Representations in a deep end-to-end driving model predict human brain activity in an active driving task

We would like to thank the reviewer for their helpful comments, which have been valuable for improving the paper, and for noting that the topic of the paper is novel and interesting. We first provide a brief summary of our changes, then address the reviewer’s points in more detail below. We have performed new baseline comparison experiments in appendix, which we have added to appendix A.2. These experiments show that the LAV DNN features are able to explain more variance in brain activity than those of a standard CNN trained on image classification, especially in high-level vision areas. We also added statistical tests for voxel encoding model performance and for the distribution of best-performing modules across the cortex, which establish the statistical significance of these results. Finally, in order to address questions about the methodology, we have revised section 3 and added appendix A.3 to clarify details about the voxelwise modeling framework as well as why this framework is rigorous and suitable for our analysis.

The reviewer expresses three main concerns. First, they suggest additional analysis would better support the results. To strengthen our analysis, we have provided statistical significance measures for per-voxel $R^2$ scores, as well as for the non-random partitioning of explained variance by each LAV module across different voxels. We have also provided figures for the individual subjects in the supplementary. We find that there is in fact good consistency between the explained variance of the LAV modules across subjects, especially for the semantic segmentation, brake, planning, and control modules. Furthermore, the prediction and BEV perception modules predict variance in functionally similar regions across subjects as shown in figure 3, even though these regions do not project to the same exact locations in the group-level space.

Second, the reviewer wonders whether the results generalize to other driving DNNs. We agree that incorporating comparisons to other driving models to improve our understanding of whether these models converge on similar levels of brain alignment and functional organization is an exciting area. Because running experiments with other models which expect different inputs (e.g. types and positions of cameras) requires rendering different data in addition to repeating regressions for each subject, this isn’t possible for us to address during the rebuttal period, but is an interesting direction for future work. However, we have added new baseline comparisons with CNN models that support the strength of the LAV DNN features at explaining brain activity, and that the benefit of LAV features over CNN features is strongest in specific functional areas.

Third, the reviewer questions the choice of VM and linear predictivity as the metric for quantifying alignment between the brain and a DNN. The metrics explored in Soni et al and frequently used in studies attempting to quantify brain alignment are population-based metrics that return a single value for the alignment between two sets of features (the entire DNN and the entire brain, or specific sub-regions of either). Therefore, they do not allow for the per-voxel analysis that we focus on in this paper, and a comparison with other methods would require major changes to our analysis that is beyond the scope of this paper. We would also like to note that VM is the most powerful method for analyzing complex brain activity recorded during naturalistic tasks, and has been validated in multiple studies [Huth et al., 2012, Huth et al., 2016, Nishimoto et al., 2011, Cukur et al., 2013, Deniz et al., 2019]. It is the only method that explicitly models the timeseries recorded from the brain, and is thus uniquely suited for analyzing data from continuous tasks. Finally, the regression methods underlying VM are statistically rigorous [Dupre la Tour et al., 2022, Nunez-Elizalde et al., 2019] and are drawn from solid mathematical foundations in linear regression.

We would like to thank the reviewer for their helpful comments, which have been valuable for improving the paper. We first provide a brief summary of our changes, then address the reviewer’s points in more detail below. We have performed new baseline comparison experiments in appendix, which we have added to appendix A.2. These experiments show that the LAV DNN features are able to explain more variance in brain activity than those of a standard CNN trained on image classification, especially in high-level vision areas. We also added statistical tests for voxel encoding model performance and for the distribution of best-performing modules across the cortex, which establish the statistical significance of these results. Finally, in order to address questions about the methodology, we have revised section 3 and added appendix A.3 to clarify details about the voxelwise modeling framework as well as why this framework is rigorous and suitable for our analysis.

The reviewer raises three main concerns. First, the reviewer suggested that comparing the LAV model against appropriate driving model baselines would strengthen the results. Unfortunately it isn’t possible to do a direct comparison with the models in [Strong et al., 2024], as these models only work when there are no intersections or turning behavior. Furthermore, as these models do not handle the state estimation problem of predicting the positions and dynamics of other vehicles from perceptual inputs, they are at a significant disadvantage compared to a DNN that processes image-based input. Finding ways to make meaningful comparisons in spite of these challenges is an exciting direction for future work.

We appreciate the suggestion of image classification models as an appropriate baseline. We have added comparisons with two new models: one derived from the activations of a randomly initialized CNN, and one from the activations of a CNN trained on ImageNet image classification. Our model performs better than both baseline models, especially in higher-level vision areas. This supports our experimental design capturing explainable brain activity beyond what can be explained with image processing features alone, and that the LAV DNN is in fact able to explain some of this additional variance. Results and more details about these experiments can be found in appendix A.2.

Second, the reviewer wanted stronger support for the claim that LAV and the brain partition features in a similar way. We agree that while it is not straightforward to evaluate the similarity in partitioning, it could nonetheless be evaluated both quantitatively and qualitatively. First, we highlight that encoding models are fit to each voxel independently; the modelling process contains no inductive bias that would encourage models for spatially proximal voxels to have similar partitioning of variance across the different LAV modules. Nevertheless, the best-performing LAV module for each voxel has quantitatively a non-random spatial distribution across the brain. To show that this pattern is statistically significant, we have added a statistical test based on the Moran’s I measure of spatial autocorrelation that finds a p-value of < 0.01 in all three subjects (please see appendix A.3 for more details). This non-random distribution suggests that each model maps to a specific network of functional regions in the brain. Second, the partitioning can be qualitatively evaluated by comparing the LAV module function with the known functional properties of the brain regions to which it is mapped. For example, the semantic segmentation and brake modules, which process RGB images, are the best-performing modules in the visual cortex but are outperformed by planning and control modules in sensorimotor regions. This functional similarity between the LAV module and corresponding brain regions during the same task suggest that they mediate the same aspects of the task. Finally, we agree with the limitation that we have evaluated only a single driving DNN, and comparison of alignment across DNN architectures will be a key direction for future work.

We would like to thank the reviewer for their helpful comments, which have been valuable for improving the paper. We first provide a brief summary of our changes, then address the reviewer’s points in more detail below. We have performed new baseline comparison experiments in appendix, which we have added to appendix A.2. These experiments show that the LAV DNN features are able to explain more variance in brain activity than those of a standard CNN trained on image classification, especially in high-level vision areas. We also added statistical tests for voxel encoding model performance and for the distribution of best-performing modules across the cortex, which establish the statistical significance of these results. Finally, in order to address questions about the methodology, we have revised section 3 and added appendix A.3 to clarify details about the voxelwise modeling framework as well as why this framework is rigorous and suitable for our analysis.

The reviewer raises three main concerns. First, the reviewer is concerned that a pool of three subjects is insufficient for drawing statistically sound conclusions. Here we would like to clarify the n in the conceptual framework underlying our analyses and demonstrate that three subjects is in fact sufficient. The small-n concern expressed by the reviewer reflects the classical psychology experiment framework, in which results from a large number of subjects are averaged to draw a group-level conclusion. Neuroimaging experiments under this framework would therefore need to collect data from a large number of subjects, and because of practical limitations, this necessitates collecting less data per subject (typically on the order of one hour per subject). This framework then seeks to create a single model, with particular parameters, for all subjects. However, because of individual differences in anatomy, cognitive strategies, the high-dimensionality of the brain, and the small amount of data collected per subject, these group-level models rarely provide good descriptions of individual subjects and thus the models are of limited use.

Our study instead follows the framework found in psychophysics and neurophysiology (particularly in non-human primates (NHP)) [Asaad et al., 2024]. In this framework, the n is not the number of subjects, but rather the amount of data collected per subject. In our study, we collected 2-3 hours of data per subject in this experiment, and also an additional 5-6 hours of anatomical and functional localizer data that enabled us to reconstruct the cortical surface and delineate known functional regions. This large amount of data from each individual subject is divided into train, validation, and test sets, and models are fit, cross-validated, and tested within each individual subject. Rather than seeking a particular instantiation of a model with particular parameters to apply to all subjects, this framework demonstrates that a particular architecture of model, with possibly different parameters per subject that can account for the idiosyncracies of each subject, can be used to accurately explain the data in all subjects. In other words, the models are fit and statistically tested within each subject, and each subject is in fact a full replication of the experiment [Asaad et al., 2024].

Indeed, studies from NHP neurophysiology and psychophysics under this framework have routinely used as few as two subjects to reveal fundamental insights into the functions of the brain. Neuroimaging studies with small n-in-subjects have also produced robust models of the human brain in complex, naturalistic tasks. Thus, we have in fact provided sufficient data to prevent overfitting and also replicate this experiment. The reviewer commented that we did not consider this in the text of the manuscript, but we note that this n-in-subjects and n-in-data contrast is a philosophical difference between standard practices across fields and is beyond the scope of this paper.

Second, the reviewer noted that the paper would benefit from more analysis of the model performance. We have added a statistical test for the encoding model performance. This test establishes the statistical significance threshold for each voxel, and we have updated figure 2(b) so that only voxels with p-values over the threshold are shown. We have also added a statistical test for the non-random distribution of best-performing modules across the cortex which shows that this is statistically significant in all three subjects. Details for both tests can be found in appendix A.3.

We would like to thank the reviewer for their helpful comments, which have been valuable for improving the paper. We first provide a brief summary of our changes, then address the reviewer’s points in more detail below. We have performed new baseline comparison experiments in appendix, which we have added to appendix A.2. These experiments show that the LAV DNN features are able to explain more variance in brain activity than those of a standard CNN trained on image classification, especially in high-level vision areas. We also added statistical tests for voxel encoding model performance and for the distribution of best-performing modules across the cortex, which establish the statistical significance of these results. Finally, in order to address questions about the methodology, we have revised section 3 and added appendix A.3 to clarify details about the voxelwise modeling framework as well as why this framework is rigorous and suitable for our analysis.

The reviewer expresses four main concerns. First, the reviewer is concerned that a pool of three subjects is insufficient for drawing statistically sound conclusions. Here we would like to clarify the n in the conceptual framework underlying our analyses and demonstrate that three subjects is in fact sufficient. The small-n concern expressed by the reviewer reflects the classical psychology experiment framework, in which results from a large number of subjects are averaged to draw a group-level conclusion. Neuroimaging experiments under this framework would therefore need to collect data from a large number of subjects, and because of practical limitations, this necessitates collecting less data per subject (typically on the order of one hour per subject). This framework then seeks to create a single model, with particular parameters, for all subjects. However, because of individual differences in anatomy, cognitive strategies, the high-dimensionality of the brain, and the small amount of data collected per subject, these group-level models rarely provide good descriptions of individual subjects and thus the models are of limited use.

Our study instead follows the framework found in psychophysics and neurophysiology (particularly in non-human primates (NHP)) [Asaad et al., 2024]. In this framework, the n is not the number of subjects, but rather the amount of data collected per subject. In our study, we collected 2-3 hours of data per subject in this experiment, and also an additional 5-6 hours of anatomical and functional localizer data that enabled us to reconstruct the cortical surface and delineate known functional regions. This large amount of data from each individual subject is divided into train, validation, and test sets, and models are fit, cross-validated, and tested within each individual subject. Rather than seeking a particular instantiation of a model with particular parameters to apply to all subjects, this framework demonstrates that a particular architecture of model, with possibly different parameters per subject that can account for the idiosyncracies of each subject, can be used to accurately explain the data in all subjects. In other words, the models are fit and statistically tested within each subject, and each subject is in fact a full replication of the experiment [Asaad et al., 2024].

Indeed, studies from NHP neurophysiology and psychophysics under this framework have routinely used as few as two subjects to reveal fundamental insights into the functions of the brain. Neuroimaging studies with small n-in-subjects have also produced robust models of the human brain in complex, naturalistic tasks. Thus, we have in fact provided sufficient data to prevent overfitting and also replicate this experiment.

Second, the reviewer asks why we chose to examine a DNN model over other possible models. There has been one prior work on non-DNN models for driving, which studies algorithms for generating speed and acceleration based on the dynamics and predicted behavior of the vehicle in front [Strong et al., 2024]. However, these dynamical models assume knowledge about the state of the vehicle and environment, and require external processes to provide these state parameters. We note that fully autonomous driving pipelines typically contain at least some DNN components, because only DNNs can reliably estimate the state of the environment from sensor inputs. The human brain drives in an end-to-end manner, and so we believe driving models that make use of DNNs are most appropriate when trying to draw connections to the brain activity of human drivers.

We would like to thank the reviewer for their helpful comments, which have been valuable for improving the paper. We first provide a brief summary of our changes, then address the reviewer’s points in more detail below. We have performed new baseline comparison experiments in appendix, which we have added to appendix A.2. These experiments show that the LAV DNN features are able to explain more variance in brain activity than those of a standard CNN trained on image classification, especially in high-level vision areas. We also added statistical tests for voxel encoding model performance and for the distribution of best-performing modules across the cortex, which establish the statistical significance of these results. Finally, in order to address questions about the methodology, we have revised section 3 and added appendix A.3 to clarify details about the voxelwise modeling framework as well as why this framework is rigorous and suitable for our analysis.

At a high level, the reviewer expressed concern that a work relating DNN models to neuroimaging data may not be appropriate to the ICLR venue. However, other papers [Benchetrit et al., 2024, Prince et al., 2024] on neuroimaging data have been accepted at ICLR 2024, which also included a workshop on the alignment of representations between artificial systems and biological neural data [Scotti et al., 2024, Nikolaus et al., 2024, Ferrante, et al., 2024].

The reviewer also expressed three more specific concerns:

First, the reviewer is concerned that a pool of three subjects is insufficient for drawing statistically sound conclusions. Here we would like to clarify the n in the conceptual framework underlying our analyses and demonstrate that three subjects is in fact sufficient. The small-n concern expressed by the reviewer reflects the classical psychology experiment framework, in which results from a large number of subjects are averaged to draw a group-level conclusion. Neuroimaging experiments under this framework would therefore need to collect data from a large number of subjects, and because of practical limitations, this necessitates collecting less data per subject (typically on the order of one hour per subject). This framework then seeks to create a single model, with particular parameters, for all subjects. However, because of individual differences in anatomy, cognitive strategies, the high-dimensionality of the brain, and the small amount of data collected per subject, these group-level models rarely provide good descriptions of individual subjects and thus the models are of limited use.

Our study instead follows the framework found in psychophysics and neurophysiology (particularly in non-human primates (NHP)) [Asaad et al., 2024]. In this framework, the n is not the number of subjects, but rather the amount of data collected per subject. In our study, we collected 2-3 hours of data per subject in this experiment, and also an additional 5-6 hours of anatomical and functional localizer data that enabled us to reconstruct the cortical surface and delineate known functional regions. This large amount of data from each individual subject is divided into train, validation, and test sets, and models are fit, cross-validated, and tested within each individual subject. Rather than seeking a particular instantiation of a model with particular parameters to apply to all subjects, this framework demonstrates that a particular architecture of model, with possibly different parameters per subject that can account for the idiosyncracies of each subject, can be used to accurately explain the data in all subjects. In other words, the models are fit and statistically tested within each subject, and each subject is in fact a full replication of the experiment [Asaad et al., 2024].

Indeed, studies from NHP neurophysiology and psychophysics under this framework have routinely used as few as two subjects to reveal fundamental insights into the functions of the brain. Neuroimaging studies with small n-in-subjects have also produced robust models of the human brain in complex, naturalistic tasks. Thus, we have in fact provided sufficient data to prevent overfitting and also replicate this experiment. The reviewer commented that we did not consider this in the text of the manuscript, but we note that this n-in-subjects and n-in-data contrast is a philosophical difference between standard practices across fields and is beyond the scope of this paper.

We would like to thank the reviewer for their helpful comments, which have been valuable for improving the paper. We first provide a brief summary of our changes, then address the reviewer’s points in more detail below. We have performed new baseline comparison experiments in appendix, which we have added to appendix A.2. These experiments show that the LAV DNN features are able to explain more variance in brain activity than those of a standard CNN trained on image classification, especially in high-level vision areas. We also added statistical tests for voxel encoding model performance and for the distribution of best-performing modules across the cortex, which establish the statistical significance of these results. Finally, in order to address questions about the methodology, we have revised section 3 and added appendix A.3 to clarify details about the voxelwise modeling framework as well as why this framework is rigorous and suitable for our analysis.

The reviewer expresses three main concerns. First, they note that we only examined a single driving model, and suggests examining additional models trained with different objectives or architectures. We agree that incorporating comparisons to other driving models to improve our understanding of whether these models converge on similar levels of brain alignment and functional organization is an exciting area. Because running experiments with other models which expect different inputs (e.g. types and positions of cameras) requires rendering different data in addition to repeating regressions for each subject, this isn’t possible for us to address during the rebuttal period, but is an interesting direction for future work. However, we have added new baseline comparisons with CNN models that support the strength of the LAV DNN features at explaining brain activity.

Second, the reviewer expresses concern that correlations between DNN parameters and brain activity do not necessarily imply functional similarity, and rather reflect correlations with other variables. We agree that this is an important consideration. However, correlations between variables are an inherent property of natural environments and naturalistic stimuli. Because both the brain and DNNs learn the statistics of the world, they both will learn these stimulus correlations, and their internal representations will reflect these correlations. It is possible to design the stimulus to control for specific confounds. In vision, for example, one proposed dataset shows subjects images of the same object but with randomly generated backgrounds to control for the effect of the background [Yamins et al., 2014]. However, these types of controls typically reduce the ecological validity of the stimulus, and, because of the nonlinear nature of the brain, may result in brain activity that is not representative of how the brain behaves under more naturalistic conditions. Carefully designing tasks that reduce the influence of specific confounds while maintaining the ecological validity of the stimulus is a promising direction for future work.

Third, the reviewer wonders whether this work is a good fit for ICLR. However, other papers [Benchetrit et al., 2024, Prince et al., 2024] on neuroimaging data have been accepted at ICLR 2024, which also included a workshop on the alignment of representations between artificial systems and biological neural data [Scotti et al., 2024, Nikolaus et al., 2024, Ferrante, et al., 2024].

Response to questions:

1. Question 1 is about comparisons with other DNN architectures. Please see response point 1 above.
2. Question 2 is about whether this approach can be applied to other interactive tasks to better study alignment. To the best of our knowledge, this is the first study that quantifies the alignment between brain activity and a DNN for an interactive task. The methodological framework demonstrated here can be directly applied to other tasks, and this is an exciting direction for future work.
3. Question 3 is about possible confounds. Please see response point 2 above.