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- Informativeness
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- Presentation
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Paper summary
The authors introduce PriorFuse, an exactly enumerable synthetic benchmark for studying how closely Prior-Data Fitted Networks (PFNs) approximate the Bayesian posterior predictive distribution induced by their training prior. The benchmark uses finite families of Boolean functions, enabling exact Bayesian model averaging (BMA). The authors train several PFNs and compare their predictions with exact BMA and different modifications of Bayesian inference, including family tempering, likelihood tempering, and output calibration.
The experiments show that increasing the inference-time context length can improve predictive performance while increasing the discrepancy from exact BMA. The authors also find that likelihood tempering provides a useful description of this discrepancy, with an inverse-length scaling of the likelihood exponent closely approximating the exponent fitted separately at longer context lengths. Additional experiments study training dynamics, a second synthetic prior, and the dependence of fitted family parameters on the representation of the prior.
Critical strengths
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The exact Bayesian reference enables a controlled evaluation of PFNs.
The use of finite and enumerable hypothesis spaces allows the authors to compute exact Bayesian posterior predictive distributions without relying on approximate inference. This provides a useful setting for studying how PFN predictions differ from their intended Bayesian target, particularly for distinguishing predictive performance from Bayesian fidelity.
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The proposed structured candidate descriptions are theoretically motivated and interpretable.
The authors introduce a comprehensive set of candidate descriptions grounded in established Bayesian concepts, including family tempering, likelihood tempering, and alternative predictive transformations. These candidates modify different components of Bayesian inference, providing a principled framework for characterizing how PFN predictions depart from exact BMA. I particularly appreciate that the authors distinguish these behavioral descriptions from claims about the networks' internal inference mechanisms.
Critical weaknesses
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The experimental findings have limited validation and generalizability, and the candidate comparisons do not fully characterize the observed Bayesian departure.
The main context-length experiment evaluates PFNs trained exclusively with eight examples on contexts containing up to twelve examples. As the authors acknowledge, this makes it difficult to distinguish systematic Bayesian approximation errors from generalization failures at unseen context lengths. Moreover, context-dependent feature normalization introduces an additional confounding factor, while the inverse-length scaling relationship is proposed post hoc and evaluated over a limited range of context lengths.
The generalizability of the findings is also unclear. The main experiments use small nanoTabPFNs and a sixteen-input Boolean domain. Although the authors include a larger-architecture comparison, it does not evaluate the central context-length or inverse-length scaling findings. Consequently, it remains uncertain whether the observed patterns extend to realistically sized PFNs or more complex task distributions.
Additionally, the candidate descriptions are mostly evaluated independently, although they may capture complementary aspects of the PFN's approximation error. For instance, likelihood tempering and output calibration could jointly explain discrepancies that neither captures individually. The candidates also have different expressive capabilities, limiting the conclusions that can be drawn from their relative performance.
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The manuscript is difficult to read, and the main contributions and conclusions are not clearly communicated.
I found the presentation unnecessarily complex, particularly in the results section. The authors report numerous detailed numerical comparisons without sufficiently describing the behavioral patterns they reveal or explaining their scientific implications. Consequently, the results often read as a sequence of numerical observations rather than a coherent analysis of how PFNs depart from Bayesian inference. The discussion also moves between different experimental objectives without clearly connecting the findings or highlighting their main takeaways.
Furthermore, although PriorFuse is presented as a benchmark, the manuscript does not clearly explain what constitutes the proposed benchmark as an independent contribution or how it is intended to be used beyond the reported experiments. Even after reading the full manuscript, I found it difficult to identify precisely what PriorFuse encompasses. I believe the paper would benefit substantially from a clearer definition of the benchmark, a more interpretable discussion of the observed PFN behaviors, and a more focused presentation of its scientific conclusions.
Questions for authors
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Have you evaluated PFNs trained with different or variable context lengths? Does the increasing Bayesian departure persist when training and evaluation lengths match?
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Does the handcrafted inverse-length scaling relationship hold for other training context lengths or under the second prior?
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How do the context-length results change when feature normalization is independent of context length?
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Do the main context-length and likelihood-tempering findings persist with larger PFN architectures? To what extent can PriorFuse provide insights into realistically sized PFNs?
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Have you evaluated likelihood tempering combined with output calibration? Does it improve over likelihood tempering alone?
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Could you explicitly clarify which components constitute PriorFuse as a reusable benchmark and what distinguishes it from existing synthetic Bayesian inference benchmarks?
6 comments
New controls for training context length and feature scaling (2/2)
W2/Q6. What is the benchmark and what does it add? Section 3 (see Figure 1 for the benchmark overview) now defines the generator, exact predictor and evaluation protocol before introducing the candidates. To reuse PriorFuse, train a model on the specified prior, score the model and Bayes on the same queries as context length changes, then fit any candidate on the calibration groups and evaluate it separately. Bayesian Prism already compares transformers with tractable Bayesian predictors across task families, and Kang et al. vary the training range in Gaussian process regression. PriorFuse matches aggregate label exposure and varies feature scaling separately from training length. This exposes a short context cost and a residual departure that a long context improvement alone would miss. It also tests whether fitted parameters change when we regroup the same prior.
W2. Readability of the results and discussion. Thank you for the feedback, we have made substantial revisions to the prose, aiming to improve the readability and connection between ideas. The revised paper explains what PriorFuse contributes, why each experiment is included, and how the findings can have practical benefits for PFNs. Sections 4 to 6 now ask in order what changes the departure from Bayes, which candidate predictions account for it, and whether it changes the cost of a decision. We moved the detailed original classification comparisons to Appendix P so the main text can focus on what the figures show. Section 7 explains why gains at longer contexts should be weighed against losses at the original training length.
Thank you for the detailed responses and the substantial additional experiments. The authors have addressed several of my main methodological concerns, particularly through the controlled comparison of training context lengths and feature normalization, and the evaluation of combined candidate descriptions.
Nevertheless, I believe three limitations remain relevant:
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Generalizability of the inverse-length adjustment (Question 2). The successful transfer to the second Boolean prior and larger models is encouraging. However, all evaluations of this adjustment still use models trained at eight examples and assess relatively nearby context lengths. Consequently, the results establish a useful empirical description within the evaluated settings rather than a general scaling relationship.
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Applicability to practical PFNs (Question 4). The larger-architecture and continuous-regression experiments substantially strengthen the results. However, the experiments with a released TabPFN checkpoint remain inconclusive regarding whether the same increase in Bayesian departure occurs in realistic pretrained PFNs. I therefore believe the practical implications should be framed cautiously.
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Critical issue: Presentation and clarity of the manuscript. Despite the revisions, I still find the paper very difficult to follow. This concern was also explicitly raised by another reviewer, who similarly highlighted substantial problems with the organization, clarity, and communication of the main contributions. In my opinion, the revised manuscript has not substantially addressed this issue. The motivation behind the different experiments, the connections between the proposed analyses, and the interpretation of the results still require considerable effort from the reader. While I acknowledge the additional experiments and methodological improvements, I believe that the clarity and presentation of a scientific contribution are essential aspects of its quality. In its current form, I do not think the manuscript reaches the presentation standards expected at ICLR.
Overall, I acknowledge that the authors have made a significant effort to address the methodological concerns raised in my original review. However, the remaining limitations, and particularly the unresolved issues with the clarity and presentation of the manuscript, prevent me from recommending acceptance in its current form. I believe that a substantial rewriting and reorganization of the manuscript is necessary to clearly communicate its contributions and findings. Without such improvements, I am unfortunately unable to increase my original score, despite recognizing the authors' efforts and the additional experimental evidence provided.
New controls for training context length and feature scaling (1/2)
We appreciate the suggestion to test whether the rise in excess log loss comes from unfamiliar context lengths or from feature scaling. Varying these two factors independently shows that training on a range of context lengths reduces the rise but does not eliminate it, even when feature scaling is held fixed. We also test the length adjustment under a second prior and in larger models, and compare the joint likelihood and output fit with each component alone.
W1/Q1. Does the increase persist when longer contexts appear in training? Yes, but it becomes smaller. The PFNs in the submitted Section 4 trained at eight examples per context. In Section 4.2 and Figure 3A of the revised paper, we train new models either at eight examples or at lengths two through twelve, using three matched initialization and task stream seed sets, the same architecture and equal total counts of context and query labels.
Mean increase in excess log loss from 8 to 12 examples at 100k updates, in nats.
Predictive log loss falls in all four conditions, even as excess log loss rises. Under population scaling, training on variable lengths improves agreement with Bayes at twelve examples but worsens it at eight in all three pairs (Appendix Q). The increase therefore persists within the range seen in training. This is not a comparison with a separately trained model at each length.
Q2. Does the adjustment transfer to another prior or training length? It transfers to the second Boolean prior with training and calibration at eight examples. We chose the adjustment after seeing the original length results, but fixed it for the second prior before inspecting the new results. At twelve examples and 100k updates, mean reductions in PFN matching KL relative to the unmodified BMA candidate are 0.006665 for the adjustment, 0.006674 for refitting and 0.001498 for leaving the exponent unchanged. The adjusted rule recovers a median 99.9% of the gain from refitting. Revised Section 5.2 and Appendix T report the individual models. The evidence for the adjustment is limited to transfer from eight to nine through twelve examples. We did not test a different fixed training length or validate the rule farther from the fitting length. The regression experiment extends the comparison of training lengths to 32 examples, but does not test this adjustment.
Q3. Can scaling features from the context explain the result? Not on its own. The second row of the Q1 table shows that excess log loss still increases when we scale features using fixed population statistics. Training on variable lengths still reduces that increase (Figure 3A). The model continues to use the mean of the context labels in place of the missing query label, so this comparison changes feature scaling but not every operation that uses the context.
Q4. What carries over to larger PFNs? The submitted Appendix K compared a larger classifier at eight examples. We now evaluate that model, which has six layers and 1.23 million parameters, across the length sweep and compare with smaller models trained at the same learning rate. At 20k, the mean rise in KL from PFN to BMA between eight and twelve examples is 0.01442 for the larger models and 0.02185 for the smaller ones. The larger models recover 98.49% to 98.96% of the gain from refitting across lengths nine to twelve using the adjustment (Section 5.2 and Appendix T). Section 4.3 adds a larger model for continuous regression. These comparisons test changes in capacity and task distribution under known priors. They do not establish that the same adjustment holds for a released TabPFN trained on a different prior.
Q5. Does combining likelihood tempering and an output transformation help? Yes. At twelve examples and 100k updates the joint fit reduces KL from PFN to candidate by 0.000098 compared with likelihood tempering alone and by 0.003684 compared with an output transformation alone. Both gains occur in all five original models. We fit on calibration tasks and evaluate on separate tasks. The joint model fits three parameters and is more flexible than either component alone. Appendix S lists what each candidate changes, its parameter count and its restrictions. For queries within the interval between the exact family predictions, family tempering fits better than likelihood tempering in all five models at both checkpoints (Section 5.3 and Appendix G). These comparisons describe what the candidates can reproduce, but not which operations the PFN carries out.