acceptodds
Under review as a conference paper at ICLR 2027

BarySLAM: Barycentric Consensus Geometry for Collaborative 3D Gaussian SLAM

Abstract

Collaborative 3D Gaussian SLAM must reconcile independently reconstructed submaps whose overlap is often partial and whose Gaussian decompositions may differ across agents. Pairwise registration and sequential fusion can make the global estimate sensitive to uncertain intermediate geometry and fusion order. We present BarySLAM, which organizes cross-agent information around Barycentric Consensus Geometry, a partially supported latent geometric representation shared by agents observing the same scene structure. BarySLAM derives structural observations from local Gaussian fields, establishes partial cross-agent support through unbalanced optimal transport, and jointly refines submap poses and consensus geometry with held-out validation to suppress inconsistent cross-agent evidence. The validated consensus is then transferred to the original Gaussian primitives for global map construction, maintaining a common geometric basis from collaborative estimation to reconstruction. Experiments on synthetic and real multi-agent benchmarks show SOTA overall performance in trajectory estimation and Gaussian reconstruction, with improved robustness under limited overlap and corrupted cross-agent registration and reduced sensitivity to fusion order. https://gaoxin09.github.io/BarySLAM/.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Collaborative SLAM, 3D Gaussian Splatting, multi-agent mapping, map fusion, multiway registration, optimal transport, robust estimation.

Reviews

Among:
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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_iMmNOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper investigates whether model-score separation observed on public LLM leaderboards transfers to smaller candidate cohorts. The authors introduce cohort-conditional separation, defined as the fraction of model pairs whose aggregate benchmark scores differ by more than a specified operational margin.

Using Open LLM Leaderboard v2 data covering 4,108 models and 133 snapshots, the paper examines three cohort constructions: full eligible frames, score-selected top-K cohorts, and uniformly sampled candidate sets. The analysis reports substantial separation compression after score-based selection and considerable dispersion for small random cohorts. The authors further propose a six-field reporting protocol intended to improve the transparency of leaderboard-based comparisons.

Critical strengths
  1. Relevant evaluation problem and clearly defined statistical framework.

The paper addresses a practical limitation of aggregate leaderboard reporting: model comparisons can depend substantially on the population of models being evaluated. The distinction between full-frame comparison, score-selected top-K cohorts, and uniformly sampled target cohorts provides a useful framework for separating different sources of variation.

  1. Broad empirical coverage and useful sensitivity analyses.

The analysis covers multiple benchmarks and 133 leaderboard snapshots. The authors provide explicit cohort constructions, threshold sensitivity experiments, finite-population arguments, and uncertainty-adjusted analyses. The distinction between selection-induced changes and sampling dispersion is useful, and the proposed reporting protocol could improve the transparency of benchmark comparisons.

Critical weaknesses
  1. The central claims about practical model selection are not adequately supported by the proposed evaluation metric.

The most important concern is the mismatch between the empirical quantity measured in the paper and the practical conclusions drawn from it.

Cohort-conditional separation measures the fraction of model pairs whose recorded scores differ by more than a fixed threshold. This is a descriptive statistic of score dispersion, not a direct measure of model-selection accuracy, benchmark validity, statistical distinguishability, or downstream deployment utility.

More importantly, the paper defines the "winner" as the benchmark achieving the highest separation rate, rather than the model that would perform best for a particular deployment task. Consequently, the reported 53.1% winner agreement among five-model cohorts does not establish that selecting the best model from a shortlist is close to random chance.

The interpretation of chance-level performance also requires stronger justification. Four benchmarks are compared, and Figure 2(b) includes both a uniform-guess baseline and a modal frame-winner baseline. The text nevertheless emphasizes agreement with 50% without adequately establishing why this constitutes the appropriate chance reference.

Furthermore, the sampled candidate cohorts are uniformly random subsets of leaderboard models. Real deployment shortlists are typically selected under correlated constraints involving cost, latency, licensing, and application requirements. No actual deployment shortlists or downstream model-selection outcomes are evaluated.

These limitations substantially weaken the paper's main practical claims and its asserted implications for enterprise model selection.

  1. Internal empirical inconsistencies, limited methodological novelty, and insufficiently controlled comparisons.

There appears to be a significant inconsistency between Figure 2(b) and the numerical results reported in the text. The plotted observed agreement for target size five appears to be approximately 66%, whereas the figure caption, Section 5.3, and conclusion report 53.1%. This discrepancy directly affects the paper's central claim about near-chance agreement and should be resolved before the empirical conclusions can be considered reliable.

The comparison across target-set sizes also changes the eligible-date population. Size-five cohorts are evaluated across 133 dates, while size-50 cohorts are evaluated across only 25 dates. Therefore, the reported improvement in agreement from 53.1% to 95.4% combines changes in cohort size with changes in the evaluated snapshot population. A matched-date comparison is needed to isolate the effect of cohort size.

The methodological novelty is also somewhat limited. The propositions largely formalize established consequences of conditioning on a selected population, range restriction, and finite-population sampling. These mathematical observations are valid, but their independent contribution is modest without stronger evidence connecting them to consequential model-selection decisions.

Finally, the operational threshold of three percentage points does not establish statistical distinguishability. The uncertainty analysis substantially reduces the reported separation rates for GPQA and MUSR, yet the main selection and agreement conclusions are not reevaluated under the same uncertainty-adjusted criterion.

Overall, the paper presents a coherent descriptive framework but does not sufficiently establish the broader practical implications claimed in its abstract and conclusion.

Questions for authors
  1. Numerical consistency and winner-agreement baseline. Could the authors reconcile the approximately 66% observed agreement shown at target size five in Figure 2(b) with the 53.1% reported in the figure caption and main text? Please provide the underlying numerical values, clarify the modal and uniform-guess baselines, and report how often the deterministic tie-breaking rule changes the benchmark winner.

  2. Connection to actual model-selection decisions. Since the reported winner identifies the benchmark with the highest separation rather than the best-performing model, what evidence supports the claim that leaderboard-based top-model selection approaches chance performance? Can the authors evaluate actual model-ranking accuracy, selection regret, or task-specific deployment shortlists?

  3. Controlled evaluation of cohort size and measurement uncertainty. Could the authors repeat the target-size comparisons using the same eligible snapshot dates across all cohort sizes? Additionally, do the main top-K compression and benchmark-winner conclusions remain robust when incorporating the archived per-model standard errors, particularly for GPQA and MUSR?

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

BarySLAM addresses collaborative SLAM with independently reconstructed Gaussian submaps. It extracts field-based structural observations, constructs a partially supported consensus atlas through unbalanced optimal transport, and jointly refines submap poses and atlas geometry. Held-out-agent validation screens associations, and consensus responsibilities regulate Gaussian opacities during map construction. Evaluation covers ReplicaMultiagent, AriaMultiagent, component ablations, and controlled robustness tests.

Critical strengths
  1. A geometric interface suited to independently optimized Gaussian maps. The localized field moments retain position and anisotropic shape without assuming one-to-one splat correspondences. the closed-form construction and rigid-motion equivariance provide a principled geometric interface for jointly estimating submap poses and consensus geometry.

  2. Explicit treatment of partially shared structure. Source-capacitated transport allows unmatched evidence to remain private, while supported atlas regions jointly constrain multiple submaps. Transferring these responsibilities to opacity control gives the shared/private distinction a concrete mapping role.

Critical weaknesses
  1. The predictive gate is insufficiently specified statistically. Eqs. (47)–(49) do not clearly connect whitening, agent-balanced weights, and statistical precision, or explain residual covariance construction and cross-covariance treatment. This limits reproducibility and assessment of the gate. These are unresolved modeling assumptions, rather than established mathematical errors, particularly given the conditional approximation and empirical calibration in D.3–D.5.

  2. Experimental attribution and reporting remain incomplete. Table 6’s backend baselines lack precise implementation details, and Table 4 does not isolate consensus-derived attenuation from simpler opacity controls. Sensitivity to submap partition and internal drift is untested, and Table 9 lacks workload-dependent scaling. G.3 also references absent main-text distribution plots and fixed-state numerical results, limiting scrutiny of the fusion-order claims.

Questions for authors
  1. In Eqs. (47)–(49), What noise or working-likelihood model connects normalized agent balancing to anchor covariance? How is Σres\Sigma^{res} constructed, and why can tested-observation/anchor cross-covariance be omitted conditional on the current state? Please distinguish model assumptions from approximations.

  2. Please identify the frontend, baseline implementations, robust estimation settings, budgets, and rerun versus published results in Tables 1–3 and 6. Can the fixed-pose CGC comparison include simple shared-opacity normalization to distinguish responsibility-specific gains from attenuation alone?

  3. Do the two BBA-based variants in Table 8 share identical poses for each permutation? If only consolidation differs, why do their ATE values differ? Please also provide the distribution plots and fixed-state deviations referenced in G.3 and the unreported perturbation severities declared in Table 5.

Reviewer_QDNrOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper proposes a method that transforms the matching of unstable Gaussians across agents into an abstract, stable geometric matching, thereby making the fusion of Gaussian submaps across multiple agents more precise. For the entire system, they propose a specific method for transforming Gaussians into sub-agent consensus, as well as a specific method for verifying this consensus.

Critical strengths

The paper proposes a comprehensive multi-map fusion method in a SLAM setting and provides a thorough analysis of the impact of Gaussian random states on the sequential fusion of submaps in a multi-agent SLAM system.

Critical weaknesses

This work requires more extensive experiments to test the validity of its theory. The ablation experiments for this method are based on synthetic datasets and do not prove that the same conclusions can be drawn in real-world scenarios. Additionally, the method may be overfitted to the limited dataset. More similar datasets with millimeter-level trajectory accuracy need to be created. For example, trajectories could be segmented into multiple segments to represent different agents. The fact that hyper-parameters remain consistent across these two similar scenarios does not imply that this consensus system will work equally well in larger indoor scenarios.

Furthermore, the authors claim that their proposed method is based on Gaussian maps. Interestingly, however, the method appears to rely solely on a single baseline: Gaussian SLAM. It is questionable whether these modules can be treated as a separate contribution that functions as a transferable module. Do these modules depend on the settings of Gaussian SLAM? Alternatively, could they benefit from improved Gaussian reconstruction methods to achieve more accurate reconstruction even in fewer overlap settings?

The ATE evaluation is also limited to synthetic datasets, where it demonstrates greater improvements. On real-world datasets, however, the improvements are modest, and its R1 score is inferior to that of MAGS-SLAM. Does this imply that, when encountering complex real-world textures, this module may not always be state-of-the-art?

The reconstruction results for the two real-world sequences appear to be state-of-the-art. However, could you provide a table analyzing hyper-parameters for different numbers of GS rendering iterations and compare them with recent work? It would be even better if FPS could be compared as well. If the system budget is really aligned, would the system remain SOTA?

In summary, this paper should conduct experiments on a more diverse set of datasets.

Questions for authors

The ablation experiments for this method are based on synthetic datasets and do not prove that the same conclusions can be drawn in real-world scenarios. Additionally, the method may be over-fitted to the limited dataset. More similar datasets with millimeter-level trajectory accuracy need to be created. For example, trajectories could be segmented into multiple segments to represent different agents. The fact that hyper-parameters remain consistent across these two similar scenarios does not imply that this consensus system will work equally well in larger indoor scenarios.

Furthermore, the authors claim that their proposed method is based on Gaussian maps. Interestingly, however, the method appears to rely solely on a single baseline: Gaussian SLAM. It is questionable whether these modules can be treated as a separate contribution that functions as a transferable module. Do these modules depend on the settings of Gaussian SLAM? Alternatively, could they benefit from improved Gaussian reconstruction methods to achieve more accurate reconstruction even in fewer overlap settings?

Could you provide a table analyzing hyper-parameters for different numbers of GS rendering iterations and compare them with recent work? It would be even better if there were an FPS comparison table. If the system budget is really aligned, would the system remain SOTA?

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

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