acceptodds
Under review as a conference paper at ICLR 2027

Parameter-State Evaluation Graphs: Structure and Prediction in Finite-Horizon Adaptation

Abstract

Learning procedures can differ not only in which updates they apply, but also in which historical parameter state each update reads. We study this choice in finite-horizon adaptation and represent it as a parameter-state evaluation graph. Common summaries describe the amount of staleness, but discard the update identity associated with each stale read. We show that this missing identity information matters. Graphs with the same updates, order, and aggregate delay statistics can still reach different endpoints because the same delays attach to different updates. An exact affine analysis explains this difference. From a single fully sequential reference trajectory, we predict the endpoints of unexecuted graphs by measuring the defect introduced by each stale read and propagating it through the remaining updates. In the primary supervised setting, this pathwise prediction improves graph ranking and captures matched-delay differences missed by aggregate summaries. Our results indicate that the parameter state read by each update should be treated as part of the finite-horizon learning algorithm, not merely as an implementation detail, and that part of its effect can be predicted from a single reference trajectory.

Primary area:
optimization
Keywords:
finite-horizon optimization, gradient-based adaptation, stale updates, delayed optimization, parameter-state evaluation graphs

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_omeeOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper studies how the parameter states used by individual updates affect finite-horizon adaptation. The authors introduce parameter-state evaluation graphs to represent these dependencies.

The paper shows that different update schedules can produce different results even when they share the same updates, order, and aggregate delay statistics. An exact affine analysis explains this effect.

The authors also propose a Fresh-reference predictor. It estimates the endpoints of alternative evaluation graphs using a single sequential reference trajectory. Experiments across several adaptation settings demonstrate the importance of read-state assignment and evaluate the predictor's accuracy and practical utility.

Critical strengths
  1. A well-defined research question supported by theory and controlled experiments.

The paper identifies an important limitation of aggregate staleness measures. The matched-delay comparisons isolate the effect of assigning stale reads to different updates.

The exact affine analysis provides a clear explanation for these differences. The empirical results further support the theoretical findings. This makes the central contribution convincing.

  1. Careful evaluation of the proposed predictor and its limitations.

The Fresh-reference predictor improves ranking performance in the primary supervised setting. For example, the median Spearman correlation increases from 0.569–0.616 with local defects to 0.722–0.772 with pathwise transport.

The authors also examine different datasets, model parameters, objectives, and adaptation horizons. Importantly, they report cases where prediction or graph selection becomes less effective. These experiments strengthen the credibility of the findings.

Critical weaknesses
  1. The practical impact of evaluation graph selection is sensitive to calibration.

The primary experiments show substantial differences between evaluation graphs. However, these differences become much smaller after controlling for initialization and graph-specific learning rates.

Table 4 shows that the Fresh–common-origin contrast decreases to 0.002–0.010 CE under joint calibration. Output calibration also removes more than 92% of the raw CE contrast.

The structural differences remain, but their practical importance under well-calibrated adaptation is less clear.

  1. The predictor does not yet provide a clear computational advantage.

The predictor improves endpoint ranking without executing every candidate graph. However, the current implementation is slower than exhaustive selection in the reported K=5 experiment.

Furthermore, the predictor-guided selector does not meet the stated noninferiority criterion relative to exhaustive selection. Its advantages also become very small after output calibration.

These results limit the practical benefit of the proposed prediction method.

  1. The predictor's effectiveness varies substantially across adaptation settings.

The predictor works well in the primary supervised setting, but its performance does not transfer consistently. For example, its pooled median rank correlation falls to 0.067 in the CLIP-LoRA setting.

The main experiments also focus on short horizons with contiguous refresh schedules and memoryless updates. It remains unclear how well the predictor extends to more general update dependencies and optimizers with internal states.

Questions for authors
  1. Under what conditions does evaluation graph selection provide meaningful benefits after both learning-rate and output calibration?
  2. Could the computational cost of the Fresh-reference predictor be reduced enough to outperform exhaustive graph evaluation?
  3. What explains the large reduction in predictor accuracy in the CLIP-LoRA setting? Can the proposed reliability diagnostics help identify when prediction should not be used?
  4. How difficult would it be to extend the evaluation graph framework to non-contiguous schedules or optimizers such as Adam?
3 comments
AuthorsOpenReview ↗

Reply to reviewer omee (part 1 of 2)

Thank you for the encouraging assessment, and for noting that the central contribution is convincing and that reporting the cases where prediction or selection becomes less effective strengthens “the credibility of the findings”. Your four questions shaped several of the additions in this revision, and we address them in order below.

"Under what conditions does evaluation graph selection provide meaningful benefits after both learning-rate and output calibration?"

Selection matters most when the step size is fixed and the refresh budget is limited. The answer depends on whether the step size can be re-tuned for each graph. If it can, re-tuning closes almost all of the fresh–batched gap, and selection retains only a small gain. If the step size is fixed, for instance when a meta-learned step size is deployed without per-graph re-tuning, and the number of refreshes is budgeted, selection matters considerably more. In both cases, PJGS uses support data only (Appendix A.12, Table 16):

SettingComparisonHeld-out CE
K=5, native step sizeexact PJGS vs. terminal-protected schedule+0.039 to +0.055 (median normalized regret to the oracle 0.114)
K=8, native step sizeexact PJGS vs. terminal-protected schedule+0.157 to +0.219
K=5, both calibrations, B=2PJGS vs. tuned fixed graph+0.00023, +0.00046 (Holm 0.041, 0.0012); none at B=3
K=5, full-support init, native → per-graph step sizefresh–batched gap0.444–0.520 → 0.002–0.010

Tuning also leaves in place the structure on which selection acts: matched-delay contrasts still vary by 0.034–0.086 CE across support orders within an episode, and the predictor ranks them with Spearman 0.938–0.996 (Table 3). In short, tuning reduces how much there is to gain from choosing a graph, but not the differences between graphs themselves.

A third condition is that graphs are scored under the same initialization convention they will run from. PJGS keeps the two consistent by design: the fold heads and the executed head both start from S1 prototypes. A new controlled experiment shows why this matters (Appendix A.12). When execution starts from the full support set but scoring keeps S1, selection falls below the best fixed graph; scoring each fold from all support images outside its validation set restores it, lowering held-out CE by 0.127 and 0.112 on two checkpoints (100 new episodes each) and raising top-1 graph-selection accuracy among four graphs from 32% to 50% and from 30% to 44%. Parameter-state conventions therefore shape the choice of a graph, not only its endpoint.

"Could the computational cost of the Fresh-reference predictor be reduced enough to outperform exhaustive graph evaluation?"

Yes: computing the shared quantities once makes prediction faster than exhaustive evaluation for complete graph families. The submitted code recomputed every stale defect and its transport for each candidate graph, although both depend only on the reference trajectory and on the (receiving update, read state) pair. The cost therefore came from this recomputation rather than from the method itself. Computing these quantities once reproduces the submitted predictions bit for bit and reverses the comparison (Table 40):

Complete familyExecute every graphCached predictor
K=8 (128 graphs)3.14 s0.46 s
K=12 (2,048 graphs, six cells)23.8 s1.27 s, 18.0–19.3× faster in every cell

These cached predictions also remain accurate at this scale: on all 2,048 graphs at K=12, each executed for ground truth on 50 new episodes, they rank the graphs with median Spearman 0.55, against 0.31 for local defects (Table 41).

Only in the ten-candidate K=5 selection protocol, where PG-JGS already shared these quantities, is directly running such a small family still faster (1.52 s vs. 1.92 s median). Beyond such small families, execution grows as K·2^(K−1) operator applications, while the cache requires O(K²) field evaluations and O(K³) JVPs, plus inexpensive vector additions, so the advantage of prediction widens with K (operation counts are given in our reply to aA49).

AuthorsOpenReview ↗

Reply to reviewer omee (part 2 of 2)

"What explains the large reduction in predictor accuracy in the CLIP-LoRA setting? Can the proposed reliability diagnostics help identify when prediction should not be used?"

Prediction fidelity tracks the size of the parameter displacements, and step-size calibration restores accurate ranking in CLIP-LoRA. The predictor propagates stale-read defects along the sequential reference trajectory. At the calibrated step size the support-side diagnostics in CLIP-LoRA are 39× (κ₀) and 103× (D_G) larger than in the supervised setting, consistent with stale reads moving the parameters far from that trajectory. Matching the step size to this regime is what works; block-recursive transport and a quadratic correction did not help. On a new bank of 80 episodes across four datasets, reducing the step size from 0.03 to 0.0075 raises the mean Spearman correlation from 0.090 to 0.506 [0.417, 0.590], full transport beats local defects by +0.206 [0.118, 0.291], and the adapted model improves over no adaptation by 0.725 CE (positive in 77 of 80 episodes). D_G tracks the recovery across episodes (Spearman −0.71) and is largest on EuroSAT, which has the lowest ranking (0.26, against 0.58–0.61 on the other three; Appendix B.5).

The diagnostics also identify this regime from support data alone. The pre-specified κ₀ and D_G track per-episode error (worst-decile AUC 0.91–0.94), and at the calibrated step size all 800 CLIP-LoRA episodes have κ₀ above the largest supervised value; a threshold set on supervised episodes would therefore abstain on every one of them. Within the supervised setting, a κ₀ threshold fixed on a development bank flags 17–20% of new episodes, whose prediction error is 3.2–3.5× that of the remaining ones (post hoc; Appendix A.22).

"How difficult would it be to extend the evaluation graph framework to non-contiguous schedules or optimizers such as Adam?"

The representation already covers both cases, and the predictor needs one additional specification for each. The evaluation graph already allows any causal read assignment (update t reads some earlier state a(t) < t), and the predictor's ingredients, namely the stale defect of update t at state a and its transport along the reference path, are defined for every pair a < t; contiguous schedules are the special case in which a(t) is a block start. For non-contiguous schedules, one additionally needs to fix the commit rule, that is, which updates are applied together and when. For Adam, the state must include the moment estimates, and one must specify whether an update reads stale moments in addition to stale parameters; the defect and transport then act on this extended state. Regarding horizon, the revision already goes beyond five updates: on the complete 128-graph family at K=8, the graded effect persists (Holm p = 0.0012), the predictor improves rank correlation over local defects, and support-only selection gains +0.157 to +0.219 CE; on the complete 2,048-graph family at K=12, the cached predictor ranks graphs with median Spearman 0.55 (local defects 0.31) while running 18–19× faster than execution. Our experiments use contiguous schedules and memoryless updates, and we see the two extensions above as the natural next steps.

We are grateful for your support of this work. We hope the revision further strengthens your confidence in it, and we remain happy to discuss any further questions.

AuthorsOpenReview ↗

Additional results on general causal schedules and adaptive prediction

Thank you for your constructive questions. We have extended the revised manuscript with new results addressing two points from your review.

Extension to non-contiguous schedules. We show that the Fresh-reference predictor applies to general causal read assignments using the same defect and transport formulation. We evaluate 24 non-contiguous schedules across 50 confirmation episodes under ResNet-12 feature-based adaptation, updating a 2,565-parameter linear head on frozen backbone features.

At the calibrated step size, the predictor achieves median Spearman 0.977 and within-budget R² 0.960, compared with 0.807 and 0.465 for the initialization-anchored second-order baseline. The same cached computation supports these schedules without additional model evaluations for each candidate graph (Appendix B.10, Table 46). Extending the method to optimizers with internal state, such as Adam, remains a separate direction.

Adaptive prediction and selection. We also turn the support-side reliability diagnostics into an adaptive predictor. Across 1,200 confirmation cases, its mean ranking correlation reaches 0.7985, above both fixed predictors. Under the two-block selection budget (B=2), the adaptive predictor reduces held-out query CE by 0.0276 relative to Always-Full on 300 strong-42 episodes. A lightweight variant separately reduces prediction-stage GPU latency by 35.9% while improving ranking over both baselines (Appendix A.22, Table 32).

These additions complement the previously reported mechanism analysis, K=12 caching results, and CLIP-LoRA step-size experiments. We appreciate the questions that motivated these extensions.

Reviewer_H4AMOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper investigates how different parameter-state reading patterns affect model performance in finite-horizon adaptation. The authors introduce Parameter-State Evaluation Graphs to characterize the historical parameter states used by individual updates. They demonstrate that different evaluation graphs can lead to different final model states, even when the number and order of updates, as well as aggregate delay statistics, remain identical.

To explain this phenomenon, the authors provide a theoretical analysis based on affine update models and propose the Fresh-Reference Predictor, which predicts the final parameter states of alternative evaluation graphs by estimating local update defects and propagating them along a single sequential reference trajectory. Experiments are primarily conducted on miniImageNet, with additional evaluations on other vision datasets, CLIP-LoRA, and test-time adaptation settings to examine the effects of parameter-state dependencies and the effectiveness of the proposed predictor.

Critical strengths
  1. The paper explicitly considers the historical parameter states accessed during optimization as an independent factor affecting learning outcomes. By comparing evaluation graphs with identical aggregate delay statistics, the authors demonstrate that the assignment of stale reads to individual updates can influence final model performance. Furthermore, the exact affine analysis provides a theoretical explanation for this phenomenon, offering a useful perspective on parameter dependencies in finite-horizon optimization.
  2. The experiments cover multiple datasets and model configurations, including different evaluation graphs, initialization strategies, learning rates, and adaptation scopes. In particular, the Fresh-Reference Predictor achieves Spearman correlations of 0.722–0.772 in the primary supervised setting, outperforming simpler local-defect predictors. These results provide empirical evidence that information from a single reference trajectory can help predict the outcomes of alternative update structures.
Critical weaknesses
  1. Although the paper demonstrates that different parameter-state reading patterns can significantly affect final model performance, Table 4 shows that the CE difference between Fresh and Common-Origin decreases from approximately 0.5–0.6 to 0.002–0.010 when using more comprehensive initialization and graph-specific learning-rate calibration. Furthermore, output calibration substantially reduces the original CE differences. These observations suggest that the reported effects are highly sensitive to optimization configurations. While differences between evaluation graphs still exist, the authors should further clarify whether parameter-state reading patterns remain an important independent factor in well-tuned practical settings and what additional benefits can be obtained by optimizing these structures.
  2. Although the Fresh-Reference Predictor achieves promising results in the primary supervised experiments, its predictive performance deteriorates substantially in other adaptation settings, such as CLIP-LoRA, suggesting limited robustness across different scenarios. Furthermore, Appendix A.15 shows that the current predictor-guided graph selection method is computationally more expensive than exhaustive evaluation and fails to meet the predefined non-inferiority criterion in some experiments. Therefore, despite its ability to predict the outcomes of alternative evaluation graphs, its practical advantages over directly evaluating candidate structures remain unclear. The authors should further clarify the conditions under which the predictor is effective and provide stronger evidence of its practical value in model adaptation.
Questions for authors

Same as Critical Weaknesses

3 comments
AuthorsOpenReview ↗

Reply to reviewer H4AM (part 1 of 2)

Thank you for the careful review, and for recognizing the value of treating the state each update reads as an independent factor. Your two weaknesses are the questions on which we focused the revision, and we address them in turn in this comment and the next. To make the setup easier to follow, the introduction now also opens with a concrete matched-delay pair, [4,1] vs. [1,4].

"[...] the authors should further clarify whether parameter-state reading patterns remain an important independent factor in well-tuned practical settings and what additional benefits can be obtained by optimizing these structures."

Read placement remains an important factor after tuning, and our fixed-step experiments show direct gains from optimizing it. Thank you for raising this important point. The answer depends on whether the step size can be re-tuned for each graph, and in both cases the read schedule matters.

When the step size is fixed, for instance when a meta-learned step size is deployed without per-graph re-tuning, optimizing the schedule pays off directly. Choosing among schedules with the same refresh budget from support data alone (exact PJGS) improves held-out CE in all six settings of Table 16, with every interval excluding zero in the five below:

Evaluated settingvs. terminal-protected schedulevs. balanced schedule
K=5, native step size+0.039 to +0.055+0.029 to +0.038
K=8, native step size+0.157 to +0.219+0.151 to +0.178
Full network (38 tensors), one fixed step size+0.064 to +0.130+0.053 to +0.162
CUB / FC100, transferred operator+0.0234 / +0.0526+0.0292 / +0.0749

The selected graph also remains close to the per-episode oracle: the median normalized regret is 0.114 at K=5 and stays below 0.15 in every K=5, K=8 and full-network setting. This is also the situation in which practitioners typically encounter the question. Meta-learned and test-time adaptation procedures usually fix the step size at training time. When such a procedure is deployed with batched or delayed reads, for instance to parallelize its updates, re-tuning for every schedule is often not an option, and the schedule becomes the remaining lever. Since PJGS uses support data only, it can be applied at deployment time.

When the step size can be re-tuned, the large average gap disappears, and the reason is simple. The operator's step size was learned for sequential (fresh) reads, so a fully batched schedule, in which all updates read the start state, runs with a step size that does not suit it. Once each graph receives its own step size, the gap nearly closes, as you correctly note. What tuning does not remove is the dependence on which update reads which state. At the three strong checkpoints each matched-delay pair shares one step size, so these contrasts isolate placement; as the table below shows, they persist through tuning, calibration and re-training of the operator:

ControlResultWhere
Native step sizebatched reads worse than no adaptation (+0.098 to +0.191 CE); fresh reads gain 0.44–0.48 CE and are 1.8–2.1 points more accurateTable 23
Graph-specific step sizebatched reads gain 0.32–0.36 CE over no adaptationTable 23
Full-support init alonebatched still 0.444–0.520 CE and 2.3–2.8 points behind freshTables 4, 23
Bothfresh–batched gap 0.002–0.010 CETable 4
Matched-delay pairs, native step size[4,1] is 1.5–1.7 and [3,2] 0.6–0.9 accuracy points above [1,4] and [2,3]Table 10
Matched-delay pairs, tuned settingvary by 0.034–0.086 CE across 120 support orders; predicted with Spearman 0.938–0.996Table 3
Output calibrationall 12 signs kept, residual 0.012–0.044 CE (92.1–94.0% of raw magnitude removed); accuracy unchangedApp. A.16, A.18
Operator meta-trained under batched readsall 3 pre-specified contrasts positive: 0.0097, 0.0159, 0.0114 CE (Holm p ≤ 0.003)App. A.24
Selection after tuning and calibrationPJGS beats the tuned fixed graph at B=2 by +0.00023 and +0.00046 CE (two of three strong checkpoints)App. A.18

The table can be read from top to bottom as a sequence of increasingly strict controls. The first four rows show that the large average gap is a step-size effect. The next three rows show that placement survives within a single step size: pairs that share every delay statistic still differ in accuracy, and their differences remain measurable and predictable after tuning and calibration. The last two rows show that the effect does not depend on how the operator was trained, and that selection still adds value after full tuning. Placement therefore also changes accuracy, and the effect is not a by-product of training the operator for fresh reads. In a well-tuned setting, read placement thus turns from a large average penalty into a structured effect that can be predicted in advance, which we discuss in the second part of our response.

AuthorsOpenReview ↗

Reply to reviewer H4AM (part 2 of 2)

"[...] its predictive performance deteriorates substantially in other adaptation settings, such as CLIP-LoRA, [...] Appendix A.15 shows that the current predictor-guided graph selection method is computationally more expensive than exhaustive evaluation and fails to meet the predefined non-inferiority criterion [...]. The authors should further clarify the conditions under which the predictor is effective and provide stronger evidence of its practical value in model adaptation."

For complete graph families, prediction is now faster than execution. The concern about cost led to the clearest improvement in the revision. The predictor's stale defects and transports depend only on the reference trajectory, so we now compute them once and reuse them for every graph, with bitwise identical predictions (Table 40; operation counts are given in our reply to aA49). The submitted code recomputed these shared quantities for every graph, although the method itself never required it. For complete graph families, prediction is now faster than execution, and the saving grows with the size of the family:

Complete familyExecute every graphCached predictor
K=8 (128 graphs)3.14 s0.46 s
K=12 (2,048 graphs, six cells)23.8 s1.27 s, 18.0–19.3× faster in every cell

In the small ten-candidate K=5 selection protocol of Appendix A.15, execution remains faster, as you point out. In this protocol, PG-JGS improves raw CE over the tuned fixed graph at B=2 (+0.00189, Holm p = 0.0104) and selects the same graph as exact PJGS in 72–80% of episodes, but it does not meet the pre-specified noninferiority margin. Where the two selectors disagree, the two best candidates are nearly tied (median gap 0.002–0.007 CE): a deterministic stability condition, evaluated on the exact scores, guarantees agreement with exhaustive selection in 27–44% of episodes, and all observed regret lies outside these certified episodes.

Regarding the conditions under which the predictor is effective, prediction fidelity is strongly associated with the size of the parameter displacements, and matching the step size gives accurate ranking in CLIP-LoRA. At the calibrated step size (0.03) the displacements are large (pooled median Spearman 0.067), and κ₀ and D_G, which need only support data, are 39× and 103× the supervised values. We therefore reduced the step size to 0.0075 (fixed from an earlier pilot) and evaluated 80 new episodes on four datasets. Mean Spearman over 120 support orders rises from 0.090 to 0.506 (paired gain +0.417 [0.318, 0.513]), full transport beats local defects by +0.206 [0.118, 0.291], and the model improves over no adaptation (+0.725 CE [0.582, 0.875], 77 of 80 episodes). Ranking reaches 0.58–0.61 on DTD, Flowers102 and FGVC-Aircraft, and 0.26 on EuroSAT, which has the largest D_G; D_G and ranking quality have Spearman correlation −0.71 across episodes (Table 44).

SettingPredictor accuracySupport-side signal
Supervised, 120 support orders (K=5)Spearman 0.722–0.772 (local defects 0.569–0.616)κ₀ / D_G track error: Spearman 0.82–0.84 / 0.79–0.83, worst-decile AUC 0.91–0.94 (Table 31)
Supervised, 128-graph K=8 familymedian 0.633 (local defects 0.520)—
Supervised, complete 2,048-graph K=12 familymedian 0.554 (local defects 0.305)—
Supervised, episodes flagged by κ₀ (17–20%; post hoc)error 3.2–3.5× the rest; ranking 0.52–0.62 vs. 0.88–0.91threshold fixed on a development bank (App. A.22)
CLIP-LoRA, step size 0.03pooled median 0.067κ₀ 39× and D_G 103× larger; all 800 episodes flagged
CLIP-LoRA, step size 0.0075 (new bank)mean 0.506 (local defects 0.300)D_G tracks ranking quality: Spearman −0.71 across episodes

The predictor answers what-if questions about read schedules without re-running the adaptation. In practice, it serves three purposes. First, before a sequential adaptation loop is changed into a batched or delayed one, a single Fresh run predicts the endpoint of every contiguous schedule; this is the question an engineer faces when parallelizing such a loop, namely which schedule can be adopted without hurting the result. Second, offline, its shortlist of the 16 best-predicted K=8 graphs, an eighth of the family, contains the actual best graph in 49.6% of episodes (12.5% by chance), with a median regret of 0.0003 CE; on the 2,048-graph K=12 family, the predicted top eighth contains it in 30.0% of episodes (12.5% by chance). Third, local defects alone identify the tasks that are most sensitive to the graph, recovering 70–80% of the top decile (10% by chance; Appendix B.6).

We appreciate that you pressed on calibration and practical value; answering these two points produced the new mechanism controls and the cached predictor. We hope that the new results address the concerns behind your current score, and if so, we would be grateful if you would consider revising it.

AuthorsOpenReview ↗

Additional evidence on predictive reliability and practical utility

Thank you again for your questions about the practical value and reliability of the proposed predictor. We have added two experimental results to the revised manuscript that directly strengthen this part of the paper.

First, we turn the support-side reliability diagnostics into an adaptive prediction method. Across 1,200 confirmation cases, reliability-guided switching improves mean graph-ranking Spearman to 0.7985, exceeding both fixed predictors (Full: 0.7726; Local: 0.7816). On 300 new strong-42 episodes, the same policy reduces held-out query CE by 0.0276 relative to Always-Full under the two-block selection budget (B=2).

A lightweight variant based on the existing prediction defects also improves ranking over both fixed predictors (Spearman 0.7911), while reducing prediction-stage GPU latency by 35.9%.

Second, we validate the predictor on non-contiguous causal read schedules. Across 24 schedules under ResNet-12 feature-based head adaptation, the predictor achieves median Spearman 0.977 and within-budget R² 0.960, using the same cached prediction method.

Together with the previously reported K=12 caching results and CLIP-LoRA step-size recovery, these additions demonstrate how the framework can support accurate and efficient prediction across different read schedules and guide graph selection under limited execution budgets.

The new results appear in Section 6, Appendix A.22, and Appendix B.10 (Tables 32 and 46). Thank you for considering these additional experiments.

Reviewer_aA49OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

The paper studies which historical parameter state each update reads during short adaptation runs. It shows that schedules with the same updates, execution order, and aggregate delay statistics can reach different endpoints, and explains this through an exact affine analysis. A predictor estimates unexecuted graph endpoints by propagating finite stale-read differences along a sequential reference trajectory for the same update order and operator. Experiments examine prediction and graph selection in supervised few-shot learning, with extensions to longer horizons, backbone adaptation, language classification, and test-time adaptation. Prediction improves in the main supervised setting, while its accuracy and decision value vary across regimes.

Critical strengths
  1. The experiments isolate the effect of read placement. Matching the data, update order, operator, and delay statistics makes the placement comparisons convincing. The affine analysis explains why the differences arise, and the calibration and initialization controls help separate the existence of the effect from its magnitude. This gives a precise account of information lost by aggregate staleness summaries.

  2. The predictor adds measurable information beyond simpler approximations. On independent evaluation episodes, transport improves order-ranking correlations from roughly 0.57–0.62 for local defects to 0.72–0.77. The eight-update experiment also improves discrimination among graphs with matched block-size multisets. These results support a real predictive contribution, and the explicit reporting of failures makes its scope easier to assess.

Critical weaknesses
  1. The predictor's value for choosing better adaptation procedures remains limited. Under the reported output calibration, predictor-guided selection offers only very small gains over a tuned fixed graph. It does not establish noninferiority to exhaustive selection at either tested budget and is slower in the measured implementation. The structural analysis is informative, but a useful trade-off between selection quality and computational cost has not been demonstrated.

  2. The benefit of transport is inconsistent outside the main prediction setting. Transport helps native order ranking and the eight-update graph family, but its gains over local defects are small or negative on several matched-delay comparisons. Prediction is poor in CLIP-LoRA, and transport adds little in the tested entropy-adaptation setting. The broader experiments establish that read placement matters more convincingly than they establish a broadly useful predictor.

  3. The practical magnitude of the read-placement effect is sensitive to tuning and calibration. Output calibration removes most of the raw structural loss differences. Separately, full-support initialization with graph-specific learning rates substantially reduces differences among schedules. The effect persists, but the large differences in the original setting do not establish comparable practical importance under well-tuned adaptation.

Questions for authors
  1. Calibration clarification: Which output temperature was assigned to PG-JGS in the calibrated comparisons? Was it fitted for PG-JGS on development data or inherited from exact PJGS? This matters when interpreting the small calibrated gains.
  2. Predictor clarification: Do the existing support-side reliability analyses distinguish cases where transport improves on local defects from cases where local defects alone are preferable?
  3. Cost clarification: For the eight-update experiment, how do the 1,792 field evaluations relate to the 34 unique state/update pairs? What is reused across graphs, and how much of the measured cost comes from transport rather than repeated field evaluation?
5 comments
AuthorsOpenReview ↗

Reply to reviewer aA49 (part 1 of 3)

Thank you for the precise questions, and for noting that the matched-delay design makes the placement comparisons convincing and that the predictor adds measurable information beyond simpler approximations. Each of your questions led to a change in the revision. We address the three questions first, together with the closely related weakness on cost, and then the remaining two weaknesses.

"Which output temperature was assigned to PG-JGS in the calibrated comparisons? Was it fitted for PG-JGS on development data or inherited from exact PJGS?"

PG-JGS inherits the temperature of exact PJGS. We did not fit a separate temperature for it; all inverse temperatures were fitted once on a separate development bank and frozen before the confirmation evaluation, as summarized below:

ArmTemperature
Exact PJGSfitted on the 400-episode development bank, per checkpoint, budget and policy (24 fits in all)
PG-JGSinherited from exact PJGS
Tuned fixed graphits own fitted value
No adaptationits own fitted value

The fitted values for PJGS and for the fixed graph differ by less than 0.2% in every cell, so temperature fitting does not explain the calibrated gain. Appendices A.15 and A.18 now state this explicitly.

"Do the existing support-side reliability analyses distinguish cases where transport improves on local defects from cases where local defects alone are preferable?"

Yes: a support-side diagnostic flags the episodes in which local defects should be preferred. We have added a test designed for exactly this question, at the level of individual episodes. Two of the three pre-specified support-side diagnostics, κ₀ and D_G, track per-episode prediction error (Spearman 0.82–0.84 and 0.79–0.83, worst-decile AUC 0.91–0.94; Table 31); D_G requires nothing beyond the predictor's own defects. We then asked, post hoc, whether κ₀ identifies the episodes in which full transport is worse than local defects. To this end, we fixed a threshold at the 0.8 quantile of a separate development bank, using support data only, and applied it to 300 new episodes (Appendix A.22). In the flagged episodes local defects are the better choice; in the remaining ones the two predictors agree and the graphs are ranked well.

This is in line with what κ₀ measures. As a read is moved from the fresh state toward the stale one, κ₀ compares how sharply the endpoint bends with how fast it moves at first. Intuitively, where this ratio is large, the first-order picture behind transport is least accurate, and local defects are the safer choice. In the table below, E denotes the error on the predicted graph-versus-Fresh CE contrasts over the 15 stale graphs, and ρ the rank correlation over the 16 graphs:

CheckpointFlaggedE, flagged / keptρ, flagged / keptE(Full) − E(Local), flagged / kept
main18%0.261 / 0.0750.59 / 0.90+0.045 / +0.004
strong-4217%0.254 / 0.0800.55 / 0.88+0.051 / +0.003
strong-4317%0.257 / 0.0790.52 / 0.90+0.051 / +0.001
strong-4420%0.207 / 0.0630.62 / 0.91+0.056 / 0.000

The difference in transport error is significant at the three strong checkpoints and remains at the 0.7 and 0.9 quantiles. Overall, transport still helps: it raises the ranking of native support orders from 0.569–0.616 to 0.722–0.772. Within an episode, which predictor is better also depends on the contrast (Table 36; median errors and the paired difference with its 95% bootstrap CI):

Matched-delay pairLocalFullFull − Local ΔE [95% CI]
[3,2] vs [2,3]0.0890.086−0.059 [−0.081, −0.039]
[4,1] vs [1,4]0.1010.160+0.076 [+0.051, +0.102]
[3,1,1] vs [1,1,3]0.0630.060−0.008 [−0.027, +0.010]
AuthorsOpenReview ↗

Reply to reviewer aA49 (part 2 of 3)

"How do the 1,792 field evaluations relate to the 34 unique state/update pairs? What is reused across graphs, and how much of the measured cost comes from transport rather than repeated field evaluation?"

The 1,792 operations stem from only 34 distinct inputs, so most of the measured cost was recomputation. Of the repeated operations, 75% were transport JVPs; the cost of the submitted code therefore came from recomputation rather than from the method itself. Each stale defect and its transport depend only on the reference trajectory and on the (receiving update, read state) pair. The revised predictor therefore computes each of them once and assembles every graph by lookup and summation, yielding bitwise identical predictions. Per episode and checkpoint at K=8:

Field evaluationsTransport JVPsTotal
Submitted code (recomputed for every graph)4481,3441,792
Distinct inputs28 stale (state, update) pairs6 reference states34
Cached predictor (computed once)285684

The median wall-clock time for the complete family is reported below (Table 40; K=12 is a six-cell replication, 18.0–19.3× faster in every cell):

K (graphs)5 (16)8 (128)10 (512)12 (2,048)
Exhaustive execution0.220 s3.14 s14.5 s23.8 s
Submitted predictor0.382 s8.84 s56.2 s—
Cached predictor0.103 s0.460 s0.932 s1.27 s

The cache requires K(K−1)/2 field evaluations and O(K³) JVPs, plus inexpensive vector additions, whereas execution requires K·2^(K−1) operator applications; the advantage therefore grows with K (Appendix B.6).

"The predictor's value for choosing better adaptation procedures remains limited. [...] a useful trade-off between selection quality and computational cost has not been demonstrated."

The predicted graph structure already pays off for profiling, screening and fixed-step selection. We agree that this trade-off should be demonstrated explicitly, and the revision now does so for these three uses. We also test separately whether prediction can replace exhaustive scoring altogether:

UseResultWhere
Profiling complete familiesK=8: ranking +0.080 [0.067, 0.099] over local defects, 0.46 s vs. 3.14 s to execute; K=12: ranking 0.55 vs. 0.31 (+0.207 [0.158, 0.248]), 18.0–19.3× fasterTables 40, 41
Screening (offline, labeled queries)top 16 of 128 graphs contain the best one in 49.6% of episodes (12.5% by chance), median regret 0.0003 CE; at K=12, the top 256 of 2,048 in 30.0% (12.5%)App. B.6
Support-only selection, fixed step sizeexact PJGS vs. terminal-protected schedule: +0.039 to +0.055 CE at K=5, +0.157 to +0.219 at K=8Table 16
Prediction-guided selection (PG-JGS)+0.00189 CE over the tuned fixed graph at B=2 (Holm p = 0.0104); same graph as exact PJGS in 72–80% of episodes; none of the 250 candidate compositions executedApp. A.15

The first three uses each show a clear gain. Profiling and screening benefit the most, since they require the whole family: execution has to pay for it graph by graph, while the cached predictor shares the work across graphs. In our fixed-step experiments, selection improves held-out CE over both structural anchors from support data alone, with each graph scored and executed under the same initialization convention. PG-JGS addresses the stricter question of whether prediction can replace exhaustive scoring. It does not reach the pre-specified noninferiority margin, and output calibration removes most of its gain. Its errors, however, are well understood: a deterministic stability condition, evaluated on the exact scores, guarantees agreement with exhaustive selection in 27–44% of episodes, and all observed regret lies outside these certified episodes, where the two best candidates are nearly tied (median gap 0.002–0.007 CE).

AuthorsOpenReview ↗

Reply to reviewer aA49 (part 3 of 3)

"The benefit of transport is inconsistent outside the main prediction setting. [...] Prediction is poor in CLIP-LoRA, and transport adds little in the tested entropy-adaptation setting."

Transport and local defects answer different questions, and the revision now makes this explicit. Thank you for raising this point. Transport ranks graphs within an episode, whereas local defects rank tasks by how sensitive they are to the graph (Appendix B.6).

TaskFull transportLocal defects
Ranking 120 support orders (K=5)0.722–0.7720.569–0.616
Ranking the 128-graph K=8 family0.633 (paired median gain +0.080 [0.067, 0.099])0.520
Ranking the 2,048-graph K=12 family0.554 (paired median gain +0.207 [0.158, 0.248])0.305
Ranking 120 support orders, CLIP-LoRA at step size 0.0075 (new bank, mean)0.506 (paired gain +0.206 [0.118, 0.291])0.300
Ranking 300 tasks by graph sensitivity (K=8)0.551–0.6080.935–0.948

On the sixteen-fold larger K=12 family, transport improves on local defects at every checkpoint and in 45 of 50 episodes, and it still separates graphs within matched block-size multisets (0.48–0.53 vs. 0.24–0.30), extending the matched-multiset result you highlighted. The binary matched-delay contrasts and the tested TTA setting fit this division, as in both cases local defects already capture most of the structure (Table 36 above). Under CLIP-LoRA, transport carries the prediction once the step size is matched: at a quarter of the calibrated step size, on a new four-dataset bank, the predictor ranks the 120 support orders with mean Spearman 0.51 against 0.30 for local defects (Appendix B.5). At the calibrated step size κ₀ flagged all 800 episodes in advance (pooled median 0.067).

"The practical magnitude of the read-placement effect is sensitive to tuning and calibration. [...] the large differences in the original setting do not establish comparable practical importance under well-tuned adaptation."

Read placement persists through every tuning and calibration control we ran. We agree that the size of the effect depends on tuning; its structure, however, does not. The large raw gap comes from the step size, which was learned for sequential reads, and giving each graph its own step size nearly closes it. What remains is the dependence on which update reads which state, which is not removed by tuning, calibration or re-training:

ControlResultWhere
Native step sizefully batched reads worse than no adaptation (+0.098 to +0.191 CE)Table 23
Full-support init, native step sizefresh–batched gap still 0.444–0.520 CE and 2.3–2.8 accuracy pointsTables 4, 23
+ graph-specific step sizegap 0.002–0.010 CETable 4
Same tuned settingmatched-delay contrasts vary by 0.034–0.086 CE across 120 support orders; predicted with Spearman 0.938–0.996Table 3
Output calibrationall 12 signs kept; 92.1–94.0% of raw magnitude removed; accuracy unchangedApp. A.16, A.18
Operator meta-trained under common-origin readsall 3 contrasts positive: 0.0097, 0.0159, 0.0114 CE (Holm p ≤ 0.003)App. A.24
Identical update mapsmatched-delay difference reduced by 80–90%App. A.25

From a practical standpoint, tuning sets how much stale reads cost on average, while the graph determines where that cost lands; once the step size is fixed, the graph is the only lever that remains. This leads to two practical rules: re-tune the step size whenever the read schedule changes, and select the graph where re-tuning is not possible.

We would like to thank you again; your questions on cost and reliability shaped two of the main additions in the revision. We hope that these answers address the concerns behind your current score, and if so, we would be grateful if you would consider updating it. We remain happy to clarify any further points.

Comments on the paper

3 comments
AuthorsOpenReview ↗

General response (part 1 of 2)

We would like to thank all reviewers for their careful and constructive reviews. We are glad that the reviewers agree that the matched-delay design isolates the effect of read placement, that the affine analysis explains why this effect arises, and that the predictor adds real information in the main setting. The reviewers also raised three shared questions: whether placement still matters after tuning, whether prediction can be cheaper than running every graph, and when the predictor can be trusted. We would like to use this general response to address these questions.

Read placement matters because different updates apply different update maps.

Schedules with the same updates, order, data and aggregate delay statistics can still reach different endpoints, and the revision shows that this is mainly because different updates apply different update maps. The affine analysis makes this precise: if every update shares one affine map, schedules with equal delay statistics reach the same endpoint, and once the maps differ, they no longer do. Delay statistics record how many reads are stale and how stale they are, but not which updates receive them, so they cannot reflect these differences. We have tested this explanation directly with new controls. Making the update maps identical removes most of the effect, and restoring them step by step brings it back. A second-order analysis further shows exactly which part of the effect a delay summary can capture.

Read placement remains measurable and predictable after tuning.

We agree with the reviewers that tuning removes most of the average gap between fresh and fully batched (common-origin) reads. The revision explains why: the operator's step size was meta-learned for sequential reads, and at that step size batched reads even end worse than not adapting at all. Once each graph receives its own step size, this mismatch disappears and the average gap nearly closes. Read placement, however, still matters after this tuning. Schedules with identical delay statistics continue to reach different endpoints, these differences survive output calibration and an operator meta-trained under batched reads, and the predictor ranks them almost perfectly.

In practice, this leads to two simple rules. If the step size can be re-tuned, it should be re-tuned whenever the read schedule changes. If it cannot, for instance because a meta-learned step size is fixed for deployment, the graph itself should be chosen, and support-only selection yields clear gains in this case. We believe the second situation is common, since meta-learned and test-time adaptation procedures usually ship with a single fixed step size.

Complete graph families can now be predicted accurately and much faster than they can be run.

Following the questions of aA49 and omee, we now compute the predictor's defects and transports once per reference trajectory rather than once per graph. The predictions are bitwise identical, and predicting all graphs in a family now takes a fraction of the time needed to run them, with the advantage growing as the family gets larger. In a new pre-registered evaluation on all 2,048 graphs of the K=12 family, with every graph executed for ground truth, the cached predictions rank the graphs with median Spearman 0.55, against 0.31 for local defects, and transport improves on local defects at every checkpoint (+0.21 [0.16, 0.25]). The reason for the speed is that all graphs in a contiguous family reuse the same small set of stale reads, so the expensive quantities are shared and only their combination differs from one graph to the next. This makes the predictor most useful exactly where execution is most expensive: before a sequential adaptation loop is turned into a batched or delayed one, a single Fresh run predicts the endpoint of every contiguous schedule, and the resulting shortlist contains the best graph far more often than chance.

Support-side diagnostics show when the predictor can be trusted.

The predictor works well in the supervised setting, and in CLIP-LoRA it ranks graphs well once the step size suits the regime (Appendix B.5, Table 44). On a new bank of 80 episodes across four datasets, a quarter of the calibrated step size (0.0075, fixed from an earlier pilot) raises the mean Spearman from 0.09 to 0.51 [0.42, 0.59], full transport beats local defects by +0.21 [0.12, 0.29], and the adapted model improves over no adaptation by 0.73 CE (77 of 80 episodes). At the calibrated 0.03, where parameter displacements are large, κ₀ placed all 800 episodes above the largest supervised value (pooled median 0.067), so the diagnostic identified that regime in advance. D_G tracks the recovery across episodes (Spearman −0.71) and needs only support data.

AuthorsOpenReview ↗

General response (part 2 of 2)

For reference, the key numbers behind this response are summarized below.

QuestionKey resultWhere
Why placement mattersidentical update maps remove 80–90% of the matched-delay differenceApp. A.25, A.26, B.9
Fresh–batched gap after per-graph step size + full-support init0.002–0.010 CE (batched reads are worse than no adaptation at the native step size)Tables 4, 23
Matched-delay contrasts in the same tuned settingvary by 0.034–0.086 CE across support orders; predicted with Spearman 0.938–0.996Table 3
Output calibration; operator re-trained for common-origin readsevery sign kept (92.1–94.0% of raw magnitude removed); all 3 contrasts stay positiveApp. A.18, A.24
Support-only selection, fixed step size, vs. terminal-protected schedule+0.039 to +0.055 CE at K=5; +0.157 to +0.219 at K=8Table 16
Ranking support orders, main settingSpearman 0.722–0.772 vs. 0.569–0.616 for local defectsSec. 6
Complete K=8 family (128 graphs)ranking +0.080 [0.067, 0.099] over local defects; 0.46 s (8.84 s before caching) vs. 3.14 s to runTable 40
Complete K=12 family (2,048 graphs)ranking 0.55 vs. 0.31 for local defects (+0.21 [0.16, 0.25]); 1.27 s vs. 23.8 s, 18.0–19.3× faster in all six timed cellsTables 40, 41
Top-16 shortlist of 128 graphs (offline)contains the best graph in 49.6% of episodes (12.5% by chance); median regret 0.0003 CEApp. B.6
Ranking tasks by graph sensitivity (offline)local defects, Spearman 0.935–0.948App. B.6
CLIP-LoRA, new bank (80 episodes)step size 0.03 → 0.0075: Spearman 0.09 → 0.51, full transport +0.21 over local defects, CE gain over no adaptation −2.60 → +0.73App. B.5, Table 44
When to trust the predictora κ₀ threshold (post hoc) flags 17–20% of supervised episodes, with 3.2–3.5× the error; at the calibrated step size it flags all 800 CLIP-LoRA episodes (pooled median 0.067)App. A.22

To summarize, the revision shows that read placement matters because different updates apply different update maps, that it remains measurable and predictable after tuning, that a complete graph family can now be predicted accurately and much faster than it can be run, and that support-side diagnostics indicate when these predictions can be trusted. We believe these additions have made the paper clearer and stronger, and we would like to thank the reviewers again for the questions that prompted them. We look forward to the discussion.

AuthorsOpenReview ↗

Summary of Contributions and Practical Significance

Dear Area Chair and Reviewers,

Thank you for the constructive discussion. We would like to highlight the broader significance of our findings and the new evidence that parameter-state evaluation graphs can improve learning procedures in practice.

A new design dimension for learning algorithms. When an update is computed, which historical parameter state should it read? This choice is usually implicit in how an algorithm is executed. We show that it matters independently of the update data, order, and aggregate delay statistics. Assigning the same delays to different updates can lead to different final models. Our affine analysis and controlled experiments explain how heterogeneous updates create these differences. Thus, parameter-state read assignments are not merely an implementation detail. They are a meaningful part of the learning procedure that we can study and deliberately design.

Making this choice computationally actionable. We predict the outcomes of alternative evaluation graphs from a single sequential reference trajectory, rather than executing every schedule. Sharing computations across 2,048 candidates yields an 18–19× speedup over independent per-graph execution. The framework also covers non-contiguous causal read schedules, while support-side reliability information helps guide prediction and selection. Evaluation graphs therefore offer a practical way to explore alternative update dependencies and identify promising learning schedules without executing every candidate.

Demonstrating improved adaptation, not just prediction. Our new frozen CLIP-LoRA confirmation evaluates two visual backbones across four datasets, with 50 held-out episodes per setting (400 backbone–episode evaluations; Section 8 and Appendix A.28). Using only support-validation data, our JVP-free cached predictor with one exact suffix verification reduces held-out query cross-entropy by 0.107 on ViT-B/16 and 0.222 on ViT-B/32 relative to development-selected fixed schedules, with paired 95% confidence intervals excluding zero. It also outperforms fixed Fresh and five-graph exact search in both four-dataset aggregates. Query accuracy improves from 76.3% to 77.4% and from 69.9% to 71.6%, respectively. Direct GPU measurements further establish 1.64× and 1.53× warm-time speedups over optimized, shared-prefix exact selection of all 16 schedules. These results show that prediction-guided read-state scheduling can deliver better adaptation outcomes while making graph selection more computationally efficient.

Where this perspective can lead. The immediate application is parameter-efficient adaptation of pretrained models, where every update matters and computational budgets are limited. Beyond this setting, our findings suggest opportunities in online and staged adaptation, where data arrives in batches, and asynchronous or distributed learning, where updates naturally read different parameter versions. Rather than only asking how to tolerate stale reads, we can begin asking which parameter-state dependencies should be chosen to improve learning.

Our central message is that parameter-state reads can be analyzed, predicted, and actively optimized as part of the learning procedure, rather than accepted as a fixed consequence of execution. By connecting structural analysis with counterfactual prediction and confirmed adaptation gains, we hope to establish a foundation for exploring this design dimension in a broader range of learning algorithms.

We are excited by the opportunities this perspective opens for more effective and computation-efficient learning. We look forward to sharing these findings and exploring their implications with the ICLR community. Thank you for your thoughtful consideration of our revised work.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.