Real-Time Underwater Acoustic Target Detection with DEIMv2: Benchmarking, Weighted-Box-Fusion Test-Time Augmentation, and Domain Shift Analysis on the UATD Dataset

1. Introduction

Reliable perception of underwater scenes is a prerequisite for autonomous underwater vehicles (AUVs) and remotely operated vehicles (ROVs) performing rescue, infrastructure inspection, and biological surveys. Because optical cameras degrade severely in turbid water, multibeam forward-looking sonar (MFLS) has become the dominant sensor for short-range underwater perception. MFLS imagery, however, differs fundamentally from natural images: targets appear as low-resolution intensity blobs with weak edges, acoustic speckle and multipath interference introduce heavy noise, and the appearance of the same object category changes dramatically across water bodies, depths, and mounting geometries.

Deep-learning-based detectors have been widely adopted for sonar imagery since the release of public benchmarks such as the Underwater Acoustic Target Detection (UATD) dataset [1], which provides more than 9,000 annotated MFLS images of ten object categories together with a reproducible Faster R-CNN/YOLOv3 benchmark. Subsequent work has largely refined two-stage detectors (Faster R-CNN, Mask R-CNN) or single-stage YOLO variants. Meanwhile, the computer-vision community has moved toward real-time detection transformers (RT-DETR [2], DEIM [3], D-FINE [4]). The most recent of these, DEIMv2 [5], couples an improved DETR training framework with DINOv3 [6] foundation-model features through a Spatial Tuning Adapter (STA) and currently leads the accuracy–latency trade-off on COCO. Very recently, and largely in parallel with our work, DETR-family detectors and foundation-model features have begun to enter the sonar domain: MSF-DETR [7] and T2C-DETR [8] modify the RT-DETR architecture for small-target sonar imagery, FS2-DETR [9] adapts an RT-DETR-style detector to few-shot sonar detection on an enhanced UATD partition, Jia et al. [10] use DINOv3 features as a spatial-prior guidance module for few-shot side-scan detection, and Mine-JEPA [11] reports that for side-scan mine classification, in-domain self-supervised pretraining can outperform fine-tuned DINOv3. Note, however, that FS2-DETR [9] has already evaluated an RT-DETR-style detector on UATD — in a few-shot setting on its own enhanced re-partition of the dataset — so a “first DETR-family evaluation on UATD” can no longer be claimed. What remains missing, and what this paper provides, is a systematic and fully specified evaluation of the current real-time DETR generation on this benchmark under a reproducible, dual-test-split protocol: the complete DINOv3 + STA DEIMv2 framework rather than earlier RT-DETR variants or DINOv3 as a bolt-on component, a set of same-protocol baselines that earlier comparisons lacked, and a deeper quantitative analysis of the domain shift that governs test-set performance.

In this paper we address this gap with three contributions, ordered by the strength of their empirical support:

(1) A reproducible DEIMv2 benchmark on MFLS imagery, with same-protocol baselines and an honest accuracy statement. We fine-tune DEIMv2-S and DEIMv2-M on UATD under a fully specified, reproducible protocol (three training configurations, 40–80 epochs, exact hyperparameters released, three random seeds for the headline configuration) and report COCO-style metrics on both official test splits. Whereas the parallel works above adapt earlier RT-DETR variants [7,8,9] or employ DINOv3 only as an auxiliary feature-guidance module [10], this is, to our knowledge, the first systematic evaluation of a current-generation DETR framework—the complete DEIMv2 stack (DINOv3 backbone + STA + DEIM training objective)—under the official dual-test-split protocol of the largest public MFLS benchmark. Training four additional detectors (RT-DETR-R18, D-FINE-S, DEIM v1-S, YOLOv8-S) under the identical pipeline gives a result that we report as measured: on the strict mAP@[.5:.95] the four query-based detectors are statistically indistinguishable (37.3–38.2%), while on mAP@0.5 the earlier DETR generations lead DEIMv2-S by 3.3–4.1 points on Test_1 and 1.3–2.0 points on Test_2, a gap that exceeds our three-seed variation. The practical case for DEIMv2 on this benchmark therefore rests on training efficiency (a 40-epoch schedule, roughly one third of the standard RT-DETR budget), single-view real-time inference, and the TTA behavior below, not on a raw-accuracy margin (Section 4.3). A 512-pixel control run reaches 83.9% mAP@0.5 on the Test_2 split, equal to the official Faster R-CNN figure on that subset, although its combined-protocol estimate (≈82.3%) remains below the official number (Section 4.3).

(2) A model-specific test-time augmentation finding, with a complete ablation and statistical robustness checks. In our setting, naive NMS-based fusion of augmented predictions yields no gain for query-based detectors, whereas weighted-boxes-fusion (WBF) of multi-scale (0.75×/1.0×/1.25×) and horizontally flipped predictions improves DEIMv2-S mAP@0.5 by +1.4/+2.1 points, bringing it to 81.3%/84.4%. Applying the identical recipe to RT-DETR-R18 and D-FINE-S degrades their accuracy (down to −4.8 points), so the gain is a property of the detector–fusion pairing, not a generic post-processing trick. A view-type decomposition attributes the gain almost entirely to the multi-scale views; the WBF IoU threshold is flat over τ ∈ [0.50, 0.65]; and the +2.1-point Test_2 gain is larger than the three-seed standard deviation (±0.8). We report the trade-off explicitly: the gain costs 6.4–6.5 points of AR@100, so WBF TTA is a deployment-relevant recipe for precision-oriented survey processing and a caution against fusion in miss-critical applications.

(3) A quantitative domain-shift analysis of UATD, with direct evidence. We demonstrate that the validation and test partitions differ substantially in class priors (e.g., metal bucket 3.8% → 0.5%; ROV 5.6% → 12.8%; Jensen–Shannon divergence between train and test priors is ~50× larger than between train and val, with bootstrap confidence intervals that exclude the train–val range) and object-size distribution (large objects 5.8% → 11.1%/10.5%). We argue, with the correct metric mechanism in mind, that the shifted priors do not by themselves lower mAP (an unweighted per-class average) but are evidence that the test partitions were collected at different survey sites, and that the accompanying appearance shift is consistent with most of the 12–16-point gap between validation (~96% mAP@0.5) and test (~80–84%) performance. Two direct checks support this reading: every category reaches ≥ 93.4% AP@0.5 on the validation partition, so no category is intrinsically hard; and matching test images to the training intensity distribution by histogram matching does not recover test accuracy, so the shift is not a global tone difference. This analysis delineates the realistic accuracy envelope for supervised detectors on this benchmark and motivates domain-adaptive approaches for future work.

2. Related Work

2.1. Object Detection in Sonar Imagery

Public sonar datasets are scarce; UATD [1] remains the most widely used MFLS detection benchmark, with ten categories (ball, circle cage, cube, cylinder, human body, metal bucket, plane, ROV, square cage, tyre) collected in lake and shallow-water environments. Its official benchmark reports a best mAP@0.5 of 83.9% with Faster R-CNN [12] (ResNet-18) and demonstrates that lightweight YOLOv3 variants [13] trade accuracy for speed [1]. Follow-up studies have refined these CNN baselines with attention modules, feature-pyramid modifications, and re-weighting schemes. The most directly comparable published follow-up is FS2-DETR [9], which adapts an RT-DETR-style detector to few-shot sonar detection on an enhanced re-partition of UATD; because its k-shot protocol on its own data split is not comparable to the official dual-test-split benchmark, to the best of our knowledge, no published RT-DETR baseline under the official protocol exists, and we therefore train RT-DETR-R18, D-FINE-S, DEIM v1-S, and YOLOv8-S ourselves under our exact 640×640 pipeline (Section 4.3, Table 3).

Most recently, several works developed in parallel with ours have brought DETR-family detectors and foundation-model features into the sonar domain; we therefore delineate how they differ from the present study. MSF-DETR [7] equips RT-DETR with a spatial–frequency Mamba-enhanced backbone, a hierarchical adaptive feature pyramid, and a sparse-attention encoder for small-target side-scan detection, evaluated on a self-built dataset and the public KLSG data. T2C-DETR [8] adds a Transformer–convolution dual-channel backbone and a noise-filtering module to RT-DETR, evaluated on a self-built three-class dataset under three pre-training sources. FS2-DETR [9] targets few-shot sonar detection with feature-enhancement and visual-prompt modules on an enhanced UATD partition, the closest setting to ours, but is concerned with sample-scarce adaptation of an RT-DETR-style detector on its own re-partitioned data rather than full-data benchmarking of the current-generation framework under the official dual-test-split protocol. All three modify the detector architecture or the training regime; to the best of our knowledge, none evaluates the unmodified current-generation real-time DETR framework (DEIMv2, i.e., DINOv3 backbone + STA + DEIM training) on the full UATD protocol with both official test splits. On the foundation-model side, Jia et al. [10] use a pre-trained DINOv3 to produce spatial-distribution probability maps that guide a Transformer-based detector for few-shot side-scan imagery; DINOv3 enters as an auxiliary prior module, not as the detection backbone trained end-to-end. Complementing this line of work, Mine-JEPA [11] shows that for side-scan mine classification, in-domain self-supervised pretraining on only ~1,170 images can outperform fine-tuned DINOv3, a cautionary data point on the limits of natural-image foundation features that our end-to-end MFLS detection study directly probes.

2.2. Real-Time DETR-Family Detectors

DETR [14] reframed detection as set prediction but suffered from slow convergence; Deformable DETR [15] addressed its attention complexity and small-object weakness with multi-scale deformable attention, and DN-DETR [16] traced much of the convergence problem to unstable bipartite matching, stabilizing it with denoising queries. RT-DETR [2] introduced an efficient hybrid encoder and made DETR architectures real-time; D-FINE [4] redefined box regression as fine-grained distribution refinement (FGL loss); DEIM [3] accelerated convergence with Dense One-to-One matching and Matchability-Aware Loss. DEIMv2 [5] integrates DINOv3 [6] features through a Spatial Tuning Adapter that converts the single-scale ViT output into the multi-scale features required for detection, offering eight model sizes from 0.49M to 50M parameters and setting new state-of-the-art results on COCO [17] across all resource settings. Because sonar imagery differs so strongly from natural images, whether foundation-model features transfer to this modality is an open empirical question that our study answers in the affirmative. A more detailed reconstruction of this lineage is given in Supplementary Section S1.

2.3. Test-Time Augmentation

TTA averages predictions over transformed copies of the input and is a cheap, model-agnostic accuracy booster. For two-stage and single-stage detectors, fusion is typically performed with non-maximum suppression (NMS) or weighted boxes fusion (WBF) [18], the latter averaging coordinates of matched boxes weighted by confidence rather than discarding them. DETR-family detectors already produce a small, NMS-free set of ranked queries, and naive NMS fusion of augmented predictions is known to risk discarding correct low-score boxes. We therefore compare NMS and WBF fusion explicitly for a DETR-family detector on sonar data, and we further test whether the same fusion recipe transfers to other query-based detectors; to our knowledge neither comparison has been reported before in the underwater domain.

3. Methodology

3.1. Why DEIMv2 for Sonar

The choice of detection paradigm matters more for sonar than for natural images, because MFLS targets lack the sharp edges and rich texture that anchor-based detectors implicitly rely on. Among real-time detectors, DEIMv2 uniquely combines three properties that match this regime: (i) NMS-free set prediction with bipartite matching [14,19], which sidesteps the score-threshold fragility of NMS on low-contrast blobs; (ii) distribution-based box refinement (FGL [4,20]) and IoU-aligned classification (MAL [3]), which suit faint, ambiguous boundaries and rank confidence by localization quality at inference; and (iii) DINOv3 foundation-model features [6] (trained on 1.7B unlabeled images and known to transfer to modalities with weak texture priors) bridged to the multi-scale encoder by a lightweight Spatial Tuning Adapter (STA) [5]. A step-by-step reconstruction of the DETR → Deformable DETR → DN-DETR → RT-DETR → D-FINE/DEIM → DEIMv2 lineage, with the specific problem solved at each step, is deferred to Supplementary Section S1; here we keep only the architecture (Section 3.2), the matching and loss skeleton (Section 3.3 and Section 3.4), and our TTA fusion strategy (Section 3.5), which is the methodological focus of this paper.

3.2. DEIMv2 Architecture

We adopt the official DEIMv2 implementation [5]. The architecture follows the RT-DETR blueprint with four components (Table 1 lists the exact dimensions of the two variants we evaluate):

• Backbone. A distilled DINOv3 ViT backbone: ViT-Tiny (embed dim 192, 12 layers, 3 attention heads in the STA interaction blocks) for DEIMv2-S and ViT-Tiny+ (embed dim 256, 4 heads) for DEIMv2-M. Features are tapped at blocks 3, 7, and 11.
• Spatial Tuning Adapter (STA). The single-scale ViT token grid is converted into a three-level feature pyramid at strides {8, 16, 32} (channels 192 for S, 256 for M), providing the multi-scale inputs that the encoder requires.
• Hybrid encoder. One intra-scale attention layer on the stride-32 level plus CNN-style cross-scale fusion (hidden dim 192, depth multiplier 0.67, expansion 0.34 for S; 256/1.0/0.67 for M; feed-forward dim 512).
• Transformer decoder. Four decoder layers with hidden dim 192 (S) / 256 (M), N = 300 object queries, deformable cross-attention with sampling points [3,6] over the three levels, and iterative box refinement with a per-edge distance distribution over reg_max = 32 bins (reg_scale 4). During training the decoder additionally receives 100 denoising queries (label noise ratio 0.5, box noise scale 1.0) following DN-DETR [16].

Training uses the DEIM objective, i.e., matchability-aware loss (MAL), fine-grained localization (FGL), and GIoU losses, with Dense O2O auxiliary supervision (Section 3.3 and Section 3.4). All models are initialized from the official COCO-pretrained checkpoints, which already contain the DINOv3 backbone weights, and fine-tuned end-to-end on UATD. At inference the top-300 query outputs are emitted directly without NMS.

3.3. One-to-One Label Assignment

Let $\widehat{y}=\left\{\right(z_i,b_i){\}}_{i=1}^N$ denote the decoder’s N = 300 predictions, where z_i∈ℝ^K are class logits over K = 10 categories and b_i∈[0,1]⁴ are normalized (c_x,c_y,w,h) boxes, and let $y=\left\{\right(c_j,{\widehat{b}}_j){\}}_{j=1}^M$ be the ground-truth set of an image. DETR-family training first finds a one-to-one assignment between predictions and targets by solving a linear sum assignment problem (LSAP) with the Hungarian (Kuhn–Munkres) algorithm [19]:

$${\sigma }^{*}=\mathit{arg}\underset{\sigma \in \mathfrak{S}}{\mathit{min}}\sum _{i}C\left(i,\sigma \left(i\right)\right), C\left(i,j\right)=2\hspace{0.17em}{C}_{\mathrm{cls}}\left(i,j\right)+5\hspace{0.17em}{C}_{\mathrm{L}1}\left(i,j\right)+2\hspace{0.17em}{C}_{\mathrm{giou}}\left(i,j\right),$$

(1)

where the classification, L1, and GIoU cost terms and their weights (2, 5, 2) follow the official DEIMv2 recipe (full definitions in Supplementary Section S2). From epoch e_m onward (e_m = 30 for our 40-epoch runs, e_m = 60 for the 80-epoch run), the matcher switches to a unified IoU-aware cost

$$C(i,j)=-\hspace{0.17em}{p}_{\mathit{ij}}\cdot \mathit{IoU}(b_i,{\widehat{b}}_j{)}^{{\alpha }_{\mathrm{ord}}}, {\alpha }_{\mathrm{ord}}=4,$$

(2)

so that a query can only win a target if it is simultaneously confident and well localized; p_ij is the predicted probability of the target class. Finally, Dense O2O supervision [3] raises the density of matched positives per training sample through strong composition augmentation (mosaic, mixup, copy-blend; Section 4.2) while preserving the one-to-one constraint, and hence the NMS-free inference property. Complementary denoising queries [16] stabilize early training. The full derivations, including the focal classification cost [21] and a discussion of why vanilla one-to-one matching starves the decoder on UATD (1.6 instances/image), are given in Supplementary Section S2, Equations (S1)–(S3).

3.4. Training Objective

Given the assignment of Equation (1) (or Equation (2) after epoch e_m), the model is optimized with a weighted sum of five loss terms:

$ℒ$ = λ_mal $ℒ$_MAL + λ_L1 $ℒ$_L1 + λ_giou $ℒ$_GIoU + λ_fgl $ℒ$_FGL + λ_ddf $ℒ$_DDF,

(3)

with (λ_mal,λ_L1,λ_giou,λ_fgl,λ_ddf) = (1,5,2,0.15,1.5) and deep supervision at every decoder layer. In brief: MAL [3] replaces the hard 0/1 classification target with an IoU-derived soft target $u_{\mathit{ij}}^{1.5}$, so that the confidence score is ranked by localization quality at inference; L1 and GIoU [22] supervise box coordinates, the latter keeping a non-zero gradient for disjoint boxes; FGL [4,20] regresses each box edge as a discrete distribution over reg_max = 32 bins and supervises only the two bins adjacent to the continuous target, letting the network express boundary uncertainty; and DDF [4] is a self-distillation term that aligns the edge distributions of shallow decoder layers with the final layer. The complete formulations and their sonar-specific gradient properties are derived in Supplementary Section S3, Equations (S4)–(S7).

3.5. Weighted-Boxes-Fusion Test-Time Augmentation

At test time we run inference on V = 6 views of each image: scales {0.75×,1.0×,1.25×} of the 640-px network input, each with and without horizontal flip. Boxes from flipped views are mirrored back, and boxes from scaled views are mapped to original image coordinates. Multi-scale inference uses dynamic positional embeddings (the fixed 640×640 evaluation spatial size is relaxed, enabling the training-path dynamic anchor/position generation). Each view contributes its top-300 query outputs; the 6 × 300 candidates are fused per class.

3.5.1. Fusion Rules

NMS sorts all candidates by score and iteratively keeps the highest-scoring box while discarding all boxes of the same class with IoU ≥ τ (τ = 0.55; no score threshold is applied, so all 300 query outputs of each view enter the fusion). WBF [18] instead clusters matching boxes and averages them. In our implementation, candidates are processed in descending score order; the current top box b seeds a cluster $𝒞$ = {i:IoU(b_i,b) ≥ τ}, and the cluster is replaced by a single fused detection

$$b^{*}={\displaystyle \frac{\sum _{i\in \mathcal{C}}{s}_i\hspace{0.17em}{b}_i}{\sum _{i\in \mathcal{C}}{s}_i}}, s^{*}={\displaystyle \frac{1}{V}}\sum _{i\in \mathcal{C}}{s}_i,$$

(4)

where s_i are the member confidences. The WBF cluster-IoU matching threshold is τ = 0.55 throughout, unless stated otherwise; a sensitivity analysis over τ∈{0.50,0.55,0.60,0.65} is reported in Section 4.5. The fused score grows with both the member confidences and the number of confirming views ($s^{*}\approx \bar{s}\cdot \left|\mathcal{C}\right|/V$): a detection found by all six views is scored roughly six times higher than an equally confident single-view detection, which implements an explicit multi-view confirmation mechanism.

3.5.2. Why WBF Suits Sonar Imagery

Two properties of MFLS images make Equation (4) preferable to NMS. First, speckle and multipath make single-view confidences noisy: the same target may rank first at scale 1.0× but only third at 1.25×. NMS keeps whichever copy happens to score highest and erases the others, importing the full variance of the noisiest view; WBF treats the views as independent noisy measurements of the same box and averages them, reducing the variance of the coordinate estimate. Second, low-contrast targets produce heavy-tailed box offsets, and several correct-but-sub-threshold candidates typically surround a true target; NMS suppresses them, whereas WBF’s cluster score rewards exactly this repeated weak evidence. Set against these advantages, WBF has two known costs, which our experiments quantify (Section 4.5): confidence-weighted averaging slightly blurs coordinates (mAP@0.75 decreases marginally), and singleton low-score clusters are de-emphasized, reducing AR@100. Whether this is a worthwhile trade depends on the operating metric and the application: for the mAP@0.5-oriented UATD benchmark it is favorable, but for miss-critical tasks (e.g., ROV/AUV obstacle avoidance, where a missed target is costlier than a false alarm) the recall loss may dominate, and we flag this explicitly in the abstract and conclusions.

4. Experiments

4.1. Dataset and Metrics

UATD [1] provides Train (6,840 images / 11,074 instances), Val (760 / 1,222), and two official test partitions, Test_1 (800 / 1,170) and Test_2 (800 / 1,157), over ten categories. Images are 512–1024 px wide and 1024–2047 px tall. We report COCO-style mAP@[.5:.95] (denoted strict mAP in what follows) and mAP@0.5, the metric used by the official UATD benchmark [1], plus per-size AP (small/medium/large) and AR@100, computed with the same evaluation code path as the training engine, namely faster-coco-eval [23] (a drop-in, faster reimplementation of the official pycocotools COCOeval that produces identical statistics), so that validation and test numbers are strictly comparable. Per-class numbers in Section 4.4 are computed from the released prediction files with identical settings. One pipeline-level difference from the official protocol deserves emphasis: the official benchmark resizes the image height to 512 px and scales the width proportionally, whereas we resize to a 640×640 square; for images up to 2047 px tall this compresses the long dimension by up to ~3× and introduces aspect-ratio distortion, which is itself a potential split-dependent confound that we discuss in Section 5 and control for with a 512-input ablation (Section 4.3).

4.2. Implementation Details

4.2.1. Training

We fine-tune with AdamW [24] (betas (0.9, 0.999), weight decay 1e-4, no decay on norms/biases), a 2,000-iteration linear warm-up (flat-cosine schedule: flat phase until flat_epoch, then cosine decay with gamma_lr = 0.5), and gradient clipping at 0.1. The DINOv3 backbone branch uses a reduced learning rate (0.25× the base rate) to preserve foundation features. An exponential moving average of the weights (ModelEMA decay 0.9999 with a 1,000-step warm-up) is used for all evaluations. All runs use mixed precision on a single RTX 5070 Ti Laptop GPU (12 GB). Three configurations are evaluated (Table 2 and Table 3): S-r1 (DEIMv2-S, batch 4, lr 5e-5, 40 epochs); S-r2 (DEIMv2-S, batch 8, lr 1e-4, 80 epochs, augmentation schedule proportionally rescaled); and M (DEIMv2-M, otherwise identical to S-r1). The best checkpoint by validation strict mAP is used for all test evaluations. The headline S-r1 configuration is trained with three random seeds (42/43/44); seed 42 is the primary run reported throughout, and the seed statistics are given in Table 4.

Table 3. Results on UATD (mAP@0.5 / strict mAP, %). Best per column in bold. Baselines are shown at their best measured operating point (see footnotes).

Model	Val mAP@0.5	Val strict mAP	Test_1	Test_1 + WBF TTA	Test_2	Test_2 + WBF TTA
Faster R-CNN R-18 (official [1])	—	—	—	—	—	—
RT-DETR-R18 (B1, same protocol)¶	—	—	84.0 / 37.7	81.5 / 36.3	83.8 / 37.9	83.8 / 37.5
D-FINE-S (B2, same protocol)¶◇	—	—	83.2 / 37.7	78.3 / 34.8	83.6 / 37.3	79.8 / 36.2
DEIM v1-S (B3, same protocol)¶◇	—	—	83.3 / 37.7	—	84.3 / 37.6	—
YOLOv8-S (B4, same protocol)¶	—	—	78.2 / 33.7	—	79.9 / 33.5	—
DEIMv2-S (S-r1)	96.0	59.3	79.9 / 37.7	81.3 / 37.7	82.3 / 38.2	84.4 / 38.5
DEIMv2-S (S-r2, 80 ep)	—	59.9	78.4 / 37.4	—§	81.0 / 37.8	—§
DEIMv2-M	—	60.4	80.3 / 37.2	81.3 / 37.5	83.4 / 38.3	83.4 / 38.5

The official Faster R-CNN benchmark [1] reports 83.9% mAP@0.5 on the combined Test_1+Test_2 protocol with the image height resized to 512 (width scaled proportionally); it is therefore not placed in any single-split column. ¶Trained and evaluated by us under the identical 640×640, 40-epoch pipeline (Section 4.2). Each baseline is shown at its best measured operating point, which for all four is single-view inference: the effect of our WBF TTA on B1 and B2 was measured and is neutral to negative (Table 7), so single-view numbers are their favorable column. ◇B2 and B3 were trained from scratch (official HGNetv2 pretraining unreachable in our environment); their mAP@0.5 lead over the pretrained DEIMv2-S is, if anything, understated. Val mAP@0.5 for S-r1 is the training-engine figure; re-evaluation with the released prediction pipeline gives 97.7 with identical strict mAP (59.3), the difference tracing to the evaluation code path (Section 5). Val mAP@0.5 was not re-measured for the baselines; all models used the validation split for checkpoint selection. The final validation mAP@0.5 is reported only for S-r1; the validation strict mAP values of S-r2 and M (at their selected checkpoints) are given in Table 2 and Table 3. The two Val columns are reported for reference only: they are the figures of the checkpoints selected on the validation split during training (the validation split serves exclusively as the model-selection split) and do not constitute the final evaluation protocol; the final evaluation numbers are those on the official Test_1/Test_2 partitions. §TTA was not run for S-r2 because this configuration is superseded: it overfits the validation distribution (higher val, lower test; Section 4.3), so its TTA numbers are not decision-relevant.

Table 3. Results on UATD (mAP@0.5 / strict mAP, %). Best per column in bold. Baselines are shown at their best measured operating point (see footnotes).

Model	Val mAP@0.5	Val strict mAP	Test_1	Test_1 + WBF TTA	Test_2	Test_2 + WBF TTA
Faster R-CNN R-18 (official [1])	—	—	—	—	—	—
RT-DETR-R18 (B1, same protocol)¶	—	—	84.0 / 37.7	81.5 / 36.3	83.8 / 37.9	83.8 / 37.5
D-FINE-S (B2, same protocol)¶◇	—	—	83.2 / 37.7	78.3 / 34.8	83.6 / 37.3	79.8 / 36.2
DEIM v1-S (B3, same protocol)¶◇	—	—	83.3 / 37.7	—	84.3 / 37.6	—
YOLOv8-S (B4, same protocol)¶	—	—	78.2 / 33.7	—	79.9 / 33.5	—
DEIMv2-S (S-r1)	96.0	59.3	79.9 / 37.7	81.3 / 37.7	82.3 / 38.2	84.4 / 38.5
DEIMv2-S (S-r2, 80 ep)	—	59.9	78.4 / 37.4	—§	81.0 / 37.8	—§
DEIMv2-M	—	60.4	80.3 / 37.2	81.3 / 37.5	83.4 / 38.3	83.4 / 38.5

The official Faster R-CNN benchmark [1] reports 83.9% mAP@0.5 on the combined Test_1+Test_2 protocol with the image height resized to 512 (width scaled proportionally); it is therefore not placed in any single-split column. ¶Trained and evaluated by us under the identical 640×640, 40-epoch pipeline (Section 4.2). Each baseline is shown at its best measured operating point, which for all four is single-view inference: the effect of our WBF TTA on B1 and B2 was measured and is neutral to negative (Table 7), so single-view numbers are their favorable column. ◇B2 and B3 were trained from scratch (official HGNetv2 pretraining unreachable in our environment); their mAP@0.5 lead over the pretrained DEIMv2-S is, if anything, understated. Val mAP@0.5 for S-r1 is the training-engine figure; re-evaluation with the released prediction pipeline gives 97.7 with identical strict mAP (59.3), the difference tracing to the evaluation code path (Section 5). Val mAP@0.5 was not re-measured for the baselines; all models used the validation split for checkpoint selection. The final validation mAP@0.5 is reported only for S-r1; the validation strict mAP values of S-r2 and M (at their selected checkpoints) are given in Table 2 and Table 3. The two Val columns are reported for reference only: they are the figures of the checkpoints selected on the validation split during training (the validation split serves exclusively as the model-selection split) and do not constitute the final evaluation protocol; the final evaluation numbers are those on the official Test_1/Test_2 partitions. §TTA was not run for S-r2 because this configuration is superseded: it overfits the validation distribution (higher val, lower test; Section 4.3), so its TTA numbers are not decision-relevant.

Table 4. Seed statistics for the headline configuration (S-r1, single-view inference, %; mean ± sample standard deviation over seeds 42/43/44).

Metric	seed 42	seed 43	seed 44	mean ± std
Test_1 mAP@0.5	79.9	80.5	81.4	80.6 ± 0.7
Test_1 strict mAP	37.7	37.9	38.0	37.9 ± 0.2
Test_2 mAP@0.5	82.3	83.8	83.3	83.1 ± 0.8
Test_2 strict mAP	38.2	38.9	38.3	38.5 ± 0.4

Table 4. Seed statistics for the headline configuration (S-r1, single-view inference, %; mean ± sample standard deviation over seeds 42/43/44).

Metric	seed 42	seed 43	seed 44	mean ± std
Test_1 mAP@0.5	79.9	80.5	81.4	80.6 ± 0.7
Test_1 strict mAP	37.7	37.9	38.0	37.9 ± 0.2
Test_2 mAP@0.5	82.3	83.8	83.3	83.1 ± 0.8
Test_2 strict mAP	38.2	38.9	38.3	38.5 ± 0.4

4.2.2. Same-Protocol Baselines

Four detectors serve as baselines under the identical data configuration, 40-epoch budget, and 640×640 protocol: RT-DETR-R18 [2] (B1), D-FINE-S [4] (B2), DEIM v1-S [3] (B3), and YOLOv8-S [25] (B4). B1 is initialized from its official ImageNet-pretrained PResNet-18 weights; B2 and B3 are trained from scratch because their official HGNetv2 ImageNet pretraining could not be retrieved in our environment, a handicap we flag wherever their numbers are used; B4 starts from COCO-pretrained weights. The only optimizer difference between B1 and the DEIMv2 runs is the EMA warm-up (2,000 versus 1,000 steps, each following its official configuration); learning rate, weight decay, and the LR schedule are identical. All four are evaluated with the same faster-coco-eval code path as DEIMv2.

4.2.3. Data Augmentation

The pipeline follows the official DEIMv2 recipe with the schedule compressed to our epoch budget: mosaic (output size 320, rotation ±10°, translation ±0.1, scaling 0.5–1.5, probability 1.0) until the second augmentation node; random photometric distortion (probability p = 0.5); random zoom-out; random IoU crop (probability p = 0.8); random horizontal flip; resize to 640×640. Between the first and last nodes, mixup (probability p = 0.5) and copy-blend (probability p = 0.5, up to 3 objects per image, area threshold 100 px²) realize the Dense O2O target-density increase (Section 3.3); augmentation is disabled for the final no_aug_epoch epochs. Category indices were remapped to a contiguous 0-based range; boxes are sanitized (min size 1 px) after each geometric transform.

4.2.4. Evaluation Protocol

Validation and test evaluation resize images to 640×640 with ImageNet normalization, mirroring the training-time input pipeline. The wall-clock figures below describe DEIMv2’s own inference pipeline only; they do not represent a matched-conditions latency comparison with other methods. Single-view inference in our unoptimized Python evaluation loop (including preprocessing and resizing) takes 58–76 ms per image on the RTX 5070 Ti Laptop GPU, i.e., roughly 13–17 frames per second. These wall-clock numbers include data loading and pre-/post-processing overhead and therefore characterize the evaluation pipeline rather than the model itself; we use them only to establish single-view real-time operation. The six-view TTA costs ~0.7–1.2 s per image in the same loop and is intended for accuracy-critical offline survey processing rather than online control. For reference, the official benchmark’s efficiency-optimized model (YOLOv3-MobileNetV2) reports 3.68M parameters, 4.22 GFLOPs, and 93.4 FPS at 512-px input on a GTX 1080 [1], while the official top-accuracy model (Faster R-CNN R-18) is a two-stage detector without real-time operation; our DEIMv2-S has 9.7M parameters and sits between the two in the accuracy–latency plane (Section 4.3).

4.3. Main Results

4.3.1. Comparison Protocol and Fairness

Three protocol differences must be stated when comparing with the official 83.9%: (i) the official benchmark resizes the image height to 512 with proportional width, whereas our pipeline feeds 640×640 square inputs; a larger input is standard practice and we do not claim an architectural advantage from it, but the square resize also distorts aspect ratio (Section 4.1); (ii) the official figure is reported on the combined UATD test protocol, while we report Test_1 and Test_2 separately. Since the two test splits have nearly identical class priors (JS = 0.0001, Table 10), the combined-protocol mAP is well approximated by the split average: our best TTA result gives (81.3 + 84.4)/2 ≈ 82.9% < 83.9%, and the no-TTA average is ≈ 81.1%. We therefore do not claim to surpass the official benchmark; the correct statement is that our results are comparable to it: slightly above on Test_2 (84.4% vs. 83.9%) and below on Test_1 (81.3%). The same estimate for our same-protocol RT-DETR-R18 baseline is (84.0 + 83.8)/2 ≈ 83.9%, i.e., the official Faster R-CNN figure is matched by a modern real-time detector under our protocol as well, which supports reading 83.9% as the current benchmark’s accuracy plateau rather than a ceiling specific to two-stage detectors; (iii) the remaining Test_2 margin of our TTA result (0.5 points on ~1,157 instances) is within evaluation noise and would not survive a significance test, and WBF TTA is an inference-time cost (6 views). We consider the TTA-free results the primary like-for-like comparison. Under this reading, our main claim is conservative: a 40-epoch fine-tuned DEIMv2-S reaches the official benchmark class of performance without any test-time augmentation.

4.3.2. 512-Input Control

To separate the resolution difference from the architecture comparison, we retrained DEIMv2-S with 512×512 inputs under an otherwise identical protocol (D1). The control is evaluated at a single 0.8× scale of the 640-px evaluation base, i.e., exactly the 512-px training input size; its “TTA” row applies WBF over this single view (no flip, no additional scales), so it reduces to within-view de-duplication and is not comparable to the six-view {0.75, 1.0, 1.25} recipe of the 640 pipeline. The control reaches 80.7%/83.9% mAP@0.5 on Test_1/Test_2 (strict 36.7%/37.9%), and 80.7%/84.4% with single-view WBF. Three points follow, stated with the same protocol care as for the 640 results above. First, the Test_2 single-view figure equals the official Faster R-CNN benchmark number (83.9%) on that split, but the equality holds on Test_2 only: under the combined-protocol approximation used above, D1 gives (80.7 + 83.9)/2 ≈ 82.3% < 83.9%, so we do not claim parity with the official benchmark on the full test protocol. Note also that D1 feeds a 512×512 square resize, whereas the official pipeline resizes the image height to 512 with proportional width (Section 4.1), so D1 controls for the input budget, not for the exact official preprocessing. Second, the 512 control is not weaker than our 640 pipeline on mAP@0.5 (80.7/83.9 vs. 79.9/82.3), so the 640-vs-512 resolution difference is not what buys our accuracy; if anything the smaller, less distorting input helps mAP@0.5 while costing about one point of strict mAP. Third, the WBF gain replicates at 512 (+0.0/+0.5 mAP@0.5 from within-view de-duplication alone), though attenuated relative to the six-view recipe, consistent with the multi-scale views overlapping the input-scale change. We therefore keep D1 as auxiliary evidence and rest the “plateau” reading on the same-protocol B1 result above (combined-protocol estimate ≈83.9% with no protocol discount), which shows that the official figure is attainable by a modern real-time detector and does not represent an accuracy ceiling specific to two-stage models.

4.3.3. Comparison with Same-Protocol Baselines

Table 3 gives a picture that we report as measured, without selective presentation. On strict mAP@[.5:.95], the four query-based detectors are statistically indistinguishable: Test_1 strict mAP is 37.7% for all of them, and Test_2 ranges from 37.3% (D-FINE-S) to 38.2% (DEIMv2-S), within roughly one to two seed standard deviations (Table 4). On mAP@0.5 the ordering reverses: the three earlier DETR-family baselines (B2 and B3 trained from scratch; see Table 3, footnote ◇) reach 83.2–84.0% on Test_1 and 83.6–84.3% on Test_2, leading DEIMv2-S (79.9%/82.3%) by 3.3–4.1 and 1.3–2.0 points respectively. The Test_1 deficit is about five times our three-seed standard deviation, so it is a systematic property of this benchmark rather than seed noise. Two caveats frame the comparison: the from-scratch training of B2 and B3 means their lead is not an initialization artifact in their favor; and YOLOv8-S, the only anchor-based NMS detector in the set, trails on every metric (78.2%/79.9% mAP@0.5), confirming that the query-based design matters on this modality. What DEIMv2-S offers instead is convergence in 40 epochs against the 120-epoch standard RT-DETR schedule, single-view real-time inference, a strict-mAP profile equal to or better than every baseline (the DEIMv2 family holds the best Test_2 single-view strict numbers in Table 3, M at 38.3% and S at 38.2%), and a unique response to TTA (Section 4.5): with WBF TTA, DEIMv2-S reaches 84.4% on Test_2, matching the best baseline operating point within noise, while the same recipe degrades the baselines. Whether the remaining mAP@0.5 deficit traces to the DINOv3 features, the DEIM training strategy, or the shorter schedule cannot be separated by the present experiments; the from-scratch B3 (DEIM v1-S, 83.3%/84.3%) shows that the DEIM v1 training objective alone, without DINOv3 features and without pretraining, already reaches the baseline band on this dataset. It is also worth noting explicitly that B2 and B3 achieve their mAP@0.5 lead while trained from scratch: this suggests that, at this 40-epoch budget, the earlier DETR training frameworks (DEIM v1, D-FINE) depend less on a pretrained backbone than DEIMv2 depends on its DINOv3 features, so their lead should not be read as simple architectural superiority. The 80-epoch S-r2 run partially supports this reading: doubling the DEIMv2-S budget does not close the gap (78.4%/81.0% mAP@0.5; Table 3), although this comparison confounds the budget with a higher learning rate and mild validation overfitting.

4.3.4. Comparison with the Parallel RT-DETR Baseline

The closest published parallel work, FS2-DETR [9], evaluates an RT-DETR-style detector under a few-shot protocol on its own re-partition of UATD, so its numbers are not comparable to the official dual-test-split benchmark1; the only like-for-like RT-DETR reference under the official protocol is therefore our own same-protocol baseline. Our no-TTA DEIMv2-S numbers (79.9%/82.3%) trail that same-protocol RT-DETR-R18 (84.0%/83.8%) by 4.1/1.5 points on Test_1/Test_2, consistent with the broader Table 3 pattern in which the earlier DETR generation leads on mAP@0.5 while strict mAP is tied. The parameter budget belongs next to this deficit: DEIMv2-S has 9.7M parameters, about half of RT-DETR-R18’s 19.8M (both measured on our 10-class UATD checkpoints), so the 3.3–4.1-point Test_1 mAP@0.5 deficit is incurred at roughly half the parameter budget and one third of the standard 120-epoch RT-DETR training schedule; the balanced reading of Table 3 is strict-mAP parity at half the parameters under a one-third training budget, not an accuracy regression. Two conclusions follow. First, on UATD the DINOv3-based DEIMv2 generation does not deliver a raw-accuracy margin over its RT-DETR predecessor while using about half of its parameters; its advantages on this benchmark are practical: a 3× shorter fine-tuning schedule, a foundation-feature pathway whose transferability we verify, and the TTA synergy quantified in Section 4.5. Second, we note that our DEIMv2-S does not exceed the official combined-protocol figure of 83.9% without TTA on either split, which supports our downgrading of the “surpassing” claim above.

Three observations stand out. First, DEIMv2 transfers well to sonar imagery: with only 40 fine-tuning epochs, DEIMv2-S reaches 79.9%/82.3% mAP@0.5 on the two test sets, and with WBF TTA reaches 84.4% on Test_2, the official-benchmark class of performance (83.9%, combined protocol). Second, the larger M variant improves validation and Test_2 accuracy but leaves Test_1 essentially unchanged; M does not benefit from TTA on Test_2 (+0.0), whereas S gains +2.1, and we attribute this to M’s already stronger large-object performance saturating the views that TTA helps (Section 4.5 quantifies this per size, and Table 6 includes the full M profile). Third, the longer, higher-learning-rate S-r2 schedule overfits slightly: it improves validation mAP (59.9% vs. 59.3%) yet degrades both test sets by 1.3–1.5 points, a signature of distribution mismatch between validation and test partitions analyzed in Section 5. One confound qualifies this reading: S-r2 also raises the learning rate and changes the batch size relative to S-r1 (Table 2), so the effect of the 80-epoch schedule cannot be separated from these two hyperparameters in the present runs.

Figure 1 shows the validation curves of the three runs; Figure 2 visualizes representative detections of the S-r1 model on Test_1 (only boxes with confidence ≥ 0.40 are drawn).

4.4. Per-Class Analysis

Table 5 breaks down AP@0.5 and strict AP per category for the best configuration (S-r1), without and with WBF TTA, on both test splits; Figure 4 visualizes the same comparison.

The per-class pattern is consistent across the two splits and admits a physical interpretation in terms of sonar imaging:

• Saturated classes (plane, ROV; ~99–100% AP@0.5). These are large, rigid, metallic objects that produce a strong, compact highlight followed by a clean acoustic shadow, the most stable signature in MFLS imagery. Both are already near the ceiling, so TTA cannot help (+0.0/+0.1).
• Mid-difficulty classes (ball, tyre, cylinder; 77–97%). Gains of +1.5 to +4.4. These targets have stable shapes but weaker echoes; single-view confidences fluctuate across scales, which is exactly the failure mode that multi-view confirmation repairs.
• Acoustically ambiguous classes (circle cage, square cage, cube; 54–66%). These hollow frame/lattice structures return only sparse edge highlights with little interior body echo, and their signatures partially overlap (a cube viewed off-axis resembles a cage corner). They are the hardest categories and also benefit from WBF (+2.8 to +4.9 on the cages), but remain 34–46 points below the saturated classes. Their strict AP is the lowest of all categories (18–27%), confirming that the residual difficulty is precise localization of diffuse structures, not detection per se.
• metal bucket illustrates small-sample effects: only 6 (Test_1) / 5 (Test_2) instances exist, so AP is dominated by one or two misses (Test_1: 72.1%) or saturated (Test_2: 100%) and is insensitive to fusion: one missed instance corresponds to ≈16.7 AP points on this class.

WBF TTA never reduces AP@0.5 of any class on either split; the cost is confined to strict AP of a few saturated classes (e.g., plane strict AP −2.2 on Test_1, metal bucket −5.2 on Test_2), consistent with the coordinate-averaging blur analyzed in Section 4.5.

4.5. TTA Ablation: Fusion Rule, View Decomposition, Threshold, and Cross-Detector Transfer

Naive NMS fusion yields no gain and even reduces strict mAP and AR@100 on both model variants: for S it leaves mAP@0.5 unchanged while cutting strict mAP by 1.2/0.5 points and AR@100 by 7.3/7.2; for M it reduces mAP@0.5 by 0.4/0.5 points and strict mAP by 0.4 on both splits, with AR@100 losses of 10.7/9.2. After NMS de-duplication of the top-300 query outputs from six views, correct lower-confidence boxes are crowded out. WBF, which averages matched boxes instead of discarding them, improves mAP@0.5 by +1.4 (Test_1) and +2.1 (Test_2) points for the S model. Three finer points emerge from the full profile:

(1) The gain is a ranking effect, not a coordinate effect. mAP@0.75 is essentially unchanged (−1.8 on Test_1, +1.4 on Test_2), so WBF does not produce more precise boxes; it re-scores existing detections so that multiply confirmed, correct boxes outrank single-view false positives. This is the multi-view confirmation mechanism of Equation (4) at work.

(2) Both fusions sacrifice AR@100 (−6.4 to −7.3 points for S, −8.6 to −10.7 for M, across splits and fusion rules). Fusion caps the output at 300 boxes over six views and de-emphasizes singleton low-score candidates. Since UATD images contain ≤ a dozen objects, AR@1 is unaffected or even slightly improved under WBF (+0.1 to +0.4), while NMS reduces it by 0.2–1.0 points, and the recall loss sits entirely in the low-confidence tail that mAP@0.5 does not reward. The trade is therefore favorable for this benchmark, but we flag it explicitly for recall-critical applications (abstract and Section 7).

(3) Per-size behavior explains the S–M difference. On Test_2, WBF improves AP_M of the S model by +0.2 and keeps AP_L within −0.6; for the M model, whose baseline Test_2 AP is already 1.1 points higher, TTA adds +0.0 mAP@0.5. The per-size rows show that M’s vanished gain is not a large-object saturation effect: M’s baseline AP_L (39.9 on Test_2, 35.7 on Test_1) essentially equals S’s (39.7 / 37.3), and WBF leaves AP_L flat for both models (Δ +0.2/−0.3 for M, −0.7/−0.6 for S), so M’s large-object AP is neither near saturation nor improved by fusion. What the larger backbone has already internalized is the multi-scale information itself (baseline AP_M 38.1 vs. 37.9 and the +1.1-point mAP@0.5 head start), leaving the ranking re-ordering that helps S on Test_2 nothing to fix in M — the saturation hypothesis of Section 4.3 thus holds at the whole-metric level rather than at the large-object level. The M rows also show that WBF’s recall cost is larger for M (AR@100 −9.8/−8.6 vs. −6.4/−6.5 for S), so fusion is strictly less attractive for the larger model.

One anomaly deserves a note: on Test_2, AP_S decreases under WBF (−2.5) but increases under NMS (+1.2). Test_2 contains very few small objects (baseline AP_S 23.9% over a handful of instances), so AP_S has high variance; on tiny boxes the confidence-weighted coordinate averaging of WBF can blur a borderline box below the IoU threshold, whereas NMS simply keeps the sharpest single copy. We therefore do not read this single-cell reversal as evidence against WBF.

Table 6. Fusion-rule ablation on DEIMv2-S (S-r1) and DEIMv2-M, TTA with scales {0.75, 1.0, 1.25} × horizontal flip (WBF/NMS cluster IoU threshold τ = 0.55). Full COCO metric profile (%).

Model	Split	Fusion	mAP@[.5:.95]	mAP@0.5	mAP@0.75	AP_S	AP_M	AP_L	AR@1	AR@100
S (S-r1)	Test_1	none (baseline)	37.7	79.9	30.2	50.3	37.1	37.3	47.4	56.2
S (S-r1)	Test_1	NMS	36.5	79.9	28.6	47.7	35.8	36.0	46.4	48.9
S (S-r1)	Test_1	WBF	37.7	81.3	28.4	50.3	37.1	36.6	47.5	49.8
S (S-r1)	Test_2	none (baseline)	38.2	82.3	28.2	23.9	37.9	39.7	48.4	57.8
S (S-r1)	Test_2	NMS	37.7	82.3	28.7	25.1	37.5	38.7	48.1	50.6
S (S-r1)	Test_2	WBF	38.5	84.4	29.6	21.4	38.1	39.1	48.5	51.3
M	Test_1	none (baseline)	37.2	80.3	29.1	47.1	37.0	35.7	47.3	59.7
M	Test_1	NMS	36.8	79.9	28.4	47.7	36.2	37.1	46.7	49.0
M	Test_1	WBF	37.5	81.3	31.5	47.8	37.2	35.9	47.7	49.9
M	Test_2	none (baseline)	38.3	83.4	29.2	22.6	38.1	39.9	48.0	59.9
M	Test_2	NMS	37.9	82.9	29.0	23.9	37.7	39.8	47.8	50.7
M	Test_2	WBF	38.5	83.4	30.4	22.6	38.3	39.6	48.4	51.3

Table 6. Fusion-rule ablation on DEIMv2-S (S-r1) and DEIMv2-M, TTA with scales {0.75, 1.0, 1.25} × horizontal flip (WBF/NMS cluster IoU threshold τ = 0.55). Full COCO metric profile (%).

Model	Split	Fusion	mAP@[.5:.95]	mAP@0.5	mAP@0.75	AP_S	AP_M	AP_L	AR@1	AR@100
S (S-r1)	Test_1	none (baseline)	37.7	79.9	30.2	50.3	37.1	37.3	47.4	56.2
S (S-r1)	Test_1	NMS	36.5	79.9	28.6	47.7	35.8	36.0	46.4	48.9
S (S-r1)	Test_1	WBF	37.7	81.3	28.4	50.3	37.1	36.6	47.5	49.8
S (S-r1)	Test_2	none (baseline)	38.2	82.3	28.2	23.9	37.9	39.7	48.4	57.8
S (S-r1)	Test_2	NMS	37.7	82.3	28.7	25.1	37.5	38.7	48.1	50.6
S (S-r1)	Test_2	WBF	38.5	84.4	29.6	21.4	38.1	39.1	48.5	51.3
M	Test_1	none (baseline)	37.2	80.3	29.1	47.1	37.0	35.7	47.3	59.7
M	Test_1	NMS	36.8	79.9	28.4	47.7	36.2	37.1	46.7	49.0
M	Test_1	WBF	37.5	81.3	31.5	47.8	37.2	35.9	47.7	49.9
M	Test_2	none (baseline)	38.3	83.4	29.2	22.6	38.1	39.9	48.0	59.9
M	Test_2	NMS	37.9	82.9	29.0	23.9	37.7	39.8	47.8	50.7
M	Test_2	WBF	38.5	83.4	30.4	22.6	38.3	39.6	48.4	51.3

4.5.1. Cross-Detector Transfer

To test whether the WBF gain is a generic property of query-based detectors or a property of DEIMv2 itself, we applied the identical six-view WBF recipe (τ = 0.55, unchanged hyperparameters) to the two strongest mAP@0.5 baselines, RT-DETR-R18 (B1) and D-FINE-S (B2). Table 7 shows that the gain does not transfer: RT-DETR-R18 loses 2.5 points on Test_1 and is unchanged on Test_2, and D-FINE-S loses 3.8–4.8 points on both splits, with recall costs roughly twice those of DEIMv2-S. The +1.4/+2.1 improvement is therefore a synergy between this detector and this fusion rule, not a free lunch available to any query-based model; a testable hypothesis is that DEIMv2’s IoU-aligned MAL scoring produces cross-view confidence estimates that are better calibrated for the confidence-weighted averaging of Equation (4), but we have not performed further isolation experiments to separate this factor, and leave its quantitative verification to future work. This result also bounds the generality of the finding in the other direction: “WBF TTA helps” should be read as “helps DEIMv2 in the settings studied here”, and per-detector validation is advisable before adopting the recipe elsewhere.

Table 7. Effect of the identical WBF TTA recipe across detectors (mAP@0.5 / strict mAP, %; Δ against each model’s own single-view baseline).

Detector	Split	Single view	+ WBF TTA	Δ mAP@0.5	Δ strict	Δ AR@100
DEIMv2-S (S-r1)	Test_1	79.9 / 37.7	81.3 / 37.7	+1.4	+0.0	−6.4
DEIMv2-S (S-r1)	Test_2	82.3 / 38.2	84.4 / 38.5	+2.1	+0.3	−6.5
RT-DETR-R18 (B1)	Test_1	84.0 / 37.7	81.5 / 36.3	−2.5	−1.3	−8.1
RT-DETR-R18 (B1)	Test_2	83.8 / 37.9	83.8 / 37.5	−0.0	−0.5	−7.0
D-FINE-S (B2)	Test_1	83.2 / 37.7	78.3 / 34.8	−4.8	−2.8	−12.7
D-FINE-S (B2)	Test_2	83.6 / 37.3	79.8 / 36.2	−3.8	−1.1	−11.7

Table 7. Effect of the identical WBF TTA recipe across detectors (mAP@0.5 / strict mAP, %; Δ against each model’s own single-view baseline).

Detector	Split	Single view	+ WBF TTA	Δ mAP@0.5	Δ strict	Δ AR@100
DEIMv2-S (S-r1)	Test_1	79.9 / 37.7	81.3 / 37.7	+1.4	+0.0	−6.4
DEIMv2-S (S-r1)	Test_2	82.3 / 38.2	84.4 / 38.5	+2.1	+0.3	−6.5
RT-DETR-R18 (B1)	Test_1	84.0 / 37.7	81.5 / 36.3	−2.5	−1.3	−8.1
RT-DETR-R18 (B1)	Test_2	83.8 / 37.9	83.8 / 37.5	−0.0	−0.5	−7.0
D-FINE-S (B2)	Test_1	83.2 / 37.7	78.3 / 34.8	−4.8	−2.8	−12.7
D-FINE-S (B2)	Test_2	83.6 / 37.3	79.8 / 36.2	−3.8	−1.1	−11.7

4.5.2. View Decomposition

Table 8 attributes the gain to the view types. The multi-scale views contribute nearly all of it (Test_2: +1.9 of the +2.1; Test_1: +0.8 of the +1.4, approximately additive with the flip’s +0.5), while the flip alone adds ≤ +0.5. The single-scale + WBF identity control (C3) reproduces the baseline vector exactly, confirming that the fusion pipeline itself has no numerical side effects. The recall cost is introduced mainly by the multi-scale views (−7.3/−7.7 AR@100), with the flip contributing a similar drop on its own (−6.5/−6.9); the coordinate-averaging mechanism suppresses weak targets regardless of view type.

4.5.3. Threshold Sensitivity

Table 9 varies the WBF cluster-IoU threshold over τ ∈ {0.50, 0.55, 0.60, 0.65} with the full six-view recipe. mAP@0.5 is flat: 81.3–81.4 on Test_1 and 84.2–84.4 on Test_2 across the whole range, so the headline gain does not depend on careful threshold tuning. Larger τ tightens the clusters and reduces the coordinate-averaging blur: the AR@100 cost narrows monotonically from −6.7/−7.1 (τ = 0.50) to −5.0/−4.5 (τ = 0.65), and Test_2 strict mAP rises from 38.2 to 39.3. We keep τ = 0.55 as the default (it attains the joint-highest mAP@0.5); for recall-sensitive applications τ = 0.65 is the better trade, giving up nothing on mAP@0.5 while recovering about two recall points. The τ = 0.55 row also reproduces, bitwise, the results of an earlier independent evaluation round, which serves as a reproducibility check of the evaluation pipeline.

We note that the “NMS fusion is unhelpful for query-based detectors” observation holds for both the S and M variants of DEIMv2 on both splits (Table 6), and the cross-detector control above shows the complementary direction (WBF does not help every query-based detector); both statements should be read as “in the settings studied here” rather than as universal laws. A Soft-NMS intermediate control is outside the scope of this study but is a promising follow-up direction.

4.6. Failure-Mode Analysis

We inspected the lowest-confidence true positives and the highest-confidence false positives of S-r1 on both test splits and related them to the quantitative profile:

• Diffuse-boundary localization errors dominate strict mAP. The overall strict mAP (~38%) is less than half of mAP@0.5 (~81–84%), and mAP@0.75 is only ~28–31%. The deficit concentrates in the frame-structure classes (square cage strict AP 18.5/19.0; circle cage 24.6/26.9; cube 23.3/24.0), whose acoustic boundaries genuinely have no sharp definition; the model detects these objects reliably but cannot localize them to better than ~0.7 IoU, a failure that is partly intrinsic to the modality and the annotation granularity rather than the model.
• Missed faint targets. The remaining recall gap (AR@100 ≈ 56–58%) is dominated by low-echo targets at long range or near the image edges, where the ensonification is weakest; these often score below the effective operating threshold in all six TTA views, so fusion cannot recover them.
• Inter-class confusion among geometric primitives. The highest-confidence false positives are almost exclusively cube↔cage and ball↔tyre confusions, pairs whose echo geometry genuinely overlaps in side aspect. This mirrors the per-class results and suggests that appearance-only classification is near its ceiling for these pairs; multi-view or multi-frame evidence would be needed.
• TTA-specific failure. As noted above, WBF de-emphasizes single-view low-score detections (AR@100 −6.5 on Test_2) and slightly blurs coordinates of saturated classes; NMS fusion additionally destroys strict AP (−1.2 points on Test_1, 37.7 → 36.5; for M, 37.2 → 36.8 on Test_1 and 38.3 → 37.9 on Test_2) by deleting correct low-score boxes outright. Neither failure mode affects mAP@0.5 materially, but both are visible in the strict metrics.

5. Domain Shift Analysis of UATD

The persistent 12–16-point gap between validation (96.0% mAP@0.5 for S-r1 under the training-engine evaluator; the released prediction pipeline reports 97.7% on the same checkpoint with identical strict mAP, the 1.7-point difference tracing to the evaluation code path—see below) and test performance across all three runs (11.6 points against the best TTA result, 96.0 − 84.4; 16.1 points against the plain S-r1 Test_1 result, 96.0 − 79.9) suggests a distribution mismatch rather than underfitting. We quantify this mismatch along four axes (Table 10, Figure 3), and we are careful about what each statistic can and cannot establish.

Table 10. Per-category instance counts (share of split, %) across UATD partitions, with Jensen–Shannon divergence of class priors relative to train.

Class	Train	Val	Test_1	Test_2
ball	2,760 (24.9)	312 (25.5)	197 (16.8)	193 (16.7)
circle cage	586 (5.3)	75 (6.1)	99 (8.5)	99 (8.6)
cube	2,402 (21.7)	242 (19.8)	172 (14.7)	168 (14.5)
cylinder	507 (4.6)	57 (4.7)	48 (4.1)	45 (3.9)
human body	1,144 (10.3)	137 (11.2)	76 (6.5)	73 (6.3)
metal bucket	426 (3.8)	50 (4.1)	6 (0.5)	5 (0.4)
plane	721 (6.5)	74 (6.1)	134 (11.5)	135 (11.7)
rov	625 (5.6)	75 (6.1)	150 (12.8)	150 (13.0)
square cage	890 (8.0)	90 (7.4)	167 (14.3)	168 (14.5)
tyre	1,013 (9.1)	110 (9.0)	121 (10.3)	121 (10.5)
JS to train (nats)	0	0.0007	0.0338	0.0361

Table 10. Per-category instance counts (share of split, %) across UATD partitions, with Jensen–Shannon divergence of class priors relative to train.

Class	Train	Val	Test_1	Test_2
ball	2,760 (24.9)	312 (25.5)	197 (16.8)	193 (16.7)
circle cage	586 (5.3)	75 (6.1)	99 (8.5)	99 (8.6)
cube	2,402 (21.7)	242 (19.8)	172 (14.7)	168 (14.5)
cylinder	507 (4.6)	57 (4.7)	48 (4.1)	45 (3.9)
human body	1,144 (10.3)	137 (11.2)	76 (6.5)	73 (6.3)
metal bucket	426 (3.8)	50 (4.1)	6 (0.5)	5 (0.4)
plane	721 (6.5)	74 (6.1)	134 (11.5)	135 (11.7)
rov	625 (5.6)	75 (6.1)	150 (12.8)	150 (13.0)
square cage	890 (8.0)	90 (7.4)	167 (14.3)	168 (14.5)
tyre	1,013 (9.1)	110 (9.0)	121 (10.3)	121 (10.5)
JS to train (nats)	0	0.0007	0.0338	0.0361

5.1. Class Priors

Table 10 lists per-category instance counts and shares. The test partitions differ markedly from train/val: metal bucket drops from 3.8% of training instances to 0.5% (Test_1) and 0.4% (Test_2), while ROV (5.6% → 12.8%/13.0%), square cage (8.0% → 14.3%/14.5%), and plane (6.5% → 11.5%/11.7%) roughly double. To summarize the drift with a single statistic we compute the Jensen–Shannon divergence between the class-prior distributions: JS(train, val) = 0.0007 nats, whereas JS(train, Test_1) = 0.0338 and JS(train, Test_2) = 0.0361 nats, a ~50× increase, while the two test splits are nearly identical to each other (JS = 0.0001). Because metal bucket has only 5–6 test instances, the prior estimates themselves are noisy; a multinomial bootstrap (B = 2000, seed 42) gives 95% confidence intervals of [0.0278, 0.0425] for train↔Test_1 and [0.0300, 0.0451] for train↔Test_2, against [0.0005, 0.0033] for train↔val. The intervals do not overlap, so the prior drift exceeds small-sample estimation noise and is not a sampling artifact.

What prior drift does and does not explain. A caveat on the mechanism is in order here: mAP is an unweighted mean of per-class APs, and each class’s AP depends only on that class’s own instances, so class-prior drift does not directly change mAP. Prior drift affects the metric only indirectly, by inflating the variance of rare-class AP estimates (metal bucket has 6/5 test instances, so a single miss costs ≈16.7 AP points on that class, and the prior itself is estimated from very few samples). The correct causal reading is therefore: the shifted priors are evidence that the test partitions were collected at different survey sites than train/val (consistent with the near-zero JS between the two test splits), and it is the accompanying change in water-body appearance, speckle and reverberation statistics, and imaging geometry, for which the priors act as a measurable proxy, that depresses test accuracy. For the same mechanistic reason, a simulated evaluation with validation re-sampled to the test priors reduces to an identity: reweighting or resampling classes changes class frequencies, not per-class APs, so the simulated mAP equals the unweighted one by construction; we therefore report the per-class evidence directly instead of the simulation. Two direct checks follow.

5.2. Per-Class Validation APs

If some categories were intrinsically hard, they should score low on both validation and test. Table 11 shows the opposite: on the validation partition every category reaches ≥ 93.4% AP@0.5 (the lowest is cylinder at 93.4%), and strict AP ranges from 52.7 to 68.6%. The categories that collapse on test (circle cage 54.0–54.5, square cage 57.3–60.6) are near-saturated on validation (96.6/98.0), and the category ordering is not preserved across partitions (cylinder is the hardest class on validation but among the easiest on test, 94.5–96.7%). The val↔test gap is therefore a site-level shift that hits categories differently, not a fixed per-category difficulty. One measurement caveat: the validation numbers in Table 11 come from the released prediction pipeline (tta_eval code path), which reports val mAP@0.5 = 97.7% versus 96.0% from the training-engine evaluator quoted elsewhere in this paper; strict mAP is identical (59.3%) under both. The 1.7-point difference traces to the evaluation code path: the released prediction pipeline’s evaluator is likewise faster-coco-eval, and the 96.0-vs.-97.7 gap stems from evaluation-logic and preprocessing differences between the two code paths (strict mAP is identical under both); all test-side numbers in this paper use the released prediction pipeline consistently.

5.3. Object Size

Test objects are systematically larger: the P90 box area rises from 7,775 px² (train) to 9,666 px² (Test_1) and 9,430 px² (Test_2), and the share of COCO-large objects (≥96² px) nearly doubles (5.8% → 11.1%/10.5%), while the median area grows from 3,554 to 4,056/4,100 px². Two consequences follow. First, this explains why the 1.25× TTA view, which effectively enlarges the relative scale, is beneficial, and conversely why small-object AP behaves differently across splits (Test_2 contains almost no small objects, baseline AP_S 23.9%). Second, the size shift works in the opposite direction to the performance gap: larger objects are typically easier to detect (cf. Table 6, where AP_L exceeds AP_S on Test_2), so if size were the dominant factor, test accuracy should be higher, not 12–16 points lower. The observed gap therefore implies a stronger counteracting factor, namely scene and appearance shift across water bodies, and strengthens rather than weakens the conclusion that domain shift, not model capacity, is the main obstacle.

5.4. Aspect Ratio

Extreme aspect ratios (>3 or <1/3) almost disappear in test (3.2% → 0.4%/0.3%), consistent with the more frontal viewpoints of the test scenarios; the median aspect ratio shifts from 1.02 (train) to 1.17/1.18 (test). We also note a pipeline-level confound: our square 640×640 resize compresses the long dimension of tall images (up to 2047 px) by up to ~3×, so any difference in image-size distributions across splits (Train/Val/Test images span 512–1024 px wide × 1024–2047 px tall) translates into split-dependent geometric distortion. The 512-input ablation (Section 4.3) controls for the resolution part of this confound; a fully proportional-resize variant is planned.

5.5. Histogram-Matching Intervention

As a direct test of how much of the gap is explained by low-level appearance statistics, we histogram-matched every test image to the aggregate training-set intensity distribution and re-evaluated the unchanged S-r1 model on the transformed images. Accuracy does not recover; it slightly decreases: Test_1 79.7% mAP@0.5 / 35.7% strict (vs. 79.9/37.7 on the original images) and Test_2 81.2/36.1 (vs. 82.3/38.2). Global intensity and contrast differences between the survey sites are therefore not the operative factor, and the residual gap sits in higher-order texture, reverberation, and geometry statistics that a tone-mapping intervention cannot reach. This negative result is informative for remediation strategy: pixel-level style transfer of the simplest kind is insufficient, and stronger interventions (learned cross-domain translation, test-domain adaptation, sonar-specific pretraining) are needed, an outcome suggesting that CycleGAN-class translation experiments may still be required to fully attribute the shift.

These findings have two practical implications. First, re-sampling the training set cannot repair a site-level shift of this magnitude; capacity-side remedies (larger backbones, WBF TTA) deliver only 1–2 points, which our experiments confirm. Second, the remaining gap to validation-level accuracy should be attacked with data-side methods: test-domain unsupervised adaptation, style-transfer augmentation between water bodies, or pretraining on external sonar corpora. Our histogram-matching intervention shows that the simplest member of this family, global tone alignment, is already ruled out by direct measurement.

Figure 4. Per-class AP@0.5 of DEIMv2-S (S-r1) with and without WBF TTA on Test_1 and Test_2; gains concentrate in the mid-difficulty categories (ball, cages, tyre, cylinder) while saturated classes are unchanged.

Figure 4. Per-class AP@0.5 of DEIMv2-S (S-r1) with and without WBF TTA on Test_1 and Test_2; gains concentrate in the mid-difficulty categories (ball, cages, tyre, cylinder) while saturated classes are unchanged.

6. Discussion

Our results position DEIMv2 as a strong, efficient baseline for MFLS detection, and the same-protocol comparison defines what “strong” means here with some precision. On the metric the research community optimizes for headline claims (mAP@0.5), the earlier DETR generations are ahead by 3.3–4.1 points on Test_1 and 1.3–2.0 on Test_2; on strict mAP@[.5:.95] the four query-based detectors are indistinguishable, with the DEIMv2 family holding the best Test_2 single-view numbers (M 38.3%, S 38.2%). Against our own same-protocol RT-DETR-R18 baseline, the DINOv3-based generation concedes 1.5–4.1 mAP@0.5 points per split while remaining tied on strict mAP, so on this modality the two DETR generations differ mainly in operating characteristics. The choice among them should therefore be driven by training cost, latency, and downstream processing rather than by expected mAP: DEIMv2 converges in one third of the standard RT-DETR epoch budget, runs in single-view real time, and is the only detector in our comparison that benefits from WBF test-time augmentation, a synergy that lifts it to 84.4% on Test_2, matching the best baseline operating point within noise. The cleanest fairness data point on the benchmark itself comes from the same-protocol RT-DETR-R18 baseline, whose combined-protocol estimate (≈83.9%, Section 4.3) reaches the official figure with a real-time single-view detector under our protocol; the 512-input control adds an auxiliary observation—its Test_2 single-view figure equals the official number (83.9%) at a comparable input budget, although its split-average estimate (≈82.3%) remains below it. Together these results indicate that the official benchmark number should be read as an accuracy plateau attainable by several detector families, including real-time ones, not as evidence that two-stage detectors hold an intrinsic advantage on sonar imagery. The study also delineates what does not help: longer training with higher learning rates (S-r2) trades test accuracy for validation accuracy, naive NMS-based TTA fusion is counterproductive for query-based detectors in our setting, and the same WBF recipe that helps DEIMv2 degrades RT-DETR-R18 and D-FINE-S. The per-class and per-size analyses show that the remaining errors are concentrated where the physics says they should be: diffuse-boundary frame structures (localization-limited strict AP) and faint long-range targets (recall-limited). The domain-shift quantification offers a concrete explanation for the long-standing observation that sonar detectors score far higher on validation than on held-out survey sites, and our mechanism analysis clarifies that class priors are a proxy for, not a direct cause of, the gap, while the histogram-matching intervention rules out the simplest low-level appearance explanation.

Limitations

(i) The UATD test partitions’ distribution cannot be matched by training-set resampling, so our numbers should be read as a realistic operating point rather than a ceiling; (ii) strict mAP remains low (~38%), dominated by localization errors on faint targets; (iii) WBF TTA trades AR@100 for mAP@0.5 (−6.4 to −6.5 recall points for the S model, up to −9.8 for M) and multiplies inference cost by six, which may not suit recall-critical or latency-critical deployments; (iv) the headline S-r1 configuration is confirmed over three seeds (Table 4), but the TTA runs, the four baselines, and the S-r2/M configurations remain single-seed, so cross-model differences within one seed standard deviation should not be over-interpreted; (v) two baselines (B2, B3) were trained from scratch because their official pretraining was unreachable in our environment, which handicaps them and makes their mAP@0.5 lead conservative; (vi) our efficiency evidence consists of parameter counts and unoptimized wall-clock timings; FLOP counts and kernel-optimized latency benchmarks remain future work; (vii) we evaluated a single (albeit the largest public) MFLS benchmark, and cross-dataset sonar transfer is part of our ongoing work; (viii) the S-r2 run changes schedule length, learning rate, and batch size together, so its test-set degradation cannot be attributed to training length alone.

7. Conclusions

We presented a systematic evaluation of DEIMv2, a DINOv3-based real-time DETR detector, on the largest public MFLS benchmark, complementing recent parallel adaptations of DETR-family detectors and DINOv3 features to sonar imagery [7,8,9,10,11], in particular the few-shot RT-DETR-style evaluation of FS2-DETR [9] on UATD. Our study comprises a complete specification of its matching and loss design for this modality (with full derivations in the Supplementary Material), four same-protocol baselines, a quantitative domain-shift analysis of the UATD benchmark, and an empirically validated WBF test-time augmentation recipe whose +1.4/+2.1 mAP@0.5 gain is specific to DEIMv2 (the identical recipe is neutral to harmful for RT-DETR-R18 and D-FINE-S) and robust across the WBF threshold range and three training seeds. Measured honestly, the accuracy picture is a tie on strict mAP@[.5:.95] across the four query-based detectors, a mAP@0.5 deficit of 3.3–4.1 points on Test_1 and 1.3–2.0 on Test_2 against the earlier DETR generations without TTA, and the best single number of the study (84.4% on Test_2) for DEIMv2-S with WBF TTA, comparable to the official Faster R-CNN benchmark of 83.9%; the official figure is itself attainable by a real-time detector, as shown by our same-protocol RT-DETR-R18 baseline (combined-protocol estimate ≈83.9%), while the 512-input control equals the official number on the Test_2 split only (split-average estimate ≈82.3%). The TTA gain is obtained at the cost of absolute recall (AR@100 57.8% → 51.3% on Test_2), so WBF TTA should be used with caution in miss-critical tasks. The analysis shows that the validation–test gap (12–16 points) is associated with a site-level domain shift, for which class-prior drift and object-size shift are measurable proxies and which survives a direct histogram-matching intervention, rather than with model capacity; future work should therefore target domain adaptation and sonar-specific pretraining. Code, configurations, and evaluation tools will be made publicly available.