Neural network (NN) models have brought spectacular progress in computer vision and visual computational neuroscience over the past decade, but their performance, until recently, was quite brittle: breaking down when images are compromised by occlusions, lack of focus, distortions, and noise — sources of nuisance variation that human vision is robust to. The robustness of recognition has substantially improved in recent models with extensive training and data augmentation.

Extensive visual experience also drives the development of human visual abilities. Humans, too, experience a vast number of visual impressions, many of them compromised and all of them embedded in a context of previous visual impressions and information from other sensory modalities, including audition, that can constrain the interpretation of the scene and drive visual learning. Do state-of-the-art robust NN models provide a good model of robust recognition in humans, then?

A new paper by Huber et al. (pp2022) suggests that a training-based account of the robustness of human vision, along the lines of the recent advances in getting NN models to be more robust through extensive training, is uncompelling. Current NN models, they argue, lack some essential computational mechanisms that enables the human brain to achieve robustness with less visual experience.

The authors measured recognition abilities in 146 children and adolescents, aged 4-15, and found that even the 4-6 year-olds outperformed current NN models at recognizing images robustly under substantial local distortions (so called eidolon distortions). They argue that back-of-the-envelope estimates of the amount of visual experience suggest that humans achieve greater robustness with less training data. The human visual system must have some additional mechanism in place that current NN models lack.

One possibility is that human vision has mechanisms to perceive the global shape of objects more robustly than current NN models. Using ingenious shape-texture-cue-conflict stimuli, which they introduced in earlier work, the authors show that the well-known human bias in favor of classifying objects by their shape is already present in the 4-6 year olds. Testing the models with the shape-texture-cue-conflict stimuli showed, by contrast, that even the most extensively trained and robust NN models rely much more strongly on texture than on shape.

To compare the amount of visual experience between humans and models, the authors offer a back-of-the-envelope calculation (their appropriate term), in which they quantify human visual experience at a given age in the currency of NN models: number of images. They use estimates of the number of waking hours across childhood and of the number of fixations per second. One fixation is assumed as roughly equivalent to a training image. According to such estimates, the best model (SWAG) requires about an order of magnitude more data to reach human-level robustness.

This calculation and the corresponding figure are interesting because they provide a starting point for an important discussion. However, the estimate suggesting an order of magnitude difference in the amount of data required could easily be off by more than an order of magnitude.

More importantly, the estimate (though it is an interesting starting point) is fundamentally flawed and should be accompanied by more critical arguments. Human visual experience is temporally continuous and dependent and therefore cannot meaningfully be quantified in terms of a number of training images or exposures (counting multiple exposures to augmented versions of the same image across epochs).

It is also unclear why fixations should be equated to images. We see a dynamic world evolve at a rate much faster than the rate of fixations. Moreover, fixations are actively chosen, so their information content may be greater than that of a similar number of i.i.d. samples. (This could count as one of the qualitative differences between primate vision and current NN models: Primate visual recognition is active perception, and visual learning is active learning: The animal makes its own curriculum and this could contribute to its learning more from less data.)

A simpler calculation (and the one I couldn’t resist typing into my calculator before getting to the authors’) would equate frames (perhaps 10 per second?) to training images. Of course, frames are not a well-defined concept, either, in the context of human visual experience and, at 10 frames per second, successive frames are highly dependent. However, temporal dependency may be a critical feature, helping rather than hurting visual learning. At 10 frames per second, the calculation yields an estimate surprisingly close to the “amount of visual experience” of the state-of-the-art models.

Another reason why comparing visual experience between models and humans is inherently difficult concerns the quality, rather than the quantity, of the visual input. The out-of-distribution generalization challenge is not (and cannot readily be) matched between humans and models. Human visual experience may include more distorted inputs due to physical processes in the world such as rain and glass obscuring the scene as well as due to optical imperfections of our eyes. As a result, human visual experience may provide better training for generalizing to the eidolon distortions than the training sets used for the most extensively trained models (SWAG and SWSL).

The claims relating to the comparison of the “amount of visual experience” between humans and models should be tempered in revision and more critically discussed with a view to directions for future studies. It would also be good to add statistical inference to demonstrate that the reported effects generalize across stimuli and subjects. The error consistency analysis is important. However, I find the boxplots hard to interpret. It would be great to see inferential comparisons between different DNNs, where currently DNNs are lumped together despite the fact that there appears to be little inter-DNN error consistency.

The authors are almost certainly correct that current NN models lack essential computational mechanisms. However, I’m not sure if the estimates of the amount of visual experience in the current version of the paper provide strong evidence for the greater data efficiency of human vision.

Overall this paper describes an important, carefully designed and executed study and offers a unique open-science human developmental cross-sectional data set on object-recognition robustness for further systematic analyses. The use of state-of-the-art models and the careful discussion of the state of the field make this a great contribution.

Strengths

• Important comprehensive novel behavioral data set
• Challenge of experimenting with kids of different ages met with carefully designed and executed experiment
• All code and data available via github
• Comparison to four NN models that represent the state of the art at out-of-distribution robust recognition and span four orders of magnitude of training-set size (1M, 10M, 100M, 1B images)
• Interesting discussion highlighting the difficulty of quantifying and comparing “the amount of visual experience” between models and humans

Weaknesses

• The “back-of-the-envelope” calculation on the amount of visual experience is not just a very rough approximation, but conceptually flawed: Human visual experience is temporally continuous and dependent, and thus cannot be approximately quantified in terms of a number of i.i.d. images.
• The out-of-distribution generalization challenge is not (and cannot readily be) matched between humans and models. Human visual experience may provide better training for generalizing to the eidolon distortions than the training sets used for the most extensively trained models (SWAG and SWSL).
• Hypotheses are not evaluated by statistical inference to generalize to the populations of subjects and stimuli.
• Age may be confounded by ability to attend on the task and by factors related to participant recruitment. (However, this reflects inherent difficulties of the research not shortcomings of this particular study.)
• Model architecture is not varied systematically and independently of training regime. (However, this is very hard to achieve given the scale of the models and training sets, and they key conclusions appear compelling despite this shortcoming.)

Minor notes

“not only subjective effortless but objectively often impressive” typo: should be “subjectively”. Also: impressiveness is inherently subjective.

knive -> knife

Fig. 4: Panel labels (a), (b) should be bigger, bold and above, not below the panels. The top should be a.

Fig. 4a: The logarithmic horizontal axis tick labels are inconsistent between the panels.

Fig. 5 (left): accuracy delta should be described “4-6 year-olds minus adults”, not vice versa

Proprioception is our sense of the motion and posture of our own body. This sixth sense uses signals from receptors in the joints, tendons, muscles, and skin that measure forces and degrees of extension. These receptors enable us to sense, for example, the posture of our body as we wake from sleep. They also provide feedback signals that help us precisely control our limbs, for example during handwriting.

Feedback is thought to be essential to motor control, enabling the controller in our brains to rapidly adapt to the unexpected. The unexpected may include changes in the environment (like something  pushing our hand that we didn’t see coming), changes in our bodies (such as muscle fatigue or injury), and shortcomings of the motor program (such as a lack of precision or a badly planned limb trajectory). Feedback can come from vision and even audition, but proprioception provides an essential additional feedback path that informs us directly about the motion and posture of our limbs, and any forces on them.

How does feedback control work in the human motor system? I want to write a ‘k’, but there are forces on my limbs resulting from the friction of chalk on this particular blackboard. Also, my muscles are recovering from tennis practice this morning, and I haven’t used chalk on a blackboard in years.

If the goal is to write a ‘k’, I have some flexibility. I am committed, not to a precise trajectory, but to a more abstractly defined objective: to write a legible ‘k’. This suggests that feedback processing should evaluate to what extent I am succeeding at the action, not at tracing out a particular trajectory. Does what I’m actually doing look like writing a ‘k’?

In a new paper, Sandbrink et al. (pp2022) report on simulations of the human musculoskeletal system and neural network models that suggest that the tuning properties of neurons in somatosensory cortex (S1) can be explained by assuming that the objective of the proprioceptive system is to recognize the action being performed.

They used recorded traces of a person writing lower-case letters to simulate the responses of muscle spindles sensing the lengths and velocities of muscles in the human arm as would be present if the hand were moved passively along these trajectories. The physical simulation uses a 3D model of the human arm with two parameters for the direction of the upper arm and two more for the direction of the lower arm. These four parameters are inferred by inverse kinematics from the hand trajectories tracing each letter in a variety of vertical and horizontal planes. A 3D muscle model then enables the authors to compute the expected spindle responses that reflect the lengths and velocities of 25 relevant upper arm muscles.

The authors then trained neural network models of proprioceptive processing that took the simulated muscle spindle signals as input. The neural net architectures included one that first integrates information over the muscle spindles and then across time (“spatial-temporal”), one that integrated across muscle spindles and time simultaneously (“spatiotemporal”), and a recurrent long-short-term-memory model.

Each architecture was trained on two objectives: to decode the trajectory (i.e. the position of the hand tracing a letter as a function of time) or to recognize the action (i.e. the letter being traced). The two objectives correspond to two hypotheses about the function of proprioceptive processing: To inform the feedback controller about either the current position of the hand or the letter being drawn.

The models trained to recognize the action developed tuning more consistent with what is known about the tuning of neurons in primary somatosensory cortex in primates. In particular, direction tuning with roughly equal numbers of units preferring each direction emerged in middle layers of the neural network models trained to recognize the action, similar to what has been observed in primate neural recordings. Direction tuning is already present in the muscle-spindle signals, but the spindle signals do not uniformly represent the directions.

The task-optimization approach to neural network modeling is inspired by work in vision, where neural networks trained on the task of image classification explained responses to novel images in populations of neurons in the inferior temporal cortex. This result suggested a tentative answer to the why question: Why do inferior temporal neurons exhibit the response profiles and representational geometry they exhibit? Because their function (or one of their functions) is to recognize the objects in the images. Here, similarly, the authors address a why question with task-optimized neural network models: Why do somatosensory cortical neurons exhibit the types of tuning that have been reported in the literature?

The function of proprioception, of course, is not for the brain to recognize which letter it is trying to write. It already knows that. The function is to sense how the current trajectory – the actual, not the intended one – differs from, say, a legible “k” (if that was the intention), and to map from that difference to a modification vector that will improve the outcome.

Why is action decoding relevant for performing the action? A key reason may be that the goal is not to produce a fixed trajectory, but to produce a legible ‘k’. A legible ‘k’ is not a single trajectory, but a class of trajectories containing an infinity of viable solutions. If someone nudged my arm while writing, adaptive feedback control should not attempt to return me to the originally intended trajectory, but to a new trajectory that traces the most legible ‘k’ that is still in the cards, which may be a different style of ‘k’ than I originally intended.

The paper contributes a useful data set for training models and a qualitative comparison of models to real neurons in terms of tuning properties. It would be good, in follow-up studies, to directly test to what extent each of the models can quantitatively predict either single-neuron responses or population representational geometries, as has been done in vision, and to perform statistical comparisons between models.

Importantly, this paper develops the idea of combining simulations body and brain, of the musculoskeletal system and the processing of control-related signals in the nervous system, which provides a very exciting direction for future research.



Strengths

• The paper introduces a highly original research program that marries simulation of the musculoskeletal system and neural network modelling to predict neural representations in the proprioceptive pathway.
• The authors performed an architecture search and trained multiple instances of different neural network architectures with each of two objectives.
• The paper includes comprehensive analyses of the proprioceptive representations from the simulated muscle-spindle signals through the layers of the models. These analyses characterize unit tuning, linear decodability, and representational similarity.
• The results suggest an explanation for the direction tuning with a roughly uniform distribution of the units’ direction preferences that has been reported previously for neurons in the primate primary somatosensory (S1) cortex.
• If the simulated muscle-spindle data set, models, and analysis code were shared along with the published paper, this work could form the basis for quantitative model evaluation and further model development.

Weaknesses

• The models are qualitatively evaluated by comparison of model unit tuning to what is known about the tuning of neurons in somatosensory cortex. Follow-up studies should quantitatively evaluate the models by inferential analyses of their ability to predict measured responses.
• The two training objectives differ in multiple respects, making it difficult to assess what the necessary requirements are for the emergence of representations similar to primate S1. Decoding the hand position may be too simple, but what about decoding velocity, or trajectory descriptors such as curvature? There may be a middle ground between trajectory decoding and action recognition that also leads to the emergence of tuning properties as found in primate S1.

Ivanova, Schrimpf, Anzellotti, Zaslavsky, Fedorenko, and Isik (pp2021) discuss whether mapping models should be linear or nonlinear. This paper is part of a Cognitive Computational Neuroscience 2020 Generative Adversarial Collaboration, with the goal to resolve an important controversy in the field.

The authors usefully define the term mapping model in contradistinction to models of brain function. A mapping model specifies the mapping between a model of brain function (some brain-representational model) and brain-activity measurements. A mapping model can relate brain-activity measurements to different types of brain-representational model: (1) descriptions of the stimuli, (2) descriptions of behavioral responses, (3) activity measurements in other brains or other brain regions, or (4) the units in some layer of a neural network model. Moreover, mapping models can operate in either direction: from the measured brain activity to the features of the representational model (decoding model) or from the model features to the measured brain activity (encoding model). Figures 1 and 2 of the paper very clearly lay out these important distinctions.

To begin addressing the question what mapping models should be used the authors consider three desiderata: (1) predictive accuracy, (2) interpretability, and (3) biological plausibility. Predictive accuracy tends to favor more complex and nonlinear models (assuming we have enough data for fitting), whereas simpler and linear models may be easier to interpret in general. Biological plausibility would appear to be irrelevant if the mapping model is not considered a model of brain function. However, in the context of an encoding model, for example, we may want the mapping model to capture physiological processes such as the hemodynamics and nonphysiological processes such as the averaging in voxels, neither of which may be considered part of the brain-computational process that is the ultimate target of our investigation.

The authors make many reasonable points about linear and nonlinear mapping models and conclude by suggesting that rather than the linear/nonlinear distinction, we should consider more general notions of the complexity of the mapping model. They suggest that researchers consider a range of possible mapping models and estimate their complexity. They discuss three measures of complexity: the number of parameters, the minimum description length, and the amount of fitting data needed for a model to achieve a given level of predictive accuracy.

The paper makes a good contribution by beginning a broader discussion about mapping models and putting the pieces of the puzzle on the table. However, a problem is that the arguments are not developed in the context of clearly defined research goals. The three desiderata (predictive accuracy, interpretability, and biological plausibility) are referred to as “goals” in the paper and further differentiated in Fig. 3:

• predictive accuracy
  • compare competing feature sets
  • decode features from neural data
  • build maximally accurate models of brain activity
• interpretability
  • examine individual features
  • test representational geometry
  • interpret feature sets
• biological plausibility
  • incorporate physiological properties of the measurements
  • simulate downstream neural readout

A lot of thought clearly went into this structure, which serves to enable insights at a more general level about the mapping model: for all cases where we desire biological plausibility, interpretability, or predictive accuracy. However, the cost of this abstraction is too great. Arguments for particular choices of mapping model are compelling only in the context of more specifically defined research goals that actually motivate researchers to conduct studies.

Neither the three top-level desiderata, nor the more specific objectives really capture the goals that motivate researchers. We don’t do studies to achieve “predictive accuracy”. Rather our goal may be to adjudicate among different computational models that implement hypotheses about brain information processing. The models’ predictive accuracy is used as a performance statistic to inferentially compare the models.

The goal to compare brain-computational models, for example, is difficult to localize in the list. It is related to “comparing competing feature sets”, “building accurate model of brain activity”, “biological plausibility”, and “testing representational geometry”, but each of these captures only part of the goal to test brain-computational models.

On a similar note, I would argue that “decoding features” is not a research goal. The relevant research goal could be defined as “testing a brain region for the presence of particular information” or “testing whether particular information is explicitly encoded in a brain region”.

It would help to start with research goals that really capture scientists motivation for conducting studies that use mapping models, and then to discuss the merits of particular choices of mapping model in each of these contexts. Some research goals are: testing if certain information is present in a region, testing if it is present in a particular format, adjudicating among representational models, and adjudicating among brain-computational models. Starting with these would make it easier for the reader to follow, and would enable the authors to make some of the arguments already made (e.g. that testing for the presence of information can benefit from nonlinear decoders) more compellingly. It might also lead to additional insights.

An important question is how this CCN Generative Adversarial Collaboration (GAC) can lead to progress beyond this position paper. One topic for further study is the suggestion made at the end that a variety of mapping models should be considered and compared in terms of their complexity and predictive accuracy. This suggestion seems potentially important, but would need (1) careful motivation in the context of particular research goals and (2) more research that develops and validates methods for actually exploring the space of mapping models with flexible regularization. This could be the basis for the aim of the GAC to lead to new research that resolves some challenge or controversy.

Specific comments

Is it that simple? Linear mapping models in cognitive neuroscience

When I read the title, I want to ask back: Is what exactly that simple? What is it? I might interpret the question in the context of the research goal I most care about (adjudicating among brain-computational theories). In that context, I guess, I’m on team linear. (I want to confine nonlinearities to the brain-computational model.) But the vagueness entailed by the absence of explicit research goals starts right there in the title.

If the features are pixels, the answer might be different than if the features are semantic stimulus descriptors (e.g. nonlinear for pixels, linear for semantic features if we are looking for their explicit representation in the brain). If the brain responses are single-cell recordings, the answer might be different than if the brain responses are fMRI voxels (in the latter case, we may want the mapping model to capture averaging within voxels). If the goal is to reveal whether particular information is present in a brain region, we might want to use a nonlinear decoding analysis. If the goal is to reveal whether particular information is explicitly encoded in the sense of linear decodability, we might want to use a linear decoding analysis. If the goal is to test a brain-computational model of perception, the answer will depend on whether the mapping model is supposed to serve solely the purpose of mapping model representations to brain representations, or whether it is supposed to be interpreted as part of the brain-computational model (i.e. whether we intend to use the brain-activity data to learn parameters of the computation we are modeling).

Figure 1 is great, because it usefully lays out a number of different scenarios in which mapping models are commonly used. These scenarios each require separate discussion. It might be useful to include a table with a row for each combination of research goal, domain, and data. Given this essential context, we can have a useful discussion about the pros and cons of linear and nonlinear mapping models with particular priors on their parameters.

“1:1 mapping”, “perfect features”

A linear mapping is much more general than a 1:1 mapping, which of these is meant here? The term “perfect features” is used as though it’s clear how it is to be defined. But that’s exactly the question to be addressed: Should we require the brain-computational model units to be related to neural responses by a 1:1 mapping, an orthogonal linear transform (which would imply matching geometries), a sparse linear transform, a general linear transform, or a particular nonlinear transform, or any nonlinear transform (which would imply merely that the model encodes the information present in the neural population).

3.1.3. Build accurate models of brain data. Finally, some researchers are trying to build accurate models of the brain that can replace experimental data or, at least, reduce the need for
experiments by running studies in silico (e.g., Jain et al., 2020; Kell et al., 2018; Yamins et al., 2014).

“Building models of data” may describe a frequent activity. But I’d say it should be motivated by some larger goal (such as testing a theory). It’s also unclear how models can or why they should replace data when the purpose of the latter is to test the former.

3.2.2. Test representational geometry: […] do features X, generated by a known process, accurately describe the space of neural responses Y? Thus, the feature set becomes a new unit of interpretation, and the linearity restriction is placed primarily to preserve the overall geometry of the feature space. For instance, the finding that convolutional neural networks and the ventral
visual stream produce similar representational spaces (Yamins et al., 2014) allows us to infer that both processes are subject to similar optimization constraints (Richards et al., 2019). That said, mapping models that probe the representational geometry of the neural response space do not have to be linear, as long as they correspond to a well-specified hypothesis about the relationship between features and data.

This doesn’t make sense to me. A linear mapping does not in general preserve the representational geometry. A particular class of linear mappings (orthogonal linear transformations) preserve the geometry (distances and inner products, and thus angles).

If a mapping model achieves good predictivity, we can say that a given set of features is reflected in the neural signal. In contrast, if
a powerful mapping model trained on a large set of data achieves poor predictivity, it provides strong evidence that a given feature set is not represented in the neural data.

Absence of evidence is not evidence of absence. “Poor predictivity” doesn’t provide “strong evidence” that the neural population doesn’t encode what we fail to find in the data.

3.3. Biological plausibility. In addition to prediction accuracy and interpretability-related considerations, biological plausibility can also be a factor in deciding on the space of acceptable feature-brain mappings. We discuss two goals related to biological plausibility: simulating linear readout and accounting
for physiological mechanisms affecting measurement.

Figure 2 suggests that be mapping model is not part of the brain model, so why does biological plausibility matter?

Even a relatively ‘constrained’ linear classifier can read out many
features from the data, many of them biologically implausible (e.g., voxel-level ‘biases’ that allow orientation decoding in V1 using fMRI; Ritchie et al., 2019).

If a linear readout from voxels is possible, then a linear readout from neurons should definitely be possible. What does it mean to say the decoded features are biologically implausible? (Many of the other points in this section seem important and solid, though.)

Even with infinite data, certain measurement properties might force us to use a particular mapping class. For instance, Nozari et al. (2020) show that fMRI resting state dynamics are best
modeled with linear mappings and suggest that fMRI’s inevitable spatiotemporal signal averaging might be to blame (although see Anzellotti et al., 2017, for contrary evidence).

Do Nozari et al. have “infinite data”? I also don’t understand what’s meant by saying “resting state dynamics are best modeled with linear mappings”. Are we talking about linear dynamics or linear mapping models? What is the mapping from and to?

3.3.2. Incorporate physiological mechanisms affecting measurement

It’s not just physiological mechanisms, but also other components of the measurement process. For example, the local averaging in fMRI voxels may be accounted for by averaging of the units of a neural network model, which can be achieved in the framework of linear encoding models.

Wang et al. (pp2020) offer an exciting concise review of the substantial progress with brain connectomes over the past decade. Better methods and bigger studies using retrograde and anterograde tracers in mouse, marmoset and macaque give a more detailed, more quantitative, and more comprehensive picture of brain connectivity at multiple scales in these species.

The review also describes how the new anatomical information about the connectivity is being used to build dynamic network models that are consistent with features of the dynamics measured with neurophysiological methods.

In 1991, Felleman and van Essen published a famous connectomic synthesis of reported results on connections between visual cortical areas in the macaque. In 2001, Stephan et al. published an updated inter-area cortical connectivity matrix in the macaque (CoCoMac). These studies presented summaries of the literature in the form of a matrix of inter-area connectivity, qualitatively assessed (as “absent”, “weak”, or “strong” in Stephan et al. 2001). Over the past two decades, tracer studies have provided quantitative results about directed connectivity. We now have comprehensive directed and weighted inter-area connection matrices, which give a better global picture of brain connectivity in macaque, marmoset, and mouse, although they don’t include all regions and are not cell-type specific.

Consider the following (non-exhaustive) list of three levels of connectomic description:

1. full synaptic connectivity of the cellular circuit
   (electron microscopy)
2. summary statistics of in inter-laminar directed connectivity between areas (tracer studies)
3. summary statistics of global undirected inter-area connectivity
   (noninvasive MR diffusion imaging with tractography analysis)

Only the first level defines a circuit in terms synaptic interactions between individual neurons that could conceivably be animated in a computer simulation to recover the information-processing function of the circuit. Such a bottom-up approach to understanding the computations in biological neural networks may eventually be feasible for worms, flies, and zebrafish. For rodents and primates, it is out of reach. The full cellular-level connectome is very difficult or even impossible to measure and would be unique to each individual animal. Moreover, even when we have it (as for C. elegans) and it is small enough for nimble simulations (300-400 neurons), it still not clear how to best use this information to understand the circuit’s computational function from the bottom up.

For rodents and primates, we must settle for statistical summaries and combine the data-driven bottom-up approach to understanding the brain with a computational-theory-driven top-down approach. The advances described by Wang et al. focus on the intermediate level 2. An important summary statistic at this level is the fraction of labeled neurons (FLN), which describes, for a retrograde tracer injected in a given region, in what proportions upstream regions contribute incoming axonal projections.

Several insights emerged from tracer-based connectivity:

• The strength of inter-area connectivity decays roughly exponentially with the areas’ distance in the brain.
• Some pairs of areas are connected, but very sparsely. Other pairs of areas have a massive tract of fibers between them. Connectivity strengths vary by five orders of magnitudes.
• The structural connectivity, in combination with a generic model of the excitatory/inhibitory local microcircuits, can be used as a basis for simulation of the network dynamics. The emergent dynamics is broadly consistent with neurophysiological observations, including slower, more integrative responses in regions further removed from the sensory input, which receive a larger proportion of their input through a broad distribution of paths through the network.
• Laminar origins of connections differ between feedforward and feedback connections. Feedforward connection tend to originate in supragranular and feedback connections in infragranular layers. Modeling superficial and deep layers with separate excitatory/inhibitory microcircuits and using lamina-specific connectivity enables modeling of more detailed hierarchical dynamics, including the association of gamma with feedforward signals and alpha/beta with feedback.
• A network model in which long-range excitation is tempered with local inhibition can explain threshold-dependent dynamics, where weak inputs fail to be propagated and inputs exceeding a threshold ignite a global response.
• When a brain is scaled up , the number of possible pairwise connections grows as the square of the number of units to be connected (e.g. neurons or areas, depending on the level at which connectivity is considered). Full connectivity, thus, is much less costly in a small brain. This means that connectivity and component placement are less constrained in a small brain. Consistently with this simple fact, the macaque brain has connections among about two thirds of all pairs of areas (half of them reciprocal), whereas the mouse brain has 97% of all possible inter-area connections. The marmoset, a much smaller primate, may have somewhat more widely distributed connectivity than the macaque, but not to the extent predicted by its smaller-scale brain. Its connectivity is in fact quite similar to that of the macaque. Species and scaling both seem to matter to the overall degree of inter-area connectivity.

These models take a bottom-up approach in which the structural constraints provided by the tracer studies and descriptions of the cortical microcircuit are used to simulate global activity dynamics. Aspects of these dynamics, such as longer timescales in higher regions are suggestive of computational functions like evidence integration. However, the models do not perform task-related information processing, and so do not explain any cognitive functions. What is still missing is the integration of the bottom-up approach to modeling with the top-down approach of deep recurrent neural networks, where parameters are optimized for a model to perform a nontrivial perceptual, cognitive, or motor control task.

Suggestions for improvements in case the paper is revised

The paper is well-written and engaging. It’s great that it links structure to dynamics and points toward links between structure and computational function, which remain to be elaborated over the next decade. My main suggestion is to slightly expand this very concise piece with a view to (a) clarifying things that are currently a little too dense and (b) adding some elements that would make the paper even more useful to its readers.

Useful additions to consider include:

• A table that compares the different available connectomic datasets in terms of the information provided and the information missing, and links to open-science resources to help neuroscientists use of the structural constraints for theory and modeling of function.
• An update to the famous Felleman and van Essen (1991) diagram, with area sizes and directed, weighted connections. This seems very important for the field to have. Is it already available or can it be constructed with relative ease, at least for a subset of the regions, e.g. the macaque visual system?
• A discussion of how the new connectomic data can be used to constrain brain-computational models (i.e. models that simulate the information processing enabling the brain to perform an ecologically relevant task such as visual recognition, categorization, navigation, or reaching).

Minor points

The correlation between inter-area connection-weight matrices from diffusion imaging and cellular tracers is cited as 0.59, and cellular tracing is referred to as ground truth. However, tracing also provides merely summary statistical information and is affected by sample error. Have the reliabilities of diffusion-based and cellular-tracing-based inter-area connection-weight estimates been established? It would be good to consider these in interpreting the consistency between the two techniques.

Second, the weight of connection (if present) between two areas decays exponentially with their distance (the exponential distance rule) [17].

Here it would be great to elaborate on the concept of distance. I assume what is meant is the Euclidean distance in the folded cortex. Readers may wonder if the cortical geodesic distance or the tract length in the white matter are more relevant. Some readers may even think of the hierarchical distance. Good to clarify and address these different notions of distance.

[R8I7]

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

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

MAJOR POINTS

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

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

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

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

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

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

(2) Testing linear separability of categories

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

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

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

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

(3) Circularity of peak-categorical MDS arrangements

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

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

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

MINOR POINTS

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

LANGUAGE, LOGIC, STYLE, AND GRAMMAR

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

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

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

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

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

Some phrase missing there.

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

demands innovation in neuroimaging techniques”

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

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

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

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

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

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

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

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

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

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

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

more decoding accuracy -> greater decoding accuracy

“within the average” Bad phrasing.

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

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

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

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

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

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

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

“boarder” -> “border”