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Under review as a conference paper at ICLR 2027

PriorFuse: How Prior-Data Fitted Networks Depart from Bayes

Abstract

Prior-Data Fitted Networks (PFNs) let researchers specify prediction rules through synthetic task priors and are trained to approximate the corresponding Bayesian posterior predictive. However, specifying a Bayesian target does not guarantee that a finite trained network will use new evidence as that target would. To study this question, we introduce PriorFuse, an exactly enumerable benchmark in which the target posterior predictive can be computed exactly by Bayesian model averaging (BMA). For five PFNs trained only with eight context examples, supplying twelve examples improves predictive log loss while increasing excess log loss over exact BMA approximately ninefold at 100k training steps. We show that the trained PFNs exhibit a systematic Bayesian departure: fitted likelihood weighting changes from amplification at several shorter context lengths to attenuation at longer lengths. At the tested longer lengths, a post hoc inverse-length adjustment to the exponent fitted at eight examples recovers about 99% of the improvement in matching PFN predictions achieved by refitting at each length, and unchanged transfer recovers much less. The same matched-length attenuation pattern also appears under a second task prior and weakens with further training. Equivalent representations of the same prior also change fitted family parameters without changing either predictor. PriorFuse thus helps researchers distinguish better prediction from more faithful inference and identify which parts of a learned prediction rule change with training and context.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
Prior-Data Fitted Networks, Bayesian model averaging, in-context learning, Bayesian inference, likelihood tempering, synthetic priors, tabular foundation models

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_iF3WOpenReview ↗
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1
Confidence
2
Informativeness
2
Presentation
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Soundness
2
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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
  1. 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.

  2. 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
  1. 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.

  2. 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
  1. Have you evaluated PFNs trained with different or variable context lengths? Does the increasing Bayesian departure persist when training and evaluation lengths match?

  2. Does the handcrafted inverse-length scaling relationship hold for other training context lengths or under the second prior?

  3. How do the context-length results change when feature normalization is independent of context length?

  4. 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?

  5. Have you evaluated likelihood tempering combined with output calibration? Does it improve over likelihood tempering alone?

  6. Could you explicitly clarify which components constitute PriorFuse as a reusable benchmark and what distinguishes it from existing synthetic Bayesian inference benchmarks?

6 comments
AuthorsOpenReview ↗

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.

Feature scalingFixed training lengthVariable training lengths
From the context0.013250.00250
From fixed population statistics0.014060.00307

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.

AuthorsOpenReview ↗

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:

  • 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.

  • 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.

  • 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.

Reviewer_iVhnOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
1
Soundness
2
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Paper summary

The paper aims to diagnose a departure of a small, pretrained PFN from its Bayes-optimal posterior predictive distribution (PPD) using a synthetic data generating process that is called PriorFuse. The main finding is that PFN indeed deviates from the true PPD at settings different from pretraining configurations. The draft also proposes a likelihood exponent calibrated on test data to suggest a possible explanation of the observed error of PFN.

Critical strengths

I like the construction of a synthetic data generating process where exact Bayesian model averaging is feasible. This can serve as benchmark to detect systematical deviation of a pretrained PFN from the population optimal Bayesian prediction rule.

Critical weaknesses

** The paper needs significant improvement in writings. **

  • Introduction contains terms like "likelihood-weighting description" and "post hoc length adjustment" before properly explaining them. This makes the sentences and paragraphs containing these words essentially uninformative, leaving the readers confused. Also, the authors list possible scenarios of how PFN can show improved loss by pretraining, but that sentence is followed abruptly by unrelated remark on distribution shift and output calibration. Moreover, the authors claim Priorfuse can help distinguish among the three possibilities, without explaining why.
  • This pattern of disconnected, random disposition is common throughout the draft, especially in the experiment sections. It is not clear in its current writing what the main hypothesis is, how it is being tested, and how figures and tables support what conclusions for each experiment. Currently, it only has mechanistic description of experiment design without purpose, followed by some description of numbers, and unusually lengthy disclaimer and antithesis.
  • Overall, it required sizable cognitive effort to try to connect the dots scattered throughout the paper. After careful reading, I still found myself hardly convinced what the main novel contribution of the paper is, which leads to the next critical weakness.

** It is not clear what the novelty and contribution of the draft is. **

  • So far, the draft has successfully reported an observation that "PFN deviates from PPD". But that result is not surprising at all, since it is a network approximation to the true prediction rule in the first place. What is more interesting and practically relevant is why/when/how does this deviation happen. The authors proposed a likelihood exponent, but as acknowledged by the authors, it is not a diagnostic tool, more of a description tool. It has statistical meaning as an approximation to pretrained PFN under some restricted function class, but I am not convinced that it represents or explains failure modes of PFN.
  • As the authors noted, several precedents like Bayesian Prism had already employed a usage of tractable Bayesian models for diagnostic of PFN. It is not clear what specifically does PriorFuse add on top ot these line of work.
Questions for authors

My main question is how much the observations and conclusions drawn from a small nanotabPFN pretrained on a specific binary-response synthetic task with only eight context length be extended to a much larger PFN with pretrained on more diverse data generating process. To address this, it could be helpful to (1) extend to continuous response, using models whose PPD is analytically tractable such as mixture of GP regressions, and (2) test if the observations also hold for larger PFN with more parameter counts.

Also, other than a likelihood exponent, could the authors come up with more robust diagnostic tools that can derive faithful explanation of how PFN deviates from PPD, and extend this to practical suggestions relevant to actual PFN training. model design or interventions?

Lastly, please improve the overall presentation of the draft. More readable writing alone itself would substantially better position the current draft I believe.

8 comments
AuthorsOpenReview ↗

PriorFuse's contribution, with new regression evidence

We agree that observing a departure from Bayes is not enough to explain what a PFN has learned. A new comparison in the revised paper shows that training on a range of context lengths improves agreement with Bayes at longer lengths but worsens it at eight examples, even with fixed feature scaling. We find a similar tradeoff with continuous responses and clarify which data we use for fitting and evaluation.

W1. Writing and presentation. We have substantially revised the paper to improve its readability, and to establish a clear flow between ideas. We have also addressed the three presentation concerns separately.

  1. Terms before definitions. The Introduction first explains how a PFN can predict better while falling farther behind Bayes. Section 3.2 defines likelihood tempering before Section 5 uses it to interpret the fits and introduces the length adjustment.
  2. Why PriorFuse separates the explanations. Section 3 explains what comparing the same context and query under the same prior makes observable. Section 4.2 then separates the range of lengths seen in training from the choice of feature scaling. Section 5.3 tests whether changing the final probabilities adds anything beyond changing the likelihood.
  3. How the experiments support the conclusions. Section 4.2 poses the question before presenting Figure 3A and uses the figure to show what remains when longer contexts are seen in training and feature scaling is fixed. The subsequent sections ask what the candidates explain and whether the difference changes abstention costs. We moved detailed classification comparisons to Appendix P so the main text can develop those conclusions.

W2. What the controlled comparison teaches us. Broader training improves agreement with Bayes at longer contexts, but it can make agreement worse at the length the original model already handles well. Seeing the longer lengths in training also does not eliminate the departure. Under fixed population scaling and matched label exposure, the rise in excess loss from eight to twelve examples falls from 0.01406 to 0.00307 nats, while agreement at eight worsens in all three paired runs (Section 4.2, Figure 3A and Appendix Q). Bayesian Prism already compares transformers with tractable Bayesian references, and Kang et al. study how pretraining range, depth and attention normalization affect Gaussian process prediction. Our comparison shows why evaluating only the longer contexts can give a misleading account of what broader training changes, even when both models see the same number of labels.

Q1/2. Continuous responses and larger models. We use a single Gaussian process so the exact predictive distribution at each query is Gaussian and the six-layer PFN's Gaussian output can represent it. A mixture would add a second question about whether the output family can represent the exact mixture predictive. With the single process, training on a range of lengths reduces excess log loss from 0.05567 to 0.01175 at 32 examples, with a paired reduction of 0.04391 nats and a 95% interval of [0.04325, 0.04457] conditional on the trained models. At eight examples excess loss rises from 0.00241 to 0.00282 (Section 4.3 and Appendix R). We also extend the larger classifier comparison to the full Boolean length sweep and evaluate the transfer rule under the second Boolean prior (Section 5.2 and Appendix T). The regression result does not establish that the tradeoff holds under mixtures of Gaussian processes.

What the fitted descriptions establish. Global exponents are fitted on calibration tasks and evaluated unchanged on separately sampled tasks, as specified in the submitted Sections 3.3, 4 and 4.1 and in the revised Section 3.3. A separate diagnostic fits a per-context quantity on three unseen inputs and evaluates it on five different inputs from that context. Independent sampling of global calibration and evaluation tasks does not rule out repeated contexts on a finite domain. We now show both KL directions, the contributions of the predictive mean and variance in regression, and how candidate comparisons depend on whether PFN predictions lie between the family predictions. Regrouping the same prior changes fitted family weights without changing either predictor. Adding an output transformation changes the fitted likelihood exponent as well as improving the match (Section 5.3). These checks show what the fitted descriptions explain without identifying an internal mechanism.

Implications for PFN training. The new coverage comparison gives a reason to evaluate a change to training at the lengths a model already handles well as well as at longer lengths. Section 6 shows where calibration using observed labels also improves decisions.

Reviewer_iVhnOpenReview ↗

Serious writing problem

Thank you for the revisions and additional experiments. However, I still find the writing difficult to follow. Since the authors asked for specific examples, I will use the abstract to illustrate the problem.

Giving a Prior-Data Fitted Network (PFN) more labeled examples can improve its predictions even as it falls farther behind the Bayesian predictor it was trained to approximate.

What do you mean by more labeled examples? Additional examples during pretraining, or additional context examples at inference time? What exactly does "falls farther behind" mean?

We introduce PriorFuse to measure what a PFN and exact Bayesian Model Averaging (BMA) gain from the same additional observations.

What are these additional observations, and where are they introduced? During pretraining or inference?

In our Boolean benchmark, five classifiers recover about three quarters of the Bayesian reduction in log loss from eight to twelve examples at 100k updates.

What is the "Bayesian reduction in log loss"? What loss is being measured? What do eight and twelve examples refer to? Why are these numbers important? The reader has not even been told that the original PFNs were pretrained with eight context examples.

Training on a range of lengths recovers more of that gain even when label exposure is matched and feature scaling is fixed, but worsens agreement at eight examples.

What is "label exposure"? Why does "feature scaling" suddenly appear? What does "agreement" mean, and agreement with what? Are we now talking about training a different PFN?

The same tradeoff occurs in Gaussian process regression.

Okay, a similar result also holds in GP regression. This extension is understandable, provided the preceding tradeoff has been properly explained.

To characterize what remains at longer classification contexts, we compare the PFN with a Bayesian predictor that gives the labels less weight, which reproduces much of the difference in their probabilities.

What do you mean by "what remains"? Are we studying the PFN trained with variable context lengths, or returning to the original PFN? What does "giving labels less weight" mean? What exactly is being fitted to what? How does this analysis explain the previous observations?

Whether that difference matters for a decision is a separate question.

Why are we suddenly introducing another question? What decision are we talking about, and how does this connect to the previous experiment?

When the original classifiers can predict or abstain, calibrating on observed labels lowers expected decision cost at twelve examples, with no clear benefit at eight.

What does "abstain" mean here? What does calibration involve? Is this calibration related to the previous likelihood-weighting analysis, or is it a separate intervention?

PriorFuse helps identify where a change to training helps or hurts before evaluation on tasks without an exact reference.

How does this conclusion follow from the preceding sentences? What exactly has PriorFuse established that can guide training on other tasks?

After reading the entire abstract, the reader is left having to reconstruct the experimental setup, the meaning of the comparisons, and the connections between experiments. Many of these questions are answered somewhere in the paper, but that does not resolve the problem with the abstract. An abstract should communicate the main argument clearly without requiring readers to consult the methods to understand nearly every sentence.

For example, I believe the authors could have written something along the following lines.

Abstract

Prior-Data Fitted Networks (PFNs) are trained on synthetic prediction tasks to approximate the Bayesian posterior predictive distribution under a specified prior. However, a trained PFN may not use additional observations as effectively as the exact Bayesian predictor. We study this discrepancy using PriorFuse, a synthetic benchmark where exact Bayesian prediction can be computed. We first train five PFNs using eight labeled context examples per task. At inference, increasing the context length from eight to twelve improves their predictive loss, but the exact Bayesian predictor improves more, increasing the gap between them. We then train new PFNs using variable context lengths. These models are closer to exact Bayes at twelve examples but slightly worse at eight, even when the total number of training labels is matched and input feature scaling is fixed. We observe a similar tradeoff in Gaussian process regression. Next, we return to the original PFNs and characterize their prediction errors by fitting modified Bayesian predictors to their outputs. At longer contexts, their predictions are well approximated by a Bayesian predictor with a weakened likelihood, although this does not explain the network's internal mechanism. Finally, we separately calibrate the PFNs' output probabilities using labeled data and evaluate whether calibration improves decisions when the classifier can either predict a label or abstain. Calibration reduces decision cost at twelve examples, but not clearly at eight. These results provide a controlled evaluation of how PFN predictions depart from exact Bayes, how training on different context lengths affects this departure, and when output calibration can improve downstream decisions.


This is only an illustrative rewrite, not necessarily the best possible abstract. The main difference is that each experiment is introduced with its setup and purpose, its results are explained in plain language, and transitions explicitly identify when the authors change models or objectives.

Reviewer_W3xpOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

PriorFuse is a small benchmark of rules on 4 inputs, where the exact Bayesian prediction (BMA) can be computed and compared with the predictions of PFNs. When given more examples than they were trained on, the PFNs predict better but fall further behind BMA. Model over-trust evidence at short contexts and under-trust it at long ones.

Critical strengths

Exact reference

  • The benchmark is small enough that the exact Bayesian prediction can be computed for every context. So departures from Bayes are measured directly rather than estimated.

Careful methodology

  • The analysis has a prespecified protocol and an independent evaluation set.

Novel Takeaway

  • Separates prediction from Bayesian fidelity. The paper shows that better predictive loss doesn’t mean behaving more like Bayes, and that fitted parameters can depend on how the prior is grouped. Both are useful cautions for anyone evaluating or interpreting PFNs.
Critical weaknesses

Downstream task Effect

  • The paper does not identify any task in which the observed departure from Bayes is harmful, or in which reducing it yields a benefit. Could the authors show a downstream task, for example one relying on uncertainty estimates such as active learning or selective prediction, where this departure measurably degrades performance, and where reducing it, for instance by adjusting predictions using the fitted likelihood exponent, improves performance?

Diversity

  • The study uses a single small domain (4 binary inputs, 16 possible inputs) and essentially two families of rules. It would strengthen the paper to include a broader and more diverse set of functions and families

Practicality

  • The paper offers neither methods nor practical guidance. It shows that trained PFNs depart from exact BMA, especially beyond the training context length, but does not discuss how a practitioner could detect this departure when no exact Bayesian reference is available, or how to choose training context lengths to avoid it.

Overall, I enjoyed reading the paper. I am not well placed to fully judge its novelty relative to prior work. However, I encourage the authors to strengthen the connection between their benchmark and real-world use of PFNs, as this would substantially increase the paper’s impact.

Questions for authors

N/A

1 comment
AuthorsOpenReview ↗

Decision costs and calibration across context lengths

To address the concern about practical relevance, we now measure the cost of predicting or abstaining in the revised paper. Calibration on observed labels lowers decision cost for the original PFNs at twelve examples, but not clearly at eight. We also test whether the tradeoff from training on a range of context lengths extends to continuous responses.

W1. Effect on selective prediction. Calibration using observed labels removes about one third of mean regret relative to the Bayes decision at twelve examples, averaged over the five original models at 100k and nine abstention costs. Without calibration, regret rises from 0.00075 at eight examples to 0.00656 at twelve. At twelve, calibration lowers mean decision cost by 0.00218, with a 95% interval of [0.00204, 0.00225] conditional on the trained models, and lowers excess log loss by 0.00512 nats. The fit uses neither the exact reference nor the likelihood exponent. It shows no clear gain for the original models at eight or for the models trained on variable lengths with population scaling at twelve. Section 6, Table 1 and Appendix U report all nine costs and coverage. The two improvements occur together, but this does not establish that one causes the other.

W2. Diversity. The original domain is small so we can compute exact Bayes for every query. The second Boolean prior changes the function families while retaining the input domain (Appendix M). We now extend the length sweep to that prior and add continuous inputs and responses from a known Gaussian process (Sections 4.3 and 5.2, Appendices R and T). Training on variable lengths brings the regression models closer to Bayes at 32 examples and slightly farther away at eight. The public data and richer synthetic comparisons lack an exact Bayesian reference, so they cannot replicate this test.

W3. Practicality. Without exact Bayes, practitioners can compare predictive log loss, calibration and decision cost on labeled data at the lengths and costs relevant to their task (Section 7). This does not estimate departure from an unknown Bayesian reference. It does show whether broader training or calibration helps where the model will be used. The matched comparison in Appendix U (Table 33) shows why to check both short and long contexts. With population scaling and no calibration, training on variable lengths lowers mean decision cost from 0.20379 to 0.19946 at twelve but raises it from 0.22087 to 0.22125 at eight.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Summary of revisions and new results

Second revision update: We have revised the paper a second time to explain why each experiment is needed, what its results establish, and what question remains for the next experiment.

If any part of the revised manuscript is still difficult to follow, we would greatly appreciate it if you could point us to the specific concept, subsection, or passage. Knowing whether the difficulty is with a definition, the motivation for an experiment, the connection between analyses, or the interpretation of a result would help us address it directly. We would like to address any remaining clarity issues, but we are not sure which passages in the revised manuscript may still be difficult to follow. If you have time, could you point us to one or two specific examples? If a particular passage is still hard to follow, a short quote of it would help us fix it directly.

Presentation and clarity. The Introduction now distinguishes two things that can happen at once. A PFN can predict better with more labels while gaining less from those labels than exact Bayesian model averaging (BMA). Section 3 defines this departure as a difference in the probabilities assigned to the same query after seeing the same labels. It also defines context length and explains why we keep the queries fixed as we reveal more labels. Section 3.1 explains why two task families are enough to test how the PFN weighs competing families, why we use additive rules and shallow trees, and how their enumerable rules let us compute exact BMA. Section 3.2 explains what each candidate comparison tests, including whether averaging over both families helps, whether their weights need to respond to the labels, and whether changing the final probabilities is enough to match the PFN. Section 3.3 distinguishes excess log loss relative to BMA from how closely a candidate matches the PFN and explains how we fit and evaluate those candidates. Figure 1 ties the setup together.

Those definitions give the results the following sequence: Section 4.1 and Figure 2 show how predictive loss can fall while the departure from BMA grows. That result motivates the control in Section 4.2 and Figure 3, which separates the lengths seen during training from feature scaling. Comparing both shows what an evaluation at the longest length would otherwise miss. Training on a range of lengths improves agreement with BMA at longer contexts but worsens it at eight. Section 4.3 tests whether the same tradeoff occurs in regression.

After Section 4 establishes where the departure grows, Section 5 asks what changes to BMA reproduce the PFN’s probabilities. It explains why we test giving the labels less weight, whether that description transfers across context lengths, and why a close fit does not identify a network mechanism. Appendix S now reports the mean exponents underlying the comparison in Section 5.3. Section 6 then asks whether the probability differences affect a decision. Even if the most likely class stays the same, calibration can change whether the classifier predicts or abstains. We fit calibration on observed labels and evaluate the cost of the resulting decisions. The Discussion brings these results back to how one would evaluate a training schedule or calibration procedure across context lengths.

A PFN can predict better as it sees more examples yet fall farther behind Bayes, because the Bayesian predictor gains more from the same observations, and the revision studies how that pattern can change. When we train on a range of context lengths with the same total exposure to context and query labels, the rise in excess log loss from eight to twelve examples becomes smaller but persists even with fixed feature scaling. Training on a range of lengths improves agreement with Bayes at longer contexts but worsens it at eight, a tradeoff we also find in a new Gaussian process regression experiment (Section 4, Figure 3 and Appendices Q and R).

The revision also asks whether the difference matters for decisions. In our abstention experiment, calibration using observed labels removes about one third of mean regret relative to the Bayes decision at twelve examples, averaged over nine abstention costs. It does not show a clear gain at eight (Section 6 and Appendix U). Section 3 now defines the benchmark before introducing the candidate predictors, and Section 5 separates what their fits explain from what they cannot establish about the network. The individual replies give the relevant comparisons and limits for each review.

First revision update: We substantially revised the manuscript to make PriorFuse’s contribution easier to follow. The introduction now explains what comparing a PFN with exact Bayes on the same tasks reveals that predictive loss alone can miss. The results sections explain why each experiment is needed, what the figures and tables establish, and how those findings inform choices about training and calibration.

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Additional check with a released TabPFN checkpoint

To complement the comparisons with larger models trained on known priors, we ran the released TabPFN 3.5 checkpoint on a small sample of the same benchmark tasks with one estimator and no weight updates. In 47 paired Boolean tasks, expected log loss fell from 0.7203 to 0.6758 as the context grew from eight to twelve examples. Excess loss relative to the exact predictor for those tasks rose by 0.0064 nats, but the paired 95% interval of [−0.0374, 0.0473] includes changes in either direction. One of the 48 sampled tasks contained only one observed class at eight examples and was excluded at both lengths.

In 24 paired Gaussian process tasks, expected squared error fell from 0.7276 to 0.4796 between eight and 32 examples. The change in excess squared error was again uncertain, at 0.0309 with a paired 95% interval of [−0.0517, 0.1066]. This comparison evaluates the predictive mean, not the full distribution. Both intervals resample tasks for one released checkpoint. The exact predictor is optimal for the benchmark tasks, not for the checkpoint's training prior, so neither comparison isolates Bayesian approximation error or tests the inverse-length adjustment.

The larger classifiers and the regression experiment were intended to extend the controlled comparisons under known priors. Although the released TabPFN 3.5 check leaves open whether the same pattern occurs in released models, the main contribution of PriorFuse is to make that pattern measurable under a known, enumerable prior, where exact BMA tells us how much both predictors could gain from the same additional labels. In Sections 4.2 and 4.3, training on a range of context lengths brings PFNs closer to BMA at longer contexts while moving them farther away at the original training length. We observe this tradeoff in both Boolean classification and Gaussian process regression, with label exposure matched and feature scaling fixed. An evaluation at a single context length would miss that tradeoff and could lead to a different choice of training schedule.

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