A brief overview of classification models in vision science

[I5R6]

 

Majaj & Pelli (pp2017) give a brief overview of classification models in vision science, leading from linear discriminants and the perceptron to deep neural networks. They discuss some of the perks and perils of using machine learning, and deep learning in particular, in the study of biological vision.

This is a brief and light-footed review that will be of interest to vision scientists wondering whether and why to engage machine learning and deep learning in their own work. I enjoyed some of the thoughtful notes on the history of classification models and the sketch of the progression toward modern deep learning.

The present draft lists some common arguments for and against deep learning models, but falls short of presenting a coherent perspective on why deep learning is important for vision science, or not; or which aspects are substantial and which are hype. It also doesn’t really explain deep learning or how it relates to the computational challenge of vision.

The overall conclusion is that machine learning and deep learning are useful modern tools for the vision scientist. In particular, the authors argue that deep neural networks provide a “benchmark” to compare human performance to, replacing the optimal linear filter and signal detection theory as the normative benchmark for vision. This misses what I would argue is the bigger point: deep neural networks provide an entry point for modeling brain information processing and engaging the real problem of vision, rather than a toy version of the problem that lacks all of vision’s essential challenges.

 

Suggestions for improvements

(1) Clearly distinguish deep learning within machine learning

The abstract doesn’t mention deep learning at all. As I was reading the introduction, I was wondering if deep learning had been added to the title of a paper about machine learning in vision science at the very end. Deep learning is defined as “the latest version of machine learning”. This is incorrect. Rather than a software product that is updated in a sequence of versions, machine learning is a field that explores a wide variety of models and inference algorithms in parallel. The fact that deep learning (which refers to learning of deep neural network models) is getting a lot of attention at the moment does not mean that other approaches, notably Bayesian nonparametric models, have lost appeal. How is deep learning different? Does it matter more for vision than other approaches? If so, why?

 

(2) Explain why depth matters

The multiple stages of nonlinear transformation that define deep learning models are essential for many real-world applications, including vision. I think this point should be central as it explains why vision science needs deep models.

 

(3) Clearly distinguish the use of machine learning models to (a) analyze data and to (b) model brain information processing

The current draft largely fails to distinguish two ways of using machine learning in vision science: to analyze data (e.g. decode neuronal population codes) and to model brain information processing. Both are important, but the latter more fundamentally advances the field.

 

(4) Relate classification to machine learning more broadly and to vision

The present draft presents a brief history of classification models. Classification is a small (though perhaps arguably key?) problem within both machine learning and vision. Why is this particular problem the focus of such a large literature and of this review? How does it relate to other problems in machine learning and in vision?

 

(5) Separate the substance from the hype and present a coherent perspective

Arguments for and against deep learning are listed without evaluation or a coherent perspective. For example, is it true that deep learning models have “too many parameters”? Should we strive to model vision with a handful of parameters? Or do models need to be complex because vision requires complex domain knowledge? Do tests of generalization performance address the issue of overfitting? (No, no, yes, yes.) Note that the modern version of the statistical modeling, which is touted as more rigorous, is Bayesian nonparametrics – defined by no limits on the parametric complexity of a model.

 

(6) Consider addressing my particular comments below.

 

Particular comments

“Many perception scientists try to understand recognition by living organisms. To them, machine learning offers a reference of attainable performance based on learned stimuli.”

It’s not really a normative reference. There is an infinity of neural network models and performance of a particular one can never be claimed to be “ideal”. Deep learning is worse in this respect than the optimal linear filter (which provides a normative reference for a task – with the caveat that the task is not vision).

 

“Deep learning is the latest version of machine learning, distinguished by having more than three layers.”

It’s not the “latest version”, rather it’s an old variant of machine learning that is currently very successful and popular. Also, a better definition of deep is that there is more than one hidden layer intervening between input and output layers.

 

“It is ubiquitous in the internet.”

How is this relevant?

 

“Machine learning shifts the emphasis from how the cells encode to what they encode, i.e. from how they encode the stimulus to what that code tells us about the stimulus. Mapping a receptive field is the foundation of neuroscience (beginning with Weber’s 1834/1996 mapping of tactile “sensory circles”), but many young scientists are impatient with the limitations of single-cell recording: looking for minutes or hours at how one cell responds to each of perhaps a hundred different stimuli. New neuroscientists are the first generation for whom it is patently clear that characterization of a single neuron’s receptive field, which was invaluable in the retina and V1, fails to characterize how higher visual areas encode the stimulus. Statistical learning techniques reveal “how neuronal responses can best be used (combined) to inform perceptual decision-making” (Graf, Kohn, Jazayeri, & Movshon, 2010).”

This is an important passage. It’s true that single neurons in inferior temporal cortex, for example, might be (a) difficult to characterize singly with tuning functions, (b) idiosyncratic to a particular animal, and (c) so many in number and variety that characterizing them one by one seems hopeless. It therefore appears more productive to focus on understanding the population code. However, it is not only what is encoded in the population, but also how it is encoded. The format determines what inferences are easy given the code. For example, we can ask what information could be gleaned by a single downstream neuron computing a linear or radial-basis-function readout of the code.

 

“For psychophysics, Signal Detection Theory (SDT) proved that the optimal classifier for a signal in noise is a template matcher (Peterson, Birdsall, & Fox, 1954; Tanner & Birdsall, 1958).”

Detecting chihuahuas in complex scenes can be considered an example of detecting “signal in noise”, and it is an example of a visual task. A template matcher is certainly not optimal for this problem (in fact it will fail severely at this problem). It would help here to define signal and noise.

The problem of detecting a fixed pattern in Gaussian noise needs to be explained first in any course of vision, so as to inoculate students against the misconstrual of the problem of vision it represents. On a more conciliatory note, one could argue that although detecting a fixed pattern in noise is a misleading oversimplification of vision, it captures a component of the problem. The optimal solution to this problem, template matching, captures a component of the solution to vision. Deep feedforward neural networks could be described as hierarchical template matchers, and they do seem to capture some aspects of vision.

 

“SDT has been a very useful reference in interpreting human psychophysical performance (e.g. Geisler, 1989; Pelli et al., 2006). However, it provides no account of learning. Machine learning shows promise of guiding today’s investigations of human learning and may reveal the constraints imposed by the training set on learning.”

In addition to offering learning algorithms that might relate to how brains learn, machine learning enables us to use realistically complex models at all.

 

“It can be hard to tell whether behavioral performance is limited by the set of stimuli, or the neural representation, or the mismatch between the neural decision process and the stimulus and task. Implications for classification performance are not readily apparent from direct inspection of families of stimuli and their neural responses.”

Intriguing, but cryptic. Please clarify.

 

“Some biologists complain that neural nets do not match what we know about neurons (Crick, 1989; Rubinov, 2015).”

It is unclear how the ideal “match” should even be defined. All models abstract, and that is their purpose. Stating a feature of biology that is absent in the model does not amount to a valid criticism. But there is a more detailed case to be made for incorporating more biologically realistic dynamic components, so please elaborate.

 

“In particular, it is not clear, given what we know about neurons and neural plasticity, whether a backpropagation network can be implemented using biologically plausible circuits (but see Mazzoni et al., 1991, and Bengio et al., 2015).”

Neural net models can be good models of perception without being good models of learning. There has also been a recent resurgence in work exploring how backpropagation, or a closely related form of credit assignment, might be implemented in brains. Please discuss the work along these lines by Senn, Richards, Bogacz, and Bengio.

 

“Some biological modelers complain that neural nets have alarmingly many parameters. Deep neural networks continue to be opaque”

Why are many parameters “alarming” from the more traditional perspective on modeling? Do you feel that the alarm is justified? My view is that the history of AI has shown that intelligence requires rich domain knowledge. Simple models therefore will not be able to explain brain information processing. Machine learning has taught us how to learn complex models and avoid their pitfalls (overfitting).

 

“Some statisticians worry that rigorous statistical tools are being displaced by machine learning, which lacks rigor (Friedman, 1998; Matloff, 2014, but see Breiman, 2001; Efron & Hastie, 2016).”

The classical simple models can’t cut it, so their rigour doesn’t help us. Machine learning has boldly engaged complex models as are required for AI and brain science. To be able to do this, it initially took a pragmatic computational, rather than a formal probabilistic approach. However, machine learning and statistics have since grown together in many ways, providing a very general perspective on probabilistic inference that combines complexity and rigor.

 

“It didn’” (p. 9) Fragment.

 

“Unproven convexity. A problem is convex if there are no local minima other than the global minimum.”

I think this is not true. Here’s my current understanding: If a problem is convex, then any local minimum is the global minimum. This is convenient for optimization and provably not the case for neural networks. However, the reverse implication does not hold: if every local minimum is a global minimum, the function is not necessarily convex. There is a category of cost functions that are not convex, but every local minimum is a global minimum. Neural networks appear to fall in this category (at least under certain conditions that tend to hold in practice).

Note that there can be multiple global minima. In fact, the error function of a neural network over the weight domain typically has many symmetries, with any given set of weights having many computationally equivalent twins (i.e. the model computes the same overall function for different parameter settings). The high dimensionality, however, is not a curse, but a blessing for gradient descent: In a very high-dimensional weight space, it is unlikely that we find ourselves trapped, with the error surface rising in all directions. There are too many directions to escape in. Several papers have argued that local minima are not an issue for deep learning. In particular, it has been argued that every local minimum is a global minimum and that every other critical point is a saddle point, and that saddle points are the real challenge. Moreover, deep nets with sufficient parameters can fit the training data perfectly (interpolating), while generalizing well (which, surprisingly, some people find surprising). There is also evidence that stochastic gradient descent finds flat minima corresponding to robust solutions.

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Example of a non-convex error function whose every local minimum is a global minimum (Dauphin et al. pp2014).

“This [convexity] guarantees that gradient-descent will converge to the global minimum. As far as we know, classifiers that give inconsistent results are not useful.”

That doesn’t follow. A complex learner, such as an animal or neural net model, with idiosyncratic and stochastic initialization and experience may converge to an idiosyncratic solution that is still “useful” – for example, classifying with high accuracy and a small proportion of idiosyncratic errors.

 

“Conservation of a solution across seeds and algorithms is evidence for convexity.”

No, but it may be evidence for a minimum with a large basin of attraction. Would need to define what counts as conservation of a solution: (1) identical weights, (2) computationally equivalent weights (same input-output mapping). Definition 2 seems more helpful and relevant.

 

““Adversarial” examples have been presented as a major flaw in deep neural networks. These slightly doctored images of objects are misclassified by a trained network, even though the doctoring has little effect on human observers. The same doctored images are similarly misclassified by several different networks trained with the same stimuli (Szegedy, et al., 2013). Humans too have adversarial examples. Illusions are robust classification errors. […] The existence of adversarial examples is intrinsic to classifiers trained with finite data, whether biological or not.”

I agree. We will know whether humans, too, are susceptible to the type of adversarial example described in the cited paper, as soon as we manage to backpropagate through the human visual system so as to construct comparable adversarial examples for humans.

 

“SDT solved detection and classification mathematically, as maximum likelihood. It was the classification math of the sixties. Machine learning is the classification math of today. Both enable deeper insight into how biological systems classify. In the old days we used to compare human and ideal classification performance. Today, we can also compare human and machine learning.”

“…the performance of current machine learning algorithms is a useful benchmark”

SDT is classification math for linear models, ML is classification math for more complex models. These models enable us to tackle the real problem of vision. Rather than comparing human performance to a normative ideal of performance on a toy task, we can use deep neural networks to model the brain information processing underlying visual recognition. We can evaluate the models by comparing their internal representations to brain representations and their behavior to human behavior, including not only the ways they shine, but also the ways they stumble and fail.

 

 

Recurrent neural net model trained on 20 classical primate decision and working memory tasks predicts compositional neural architecture

[I8R8]

 

Yang, Song, Newsome, and Wang (pp2017) trained a rate-coded recurrent neural network with 256 hidden units to perform a variety of classical cognitive tasks. The tasks combine a number of component processes including evidence accumulation over time, multisensory integration, working memory, categorization, decision making, and flexible mapping from stimuli to responses. The tasks include:

  • speeded response indicating the direction of the stimulus (stimulus-response mapping)
  • speeded response indicating the opposite of the direction of the stimulus (flexible stimulus-response mapping)
  • response indicating the direction of a stimulus after a delay during which the stimulus is not visible (working memory)
  • decision indicating which of two noisy stimulus inputs is stronger (evidence accumulation)
  • decision indicating which of two ranges of the stimulus variable the stimulus falls in (categorization)

The 20 distinct tasks result from combining in various ways the requirements of accumulating stimulus evidence from two sensory modalities, maintaining stimulus evidence in working memory during a delay, deciding which category the stimulus fell in, and flexible mapping to responses.

The tasks reduce cognition to its bare bones and the model abstracts from the real-world challenges of perception (pattern recognition) and motor control, so as to focus on the flexible linkage between perception and action that we call cognition. The input to the model includes a “fixation” signal, sensory stimuli varying along a single circular dimension, and an rule input, that specifies a task index.

The fixation signal is given through a special unit, whose activity corresponds to the presence of a fixation dot on the screen in front of a primate subject. The fixation signal accompanies the perceptual and maintenance phases of the task, and its disappearance indicates that the primate or model should respond. The sensory stimulus (“direction of stimulus from fixation”) is encoded in a set of direction-tuned units representing the circular dimension. Each of two sensory modalities is represented by such a set of units. The task rule is entered in one-hot format through a set of task units that receive the task index throughout performance of a task (no need to store the current task in working memory). The motor output is a “saccade direction” encoded, similarly to the stimulus, by a set of direction-tuned units.

Such tasks have long been used in nonhuman primate cell recording and human imaging studies, and also in rodent studies, in order to investigate how basic building blocks of cognition are implemented in the brain. This paper provides an important missing link between primate cognitive neurophysiology and rate-coded neural networks, which are known to scale to real-world artificial intelligence challenges.

Unsurprisingly, the authors find that the network learns to perform all 20 tasks after interleaved training on all of them. They then perform a number of well-motivated analyses to dissect the trained network and understand how it implements its cognitive feats.

An important question is whether particular units serve task-specific or task-general functions. One extreme hypothesis is that each task is implemented in a separate set of units. The opposite hypothesis is that all tasks employ all units. In order to address the degree of task-generality of the units, the authors measure the extent to which each unit conveys relevant information in each task. This is measured by the variance of a unit’s activity across different  conditions within a task (termed the task variance). The authors find that the network learns to share some of the dynamic machinery it learns among different tasks.

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Figure 4 from the paper shows the extent to which two tasks are subserved by disjoint or overlapping sets of units. Each panel shows a comparison between two tasks (decision making about modality 1, DM1; delayed decision making about modality 1, Dly DM 1; Context-dependent decision making about modality 1, Ctx DM 1; delayed match to category, DMC; delayed non-match to category, DNMC). The histograms show how the 256 units are distributed in terms of their “fractional task variance” (FTV), which measures the degree to which a unit conveys information in task 1 (FTV = -1), in task 2 (FTV = 1) or in both equally (FTV = 0).

The authors find evidence for a compositional implementation of the tasks in the trained network. Compositionality here means that the tasks employ overlapping sets of functional components of the network. Rather than learning a separate dynamic systems for each task, the network appears to learn dynamic components serving different functions that can be flexibly combined to enable performance of a wide range of tasks.

The authors’ argument in favor of a compositional architecture is based on two observations: (1) Pairs of tasks that share cognitive component functions tend to involve overlapping sets of units. (2) Task-rule inputs, though trained in one-hot format, can be linearly combined (e.g. Delay Anti = Anti + Delay Go – Go) and the network given such a task specification (which it has never been trained on) will perform the implied task with high accuracy.

 

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Figure 6 from the paper supports the argument that the network learns a compositional architecture. During training, the task rule index is given in the form of a one-hot vector (a). The trained network can be given a linear combination of the trained task rules (c), such that the that adding and subtracting component functions (e.g. anti-mapping of stimuli to responses, working memory maintenance over delay, speeded reaction) according to the weights specifies a different task (Delay Anti = Anti + Delay Go – Go). The network then performs the compositionally specified task with high performance, although the task rule input corresponding to that task was 0.

These analyses are interesting because they help us understand how the network works and because they can also be applied to primate cell recordings and help us compare models to brains.

When the network is sequentially trained on one task at a time, the learning of new tasks interferes with previously acquired tasks, reducing performance. However, a continual learning technique that selectively protects certain learned connections enabled sequential acquisition of multiple tasks.

Overall, this is a highly original paper presenting a simple, yet well-motivated model and several useful analysis methods for understanding biological and artificial neural networks. The model extends the authors’ previous work on the neural implementation of some of these components of cognition. Importantly, the paper helps strengthen the link between rate-coded neural network models and primate (and rodent) cognitive neuroscience.

 

Strengths

  • The model is simple and well-designed and helps us imagine how basic components of cognition might be implemented in a recurrent neural network. It is essential that we build task-performing models to complement our fallible intuitions as to the signatures of cognitive processes we should expect in neuronal recordings.
  • The paper links primate cognitive neurophysiology to rate-coded neural networks trained with stochastic gradient descent. This might help boost future interactions between neurophysiologists and engineers.
  • The measures and analyses introduced to dissect the network are well-motivated, straightforward, and imaginative. Several of them can be equally applied to models and neuronal recordings.
  • The paper is well-written, clear, and tells an interesting story.
  • The figures are of high quality.

 

Weaknesses

  • The tasks are so simple that they do not pose substantial computational challenges. This is a strength because it makes it easier to understand neuronal responses in primate brains and unit responses in models. We have to start from the simplest instances of cognition. However, it is also a weakness. Consider the comparison to understanding the visual system. One approach is to reduce vision to discriminating two predefined images. The optimal algorithm for this task is a linear filter applied to the image. The intuitive reduction of vision to this scenario supports the template-matching model. However, this task and its optimal solution fundamentally misconstrues the challenge of visual recognition in the real world, which has to deal with complex accidental variation within each category to be recognized. The dominant current vision model is provided by deep neural networks, which perform multiple stages of nonlinear transformation and learn rich knowledge about the world. Simple cognitive tasks provide a starting point, but – like the two-image discrimination task in vision – abstract away many essential features of cognition. In vision, models are tested in terms of their performance on never seen images – a generalization challenge at the heart of what vision is all about. In cognition as well, we ultimately have to engage complex tasks and test models in terms of their ability to generalize to new instances drawn randomly from a very complex space. The paper leaves me wondering how we can best take small steps from the simple tasks dominating the literature toward real-world cognitive challenges.
  • The paper does not compare a variety of models. Can we learn about the mechanism the brain employs without comparing alternative models? Rate-coded recurrent neural networks are universal approximators of dynamical systems. This property is independent of particular choices defining the units. It is entirely unsurprising that such a model, trained with stochastic gradient descent, can learn these tasks (and the supertask of performing all 20 of them). Given the simplicity of the tasks, it is also not surprising that 256 recurrent units suffice. In fact, the authors report that the results are robust between 128 and 512 recurrent units. The value of this project consists in the way it extends our imagination and generates hypotheses (to be tested with neuronal recordings) about the distributions of task-specific and task-general units. The simplicity of the model and its gradient descent training provides a compelling starting point. However, there are infinite ways a recurrent neural network might implement performance at these tasks. It will be important to contrast alternative task-performing models and adjudicate between them with brain and behavioral data.
  • The paper does not include analyses of biological recordings or behavioral data, which could help us understand the degree to which the model resembles or differs from the primate brain in the way it implements task performance.

Addressing all of these weaknesses could be considered beyond the scope of the current paper. But the authors should consider if they can go toward addressing some of them.

 

Suggested improvements

(1) It might be useful to explicitly model the 20 tasks in terms of cognitive component functions (multisensory integration, evidence accumulation, working memory, inversion of stimulus-response mapping, etc.). The resulting matrix could be added to Table 1 or shown separately. This compositional cognitive description of the tasks could be used to explain the patterns of unit involvement in different tasks (e.g. as measured by task variance) using a linear model. The compositional model could then be inferentially compared to a non-compositional model in which each task is has a single cognitive component function. This more hypothesis-driven approach might help to address the question of compositionality inferentially.

(2) The depiction of the neural network model in Figure 1 could give a better sense of the network complexity and architecture. Instead of the three-unit icon in the middle, how about a directed graph with 256 dots, one for each recurrent unit, and a separate circular arrangements of input and output units (how many were there?). Instead of the network-unit icon with the cartoon of the nonlinear activation, why not show the actual softplus function?

(3) It would the good to see the full 2562 connectivity matrix (ordered by clusters) and the network as a graph with nodes arranged by proximity in the connectivity matrix and edges colored to indicate the weights.

(4) The paper states that “the network can maintain information throughout a delay period of up to five seconds.” What does time in seconds mean in the context of the model? Is time meaningful because the units have time constants similar to biological neurons? It would be good to add supplementary text and perhaps a figure that explains how the pace of processing is matched to biological neural networks. If the pace is not compellingly matched, on the other hand, then perhaps real time units (e.g. seconds) should not be used when describing the model results.

(5) Please clarify whether the hidden units are fully recurrently connected. It would also be good to extend the paper to report how the density of recurrent connectivity affects task performance, learning, clustering and compositionality.

(6) The initial description of task variance is not entirely clear. State explicitly that one task variance estimate is computed for each task, reflecting the response variance across conditions within that task, and thus providing a measure of the stimulus-information conveyed during the task.

(7) Clustering is useful here as an exploratory and descriptive technique for dissecting the network, carving the model at its joints. However, clustering methods like k-means always output clusters, even when the data are drawn from a unimodal continuous distribution. The title claim of “clusters” thus should ideally be substantiated (by  inferential comparison to a continuous model) or dropped.

(8) The clustering will depend on the multivariate signature used to characterize each unit. Instead of task variance patterns, a unit’s connectivity (incoming and outgoing) could be used as a signature and basis of clustering. How do results compare for this method? My guess is that using the task variance pattern across tasks tends to place units in the same cluster if they contribute to the same task, although they might represent different stimulus information in the task. If this is the motivation, it would be good to explain it more explicitly.

(9) It is an interesting question whether units in the same cluster serve the same function. (It seems unlikely in the present analyses, but would be more plausible if clustering were based on incoming and outgoing weights.) The hypothesis that units in a cluster serve the same function could be made precise by saying that the units in a cluster share the same patterns of incoming and outgoing connections, except for weight noise resulting from the experiential and internal noise during training. Under this hypothesis incoming weights are exchangeable among units within the same cluster. The same holds for outgoing weights. The hypothesis could, thus, be tested by shuffling the incoming and the outgoing weights within each cluster and observing performance. I would expect performance to drop after shuffling and would interpret this as a reminder that the cluster-level summary is problematic. Alternatively, to the extent that clusters do summarize the network well, one might try to compress the network down to one unit per cluster, by combining incoming and outgoing weights (with appropriate scaling), or by training a cluster-level network to approximate the dynamics of the original network.

(10) The method of t-SNE is powerful, but its results strongly depend on the parameter settings, creating an issue of researcher degrees of freedom. Moreover, the objective function is difficult to state precisely in a single sentence (if you disagree, please try). Multidimensional scaling by contrast uses a range of objective functions that are easy to define in a single sentence. I wonder why t-SNE should be preferred in this particular context.

(11) Another way to address compositionality would be to assess whether a new task can be more rapidly acquired if its components have been trained as part of other tasks previously.

(12) In Fig. 3 c and e, label the horizontal axis (cluster).

(13) It is great that the Tensorflow implementation will be shared. It would be good if the model data could also be shared in formats useful to people using Python as well as Matlab. This could be a great resource for students and researchers. Please state more completely in the main paper exactly what (Python code? Task and model code? Model data?) will be available where (Github?).

(14) After sequential training, performance at multisensory delayed decision making does not appear to suffer compared to interleaved training. Was this because multisensory delayed decision making was always the last task (thus not overwritten) or is it more robust because it shares more components with other tasks?

(15) A better word for “linear summation” is “sum”.

Deep convolutional networks explain substantial variance in fMRI responses during movie viewing

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Wen, Shi, Zhang, Lu & Liu (pp2016) used a deep feedforward convolutional neural network (CNN) as an encoding model for fMRI data acquired while human subjects viewed movies. Previous studies (Yamins et al. 2014; Khaligh-Razavi & Kriegeskorte 2014; Güçlü & van Gerven 2015; Eickenberg et al. 2016) found that deep convolutional networks provide good models of the representation of natural images in higher ventral-stream areas. Wen et al.’s deep-net prediction of fMRI responses during movie viewing extends these findings to dynamic viewing conditions (see also Eickenberg et al. 2016 for initial deep net analyses of movie fMRI data).

The deep net was similar to AlexNet in architecture and had been trained to classify static images. The model processed each frame separately through its purely feedforward hierarchy and had no mechanism for recognising visual motion and more complex visual dynamics. Nevertheless, it did quite well at explaining visual fMRI responses during movie viewing. This is perhaps expected based on previous studies of fMRI responses during movie viewing (Hasson et al. 2001), which showed that category-selective regions respond as expected during movie viewing, when their preferred categories are present in the scene.

The authors conduct a series of original and well-motivated analyses, including decoding and deconvolution, to explore the degree to which the deep network captures the dynamic representations at multiple levels. Overall, this is a technically excellent study providing further evidence that deep feedforward neural networks constitute good models of ventral-stream responses, with layers roughly corresponding to stages of processing along the ventral stream.

Results are largely consistent with expectations from previous studies, but the study is a good contribution because it replicates and generalises earlier findings. We are wondering whether more novel insights could be gained by empirically demonstrating the limitations of the model (feedforward, no motion or dynamic perception). This could be achieved by showing that the model does not explain all the explainable variance in the data and where in the brain the deep convolutional feedforward model falls short. Eventually, the field will need to compare multiple deep neural network models (including feedword models that take multiple frames as input, and recurrent models that can dynamically compress the recent stimulus history as biological visual systems probably do).

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Figure: Visualising the image features that drive fMRI voxel responses in the context of particular images. Using the deconvolutional visualisation technique of Zeiler & Fergus on voxel encoding models (deep convolutional network + ridge regression), enables the authors to visualise to what extent adjusting pixels of a particular image (photos on the left) would change the encoding model’s prediction about voxel activity. Results shown here are for three voxels at different stages of the hierarchy. Voxel 4 has a localised central small receptive  field. Voxels 5 and 6 have larger receptive fields.

 

Main findings

Voxel-to-units matching characterises cortical responses

The paper demonstrates the functional alignment between the visual cortex and the CNN using a simple and effective method: each voxel’s time course during movie viewing is correlated with the output of each CNN unit when exposed to the frames of the movie (after convolution with a kernel to account for the delay and smoothness of the hemodynamic response). The highest-correlating units are then considered as matches. Note that this simple matching of each voxel to a set of units is easier to interpret than fitting a linear encoding model, which would have continuous weights spread over a large number of units. A disadvantage of simple voxel-to-unit matching might be that it doesn’t account for the averaging in fMRI voxels.

  • For early visual areas, the authors estimate population receptive field properties of each voxel by averaging the matching CNN units’ receptive field properties. The authors restrict this analysis to layer 1 of the CNN and recover plausible retinotopic maps from the movie responses with this method.
  • Across the stages of the visual hierarchy, the authors label each voxel with the CNN layer that best explains it (see also Güçlü & van Gerven 2015). Here the authors assigned each voxel to the CNN layer containing the unit that achieved the maximum correlation with the voxel response. Consistent with the previous studies, this reveals a largely monotonic correspondence between the stages of the visual hierarchy and the layers of the CNN.

 

The CNN layer-8 face detector unit is correlated with the fusiform face area

The authors correlated voxels with an output unit trained to detect faces. The resulting univariate brain map highlights face-selective regions, including the fusiform face area (FFA). We already knew that FFA responds to faces, and does so during natural vision (movies; e.g. work by Hasson et al.). We also know that CNNs can recognise faces. Putting these together, CNNs must be able to predict responses of the FFA to some degree. Indeed previous studies have already explicitly shown that CNNs explain variance in FFA (Khaligh-Razavi et al. 2014, Fig. S3b; Eickenberg et al. 2016). Being able to detect faces is necessary for a computational account of FFA, but it is not sufficient. We are left wondering whether the model can explain the FFA profile of activation within faces and within inanimate images (Mur et al. 2012) or the representational geometry within those two categories.

 

Encoding models linearly combining CNN units can predict voxel responses to novel movie segments

The authors used CNN units as nonlinear image features of ridge regression models of voxel responses. They logarithmically transformed the CNN outputs to model a saturating response that better matches the distribution of fMRI response amplitudes across images. They convolved the unit responses to movie frames with a hemodynamic response function to model the smoothness and delay of fMRI responses. As in previous studies, these models were tested for generalisation to novel stimuli (different movie segments here). They explained significant variance across large swaths of visual cortex.

 

FFA encoding model prefers face images

The authors attempted to visualise the preferences of the FFA by presenting 20,400 images from the same 15 categories to the encoding model. These images were not used for training the deep net and were not part of the fMRI experiments used to train the encoding model. Of the 1,000 (out of 20,400) images, for which the FFA voxel’s encoding model predicted the greatest response, 90.4% were faces.

The authors then averaged the images most strongly driving the FFA encoding model. They state: “Strikingly, the average visualization showed a blurred but discernable picture of a human face (Fig. 3.c, middle). For the first time, this result provides the direct visualization of the highly face-selective functional representation at FFA.”

This result is not particularly compelling and invites incorrect interpretations. It reflects the known fact that FFA responds to faces (Kanwisher et al. 1997) and the central/frontal-view bias for faces in the image set used to make the visualisation. Visualising the FFA response as an image template misses the point of a deep hierarchy of nonlinear transformation: If an image template could characterise the response of FFA, multiple nonlinear transformations would not be needed.

To test for the necessity of multiple nonlinear stages, the encoding model could be replaced by a template matcher. More generally, model compression could be used to attempt to explain the FFA response with a shallower model. This might yield deeper insights into the computations underlying FFA responses.

 

Deep convolutional encoding models can be combined with deconvolutional inversion to visualise what image features drive individual voxels

The authors use the deconvolutional visualisation technique of Zeiler & Fergus on voxel encoding models (deep convolutional network + ridge regression). This is a good idea. It enables the authors to visualise, for a particular image, what pixels most strongly affect the encoding model’s prediction of voxel activity. Again, a single template image cannot characterise a deep convolutional encoding model. However, looking at the encoding model’s gradient in image space in the context of many probe images might help us understand the model’s computation.

 

Images and semantic categories can be decoded not only within, but also between subjects

The authors analyse to what extent encoding and decoding models fitted with one subject’s data generalise to other subjects. It’s good to have these analyses in the paper because they give us a more quantitative sense of the degree to which the anatomical intersubject alignment succeeds at matching up functionally similar responses. As expected, within-subject encoding and decoding predictions are more accurate, but generalisation across subjects does work somewhat.

 

Decoding models can reconstruct natural movie stimuli and reveal semantic categories

The authors estimated multivariate regression models to predict time-varying feature maps of CNN layer 1 based on distributed cortical fMRI signals. Training was performed using an L1 (sparsity encouraging) penalty on the weights and random dropping out of a subset of the voxels during training with stochastic gradient descent. The layer-1 representation was then converted back to an image. As expected from previous studies (Thirion et al., Nishimoto et al., Miyawaki et al.) this works to some extent, highlighting regions of the image with high edge energy. The authors also decode semantic categories, which works quite well (again, not unexpectedly).

 

Strengths

  • tests a task-performing neurobiologically plausible (though abstract) deep neural network model
  • replicates previous findings on deep convolutional nets as models of fMRI visual responses and generalises these findings to movie viewing
  • analyses technically excellent in many respects
  • analyses are comprehensive and well motivated
  • brings the deconvolutional technique of for visualization of the model unit preferences (as gradient in image space in the context of particular preferred images) into the analysis of brain data
  • high-quality figures
  • well written

 

Weaknesses

  • The authors follow the widespread approach of looking to confirm what the field already believes. The rationale of this approach could be described as follows: “Here’s a really cool and novel demonstration of what you already believe.” It is as though we are afraid to learn something new or do not trust our methods unless they confirm current opinion. If our methods are sound, we should be able to apply them to questions whose answers we don’t know yet. As a result, the analyses here largely confirm what we know (or think we know) rather than providing surprising or contradictory new leads.
  • Some of the analyses shown are affected by selection bias. This is a widespread problem in systems neuroscience (Kriegeskorte et al. 2009). While the authors are certainly aware of the related challenges of overfitting, circularity, and selection bias (using separate training and test sets for both deep net training, and the fitting of encoding models), selective presentation of results in Figs. 2d, 3a, 7 might be misleading. It’s important to note that this problematic practice is widespread, motivated by a rationale that could be stated as follows: “Let me show what you already believe in a beautiful graph based on data selected to conform with what you believe and therefore biased (to an unknown degree) to confirm your belief.”

 

Points the authors may wish to address in revision

Selection bias

State clearly what data and criteria have been used to select voxels and ROIs whose results are shown (Figs. 2d, 3a, 3c, 7). Use independent data sets (1) for selection and ROI definition and (2) for estimating and plotting effects in the ROIs.

 

Inference must account for serial autocorrelation of fMRI time courses

Time points in fMRI are highly dependent, so cannot be considered exchangeable under H0. You could use prewhitening (e.g. the Cochrane-Orcutt method) or simulate a realistic null distribution by block permutation. Temporal block permutation could use long blocks and just enough of them to have a sufficient number of permutations. Some contexts where this applies are as follows:

  • “The significance of the cross correlation was assessed by calculating the p-value with the degree of freedom equal to the number of time points minus 2 (DOF=238, p<0.001, Bonferroni correction for the number of voxels).”
  • “The significance of the cross correlation was assessed by calculating the p-value with the degree of freedom equal to the number of time points minus 2 (DOF=238 with Bonferroni correction to account for the number of voxels and p<0.001).”
  • “To test the statistical significance of the average prediction accuracy, we performed a permutation test. From the fMRI-estimated feature maps, a large set of permuted feature maps were created by randomly and temporally shuffling the estimated feature maps for 10000 times.”
    The shuffled entities should not be single time points.
  • “For example, a ‘face’ neuron in the CNN was significantly correlated with the fusiform face area (FFA) (r=0.25±0.057, p<0.01, corrected) (Fig. 2.d, right).” Does this take serial autocorrelation into account?

 

Analyse where the deep convolutional net falls short

It would be great to visualise the ways the deep convolutional encoding model falls short.

  • To what extent can the replicable movie-responses in higher parietal, temporal and frontal cortices that appear in Fig. 2a be explained by the deep net? What layers best explain them?
  • In addition to the whole-brain cortical surface map of where the deep net explains significant variance, it would be good to see where it explains significantly less variance than another measurement for the same subject and the same movie segment. This would reveal where in the brain the deep net fails to explain all explainable variance.
  • It would also be good to show what aspects of visual responses the deep net misses in regions where it performs well overall. One way to do this would be to compare the fMRI-based image reconstruction to an image reconstruction obtained with the same method from the encoding-model-predicted fMRI responses. We might expect, for example, that the encoding model misses the attentional mechanisms of the brain. The reconstructions from the encoding model prediction might therefore reflect the edge energy in the image, equally representing foreground object and background scene, whereas the fMRI reconstruction reflects attentional selection of the foreground object.

 

Deconvolution cannot invert a deep convolutional feedforward network

Several passages in the paper currently suggest that deconvolution exactly inverts the convolutional feedforward processing, for example:

  • “It is worth noting that nonlinear features coded in the CNN were not isolated functions, but connected through hierarchical networks that are fully computable either bottom-up or top-down.”
  • “In addition, the model is fully observable and computable both forward and backward (Zeiler and Fergus, 2014), such that the extracted features can be transformed, either top-down or bottom-up, to visualize their internal representations, to reconstruct the visual input, as well as to deduce its semantic categorization.”

However, rectified linear units and max-pooling are noninvertible, image-dependent switches and “transpose as inverse” only provide approximations, and many dimensions are intentionally discarded across stages of the feedforward hierarchy. Please clarify these approximations and how they relate to (a) the goal of reconstruction of the image and (b) the goal to visualise the image features driving particular model responses.

 

Open science

Will data and code be available for other researchers to build on the findings?

 

Image reconstruction with error-flow from all layers

Reconstruction of natural movie stimuli is performed based on the decoding from fMRI of the 1st layer of the CNN only. Higher layers of the CNN should be better decodable from higher cortical regions. The ideal reconstruction would simultaneously decode all layers of the CNN from all cortical regions, using this information as a joint constraint for image reconstruction. Image reconstruction could rely on backpropagation down to the image input, with error flow from all layers of the CNN.

fMRI-like preprocessing of the CNN outputs

The authors take the logarithm of CNN outputs and convolve with an HRF model kernel peaking at 4 s latency. It would be good to know how this reasonable approach performs in comparison to other approaches, e.g. leaving out the logarithmic transform and/or estimating the HRF and its peak latency for each voxel (e.g. Pedregosa et al. pp2014).

 

Motivation for different weight priors implicit to regularisation in encoding and decoding

In the encoding models, the weight regularizer is an L2 penalty (ridge regression), whereas in the decoding models it is an L1 penalty (LASSO).

  • What’s the motivation for these choices?
  • Were both approaches tried for both encoding and decoding? If results were different, what would be the implications?
  • What is the motivation for dropout (another approach to regularisation) in fitting the decoders? Is it to prevent informative voxels to be pushed down because the L1 penalty encourages sparsity?

 

Language

There are some typos and minor grammatical errors (e.g. “in details” -> “in detail”).

 

– Nikolaus Kriegeskorte & Johannes Mehrer

Can the contents of consciousness be decoded from patterns of integrated information?

[I8R5]

Consciousness is fascinating and elusive. There is “the hard problem” of how the dynamics of matter can give rise to subjective experience. “The hard problem” (Chalmers) is how some philosophers describe their own job, a job that is both appropriately glamorous and career safe, because it is not about to be taken away from them anytime soon and so difficult that lack of progress in our lifetime cannot reasonably be held against them. Brain scientists are left with “the easy problem” of explaining how the brain supports perception, cognition, and action. What’s taking so long?

Transcending this division of labour, at the intersection between philosophy and brain science, researchers are working on what Anil Seth has called “the real problem”:

“how to account for the various properties of consciousness in terms of biological mechanisms; without pretending it doesn’t exist (easy problem) and without worrying too much about explaining its existence in the first place (hard problem).”

There is a range of interesting ideas toward a theory of consciousness, from metaphors like “fame in the brain” to detailed accounts like the “neuronal global workspace” (Baars, Dehaene). In my mind, it remains unclear to what extent existing proposals are alternative theories that are mutually exclusive or complementary descriptions of the same set of phenomena.

One of the more inspiring sets of ideas about consciousness is integrated information theory (Tononi). IIT posits that consciousness arises from the interactions between the parts of a physical system and allows of degrees. The degree of consciousness of a system can be measured by an index of the overall interactivity among the parts.

States of heightened consciousness are states in which we experience an enhanced capacity to bring together in the present moment all we perceive and all we know with our needs and goals, toward adaptive action.

Our brains, mysteriously, perform an amazing feat of flexible integration of information across many scales of time (from long-term memories to our current situational model and to the momentary glimpse, in which we sense the states of motion of the objects around us), across our peripersonal space (from the scene surrounding us, in memory, to the fixated point), and across sensory modalities (as we combine what we see, hear, feel, smell and taste into an amodal percept of the scene).

And this is just the perceptual part of the process, which is integrated with our sense of current needs and goals to guide our action. It is plausible that this feat of intelligence, which is unmatched by current AI systems, requires high-bandwidth interactions between the brain components that sustain it. IIT suggests that those pieces of information, from perception or memory, that are currently most richly interrelated are the conscious ones. This doesn’t follow, but it is an interesting idea.

Intuitions about social interaction similarly suggest that interactivity is essential for efficient information processing. For example, it is difficult to imagine a team of people working together optimally efficiently on a complex task, if a subset of them is not integrated, i.e. does not interact with the rest of the group. Of course, there are simple tasks, for which independent toiling is optimal. I’m thinking here of tasks that do not require considering all the relationships between subsets of the input. But for complex tasks, like writing a paper, we might expect substantial interactivity to be required.

In computer science, NP hard tasks are those, for which no trick exists that would enable us to partition the elements into a manageable set of subsets, and tackle each in turn. Instead relationships among elements may need to be considered for all subsets, and the number of subsets is exponential in the number of the elements. The elements have to be brought into contact somehow, so we expect the system that can solve the task efficiently to be highly interactive.

A key idea of IIT is that a conscious system should be well integrated in the sense that no matter how we partition it, the partitions are highly interactive. IIT uses information theoretic measures to quantify integrated information. These measures are related to Granger causality. For two components A and B, A is said to Granger-cause B if the past values of A help predict B, beyond what can be achieved by considering only the past of B itself. For the same system composed of parts A and B, a measure of integrated information would assess to what extent taking the interactions between A and B into account enables us to better predict the state of the system (comprising both A and B) than ignoring the interactions.

For a more complex system, integrated information measures consider all subsets. The integrated information of the whole is the maximum of the integrated information values of the subsets. In other words, the system inherits its level of integrated information φmax from its most strongly interactive clique of components. Each subset’s interactivity is judged by the degree to which it cannot be partitioned (and interactions across partitions ignored) in predicting the current state from the past. A system is considered highly interactive if any partitioning greatly reduces an estimate of the mutual information between its past and present states.

Note that to achieve high integrated information, the information flow must not simply spread the information, rendering it redundant across the parts. Rather the information in different parts must be complementary and must be encoded such that it needs to be considered jointly to reveal its meaning.

For example, consider binary variables X, Y, and Z. X and Y are independent uniform random variables and Z = X xor Y, i.e. Z=1 if either X or Y is 1, but not both. Each variable then has an entropy of one bit. X and Y each singly contain no information about Z. Being told X does not tell us anything about Z, because Y is needed to interpret the information X conveys about Z. Conversely, X is needed to interpret the information Y conveys about Z. X and Y together perfectly determine Z. (The mutual information I(X;Z) = 0, the mutual information I(Y;Z)=0, but the mutual information I(X,Y;Z) = 1 bit.)

screenshot1365

Figure | The continuous flash suppression paradigm used by the authors. A stimulus presented to one eye is rendered invisible by a sequence of Mondrian images presented to the other eye.

In a new paper, Haun, Oizumi, Kovach, Kawasaki, Oya, Howard, Adolphs, and Tsuchiya (pp2016) derive some interesting predictions from integrated information theory and test them with electrocorticography, measuring neuronal activity in human patients that have implanted subdural electrodes in their brains. The authors use the established psychophysical paradigms of continuous flash suppression and backward masking to render stimuli that are processed in cortex subjectively invisible and their representations, thus, unconscious.

The paper uses the previously described measure φ* of integrated information. This measure uses estimates of mutual information between past and present states of a set of measurement channels. The mutual information is estimated on the basis of multivariate Gaussian assumptions. Computing φ* involves estimating the effects of partitioning the set of channels, by modelling the partition distributions as independent (i.e. the joint distribution obtains as the product of the partitions’ distribution). φ* is the loss in system past-to-present predictability incurred by the least destructive partitioning.

The paper introduces the concept of the φ* pattern, the pattern of φ* estimates across subsets of components of the system (where electrodes pragmatically serve to define the components). The  φ* pattern is hypothesized to reflect the compositional structure of the conscious percept.

Results suggest that stronger φ* values for certain sets of electrodes in the fusiform gyrus, which pick up on face-selective responses, are associated with conscious percepts of faces (as opposed to Mondrian images or visual noise). This association holds even across sets of trials, where the physical stimulus was identical and only the internal dynamics rendered the face representation conscious or unconscious. The authors argue that these results support IIT and suggest that the φ* pattern reflects information about the conscious percept.

 

Strengths

  • The ideas in the paper are creative, provocative, and inspiring.
  • The paper uses well-established psychophysical paradigms to control the contents of consciousness and disentangle conscious perception from stimulus representation.
  • The φ* measure is well motivated by IIT and has been introduced in earlier work involving some of the authors – even if its relationship to consciousness is speculative.

 

Weaknesses

  • The authors introduce the φ* pattern and hypothesize that it reflects the compositional structure of conscious content. However, theoretically, it is unclear why it should be that pattern across subsets of components, rather than simply the pattern across components that reflects the compositional structure of conscious content. Empirically, results are most parsimoniously summarised by saying that φ* tends to be larger when the content represented by the underlying neuronal population is conscious. The evidence for a reflection of the compositional structure of conscious content in the φ* pattern is weak.
  • It is unclear how φ* is related to the overall activity in sets of neurons selective for the perceptual content in question (faces here). This leaves open the possibility that face selective neurons are simply more active when the face percept is conscious and this greater activity is associated with greater interactivity among the neurons, reflecting their structural connectivity.
  • The finding that the alternative measures, state entropy H and (past-present) mutual information I, are less predictive of conscious percepts does not provide strong constraints on theory, because these measures are not particularly plausible to begin with and no compelling theoretical motivation is given for them.
  • IIT suggests that integrated information across the entire brain supports consciousness. An unavoidable challenge for empirical studies, as the authors appropriately discuss, is the limitation of the φ* estimates to small sets of empirical measurements of brain activity.

 

Particular points the authors may wish to address in revision

(1) Are face-selective populations of neurons simply more active when a face is consciously perceived and φ* rises as an epiphenomenon of greater activity in the interconnected set of neurons?

It is left unclear whether the level of percept-specific neuronal activity provides a comparably good or better neural correlate of conscious content. The data presented have been analysed with more conventional activity-based pattern classification in Baroni et al. (pp2016) and results suggest that this also works. What if the substrate of consciousness is simply strong activity or activity in certain frequency bands and the φ* just happens to be a measure correlated with those simpler measures in a population of neurons? After all, we would expect an interconnected neuronal population to exhibit greater dynamic interactivity when it is strongly driven by a stimulus. The key challenge left unaddressed is to demonstrate that φ* cannot be reduced to this classical neuronal correlate of perceptual content. Do the two tend to be correlated? Can they be disentangled experimentally?

A compelling demonstration would be to show that φ* (or another IIT-motivated measure) captures variance in conscious content that is not explained by conventional decoding features. For example, two populations of neurons – one coding a face, the other a Mondrian – might be equally activated overall by a stimulus containing both a face and a Mondrian, but φ* computed for each population might enable us to predict the consciously perceived stimulus on a trial-by-trial basis.

 

(2) Does the φ* pattern reflect the conscious percept and its compositional structure?

A demonstration that the φ* pattern (across subsets) reflects the compositional structure of the content of consciousness would require an experiment eliciting a wider range of conscious percepts that are composed of a set of elements in different combinations.

The authors’ hypothesis would then have to be compared to a range of simpler hypotheses about the neural correlates of compositional conscious content (NC4) , including the following:

  • the pattern of activity across content-selective neural sites
    (rather than the across a subsets of sites)
  • the pattern of activity across subsets of sites
  • the connectivity across content-selective neural sites (where connectivity could be measured by synchrony, coherence, Granger causality or any other measure of the relationship between two sites)
  • the connectivity across content-selective neural subsets of sites

This list could be expanded indefinitely and could include a variety of IIT-inspired but distinct NC4s. There are many ideas that are similarly theoretically plausible, so empirical tests might be the best way forward.

In the discussion the authors argue that integrated information has greater a priori theoretical support than arbitrary alternative neural correlates of consciousness. There is some truth to that. However, the theoretical motivation, while plausible and and interesting, is not so uniquely compelling that it supports lowering the bar of empirical confirmation for IIT measures.

 

(3) Might the selection of channels by maximum φ* have introduced a bias to the analyses?

I understand that the selection was performed without using the conscious/unconscious trial labels. However, conscious percepts are likely to be associated with greater activity, and φ* might be confounded by greater activity. More generally, selection biases are often complicated, and without a compelling demonstration that there can be no selection bias, it is difficult to be confident. A simple way to rule out selection bias is to use independent data for selection and selective analysis.

 

– Nikolaus Kriegeskorte

 

Acknowledgement

I thank Kate Storrs for discussing integrated information theory with me.

Discrete-event-sequence model reveals the multi-time-scale brain representation of experience and recall

[I8R7]

Baldassano, Chen, Zadbood, Pillow, Hasson & Norman (pp2016) investigated brain representations of event sequences with fMRI. The paper argues in favour of an intriguing and comprehensive account of the representation of event sequences in the brain as we experience them, their storage in episodic memory, and their later recall.

The overall story is quite amazing and goes like this: Event sequences are represented at multiple time scales across brain regions during experience. The brain somehow parses the continuous stream of experience into discrete pieces, called events. This temporal segmentation occurs at multiple temporal scales, corresponding perhaps to a tree of higher-level (longer) events and subevents. Whether the lower-level events precisely subdivide higher-level events (rendering the multiscale structure a tree) is an open question, but at least different regions represent event structure at different scales. Each brain region has its particular time scale and represents an event as a spatial pattern of activity. The encoding in episodic memory does not occur continuously, but rather in bursts following the event transitions at one of the longer time scales. During recall from memory, the event representations are reinstated, initially in the higher-level regions, from which the more detailed temporal structure may come to be associated in the lower-level regions. Event representations can arise from perceptual experience (a movie here), recall (telling the story), or from listening to a narration. If the event sequence of a narration is familiar, memory recall can help reinstate representations upcoming in the narration in advance.

There’s previous evidence for event segmentation (Zacks et al. 2007) and multi-time-scale representation (from regional-mean activation to movies that are temporally scrambled at different temporal scales; Hasson et al. 2008; see also Hasson et al. 2015) and for increased hippocampal activity at event boundaries (Ben-Yakov et al. 2013). However, the present study investigates pattern representations and introduces a novel model for discovering the inherent sequence of event representations in regional multivariate fMRI pattern time courses.

The model assumes that a region represents each event k = 1..K as a static spatial pattern mk of activity that lasts for the duration of the event and is followed by a different static pattern mk+1 representing the next event. This idea is formalised in a Hidden Markov Model with K hidden states arranged in sequence with transitions (to the next time point) leading either to the same state (remain) or to the next state (switch). Each state k is associated with a regional activity pattern mk, which remains static for the duration of the state (the event). The number of events for a given region’s representation of, say, 50 minutes’ experience of a movie is chosen so as to maximise within-event minus between-event pattern correlation on a held-out subject.

It’s a highly inspired paper and a fun read. Many of the analyses are compelling. The authors argue for such a comprehensive set of claims that it’s a tall order for any single paper to fully substantiate all of them. My feeling is that the authors are definitely onto something. However, as usual there may be alternative explanations for some of the results and I am left with many questions.

 

Strengths

  • The paper is very ambitious, both in terms brain theory and in terms of analysis methodology.
  • The Hidden Markov Model of event sequence representation is well motivated, original, and exciting. I think this has great potential for future studies.
  • The overall account of multi-time-scale event representation, episodic memory encoding, and recall is plausible and fascinating.

 

Weaknesses

  • Incomplete description and validation of the new method: The Hidden Markov Model is great and quite well described. However, the paper covers a lot of ground, both in terms of the different data sets, the range of phenomena tackled (experience, memory, recall, multimodal representation, memory-based prediction), the brain regions analysed (many regions across the entire brain), and the methodology (novel complex method). This is impressive, but it also means that there is not much space to fully explain everything. As a result there are several important aspects of the analysis that I am not confident I fully understood. It would be good to describe the new method in a separate paper where there is enough space to validate and discuss it in detail. In addition, the present paper needs a methods figure and a more step-by-step description to explain the pattern analyses.
  • The content and spatial grain of the event representations is unclear. The analyses focus on the sequence of events and the degree to which the measured pattern is more similar within than between inferred event boundaries. Although this is a good idea, I would have more confidence in the claims if the content of the representations was explicitly investigated (e.g. representational patterns that recur during the movie experience could represent recurring elements of the scenes).
  • Not all claims are fully justified. The paper claims that events are represented by static patterns, but this is a model assumption, not something demonstrated with the data. It’s also claimed that event boundaries trigger storage in long-term memory, but hippocampal activity appears to rise before event boundaries (with the hemodynamic peak slightly after the boundaries). The paper could even more clearly explain exactly what previous studies showed, what was assumed in the model (e.g. static spatial activity patterns representing the current event) and what was discovered from the data (event sequence in each region).

 

Particular points the authors may wish to address in revision

 (1) Do the analyses reflect fine-grained pattern representations?

The description of exactly how evidence is related between subjects is not entirely clear. However, several statements suggest that the analysis assumes that representational patterns are aligned across subjects, such that they can be directly compared and averaged across subjects. The MNI-based intersubject correspondency is going to be very imprecise. I would expect that the assumption of intersubject spatial correspondence lowers the de facto resolution from 3 mm to about a centimetre. The searchlight was a very big (7 voxels = 2.1cm)3 cube, so perhaps still contained some coarse-scale pattern information.

However, even if there is evidence for some degree of intersubject spatial correspondence (as the authors say results in Chen et al. 2016 suggest), I think it would be preferable to perform the analyses in a way that is sensitive also to fine-grained pattern information that does not align across subjects in MNI space. To this end patterns could be appended, instead of averaged, across subjects along the spatial (i.e. voxel) dimension, or higher-level statistics, such as time-by-time pattern dissimilarities, could averaged across subjects.

If the analyses really rely on MNI intersubject correspondency, then the term “fine-grained” seems inappropriate. In either case, the question of the grain of the representational patterns should be explicitly discussed.

 

(2) What is the content of the event representations?

The Hidden Markov Model is great for capturing the boundaries between events. However, it does not capture the meaning and relationships between the event representations. It would be great to see the full time-by-time representational dissimilarity matrices (RDMs; or pattern similarity matrices) for multiple regions (and for single subjects and averaged across subjects). It would also be useful to average the dissimilarities within each pair of events to obtain event-by-event RDMs. These should reveal, when events recur in the movie, and the degree of similarity of different events in each brain region. If each event were unique in the movie experience, these RDMs would have a diagonal structure. Analysing the content of the event representations in some way seems essential to the interpretation that the patterns represent events.

 

(3) Why do the time-by-time pattern similarity matrices look so low-dimensional?

The pattern correlations shown in Figure 2 for precuneus and V1 are very high in absolute value and seem to span the entire range from -1 to 1. (Are the patterns averaged across all subjects?) It looks like two events either have highly correlated or highly anticorrelated patterns. This would suggest that there are only two event representations and each event falls into one of two categories. Perhaps there are intermediate values, but the structure of these matrices looks low-dimensional (essentially 1 dimensional) to me. The strong negative correlations might be produced by the way the data are processed, which could be more clearly described. For example, if the ensemble of patterns were centered in the response space by subtracting the mean pattern from each pattern, then strong negative correlations would arise.

I am wondering to what extent these matrices might reflect coarse-scale overall activation fluctuations rather than detailed representations of individual events. The correlation distance removes the mean from each pattern, but usually different voxels respond with different gains, so activation scales rather than translates the pattern up. When patterns are centered in response space, 1-dimensional overall activation dynamics can lead to the appearance of correlated and anticorrelated pattern states (along with intermediate correlations) as seen here.

This concern relates also to points (1) and (2) above and could be addressed by analysing fine-grained within-subject patterns and the content of the event representations.

screenshot1350

Detail from Figure 2: Time-by-time regional spatial-pattern correlation matrices.
Precuneus (top) and V1 (bottom).

 

(4) Do brain regions really represent a discrete sequence of events by a discrete sequence of patterns?

The paper currently claims to show that brain regions represent events as static patterns, with sudden switches at the event boundaries. However, this is not something that is demonstrated from the data, rather it is the assumption built into the Hidden Markov Model.

I very much like the Hidden Markov Model, because it provides a data-driven way to discover the event boundaries. The model assumption of static patterns and sudden switches are fine for this purpose because they may provide an approximation to what is really going on. Sudden switches are plausible, since transitions between events are sudden cognitive phenomena. However, it seems unlikely that patterns are static within events. This claim should be removed or substantiated by an inferential comparison of the static-pattern sequence model with an alternative model that allows for dynamic patterns within each event.

 

(5) Why use the contrast of within- and between-event pattern correlation in held-out subjects as the criterion for evaluating the performance of the Hidden Markov Model?

If patterns are assumed to be aligned between subjects, the Hidden Markov Model could be used to directly predict the pattern time course in a held-out subject. (Predicting the average of the training subjects’ pattern time courses would provide a noise ceiling.) The within- minus between-event pattern correlation has the advantage that it doesn’t require the assumption of intersubject pattern alignment, but this advantage appears not to be exploited here. The within- minus between-event pattern correlation seems problematic here because patterns acquired closer in time tend to be more similar (Henriksson et al. 2015). First, the average within-event correlation should always tend to be larger than the average between-event correlation (unless the average between-event correlation were estimated from the same distribution of temporal lags). Such a positive bias would be no problem for comparing between different segmentations. However, if temporally close patterns are more similar, then even in the absence of any event structure, we expect that a certain number of events best captures the similarity among temporally closeby patterns. The inference of the best number of events would then be biased toward the number of events, which best captures the continuous autocorrelation.

 

(6) More details on the recall reactivation

Fig. 5a is great. However, this is a complex analysis and it would be good to see this in all subjects and to also see the movie-to-recall pattern similarity matrix, with the human annotations-based and Hidden Markov Model-based time-warp trajectories superimposed. This would enable us to better understand the data and how the Hidden Markov Model arrives at the assignment of corresponding events.

In addition, it would be good to show statistically, that the Hidden Markov Model predicts the content correspondence between movie and recall representations consistently with the human annotations.

 

(7) fMRI is a hemodynamic measure, not “neural data”.

“Using a data-driven event segmentation model that can identify temporal structure directly from neural measurements”; “Our results are the first to demonstrate a number of key predictions of event segmentation theory (Zacks et al., 2007) directly from neural data”

There are a couple of other places, where “neural data” is used. Better terms include “fMRI data” and “brain activity patterns”.

 

(8) Is the structure of the multi-time-scale event segmentation a tree?

Do all regions that represent the same time-scale have the same event boundaries? Or do they provide alternative temporal segmentations? If it is the former, do short-time-scale regions strictly subdivide the segmentation of longer-time-scale regions, thus making the event structure a tree? Fig. 1 appears to be designed so as not to imply this claim. Data, of course, is noisy, so we don’t expect a perfect tree to emerge in the analysis, even if our brains did segment experience into a perfect tree. It would be good to perform an explicit statistical comparison between the temporal-tree event segmentation hypothesis and the more general multi-time-scale event segmentation hypothesis.

 

(9) Isn’t it a foregone conclusion that longer-time-scale regions’ temporal boundaries will match better to human annotated boundaries?

“We then measured, for each brain searchlight, what fraction of its neurally-defined boundaries were close to (within three time points of) a human-labeled event boundary.”

For a region with twice as many boundaries as another region, this fraction is halved even if both regions match all human labeled events. This analysis therefore appears strongly confounded by the number of events a regions represents.

The confound could be removed by having humans segment the movie at multiple scales (or having them segment at a short time scale and assign saliency ratings to the boundaries). The number of events could then be matched before comparing segmentations between human observers and brain regions.

Conversely, and without requiring more human annotations, the HMM could be constrained to the number of events labelled by humans for each searchlight location. This would ensure that the fraction of matches to human observers’ boundaries can be compared between regions.

 

(10) Hippocampus response does not appear to be “triggered” by the end of the event, but starts much earlier.

The hemodynamic peak is about 2-3 s after the event boundary, so we should expect the neural activity to begin well before the event boundary.

 

(11) Is the time scale a region represents reflected in the temporal power spectrum of spontaneous fluctuations?

The studies presenting such evidence are cited, but it would be good to look at the temporal power spectrum also for the present data and relate these two perspectives. I don’t think the case for event representation by static patterns is quite compelling (yet). Looking at the data also from this perspective may help us get a fuller picture.

 

(12) The title and some of the terminology is ambiguous

The title “Discovering event structure in continuous narrative perception and memory” is, perhaps intentionally, ambiguous. It is unclear who or what “discovers” the event structure. On the one hand, the brain that discovers event structure in the stream of experience. On the other hand, the Hidden Markov Model discovers good segmentations of regional pattern time courses. Although both interpretations work in retrospect, I would prefer a title that makes a point that’s clear from the beginning.

On a related note, the phrase “data-driven event segmentation model” suggests that the model performs the task of segmenting the sensory stream into events. This was initially confusing to me. In fact, what is used here is a brain-data-driven pattern time course segmentation model.

 

(13) Selection bias?

I was wondering about the possibility of selection bias (showing the data selected by brain mapping, which is biased by the selection process) for some of the figures, including Figs. 2, 4, and 7. It’s hard to resist illustrating the effects by showing selected data, but it can be misleading. Are the analyses for single searchlights? Could they be crossvalidated?

 

(14) Cubic searchlight

A spherical or surface-based searchlight would the better than a (2.1 cm)3 cube.

 

– Nikolaus Kriegeskorte

 

Acknowledgement

I thank Aya Ben-Yakov for discussing this paper with me.

 

 

 

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

[R8I7]

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.

 

ScreenShot1269.png

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).

 

 

 

screenshot1271Figure 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

[R7I7]

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

 

 

 

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:

  1. as the accuracy of prediction of a stimulus-response matrix,
  2. as the accuracy of prediction of a representational dissimilarity matrix, or
  3. 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

 

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