficult to interpret.

(2) Discuss the caveats to the current interpretation of the results

Discuss the question whether priors resulting from subjects understanding of the restricted stimulus set might have affected the processing of the stimuli. Consider the involvement of recurrent computations within 200 ms and discuss the continuing rise of decodability until 500 ms. Discuss the possibility that the model will not generalise to action recognition in the wild.

(3) Test several control models

Can Gabor, HMAX, and deep convolutional neural net models support similarly invariant action decoding? These models are relatively easy to test, so I think it’s worth considering this for revision. Computer vision models trained on dynamic action recognition could be left to future studies.

(4) Test models by comparison of its representations with the brain representations

The computational model is currently only compared to the data at the very abstract level of decoding accuracy. Can the model predict the representations and representational dynamics in detail? It might be difficult to use the model to predict the measured channels. This would require the fitting of a linear model predicting the measured channels from the model units and the MEG data (acquired for only 5 actions x 5 actors x 2 views = 50 conditions) might be insufficient. However, representational dynamics could be investigated in the framework of representational similarity analysis (50 x 50 representational dissimilarity matrices) following Carlson et al. (2013) and Cichy et al. (2014). Note that this approach does not require fitting a prediction model and so appears applicable here. Either approach would reveal the dynamic prediction of the feedforward model (given dynamic inputs) and where its prediction diverges from the more complex and recurrent processes in the brain. This would promise to give us a richer and less purely confirmatory picture of the data and might show the merits and limitations of a feedforward account.

(5) Perform temporal cross-decoding

Temporal crossdecoding (Carlson et al. 2013, Cichy et al. 2014) could be used to more richly characterise the representational dynamics. This would reveal whether representations stabilise in certain time windows, or keep tumbling through the representational space even as stimuli are continuously decodable.

(6) Improve the inferential analyses

I don’t really understand the inference procedure in detail from the description in the methods section.

“We recorded the peak decoding accuracy for each time bin,…”

What is the peak decoding accuracy for each time bin? Is this the maximum accuracy across subjects for each time bin?

“…and used the null distribution of peak accuracies to select a threshold where decoding results performing above all points in the null distribution for the corresponding time point were deemed significant with P < 0.01 (1/100).”

I’m confused after reading this, because I don’t understand what is meant by “peak”.

The inference procedure for the decoding-accuracy time courses seems to lack formal multiple-testing correction across time points. Given enough subjects, inference could be performed with subject as a random effect. Alternatively, fixed-effects inference could be performed by permutation, averaging across subjects. Multiple testing across latencies should be formally corrected for. A simple way to do this is to relabel the experimental events once, compute an entire decoding time course, and record the peak decoding accuracy across time (or if this is what was done, it should be clearly described). Through repeated permutations, a null distribution of peak accuracies can be constructed and a threshold selected that is exceeded anywhere under H0 with only 5% probability, thus controlling the familywise error rate at 5%. This threshold could be shown as a line or as the upper edge of a transparent rectangle that partially obscures the insignificant part of the curve.

For each inferential analysis, please describe exactly what the null hypothesis was, what event-labels are exchangeable under this null hypothesis, and how the null distribution was computed. Also, explain how the permutation test interacted with the crossvalidation procedure. The crossvalidation should ideally generalise to new stimuli and label permutation be wrapped around this entire procedure.

“Decoding analysis was performed using cross validation, where the classifier was trained on a randomly selected subset of 80% of data for each stimulus and tested on the held out 20%, to assess the classifier’s decoding accuracy.”

Does this apply only to the within-view decoding? In the critical decoding analysis with generalisation across views, it cannot have been 20% of the data in the held-out set, since 0-deg views were used for training and 90-deg views for testing (and vice versa). If only 50% of the data were used for training there, why didn’t performance suffer given the smaller training set compared to the within-view decoding?

It would also be good to have estimates and inferential comparisons of the onset and peak latencies of the decoding time courses. Inference could be performed on a set of single-subject latency differences between two conditions modelling subject as a random effect.

(7) Qualify claims about biological fidelity of the model

The model is not really “designed to closely mimic the biology of the visual system”, rather its architecture is inspired by some of the features of the feedforward component of the visual hierarchy, such as local receptive fields of increasing size across a hierarchy of representations.

(8) Open stimuli and data

This work would be especially useful to the community if the video stimuli and the MEG data were made openly available. To fully interpret the findings, it would also be good to be able to view the movie clips online.

(9) Further clarify the title

The title “Fast, invariant representation for human action in the visual system” is somewhat unclear. What is meant are representations of perceived human actions, not representations for action. “Fast, invariant representation of visually perceived human actions” would be better, for example.

(10) Clarify what stimuli MEG data were acquired for

The abstract states “We use magnetoencephalography (MEG) decoding and a computational model to study action recognition from a novel dataset of well-controlled, naturalistic videos of five actions (run, walk, jump, eat, drink) performed by five actors at five viewpoints.” This suggests that MEG data were acquired for all these conditions. The methods section clarifies that MEG data were only recorded for 50 conditions (5 actions x 5 actors x 2 views). Here and in the legend of Fig. 1, it would be better to use the term “stimulus set” in place of “data set”.

(11) Clarify whether subjects were fixating or free viewing

Were subjects free viewing or fixating? This should be explicitly stated and the choice motivated in either case.

(12) Make figures more accessible

The figures are not optimal. Every panel showing decoding results should be clearly labelled to state what variables the crossvalidation procedure tested for generalisations across. For example, a label (in the figure itself!) could be: “decoding brain representations of actions with invariance to actor and view”. The reader shouldn’t have to search in the legend to find this essential information. Also every figure should have a stimulus bar depicting the period of stimulus presence. This is important especially to assess stimulus-offset-related effects, which appear to be present and significant.

Fig. 3 is great. I think it would be clearer to replace “space-time dot product” with “space-time convolution”.

(13) Clarify what the error bars represent

“Error bars represent standard deviation.”

Is this the standard deviation across the 8 subjects? Is it really the standard deviation or the standard error?

(14) Clarify what we learn from the comparison between the structured and the unstructured model

For the unstructured model, won’t the machine learning classifier learn to select random combinations that tend to pool across different views of one action? This would render the resulting system computationally similar.

Pattern-component modelling disentangles the code and the noise in representational similarity analysis

[R8I8]

This paper proposes an interesting and potentially important extension to representational similarity analysis (RSA), which promises unbiased estimates of response-pattern similarities and more compelling comparisons of representations between different brain regions.

RSA consists in the analysis of the similarity structure of the representations of different stimuli (or mental states associated with different tasks) in a region of interest (ROI). To this end, the similarity of regional response patterns elicited by the different stimuli is estimated, typically by using their linear correlation coefficient across voxels (or neurons or recording sites in electrophysiology). It is often desirable to be able to compare these pattern similarities between different regions. For example, we would like to be able to address whether stimuli A and B elicit more highly correlated response patterns in region 1 or region 2. However, such comparisons are problematic, because the pattern correlations depend on fMRI noise (which might be different between the regions), voxel selection (e.g. selecting additional noisy voxels will reduce the pattern correlation), and unspecific pattern components (e.g. a strong shared component between all stimuli will increase the pattern correlation, with the high correlation not specific to the particular pair of stimuli).

ScreenShot687 — Pattern-component modelling yields estimates of the similarity of representational patterns that are not systematically distorted by noise and common components. Representational pattern similarity is measured here by the correlation across measurement channels (e.g. fMRI voxels) and is plotted as a function of the noise level (horizontal axes) for different amplitudes (shades of gray) of a common pattern component shared by both representational patterns. Figure from Diedrichsen et al. (2011).

When representational dissimilarities (or, equivalently similarities) are estimated from estimates of response patterns in a multidimensional space, the dissimilarity estimates are positively (or the similarity estimates negatively) biased. This is because the inevitable noise affecting the pattern estimates will typically increase the apparent distance between any two patterns (the probability of a decrease of the distance due to noise is 0.5 in 1 dimension and drops rapidly as dimensionality increases).

Instead of estimating the distances from pattern estimates, the authors therefore propose to estimate the distances from a covariance component model that captures the pattern variances and covariances across space. The approach requires that each stimulus (or, more generally, each experimental condition) has been repeated multiple times to yield multiple pattern estimates. Whereas simple RSA would consider the average pattern for each stimulus, the authors’ approach models the original trial-by-voxel matrix Y as a linear combination of a set of stimulus-related patterns U (thought to underlie the observed patterns) and noise, and estimates the covariance structure of the patterns. The noise E is assumed to be independent between trials, but there is no assumption of independence of the noise between voxels. This is important because fMRI error time series from voxels closeby within a region are known to be correlated.

This is an original and potentially important contribution. The core mathematical model appears well developed. The demonstration of the advantages of the method is compellingly demonstrated based on simulated data. The paper is well written. However, it requires a number of improvements to ensure that it successfully communicates its important message. (1) The authors should more clearly explain the assumptions their pattern-covariance modelling approach relies upon. (2) The authors should add a section explaining the practical application of the approach (3) A number of clarifications and didactical improvements, notably to the presentation of the analysis of the real fMRI data, would be desirable. These three major points are explained in detail below.

[This is my original secret peer review of Diedrichsen et al. (2011). Most of the suggestions for improvements were addressed in revision and are no longer relevant.]

MAJOR POINTS

(1) Assumptions and consequences of violations

The advantages of pattern-covariance modeling are well explained. However, the assumptions of this approach should be more clearly communicated, perhaps in a separate section.

Does the validity of the approach depend on assumptions about the probability densities of the response amplitudes? Are there any other assumptions about the nature of the response patterns?
What are the effects of violations of the assumptions? Please give examples of cases where the assumptions are violated and describe the expected effects on the analysis.
As long as statistical inference is performed at the level of the variability across subjects or by using randomisation testing, results might be robust to certain violations. Please clarify if and when this is the case.

(2) Practical application of the new approach

Please add a section explaining how to apply this method to fMRI data, addressing the following questions:

Do the authors plan to make matlab code available for the new method? If so, it would be good to state this in the paper.
Is there a function that takes the regional data matrix Y, the design matrix Z (including effects of no interest) and perhaps a predictor selection vector for selecting effects of interest as input and returns the corrected correlation (and perhaps Euclidean) distance matrix?
Does the method only work with slow event-related designs (with approximately independent trial estimates)?
Can we use the method on rapid-event-related designs where we do not have separate single-trial estimates (because single-trial responses overlap in time and multiple trials of the same condition must be estimated together for stability)?
What if we have only one pattern estimate per condition, because our design is condition-rich (e.g. 96 conditions as in Kriegeskorte et al. 2008) and rapid-event related?
More generally, what are the requirements and limitations of the proposed approach?

(3) Particular clarifications and didactical improvements

In classical multivariate regression, we get an estimate of the error of a spatial response pattern estimate as a multinormal (characterised by a scaled version of the voxel-by-voxel covariance matrix of the residuals, where the scaling factor reflects the amount of averaging for the case of binary nonoverlapping predictors, and, more generally, the sums of squares and products of the design matrix). Couldn’t this multinormal model of the variability of each condition-related pattern estimate be used to get an unbiased estimate of the correlation of each pair of pattern estimates? If so, would this approach be inferior or superior to the proposed method, and why?

7: What exactly are the ‘simplifying assumptions’ that allow a to be estimated independently of G by averaging the trial response patterns within conditions?

“The corrected estimate from the covariance-component model is unbiased over a large range of parameter settings.” What are the limits of this range? Is the estimate formally unbiased or just approximately so?

Can question a) “Does the region encode information about the finger in the movement and/or stimulation condition?” be addressed with the traditional and the proposed RSA method? It seems that that would necessitate estimating the replicability of patterns elicited by moving the same finger (and similarly for sensation). It is a typical and important neuroscientific question, so please consider addressing in the framework of RSA (not just in terms of a possible classifier analysis as in the current draft).

Across different runs, pattern correlations are usually found to be much lower (e.g. Misaki et al. 2010). This phenomenon requires further investigation. The authors suggest error correlations among trials closeby in time within a run as the cause. However, I suspect that such error correlations, though clearly present, might not be the major cause of this. Other causes include scanner drifts and greater head-motion-related disalignment (due to greater separation in time), which can cause distortions, that head-motion-correction cannot undo. It would be good to hear the authors’ assessment of these alternative causes.

The notation u_beta[c,1,…4], where c is an element of {1,2} is confusing to me. Shouldn’t it be u_beta[c,d], where c is an element of {1,2}, and d is an element of {1,2,3,4}?

Eq. 8 requires more unpacking. Perhaps a figure with the vertical and horizontal dimensions marked (“task effects: movement vs sensation”, “individual finger effects: (1) movement, (2) sensation”) and arrows pointing from conceptual labels (“shared pattern between all movement trials”, “shared pattern between all sensation trials”, etc.) to the variance components could serve this function.

Figures 1-4 are great.

Figures 6 and 7: This comparison between traditional RSA and the proposed method is not completely successful. Figure 6 the traditional approach is very comprehensible. Figure 7 is cryptic (partly due to lack of meaningful labeling of the vertical axes). Moreover, the relationship between the traditional and the proposed approach to RSA remains unclear (or anyway difficult to grasp at a glance). I suggest adding a figure that compares traditional RSA and the proposed method side by side. The top row should show the correlation matrices (sample correlation versus unbiased estimates from covariance component model). The next three rows should address the three questions raised in the text: “a) Does the region encode information about the finger in the movement and/or stimulation condition? b) Are the patterns evoked by movement of a given finger similar to the patterns evoked by stimulation of the same finger? c) Is this similarity greater in one region than another?” Results from the traditional and the proposed RSA should be shown for each question to demonstrate how the results appear in both approaches and where the traditional approach falls short.

MINOR POINTS

In Eq. 8, u_beta[1,2] should read u_beta[1,1], I think.

“The decomposition method offers an elegant way to control for all these possible influences on the size of the correlation coefficients. In addition to noise (ε), condition ( , ), and finger ( , ) effects (Eq. 7), we also added a run effect.” Should say Eq. 8, I think.

Does U stand for ‘(u)nderlying patters’ and a for spatial-average (a)ctivation? It would help to make this explicit.

Figure 6 : Please label the vertical axes (intuitive and clear conceptual label). Please mark all significant effects. Please add a colorbar (grayscale code for correlation). Legend: “(D) These correlations” Which correlations exactly? (Averaged across sense and move now?)

Figure 7: The vertical axes need to be intuitively labeled. The reader should not have to decode mathematical symbols from the legend to understand the meaning of the bar graphs. Even after a careful read of the legend (and after spending quite a bit of time on the paper), the neuroscientific findings are not easy to grasp here. As a result, the present version of this figure will leave readers preferring traditional RSA (Figure 6) as it at least can be interpreted without much effort. Please label gray and white (“sense” and “move”) bars as in Figure 6.

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