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Paper summary
This paper studies what happens when you train a transformer to perform Bayesian posterior prediction iteratively. It is given as an input a summary of the prior over the parameters of the data generating function (for example mean and variance) and a bunch of observed data points corresponding to such distribution, and it outputs a posterior over these parameters. Since it is know that exact Bayesian updating (this is feeding the posterior at time as the prior for time ) gives the same answer independently of wether the data arrives all at once or in different batches, this paper asks whether the trained transformer inherits this property, which a priori is not guaranteed.
To this end, the paper fixes each dataset and varies the number of batches it is spliced across. Then they measure two things: how the the step-by-step answer differs form (1) the one-call answer and (2) the true correct Bayesian posterior (which can be computed in close form in the settings used).
The main conclusion is that the posterior produced by the transformer should always be checked at each iteration before using it as a prior in the subsequent calls.
Critical strengths
- The experimental design is clean and well thought. Using tasks that have exact posteriors and splitting the data in different ways lets the paper separate correctness from consistency.
- The pair seems transparent and reproducible. Limitations and failed checks are reported openly, and the code is provided.
Critical weaknesses
This paper should be rejected because the main result, although useful, is widely known already as “distribution shift” and highly expected. The network is trained in priors coming always from a fixed sampler, but then, during reuse, it receives its own outputs, which the sampler never produces, so we can not expect it to preform good there. In fact, the paper already shows this: (1) when intermediate priors stay within the training regime, the chained error is more or less the same as the one call error. (2) Larger errors just occur when the prior leaves the training regime. The main contribution then is a negative result that is expected and known.
Some fixes are then attempted. The most relevant ones are: (1) training on intermediate priors (which is a standard method for these problems) and (2) creating a network that outputs a factor per observation and then gives posterior ∝ prior × factor(obs 1) × factor(obs 2) × … × factor(obs n) which is then normalized to one, guaranteeing agreement by design independently of how the data is split (since multiplication is associative); However, this design is already established in the literature: in particular, this method is how neural likelihood methods combine independent observations in neural processes (Volpp et al., ICLR 2021, not cited).
Questions for authors
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Which existing systems reuse their outputs as priors in practice? Could you show the problem on at least one of them, on its own task? In which realistic settings does chaining a network's outputs beat simply rerunning it on all the data?
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Is there a failure specific to the chining mechanism, beyond the network receiving priors it was not trained on?
4 comments
Response to reviewer RYXC (2/3)
R3. Training on intermediate priors and multiplying local factors are established
We now cite Volpp et al. (ICLR 2021) for incremental Gaussian evidence aggregation, and scheduled sampling and training on induced states as precedents for exposure to model outputs. Fixed positive observation-local factors are a structural control: when the same factors are reused and no lossy projection intervenes, normalization cancels and the result is partition-invariant. We do not claim novelty for that construction.
Agreement does not imply accurate likelihood factors. The learned Gaussian factors agree across splits but fit the continuous logistic reference less accurately than a Gaussian given the reference moments. The same-backbone comparison also missed its planned one-call matching criterion overall (only one of six pairs qualified), so it does not isolate an accuracy gain from additivity. Its attention/additive 16-call error ratios are 1.90 for linear regression and 3.34 for grid logistic inference. The much larger endpoint ratios, 474 and 23.1, compare different architectures and one-call accuracies; Appendix G puts these contrasts together rather than treating them as the same effect.
Revised manuscript: §§4–6; Proposition 2 and Appendix B.3; Appendices G–H and K (Table 16).
R4. Which systems recurse in practice, and does the result transfer to their native task?
Distribution Transformers use an approximate filtered state to form the next predictive prior, and their published depth comparison already measures error accumulation against a particle filter. Streaming Variational Bayes and online Laplace also carry approximate state. We added a test of model-prior exposure on the released Distribution Transformers sensor simulator, preserving its Gaussian-mixture state, dynamics, and latent-state training score. It is an adaptation: the released configuration differs from the published setup, and its particle likelihood does not match the observation sampler. The primary held-out score is NLL at the known simulated latent state, which does not require a particle reference. A particle-reference convergence gate did not pass, so there is no reference-projected training arm or native exact-posterior or partition comparison.
One 130-epoch baseline supplies the weights for nine continuation runs: three seeds each for fresh and model-prior exposure (200 updates), and longer fresh continuation (300 updates). All restart the optimizer with the same schedule design. On 100 held-out trajectories, the model-prior minus equal-example fresh dense NLL is −0.0143 (conditional 95% interval [−0.0303, 0.0010]). Relative to longer fresh it is +0.0212 ([0.0087, 0.0336]), with longer fresh better in all three pairs. Longer fresh is not exactly time-matched. The untouched baseline (−0.1544) beats every continuation. The intervals reflect trajectory variation conditional on one trained baseline and these seeds, not variation over independently trained baselines. The adaptation does not show convincing benefit under the tested recipe, and it does not identify why restarting from that baseline hurts.
Revised manuscript: §§4, 6–7; Appendices M, Q, and R.4 (Table 23).
R5. When does chaining beat rerunning the inference on all past data?
We have not shown a workload in which the learned updater beats rerunning on the full history at the same output schedule. In the separate online Laplace pilot, state carryover lowers retained solver state and cumulative fitting time when a fit is required at every arrival, with worse prediction. At 16 arrivals, it retains 7,936 bytes of Gaussian state. History refitting also stores 114,688 bytes of standardized design and labels. Median cumulative fitting time is 1.56 ms online versus 2.79 ms for history refits. If only the final answer is required, one pooled fit takes about 0.50 ms. The measurements exclude offline scaling and per-arrival prediction and are not end-to-end latency or total memory. The held-out accuracy loss also falls below the prespecified 0.01-nat threshold on every primary split.
The native filtering experiment has no matched history-rerun comparator. Scoring every fourth or sixteenth step merely subsamples dense outputs. Reported times (189.7 s fresh, 222.5 s model-prior, 282.9 s longer fresh) are for training plus prior generation, not deployment inference.
Revised manuscript: §7; Appendix Q, Table 19; Appendix R.4, Table 23.
(Continued)
Response to reviewer RYXC (3/3)
R6. Is there a special chaining failure apart from receiving unfamiliar priors?
We find a violation of the partition identity, but do not identify a distinct mechanism beyond approximation and shift. Same-input replay shows that the learned update rules differ when given the same prior and block, and the logistic reversal survives using another seed to generate the model-arm path. The prior source still changes across paths. The scalar independent-residual control produces substantial recursive error without retaining the learned updater's error dependencies. Replacing just the last logistic call with exact Bayes leaves most error but does not locate its cause.
When we hold the supplied prior and lead history fixed and vary the next block, the logistic ranking reverses between exact and other-seed model one-step priors at all four tested block sizes. Neither source matches the fresh component of the training law. Holding block length fixed throughout a separate rollout removes shrinking blocks from that comparison, but the total observations and carried priors change with horizon. These controls address particular confounds without decomposing endpoint error into causal shares.
Revised manuscript: §§2–4 and 7, Figure 2; Appendices E, P, R.1, and R.3.
R7. Is the recommendation to check every posterior before using it as a prior?
No. We recommend testing the intended update schedule on held-out tasks before deployment, including the model-generated priors the estimator will actually receive. Report partition disagreement separately from reference error where a reference is available, and recheck short-input accuracy if the training prior law changes. We do not assume that an exact posterior is available at deployment or offer an update-by-update certificate. Agreement across splits alone cannot certify correctness.
Revised manuscript: §§2 and 7, Box 2.
Closing
The revised contribution is an evaluation result within distribution shift: in the logistic study, exact-prior and model-prior evaluations favor different updaters. For the community, this motivates testing the prior distributions induced by the intended update schedule, alongside one-shot accuracy. The paper supplies controlled evidence for that recommendation without claiming a universal training remedy.
Clarified Findings, Limited Contribution
Thank you for the clarifications and additional experiments. The logistic example shows that testing on exact intermediate posteriors can favor an updater that performs worse when used repeatedly. I still find the contribution limited because this refines a familiar recommendation to test models under the conditions in which they will be used. The same finding did not carry over to the Gaussian example, and the filtering experiment showed no clear improvement over the baseline. I therefore keep my original score.
Response to reviewer RYXC (1/3)
Thank you for recognizing the clean experimental design, the distinction between correctness and consistency, and the transparent reporting of limitations and failed checks. Your concern about distribution shift helped us sharpen the contribution: which evaluation priors identify an updater that performs well under recursive reuse?
R1. The effect is expected under distribution shift; what does the study add?
We agree that self-feeding shifts inputs and that training on model-induced inputs has precedent. Our observation is that even a one-step test on exact intermediate posteriors can favor the wrong updater for a particular recursive input law. On identical logistic prior/block pairs, the exact- and model-prior arms have local root-JS errors of 0.0401 and 0.1245 on exact paths, and 0.1156 and 0.0322 on model-arm paths generated by other training seeds. All eight updater-seed comparisons reverse. The original replay crossed three updaters with four paths: the exact reference and the three learned rollouts. The other-seed follow-up shows that the reversal is not limited to an updater's own outputs, but it does not establish a model-arm advantage on other learned path families. Crossed seed pairs share checkpoints and tasks, so they are not independent training replications.
Separately, in new fits matched on useful training time including prior generation, the model arm has lower 32-call self-rollout error than the exact arm at both 45 and 180 seconds. At 180 seconds the errors are 0.173 versus 0.441, despite worse one-call error (0.012 versus 0.011). This controls elapsed training time, not FLOPs or one-call accuracy. The local ranking reversal is a replay result, not a measurement on those new fits. Scalar Gaussian does not reproduce the local reversal and favors the exact arm on average in the matched-time runs. The native filtering adaptation does not beat its baseline. We therefore draw a conditional conclusion about which priors to use in evaluation, not a new explanation of distribution shift or a general remedy.
Revised manuscript: Abstract, §§1 and 4, Tables 3–4; Appendices P (Table 18), R.1 (Table 20), R.2 (Table 21), and R.4 (Table 23).
R2. Similar shallow accuracy in range suggests range departure may explain the loss
The shallow scalar results support your point about accuracy: the recursive-to-one-call reference-error ratios are 1.04, 1.25, and 0.94 on the retained two-block tasks. The learned answers still disagree across partitions. Selection uses the exact intermediate posterior's box membership, not the model output, and exact and learned membership agree in 479 of 480 cases. This supports the narrower statement that partition disagreement can occur without a hard range exit. It does not show a systematic in-range accuracy penalty. At 16 calls, all exact scalar trajectories in the original stress test leave the box before the last call.
The follow-up distinguishes a genuinely fresh prior/block law from mere overlap with the training range. Of 96 exact Gaussian one-step priors, 47 fall inside the fresh-prior box, but this subset does not match the fresh prior density or its joint law with the block. In grid logistic inference, many one-step priors have fitted Gaussian shape parameters inside the box, yet no continuation prior meets the numerical diagnostic for the fresh Gaussian-shaped family. At a fixed two observations per call, the logistic rollout gap versus a same-total single call remains, but the rolled-in states are still shifted. Widening the fresh scalar sampler in a separate fixed-budget experiment did not improve absolute error in those cells. None of these tests rules out range departure as a contributor to the deep scalar accuracy loss, or establishes what a distribution-matched deep test would find.
Revised manuscript: §§3–4, Figure 2a; Appendices D.6, F.2–F.3, and R.3 (Table 22 and support analysis).
(Continued)