Understanding and Mitigating Distribution Shifts for Machine Learning Force Fields

Comment: How can the authors evaluate force distribution shifts without access to test dataset labels?

Since part of our paper is about understanding the distribution shifts that MLFFs face, we only used the test labels in Fig. 2 as a means of understanding the failure modes of current state-of-the-art MLFFs. Similarly, in Fig. 5 the force norms were only used to generate the bins in the plot to help demonstrate the distribution shift. We emphasize that no test labels were used at any point during the training / test-time refinement process.

Interestingly, we notice that despite the priors having large force MAEs compared to the ground truth, the force norms of the prior do correlate strongly with the reference calculations. Thus, the prior itself can be used to diagnose force norm distribution shifts. See the new Fig. 13.

Comment: Why are there no experiments combining MACE+TTT and GemNet-T+RR?

We have added an experiment applying RR to the JMP foundation model, which uses a GemNet backbone (see Tab. 6 and 7, section C.3). Due to the computational cost of training MACE models on large datasets (>2 weeks) we focused on the GemNet model for the SPICEv2 experiment. MACE-OFF would have to be retrained using the pre-train with prior, freeze, finetune approach in order to use TTT.

Comment: Is TTT more accurate than models trained directly using prior labels, such as those from classical force fields? Yes, TTT is more accurate than the prior used, so it will also be more accurate than any model trained just on those labels. See Table 14 and the results in section 4.

Comment: Why were MACE, GemNet-T, and NequIP chosen as the MLFF models? Do they represent the broader MLFF landscape?

Yes, they do represent the diversity of the broader MLFF landscape. We picked these because they are some of the best performing models on various modeling tasks, and they are widely used. They are the best on a number of different tasks [1][3].

Comment: Why are "Necessity of Proper Pre-training for Test-Time Training" (Sec. C) and "Notes on the Prior" (Sec. F.4) in the Appendix?

Due to space limitations, we had put them in the appendix in the initial version. We adjusted and included more details about TTT in the main text.

Comment: With ionization, electrostatic forces should be considered, as this represents a significant problem setting change, not merely a distribution shift.

We agree, and we removed this. Charge is still a very hard problem, though we think it is an interesting direction for future work.

Comment: At lines 261-262, what does “for many molecular datasets” mean specifically? Additional information on the datasets would clarify this statement.

We have clarified in the text that we were referring to SPICE, MD17, MD22, and ANI-1x.

Comment: In Figure 1’s caption, “(middle)” appears to be missing after “high force norms (…).”

Thank you very much for the detailed feedback. We have added “middle” to the caption.

[1] Xiang Fu, et. al. Forces are not enough: Benchmark and critical evaluation for machine learning force fields with molecular simulations. Transactions on Machine Learning Research, 2023.

[2] Maya Bechler-Speicher, et. al. Graph neural networks use graphs when they shouldn’t, 2024. URL https://arxiv.org/abs/2309.04332.

[3] Kovács, D., Batatia, I., Arany, E., & Csányi, G. (2023). Evaluation of the MACE force field architecture: From medicinal chemistry to materials science. The Journal of Chemical Physics, 159(4).

We would like to thank the reviewer for the thoughtful and constructive feedback. We are glad you found our identification and exploration of distribution shifts novel for the community.

Comment: The method assumes prior knowledge of test data

We want to clarify that we do not assume knowledge of the test data prior to testing. For instance, for the MD17 experiments, the model is first trained on prior labels from aspirin, benzene, and uracil, and then fine-tuned on the DFT labels for the same molecules. We do not assume anything about the testing molecules at this point. It is only at test time that the prior is used to quickly label the test molecules (naphthalene and toluene), taking less than 5 minutes (since the prior is very cheap). These labels are then used to conduct test-time training. For the radius refinement technique, again there is no assumption a priori about the test data: at test time the optimal radius is efficiently picked by comparing graph Laplacian eigenvalues. We have clarified our problem set up throughout the paper.

Comment: Most results provided do not reach chemical accuracy

We note that for many individual molecular systems, the errors are brought down by up to an order of magnitude, and for many systems (more than 8,000 / 10,000) the errors are below 25 meV / Å on SPICEv2. In section 4.2 with MD17, errors are brought down from >200 to less than 22 meV / Å for both naphthalene and toluene, enabling stable simulations. Section C.4 has errors well below 30 meV / Å on MD22. We have also added Fig. 10 that explicitly shows that many molecular systems start with higher errors and get errors brought down closer to ID performance with TTT and RR.

We note that our experiments establish a lower bound on the performance gains that can only be improved with further architectural and training innovations. Moreover, they help us understand how MLFFs generalize, and they also provide evidence for the hypothesis that MLFFs can be trained to generalize more effectively.

Comment: practitioners may prefer simple data generation or active learning

We emphasize that our proposed methods can be combined with active learning / data generation and are not a replacement for them (see section 2.2 around line 210). By decreasing errors on OOD systems purely through improved training strategies, TTT and RR provide a better starting point for active learning / further fine-tuning, likely requiring less data collection. We leave further investigation combining TTT and RR with other methods for future work.

Comment: Clarification of problem setup and limitations in introduction, abstract, and conclusion (and maybe in limitation).

We appreciate the feedback. We have added clarifications throughout the text on our problem setup. We reiterate important points here:

• We do not assume access to test structures during training.
• Labels from the prior can be quickly computed at test time, since the prior is very computationally efficient to compute (see appendix F).
• We argue that a cheap prior is almost always widely available since one could always use a simple analytical potential (like EMT or Lennard-Jones). A different (cheaper) level of quantum mechanical theory or a semi-empirical potential (see appendix C.1 and Tab. 4 for an added experiment with GFN2-xTB) can also be used, which is available for many systems.

See appendix B, E, and F for more details.

Comment: Adjusting the cutoff radius in RR may introduce unexpected potential discontinuities

We note that RR does not introduce any new discontinuities compared to current approaches, since all MLFFs that use a radius cutoff or a k-nearest neighbor graph also experience discrete connectivity changes during simulations (since an atom can exit or enter the cutoff). We have also added clarifications on the theoretical motivation behind our method in appendix F.

Comment: Examination of the cutoff radius effect on MD simulations is advised.

We have added MD simulations with models that use RR to Table 3, and find that RR is able to help improve MD stability.

Comment: NVE simulations

We have run NVE simulations with our model on the MD17 dataset with results presented below and in Tab. 5 in appendix C.2 (reported mean plus minus standard deviation stability over 3 seeds).

Even though GemNet-T + TTT is slightly less stable with NVE simulations on naphthalene compared to NVT, TTT still enables longer stable NVE simulations. We also emphasize NVT simulations are more commonly used [1], which is why we focused on those in the initial version.

Thank you for your hard work to tackle the reviewers' comment.

It is only at test time that the prior is used to quickly label the test molecules (naphthalene and toluene),

For me, this sentence shows that this method needs prior knowledge of the test data label (either pseudo label or true label). Can you please explain more why you can claim that you do not assume knowledge of the test data prior to testing? I have understood that test set prior knowledge is not used during training but TTT in theory require test data knowledge when utilized.

We note that our experiments establish a lower bound on the performance gains that can only be improved with further architectural and training innovations. Moreover, they help us understand how MLFFs generalize, and they also provide evidence for the hypothesis that MLFFs can be trained to generalize more effectively.

At a high level, we want to emphasize that our paper is about characterizing and better understanding distribution shifts in machine learning force fields. (General Remark)

According to the modified draft (blue colored font part), I still cannot see the above claim enough in the abstract, introduction, and problem setting. Rather, now the claim is not consistent in the manuscript (partly saying the objective is to improve MLPI performance and other part saying the objective is more on the better understanding on distribution shift). The authors should clearly state the above claim in the draft more consistently.

Overall, I think that the present draft still lacks consistency in terms of the motivation and objective as mentioned above, which would make the reader confused to evaluate this paper. In particular, I feel the definition of "test time" is unclear for me and should be clarified in the problem setting. For example, if it is purely ML terminology, TTT is cheating. However, if it means a real-world application case, TTT/RR can be interpreted as a good fine-tuning method ("test data" is the same training data but different label). I would really appreciate an effort to tackle this point for future readers.

Thank you for the authors' serous work to approach my request. I am now basically satisfied with the paper and raise my score.

We emphasize that test-time training is not cheating since no test labels are used to update the model.

I think that test data set is usually used to evaluate generalization ability of the model and I imagine TTT would induce an overfitting to test data set. One interesting question would be if the model performance on the original validation data set is the same even after TTT (which is not a request but just a comment out of curiosity).

We would like to thank the reviewer for the thoughtful and constructive feedback. We are glad that you are also interested in the problem of OOD for MLFFs and that our analyses are interesting for the community.

Comment: SPICE-trained models and MD simulation

We have added MD simulation results in Table 2 and 3 for models trained on SPICE. TTT and RR help SPICE-trained models simulate more stably compared to without these strategies.

Comment: How the OOD-ness of a test molecule impacts MD performance.

As mentioned above, we have added some simulations with SPICE trained models showing that TTT also improves stability of the simulation. In section 4.2, we also showed that TTT was able to mitigate distribution shifts enough to enable stable MD simulations on MD17. Unfortunately, we were not able to run MD simulations across the whole test set present in tables 5-7 because it is prohibitively computationally expensive (10,000 molecules * 3-4 hours per molecule = >30,000 hours), but our results on subsets of the test set show that there is stability improvement with TTT and that distribution shifts lead to worse MD performance (for example on MD17).

Comment: Why does the author train the GemNet-T model with only 10% of the data?

We had initially run a GemNet-T model on only 10% of the data because training on the full dataset is computationally expensive (> 2 weeks of training time). We also noticed in small scale experiments that scaling from 30k-100k data points did not change the OOD performance very much. This is also in line with Fig. 2 and section 2, which suggest that adding more in-distribution data does not help these models generalize as well. Nevertheless, we have started a new experiment with a GemNet-T model trained on the same data as MACE and have reported the results for the model trained so far in Tab. 1. We will update the final results after the model has fully converged for the final version of the paper.

Thank you for the questions.

Comment: How are the molecules in table 2/3 selected?

To demonstrate that RR and TTT are effective across a range of errors, we randomly selected six molecules from the top 1,000 most improved with TTT and RR. Specifically, two molecules were randomly chosen from each of the following force error bins: 0–40, 40–100, and >100 meV / Å. We have clarified this in appendix C.1. Note that we also added a new Fig. 10, which shows that there are many more molecules that also see strong improvements from TTT and RR.

Comment: Could you include the scaling experimental results in the paper?

Certainly, we have included those results in Fig. 17. We also present them in the following table:

Based on the additional computational cost of training on the full dataset, paired with the diminishing returns we observed from 50k to 100k, we had included the 100k results in the original version. We have also now updated the paper to include results with the model trained on all the 951k structures in the dataset (same as MACE-OFF).

We would like to thank the reviewer for the thoughtful and constructive feedback. We are glad that you think our investigation of distribution shifts is useful to the MLFF community.

Comment: falling short of significantly improving OOD sample prediction accuracy to levels comparable with in-distribution (ID) samples or chemical accuracy

Matching in-distribution performance is a challenging open machine learning problem. Previous test-time training works are also unable to fully match ID performance [1][2]. Although we agree this is the ideal to reach, it is an unreasonably hard initial expectation, since we are updating fewer parameters and not using ground truth labels. Our initial results establish a lower bound on the performance gains that can only be improved with further architectural, data, and training innovations. One of our goals is to also help us understand how MLFFs generalize, and these initial training strategies provide evidence for the hypothesis that MLFFs can be trained to generalize more effectively.

We do note that for many individual molecular systems, the errors are brought down by up to an order of magnitude, and for many systems (more than 8,000 / 10,000) the errors are below 25 meV / Å on SPICEv2. In section 4.2 with MD17, errors are brought down from >200 to less than 22 meV / Å for both naphthalene and toluene, enabling stable simulations. Section C.4 has errors below 30 meV / Å on MD22. We have also added Fig. 10 that explicitly shows that many molecular systems start with higher errors and get errors brought down closer to ID performance with TTT and RR.

Comment: Prior model used in the test-time training strategy (sGDML) may also face generalization issues.

While it is true that the prior can also face generalization issues, we emphasize that the prior is only used to learn representations. Empirically we find that even in cases when the prior also generalizes quite poorly and has large errors (see for example Fig. 11), it can still be used to improve representations. In other words, as long as the prior can regularize the MLFF, it can still be used to improve test-time performance.

Comment: Using semi-empirical methods as the prior model

This is a good point about trying a different prior. Since our proposed TTT method is agnostic of the chosen prior, we have added an experiment to the appendix showing that a semi-empirical method (GFN2-xTB) can also be used with TTT (see appendix C.1 and Tab. 4).

Comment: Clarification of the motivation behind aligning spectra as a strategy for managing distribution shifts.

Thank you for the comment. We have added further details to appendix F explaining some of the theoretical motivation for our RR approach. To summarize, [3] showed that GNNs struggle to generalize to new types of graph structures at test time. In particular, GNNs struggle more severely when graphs are not regular. Therefore, we were motivated to make the molecular graph structures at test time more similar to the training distribution (and more regular). To characterize graph connectivities, we study the eigenvalue distributions of Laplacian matrices. We find that by aligning spectra, we can make test graph connectivities that resemble training connectivities, making test connectivities more regular and helping MLFFs generalize better (see our new Fig 15 in the paper).

Comment: Statistical analyses for Table 1.

We have added 95% confidence intervals to Table 1. As you mentioned, when considering systems from SPICEv2 without new elements, the improvements from RR are not significant in aggregate. All other differences in the table are significant (including TTT results and RR across the whole test set). We also note that the reason the differences are small in this table is because this is aggregated over the 10,000 test molecules from SPICEv2. Many molecules only improve a little with TTT and RR when the system is already very close to in-distribution. For individual molecules, the differences are much larger for both RR and TTT (see Tab. 2 and Tab 3). Our new Fig. 10 also highlights that many molecules improve significantly with RR and TTT.

[1] Yu Sun, et. al. Test-time training with self-supervision for generalization under distribution shifts, 2020.

[2] Yossi Gandelsman,et. al. Test-time training with masked autoencoders. Advances in Neural Information Processing Systems, 2022.

[3] Maya Bechler-Speicher, et. al. Graph neural networks use graphs when they shouldn’t, 2024. URL https://arxiv.org/abs/2309.04332.

We would like to thank the reviewer for the thoughtful and constructive feedback. We are happy that you find our analysis of current MLFFs interesting for the community.

Comment: Performance is still magnitudes away from the desirable chemical accuracy.

We want to emphasize that errors are not “magnitudes away” from chemical accuracy. For many individual molecular systems, the errors are brought down by up to an order of magnitude, and for many systems (more than 8,000 / 10,000) the errors are below 25 meV / Å on SPICEv2. In section 4.2 with MD17, errors are brought down from >200 to less than 22 meV / Å for both naphthalene and toluene, enabling stable simulations. Section C.4 has errors well below 30 meV / Å on MD22. We have also added Fig. 10 that explicitly shows that many molecular systems start with higher errors and get errors brought down closer to ID performance with TTT and RR.

We note that our experiments establish a lower bound on the performance gains that can only be improved with further architectural and training innovations. They can also help us understand how MLFFs generalize, and they provide evidence for the hypothesis that MLFFs can be trained to generalize more effectively.

Comment: The actual distance for radius refinement is quite simple, and may not capture more detailed information in the graph connectivity.

This is an interesting point made by the reviewer. While we experimented with using more complicated distance metrics for measuring discrepancies between graphs (such as a KL-divergence between eigenvalue distributions), we found that it made minimal difference in performance compared to the heuristic used in the paper. We have clarified this in appendix E and F, and we think it is an interesting direction for future research to further study distribution shifts in graph structure.

Comment: Also, for the train eigenvalues, since we could have multiple molecules during training, do we aggregate their overall eigenvalue distribution?

Yes, that is correct! Based on our heuristic, we calculate the percentage of graph Laplacian eigenvalues that fall within the range of [0.9, 1.1] for each molecule in the SPICE training dataset. We then average this percentage across training molecules to represent the training distribution. As mentioned above, we experimented with more involved versions of representing the training distribution, such as averaging probability density functions of eigenvalue distributions, but found that this made little difference since the connectivity was so uniform across the training molecules (generally regular well connected graphs). We have clarified this in appendix E and F.

Comment: As long as there is one training molecule graph that is similar to the test, the generalization performance could be better.

This is an interesting point. However, a single data point with a “new” connectivity is not enough for the model to generalize to these structures. This can be seen in Fig. 6 where the errors smoothly go up for connectivities that are more poorly represented in the training distribution (shown in gray).

Comment: More case studies should be provided for RR

We have added Fig. 15, to further clarify the effect of RR on graph connectivity. For those molecular systems where the connectivity does change by refining the radius (for some molecular systems the connectivity doesn’t change unless the radius is made very small), we clearly see that RR decreases the difference in connectivity when compared to the training distribution. This is measured based on our eigenvalue heuristic. The training graphs had an average of 55% of their eigenvalues in the range of [0.9, 1.1]. We calculated the absolute difference between this training percentage, and the percentage of eigenvalues that fell in [0.9, 1.1] before and after RR. We also observe that the standard deviation of node degree decreases after RR, indicating that graphs become more regular. This improved connectivity translates into the improved errors seen in Fig. 6 and Table 1.

Comment: The idea of test-time-training is not novel, and many previous works have utilized low-cost priors for MLFF training/fine-tuning.

We appreciate the feedback. To the best of our knowledge, prior work has not used TTT in the field of MLFFs, although as you mention, TTT has been explored in other areas of machine learning. We provided an in-depth discussion comparing our methods to other multi-fidelity work in the field in appendix A. To summarize here, in contrast to previous multi-fidelity works, our TTT and RR methods explicitly tackle the problem of generalization. We also explore freezing and joint training approaches that explicitly enable addressing distribution shifts. Our experiments help us understand how current MLFFs fail to generalize, and they suggest that MLFFs can be more effectively trained to handle distribution shifts. Our approaches can also be combined with other multi-fidelity work, such as Delta learning, to further boost performance.

Comment: Some assumptions about the generalization issue may not be practical

While we agree that generalizing to new elements and substructures is challenging, we argue that this should be a goal to aim for with foundation MLFFs, especially given that first-principles methods are mostly able to tackle arbitrary substructures. Our experiments in section 2 are targeted at understanding the generalization gaps that a good MLFF should be able to capture, which can help guide the development of new MLFFs. Our experiments in section 4 take first steps at mitigating these distribution shifts formalized in section 2. We show through TTT and RR that MLFFs are expressive enough to generalize to new elements and substructures (see Fig. 7b where errors on new elements are well below 40 meV / Å for the top 10% of molecules and section 4.2 where TTT enables simulation of new molecules). These results can only be further improved with architecture, data, and training innovations. This is intentionally designed as a challenging evaluation, and we highlight it because the community is moving towards more general models that aim for better OOD performance.

Comment: The main paper should include at least a brief summary of the related work.

Due to space limitations, we had included only a short paragraph in the introduction about related works (lines 86-89) in the main text, and we had a longer section about the rest of the related works in appendix A. We have cut down the manuscript and reordered it to include more discussion of the related work in the main text.

We appreciate the reviewer’s comments and detailed feedback. We respond to specific points below.

Comment: There is still a gap in performance to ID, making the method not entirely practical

Our paper is about both understanding and mitigating distribution shifts. We characterize and understand the distribution shifts in section 2 in order to motivate the strategies presented in section 3. In turn, the mitigation strategies provide insights into why MLFFs are susceptible to distribution shifts, namely overfitting and poorly regularized representations (as opposed to only poor data or weak architectures).

In addition to these mitigation strategies helping us understand how MLFFs fail to generalize, our test-time refinement strategies take first steps at mitigating distribution shifts. We agree that there is still a gap in performance to ID, and we emphasize that matching in-distribution performance without access to reference labels is in general an extremely challenging machine learning problem. Achieving in-distribution performance in an out-of-distribution task is an extremely high bar since we are updating fewer parameters and not using ground truth labels. Nevertheless, our new Fig. 10, section 4.2 MD17 results, and section C.4 MD22 results show that the majority of errors are below 25 meV / Å (>8,000 / 10,000 for SPICEv2, and all the MD17 and MD22 results). Beyond enabling stable simulations (section 4.2), TTT also drastically reduces the amount of data needed for further fine-tuning (see further details below and the new Fig. 18), showing practical utility.

Comment: I feel that the work's technical contribution is limited.

We understand that the assessment of technical contributions can be somewhat subjective. To provide further clarity, we highlight and clarify some of the key contributions made by the paper, which we believe demonstrate its significance and impact:

• We formalize multiple common distribution shifts faced by MLFFs.
• We show that multiple state-of-the-art models predictably struggle with these distribution shifts.
• We show how to address connectivity distribution shifts with our test-time radius refinement algorithm.
• We describe how to implement test-time training for MLFFs with a cheap prior
• We demonstrate with extensive experiments that our test-time refinement strategies are effective at mitigating distribution shifts.
• We demonstrate that these mitigation strategies also provide insights into why MLFFs are susceptible to distribution shifts

The success of these methods and the predictability of the distribution shifts suggest that MLFFs are indeed overfitting to training distributions, and that they can be better trained to generalize. Our experiments also provide benchmarks for evaluating the generalization ability of MLFFs.

Comment: I don't see an intuitive explanation for “more complicated strategies might not bring benefits”

We have added appendix F, which provides theoretical motivation for why GNNs overfit to training graph structures and generalize better with regular graphs. Fig. 15 shows that empirically, RR brings graphs closer to the training distribution at test-time by making graphs more regular. Even though it is hard to formalize an “intuition” for this, based on the theoretical results discussed in appendix F, any method that makes graphs more regular would likely help mitigate connectivity distribution shifts. Although it is possible that more complicated methods for quantifying and modifying graph connectivity could bring benefits for certain systems, we did not see this clearly in empirical results and our current instantiation of RR still provides evidence that MLFFs do overfit to graph distributions.

Comment: The authors reply that TTT can be used together with fine-tuning/active learning but leave the investigation to future work

TTT can be readily used together with other methods. To illustrate this point, we have added Fig. 18 in the paper to show that a model after TTT requires 10x less data when fine-tuning on an OOD molecule to get to the in-distribution performance (<15 meV / Å on MD17), compared to a model without TTT. The results are shown in the following table:

Comment: Some theoretical guarantees based on the size of the available data

In general, guarantees about errors as a function of data are challenging to make precise in the field of deep learning. Although there are rigorous guarantees for simplified cases, like linear models [5][6], results for deep learning models often take the form of empirical scaling laws driven by large amounts of computing power [2][3]. In this regard, in the context of our paper, see Fig. 17 for a scaling experiment with TTT.

This same issue holds for any fine-tuning or active learning method, where there are few theoretical guarantees to dictate how much data is needed to reach a certain level of performance. We do think further theoretical work on understanding fine-tuning in the field of deep learning is an interesting direction for research, and is likely a paper in and of itself [1][2][3][4].

Comment: How should the user know and modify if they don't have test data to verify?

We note that this issue of evaluating a model with limited data also applies to any other active learning or fine-tuning techniques (or any machine learning method for that matter): if one wants to verify an answer on a test set, one needs to calculate the ground truth label. One option to evaluate MLFFs with limited data is to look at simulation stability to determine the accuracy of a model. However, we expect that this approach would only rule out very bad models. Additionally, when using TTT, the accuracy of the prior head can be used to estimate how close the main task error is to the in-distribution performance (see Fig. 9b).

[1] Utkarsh Sharma, & Jared Kaplan. (2020). A Neural Scaling Law from the Dimension of the Data Manifold.

[2] Jared Kaplan, Sam McCandlish, Tom Henighan, Tom B. Brown, Benjamin Chess, Rewon Child, Scott Gray, Alec Radford, Jeffrey Wu, & Dario Amodei. (2020). Scaling Laws for Neural Language Models.

[3] Jordan Hoffmann, Sebastian Borgeaud, Arthur Mensch, Elena Buchatskaya, Trevor Cai, Eliza Rutherford, Diego de Las Casas, Lisa Anne Hendricks, Johannes Welbl, Aidan Clark, Tom Hennigan, Eric Noland, Katie Millican, George van den Driessche, Bogdan Damoc, Aurelia Guy, Simon Osindero, Karen Simonyan, Erich Elsen, Jack W. Rae, Oriol Vinyals, & Laurent Sifre. (2022). Training Compute-Optimal Large Language Models.

[4] Roberts, D., Yaida, S., & Hanin, B. (2022). The Principles of Deep Learning Theory: An Effective Theory Approach to Understanding Neural Networks. Cambridge University Press.

[5] Daniel Hsu, Sham M. Kakade, & Tong Zhang. (2014). Random design analysis of ridge regression.

[6] Ng, A., & Jordan, M. (2001). On Discriminative vs. Generative Classifiers: A comparison of logistic regression and naive Bayes. In Advances in Neural Information Processing Systems. MIT Press.