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Withdrawn from ICLR 2027

MemReq: Contract-Conditional Requirement Profiles for Diagnosing Agent Memory Failures

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

End-to-end memory scores do not identify whether a named operation was exercised, its prerequisite state was retained, or evidence reached the Reader. We introduce MemReq, an offline diagnostic protocol that freezes the workload, information, Reader, resource, and scoring contract; contrasts executed operations; probes prerequisites; audits frozen-state evidence; and tests a bounded, gold-free intervention. Its requirement profiles are empirical and contract-conditional, not workload-intrinsic necessities. On 58 shared multi-hop questions with byte-identical contexts and matched 16,384-token completion caps, Qwen35 and GPT-OSS-120B yield V×C interactions of +27.59 and −5.17 percentage points, respectively. Reader identity and reasoning settings both differ, so this is not a model-only causal effect. In a crossed Mem0-RV diagnostic, 62/64 instances with a valid update opportunity reach latest-only state: apparent version failure can originate before replacement is possible. On frozen stores, version filtering improves Additive and A-MEM under dense and graph readout but leaves RV near zero; RV’s tested graph contexts do not change under filtering. The graph intervention does not reproduce its 6k gain on the official 32k-history configuration, where query anchoring limits delivery. MemReq therefore localizes observable failures without inferring unexercised primitives or universal architecture rankings.

Primary area:
datasets and benchmarks
Keywords:
LLM Agents, Agent Memory, Long-Term Memory, Memory Evaluation, Diagnostic Evaluation, Memory Retrieval, Version Resolution, Structured Composition

Reviews

Among:
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1234this paper, Bottom 1%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.00 over 3 reviews, above 0% of the others.
Reviewer_VZoDOpenReview ↗
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1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

The paper proposes a method for analyzing where memory system errors occur when evaluating on existing memory benchmarks. The work begins by proposing a formal definition of "sufficiency," a measurement of which memory operations are actually needed to solve a task. It then proposes a mechanism where one can hold everything fixed and ablate only individual memory operations in order to attribute credit. Specifically, the authors propose a mechanism where instead of providing the retrieved memories to the answer agent, the framework builds a graph over the memories, clustered by subject/predicate, and uses this as context. If the answer agent is able to get this right, the error can be attributed to a retrieval failure, otherwise it can be attributed to a write failure. The results on MemoryAgentBench show that different memory systems exhibit different failure modes; some fail to extract the facts in the first place, while some fail to retrieve them later on.

Critical strengths

None

Critical weaknesses
  • The paper is extremely difficult to read; many terms and variables are frequently introduced without being defined or explained, making the method and contribution hard to follow. The empirical results and metrics are also disorganized and scattered throughout the paper in long paragraphs, rather than being organized into charts or tables, which makes them difficult to compare and understand. It is also unclear how the formal definition of sufficiency (a measurement of the minimal number of operations needed to answer a question) in Equation 1 is used empirically or what the high-level motivation for this formalism is.
  • The novelty of the work is unclear; the paper does not clearly position itself against prior works nor provide sufficient motivation for its high level ideas and algorithms. It's unclear how the V/C transform algorithm is different from existing works that dump memories into context to analyze the errors, nor how the broader implications of this paper for memory systems are different from prior works.
  • The method does not seem very general and only applies to particular types of memory benchmarks; in particular the V/C transform groups memories by subject/predicate; the V step also removes all memories that are older than the most recent one for a given topic, which may not be desirable for all memory tasks.
Questions for authors
  1. How does the diagnosis from the V/C transform method differ from dumping the entire memory into the context of the agent? It seems that both would tell us whether or not the memory relevant to the query being answered exists in the memory bank
  2. Are there any broader implications of the results? Prior works have already established that different memory systems and models can exhibit different failure modes/behaviors, what new insights does this work provide?
  3. The paper states in Section 8 that "earlier split-epoch estimate attenuates in the complete replication (11/58 changed arm outcomes; 8.62 pp interaction shift)" which I interpret as meaning 11/58 outcomes changed between identical runs. Could the authors provide confidence intervals or quantify the run-to-run variance? With almost 20% of the decisions flipping from run-to-run, it is currently difficult to trust that any of the single-seed results are statistically significant.
2 comments
AuthorsOpenReview ↗

Clarifications on Failure Attribution, Dump-All Controls, Novelty, Generality, and Run Variability

We thank the reviewer for the detailed assessment. We revised the explanation of MemReq and added Dump-All controls, cross-history tests, human evidence audits, and repeated-run measurements.

1. Attribution and Dump-All (Q1). MemReq does not label every failed transformed answer as a write failure, or every successful one as a retrieval failure. It examines Store, Graph, and Reader Context evidence; V/C transforms test the response to changing readout, with UNKNOWN retained when support cannot be established.

Direct native-Store Dump-All controls are now in Appendix X (Tables 47–49). On the original MAB Stores, Qwen9 scores 5/58 with the full A-MEM dump versus 47/58 with Strict-V+C; for Additive, 5/58 versus 39/58. On five shorter histories, Full Dump versus V-dense scores 39/60 versus 52/60 (Additive), 50/60 versus 58/60 (A-MEM), and 55/60 versus 53/60 (RV-generic). Thus neither readout is universally better; lengths also differ.

The audit identifies a more specific boundary: 60/60 Stores and 45/60 Graphs contain complete support, but only 4/60 original Graph Contexts do. A gold-free intervention, frozen before five additional histories, raises complete Context support from 16/60 to 48/60 and accuracy from 12/60 under the original strict Graph readout to 47/60 (Table 4). Random seeding scores 33/60; V-dense remains higher at 52/60, with 37/60 seeded Contexts byte-identical to V-dense. This tests evidence delivery, not Graph superiority.

2. Novelty and broader implications (Q2/W2). Version selection and graph traversal are not new operators. Related Work now discusses Reddy and Challaram (2026), the concurrent Contract Memory Compiler (Song et al., 2026), and HippoRAG. MemReq instead links controlled operation responses to prerequisite formation and observed Store-to-Context evidence loss. Across five histories, changing only RV's extraction prompt raises literal update opportunities from 1/60 to 58/60 and native-readout accuracy from 7/60 to 52/60. With fixed dense readout, version filtering helps Additive by 38.33 pp and A-MEM by 43.33 pp, but hardly changes the RV variants (Appendix T). Consequently, a poor conflict-resolution score alone cannot establish that an update primitive failed.

3. Scope of V/C (W3). Strict-V/C uses MAB surface grammar and visible ingestion order; it is not validated for arbitrary natural-language memories. Latest-only filtering can also discard history needed for past-state questions. GPT-OSS scores 56/56 on SH6k with either AllVersion or LatestGlobal (a ceiling-bound result), so V is a tested operation, not a universal default. The prospective histories contain only 48–56 facts each. Their evaluated questions and full source chains are new, but 18–20 fact instances and 9–10 of 12 distinct MH answer strings per history overlap prior MQuAKE-T panels (Table 38). This is same-family, not cross-domain, validation.

4. Run variability (Q3). The concern is supported. Across five GPT-OSS runs, 40/232 arm–query cells (17.2%) vary under server defaults; 24/232 (10.3%) vary under a separate temperature-zero/seed-request contract. Most GPT-OSS runs fail strict completeness. In contrast, only 1/232 cells (0.4%) varies across three Qwen9 runs, whose V×C interactions range from +32.76 to +34.48 pp (Appendix Y, Table 50). Primary cross-history and prospective findings use Qwen9. Single-run GPT-OSS estimates are descriptive; model identity and reasoning settings are not isolated.

5. Equation 1 and presentation (W1). Equation 1 defines point-estimate sufficiency relative to an empirical reference and tolerance, with an inclusion-minimal frontier only among tested configurations. On CrossEp-Emb/Qwen9, the prior matches the reference at 75/121; retrieval scores 68/121. At a 5 pp margin, only the prior meets the point-estimate criterion; this is not established paired non-inferiority. We acknowledge the presentation problems; we aligned RQ wording, clarified prior-work distinctions, and consolidated prospective results in Table 4.

We retain the negative result that Full MemReq did not improve repair selection over Store+Trace (488/555 versus 486/555). The supported contribution is stage-specific diagnosis and bounded intervention testing, not general repair-policy superiority.

We welcome further questions.

Locations: Sections 2–3 and 6–8; Table 4; Appendices S, T, V, W, X, Y.

Thank you for your additional experiments and clarifications. The author response seems to concede critical points such as a lack of novelty, significant run variability ("the concern is supported"), and that the method does not work over simpler alternatives ("Full MemReq did not improve repair selection over Store+Trace"); given these, I maintain my original score.

Reviewer_WTzqOpenReview ↗
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Paper summary

The paper talks about a protocol for offline diagnostics of an agentic system. It raises questions that revolve around diagnosing memory failures.

Critical strengths
  • The memory-failure question is an important one.
  • The assertion (part of originally stated RQ2) that before "blaming" an operation for a failure, the operation should be given an opportunity to execute is meaningful.
Critical weaknesses
  • Very difficult to read, inconsistent writing (e.g., research questions RQ1-RQ3 "evolve" and shift as the paper goes on).
  • It is unclear how empirical evidence maps to the research questions.
  • The core scientific contribution is unclear.
Questions for authors

What is a novel scientific conclusion beyond the empirical observation that memory failures may arise because prerequisite state was never formed or relevant evidence was not delivered to the Reader? What is the strongest result in the paper that supports that conclusion?

1 comment
AuthorsOpenReview ↗

Clarifying the Scientific Contribution and Its Empirical Support

We thank the reviewer for highlighting the unclear scientific contribution and the difficulty of connecting the research questions to the experimental evidence. We have clarified these connections and added cross-history validation and a prospective intervention test.

The clearest controlled finding is that an apparent failure of a named memory operation can be substantially explained by the prerequisite state formed upstream, rather than by the operation itself.

In the tested Mem0-RV configuration, changing only the extraction prompt increases observable old/current update opportunities from 1/60 to 58/60 across five new MQuAKE-T-derived histories. Among the 58 opportunity-present cases, 52 reach literal latest-only state. Native-readout multi-hop accuracy also increases from 7/60 to 52/60 (Table 41).

Only the extraction prompt changes; the writer model, updater, embedding service, and Reader contract remain unchanged. This identifies upstream extraction as a major bottleneck in the tested RV configuration. It does not establish that every subsequent update succeeds semantically.

A second finding is that the same version-filtering operation produces different responses depending on the evidence state retained by the system.

Under the same fixed parser and dense readout, the five-history results are:

RV-native: VD−ID = 0 pp.

RV-generic: VD−ID = +1.67 pp.

Additive: VD−ID = +38.33 pp [18.33, 56.67].

A-MEM: VD−ID = +43.33 pp [31.67, 53.33].

The prerequisite and Store audits help interpret this pattern (Sections 6–7; Appendix T). Native RV rarely forms an observable update opportunity. RV-generic has already resolved most observable old/current conflicts in the Store. Additive and A-MEM show larger benefits from query-time version filtering.

Thus, a low end-to-end conflict score or a near-zero filtering response does not, by itself, establish that a named memory operation is ineffective. Its prerequisite and retained-evidence conditions must first be examined.

A third result tests a specific evidence-delivery diagnosis.

In a development audit, 45/60 Graphs contained complete supporting evidence, but only 4/60 Reader Contexts did. We then froze a gold-free readout intervention before evaluating five additional histories. Relative to the original strict Graph readout, accuracy increased from 12/60 to 47/60, and complete Context support increased from 16/60 to 48/60 (Table 4). Random seeding achieved 33/60, while V-dense remained stronger at 52/60.

This supports a specific delivery diagnosis and intervention response, not a new or superior graph retrieval algorithm. The held-out histories remain within the same task family. Each history shares 18–20 fact instances and 9–10 of its 12 distinct MH answer strings with earlier MQuAKE-T panels (Table 38).

Presentation and organization

The RQ1–RQ3 statements in the Introduction now match those at the beginning of Sections 5–7. We have clarified the evidence associated with each question: Section 5 measures operation response, Section 6 examines prerequisite formation, and Section 7 studies frozen-state evidence and intervention response.

We also rewrote the abstract around the main quantitative findings, added an empirical example for Equation 1, clarified the relationship to prior work, and consolidated the prospective validation in Table 4. The original research questions and diagnostic framework remain unchanged.

Finally, the complete repair-selection policy did not outperform Store+Trace (488/555 versus 486/555). We therefore distinguish the demonstrated value of specific stage-level diagnoses from the unestablished value of the full workflow for automated repair selection.

The revised evidence supports a bounded scientific conclusion: an operation's observed response depends on the prerequisites and retained evidence available to it, and a diagnosed delivery bottleneck can be evaluated through a frozen intervention.

Revised manuscript: Sections 3 and 5–8, Table 4, and Appendices T–W.

We welcome further discussion or questions about this interpretation.

Reviewer_ruyPOpenReview ↗
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Paper summary

This paper proposes MemReq, a protocol for diagnosing agent memory failures under fixed evaluation settings. It combines controlled operation tests, prerequisite probes, frozen-store audits, and interventions without gold information. The main finding is that an apparent memory-operation failure may come from missing prerequisite state or poor evidence delivery. Experiments also show that intervention effects depend on the Reader and workload.

Critical strengths
  1. The paper shows that poor extraction can prevent an update opportunity from being created. Among 64 cases with a valid opportunity, 62 reach the latest-only state. This helps explain why a failed behavioral test does not necessarily mean that the update operation itself failed.

  2. Well-controlled frozen-store comparisons. The ID/VD/IG/VG comparisons make version-filtering effects easier to interpret under fixed readout policies. The paper also reports negative results, including unchanged RV graph contexts and failed transfer of the large gains to the 32k setting.

Critical weaknesses
  1. The main intervention results come from one history. The 28 valid snapshots are built from the same 455-event stream. More builds help study variation in store construction, but they do not show whether the findings hold across different histories.

  2. The diagnostic labels need stronger validation. Literal evidence matches do not show that the full supporting path is available. In the selected audit, only 12 of 24 literal-present cases contain full support. The paper acknowledges this, but does not establish how reliably these labels support practical diagnosis.

  3. The probes use fresh instances, and identical probe profiles can appear in systems with different failure patterns. It remains unclear how much these probes help diagnose the actual workload beyond directly inspecting its store and retrieval traces.

  4. The value of the complete workflow is not clearly measured. The paper provides useful results for individual stages, but does not clearly show that combining them leads to better diagnoses or better intervention choices than a simpler store-and-context audit.

Questions for authors
  1. Do you have results on independent histories using the complete diagnostic workflow with a fixed parser and readout policy?

  2. How often do the diagnostic labels agree with human judgments based on complete semantic evidence, and how often is the result UNKNOWN?

  3. Is there evidence that the probes and operation profiles help select better interventions than inspecting store and retrieval traces alone?

1 comment
AuthorsOpenReview ↗

Cross-History Validation, Semantic Evidence Reliability, and Diagnostic Utility

We thank the reviewer for the careful assessment. We have added post-review experiments to examine cross-history reproducibility, diagnostic-label reliability, and the practical value of the complete workflow. The revised evidence addresses the three questions as follows.

  1. Independent histories and fixed diagnostic operations

We constructed five new MQuAKE-T-derived histories, each containing 50 fact events and 12 multi-hop questions. The same frozen parser and readout rules were applied to four separately built Store variants (Appendix T, Tables 39–41).

The results provide partial cross-history replication:

Extraction prerequisites: Changing only Mem0-RV's extraction prompt increases literal old/current update opportunities from 1/60 (RV-native) to 58/60 (RV-generic). Among the latter, 52/58 reach latest-only state, and native-readout accuracy increases from 7/60 to 52/60.

Fixed version filtering: Under the same dense readout, VD−ID improves Additive by 38.33 pp (95% history-bootstrap CI [18.33, 56.67]) and A-MEM by 43.33 pp ([31.67, 53.33]). The corresponding effects are 0 pp for RV-native and +1.67 pp for RV-generic.

Graph readout: The earlier positive Graph-versus-dense interaction does not replicate for Additive. Its IG and VG readouts score 0/60 and 3/60, respectively, revealing a substantial evidence-delivery problem.

We investigated this problem through semantic evidence auditing and froze a gold-free Dense-seeded Graph intervention before testing five additional histories. Accuracy increased from 12/60 under the original strict Graph readout to 47/60, compared with 33/60 under random seeding. Human-judged complete Context support increased from 16/60 to 48/60 (Table 4, Appendix V). Plain V-dense remained stronger at 52/60, and 37/60 seeded Contexts were byte-identical to V-dense.

The five prospective histories are shorter (48–56 facts each) and belong to the same task family. Their evaluated questions and complete source chains do not repeat earlier panels, but 18–20 fact instances and 9–10 of 12 distinct MH answer strings per history also occur in earlier MQuAKE-T panels (Table 38). The intervention rule was frozen before selecting and scoring these histories, but the overlap limits independence and external validity. We therefore claim conditional replication and validation of a specific delivery intervention, not cross-domain generalization or complete workflow superiority.

  1. Reliability of diagnostic labels

We completed a random human audit of 120 MAB observations (Appendix U, Tables 42–43).

Among evaluable literal-positive cases, complete semantic support was confirmed in 38/55 Contexts (69.1%) and 43/72 Stores (59.7%). No false negatives were observed among adjudicable FULL cases (38/38 Contexts and 43/43 Stores), but Store support remained UNKNOWN in 41/120 observations. Inter-annotator agreement was κ=0.877 for Context and κ=0.520 for Store.

These measurements assess the literal evidence proxy used in stage localization, not the accuracy of every diagnostic stage label. A separate, non-random external census showed lower agreement (κ=0.455 for Context and 0.206 for Store). Literal matching can locate candidate evidence, but it cannot reliably certify complete semantic support. Store-level semantic judgments remain particularly uncertain.

  1. Incremental value of the complete workflow

We directly compared Full MemReq with Store+Trace across 555 questions and 15 system–history decision units (Appendix W, Tables 45–46). Full MemReq achieved 488/555 versus 486/555 for Store+Trace, a difference of +0.36 pp with a history-bootstrap 95% CI of [-5.95, 7.75]. Full MemReq also caused more harmful interventions (33 versus 13).

Adding prerequisite-based routing alone reduced accuracy to 440/555 and caused 62 harms, including 49 in A-MEM (37 from matched-Dump choices and 12 from ID readout). The existing traces do not establish whether these failures arose from incorrect diagnostic labels or from mapping labels to unsuitable actions. This remains unresolved.

The complete workflow has therefore not demonstrated superior repair selection over the stronger baseline. The fresh-state probes and operation profiles have also not established independent predictive value for selecting repairs.

The supported contribution is narrower: prerequisite checks and semantic evidence audits identify observable failure boundaries, and controlled interventions can test specific diagnoses. The RV extraction results, cross-history version-filtering responses, and prospective evidence-delivery intervention provide evidence for this interpretation.

Revised manuscript: Sections 6–8 (pp. 7–10), Table 4, and Appendices S–W.

We welcome further questions about the revised evidence and its limitations.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of Revisions and Post-Review Validation

We thank the reviewers and Area Chair for their time and constructive feedback. We have uploaded a revised manuscript that retains the original MemReq framework and research questions. The revision focuses on clarifying the scientific contribution, improving presentation, and providing additional evidence for the diagnostic claims.

The main revisions are summarized below.

1. Cross-history validation (Sections 6–7; Appendix T).

We evaluated four Store variants on five new MQuAKE-T-derived histories using fixed parsers and readout policies.

Changing only Mem0-RV's extraction prompt increases literal update opportunities from 1/60 to 58/60, with 52/58 opportunity-present cases reaching latest-only state. Native-readout accuracy increases from 7/60 to 52/60.

Under fixed dense readout, version filtering improves Additive by 38.33 pp and A-MEM by 43.33 pp, while providing little additional benefit for the RV variants. However, the earlier positive Additive Graph-versus-dense interaction does not replicate.

2. Human semantic auditing and prospective intervention (Table 4; Appendices U–V).

Human evaluation confirms that literal evidence matches cannot reliably establish complete semantic support.

We also tested a frozen, gold-free evidence-delivery intervention on five additional histories. Relative to the original strict Graph readout, accuracy increases from 12/60 to 47/60, compared with 33/60 under random seeding. Human-judged complete Context support increases from 16/60 to 48/60.

Plain V-dense remains stronger at 52/60, and 37/60 Dense-seeded Contexts are byte-identical to V-dense. These results support a specific evidence-delivery diagnosis, not Graph superiority.

The prospective histories contain 48–56 facts each. Their evaluated questions and complete source chains are distinct from earlier panels, but 18–20 fact instances and 9–10 of 12 distinct MH answer strings per history overlap earlier MQuAKE-T panels. Thus, the evidence remains limited to the same task family.

3. Additional controls and negative findings (Appendices W–Y).

We added direct Dump-All comparisons, repeated Reader evaluations, and a repair-selection policy comparison.

Full MemReq does not outperform the stronger Store+Trace baseline in repair selection (488/555 versus 486/555) and causes more harmful interventions (33 versus 13). GPT-OSS also exhibits substantial run-to-run variability. We retain these negative results and limit our conclusions accordingly.

4. Presentation and scientific positioning.

We aligned the RQ1–RQ3 wording across the Introduction and Sections 5–7, rewrote the abstract around the main quantitative findings, added an empirical example for Equation 1, expanded the discussion of closely related work, and consolidated the prospective validation in Table 4.

The revision does not introduce a new memory architecture or claim novelty in deterministic version selection or graph traversal.

Overall, the revised evidence supports a more specific conclusion: the observed effect of a memory operation depends on whether its prerequisites were formed and what evidence was retained and delivered. These conditions can be examined through stage-level audits and tested with bounded interventions. The complete workflow's superiority in automated repair selection remains unestablished.

We appreciate the reviewers' feedback and welcome further questions about the revised evidence and its limitations.

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

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