Thompson sampling is a widely used strategy for contextual bandits: at each round, it samples a reward function from a Bayesian posterior and acts greedily under that sample. Prior-data fitted networks (PFNs), such as TabPFN v2+ and TabICL v2, are attractive candidates for this purpose because they approximate Bayesian posterior predictive distributions in a single forward pass. However, PFNs predict noisy future rewards, while Thompson sampling requires uncertainty over the latent mean reward function. We propose PFN-TS, a Thompson sampling algorithm that converts PFN posterior predictives into mean-reward samples using a subsampled predictive central limit theorem. The method estimates posterior variance from a geometric grid of O(logn) dataset prefixes rather than the full O(n) predictive sequence used in previous predictive-sequence approaches, and reuses TabICL's cached representations across rounds. We prove consistency of the subsampled variance estimator and, for bounded rewards, bound Bayesian regret by an information-gain term and accumulated sampler error on encountered histories, with an extension to continuous rewards under additional assumptions. Empirically, PFN-TS achieves the best average rank across nonlinear synthetic and OpenML classification-to-bandit benchmarks, remains competitive on linear and BART-generated rewards, and attains the highest estimated policy value in an offline mobile-health evaluation.
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.Reviewer_MkhSOpenReview ↗
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3
Confidence
2
Informativeness
1
Presentation
1
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Paper summary
This paper attempts to reconcile the two worlds of bandit-based continual learning and foundation models by analyzing the nature of prior-fitted networks (PFN) and applying it into a performant bandit algorithm. The analysis on the output of PFNs acknowledges that PFN does not produce the perfect distributions for reward-based problems, and hence introduces a correction to the sampling of predictive distribution. In addition, the authors introduced SubCLT which uses a geometric sequence of training prefixes to run the prefix evaluations at a lower computational complexity. Upon combining both aforementioned components, PFN-TS achieves the best rank performance in terms of cumulative regret on eight OpenML datasets and eight synthetic datasets.
Critical strengths
The motivation is strong as utilizing priors in foundation models for bandit tasks makes sense
A valuable problem to be solved
SubCLT can be genuinely useful, even for applications beyond the scope of this paper
A major applied, technical contribution that accompanies the main results
The approximation is clearly distinguished from the established theory of PPD of PFNs
The theoretical contribution is explicit about the approximations and provide proofs for it
Critical weaknesses
Runtime seems to the primary drawback in practice, especially above 5000 steps
Minor weakness but a significant consideration against real-world use cases
Relatively difficult paper to understand, especially Section 2
Could not probably validate the soundness of the theoretical contributions
Questions for authors
Can you explain the implications of having Epsilon_T in Theorem 2? Does it truly imply sublinear regret in a conventional sense?
Given SubCLT is an asymptotic approximation, how significant are the deviation in uncertainty estimates in the early stages?
Have you tried using TabPFN instead of TabICL v2? Is there a specific reason to prefer TabICL?
Thank you acknowledging the strong motivation and usefulness of our method and for your thoughtful questions. We have revised our manuscript in response to your questions and address them directly below.
Q1. Does Theorem 2 imply sublinear regret? The accumulated error is ET=∑t=1TEQ[ηt], where ηt compares PFN-TS’s action distribution with exact TS at the history PFN-TS actually encountered. For fixed K, the bound yields sublinear regret if ITQ=o(T) and ET=o(T). We are not able to prove either bound because (1) The TabICL prior is defined algorithmically and has not been explicitly written down, making it impossible for us to assess its information gain, (2) It is unclear how much the implemented TabICL’s approximate posterior deviates from the idealized value.
Q2. Early uncertainty error. Figure 3 shows that when applying the martingale posterior construction with TabICL, nominal 95% intervals at n=16 cover about 73% of latent means with SubCLT and 94% with FullCLT. We have now conducted additional experiments with Bayesian linear regression and show the comparison in Figure 9. Both methods undercover at small sample sizes. Coverage improves with more data, although at n=1,024 SubCLT still covers 86%, compared with about 95% for both FullCLT and the exact posterior.
In a further additional experiment, we evaluated the intervals on histories collected by exact Thompson sampling for a Bayesian linear model. SubCLT coverage rose from 61% at 10 pulls per arm to 80% at 320 pulls. The difference in arm-selection probabilities between SubCLT and exact TS, measured by total variation, fell from 0.119 just after warm-up to 0.034 at round 1,000. Thus the differences in action probabilities were much more modest than the undercoverage suggests.
One possible explanation for persistent undercoverage is that the prior keeps early predictions close together even while substantial uncertainty remains. SubCLT estimates uncertainty from how much those predictions move, so small early movements can lead to intervals that are too narrow. We plan to investigate finite-sample corrections in further revisions of our work.
Q3. Why TabICLv2? When developing PFN-TS, we compared using TabICLv2 vs TabPFNv2.5 (this was before v3’s release) and found TabICLv2 to be drastically faster. We believe this is due to key-value caching. PFN-TS repeatedly queries the same fixed training prefixes as new contexts arrive. TabICLv2’s key–value caching lets us reuse the attention state for each prefix, while TabPFNv2.5 by default does not use any caching. Although it does in principle support caching, it seems that the 2D attention architecture it uses creates a memory bottleneck.
Thank you again for taking the time to review our paper. We have uploaded a revised manuscript and posted our response to your comments.
Before the discussion period closes, we would greatly appreciate it if you could let us know whether our revisions and responses have adequately addressed your concerns. We would be happy to provide further clarification on any remaining points.
The paper introduces a novel and interesting method for contextual multi-armed bandits, based on Prior-Data Fitted Neural Networks (PFN) and the Thompson Sampling (TS) selection mechanism. As a means to achieve this, a computationally feasible way to obtain the uncertainty of the predicted posterior is proposed. The resulting algorithm, referred to as PFN-TS, is theoretically motivated through a Bayesian regret bound and experimentally validated using the specific openly available PFN TabICL v2.
Critical strengths
The main strength of the paper is the creative use of Prior-Data Fitted Networks, which have demonstrated impressive performance for supervised learning tasks on tabular data recently, for online learning in a contextual bandit context. The idea is novel and supported by a theoretical regret analysis, which is missing for many of the competing algorithms. The experiments are extensive enough to demonstrate the effectiveness of the proposed method, provided that the results and relative performance hold under my requested tightening of the baseline comparisons (see my comments under Critical Weaknesses).
Furthermore, the code for reproducing the results has been made public, which provides additional transparency and strength.
Critical weaknesses
The main weakness of the paper is a non-rigorous and unfair comparison to previous works in many of the experiments. In particular, for many of the experiments were the paper claims superiority in terms of regret minimization, the authors run competitive methods without extensive hyperparameter tuning. This work includes many datasets absent from the experiments of prior works, and so no optimized hyperparameters are available for plug and play. The specific configurations can have a significant impact on the performance for neural network and tree ensemble based methods, such as learning rate, regularization factors, size of networks/ensembles/trees, etc. Still, the paper (Appendix C.2) only reports using "default" parameters for NeuralTS, BFTS, RFTS and XGBoostTS without any tuning for the specific datasets. The authors claim that a strength of PFN-TS is its ability to perform well without hyperparameter tuning, and state that:
"... Compounding these model-specific weaknesses, all these approaches require hyperparameter choices, such as kernel bandwidth, network architecture or tree depth, that are difficult to tune online."
This is a fair argument, but it is misleading to then report the relative performance of PFN-TS in terms of regret minimization against baselines without any hyperparameter tuning.
A second minor weakness of the paper is that the authors do not consider the UCB-based counterparts to NeuralTS (NeuralUCB), RFTS (RFUCB) and XGBoostTS (XGBoostUCB), which often perform better in practice. Since the authors do consider both LinearTS and LinearUCB, it would provide great value to see the performance of more complex UCB-based also.
Questions for authors
Q1: How was hyperparameter selection done for the baseline model and dataset combinations where no previously reported optimized hyperparameter exist?
Q2: What are the reasons for omitting NeuralUCB, RFUCB and XGBoostUCB from the experimental comparisons?
Thank you for highlighting our creative and novel use of PFNs, theoretical analysis, extensive experiments, and transparency. Thank you also for the thoughtful questions regarding our evaluation protocol. We have revised our manuscript in response to your questions and address them directly below.
Q1. How were baseline hyperparameters selected? We intended to follow the benchmark protocol of Deng et al. (the BFTS study). BFTS used its published configuration, which the original study tested in a sensitivity analysis on four OpenML datasets. LinUCB used the implementation default α=1 without per-dataset tuning. For RFTS and XGBoostTS, we fixed ν=1 following Nilsson et al. and used their code’s default initialization threshold of 10 on all datasets, which gives nine random pulls. Nilsson et al.’s Shuttle script instead uses a threshold of 70, which we did not adopt. Appendix C.2 lists the settings used in our experiments.
For LinTS and NeuralTS, the BFTS study selected hyperparameters per scenario on separate pilot runs. Our submitted appendix described that protocol, but a code review revealed that our original runs used the implementation defaults rather than the tuned hyperparameters. We corrected the revised runs to use the BFTS-selected values, transferring the settings from the original versions for the five modified Friedman tasks.
Separately, in response to 43Bm’s concern about early exploration, we added a warm-up comprising five shuffled round-robin pulls per arm to LinTS and LinUCB. Appendix F.5. compares this version of both algorithms vs. the original with no warm-up and shows that the warm-up generally improves performance.
We have now repeated all the experiments in our paper with these corrections, which indeed narrows some of the gaps. Nonetheless, the average rank of PFN-TS does not change. It remains the best across the eight synthetic scenarios (1.25) as well as the eight OpenML scenarios (1.625).
Q2. Omitting nonlinear UCB counterparts. We agree that NeuralUCB, RFUCB, and XGBoostUCB would broaden the comparison across exploration rules. However, the central experimental question is how different reward models support Thompson sampling. We prefer to focus on the Thompson sampling paradigm because it offers certain advantages that may not be reflected in regret alone. For example, it enforces randomization with known probabilities and adequate overlap which allows for principled inference over reward functions or parameters. This is especially important in mobile-health in which the bandit deployment doubles as a randomized trial.
Thank you again for taking the time to review our paper. We have uploaded a revised manuscript and posted our response to your comments.
Before the discussion period closes, we would greatly appreciate it if you could let us know whether our revisions and responses have adequately addressed your concerns. We would be happy to provide further clarification on any remaining points.
The authors use tabular foundation models (TabICLv2) as the reward model for Thompson sampling in contextual bandits. Since these networks are trained as in-context learners, and predict noisy rewards, the authors propose to estimate mean-reward uncertainty with "SubCLT". SubCLT is an estimator based on the epistemic uncertainty estimator of Fortini, that is computationally more efficient since it uses O(logn) points. Based on this estiamtor, they propose PFN-TS, a Thompson sampling based method for contextual bandits. PFN-TS ranks best on average over eight synthetic and eight OpenML tasks.
Critical strengths
The paper makes a tabular foundation model usable for Thompson sampling at O(logn) rather than O(n) evaluations.
The method correctly addresses on of the problems of using tabular models (PFNs) in bandits. PFNs predict noisy rewards, while TS requires the epistemic uncertainty. Numerical results show that sampling the predictive directly is much worse on seven of the eight synthetic tasks .
The estimator is simple, and based on prior work. The proof seems correct, and the novelty lies in reducing the number of evaluations from O(n) to O(logn) evaluations.
The OpenML results against tree-based Thompson sampling are strong. PFN-TS beats BFTS and XGBoostTS on six of the eight datasets.
Critical weaknesses
The regret theorem (thm 2) holds for every policy and is not specific to PFN-TS. The proof decomposition appears also in the proof of thm 2 of Zhang et al. (NeurIPS 2025, App. A.4.5), whom the paper cites only for their algorithm. Furthermore, the error term in the regret theorem is problematic. The paper's route to bounding this error term gives (prop 4) seems to be linear in time.
To see this, note that in prop 4 each ηt is bounded by ρt plus a non-negative KL term. So the paper's bound of the error term is atleast ∑tE[ρt], where ρt is the total-variation distance between exact posterior sampling on the full history and a gaussian centred at the considered predictive mean. However, since the estimate is updated only when an arm's count doubles, so just before every update it ignores nearly half of that arm's data, which I suspect leads to a linear bound.
To observe this, take a favourable case: one arm pulled every round, Gaussian rewards with known variance σ2 and a flat prior, an exact predictive, and the exact snapshot variance (I use the exact variance for simplicity, what really matters is the gap in the mean values).
Then ρn=TV(N(mn,vn),N(ms,vs)) where s=2⌊log2n⌋. The total variation doesn't change if we subtract mn and divide by vn, hence
ρn=TV(N(0,1)N(μn,vs/vn)),μn=vnms−mn.
Let u=n/s. With a flat prior, the variance vn=σ2/n, thus vs/vn=u. We can also rewrite μn in another way: note that given the first s point the difference ms−mn is Gaussian with mean 0 and varaince vs−vn. Hence μn∼N(0,(vs−vn)/vn), that is μn=u−1Z,Z∼N(0,1).
Therefore E[ρn]=EZ[TV(N(0,1),N(u−1Z,u)]. Using the event E={x≤0}, we lower bound the TV as follows
EZ[TV]≥EZ[∣1/2−Φ(Z1−1/u)∣]≥1−1/u/4≥u−1/8.
Writing n=2k+j, and s=2k, we have u=1+j/2k with j=0,..,2k−1. Hence , for T=2K+1 we have
One can see that the last sum is linear in T, since ∑k=1K2k=T−2.
The uncertainty estimate seems overconfident at the small sample sizes where Thompson sampling explores. Fig. 3 compares SubCLT with the FullCLT estimator of Eq. 7 on the same TabICL predictions, so the gap between them comes from the subsampled estimator itself. On Linear at n=16, SubCLT covers ~73% of true means against ~94% for FullCLT, and it stays below teh target line at every sample size in both panels. Line 375 calls this ''slightly undercovers'', while lines 472–474 concede poor calibration "when arm histories are short or weakly informative". Fig. 3 is also easier than the bandit: it uses i.i.d. data rather than bandit-collected histories.
In the released code, five of the eight synthetic tasks use App. C.3's "shared" arm 2, μ2=μ1+5sin(πx1x2)≥0 (lines 1067–1070), so arm 2 is best at every context. App. C.3 names this variant only for Friedman-Heteroscedastic (lines 1072–1073). These 5 are where PFN-TS wins the most. Where the best arm does vary, PFN-TS beats BFTS by a modest margin on Friedman-Sparse-Disjoint, ties it on SynBART and trails both linear methods on Linear.
On some of these tasks the linear baselines barely explore, because of how they are configured. I suspect LinUCB essentially never tries arm 2, since the code gives the linear agents no warm-up and unscaled rewards, so after their first pulls they rarely try the other arm. Running the released LinUCB on Friedman, it never pulls arm 2 in 12 of 12 runs. Separately, the code runs NeuralTS with ν=10−5 everywhere, outside the grid that App. C.2 says was tuned (lines 1040–1043).
The ablations do not show that the estimator's exploration, or the adaptive encoding, is what lowers regret. Acting greedily on the predictive mean beats PFN-TS on three of the eight synthetic tasks, including two of the three that, as released, have a context-dependent best arm, for example about 360 against 570 at T=2000 on Friedman-Sparse-Disjoint (Fig. 13). PFN-TS wins the other five, mostly tasks with one globally best arm.
Questions for authors
With an exact posterior predictive, for example Bayesian linear regression, how well do SubCLT intervals cover the true mean at small n, between grid points and on bandit-collected histories?
Thank you for the careful reading of our paper and for appreciating the simplicity and effectiveness of our proposed method. Your comments have helped us to strengthen our empirical evaluation and improve the quality of our paper. We first respond to your question and then address comments about our paper’s weaknesses.
Q1. With an exact posterior predictive, for example Bayesian linear regression, how well do SubCLT intervals cover the true mean at small n, between grid points and on bandit-collected histories?
We conducted an additional experiment with a three-arm Bayesian linear bandit (Appendix E.2). On histories collected by exact Thompson sampling, the nominal 95% SubCLT intervals covered 61% of true means at 10 pulls per arm and 61% at 19 pulls, just before the next refresh. Later, coverage was 77% at 319 pulls and 80% after the refresh at 320 pulls. The analytic posterior intervals based on the same snapshots stayed near 95% both at and between refreshes.
Figure 9 shows a complementary experiment with i.i.d. data and no staleness. Using the same exact predictive means, SubCLT, FullCLT, and the analytic posterior covered 63%, 76%, and 95% of true means at n=16, respectively. By n=1,024, SubCLT reached 86%, while FullCLT and the analytic posterior were both near 95%. We agree that “slightly undercovers” understated the gap and have revised the manuscript wording.
Nonetheless, the differences in action probabilities were much more modest than the undercoverage suggests. The mean total variation distance between SubCLT and full-history exact TS fell from 0.119 just after warm-up to 0.034 at round 1,000.
One possible explanation for the undercoverage is that prior shrinkage keeps early predictive means close together even when substantial uncertainty remains. SubCLT estimates uncertainty from changes in those means, so small early changes can lead to intervals that are too narrow. We plan to investigate finite-sample adjustments in future work.
Theorem 2 and the doubling schedule. Thank you for bringing to our attention that Zhang et al. (NeurIPS 2025, Appendix A.4.5) use the same core argument. We now cite this precedent alongside Theorem 2.
We agree with the limitation illustrated by your Gaussian example. With doubling refreshes, even exact posteriors based on the snapshot and the full history can stay separated in total variation over a positive fraction of rounds. As a result, summing the posterior-TV upper bound in Proposition 4 can give a linear-in-T term. However, this does not imply that the accumulated action TV ET is linear. Similar to the experiment described earlier, the action-TV could be a lot smaller than the posterior approximation error.
Synthetic tasks and baseline configurations. Thank you for pointing out that arm 2 was optimal almost surely in five of the submitted Friedman tasks. This was unintentional and was inherited from Deng et al. (BFTS paper)’s configuration, which we followed. We have reran all methods on these tasks with a signed reward gap, 5sin(π(2x1−1)x2). Each arm is now optimal on half the contexts, and the distribution of the absolute gap is unchanged.
To ensure that LinTS and LinUCB explore adequately, we have followed your suggestion and re-implemented them to start with a warm-up of five round-robin pulls per arm. In addition, upon a code review, we have also found that LinTS and NeuralTS both used the implementation defaults instead of the scenario-specific pilot settings from the BFTS study. We reran both with the BFTS-selected values and updated Appendix C.2 to describe all settings used.
We have now repeated all the experiments in our paper with these corrections, which indeed narrows some of the gaps. Nonetheless, the average rank of PFN-TS does not change. It remains the best across the eight synthetic scenarios (1.25) as well as the eight OpenML scenarios (1.625).
Decision rule ablations. We now compare SubCLT TS, greedy, and direct predictive sampling under the same encoding, separately for joint and disjoint encoding (Figure 15 and Figure 14 respectively). Neither TS nor greedy uniformly dominate the other. However, the performance of greedy is much more variable, and it sometimes seemingly incurs linear regret.
We sincerely thank you for your time and careful consideration of our work. We also appreciate the reviewers’ thoughtful and constructive feedback. For your convenience, we summarize the strengths highlighted by the reviewers and our rebuttal and revisions below.
Strengths recognized by the reviewers
Well-motivated application of tabular foundation models to contextual bandits. The reviewers recognized the value of making PFNs usable for Thompson sampling by extracting uncertainty about latent mean rewards, rather than directly sampling noisy predictive rewards. Reviewer fB1R described this application as creative and novel, and Reviewer MkhS highlighted its strong motivation.
Simple and computationally efficient uncertainty estimation. Reviewer 43Bm highlighted SubCLT’s reduction from O(n) to O(logn) prefix evaluations. Reviewer MkhS identified SubCLT as a valuable technical contribution with potential applications beyond bandits.
Strong empirical performance and transparent evaluation. Reviewer 43Bm highlighted the OpenML results against tree-based Thompson sampling methods. Reviewer fB1R recognized the breadth of the experiments and the publicly available reproduction code, while requesting tighter baseline comparisons.
Responses to the reviewers’ concerns
Reviewer fB1R. We corrected LinTS and NeuralTS to use the scenario-specific hyperparameter settings selected in the BFTS study. We also added five shuffled round-robin warm-up pulls per arm to LinTS and LinUCB, with a separate warm-up ablation in Appendix F.5. The updated comparisons narrow some performance gaps, but PFN-TS retains the best average rank across the eight synthetic scenarios (1.25) and eight OpenML datasets (1.625). We explained our focus on comparing reward models within Thompson sampling.
Reviewer MkhS. We clarified that Theorem 2 does not establish a PFN-TS-specific sublinear regret rate without further control of information complexity and accumulated sampler error. We added exact-predictive Bayesian linear calibration experiments, both with i.i.d. observations and on histories collected by exact Thompson sampling (Appendix E.1–E.2). These show that undercoverage persists at finite sample sizes, and we strengthened the manuscript’s wording accordingly. We also explained our choice of TabICLv2 for cached inference and documented runtime comparisons, retaining longer-horizon runtime growth as a practical limitation.
Reviewer 43Bm. We corrected five Friedman scenarios so that the optimal arm varies with context while preserving the absolute reward-gap distribution, and updated the benchmark comparisons. We added matched-encoding decision-rule ablations under both disjoint and joint encoding (Figures 14–15), which support latent-mean sampling over noisy predictive sampling while showing that greedy selection remains competitive on some tasks. We also added the citation to Zhang et al.’s related regret argument and explicitly acknowledged that the posterior-TV bound in Proposition 4 can accumulate linearly under doubling refreshes.
As of this writing, Reviewer 43Bm has explicitly acknowledged that the revised Friedman tasks and corrected baseline settings address their concern, and appreciated the additional calibration evidence, corrected wording, and Zhang et al. citation. Their remaining concern is the strength of the theoretical support. They requested accumulated action-TV measurements on PFN-TS’s own histories and an ablation increasing SubCLT sampling variance.
In response, we obtained preliminary results from TabICL-based PFN-TS on the Linear benchmark over 4,096 rounds in each of four runs. At every post-warm-up round, we compared PFN-TS’s action probabilities with exact full-history Bayesian LinearTS probabilities using the context and history encountered by PFN-TS. The running mean action TV, averaged across runs, decreased from 0.104 at T=1,024 to 0.080 at T=2,048 and 0.064 at T=4,096. This provides finite-horizon evidence that average action discrepancy decreases along PFN-TS’s own trajectories in this setting.
Regarding variance inflation, Figure 13 provides a related targeted ablation on Shuttle. With TabICL, joint encoding, and covariance shrinkage held fixed, adding a decaying variance floor reduced mean cumulative regret at T=2,000 from approximately 101 to 69 across five runs. This shows that selectively increasing small sampling variances can improve decisions. It does not replace the broader variance-scaling experiment suggested by the reviewer.
We believe the revisions substantially strengthen the empirical evaluation and clarify the scope of the theory. We hope the paper can be assessed on its combined methodological and practical contribution, while recognizing finite-sample calibration and end-to-end regret guarantees for the implemented sampler as open problems.
Best regards,
The Authors
From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.
Thank you acknowledging the strong motivation and usefulness of our method and for your thoughtful questions. We have revised our manuscript in response to your questions and address them directly below.
Q1. Does Theorem 2 imply sublinear regret? The accumulated error is ET=∑t=1TEQ[ηt], where ηt compares PFN-TS’s action distribution with exact TS at the history PFN-TS actually encountered. For fixed K, the bound yields sublinear regret if ITQ=o(T) and ET=o(T). We are not able to prove either bound because (1) The TabICL prior is defined algorithmically and has not been explicitly written down, making it impossible for us to assess its information gain, (2) It is unclear how much the implemented TabICL’s approximate posterior deviates from the idealized value.
Q2. Early uncertainty error. Figure 3 shows that when applying the martingale posterior construction with TabICL, nominal 95% intervals at n=16 cover about 73% of latent means with SubCLT and 94% with FullCLT. We have now conducted additional experiments with Bayesian linear regression and show the comparison in Figure 9. Both methods undercover at small sample sizes. Coverage improves with more data, although at n=1,024 SubCLT still covers 86%, compared with about 95% for both FullCLT and the exact posterior.
In a further additional experiment, we evaluated the intervals on histories collected by exact Thompson sampling for a Bayesian linear model. SubCLT coverage rose from 61% at 10 pulls per arm to 80% at 320 pulls. The difference in arm-selection probabilities between SubCLT and exact TS, measured by total variation, fell from 0.119 just after warm-up to 0.034 at round 1,000. Thus the differences in action probabilities were much more modest than the undercoverage suggests.
One possible explanation for persistent undercoverage is that the prior keeps early predictions close together even while substantial uncertainty remains. SubCLT estimates uncertainty from how much those predictions move, so small early movements can lead to intervals that are too narrow. We plan to investigate finite-sample corrections in further revisions of our work.
Q3. Why TabICLv2? When developing PFN-TS, we compared using TabICLv2 vs TabPFNv2.5 (this was before v3’s release) and found TabICLv2 to be drastically faster. We believe this is due to key-value caching. PFN-TS repeatedly queries the same fixed training prefixes as new contexts arrive. TabICLv2’s key–value caching lets us reuse the attention state for each prefix, while TabPFNv2.5 by default does not use any caching. Although it does in principle support caching, it seems that the 2D attention architecture it uses creates a memory bottleneck.