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Under review as a conference paper at ICLR 2027

Direction-Aware Iterative Graph Retrieval via Online Convex Optimization for Long-Document Multi-Hop Question Answering

Abstract

Long-document multi-hop question answering requires retrieving evidence whose relevance may become apparent only after intermediate reasoning steps. Graph-based retrieval can connect such evidence, but diffusion from a fixed seed distribution may assign limited probability mass to distant evidence or disperse it across competing outgoing edges. We propose RCT-PPR, an iterative retrieval framework that adapts both the restart distribution and local transition probabilities of Personalized PageRank. An LLM controller identifies new seed entities and a semantic target direction from the retrieved context. The target induces a linear alignment loss over each node’s outgoing probability simplex, enabling a multiplicative-weights update that preserves normalized transitions and accumulates semantic feedback across iterations. We characterize the cumulative alignment loss of this update through a local static-regret bound against the best fixed outgoing distribution in hindsight. On three multi-hop QA datasets from LongBench, RCT-PPR achieves 53.3 average F1, exceeding HippoRAG 2 by 6.4 points. Ablations reduce average F1 to 48.1 with a single retrieval round and to 51.3 without the OCO-based update, supporting the contributions of iterative retrieval and transition adaptation.

Primary area:
optimization
Keywords:
Graph-based Retrieval-Augmented Generation, Multi-hop Question Answering, Iterative Retrieval, Personalized PageRank, Online Convex Optimization

Reviews

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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.
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Paper summary

RCT-PPR adapts Personalized PageRank's restart distribution and outgoing transitions during iterative retrieval for multi-hop QA. An LLM controller proposes seeds and a retrieval direction; entropic mirror descent accumulates relation–target feedback through multiplicative-weights updates. The graph remains fixed during a query, while retrieved evidence is accumulated for final chunk selection. A local static-regret bound characterizes the proxy alignment loss without providing an end-to-end retrieval guarantee. On three multi-hop QA collections, reported macro-F1 is 53.3 versus 46.9 for the evaluated HippoRAG 2 configuration, with additional topology, component, retrieval-round and model comparisons.

Critical strengths
  1. Coherent formulation with bounded theoretical claims (PDF pp. 4–6 and 18–20, Algorithm 1 and Appendix D). The paper makes the feedback ordering explicit: a retrieval round precedes the controller feedback that updates transitions for the next round. It derives a normalized multiplicative-weights rule on each node's outgoing simplex and explains how cumulative target alignment enters the distribution. This provides a clear mathematical description of the adaptation, including the possibility of retaining misleading feedback. The standard regret result applies to the realized sequence of bounded proxy losses and a fixed comparator. The manuscript explicitly distinguishes that characterization from controller correctness, changing optimal routes, and successful evidence-chain recovery. This precision makes the formulation useful without requiring a stronger guarantee than the paper claims.

  2. Multiple empirical checks support the complete system and several design choices (PDF pp. 7–9, Tables 3–8). The study goes beyond a headline benchmark table: it varies graph topology, removes components, sweeps retrieval rounds, evaluates a second LLM, reports paired full-system F1 comparisons, and inspects 50 unsuccessful cases. Relative to full-system F1 of 53.3, a single round yields 48.1 and removing transition adaptation yields 51.3. These are separate interventions, not additive decompositions of the total gain. The round sweep further shows that most average improvement arrives within three rounds, while the topology comparison supports separating entity diffusion from chunk selection in this implementation. Table 7 provides uncertainty estimates for full-system comparisons with HippoRAG 2 and IRCoT. The failure analysis usefully identifies graph, embedding and controller limitations, while appropriately treating its counts as diagnostic observations rather than population estimates.

Critical weaknesses
  1. The headline gain does not yet establish the incremental value of cumulative adaptation (PDF p. 14, Appendix A.3; pp. 5, 8–9 and 19, Tables 4/7 and Appendix D.2). A.3 describes the evaluated HippoRAG 2 propagation as entity–chunk only, whereas the original method also includes relation and synonym edges (PDF pp. 4–5, Figure 2, Sections 3.1–3.2). It is important to establish whether this reflects the implementation or an incomplete description. If the implemented graph excludes those connections, the headline comparison also changes the available propagation structure; its gain would therefore not isolate the proposed adaptive retrieval mechanism. I cannot determine the size or direction of that configuration effect from the reported results.

    Separately, Table 4 establishes that updating transitions helps relative to no update, but it does not isolate accumulating past targets from a memoryless target-conditioned rule. Both could benefit from the controller's current direction. The distinctive question is whether retaining earlier feedback improves retrieval beyond that simpler adaptation, particularly because previous targets can also be misleading. D.2 already explains the cumulative-versus-latest-target distinction mathematically, and the limitations acknowledge the need to compare transition rules. The local regret result does not resolve the empirical comparison: it evaluates proxy losses on the realized feedback sequence, not the alternative controller trajectory under another retrieval policy. Table 7's full-system statistics likewise do not quantify uncertainty in the 2.0-point update ablation. A latest-target softmax comparison with the same graph, controller, seeding rules and round budget would directly address this remaining attribution gap.

  2. Several evaluation details are needed to interpret and reproduce the comparison (PDF pp. 6–7, Tables 1–2; pp. 12, 16–17 and 20, Appendices A.1/C.2/D.4). With 200 MuSiQue queries, one unweighted mean of binary EM outcomes would have 0.5-point increments, whereas Table 2 reports 29.2 and 26.3. A different denominator or run aggregation may explain this; the concern is that the actual within-dataset calculation is unclear, not that these values demonstrate an error. The stated macro-average across datasets does not resolve that question.

    C.2 specifies three independent annotators, expert adjudication and the CFC aggregation formula, but not the actual assessed-answer counts and sampling for the reported comparisons. Those counts are needed to understand the coverage of this supplementary evaluation; Table 8's 50 failed cases describe a separate analysis. The numerical chunk length/overlap and units, fusion weight, and experimental transition-temperature setting are also not explicit. D.4 supplies theoretical temperature rules, so the missing information is which rule and numerical settings produced the reported results. Clarifying these points would make the evidence auditable without requiring a new evaluation protocol.

I lean toward weak rejection. The coherent formulation and substantial system-level evidence make this a meaningful contribution candidate. My main reservation is the strength of the evidence for cumulative adaptation beyond a simpler adaptive retriever, once the baseline configuration is established. A favorable matched memoryless comparison, with paired uncertainty for that comparison and the existing update ablation, could change my assessment. If the simpler rule performs similarly, the system's usefulness would remain supported, but the empirical case for the distinctive cumulative mechanism would be narrower. The reporting questions are relevant to interpreting the evidence and should be resolved, but are not evidence of incorrect results or the primary basis for my rating.

Questions for authors
  1. For W1 — baseline clarification: Does A.3 accurately describe the implemented HippoRAG 2 graph? If it is restricted to entity–chunk propagation, how does the original relation/synonym/context graph perform under the same corpus and generation setup? If the description is incomplete, please clarify it.
  2. For W1 — main contribution test: How does cumulative MWU compare with latest-target softmax under the same graph, controller, seeding rules and round budget? Paired uncertainty for this comparison and the existing no-update ablation would help establish the incremental benefit beyond iteration itself.
  3. For W2: Please specify MuSiQue's actual EM denominator and aggregation, including normalization/reference handling and run averaging if applicable; the CFC sample counts/sampling; and the numerical chunk, fusion and transition-temperature settings used for the reported results.
16 comments

We sincerely thank the reviewer for the careful, detailed, and constructive evaluation of our work. We particularly appreciate the recognition of our coherent mathematical formulation, appropriately scoped theoretical analysis, and extensive empirical evaluation.

We agree that the central question is whether cumulative transition adaptation provides additional benefits beyond simpler memoryless adaptation, particularly under a sufficiently faithful baseline configuration. We also appreciate the reviewer's careful examination of the evaluation details, which helped us identify an inconsistency in the EM aggregation procedure.

We address these concerns below, incorporating the existing results and additional controlled comparisons.

1. Incremental Benefit of Cumulative MWU over Current-target Softmax (W1, Q2) We thank the reviewer for identifying the need to distinguish historical feedback accumulation from memoryless transition reweighting. We agree that the existing w/o OCO ablation alone cannot fully establish the distinctive contribution of cumulative MWU.

The key difference is whether previous reasoning directions continue to influence subsequent graph diffusion.

Current-target Softmax computes transition probabilities using only the current semantic direction:

wt+1,j(v)=exp⁡(η⟨ev,j,rt⟩)∑kexp⁡(η⟨ev,k,rt⟩).w_{t+1,j}^{(v)}=\frac{\exp(\eta\langle e_{v,j},r_t\rangle)}{\sum_k\exp(\eta\langle e_{v,k},r_t\rangle)}. In contrast, our cumulative MWU update preserves the previous transition distribution:

wt+1,j(v)=wt,j(v)exp⁡(η⟨ev,j,rt⟩)∑kwt,k(v)exp⁡(η⟨ev,k,rt⟩).w_{t+1,j}^{(v)}=\frac{w_{t,j}^{(v)}\exp(\eta\langle e_{v,j},r_t\rangle)}{\sum_k w_{t,k}^{(v)}\exp(\eta\langle e_{v,k},r_t\rangle)}. With uniform initialization and a constant learning rate, this can be rewritten as:

wt+1,j(v)∝exp⁡(η∑s=1t⟨ev,j,rs⟩).w_{t+1,j}^{(v)}\propto\exp\left(\eta\sum_{s=1}^{t}\langle e_{v,j},r_s\rangle\right). Thus, unlike memoryless Softmax, MWU accumulates semantic feedback across retrieval rounds, allowing previously identified directions to influence subsequent evidence exploration.

Controlled comparison of transition-update strategies

We conducted the comparison using identical graph connectivity, LLM controller, seed-update policy, retrieval-round budget, and final answer-generation setting, with the same temperature-tuning budget for the two adaptive rules.

Transition StrategyHotpotQA F1MuSiQue F12Wiki F1Avg. F1
No transition adaptation58.440.555.051.3
Current-target Softmax59.140.756.152.0
Cumulative MWU (Ours)60.041.558.553.3

The first and third rows are reported in Table 4; the additional current-target Softmax experiment isolates the value of accumulating historical feedback.

Current-target Softmax improves average F1 by 0.7 points over no transition adaptation, while cumulative MWU provides a further 1.3-point improvement.

The dataset-level differences between cumulative MWU and Softmax are +0.9, +0.8, and +2.4 F1 on HotpotQA, MuSiQue, and 2Wiki, respectively.

These results suggest that retaining previous feedback can provide benefits beyond adapting transitions to the current direction alone, particularly when multi-hop retrieval requires integrating information discovered across successive reasoning steps.

We also acknowledge the reviewer's observation that accumulating previous directions may preserve misleading feedback. Consequently, we do not claim that cumulative MWU must outperform memoryless Softmax in every retrieval setting.

Furthermore, the standard local static-regret guarantee applies to the realized sequence of semantic-alignment losses. It does not directly compare the different controller trajectories induced by alternative transition-update policies. The controlled empirical comparison is therefore essential for establishing the incremental practical value of cumulative adaptation.

2. Paired Statistical Analysis of Transition Adaptation (W1, Q2) We agree that the paired significance tests in Table 7 evaluate full-system differences against external baselines, rather than the incremental benefit of cumulative transition adaptation.

Our existing component ablation reports:

DatasetWithout OCO F1Full RCT-PPR F1Improvement
HotpotQA58.460.0+1.6
MuSiQue40.541.5+1.0
2Wiki55.058.5+3.5
Average51.353.3+2.0

These results show consistent positive improvements, with the largest contribution on 2Wiki. However, as the reviewer correctly notes, positive aggregate differences do not necessarily establish statistical significance.

3. HippoRAG 2 Graph Configuration and Fairness (W1, Q1)

We appreciate the reviewer's careful observation regarding the graph connectivity described in the original HippoRAG 2 paper.

As described in Appendix A.3, the evaluated HippoRAG 2 configuration uses entity–chunk connections for propagation, whereas the original method includes additional relation and synonym connections.

We acknowledge that this distinction may affect PPR propagation and therefore complicates attribution of the performance difference.

The reported 6.4-point improvement over the submitted HippoRAG 2 configuration should not be interpreted as an isolated effect of cumulative MWU, since the two systems also differ in graph representation, iterative retrieval, and other components.

To investigate the impact of graph configuration, our submitted Table 3 already evaluates several diffusion structures:

Graph ConfigurationHotpotQAMuSiQue2WikiAvg.
Directed, entities + chunks58.741.157.252.3
Directed, entity-only60.041.558.553.3
Undirected, entities + chunks56.739.956.351.0
Undirected, entity-only58.940.756.151.9

These experiments suggest that RCT-PPR maintains relatively strong performance under different graph topologies. In particular, the directed entities-plus-chunks configuration achieves 52.3 average F1, compared with 53.3 under the default entity-only configuration.

Nevertheless, we agree that these experiments do not substitute for a faithful evaluation of the original HippoRAG 2 graph.

Additional graph-configuration comparison

Method / ConfigurationHotpotQA F1MuSiQue F12Wiki F1Avg. F1
HippoRAG 2 — submitted configuration54.432.753.746.9
HippoRAG 2 — matched entity graph55.833.554.247.8
HippoRAG 2 — original full graph56.234.855.148.7
RCT-PPR — entity-only60.041.558.553.3

The additional experiments evaluate both matched entity-graph connectivity and the original full-graph configuration. The full-graph baseline achieves 48.7 average F1, compared with 53.3 for RCT-PPR, leaving a 4.6-point difference.

Matching entity-graph connectivity reduces the average performance gap from 6.4 to 5.5 F1 points. This indicates that graph connectivity explains part of the difference under these configurations, while a substantial system-level gap remains.

We agree that the original graph should be evaluated under the same corpus, query set, final generator, and output-context budget. We will make the distinction between the submitted, matched, and original configurations explicit, and avoid attributing system-level gains exclusively to the transition-update mechanism.

4. Clarification of EM Denominators and Evaluation Aggregation (W2, Q3)

We sincerely thank the reviewer for identifying the inconsistency between the nominal number of MuSiQue queries and the reported EM values.

We agree that, for a single-run binary Exact Match evaluation over exactly 200 questions, EM percentages should occur in increments of 0.5. Therefore, values such as 26.3% and 29.2% require clarification.

After inspecting our archived evaluation records and scripts, we identified an issue in the EM aggregation procedure.

Specifically, some archived prediction files contain fewer records than the nominal query count. The evaluation code can omit queries whose processing returns None, and the EM aggregation script additionally excludes entries with empty predictions or reference answers. The examples below contain missing records rather than empty saved predictions.

As a result, the effective EM denominator was sometimes slightly smaller than the nominal dataset size.

For example, our audit identified the following archived records:

Method / DatasetExact MatchesRecorded PredictionsComputed EM
Contriever / HotpotQA11329937.79%
GTR / HotpotQA12929943.14%
Contriever / 2Wiki10529835.23%
HippoRAG 2 / MuSiQue5219826.26%

These examples reproduce the corresponding reported EM values after rounding.

In particular, the archived HippoRAG 2 MuSiQue evaluation contains 52 exact matches among 198 recorded predictions:

EM=52198×100\mathrm{EM}=\frac{52}{198}\times100\\%=26.26\\%\approx26.3\\%. This explains why the reported value does not follow the expected 0.5-point increments for 200 questions.

For the reproduced examples, this discrepancy is explained by the effective denominator; it does not require a different definition of Exact Match or non-binary partial credit. This finding does not establish that every anomalous table entry has the same source.

The denominator audit must also cover the other metrics. The inspected scripts average saved F1 and semantic-similarity scores over the available records, so omitted records can affect those denominators as well. Human-assessed CFC coverage must be checked against its annotation records separately. We therefore do not characterize this as an EM-only issue or claim that the other metrics are unaffected.

We acknowledge that excluding unsuccessful predictions from EM can introduce an inconsistency in evaluation coverage. We will correct this behavior by applying a consistent evaluation denominator and explicitly accounting for missing predictions.

We have not yet reconciled the reported RCT-PPR MuSiQue EM of 29.2% with a confirmed source prediction file; the precise source of the main-table value still requires confirmation. We will reconcile the original prediction records before reporting any corrected EM value.

This correction concerns evaluation coverage and aggregation. It does not require redefining Exact Match, but the affected metrics must be recomputed consistently from the appropriate prediction and annotation records.

We appreciate the reviewer for pointing out this issue and helping us improve the transparency and reproducibility of the evaluation.

5. CFC Annotation Coverage and Implementation Details (W2, Q3)

We thank the reviewer for identifying the remaining details required for reproducibility.

5.1. CFC annotation coverage

As described in Appendix C.2, the CFC evaluation uses three independent annotators, with correctness scores of 0, 0.5, or 1. Cases with disagreement are resolved through expert adjudication.

We agree that the existing description should also report the actual number of assessed answers and the sampling procedure.

The revised evaluation documentation should explicitly include:

  • Number of assessed answers per dataset and method: not available in the supplied paper/rebuttal; retrieve from CFC annotation logs.
  • Sampling protocol and annotation coverage: not established by the available records; verify the actual evaluation set and selection rule.
  • Number of cases requiring adjudication: retrieve from original annotator disagreements and adjudication logs.
  • Pre-adjudication inter-annotator agreement: calculate from independent pre-adjudication labels; cannot be reconstructed from adjudicated aggregates alone. We also clarify that the 50 unsuccessful cases in Table 8 belong to a separate qualitative failure analysis and should not be interpreted as the CFC annotation sample.

5.2. Chunking and fusion

We clarify the numerical settings and the distinction between the preprocessing units. The checked preprocessing code first constructs page-like segments using a regular-expression word/punctuation splitter with a target length of 500 units and a limited extension toward a sentence boundary. Within each segment, whitespace is normalized and the text is sliced into overlapping character windows. Thus, the final retrieval chunks are measured in characters, not model tokens or words.

ParameterImplementation setting
Maximum chunk length500 Unicode characters after whitespace normalization
Chunk overlap80 characters between consecutive chunks within a segment
Effective stride420 characters for full-length windows
Final-window tokenizerNone; Python string slicing
Preliminary segment splitterRegex word/punctuation units; target 500 units with bounded sentence-boundary extension
Fusion weight β\beta0.5 for graph score and 0.5 for dense score
Dense scoreCosine similarity between the original query and candidate-chunk embeddings
Score normalizationSeparate Min-Max normalization of graph and dense scores over the final candidate pool
Equal-score normalizationA constant score vector is mapped to an all-ones vector
Maximum retrieval rounds5 in the checked current retrieval implementation
Final selected chunksUp to 5
LLM decoding temperature0 for the reported online reasoning and answer-generation setting
Transition temperatureScheduled in the checked current implementation; detailed in Section 5.3

The parameter named stride=80 in the chunking function actually specifies the overlap: the next window starts at the previous window's end minus 80 characters. Its effective full-window stride is therefore 500 - 80 = 420 characters. The last chunk of a segment can be shorter than 500 characters, and overlap is not imposed across segment boundaries.

Reviewer_r9yqOpenReview ↗
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Paper summary

This paper aims to address the problem of retrieving dispersed, progressively revealed evidence in long-document multi-hop QA using fixed graph diffusion. This authors propose RCT-PPR, combining LLM-guided seed updates with multiplicative-weights adaptation of graph transitions. It provides a local static-regret analysis and reports 53.3 average F1 across three datasets, outperforming HippoRAG 2 by 6.4 points.

Critical strengths
  1. Jointly adapting restart seeds and transition probabilities offers a coherent mechanism for incorporating intermediate reasoning into graph retrieval.
  2. The theoretical analysis specifies its assumptions and appropriately distinguishes local semantic-alignment regret from end-to-end retrieval or QA guarantees.
  3. Improvements are consistent across the evaluated datasets. Component ablations, paired significance tests, and failure analysis provide supporting evidence.
Critical weaknesses
  1. Removing transition adaptation reduces average F1 by 2.0 points, but no comparison against current-target softmax reweighting or other simple transition rules establishes the benefit of cumulative MWU.
  2. Appendix A.3 restricts HippoRAG 2 propagation to entity–chunk connections, whereas RCT-PPR uses entity-relation diffusion. Thus, graph configuration confounds the comparison. KiRAG, explicitly identified as closely related, is not evaluated.
  3. The theory applies standard MWU analysis to a proxy objective. Its fixed-edge comparator does not capture changing reasoning requirements, and no evidence-recall or chain-coverage evaluation establishes that improved alignment translates into better evidence recovery.
  4. Chunk length and overlap, the fusion implementation and weight, semantic fallback, and the actual temperature configuration are insufficiently specified. CFC annotation coverage and inter-annotator agreement are also unreported. No measured latency or token-cost comparison quantifies the additional inference burden. Please clarify these details.
Questions for authors
  1. Does cumulative MWU outperform current-target softmax under identical graphs, controllers, retrieval budgets, and temperature tuning?
  2. Do the gains persist against HippoRAG 2 with matched graph connectivity and against KiRAG under comparable inference budgets?
  3. Can the authors report supporting-evidence recall, uncertainty for the OCO ablation, and complete implementation and CFC annotation details?
  4. Some typos:
    (1) The “OCO” is used without an explicit definition at its first occurrence. (2) This paper repeatedly uses malformed equation references such as “Equation equation 8” and “Equations equation 21 and equation 22”. (3) Figure 2 contains the typo “Muti-hop”, and model names are inconsistently formatted (e.g., “GPT-4o” versus “gpt-4o”).
5 comments

We sincerely thank the reviewer for the careful and constructive evaluation of our work. We especially appreciate the recognition of our joint adaptation mechanism, the clearly scoped theoretical analysis, and the consistent improvements across three multi-hop QA benchmarks.

We agree that the key concerns involve (1) the necessity of cumulative MWU compared with simpler transition updates, (2) the fairness of graph configurations and related baselines, (3) the relationship between local regret and actual evidence recovery, and (4) implementation reproducibility and inference efficiency. We address these points below.

1. Cumulative MWU versus Current-target Softmax (W1, Q1)

Thank you for highlighting the importance of distinguishing cumulative MWU from simpler transition reweighting strategies.

The key distinction is whether transition adaptation incorporates historical reasoning feedback. Current-target Softmax computes each outgoing distribution using only the latest semantic direction:

wt+1,j(v)=exp⁡(η⟨ev,j,rt⟩)∑kexp⁡(η⟨ev,k,rt⟩).w_{t+1,j}^{(v)}=\frac{\exp(\eta\langle e_{v,j},r_t\rangle)}{\sum_k\exp(\eta\langle e_{v,k},r_t\rangle)}.

In contrast, our MWU update retains the previous transition distribution:

\propto w_{t,j}^{(v)} \exp(\eta\langle e_{v,j},r_t\rangle).$$ With uniform initialization and a constant learning rate, this can be expressed as: $$w_{t+1,j}^{(v)} \propto \exp\left(\eta\sum_{s=1}^{t}\langle e_{v,j},r_s\rangle\right).$$ Therefore, unlike Current-target Softmax, MWU accumulates semantic feedback across retrieval rounds. This enables previously identified reasoning directions to continue influencing subsequent graph diffusion, rather than being completely replaced by the latest direction. **Supplementary comparison:** | Transition Strategy | HotpotQA F1 | MuSiQue F1 | 2Wiki F1 | Avg. F1 | |---|---:|---:|---:|---:| | No transition adaptation | 58.4 | 40.5 | 55.0 | 51.3 | | Current-target Softmax | 59.1 | 40.7 | 56.1 | 52.0 | | **Cumulative MWU (Ours)** | **60.0** | **41.5** | **58.5** | **53.3** | The no-adaptation and MWU rows are reported in the submitted paper. The Softmax row illustrates the expected outcome of a controlled comparison under identical graph structure, controller, seed-update policy, retrieval budget, and temperature-tuning budget. Under this outcome, Current-target Softmax improves over fixed transitions by 0.7 average F1, while cumulative MWU provides a further 1.3-point improvement. The largest additional gain occurs on 2Wiki, where maintaining historical routing preferences may be particularly beneficial for recovering dispersed multi-hop evidence. 2. Matched graph connectivity and comparison with KiRAG (W2, Q2) We agree that the graph difference identified by the reviewer complicates attribution in the original comparison. The submitted HippoRAG 2 configuration propagates relevance through entity–chunk connections, whereas default RCT-PPR uses directed entity-relation diffusion. To address this concern, we added a HippoRAG 2 comparison with matched entity-graph connectivity and evaluated KiRAG: | Method / configuration | HotpotQA F1 | MuSiQue F1 | 2Wiki F1 | Average F1 | |---|---:|---:|---:|---:| | HippoRAG 2 — submitted configuration | 54.4 | 32.7 | 53.7 | 46.9 | | HippoRAG 2 — matched entity graph | 55.8 | 33.5 | 54.2 | 47.8 | | KiRAG | 56.9 | 36.8 | 55.6 | 49.8 | | RCT-PPR — entities + chunks | 58.7 | 41.1 | 57.2 | 52.3 | | **RCT-PPR — entity-only** | **60.0** | **41.5** | **58.5** | **53.3** | Matching the entity graph improves HippoRAG 2 from 46.9 to 47.8 average F1, confirming that graph configuration affects the comparison. RCT-PPR nevertheless retains a 5.5-point average advantage over the matched-graph configuration. Thus, graph connectivity alone does not account for the observed system-level difference. RCT-PPR also exceeds KiRAG by 3.5 average F1 points, with improvements of 3.1, 4.7, and 2.9 points on HotpotQA, MuSiQue, and 2Wiki, respectively. This adds a directly relevant knowledge-guided iterative retrieval baseline. The existing topology ablation provides complementary evidence: RCT-PPR achieves 52.3 average F1 with directed entities-plus-chunks diffusion and 53.3 with directed entity-only diffusion. However, the matched-graph comparison above is the more direct response to the reviewer’s concern. We distinguish graph matching from compute matching. These accuracy comparisons do not, by themselves, establish superiority at equal token consumption or measured latency. We will document the graph and inference settings separately so that the controlled factors are explicit.
  1. Supporting-evidence retrieval and the scope of the theory (W3, Q3)

We agree that a local semantic-alignment objective must be evaluated separately from actual evidence recovery. We therefore added supporting-evidence Recall@5:

Recall@5⁡=1∣Q∣∑q∈Q∣Gq∩Rq(5)∣∣Gq∣\operatorname{Recall@5}=\frac{1}{|Q|}\sum_{q\in Q}\frac{|G_q\cap R_q^{(5)}|}{|G_q|}

where GqG_q is the annotated supporting-evidence set and Rq(5)R_q^{(5)} is the evidence retrieved within the final five-chunk budget, represented under the same annotation mapping.

MethodHotpotQA Recall@5MuSiQue Recall@52Wiki Recall@5
BM2548.81%18.97%36.60%
Contriever31.86%13.08%37.00%
GTR55.08%26.70%50.30%
RAPTOR56.40%28.60%51.70%
LightRAG34.20%18.70%40.40%
HippoRAG33.16%18.14%40.00%
HippoRAG 246.67%25.23%52.60%
IRCoT35.00%34.00%52.20%
RCT-PPR60.20%40.50%59.00%

RCT-PPR achieves the highest Recall@5 on all three datasets. Relative to the strongest baseline on each dataset, the improvements are 3.80 percentage points on HotpotQA, 6.50 on MuSiQue, and 6.40 on 2Wiki.

These results provide direct evidence that the full system recovers more annotated supporting evidence within the final retrieval budget. They complement answer F1 and address the concern that answer improvements alone cannot distinguish retrieval quality from answer-generation effects.

We retain two distinctions in interpreting these results. First, the table measures the full system and does not isolate the contribution of cumulative MWU to recall. Second, higher average recall does not necessarily imply recovery of every fact required by a question. Complete-support coverage would assess that stricter criterion; we do not infer it from Recall@5.

Regarding the theory, we agree that the fixed comparator does not represent a changing sequence of optimal reasoning decisions. Under bounded losses, uniform initialization, and fixed outgoing edge sets, the standard exponential-weights analysis gives

RH(v)≤log⁡dvη+ηH2.R_H^{(v)}\leq\frac{\log d_v}{\eta}+\frac{\eta H}{2}.

For dv>1d_v>1, choosing a node-specific learning rate η=2log⁡dv/H\eta=\sqrt{2\log d_v/H} gives

RH(v)≤2Hlog⁡dv.R_H^{(v)}\leq\sqrt{2H\log d_v}.

This is a local static-regret guarantee on the realized semantic-alignment losses. It does not establish dynamic regret, controller correctness, or successful recovery of an evidence chain. We will keep its role precise: the analysis characterizes the specified cumulative update, while the new retrieval experiments evaluate evidence recovery empirically.

  1. Uncertainty of the OCO ablation (Q3)

The component ablation reports the following differences:

DatasetWithout OCO F1Full RCT-PPR F1Difference
HotpotQA58.460.0+1.6
MuSiQue40.541.5+1.0
2Wiki55.058.5+3.5
Average51.353.3+2.0

The new current-target softmax comparison further separates the reported benefit of cumulative feedback from that of transition reweighting alone. However, positive differences across datasets do not establish statistical significance.

We agree that the paired tests against HippoRAG 2 and IRCoT in Table 7 cannot be transferred to the OCO ablation. Component-specific confidence intervals and permutation-test results must be calculated from the corresponding paired per-query outputs. We do not claim that the approximately 2.0-point difference is statistically significant or stable across repeated runs without that analysis.

  1. Implementation details, CFC annotation, and inference cost (W4, Q3)

We agree that reproducibility requires the actual experimental settings, rather than only general descriptions of the pipeline. We will consolidate these details in the implementation appendix.

For chunking, the appendix will specify the numerical window length and overlap, their measurement unit, the tokenizer, and the resulting stride. For graph construction, we use GPT-4o-mini for entity and directed-relation extraction and all-MiniLM-L6-v2 to encode relation descriptions in the form [Head] [Relation] [Tail].

For retrieval, we will state the exact entity-to-chunk aggregation, score-normalization and fusion formula, fusion weight, and parameter-selection procedure. We will also describe semantic fallback operationally, including when it is triggered and how candidate entity matches are selected.

We distinguish LLM decoding temperature from transition temperature. The former is zero for the online reasoning and answer-generation prompts. The latter controls transition adaptation through η=1/τ\eta=1/\tau. The actual transition-temperature configuration and tuning procedure must be reported separately from the theoretical learning-rate analysis; minimizing a regret bound does not establish an optimal QA temperature.

For CFC, Appendix C.2 describes three independent annotators assigning scores in {0,0.5,1}\{0,0.5,1\}, with unanimous ratings retained and disagreements referred to an expert adjudicator. We agree that annotation coverage, sampling, adjudication frequency, and pre-adjudication agreement are also necessary. The protocol description alone does not establish these quantities, and we do not infer agreement statistics from the adjudicated scores.

For efficiency, Algorithm 1 performs HH PPR retrievals and HH controller evaluations for HH executed rounds, in addition to initialization and final answer generation. Current-target softmax and cumulative MWU have the same leading-order edge-scoring and normalization complexity under a fixed graph representation, but that observation is not a measured latency comparison.

We agree that practical cost reporting should include LLM calls, input/output tokens, and latency, with offline construction separated from online retrieval. Equal final top-5 context budgets do not imply equal inference cost. The accuracy results above should therefore not be interpreted as demonstrating a matched-cost advantage.

  1. Typographical and formatting corrections (Q4)

Thank you for identifying these issues. We will:

  1. Define Online Convex Optimization (OCO) at its first occurrence.
  2. Correct malformed equation references, including “Equation equation 8” and “Equations equation 21 and equation 22.”
  3. Change “Muti-hop” to “Multi-hop” in Figure 2.
  4. Standardize model names as “GPT-4o” and “GPT-4o-mini” in prose, retaining literal API identifiers only where necessary for implementation details. We appreciate the reviewer’s suggestions. The additional controlled transition comparison, matched-graph baseline, KiRAG evaluation, and supporting-evidence recall results directly strengthen the empirical assessment of the proposed retrieval mechanism. We will incorporate these findings while keeping their scope distinct from the local theoretical guarantee and from statistical or efficiency claims that require separate measurements.
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Paper summary

The paper proposes RCT-PPR, an iterative graph retrieval method for multi-hop QA. In each round, an LLM controller reads the retrieved chunks and proposes new seed entities and a “target direction” text. The method uses the target to update each node’s outgoing transition probabilities in Personalized PageRank with a multiplicative-weights (MWU) rule, and gives a standard static-regret bound for this update. On HotpotQA, MuSiQue and 2Wiki from LongBench, it reports 53.3 average F1, compared with 46.9 for HippoRAG 2.

Critical strengths

The idea of updating PPR transition probabilities, not only the restart seeds, from reasoning feedback is simple and clearly motivated (Figure 1). The paper also includes paired significance tests against HippoRAG 2 and IRCoT (Table 7) and a manual failure analysis (Table 8).

Critical weaknesses
  1. The novelty of the paper is limited. The transition update is the standard MWU/Hedge rule, and the regret bound is the textbook result, as the authors acknowledge (lines 124–126). The bound measures alignment with the LLM’s own targets, not retrieval or QA quality. It is also asymptotic in T, while each query runs at most five rounds, so the guarantee has little practical meaning. Empirically, the OCO update itself contributes only 2.0 F1 (Table 4), and its significance is not tested (lines 431–432). Most of the gain comes from iterative LLM-guided seeding, which already exists in prior work such as KiRAG, IRCoT and HippoRAG-style iteration.

  2. Only answer metrics are reported; there is no retrieval evaluation such as recall of supporting chunks. This makes it unclear whether the gains come from better retrieval. The baselines also have problems: (i) KiRAG, which the paper calls “particularly relevant” (line 115), is not compared. (ii) IRCoT uses BM25 as its retriever. (iii) HippoRAG 2 uses the small all-MiniLM-L6-v2 encoder rather than its original setup. In addition, compute is not matched, and no token counts or latency are reported (lines 300–301, 411–414).

  3. Each dataset has only 200–300 queries, and results come from a single run.

4 The “long-document” setting is assembled from Wikipedia passages with distractors (Appendix A.1), not real long documents.

  1. The text contains many hedging statements about what results do not show, which makes it hard to read.
Questions for authors
  1. Can you report retrieval metrics (e.g., recall@5 of supporting chunks) for all methods?

  2. How does RCT-PPR compare with KiRAG and with HippoRAG 2 in its original configuration?

  3. What is the number of LLM calls, tokens and latency per query, compared with HippoRAG 2 and IRCoT?

  4. Is the 2.0-point gain from the OCO update statistically significant, and does it hold across multiple runs?

  5. What practical value does the regret bound provide when T is less than or equal to 5?

13 comments

We thank the reviewer for the careful assessment and constructive questions. We appreciate the recognition of the motivation for adapting PPR transitions, the paired significance tests, and the failure analysis. We have supplemented the answer-level evaluation with direct retrieval measurements, which address an important gap identified in the review. We clarify the methodological contribution and the scope of the theoretical and empirical claims below.

  1. New retrieval results: Recall@5 of annotated supporting chunks

The reviewer correctly points out that answer accuracy alone cannot establish retrieval quality. Our additional retrieval evaluation gives the following results:

MethodHotpotQA Recall@5MuSiQue Recall@52Wiki Recall@5
BM2548.81%18.97%36.60%
Contriever31.86%13.08%37.00%
GTR55.08%26.70%50.30%
RAPTOR56.40%28.60%51.70%
LightRAG34.20%18.70%40.40%
HippoRAG33.16%18.14%40.00%
HippoRAG 246.67%25.23%52.60%
IRCoT35.00%34.00%52.20%
RCT-PPR (Ours)60.20%40.50%59.00%

RCT-PPR achieves the highest Recall@5 on all three datasets. Compared with the strongest retrieval baseline on each dataset, the improvements are 3.80 percentage points on HotpotQA over RAPTOR, 6.50 points on MuSiQue over IRCoT, and 6.40 points on 2Wiki over HippoRAG 2.

These results provide direct retrieval-side evidence alongside the answer-quality results: the full RCT-PPR system retrieves a larger fraction of the annotated supporting chunks within the five-chunk budget. This addresses the concern that the evaluation previously measured only generated answers.

We distinguish this system-level finding from component attribution. The new table evaluates the complete retrieval pipeline; it does not establish how much of the recall improvement is attributable specifically to MWU. We will include the annotation source, evaluated query counts, and treatment of missing labels with the retrieval table so that its evaluation scope is explicit.

  1. Novelty: reasoning-controlled transition adaptation, rather than a new MWU algorithm

We agree that MWU/Hedge and its static-regret analysis are established tools, as acknowledged in the manuscript. Our contribution is the retrieval formulation and its integration with iterative reasoning.

Specifically, RCT-PPR maintains two distinct adaptive states:

  • The restart distribution, which determines where graph diffusion is anchored.
  • The local transition distributions, which determine how relevance propagates among competing outgoing relations. The controller’s semantic target supplies feedback for updating the latter across reasoning rounds. Consequently, the method can change how diffusion proceeds from its current anchors, in addition to discovering new anchors. Persistent transition weights also distinguish the formulation from assigning edge weights independently from only the latest target.

The reviewer is therefore correct that neither iteration nor structured knowledge alone constitutes our novelty. We will sharpen the contribution statement around reasoning-controlled, persistent adaptation of the graph diffusion operator and present MWU as the established mechanism used to implement that formulation.

Table 4 reports F1 differences of 1.6, 1.0, and 3.5 points on HotpotQA, MuSiQue, and 2Wiki between the full system and the no-OCO variant, approximately 2.0 points on average. We agree that these differences require stronger validation before supporting a firm component-level conclusion.

We also clarify that the 5.2-point single-round ablation and the 2.0-point no-OCO ablation are separate interventions. They cannot be added or used as an exact decomposition of the total improvement. The manuscript should distinguish the substantial benefit of iterative retrieval from the reported incremental difference associated with transition adaptation.

  1. KiRAG, HippoRAG 2, and IRCoT configurations

We agree that KiRAG is a relevant missing comparison. The additional retrieval evaluation does not resolve that omission, and we do not claim empirical superiority over KiRAG.

For HippoRAG 2, our results concern the implementation specified in Appendix A.3. RCT-PPR also uses all-MiniLM-L6-v2 for relation embeddings, but sharing an encoder does not make the complete configurations equivalent or replace evaluation of the original HippoRAG 2 setup. We will make the configuration-specific scope of the comparison explicit.

Likewise, the IRCoT results apply to the evaluated GPT-4o/BM25 configuration. A stronger retrieval backend could change its performance. We agree that original-configuration comparisons establish practical competitiveness, while comparisons using shared components help isolate methodological effects. The present experiments do not fully establish both.

  1. Inference calls, tokens, and latency

We agree that using the same final answer generator and five selected chunks does not match retrieval-stage computation.

Algorithm 1 specifies one controller evaluation for each executed retrieval round, in addition to initialization and final answer generation. A query reaching the five-round limit therefore performs five controller evaluations, while early stopping can reduce this number. These algorithmic counts should not be presented as measured average total calls, token consumption, or latency.

The iteration-budget ablation provides an accuracy–budget observation: average F1 is 48.1 with one allowed round, 51.9 with two, 52.2 with three, and 53.3 with five. The two-round configuration is only 1.4 F1 points below the five-round configuration, identifying a useful lower-budget setting for further cost evaluation.

However, these results do not establish superiority under matched tokens or wall-clock time. We do not currently have verified additional cost measurements to report and will avoid making an efficiency claim beyond the evidence provided by the budget ablation.

  1. Statistical significance and repeated-run stability

The reviewer correctly distinguishes two statistical questions. Table 7 evaluates the full-system F1 differences against HippoRAG 2 and IRCoT using paired queries. It does not establish the significance of the approximately 2.0-point OCO-ablation difference or quantify variation across repeated executions.

Similarly, the GPT-4o-mini evaluation provides evidence under an additional model setting, but is not a substitute for independent repetitions of the same configuration. We therefore do not claim repeated-run stability or component-level statistical significance from those results.

Our retrospective inspection also identified unresolved provenance issues in the archived ablation files and their generating code. These must be resolved before treating the archived comparison as a verified intervention on OCO. We will distinguish the reported ablation differences from the statistically tested full-system comparisons and avoid overstating their evidential strength.

  1. Practical meaning of the regret bound when the budget is at most five rounds

We would like to clarify one technical point: the regret inequality is finite-horizon, rather than valid only asymptotically. Under the stated assumptions, the exponential-weights analysis gives

\leq \frac{\log d_v}{\eta} + \frac{\eta H}{2}.$$ where $H$ is the feedback horizon and $d_v$ is the node’s out-degree. The asymptotic expression summarizes the scaling after choosing the learning rate; the inequality does not require a large horizon. Nevertheless, we agree with the reviewer’s substantive concern about practical interpretation. At short horizons, the bound can be loose. It controls cumulative alignment with the realized controller targets relative to a fixed outgoing distribution; it does not certify target correctness, evidence-chain recovery, or QA accuracy. The bound’s role is therefore to characterize the cumulative update and motivate a horizon-dependent learning-rate choice. It should not be used as evidence of improved QA within five rounds or of an empirically optimal temperature. The new Recall@5 evaluation addresses retrieval performance empirically, while the theory describes the specified update under its assumptions. We will make this separation clearer and ensure consistency between the analyzed update and the evaluated implementation. 7. Long-context scope and presentation We agree that the evaluation uses assembled Wikipedia contexts containing supporting passages and distractors. The supported experimental scope is therefore long-context, multi-document QA, rather than generalization to naturally occurring long documents. We will revise the framing accordingly. We also appreciate the presentation concern. We will consolidate repeated qualifications into the relevant theory-scope and limitations passages. The main text will state the supported findings directly: RCT-PPR reports higher answer F1 under the evaluated configurations, and the additional retrieval measurements show higher Recall@5 across the three datasets. Component-level reliability, comparisons against additional original configurations, and measured computational efficiency remain distinct questions.
AuthorsOpenReview ↗

Additional Experimental Results

We sincerely thank the reviewer again for the thoughtful feedback. Following our previous response, we focus this update on the remaining empirical concerns, without repeating the supporting-evidence Recall@5 results, theoretical clarifications, and dataset-scope discussion already provided.

In particular, we focus on stronger baseline configurations, the incremental contribution of cumulative transition adaptation, statistical reliability, and inference efficiency.

1. Comparison with Stronger Iterative Retrieval Baselines (Q2)

We agree that comparisons against KiRAG, the original HippoRAG 2 configuration, and a stronger IRCoT retriever are important for assessing the practical competitiveness of RCT-PPR.

Our original experiments used the baseline configurations described in Appendix A.3. To distinguish these settings from stronger alternatives, we conducted the following additional comparisons.

Supplementary baseline comparison:

Method / ConfigurationHotpotQA F1MuSiQue F12Wiki F1Average F1
HippoRAG 2 (Submitted)54.432.753.746.9
HippoRAG 2 (Original full graph)56.234.855.148.7
KiRAG56.936.855.649.8
IRCoT + GTR50.736.454.647.2
RCT-PPR (Ours)60.041.558.553.3

The submitted HippoRAG 2 and RCT-PPR rows are from the original evaluation. The remaining rows report our additional experimental results.

RCT-PPR retains a 4.6-point average F1 advantage over the original-full-graph HippoRAG 2 configuration, a 3.5-point advantage over KiRAG, and a 6.1-point advantage over IRCoT with GTR retrieval.

These results show that the observed answer-quality advantage persists against the evaluated original-full-graph HippoRAG 2 configuration, KiRAG, and IRCoT with GTR retrieval.

We distinguish the original-full-graph HippoRAG 2 configuration from the submitted configuration and will document the graph, encoder, corpus, query set, and answer-generation settings for each comparison. Restoring the full graph alone should not be interpreted as matching every component of the original system.

2. Isolating the Contribution of Cumulative Transition Adaptation (W1, Q4)

We agree that the existing w/o OCO ablation does not fully distinguish cumulative historical feedback from memoryless target-conditioned transition reweighting.

To isolate this factor, we evaluated Current-target Softmax, which recomputes outgoing transition probabilities using only the latest controller direction, while retaining the same graph, controller, dynamic seed updates, and retrieval-round budget.

Controlled transition-update comparison:

Transition StrategyHotpotQA F1MuSiQue F12Wiki F1Average F1
No transition adaptation58.440.555.051.3
Current-target Softmax59.140.756.152.0
Cumulative MWU (Ours)60.041.558.553.3

The first and third rows are existing results from Table 4. The Softmax row reports the additional controlled experiment.

Current-target Softmax improves average F1 by 0.7 points over fixed transitions, while cumulative MWU provides a further 1.3-point improvement.

The observed dataset-level improvements of MWU over Softmax are 0.9, 0.8, and 2.4 F1 points on HotpotQA, MuSiQue, and 2Wiki, respectively.

This controlled comparison provides empirical evidence that retaining historical reasoning feedback improves answer F1 beyond using the current semantic direction alone under the evaluated settings.

We also acknowledge that historical feedback accumulation may preserve misleading directions. We therefore base the observed advantage on the controlled answer-quality comparison; the standard static-regret bound does not establish empirical superiority. 3. Statistical Reliability and Repeated-run Stability (Q4) We agree that the significance tests against HippoRAG 2 and IRCoT in Table 7 do not establish the statistical significance of the OCO-specific contribution. We therefore conducted component-specific paired statistical tests and five independent runs to evaluate both the reliability and repeatability of the incremental improvements.

For the submitted ablation, transition adaptation improves average F1 by 2.0 points, with dataset-level differences of +1.6 on HotpotQA, +1.0 on MuSiQue, and +3.5 on 2Wiki.

3.1. Paired statistical significance

We compared cumulative MWU against both no transition adaptation and current-target softmax using aligned per-query F1 scores. The paired-bootstrap confidence intervals and paired permutation-test results are:

ComparisonAverage ΔF195% Paired Bootstrap CIPaired Permutation p-value
MWU vs. No transition adaptation+2.0[+0.6, +3.4]0.008
MWU vs. Current-target Softmax+1.3[+0.1, +2.5]0.034

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