acceptodds
Under review as a conference paper at ICLR 2027

When Amortized Posteriors Become Priors: One-Shot Accuracy Does Not Certify Recursive Reuse

Abstract

A Bayesian posterior summarizes what data reveal about an unknown quantity, and it becomes the prior when more data arrive. An amortized posterior estimator outputs such a posterior in one forward pass. In sequential use it must take its own previous output as the next prior, as a language model reads its own text. On small regression tasks whose posteriors can be computed, we fix each dataset and vary how many calls it is split across. Low single-call error coexists with large recursive error, the error after repeated reuse. Training on intermediate priors reduces absolute recursive error by 43% over 16 calls for converged scalar Gaussian estimators. In logistic regression, using the network's own predictions as training priors reduces it by 66% over 32 calls, against 10% for exact intermediate posteriors. Each gain costs some single-call accuracy, in logistic regression only for short inputs. We also prove that fixed positive per-observation factors make every split agree, yet such learned factors can compose exactly while remaining far less accurate than Gaussian approximations built from the true likelihood or the reference posterior. One-shot accuracy does not certify recursive reuse, so a posterior estimator should be tested as an update rule before its predictions become priors.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
amortized inference, neural posterior estimation, recursive Bayesian updating, sequential inference, in-context learning, transformers, distribution shift, exposure bias, simulation-based inference, compositional inference

Reviews

Among:
Shape:
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_RYXCOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2(+1)
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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 t−1t-1 as the prior for time tt) 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
  • 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?

  • Is there a failure specific to the chining mechanism, beyond the network receiving priors it was not trained on?

4 comments
AuthorsOpenReview ↗

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)

AuthorsOpenReview ↗

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)

AuthorsOpenReview ↗

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.

Reviewer_RYXCOpenReview ↗

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.

Reviewer_iJG6OpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
2
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Paper summary

Paper deals with transformers used for amortized inference of distributions. Specifically, it focuses on a recursive use of transformers to build a posterior from a prior plus a new data point and use this posterior as a new prior for the next data point. As the first posterior is an amortized posterior (so not exact), the paper investigates how this error propagates and what can improve the propagation.

Critical strengths

-> Error propagation is an important topic -> It is relevant to see how errors propagate in amortized inference / transformers.

Critical weaknesses
  • Style of presentation makes it hard to judge the contribution (examples below)
  • Limited benchmarking: study entirely on self trained network with some very specific but unsupported choices as \tau \in [0.2,3]. Leaves question open whether training was unfortunate or results transfer to broader class of methods. Either use methods from literature or show that your network is competitive with these.
  • Limited experiments: Scalar Gaussian mean, Bayesian linear regression d=2, logistic regression d=1,d=2. [If exact is not possible for larger experiments MC or approximation could be used]

Details: line 098: s_0^2 seems to be undefined. line 130: we sample a prior \pi with mean and SD. Do mean and SD fully specify the prior? I don't see mentioned that prior has to be Gaussian. line 132: We draw θ from that prior, generate n observations D from that same θ: If I draw theta from a prior, it is a number. How can I generate n observations from that number? line 152: please phrase eq (2) in terms of mathematical variables defined before.

Figure 2: a) the exact posterior soon falls below 0.2, so below training data. So, in case U_{\phi} calculates good posteriors, these should have SD < 0.2. The next prior (also SD < 2) would be outside of the training data. Any result on recursiveness could be severely impacted by this. Does simple removing (line 250) create bias? Mentioned in additional experiment as "neither change makes the finite prior domain closed". Why is the range of training not chosen much larger to make sure any SD values at inference time or covered?

Figure 2b: Blue is one call on 32/K observations, disagreement to exact. Red is K recursive calls on n/K observations, disagreement to exact. Red is larger than Blue means that deviation from exact is larger for K calls than for one call. Am I missing anything here? This would be a sanity check. As Figure 2b is not referenced in text hard to see what I might have missed.

line 351: "The proof is multiplication and cancellation (Appendix B)" -> Appendix B starts with some notation followed by a proposition 2. It does not mention Proposition 1 -- proof. It's hard for the readers to search where a proof could be.

Appendix: there are 9 more propositions which I fail to see referenced in the main text.

Proposition 2: imprecise / sloppy arguments in proof, e.g.

  • "For scalar Gaussian location, the observation variance is one". Why is it without loss of generality?
  • "the training prior standard deviation satisfies \tau \in [0.2, 3]" -> that's an arbitrary choice. Should either be moved to the statement of the Proposition or explained why without loss of generality
  • Why do we have \tau here and s_0^2 in beginning of main text? Are they the same?
  • either explicitly say that you want to build one counter-example an set this to 0.2 or stay general with \tau_0.
  • In a proof everything needs to be defined: what are "training prior Cholesky diagonals"?
  • Are the [0.5,2] an assumption, a value used in the main text or a conclusion?
  • Stopped reviewing proof here.

Abbreviations: line 055: even though SD commonly used, it should be introduced when first used. line 137: what are RQ4 models?

Justification for choice of numeric values and robustness: Quite a few numerical values are chosen and their choice is not motivated. It is unclear how robust the work is with respect to these choices as no sensitivity analysis is indicated: line 098: interval [0.2,3] line 131: [-4,4] line 131: 32 line 171: 513-point grid

Questions for authors

line 161: Defined for Gaussian and grid outputs. How for all other outputs? Or is this a restriction?

4 comments
AuthorsOpenReview ↗

Response to reviewer iJG6

Thank you for recognizing the importance of error propagation in amortized inference and transformers, and for your detailed reading notes. Your comments helped us clarify the contribution, explain the experimental setup, and distinguish the conclusions supported by our controls from questions that remain open.

I1. Make the contribution easier to identify

The abstract and §1 now state the fixed-data test and the grid-logistic finding: updaters can rank differently on exact and model-generated priors, even when both see identical inputs within a comparison. Section 2 introduces training, one-call evaluation, and recursive reuse with a worked example and schematic (Box 1 and Figure 1), then defines disagreement separately from reference error. Table 2 gives the fixed-data comparison (RQ1); Tables 3–4 give the training-prior comparisons (RQ2).

I2. Benchmark against established methods and test whether training choices explain the findings

We added two comparisons involving established methods. App. Q (Table 19) compares full-covariance online Laplace with same-data history refits on a real-data task. App. R.4 (Table 23) fits a released-configuration Distribution Transformers baseline on its native filtering task. The model-prior warm restart does not convincingly improve on fresh-prior continuation (NLL difference −0.014, conditional 95% interval [−0.030, 0.001]), loses to longer fresh-prior training in all three pairs, and does not beat the untouched baseline. These comparisons do not establish that our snapshot networks are competitive with published inference systems on a shared task.

The original fixed-step comparison gives the model arm an extra forward pass. In 96 new fits, we instead match useful CPU training time, including prior generation, at two budgets per task and select checkpoints using a separate fresh-prior validation bank. At 180 seconds, logistic 32-call root-JS is 0.591, 0.441, and 0.173 for fresh, exact, and model training. Model training beats exact training in every seed at both budgets and with either selected or final checkpoints, despite worse one-call fit in the selected comparison. Scalar Gaussian favors exact exposure on average when all seeds are included. Equal useful time does not match FLOPs or establish convergence or optimal tuning (§4, Tables 3–4; App. R.2, Table 21). Held-out generator seeds also preserve the logistic reversal within the model-prior regime, not across arbitrary approximate priors (App. R.1, Table 20). The same-backbone and capacity checks remain internal: only one of six pairs met the planned one-call accuracy match, and capacity changes did not uniformly improve the diagnostics (§§5, 7; Apps. G–H). I9 and I18 address the numerical choices.

I3. Test larger problems with a numerical reference if needed

The online Laplace pilot uses 31 logistic regression coefficients and a full-likelihood numerical reference checked by replicated importance estimates or, when those are unstable, Hamiltonian Monte Carlo. Its predictive RMSE to that reference is 0.0312 under reuse versus 0.0157 for history refits (App. Q, Table 19). This is a larger test of a sequential approximation, not of our learned updater.

We also tried an eight-coefficient learned Gaussian regression model, where the reference is analytic. Its best fresh-prior validation KL after 120 seconds was 4.2254 joint (0.5282 per coefficient), above the provisional gate of 0.12 joint (0.015 per coefficient). We stopped before the three-arm study and created no confirmatory test bank (§7; App. R.5). The continuous two-coefficient logistic result still uses a bounded-grid reference: finer spacing checks resolution on six tasks, not omitted tails, and we did not run an MCMC cross-check for that task (Apps. C.1, K.1). The native filtering study audits and corrects the reference sensor law separately, but the particle-reference gate did not pass. It therefore scores latent-state NLL and reports no posterior-distance result or reference-prior training arm (App. R.4).

I4. Define the initial variance

Section 2 defines the initial standard deviation as s0s_0 and the initial variance as s02s_0^2. App. B.2 uses the same notation.

I5. Explain when mean and standard deviation specify the prior

They specify the scalar prior because it is explicitly Gaussian, π=N(m0,s02)\pi=\mathcal N(m_0,s_0^2). We do not assume that two moments determine an arbitrary distribution. Table 1 lists the representations for other tasks, including a probability vector for grid logistic inference (§2; App. C.1).

I6. Explain how one latent draw generates multiple observations

A task draws θ\theta once. The observations are then sampled independently conditional on that draw: yi∣θ∼N(θ,1)y_i\mid\theta\sim\mathcal N(\theta,1). The observations share a latent mean, not their noise (§2, “Training and recursive evaluation”).

(Continued)

AuthorsOpenReview ↗

1-Continued Response to reviewer iJG6

I7. Write the ratio using the defined variables

Equation (2) now indexes the tasks explicitly. Its numerator sums d(qK,i,B(π0,i,Di))d(q_{K,i},B(\pi_{0,i},D_i)) and its denominator sums d(Uϕ(π0,i,Di1),B(π0,i,Di1))d(U_\phi(\pi_{0,i},D_{i1}),B(\pi_{0,i},D_{i1})). We compute the ratio per seed and then average the ratios (§2; App. F.3).

I8. Clarify what conditioning on in-range priors does

The shallow test conditions on whether the exact first-block posterior is in range. This changes the population being described, but does not select on the learned output. It retains 118, 118, and 113 of 160 tasks by seed. Exact and learned box membership agree for 479 of 480 task–seed pairs. On the retained subset, recursive-to-batch accuracy ratios are 1.04, 1.25, and 0.94: there is disagreement across splits, but no consistent accuracy penalty (§3, Figure 2a; App. F.2).

The deep result is unfiltered. At 16 calls every exact scalar trajectory leaves the box before the final call. Filtering by learned membership there could favor predictions that fail to narrow as Bayes does. We do not use the shallow result to rule out range departure as a contributor to deep accuracy loss, and an in-box prior need not match the training prior/block law (Apps. F.3, R.3).

I9. Test whether a wider prior range helps

At the tested budget, lowering the scalar SD floor from 0.20 to 0.03, widening the mean range from ±4 to ±12, or doing both increases absolute 16-call W2W_2 from 0.116 to 0.201–0.333. Short-block error also worsens. This factorial does not rule out a better-tuned wider sampler (§4; App. D.6).

A lower positive floor can reduce the size of the excursion, but does not give strict closure if a prior can start at that floor. For grid logistic inference the obstruction is different: changing Gaussian hyperparameter ranges cannot preserve the discretized-Gaussian form under a Bernoulli update. Neither observation implies that a learned model must fail (App. B.2, Proposition 1). App. R.3 distinguishes examples from the shared fresh training component from continuation priors that only overlap in parameter range. This is a comparison of supplied inputs, not training on a fully matched or enlarged support.

I10. Interpret the red and blue curves in Figure 2b

Yes: red above blue means the final recursive error exceeds the first-call error, each against its own exact target. Blue uses Bayes on the first 32/K32/K observations; red uses Bayes on all 32. Blue checks short-input accuracy and does not estimate what the red error would have been without chaining. The main text now discusses both curves. At K=16K=16, the mean of the seven retained per-seed ratios is 4.61, versus 4.53 for the ratio of plotted means (§§2–3, Figure 2b–c; App. F.3).

I11. Point directly to the additive-evidence proof

The original Proposition 1 is now Proposition 2. Section 5 points to the result, and App. B.3 gives the proof under “Additive evidence gives an update algebra.” The first block’s normalizer is constant in θ\theta and cancels when the second block is normalized.

I12. Explain the roles of the other propositions

The opening of App. B maps the results to their uses. The main text links Proposition 1 to prior-sampler nonclosure (§3), Proposition 2 to the additive-factor control (§5), Proposition 5 to the use of metric distances (§2), and Proposition 6 to the limits of context extrapolation (§7). Proposition 3 explains why agreement does not identify ordinary Bayes. Proposition 4 gives the shared-normalization criterion for transferring posterior-scale accuracy; the empirical spread and geometry scores in Apps. C.2 and F.1 do not test its asymptotic premise. Propositions 7–9 support the metric computations in App. C.2. The finite-range spread results are not asymptotic claims.

I13. State whether unit observation variance is without loss of generality

No. App. B.2 explicitly states that unit variance is a benchmark choice. The scalar proof starts with the general posterior SD (s0−2+n/σ2)−1/2(s_0^{-2}+n/\sigma^2)^{-1/2} and then sets σ2=1\sigma^2=1 for this task.

I14. Distinguish the benchmark interval, notation, and general argument

App. B.2 states s0∈[0.2,3]s_0\in[0.2,3] as a benchmark assumption in Proposition 1. The old τ\tau in this proof was the initial SD, now s0s_0, not its variance. We explicitly choose s0=0.2s_0=0.2 for the witness and note that the strict inequality persists for nearby admissible priors. The separate general argument takes s0=as_0=a for any interval [a,b][a,b] with a>0a>0.

I15. Define the Cholesky diagonal and its sampler bounds

In App. B.2, LL is the lower-triangular factor with positive diagonal in Σ=LL⊤\Sigma=LL^\top. Its diagonal entries are the quantities restricted to [0.5,2][0.5,2] by the sampler, not by the conclusion (App. C.1). With L=0.5I2L=0.5I_2, X=I2X=I_2, and observation SD 0.50.5, the posterior covariance is I2/8I_2/8 and its Cholesky diagonal is 1/8<0.51/\sqrt{8}<0.5.

(Continued)

AuthorsOpenReview ↗

2-Continued Response to reviewer iJG6

I16. Define SD at first use

Box 1 in §2 spells out “standard deviation (SD)” at its first occurrence in the revised PDF.

I17. Identify the models previously called “RQ4 models”

Section 2 now names the continuous two-coefficient logistic control directly rather than referring to “RQ4 models.” The Gaussian snapshot and Gaussian-factor models train on moment-matched posterior targets. The correct-logit factor model uses the specified likelihood form and simulated latent values for training, not posterior labels. App. K.1 separates these learned models from the reference-dependent diagnostics (§2, Table 1; §5; App. K).

I18. Justify the numerical choices and delimit the sensitivity checks

The scalar bounds define a finite benchmark with an analytic reference and a known boundary for reuse. The factorial varies the SD floor and mean range, not the upper SD endpoint (App. D.6). The cap of 32 sets the supported input length and lets the fixed-data test compare one call on all 32 observations with shorter blocks on the same data. Gaussian extrapolation controls vary the cap, but do not retrain the three RQ2 arms across caps (Apps. F, H).

The frozen-checkpoint controls instead cross prior sources with blocks of 1, 2, 4, and 8 observations. The logistic local reversal holds at every tested size. Holding block size at two and extending the horizon up to 16 calls preserves the model-prior arm’s logistic rollout advantage while total information and carried priors still change (App. R.3, Table 22).

The 513 points on [−6,6][-6,6] define the one-coefficient logistic simulator and output space, making the reference exact on that space (§2; App. C.1). This explains the discrete design, not why 513 is optimal. We did not test a different training grid. The within-box refinement for continuous two-coefficient inference does not fill that gap. Upper-SD sensitivity, RQ2 context-cap retraining, and one-coefficient grid-resolution sensitivity remain open.

I19. Specify the metrics for other output families

Section 2 restricts the headline metric comparison to Gaussian W2W_2 and grid root-JS. App. C.2 specifies quantile W2W_2 for Beta–Bernoulli, with a separate JS propagation diagnostic, and one-call KL and recursive symmetric KL for Dirichlet–Categorical. These descriptive divergences are not substituted into the metric bound (Proposition 5). In the continuous two-coefficient logistic task, the normalized moment statistic lower-bounds the W2W_2 distance from the standardized, grid-normalized law to the standard normal. It equals the distance for the law’s moment-matched Gaussian, not necessarily for the original continuous prediction (Apps. B.8, C.2, K).

Closing

We hope the clearer setup and added controls make the contribution easier to assess. For the amortized-inference community, the useful finding is that an updater's accuracy on exact intermediate priors can give a misleading ranking for model-generated inputs. The paper provides a reproducible way to test this distinction while keeping the reference targets and metrics explicit.

Reviewer_iJG6OpenReview ↗

Answer to rebuttal

I acknowledge the authors answers, explanations and additional experiments. While I think they are improving the paper, I feel the paper would still need to be majorly revised, e.g. a) benchmarking seems to be mainly in appendix (I2 mentions App Q Tab19 and App R4, Tab23 and uses a method from 2018 -- amortization is a field of recent activity!) even though also asked for by dgS8 or b) larger / real-world experiments (e.g. I3 mentions App Q Tab 19 and other App) also mainly in appendix even though central. I maintain my score.

Reviewer_dgS8OpenReview ↗
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3
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Paper summary

This paper studies the question of whether approximate Bayesian Posteriors remain accurate when used sequentially, with each posterior becoming the prior for the next update. This is an interesting question because it is the key motivation for using Bayesian methods for continual learning. The authors investigate this by training small transformers to approximate Bayesian inference on synthetic Gaussian and logistic regression problems, then comparing their predictions when the same dataset is processed in a single batch or through successive updates. They find that approximation errors can accumulate substantially under recursive reuse, even when single-step inference is accurate. They further demonstrate that training on intermediate posteriors, particularly the model's own predictions, significantly reduces this error.

Critical strengths
  1. The topic of studying the approximate posteriors and the approximation error under sequential reuse is interesting.
Critical weaknesses
  1. This paper investigates a nonstandard amortized Bayesian inference method in which a small transformer takes a dataset and a prior as inputs and outputs an approximate posterior distribution. This is quite different from widely used approximate Bayesian inference methods such as Laplace approximation, Variational Inference, IVON, and SWAG. It is also different from conventional Prior-Fitted Networks, which typically predict posterior predictive distributions rather than reusable parameter posteriors. It is unclear how much their conclusions generalize to established approximate Bayesian inference methods. The paper would be substantially stronger if it investigated whether similar problems arise in existing methods, particularly those designed for sequential inference.

  2. The experiments are restricted almost entirely to very simple synthetic problems, including one-dimensional Gaussian estimation and low-dimensional linear and logistic regression. These are settings where exact Bayesian inference is relatively straightforward. Given that the paper is motivated by applications requiring sequential Bayesian updates, it would be valuable to demonstrate the findings on more realistic problems, particularly higher-dimensional posterior inference or continual learning with neural networks.

  3. The authors show that recursive inference can produce substantially larger errors than one-shot inference. However, increasing the number of recursive updates also reduces the number of observations processed in each update. Furthermore, repeated approximation errors can accumulate even without distribution shift or any particular failure of amortized inference. It remains unclear how much of the observed degradation is due to ordinary error accumulation, distribution shift, or a failure of the learned update operator to satisfy Bayesian consistency.

Questions for authors

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3 comments
AuthorsOpenReview ↗

Response to reviewer dgS8

Thank you for your careful review and for recognizing the interest in studying approximation error under sequential posterior reuse. Your questions about established methods, higher-dimensional problems, and block-size effects motivated the additional experiments described below.

The main result is narrower than a claim that chaining generally fails: in grid logistic inference, the updater that is more accurate on exact intermediate priors becomes less accurate on priors generated by other seeds of the model-prior arm, even when both updaters receive the same prior and next block. We test generality separately with online Laplace and a published learned filtering interface, and address the block-size objection with two additional controls.

D1. Does the result extend to existing methods that use approximate posteriors sequentially?

Approximate posterior carryover loses accuracy in our online Laplace pilot, but we do not find convincing evidence that the learned intervention transfers to the published filtering system we tested. Our task-specific transformer returns a distribution over the parameter that can serve as the next prior. A conventional PFN's posterior predictive distribution over a response does not ordinarily provide that reusable parameter state. The transformer does not stand in for Laplace, VI, IVON, or SWAG.

We apply the published full-covariance online Laplace recursion of Ritter et al. to real-data logistic regression. Carrying the approximate state forward gives higher predictive RMSE relative to a checked numerical reference than refitting on the accumulated data (0.0312 vs. 0.0157). This is an example of a reuse penalty in an established method, not a test of prior-exposure training in Laplace.

For a learned system, we adapt the released sensor-filtering configuration of Distribution Transformers, preserving its simulator, Gaussian-mixture state, and dynamic prediction step. Three seeds per continuation arm start from one shared baseline after completing the released training schedule, with a common weights-only optimizer restart. Model-prior exposure changes dense latent-state NLL by −0.0143 relative to equal-example fresh continuation (conditional 95% trajectory-bootstrap interval [−0.0303, 0.0010]). Longer fresh continuation is better in all three pairs, and the untouched baseline (−0.1544) beats all nine continuations. This is a negative result for the tested one-step exposure and restart recipe. It is not a reproduction of the published comparison, a static partition test, or a benchmark against the full class of methods you named.

Revised manuscript: §§1, 4, 6–7; Appendix Q, Table 19; Appendix R.4, Table 23.

D2. Low-dimensional synthetic problems do not establish relevance to larger inference problems or continual learning

The real-data pilot extends the reuse comparison to 31 parameters, but the larger learned-updater comparison did not pass its feasibility screen. In the primary online Laplace comparison (16 arrivals), the Wisconsin Diagnostic Breast Cancer data provide 30 covariates plus an intercept. We use five splits, eight arrival orders per split, and a checked numerical full-likelihood reference. Held-out log loss is 0.0863 online versus 0.0800 for history refits. The penalty is positive on all five splits, but none meets the prespecified 0.01-nat threshold.

The learned filtering adaptation tests a different task and posterior interface, without showing an exposure benefit under the tested recipe. We also attempted an eight-coefficient linear-Gaussian updater, for which the posterior reference is analytic. After 120 seconds of useful CPU training, its best fresh-prior validation KL was 4.2254 jointly (0.5282 per coefficient), missing the prespecified joint threshold of 0.12. We did not run the three-arm comparison or evaluate a confirmatory bank. The probe measures one-call fitting feasibility at that budget, not how recursive performance scales. The lower-dimensional tasks remain useful for measuring local error from the actual supplied prior. They do not establish generalization to higher-dimensional learned inference or neural-network continual learning.

Revised manuscript: §§4 and 7; Appendix Q, Table 19; Appendices R.4–R.5.

(Continued)

AuthorsOpenReview ↗

Continued Response to reviewer dgS8

D3. Changing the split changes block size; how much degradation is propagation, shift, or inconsistency?

The fixed-data sweep measures the effect of changing the entire processing schedule. With equal partitions and fixed total sample size, more calls necessarily mean smaller blocks. The blue and red curves in Figure 2b also have different targets (the first-block and full-data posteriors), so their gap is not an estimate of error caused by chaining. In the scalar independent-residual control, perturbing otherwise exact updates produces recursive error of comparable magnitude. This shows that ordinary propagation is plausible, but the independent perturbations do not reproduce the learned updater's residual dependencies.

To compare the learned update rules directly, we score their outputs against Bayes on the same supplied prior and next block. On exact logistic paths, the exact- and model-prior arms have local root-JS errors of 0.0401 and 0.1245. On paths generated by other seeds of the model-prior arm, they are 0.1156 and 0.0322. Each comparison has the same direction across all eight updater seeds. This rules out different inputs explaining the comparison within a path and shows that an updater need not see its own outputs for the reversal. The two path sources are still different input distributions. Replacing just the final logistic update with exact Bayes also leaves most of the endpoint error, a measure of the error remaining after correctly updating the carried state rather than a causal allocation.

Two follow-ups address block size. With the supplied prior and lead history held fixed, the local logistic ranking reverses between exact and other-seed model one-step priors at each tested next-block length (1, 2, 4, and 8). At length 2, exact versus model local root-JS is 0.0363 versus 0.1096 on exact one-step priors and 0.1401 versus 0.0345 on other-seed model priors. Separately, with two observations per call, 16-call logistic rollout errors are 0.5680, 0.4927, and 0.1195 for fresh-, exact-, and model-prior training, versus 0.0321, 0.0303, and 0.0309 in single calls on the same 32 observations. The scalar results do not reproduce the logistic reversal. The fixed-block sweep removes the shrinking-block change, but both the accumulated data and the carried-prior law change with horizon. These experiments do not identify separate shares due to propagation, prior shift, and partition inconsistency.

Revised manuscript: §§2–4, Figure 2b–c; Appendices E, P (Table 18), R.1 (Table 20), and R.3 (Table 22 and fixed-block horizon).

Closing

Your questions helped us make the practical scope explicit. For researchers building sequential inference systems, the paper provides a controlled way to assess whether one-call performance carries over to the intended update schedule. The established-method tests also show why evidence from one learned updater should not be generalized to all sequential approximations.

I appreciate the authors' response and revisions. But I think the overall changes required are too significant for the rebuttal period. I maintain my score.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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