acceptodds
Under review as a conference paper at ICLR 2027

Retention Geometry: Where the Evidence Sits Decides How KV-Cache Compressors Rank

Abstract

KV-cache compression methods are compared by one accuracy number per benchmark. That number cannot identify how two methods rank once their position-resolved accuracies cross, and the deployed compressors make crossings common: at a matched budget, what a method keeps, and so whether the model answers, depends on where in the context the evidence sits. We formalise this with a method's evidence retention profile and a benchmark's evidence-position prior : a reported pairwise comparison has the sign of for the depth-resolved accuracy contrast , and window templates and accumulated attention have profiles that cross the random-eviction null's by construction. On a controlled grid (three models, 8K–32K, ten presses, six matched budgets, up to 21 depths paired within each item, two deployment protocols; 692,960 scored answers), the contrast between published methods changes sign with depth in 1–8 of 15 pairs in each harder-task cell under query-aware compression, certified by a bootstrap band corrected over depths and pairs; the count holds when the model's own greedy output is scored instead of teacher-forced tokens, though most reversals involve the first or last depth. A monotone link from predicts a held-out method's position-resolved accuracy at 0.47–0.77, against 0.41–0.58 for depth-averaged retention, an advantage carried by the window templates under query-aware compression and shared by most methods under query-agnostic compression. On natural documents scored by RULER's contains-match, 160 items certify 2 published pairs, only at the largest budget, and 7 under query-agnostic compression; RULER's own 996 QA rows, where depth is observed rather than paired, certify none, and re-weighting the grid by a task's measured prior does not forecast that task's ranking: the result is non-identifiability, not a forecast. An audit of 20,081 benchmark items puts the mean first-occurrence depth of 12 localisable tasks between 0.20 and 0.53, and finds one sub-task whose mean moves by 0.44 across RULER's releases. We recommend depth-resolved reporting and release a one-prefill retention probe. All code and every scored record are in the supplementary material and will be made public at https://github.com/xxx/xxx upon acceptance.

Primary area:
foundation or frontier models, including LLMs
Keywords:
kv-cache compression, long-context evaluation, retention operators, benchmark design, evidence position, method ranking, llm inference

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_csquOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

This paper studies how evidence position affects the evaluation of KV-cache compression methods. It introduces evidence retention profiles and evidence-position priors to explain why aggregate rankings can change when methods have crossing position-resolved accuracy curves. The authors evaluate this framework using controlled retrieval tasks, experiments constructed from natural documents, and original benchmark examples. They also audit evidence positions in existing benchmarks and recommend depth-resolved reporting and a retention probe.

Critical strengths

Overall, the paper identifies a useful evaluation concern and investigates it with substantial experimental effort. Details are as follows:

1.Relevant observation about aggregate rankings. The distinction between a method’s position-resolved performance and its benchmark-averaged score is useful.

2.Careful controlled comparisons. The within-item depth comparisons, materialized matched cache budgets, and separate query-aware and query-agnostic protocols help isolate the factors under study. The free-generation checks also provide evidence that the observed reversals are not solely artifacts of teacher-forced scoring.

3.Transparent reporting of limitations. The paper reports unsuccessful transfer to benchmark rankings, failures of the retention model, and the concentration of reversals at boundary positions. These negative results make the scope of the findings more assessable.

Critical weaknesses

Overall, my main concern is that the paper establishes the possibility of position-dependent rankings more convincingly than it establishes their practical importance or the added value of the proposed framework.

  1. Limited evidence of consequential ranking instability on existing benchmarks. Section 5 reports no certified reversals among the published methods on the 996 original RULER QA examples or the 593 located LongBench examples under their respective benchmark metrics. On the controlled natural-document experiment, query-aware compression certifies only two published pairs, both at the largest budget; the stronger query-agnostic result certifies seven pairs there. Moreover, reweighting the synthetic grid by measured task priors does not reliably improve prediction of the actual task rankings. I agree that the unpaired benchmark data have confounding and power limitations, so these findings do not disprove the phenomenon. However, they leave its practical impact on existing benchmark comparisons insufficiently established. The paper supports a caution about interpreting aggregate scores, but provides weaker evidence that this caution materially changes conclusions in realistic evaluations.

  2. Much of the query-aware effect is concentrated in predictable window-boundary behavior. Appendix X.8 reports certified reversals in 26.1% of observations involving a window-template method, compared with 1.5% for content-versus-content pairs under query-aware compression. Most template certifications involve the final depth, and no certified content-versus-content reversal survives removing both endpoints. This is consistent with the proposed mechanism, but much of the strongest evidence reflects the expected fact that a recent-window policy retains tail evidence and discards interior evidence. The broader query-agnostic results are valuable, but the paper does not sufficiently establish how often the phenomenon changes a practically relevant choice between competitive methods. Consistently, the audited task priors rarely change the query-aware winner.

  3. The formal framework adds limited explanatory power beyond its assumptions. Proposition 1 follows directly from expressing benchmark performance as a weighted average, while Proposition 2 obtains the correspondence between retention and accuracy rankings by assuming a shared monotone availability function and shared answering regimes. These statements organize the observation, but do not themselves establish that the assumptions describe real compressed models. Section 4.4 demonstrates a failure of the shared-floor assumption, and Appendix X.6 shows that the query-aware predictive advantage over depth-averaged retention is driven by window templates, with press-level intervals including zero in all four harder-task cells. The paper should more clearly separate mathematical bookkeeping, conditional predictions, and empirically established mechanisms. The current density of definitions and propositions makes the conceptual contribution appear broader than the demonstrated explanatory gain.

  4. The practical advantage of the proposed diagnostic remains unclear. Depth-resolved reporting is sensible, but the retention probe’s additional value over a small direct evaluation is less convincing. Appendix X.11 reports that one labeled item evaluated across methods, budgets, and depths predicts the target accuracy surface better than the retention link, although that comparison is partly in-sample and requires more scoring. The probe also requires known evidence positions, while its accuracy link is fitted using scored data from other methods. Given the unsuccessful transfer to natural-task rankings, it remains unclear when the probe provides a sufficiently reliable and economical basis for a concrete evaluation or deployment decision.

Questions for authors
  1. Practical significance: Given the absence of certified reversals on the original RULER and LongBench examples, what is the strongest supported conclusion about existing benchmark rankings? Using the current results, can the authors identify a practically meaningful method-selection conclusion that changes after accounting for evidence position, distinguishing actual benchmark measurements from reweighted synthetic results?

  2. Scope beyond boundary effects: Could the authors consolidate the existing endpoint-removal and method-family analyses into a main-text summary, separately for the two protocols? In particular, what practically meaningful reversals remain between competitive content-driven methods, and how much probability mass do the audited benchmark distributions assign to the depths responsible for them?

  3. Added value of the formalization: Which result provides explanatory or predictive content beyond the weighted-average identity and the known retention pattern of window policies? How should readers determine whether the shared-link assumptions are adequate in a new setting, especially when retained representations can carry information from evicted evidence?

  4. Use case for the probe: Under what concrete conditions should a practitioner use the retention probe instead of directly evaluating a small labeled set? Could the authors clarify the required annotations, fitting data, computational costs, and reliability of the resulting decisions, taking the negative results in Appendices X.3 and X.11 into account?

Reviewer_1vJrOpenReview ↗
Rating
3
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper argues that single-scalar benchmark evaluations of KV-cache eviction methods ("presses") suffer from a fundamental non-identifiability problem: each press mm at budget BB induces a position-dependent evidence retention profile ρm(p;B)\rho_m(p; B) (the expected fraction of gold evidence tokens EE retained when EE sits at relative context depth p∈[0,1]p \in [0, 1]), while each benchmark induces an unstated evidence-position prior D(p)D(p).

The authors formalize this measurement framework through three propositions:

  1. Non-Identifiability & Prior-Invariant Summaries (Proposition 1, Corollary 1): For two presses with depth-resolved accuracy contrast δ(p)=am1(p;B)−am2(p;B)\delta(p) = a_{m_1}(p; B) - a_{m_2}(p; B), the benchmark contrast Am1(D)−Am2(D)=∫δ(p) dD(p)A_{m_1}(D) - A_{m_2}(D) = \int \delta(p)\, dD(p) spans the Ranking-Instability Interval RII(m1,m2;B)=[inf⁡pδ,sup⁡pδ]\mathrm{RII}(m_1, m_2; B) = [\inf_p \delta, \sup_p \delta]. Whenever 0∈int(RII)0 \in \mathrm{int}(\mathrm{RII}), there exist priors DD that rank the pair either way. The authors propose reporting RII\mathrm{RII}, the worst-depth score Wm=min⁡pam(p)W_m = \min_p a_m(p), and the lead fraction Φ(m1,m2)=∣{p:δ(p)>0}∣/∣P∣\Phi(m_1, m_2) = |\{p : \delta(p) > 0\}|/|\mathcal{P}|.
  2. Retention Mediation (Assumption 1, Proposition 2): Under a two-regime model am(p;B)=β+(α(p)−β)g(ρm(p;B))a_m(p; B) = \beta + (\alpha(p) - \beta)g(\rho_m(p; B)) with shared floor β\beta, ceiling α(p)\alpha(p), and monotone link gg, per-depth accuracy rankings reverse only where retention profiles ρm(p;B)\rho_m(p; B) cross.
  3. Structural Positional Priors (Proposition 3, Corollary 2, Proposition 4): Under a uniform/exchangeable attention null, accumulated attention scores decay harmonically (ci=HT−Hi≈ln⁡(T/i)c_i = H_T - H_i \approx \ln(T/i), early-biased), window templates form step functions with an interior hole (ρ=0\rho = 0 on [s,T−(B−s))[s, T-(B-s)) and 11 on the tail), and random eviction is flat (ρrand≡B/T\rho_{\mathrm{rand}} \equiv B/T), forcing structural crossings between press families.

The authors test this framework on a large controlled multi-key retrieval grid (K = 11 or 21 needles paired within each haystack prefill across 3 models, 8K-32K lengths, 10 presses, 6 materialized budgets B in [64, 2048], and 2 deployment protocols: query-aware P-late vs. query-agnostic P-early, totaling 692,960 teacher-forced answers plus greedy-decoding and natural-SQuAD replications), run verbatim evaluations on RULER (996 rows) and LongBench (593 rows), and audit gold-evidence positions across 20,081 items in 15 benchmark tasks.

Critical strengths
  1. Paired Within-Item Experimental Design and Transparent Reporting of Negative Control Outcomes: The empirical design is carefully controlled:

    • By embedding K = 11 (or 21) needles at controlled depths within the same haystack and querying them from a shared uncompressed prefill (while checking in Appendix G that K = 1 unpaired haystacks yield similar patterns), cross-depth and cross-press contrasts are paired within-item.
    • Budgets are physically materialized (gather of B(l) entries per layer and KV head) rather than attention-masked, and checked by a 73-check test suite.
    • The authors also run 48 control experiments and report all 18 negative or qualifying outcomes in Table 3 and Appendix X (including cross-GPU level shifts in Appendices N and W.5 and the failure of prior re-weighting to forecast real benchmarks in Appendix X.3).
  2. Empirical Audit of Evidence Placement in Long-Context Benchmarks and Protocol Separation (P-late vs. P-early): The audit of 20,081 items across 15 benchmark tasks (Section 6, Figure 2a, Table 6, Appendix U) is a useful diagnostic resource. Showing that localizable tasks have mean first-occurrence depths ranging from 0.20 to 0.53, that RULER's qa-1 mean depth swings by 0.44 across its own 4K (0.72), 8K (0.28), and 16K (0.50) releases due to generator slotting, and that conflating query-aware (P-late) with query-agnostic (P-early) protocols shifts rho(m, p; B) and re-orders leaders (Table 10, Figure 12) helps clarify why different evaluation setups favor different heuristics.

Critical weaknesses
  1. Under Query-Aware Compression (P-late), Certified Reversals Are Dominated by Trivial Boundary Effects (p = 1 Recency Window vs. Interior) and Rarely Affect Content-Driven Scorers or Audited Task Winners:

    • In the standard query-aware protocol (P-late)—the actual setting for which SnapKV, PyramidKV, and TOVA were designed—the headline claim that "the contrast between published methods changes sign with depth in 1-8 of 15 pairs" is overwhelmingly driven by comparing recency-window templates (StreamingLLM and H2O, which hard-allocates 50% of its budget to the most recent tokens) against content-driven scorers at the final grid endpoint p = 1.
    • Specifically, Appendix X.8 (lines 2533-2550) and Table 2 (fw int.) show that under P-late:
      1. Pairs involving a window template account for 26.1% (127/486) of family-wise certifications, whereas pairs of content-driven presses (SnapKV, PyramidKV, TOVA, KeyNorm) certify in only 1.5% (5/324) of observations across all 9 primary cells.
      2. In Table 2 (fw int.), when the two grid endpoints p = 0 (the 4 sink tokens) and p = 1 (the recent window tail) are excluded, the number of certified reversals in the primary task-H cells under P-late is 0 at every single budget except the largest (B = 2048).
      3. Withholding p = 0 alone leaves 0 out of 5 content-vs-content certifications under P-late (line 2545).
    • That StreamingLLM/H2O retain 100% of a needle placed inside the final B tokens (p = 1) and 0% in the middle (p in [0.1, 0.8]), whereas query-anchored methods retrieve from the middle, is already well understood by practitioners. Moreover, when H1 is re-weighted by the empirical priors of the 12 audited benchmark tasks under P-late (Table 10), SnapKV or TOVA wins 12 out of 12 tasks at every budget (and on the 996 verbatim RULER QA rows and 593 LongBench QA rows, 0 published pairs are certified under their native metrics).
  2. Missing the Role of Competitor Density and Head-Specific Retrieval Structure Explains Why Depth Re-Weighting Fails to Forecast Real Benchmarks:

    • Why depth-prior re-weighting fails on real tasks: In Section 5 (lines 404-408), Appendix K.1, and Appendix X.3, re-weighting the controlled grid by a task's measured depth prior D-hat performs worse than unweighted uniform predictions under P-late (Delta-tau = -0.18 on RULER's 996 QA rows and -0.16 on LongBench's 593 QA rows), and the isotonic link g fitted on H1 fails to transfer to the 160-item SQuAD cell (R^2 = 0.32 under P-late and -4.16 under P-early, line 1702). Theoretically, under top-B eviction, an evidence span E survives iff the rank of its weakest required token is <= B, which depends on the number of competing distractor tokens C(L) that outscore E and evidence redundancy, not position p alone. Natural documents have heterogeneous competitor densities and multi-span cues that a 1D positional prior D(p) cannot represent.
    • Uniform head/layer averaging in Definition 1: Definition 1 defines rho(m, p; B) as a uniform average across all LxH (layer, KV-head) pairs. Because long-context retrieval is performed by a small subset of retrieval heads while most heads act as streaming or local heads, uniform averaging conflates retention in non-retrieval heads with retention in retrieval heads. Indeed, Appendix X.5 demonstrates that weighting heads by their uncompressed attention on E raises mean R^2 from 0.77 to 0.92 and fixes the worst mispredictions on H2O-acc (0.13 to 0.72) and KeyNorm (0.25 to 0.83), while Appendix X.11 shows that decoding just 1 single labelled item (R^2 = 0.88) beats the unweighted retention probe (R^2 = 0.77).
    • Dense, telegraphic prose in the main text: While the 51-page document is packed with valuable data, the 9-page main body is written in an overly compressed style with dozens of parenthetical statistics and constant pointers to 24 separate appendices (Appendices A-X), requiring substantial effort to piece together without constantly flipping between the main text and appendices.
Questions for authors

Clarification Requests

  1. Interior Reversals Among Content-Driven Scorers Under Plate\mathsf{P}_{\mathrm{late}}: In Appendix X.8 (line 2545), you note that under Plate\mathsf{P}_{\mathrm{late}} there are only 5 content-vs-content certifications out of 324 observations across the nine primary cells, and that withholding p=0p = 0 leaves 0 content-vs-content certifications. Does this mean that across all models, context lengths, and budgets, content-driven query-aware methods (SnapKV, PyramidKV, TOVA, KeyNorm) never exhibit a statistically certified ranking reversal across interior depths p∈(0,1)p \in (0, 1) under query-aware compression?
  2. Promoting Attention-Weighted Head Aggregation from Appendix X.5 to Definition 1: Given that weighting ρm\rho_m by each head's uncompressed attention mass on EE (Appendix X.5) requires no extra prefill, remains completely decode-free and label-free, improves leave-one-press-out R2R^2 from 0.770.77 to 0.920.92, and resolves the link failures on H2O-acc and KeyNorm, why keep the uniform head average in Definition 1 and Figure 11 rather than adopting the head-weighted retention profile as the primary definition?
  3. Streamlining Presentation: Could the main text be made more self-contained by moving the key breakdown of template-vs-content reversals and interior-only counts (fw int. from Table 2 and Appendix X.8) directly into Section 4.2, while pruning some of the secondary parenthetical numbers that currently require jumping to Appendices K–X?

Suggestions for Future Work

  1. Joint Position-and-Competitor Retention Profiles: Extending the retention profile ρm(p,c;B)\rho_m(p, c; B) to condition on both relative depth pp and local competitor score density cc (the number of non-evidence tokens exceeding the evidence span's score threshold) would bridge the gap between homogeneous synthetic haystacks and heterogeneous natural QA benchmarks where prior re-weighting currently fails.
Reviewer_QitTOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This work highlights a genuine yet often overlooked issue in the current evaluation of KV-cache compression: the specific location within a long context where the evidence required for the correct answer resides. The experimental design controls for "evidence depth" within individual items, covering a dataset of 20,081 real-world benchmark items.

Critical strengths
  1. The premise of this work is excellent and intriguing. Many papers tend to collapse depth-dependent results into a single scalar value, overlooking the nuances of position.
  2. The experimental design and validation approach are particular highlights. By embedding multiple sets of evidence within the same "haystack" and placing them at 11 or 21 distinct depths, the authors enable paired comparisons for the same item across different depths. This effectively eliminates the confounding factor where questions at the beginning of a context might inherently differ in difficulty from those at the end.
Critical weaknesses
  1. While the core contribution—fairly evaluating KV-cache compressors—is compelling, the writing in certain sections is excessively verbose and the paragraph structure is poor, particularly in Chapter 4.
  2. The claim that "evidence depth can alter rankings" has been well validated; however, the extent to which it actually changes final rankings in real-world benchmarks has not been demonstrated with equal strength. In fact, regarding the 15 published pairs on the original RULER rows, the aggregate performance of 13–14 pairs is clearly distinguishable; yet, there is no evidence showing that their relative superiority/inferiority flips based on evidence depth. The strongest evidence comes from the authors' reconstructed controlled benchmark, rather than the existing benchmarks themselves.
  3. In Appendix W.4, when considering only the first answer token—a position that cannot possibly benefit from the teacher-forced gold prefix—the number of reversals for Pearly remains largely unchanged, whereas for Plate, it drops from 84 to 14. This suggests that, beyond the evidence itself, other factors are at play, such as information remaining in the query window after the evidence has been processed, or teacher forcing providing an answer prefix for subsequent tokens.
  4. \pho calculates a uniform average of evidence retention across all layers and KV heads. However, different heads are not necessarily of equal importance. Furthermore, the distribution of evidence in real-world workloads is not fixed.
Questions for authors

Overall, while the paper starts from a promising premise and addresses an interesting problem, its specific theoretical and methodological contributions are relatively simple, and its level of innovation seems insufficient. Specific questions can be found in the above weaknesses.

Comments on the paper

5 comments

Dear Authors, Thank you for the detailed response and the additional Lost-in-the-Middle experiments. I appreciate the clear characterization of the positional effect and the transparent reporting of both positive and negative results.

The new Lost-in-the-Middle results demonstrate significant winner switches between extreme first and last placements on paired real QA data, whereas the original unpaired RULER QA and LongBench rows certify zero reversals. However, I remain concerned about the query-aware setting, where significant winner switches no longer hold under soft placements (0/4 budgets). Specifically, I still have two concerns (given the limited remaining discussion time, no additional experiments are needed, and a brief discussion based on your existing findings is sufficient):

Practical effect size and possible mechanisms: Under query-aware compression, does the lack of significant switches under soft placements (and unpaired RULER/LongBench) reflect insufficient statistical power, or does it suggest that the practical impact on rankings becomes limited away from extreme endpoints? Could you also briefly discuss the possible mechanisms explaining why this occurs in the query-aware setting while query-agnostic compression still shows significant switches under soft placements?

Concrete guidance for practical evaluation: How should practitioners and benchmark designers apply your framework in practice? Specifically, should future evaluation sets adopt paired multi-slot layouts, and how should average accuracy be combined with worst-depth metrics ( WmW_m ) when making concrete selection decisions?

If you can clearly address these two points, I will be happy to re-evaluate my score.

Dear Reviewers,

The authors have provided their rebuttal, but no follow-up comments have been posted yet. As the author-reviewer discussion period is ending soon, please review and acknowledge the rebuttal, and engage in further discussion if any concerns remain unresolved.

AC

Thank you. We agree that the query-aware soft-placement results narrow the practical claim. The interpretation below uses the existing records only, and App. X.15 of the revised PDF now states it in the same terms.

1. Effect size, power, and mechanism. For the two tested models and the specified geometric priors, the endpoint effect is substantially attenuated. Qwen's point-estimate winner is unchanged at all four budgets. For Llama at B=128–512, StreamingLLM's back-loaded advantage is only 1.4–2.5 percentage points, and the adjusted intervals cross zero, with upper limits of 4.3–5.3 points. A reliable query-aware winner switch is therefore not established under these priors, although benefits of a few points remain possible. We do not attribute this result solely to insufficient power.

The slot curves suggest why. For Qwen at B=256, SnapKV scores 0.42–0.60 across slots, whereas StreamingLLM scores 0.25–0.27 everywhere except the last slot, where it reaches 0.68. This is consistent with query-aware scoring retaining useful evidence across positions, while the recent window's advantage is concentrated at the endpoint and is diluted when the placement spreads to other slots.

Under query-agnostic compression, the keep set cannot use the downstream question. The scoring rules remain content-dependent, but the measured profiles show stronger front and tail biases, without the broad interior advantage of the query-aware content scorers. H2O's front advantage and the competing methods' tail advantage remain large enough for significant soft-placement switches at B=64 and 128 in both models. At B=128, for example, H2O leads StreamingLLM under front-loading by 12.3 points for Qwen and 11.9 for Llama, while StreamingLLM leads under back-loading by 8.0 and 5.0 points. At larger budgets H2O's deficit at the last slot shrinks (Qwen: 16 points at B=128, 7 at B=256), and these switches are no longer significant.

The unpaired RULER and LongBench results cannot resolve the power-versus-impact question. Sparse tail coverage in RULER (38 of 996 rows at the largest budget) further limits inference, but it does not establish that the measured rankings would change with more power.

2. Practical evaluation and selection. For benchmark designers: yes. Where relocating the evidence preserves the task, use paired layouts that contain both endpoints and interior positions, with enough resolution near retention boundaries. Report per-slot accuracy with paired uncertainty, alongside the average under a declared placement distribution, the worst tested-slot score W_m, and the compression protocol and budget. Our seven-slot experiment is an example, not a universal sampling prescription.

For practitioners: measure these curves on representative workload data, with the deployed model, protocol and budget, and estimate the deployment's placement distribution D using the same position definition. Then A_m(D) is the relevant expected-accuracy criterion. Estimating D alone does not justify transferring a synthetic or unrelated task's accuracy curves; that is the transfer our re-weighting results do not support.

W_m serves a different, explicit objective. Over arbitrary placements on the tested grid, the minimum of A_m(D) equals W_m, so maximising W_m is the worst-case choice. If a minimum performance at every tested position is required, select the highest-average method among those meeting a pre-specified W_m threshold. If only a restricted range of placements is plausible, evaluate A_m over that range rather than switching automatically to the largest W_m. As a quick sensitivity check, App. X.15 also tabulates the last-slot share at which two presses tie when the remaining mass is spread evenly.

For example, for Qwen at B=256 under query-aware compression, SnapKV is ahead of StreamingLLM in both uniform-average accuracy (0.47 vs 0.32) and worst-slot accuracy (0.42 vs 0.25). StreamingLLM would need 59% of the evidence on the last slot, with the rest spread evenly, to tie. This supports a concrete choice for that evaluated setting, without claiming a universal deployment winner.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.