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Cross-Architecture Foundation-Model Distillation for Edge Flood Segmentation

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Cross-Architecture Foundation-Model Distillation for Edge Flood Segmentation

arXiv:2609.20441v1 [cs.CV] 17 Sep 2026

Fabian Schmalstieg, Karsten Müller, and Wojciech Samek

Abstract—Geospatial foundation models can provide strong flood-segmentation performance, but their size limits deployment on memory-constrained edge hardware. We distill a 300-millionparameter Prithvi-EO-2.0 teacher, fine-tuned on the 252 manually labeled Sen1Floods11 training scenes, into a 0.7-millionparameter EfficientViT-B0 student. The teacher supervises additional unlabeled Sentinel-2 imagery, allowing the student training set to grow without new manual annotations. At the matched budget of 252 scenes, teacher-supervised training is competitive with direct training and improves STURM-Flood performance across tested configurations; a geometry-matched control shows that label source alone does not explain the difference. Scaling the teacher-supervised pool to 2,500 scenes narrows the remaining student–teacher gap: the float student reaches 0.787 water intersection over union on the Sen1Floods11 test split against 0.822 for the teacher, matches the teacher on STURM-Flood under our evaluation protocol, and remains below it on WorldFloodsv2. After activation replacement and quantization-aware training, the student runs as a 1.5-megabyte 8-bit integer (INT8) TensorRT engine on a Jetson Xavier NX at 5.57 milliseconds of graphics processing unit (GPU) compute per 512-by-512 image, with approximately 14 megabytes of runtime device memory. A fixed modified normalized difference water index (MNDWI) threshold is competitive with both models on the two clean external benchmarks, so we interpret those benchmarks as generalization tests rather than as evidence of learned-model superiority over a spectral rule. The results support the conclusion: foundationmodel supervision can amplify a fixed manual annotation budget into a substantially larger training set and yield a compact, deployable edge model. Index Terms—edge inference, flood segmentation, geospatial foundation models, knowledge distillation, model compression, pseudo-labeling, quantization-aware training, Sentinel-2.

I. I NTRODUCTION

LOOD is among the most frequent and most costly natural disasters globally, and timely spatial mapping of inundated areas directly informs evacuation routing, damage assessment, and relief logistics. Operational flood response typically combines numerical weather prediction, hydrological runoff modeling, and hydraulic inundation simulation; satellite-based segmentation provides complementary observational evidence that is not dependent on model assumptions and can validate or correct model output after an event. For satellite observation, both synthetic aperture radar (SAR) and optical sensors are used. Sentinel-1 SAR can penetrate cloud cover, which is important during active precipitation events, while Sentinel-2 multispectral imagery provides Fabian Schmalstieg, Karsten Müller, and Wojciech Samek are with the Department of Artificial Intelligence, Fraunhofer Heinrich Hertz Institute, 10587 Berlin, Germany (e-mail: [email protected]; [email protected]; [email protected]). Corresponding author: Fabian Schmalstieg.

a richer spectral signature and is the basis for most largescale geospatial pretraining. In particular, the Harmonized Landsat Sentinel-2 (HLS) corpus on which Prithvi-EO-2.0 was pretrained covers six spectral bands (B2, B3, B4, B8A, B11, B12), and the same six-band input is used throughout this work. Real-time acquisition during cloud-covered flood events remains a practical limitation of this modality; here we focus on the mapping and compression problem, treating near-realtime applicability as future work. On the modeling side, geospatial foundation models (GFMs) pretrained on large multispectral satellite corpora generalize well to flood events and geographic regions not seen during fine-tuning [1]. Prithvi-EO-2.0 (300 M parameters), fine-tuned on the Sen1Floods11 labeled dataset, reaches 0.755 mean intersection over union (mIoU) on our protocol of the STURM out-of-distribution (OOD) benchmark, a considerably harder evaluation set than the Sen1Floods11 test split. The difficulty lies in deployment. Running flood segmentation close to the sensor, rather than in a data center, shortens the path between acquisition and an actionable map and removes the dependency on connectivity, which is often degraded in a disaster zone. On-board inference for Earth observation is already being demonstrated, for example in the European Space Agency (ESA) Φ-sat missions [2]. We do not claim a quantified industry-wide trend. The hardware that local authorities and relief organizations operate is not well documented and varies considerably, from ruggedized laptops through embedded graphics processing units (GPUs) to custom field-programmable gate arrays (FPGAs). What these platforms share is a strict memory budget. A 300 Mparameter Vision Transformer (ViT) at 32-bit floating point (FP32) is a poor fit for memory-constrained embedded targets, whereas a compact 8-bit integer (INT8) model offers a more accessible deployment path. Sixteen-bit floating point (FP16) or structured pruning remain alternatives where more memory headroom is available. The gap between the models that perform best in research and those that can run in the field thus remains little studied for geospatial flood segmentation. Knowledge distillation (KD) is a natural route from a large foundation model to a compact student, but our setting adds a data constraint. Sen1Floods11 contains only 252 manually labeled training scenes. Training a compact model directly on that split fixes the amount and geographic scope of supervision, whereas a teacher that has already been adapted to the task can apply its supervision to additional unlabeled imagery. We therefore use Prithvi-EO-2.0 as a frozen task teacher, generate supervision on Sentinel-2 tiles retrieved around flood events from the Global Disaster Alert and Coordination System (GDACS), and train a compact EfficientViT-B0 student

on those scenes. No additional manual annotation is acquired. This design separates two questions that are often conflated. First, at the same scene budget, does teacher-supervised training provide a viable substitute for direct training on the original human-labeled split? Second, once a task teacher exists, does scaling the supervised image pool beyond the fixed annotation set narrow the student–teacher gap? The first question is tested at N = 252 with matched architectures, objectives, augmentation and seeds. The second is tested by scaling the teacher-supervised pool to N = 2,500 while keeping the teacher fixed. External evaluation on STURMFlood and WorldFloods-v2 then tests whether the resulting student remains useful outside Sen1Floods11. We therefore restrict the interpretation in two ways. Synthetic gain, haze, and per-band radiometric perturbations are treated as diagnostics rather than as a robustness contribution. The two training sources differ in acquisition geometry as well as in imagery, and no experiment isolates training-pool diversity as a cause. Because a fixed-threshold modified normalized difference water index (MNDWI) baseline is competitive on both external benchmarks, we present external accuracy as evidence of generalization rather than superiority of a learned model over a spectral rule. The deployment question is independent of those secondary diagnostics. The practical target is a student small enough to compile to TensorRT and run with low latency and memory use on embedded hardware while retaining most of the teacher’s in-distribution flood-water accuracy. The resulting compression ratio is about 430× in parameter count, from 300 M parameters to 0.7 M. Contributions: • Annotation-budget amplification through teacher supervision. At the matched budget of 252 scenes, teachersupervised training is a competitive substitute for direct training on the Sen1Floods11 labels and raises STURMFlood mIoU in all five tested architecture–objective cells, four of which survive Holm correction over the block. A geometry-matched control shows that the size of the effect is partly entangled with acquisition geometry. The claim is therefore substitution at a fixed manual annotation budget, not superiority of teacher-generated labels over human annotations. • Scaling beyond the fixed manual split. Because additional teacher-supervised scenes require no new manual labeling, the student training set can grow beyond the 252-scene annotation budget. At N = 2,500, the EfficientViT-B0 student narrows the in-distribution water intersection-over-union (IoU) gap to the teacher and matches its STURM-Flood mIoU under our evaluation protocol, while remaining lower on WorldFloods-v2. This establishes both the benefit and the limit of the scaling strategy, without claiming parity across out-ofdistribution settings in general. • Edge deployment of a highly compressed student. ReLU6 retraining and quantization-aware training produce a 1.5 MB INT8 TensorRT engine for the 0.7 Mparameter student. On a Jetson Xavier NX it runs at 5.57 ms of GPU compute per 512 × 512 image, with

approximately 14 MB of runtime device memory and a further 0.4 ms of host–device transfer. The deployment contribution is the small, measured engine footprint and latency, not a claim that the 300 M teacher is impossible to execute on every embedded platform. II. R ELATED W ORK Geospatial foundation models: Satellite foundation models such as SatMAE [3], SpectralGPT [4], and Prithvi [1] use large-scale self-supervised pretraining to transfer across geographies and tasks. Prithvi-EO-2.0, our teacher, is pretrained globally on Harmonized Landsat Sentinel-2 imagery. Earlier flood studies show the value of this pretraining outside the fine-tuning distribution: Li et al. [5] report stronger geographic generalization for the original Prithvi than conventional segmentation baselines, while Polushko et al. [6] study label efficiency when adapting Prithvi-EO-2.0 to airborne RGB imagery. Garg et al. [7] use a large pool of unlabeled pairs to distill an optical flood teacher into a Sentinel-1 student. Their goal is cross-modal label efficiency rather than compact edge deployment. To our knowledge, distilling a geospatial foundation model into an INT8-deployable flood-segmentation student without acquiring additional ground-truth labels has not been studied. Knowledge distillation and compact segmentation: Knowledge distillation transfers a teacher’s output distribution to a student [8] and has since been extended to feature- and attention-level objectives [9], [10]; Himeur et al. [11] survey its use in remote sensing. Cross-architecture transfer is harder when teacher and student expose incompatible intermediate representations [12]. One-for-All (OFA) [13] avoids direct feature matching by attaching lightweight student branches that predict the teacher’s final output at several depths, which makes it a natural fit for transfer from a ViT to a convolutional neural network (CNN). The closest foundation-model deployment pipeline is InstaGeo [14]: it distills fine-tuned geospatial foundation models into smaller versions of the same architecture for cloud serving. Our setting differs in the much larger cross-architecture compression, training on teacher-labeled scenes rather than ground-truth scenes, and quantized on-device evaluation. UNet-ResNet50 [15] is a standard flood-segmentation baseline. EfficientViT [16] combines local depthwise convolutions with linear attention and provides a favorable accuracy– efficiency trade-off for dense prediction. We use EfficientViTB0 as the primary student because it is compact, remains competitive in our OOD controls, and can be carried through the deployment path described in §III-D. Flood benchmarks and acquisition robustness: Sen1Floods11 [17] is the in-distribution training benchmark. STURM-Flood [18] and WorldFloods-v2 [19] provide complementary Sentinel-2 OOD evaluations built from Copernicus emergency-mapping activations; recent multimodal datasets [20], [21] address a broader sensor setting than the optical-only student studied here. Robustness to acquisition conditions is distinct from clean-benchmark accuracy. Sentinel-2 radiometric uncertainty is naturally

STAGE 1 · TEACHER PSEUDO-LABEL GENERATION

STAGE 2 · DIVERSITY-AWARE DATASET CURATION

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fine-tuned on Sen1Floods11 (frozen teacher)

1. Patch Embedding 14x14 patch grid at 224x224 → tokens

↓ ViT-L encoder — 24 Transformer blocks embedding dimension 1024, 16 attention heads

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↓ Feature outputs from blocks 6, 12, 18, and 24 → UPerNet decoder, 256 decoder channels, 2 output classes

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encoder blocks (LayerNorm + residual connections)

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Maps / descriptors stored per tile

Curated Training Subset

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TensorRT Optimization

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Teacher pseudo-labels (Stage 1 maps) — supervise the 4 OFA losses

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DEPLOYMENT · EMBEDDED INT8 INFERENCE

Hardswish (baseline activation)

Input Image

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23,720 GDACS Sentinel-2 tiles (unlabeled)

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STAGE 3 · EFFICIENTVIT STUDENT — TRAINING WITH OFA DISTILLATION

15-D spectral + Teacher descriptor Embedding

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Fig. 1: Overview of the distillation-to-deployment pipeline: pseudo-labeling of the unlabeled GDACS pool by the frozen foundation-model teacher, filtering and subset selection, cross-architecture distillation into the compact student, and quantized deployment. Only the hard mask, confidence map, and 15-dimensional descriptor are stored during pool generation; soft targets are produced by live frozen-teacher inference during student training. The pool holds two acquisitions per location, one inside the event window and one pre-event baseline, which enables the pre-event teacher-semantics audit of §IV-G.

expressed in relative terms [22], motivating our gain diagnostic, while atmospheric haze is well modeled as an additive wavelength-dependent contribution [23]. We therefore test gain and haze directly in reflectance space (§IV-F) rather than relying on generic natural-image corruptions. III. M ETHOD Figure 1 summarizes the pipeline. Its four stages are pseudolabeling, filtering and subset selection, distillation, and quantization. They are described in turn below. A. Foundation Model Teacher and Pseudo-label Generation We use Prithvi-EO-2.0 [1] fine-tuned on the Sentinel-2 subset of Sen1Floods11 (S11) as our teacher. We take the official IBM/NASA Prithvi-EO-2.0-300M-TL-Sen1Floods11 segmentation checkpoint released on Hugging Face, without any further fine-tuning of our own, so the teacher is the publicly available model. On the S11 test split we measure 0.897 mIoU and 0.822 water IoU against the 0.900 and 0.826 reported for this checkpoint [1]; the remaining 0.003–0.004 is a protocol difference, not a different model. At inference it processes a single 512 × 512 six-band Sentinel-2 image (bands B2, B3, B4, B8A, B11, B12) and produces perpixel class probabilities pT (x) ∈ [0, 1]H×W for binary flood segmentation. Choice of teacher: The labeler is applied only to scenes no one has annotated, so the property that matters is its accuracy outside the fine-tuning distribution. We select PrithviEO-2.0 because it provides strong external performance after

task adaptation. This study does not test whether foundationmodel pretraining itself is required for the observed transfer. This is a design decision supported by measured out-ofdistribution accuracy, not a demonstration that a foundation model is required: we did not compare Prithvi with a second learned teacher of comparable capacity and provenance (§VII). Section IV-G measures which of the teacher’s annotation conventions the student reproduces, and Supplementary Sections S4 and S8 contain additional labeler diagnostics. What the pseudo-labels contain: Supervision enters on two axes, the labeling of the GDACS pool and the objective. Adding the temperature-scaled soft term to the hard-target loss increases STURM mIoU by 0.018 at a matched budget of 252 scenes (Table I). This difference is consistent with the soft teacher probabilities carrying useful spatial information beyond the hard argmax. The two rows also differ in temperature and in the weight on the hard target (§III-C), so the contribution of the soft target alone is not isolated. OFA adds a smaller further gain; the gradient diagnostics in §V are consistent with deep supervision contributing to this effect. The teacher is used strictly for inference from here on; nothing in this paper trains or fine-tunes it on the unlabeled pool. We run it once, frozen, over all 23,720 GDACS tiles at the 224×224 pool-labeling resolution (Sentinel-2 imagery downloaded via Google Earth Engine (GEE) for GDACS flood events; see §IV-A) and store per tile: the hard argmax pseudomask, a per-pixel confidence map, and a 15-dimensional summary vector (flood fraction, mean confidence, confidence standard deviation, and per-band mean and std across the 6 input channels) used for curation.

B. Pseudo-label Filtering and Subset Selection The GDACS pool U (§IV-A) is spatially and temporally correlated: large flood events generate many overlapping acquisition strips, so the most frequent event types and geographies are heavily over-represented, and half of it is a pre-event acquisition that the teacher labels no differently from the rest. A selection stage therefore has two plausible jobs, removing tiles whose labels are unusable and spreading the remainder over the feature space. We designed the stage for both; only the first is measurable at our operating point (Supplementary Section S2). After pre-filtering and selection the curated pool is capped at N = 2,500 scenes drawn from the 5,987 that survive the filter, and this is the operating point for all full-pool experiments. Our curation uses three steps. Step 1: Pre-filtering: We first restrict U to tiles that contain informative boundary signal. Let ŷT (u) = (c) arg maxc pT (u) be the teacher’s hard class prediction at pixel u (flood or non-flood), and pT (u) ∈ [0, 1] the teacher’s flood probability at pixel u. We define: P 1 • f (x) = |Ω| u∈Ω 1[ŷT (u) = flood]: the fraction of pixels in tile x P that the teacher predicts as flood. 1 • µT (x) = |Ω| u∈Ω pT (u): the spatial mean of the teacher’s flood across the tile. q probability P 1 2 • σT (x) = (p u∈Ω T (u) − µT (x)) : the spatial |Ω| standard deviation of the teacher’s confidence map, which measures how much uncertainty is present within the tile. We then define: U ′ = x ∈ U fmin ≤ f (x) ≤ fmax ∧ σT (x) ≥ σmin , (1) with fmin = 0.05, fmax = 0.85, σmin = 0.05, fixed a priori and never tuned against a benchmark. The lower bound on f removes background-only tiles, the upper bound removes tiles that are almost entirely flooded with no land boundary, and the σT threshold removes tiles where the teacher is uniformly confident, which are scenes that provide no gradient information about the flood boundary. This reduces 23,720 to 5,987 candidates. The pre-filter is the curation component that measurably matters, and it acts in both directions. It also has two side effects that follow from the rule rather than from our data. The lower bound f ≥ fmin admits 2,127 of the 11,825 preevent baselines (35.5% of the candidate pool), which are by construction the pre-event tiles the teacher marked as water (§IV-G); and it guarantees that no training tile is flood-free, so the student never sees a fully dry scene (§VII). Neither was intended. Step 2: Feature embedding: Each remaining tile is embedded into a compact descriptor built entirely from quantities already stored during pseudo-label generation; no additional teacher inference is required: ϕ(x) = f (x), µT (x), σT (x), (2) x̄1 , . . . , x̄K , σx1 , . . . , σxK ∈ R2K+3 , where K = 6 is the number of spectral bands, x̄k and σxk are the mean and standard deviation of band k over the tile. This gives a 15-dimensional vector (2 × 6 + 3). The first three

dimensions, f (x), µT (x), and σT (x), are the same quantities used in Step 1 pre-filtering and capture flood content and label uncertainty. The remaining twelve dimensions are the per-band mean and standard deviation of the raw Sentinel-2 reflectance, which encode spectral appearance and, because spectral statistics vary systematically across geographic regions and seasons, serve as a proxy for geographic and environmental diversity. A flood over dry, bare ground reflects light very differently from a flood in a dense green landscape, so the two scenes have different per-band statistics even when the same fraction of each is under water. By including both the pseudo-label statistics and the raw spectral statistics in ϕ, the farthest-point sampling (FPS) step diversifies the selected set along both the “what the teacher predicts” and “what the scene looks like” axes simultaneously. Step 3: Farthest-point sampling: Given the embedded pool {ϕ(x) : x ∈ U ′ }, we select a diversity-maximising subset D∗ ⊂ U ′ of size N by greedy FPS. Starting from an arbitrary seed d0 ∈ U ′ , we iteratively add the point that maximizes the minimum distance to all already-selected points: dt+1 =

arg max

min

x ∈ U ′ \{d0 ,...,dt } 0≤j≤t

ϕ(x) − ϕ(dj ) 2 .

(3)

Greedy FPS repeatedly adds the candidate farthest from its nearest selected neighbor, giving the standard k-center coverage approximation in the 15-dimensional descriptor space [24]. This is a geometric coverage property, not a distributional guarantee. FPS is expected to outperform confidence-ranked selection, which concentrates the pool in the region of ϕ-space with high µT and low σT . We tested this against alternative selectors and random controls (Supplementary Section S2). It does not hold at our operating point: once the pre-filter has run, differences between ranking rules are within the seed spread. It does hold without the pre-filter, where confidence ranking degrades as the active-learning literature predicts. We therefore report FPS as the selector we deploy rather than as a component whose contribution we can measure. C. Distillation Objective: OFA Given pseudo-label set D = {(xi , zi )} with zi = T (xi ), we train EfficientViT-B0 (Sθ ) using the OFA objective [13]. Lightweight branch decoder heads {Bϕi }L i=1 are attached to the student’s intermediate feature maps Fiθ (x) at each of the L encoder stages. Branch i produces a prediction bi (x) = Bϕi (Fiθ (x)) targeting the teacher’s final output. The full training loss is: LOFA (θ, ϕ) = Lhead (θ) + αOFA

L X

Ex∼D [ ℓbr (bi (x), pT (x))] ,

i=1

(4)

where the main-head loss is the fixed mixture Lhead (θ) = (1−α) ℓfocal (Sθ (x), ỹ) + α ℓKD ,

α = 0.5, (5) of a hard-label focal term [25] and the temperature-scaled logit distillation term. The hard target ỹ is the teacher’s argmax ŷT (x) = arg maxc pT (x) in the pseudo-label configurations

and the human annotation in the Sen1Floods11 ones (Supervision in the Sen1Floods11 experiments, below), L = 4 is the number of encoder stages, and the branch parameters ϕ are discarded at inference. The branch loss ℓbr is the OFA loss of Hao et al. [13] (their Eq. 6), applied per pixel: X γ pcT log bci , (6) ℓbr (bi , pT ) = − 1 + pỹT log bỹi − c̸=ỹ

where pcT is the temperature-scaled teacher probability of class c and bci the branch softmax output at that pixel. The modulation exponent γ = 1.2 raises the weight of the hard-target class where the teacher is confident in it. Setting γ = 0 removes the modulation and leaves standard knowledge-distillation crossentropy on the branch; γ = 1 retains a factor (1+pỹT ) ∈ [1, 2] on the target term. Equation 5 is the KD+cross-entropy (CE) mixture analyzed in Supplementary Section S9. The same head loss without the distillation term (focal only) is the “CE” baseline of the tables; with the distillation term but without branch heads it is the Logit-KD baseline. The model is therefore identical in architecture to a vanilla EfficientViT-B0. OFA was designed for heterogeneous teacher-student pairs [13], which is our case (ViT → CNN). Beyond the architecture argument, we show in Section V that OFA is a natural fit for pseudo-label training specifically: every term in Eq. 4 targets the teacher’s output and introduces no competing supervisory signal. Its gain over standard logit KD comes from deep-supervision gradient conditioning [26] rather than from a different optimal student, a distinction that has practical consequences for how to interpret and extend the results. Note that no term in Eq. 4 matches intermediate features, which is deliberate. The reason is empirical: adding a meansquared-error matching term between intermediate student and teacher features did not improve any benchmark in our experiments. A representation-alignment measurement in Supplementary Section S8 is consistent with that null, showing that the student trained on the full pseudo-label pool already reaches high deep-stage alignment with the teacher through logit-level supervision alone. That measurement is a similarity diagnostic rather than a demonstration that feature matching cannot help, and the alignment it reports depends on both the label source and the objective. Supervision in the Sen1Floods11 experiments: Both label sources are run through the same objectives, so “Sen1Floods11 Logit-KD” and “Sen1Floods11 OFA” are distillation configurations too, not teacher-free baselines. They load the identical frozen teacher, and the soft term of Eq. 4 and the non-target term of Eq. 6 are that teacher’s output on the Sen1Floods11 images. What the label source switches is the hard target ỹ: in the pseudo-label configurations it is the teacher’s argmax ŷT (x), and in the Sen1Floods11 configurations it is the human annotation, with Eqs. 4 and 6 otherwise unchanged. The two label sources therefore share the teacher, the objective, the architecture, the recipe and the same 252-scene annotation provenance, and differ in which images are trained on and in the source of the hard target. The two pools are not matched in native chip extent; the geometry-matched control is reported in §IV-C. The only teacher-free configuration in this paper is Sen1Floods11 CE.

Use of the Sen1Floods11 labels: The Sen1Floods11 labels are available, so a reader might ask why the student does not use them as well. Mixing the ground-truth scenes into the pseudo-label pool degrades performance at the full pool, and helps only when the pseudo pool is very small, where a same-size pseudo pool does better anyway. A two-stage schedule is cleaner to interpret and gives the same answer: initializing from a pseudo-label-trained checkpoint and finetuning on the ground truth costs 0.017 mIoU on STURM on all four seeds and multiplies the seed spread by six, while the reverse order (ground truth first, then pseudo-labels) reproduces the pseudo-only result to within 0.003 on every benchmark. The 2,500 tiles of second-stage training simply overwrite the initialization. One possible explanation is a mismatch in annotation conventions, rather than a lack of information. Boundaries are subjective at the pixel level, and human annotations frequently assign a hard label where the teacher’s probability is 0.3– 0.7; training on both at once asks the student to fit two conventions on the same object. The consequence is that there is no measured benefit to using the Sen1Floods11 labels directly, and on STURM-Flood a measured penalty, so the pseudo-label-only pipeline is not a compromise forced by their absence. Adaptation to dense prediction: The original OFA paper [13] targets image classification: branch heads are implemented as global average pooling followed by a linear layer, producing a single class-score vector per image. Flood segmentation is a dense prediction task: each branch head must produce a C × H × W output at the same spatial resolution as the teacher’s mask. We implement each branch Bϕi as a lightweight decoder comprising a 1×1 convolutional projection followed by bilinear upsampling to the student’s main-output resolution. In the main experiments, branch outputs, student logits, and live teacher targets are evaluated at the 224×224 training resolution. The branch loss ℓbr of Eq. 6 is then computed per pixel and averaged over the tile. EfficientViT-B0 has four encoder stages with channel widths C0 = 16, C1 = 32, C2 = 64, C3 = 128. Each branch head Bϕi projects from Ci to 2 classes (flood / non-flood) via a single 1 × 1 convolution with bias: the per-branch parameter counts are 34, 66, 130, and 258 respectively, summing to 488 parameters in total, which is less than 0.07% of the 0.7 M student budget. This overhead is negligible during training and absent at inference; the deployed model is architecturally identical to a vanilla EfficientViT-B0. D. Activation Replacement and Quantization-Aware Training (QAT) Activation replacement: The standard EfficientViT-B0 uses Hardswish activations throughout the backbone. Under TensorRT 8.4’s per-tensor INT8 quantization, Hardswish was not viable in our deployment: the activation’s piecewise shape produces strongly varying dynamic ranges in adjacent layers, and per-tensor scale calibration degenerates to accuracy collapse after quantization. We therefore train a separate ReLU6-from-scratch model on the same pseudo-label set. The activation replacement effects are reported in §VI.

Direct fine-tuning from the Hardswish checkpoint (swapping activations then continuing training) does not work: the Hardswish pre-trained BatchNorm running statistics are computed for a different activation distribution, and they do not settle within a reasonable fine-tuning budget. Training ReLU6 from scratch is required. Quantization-aware training: We fine-tune the ReLU6 model with 8-bit weights and activations (W8A8) quantization-aware training. Quantize–dequantize (QDQ) nodes are placed on convolution inputs and weights, but not on convolution outputs; keeping the final logits in floating point avoids a background-dominated output scale that otherwise collapses the flood range. Batch normalization (BN) affine parameters and running statistics are frozen during QAT. Without that constraint, folded biases in a few channels inflate the per-tensor activation scale by up to 9× and crush the remaining channels toward zero. Export and compilation: The QAT model is exported to the Open Neural Network Exchange (ONNX) format with torch.onnx.export, simplified, and fixed to a static 1 × 6 × 512 × 512 input for TensorRT 8.4. LiteMLA MatMul operations remain in FP16 because per-tensor INT8 collapses their attention accumulator; the deployed engine is therefore a mixed INT8/FP16 graph. Compilation is performed on the Jetson Xavier NX itself (JetPack 5.0, TensorRT 8.4), and the resulting engine is tied to that target architecture. Supplementary Section S7 gives the export-graph rewrite and the numerical precision diagnostics. IV. E XPERIMENTS A. Datasets and Evaluation Sen1Floods11 (S11) [17]: 446 paired Sentinel-1 and Sentinel-2 images across 11 flood events in 11 countries, with pixel-level binary flood labels. We use the Sentinel-2 six-band (B2, B3, B4, B8A, B11, B12) subset to match the PrithviEO-2.0 input specification, and the official split of 252 / 89 / 90 hand-annotated chips with the 15 Bolivia chips reserved as a transfer set. Our matched-budget series is capped at N = 252, the full training list. Performance is reported as mean intersection over union (mIoU) averaged over flood and non-flood classes. One property of these labels bears on the interpretation of every result below. Sen1Floods11 is a surface-water dataset: its analysts were asked to mark water areas inside a flood scene, starting from a Sentinel-2 water classification, so permanent water is part of the positive class rather than something subtracted from it [17], and the Prithvi-EO-2.0 authors describe it the same way and score it as a waterclass IoU [1]. A model trained on this target is therefore a water segmenter, not a flood-increment detector, and so is any label it writes. We claim no flood-versus-permanentwater discrimination anywhere. Accordingly we report the positive class as water IoU throughout, including on the two emergency-mapping benchmarks, where the ignore protocol of the following paragraphs removes reference water before scoring. STURM-Flood [18]: OOD benchmark from the Copernicus Emergency Management Service (EMS) activations disjoint

from S11, acquired by the same Sentinel-2 sensor; we select the six S11-matching bands from the nine it stores (Appendix A). Our evaluation uses 2,675 chips from 46 flood maps spanning 29 EMS activations. The release’s often-quoted 60 events is the Sentinel-1 ∪ Sentinel-2 union, of which our optical-only evaluation touches 29. The grouping hierarchy chip → flood map → event is what the per-group statistics of §IV-C and §IV-F use. STURM labels five water classes; we score flooded (1) and river-related (2) as flood and set open water, reservoirs and lakes (3–5) to ignore (≈3.3% of pixels). This is not STURM’s own protocol, which merges classes 1–5 into one water class over a 267-chip test split, so our STURM values are not comparable to any published STURM baseline. Because our class mapping and evaluation protocol differ from the published STURM protocol, we use STURM as a controlled OOD benchmark and do not compare its absolute scores with published baselines. Appendix A gives evidence that STURM also carries a processing-level shift relative to the Level-1C products used everywhere else here, and substitutes B8 for B8A. Both affect every model identically, which is why we use this benchmark only for paired comparisons in which the two experiments share architecture, objective, budget and augmentation: such a comparison is insensitive to a shift common to both experiments, whereas using an absolute score is not. Where we do report an STURM number, as in the student–teacher comparison of §IV-C, the processing-level shift remains a candidate explanation for part of the value and we say so there. WorldFloods-v2 [19]: the second OOD benchmark, 509 Sentinel-2 Level-1C (L1C) scene pairs, of which the test split holds 18 Copernicus EMS areas of interest (AOIs) from 11 events, tiled to 785 native 512×512 windows. Pixels marked permanent in the co-registered Joint Research Centre (JRC) yearly-history layer are set to ignore and seasonal water stays scorable; tables abbreviate this flood-only protocol as WF-fo. Permanent-water harmonization: STURM explicitly separates permanent-water classes, whereas WorldFloods does not. For a common flood-increment target we ignore permanent-water pixels in both OOD evaluations. On WorldFloods, scoring those pixels as positive raises every model’s water IoU by 0.08–0.09 but does not change any model ranking. For water-class scoring, the masking is the same operation as applying a reference-water mask before evaluation; the surface-water semantics retained from the teacher are examined separately in §IV-G. GDACS pseudo-label pool: unlabeled Sentinel-2 L1C tiles acquired around flood events listed by the Global Disaster Alert and Coordination System (GDACS), downloaded via Google Earth Engine [27]. GDACS assigns each event a Green/Orange/Red alert level from its estimated humanitarian impact; we query only Orange and Red alerts, on the rationale that higher-impact events are the ones likely to have produced an inundation large enough to be visible in a Sentinel-2 tile. GDACS reports an event as a point rather than a polygon, so a footprint has to be chosen around it: we fetch the six Prithvi fine-tuning bands over a 1,320 m radius of that point, which at the delivered ≈9.9 m sampling is a 264×264 pixel tile covering ≈2.60 km. This is the largest window we could retrieve for

every event in the catalog within the Earth Engine request budget, and it is the one respect in which the pool is unlike the two OOD benchmarks: a STURM chip (1282 , 1.28 km) or a WorldFloods AOI (a full scene, tiled) is cut from a delineated flood extent, whereas a GDACS tile is centered on a reported epicentre and may or may not contain inundation at all, which is precisely what the pre-filter of §III-B then has to decide. All three are mapped to a common input size and a common normalization before any model sees them (Appendix A). Because floods are caused by severe weather, the flood-dense scenes we most want are also the most cloud-contaminated, so a strict cloud filter would preferentially discard the imagery of interest; we accept up to 50% cloud cover, falling back to 80% for events where nothing else passes, and apply no cloud masking at any stage. What survives download and screening is 23,720 tiles from 3,603 distinct events, acquired between December 2015 and July 2026 and spanning 46◦ S–68◦ N; the N = 2,500 training subset draws on 1,404 of them. Half the pool is a second acquisition: 11,895 tiles lie inside an event window and 11,825 are pre-event baselines of the same location, drawn 30–395 days before the event start. Relative to the paired eventwindow acquisition, the realized separation is 25–502 days (median 300); baselines are retrieved under a stricter 20% cloud gate, and an audit of the acquisition dates finds every baseline strictly earlier than every event-window scene at its location. Acquisition and labeling of the pool: Event-window scenes are retrieved inside the GDACS event’s own reported interval (fromdate–todate), widened by seven days on each side only when no scene passes the cloud gate; pre-event baselines use the same fixed 30–395-day window before the event start described above. Where several Sentinel-2 Level1C scenes fall inside a window we take the single leastcloudy one and never composite. Each tile is stored at native resolution (264×264 for the 10 m bands, 132×132 for the 20 m bands); the 20 m bands are bilinearly resampled onto the 10 m grid and the tile is bilinearly resized to 224×224 before the teacher, which is also the resolution at which the teacher’s hard mask and per-pixel confidence map are stored. The 512×512 input size used elsewhere in this paper applies to benchmark evaluation, not to pool generation. Contamination audit: Because GDACS and the OOD benchmarks describe some of the same flood events, we checked geographic and temporal overlap explicitly. At the matched budget, no STURM chip or WorldFloods test AOI lies within 25 km of any of the 252 pseudo-labeled training tiles. At N = 2,500, a stricter 5 km/2-day test leaves no overlap on either benchmark. A looser 25 km/30-day screen flags three STURM activations; removing them leaves the matched-budget pseudo-minus-Sen1Floods11 gap essentially unchanged (+0.0193 mIoU per flood map over all 46, +0.0189 over the remaining 42). Distances are computed between chip and AOI centroids. STURM and WorldFloods also share a small number of EMS activations, so we treat them as complementary rather than independent; removing the overlapping WorldFloods AOIs changes all reported values by less than 0.001. The full distance/date audit is reported in

Supplementary Section S1. All models are evaluated on the same held-out test splits. Reported numbers are mean ± std across 4 random training seeds, except the teacher (single run). Micro and macro aggregation: We report both pixelpooled (micro) and unweighted per-scene (macro) IoU. This matters most on WorldFloods, where scene sizes and floodpixel counts are highly imbalanced and the model ordering can change with the aggregation rule. STURM is also strongly size-imbalanced, and scene size correlates with difficulty there (Spearman +0.709 over 46 flood maps, p < 10−4 ). Absolute micro and macro values therefore answer different weighting questions and are never compared directly. Statistical Protocol and Units of Replication: Most comparisons here can be tested along two axes. Seed level (n = 4) asks whether another training seed would reproduce an effect. We report such results as “consistent across four seeds” and not as significance. Group level asks whether another flood scene would reproduce it, and there n = 46 flood maps or 29 events on STURM and 18 scenes or 11 events on WorldFloods. We average the four seeds within each group first, so the unit of replication is the scene and not the seed, pair them across groups, and report the two-sided Wilcoxon signed-rank test [28] with Pratt’s treatment of zero differences [29]. For predefined families of related comparisons, we control the family-wise error rate using Holm’s step-down correction [30]. A 10,000-sample group bootstrap gives the one confidence interval we report, on the student–teacher difference. Because scenes inside one EMS activation are correlated, we also give the coarser event-level result for the two comparisons on which the paper’s claims rest. Secondary statistics, including exact sign tests, win rates, and alternative groupings, are in Supplementary Section S1. Choice of student architecture: The choice is a deployment constraint first and an accuracy result second, so we state what it does and does not rest on. Under the two objectives that all backbones share, an ablation against MobileNetV3Small (3.55 M) and a non-pretrained 1.64 M CNN puts the three architectures within 0.015 mIoU of each other under each shared objective on STURM, of the order of their seed spreads (Supplementary Section S8; those runs share one recipe with each other but not with Tables I and II): no architecture dominates on a comparable basis, and we do not claim EfficientViTB0 is intrinsically the best OOD backbone. The deciding property is the deployment path. EfficientViT-B0 with OFA is the best row of that ablation at 5× fewer parameters than the runner-up (MobileNetV3-Small with Logit-KD, 3.55 M), it is the smallest of the three, and it is the configuration we carried to INT8 on-device after the activation replacement of §III-D. We did not port OFA’s branch heads to the other backbones, so we cannot rule out that OFA would help them too. Naming. Two supervision sources are compared throughout, and each has exactly one name. Sen1Floods11 (abbreviated S11 in table headers and figure legends) means the handdrawn masks of the Sen1Floods11 training split, at most 252 of them; pseudo means masks written by the frozen teacher on GDACS tiles. A configuration is named by its label source, so “the Sen1Floods11 student” is the student trained on those

masks, never the student evaluated on that benchmark. Every benchmark is named explicitly where it is used. B. Baselines and Implementation Details We compare against the following baselines: • Teacher (Prithvi-EO-2.0, 300 M): upper reference only; not benchmarked on the embedded targets in this study. • UNet-ResNet50, CE, S11 (32.5 M): standard UNet [15] with ResNet-50 encoder, trained on Sen1Floods11 labels. • EfficientViT-B0, CE, S11 (0.7 M): student architecture trained on Sen1Floods11 labels only. This is the one configuration in the paper with no teacher involvement at all. • EfficientViT-B0, Logit-KD and OFA, S11 (0.7 M) and UNet-ResNet50, Logit-KD, S11 (32.5 M): the labelsource counterparts of the pseudo-label entries below, with the same objectives and the same frozen teacher, with the Sen1Floods11 human masks as the hard target (§III-C). These are the Sen1Floods11 rows of Table I and the Sen1Floods11 curves of Figs. 4 and 5, and Supplementary Fig. S4. • EfficientViT-B0, CE, pseudo (0.7 M): student trained on pseudo-labels with plain cross-entropy, no distillation loss. • UNet-ResNet50, CE, pseudo (32.5 M): the heavy baseline trained on the same pseudo-label pool. • EfficientViT-B0, Logit-KD, pseudo (0.7 M): standard temperature-scaled logit distillation. • UNet-ResNet50, Logit-KD, pseudo (32.5 M): a highercapacity non-edge reference. • EfficientViT-B0, OFA, pseudo (ours) (0.7 M): our primary model. Every pseudo-label entry at a given budget is trained on the same FPS-curated subset of the GDACS pool, so architecture and loss comparisons are made on identical data. EfficientViTB0 is initialized from ImageNet-pretrained weights and UNetResNet50 from an ImageNet-pretrained ResNet-50 encoder; all models use AdamW with a cosine learning-rate schedule. Every Sen1Floods11-versus-pseudo-label comparison is augmentation-matched: both configurations train with the same dihedral flips and the same per-channel multiplicative jitter in [0.80, 1.20]. For Logit-KD and OFA, soft targets are obtained from a live forward pass of the frozen teacher on the correspondingly augmented image; no soft logit map is stored in the pseudo-label pool (Appendix A). Because mixed precision and non-deterministic kernels alone move results by 0.003–0.010 mIoU, each table is trained under a single recipe, stated in its caption, and numbers are never compared across recipes. Full hyperparameters are in Appendix A. C. Main Results We report two operating points, and keep them in separate tables because they answer different questions. Table I fixes the training budget at 252 scenes, the complete Sen1Floods11 training split, and therefore the largest budget at which the Sen1Floods11 and teacher-labeled configurations can be compared at all, and asks what routing the labels through the

teacher is worth. Table II removes that cap and reports the deployment configuration. Matched-budget comparison: Table I asks whether a fixed manual annotation budget is more useful when the compact student is trained directly on the 252 Sen1Floods11 scenes or when the same task teacher supervises 252 different flood-event scenes. On STURM-Flood the teacher-supervised configuration is ahead in all five architecture×objective cells, by +0.017 to +0.024 mIoU per flood map. Four of the five paired Wilcoxon comparisons survive Holm correction within the five-cell block (Holm-corrected p: EfficientViT-CE 3.8 × 10−3 , Logit-KD 3.3 × 10−3 , OFA 8.9 × 10−3 , UNetLogit-KD 3.3 × 10−4 ); UNet-CE does not (p = 0.086). At the coarser event level (29 activations) three of the five survive. This supports teacher supervision as a competitive substitute for direct use of the manual split on this benchmark, not teacher-generated labels being intrinsically better than human annotations. The comparison carries a geometric qualification. Sen1Floods11 and GDACS chips do not cover the same ground extent before the common training resize. Retraining the Sen1Floods11 arm with each chip center-cropped to the GDACS tiles’ extent (four seeds, otherwise identical recipe) changes the three EfficientViT cells differently: OFA falls to +0.006 mIoU per flood map (27 of 46, p = 0.071), crossentropy to −0.0004 (25 of 46, p = 0.84), while Logit-KD rises to +0.025 (38 of 46, p = 7.9 × 10−6 ). The crop is not a clean isolation of extent, since it also removes more than half of the positive area from 86 of the 252 chips and brings training sampling closer to evaluation sampling. It does establish that the matched-budget difference cannot be attributed to label source alone. The scaling experiment is not bound by the same fixed-data constraint: additional unlabeled scenes can be supervised by the teacher without requiring new manual annotations. On the Sen1Floods11 test split, direct supervision remains favoured in most matched cells, as expected for samedistribution training. WorldFloods-v2 is more sensitive to aggregation because a single AOI carries 57% of its flood pixels, so the pooled score is close to a one-scene measurement; we therefore report both pooled and per-scene summaries and do not use that benchmark for a general label-source claim. Effect of the soft-target term at matched budget: In the EfficientViT block, plain cross-entropy on teacher-generated labels is the weakest of the three pseudo-label configurations on all three benchmarks, and adding the temperature-scaled soft term to the hard-target loss moves it by +0.018 mIoU on STURM, +0.017 on S11 and +0.005 on WorldFloods. That step changes three things at once, the soft term, its weight and the temperature, so we attribute the effect to the step and not to the soft target alone. Resolved per flood map on STURM the step is +0.0119 on 34 of 46 maps (p = 2.6 × 10−4 ), so only the CE-to-Logit-KD difference is statistically resolved at this budget. We state it as a property of this regime and not as a general claim about soft labels, because the same step on Sen1Floods11 labels produces a comparable +0.016 on STURM at N = 252. What remains specific to the pseudo-label regime is that an argmax discards

TABLE I: Matched training budget, N = 252 scenes. Every row trains on 252 images. This is the complete Sen1Floods11 training split and therefore the largest budget at which the two label sources can be compared directly: the Sen1Floods11 rows use that split, while the pseudo rows use 252 GDACS tiles labeled by the frozen Prithvi teacher, which was fine-tuned on the same split and never on GDACS. Architectures, objectives, hyperparameters, seeds and augmentation are identical. What differs is the label source and the imagery each pool supplies with it, including its native chip extent (4.63 × 5.12 km for Sen1Floods11, 2.60 × 2.62 km for GDACS; Appendix A). Mean ± std over 4 seeds, pixel-pooled (micro); teacher single-run. Bold marks the better of each Sen1Floods11/pseudo pair per column.

Model (params) Teacher, Prithvi-EO-2.0 (300 M)

Labels —

S11 test (in-distribution)

STURM-Flood (OOD)

WorldFloods-v2 (OOD)

mIoU

water IoU

mIoU

water IoU

mIoU

water IoU

0.897

0.822

0.755

0.643

0.771

0.641

Sen1Floods11 pseudo Sen1Floods11 pseudo Sen1Floods11 pseudo

0.844 ± .002 0.731 ± .005 0.825 ± .008 0.696 ± .013 0.836 ± .006 0.717 ± .009 0.842 ± .005 0.727 ± .009 0.853 ± .001 0.745 ± .001 0.852 ± .002 0.743 ± .003

0.717 ± .018 0.597 ± .017 0.744 ± .018 0.606 ± .029 0.735 ± .003 0.615 ± .005 0.748 ± .015 0.607 ± .024 0.733 ± .009 0.618 ± .011 0.752 ± .004 0.617 ± .005 0.753 ± .002 0.642 ± .003 0.753 ± .014 0.614 ± .023 0.736 ± .006 0.623 ± .006 0.770 ± .008 0.645 ± .012 0.753 ± .007 0.640 ± .011 0.760 ± .010 0.625 ± .017

Sen1Floods11 pseudo Sen1Floods11 UNet-ResNet50, Logit-KD (32.5 M) pseudo

0.862 ± .018 0.762 ± .028 0.842 ± .011 0.724 ± .020 0.876 ± .007 0.784 ± .012 0.863 ± .004 0.761 ± .007

0.721 ± .024 0.616 ± .026 0.772 ± .007 0.650 ± .008 0.736 ± .015 0.613 ± .025 0.759 ± .008 0.625 ± .012 0.739 ± .010 0.632 ± .007 0.785 ± .003 0.667 ± .005 0.763 ± .002 0.658 ± .003 0.780 ± .006 0.658 ± .010

EfficientViT-B0, CE (0.7 M) EfficientViT-B0, Logit-KD (0.7 M) EfficientViT-B0, OFA (0.7 M) UNet-ResNet50, CE (32.5 M)

the teacher’s confidence field. The soft target retains that spatial confidence information, which can improve sample efficiency even though it introduces no independent label source (Supplementary Section S9). We do not use the size of the observed gain as an information bound. Objective comparison, resolved per flood map: On pseudo-labels the ordering CE → Logit-KD → OFA is monotone on S11 and WorldFloods, while on STURM the top two objectives tie (0.735 → 0.753 → 0.753). With four seeds, no individual step is significant because the exact sign test cannot reach p < 0.05 at n = 4. We therefore resolve the two steps per flood map, over the 46 STURM flood maps. The result is the same for both label sources at this budget: the Logit-KD step is statistically resolved and the OFA step is not. On Sen1Floods11 labels the Logit-KD step is +0.0169 on 37 of 46 maps (p = 2.4 × 10−5 ) and the OFA step is −0.0023 on 18 of 46 (n.s.); on pseudo-labels they are +0.0119 on 34 of 46 (p = 2.6 × 10−4 ) and −0.0018 on 22 of 46 (n.s.). At the deployment budget neither survives. This is consistent with Fig. 2: OFA’s advantage over logit distillation occupies a window that closes at N ≈ 251, and the full Sen1Floods11 budget of 252 sits just past its right edge. We therefore do not claim OFA is the better objective at a matched budget, only that it has the strongest seed mean in the intermediate range 50 ≤ N < 252; below that range the sign is not consistent. We deploy it for the reasons given in §IV-C and §III-D. Student–teacher comparison at N = 2,500: Removing the 252-scene cap moves the compact OFA student to 0.756 ± 0.005 on STURM against the teacher’s 0.755. Averaging per flood map rather than per pixel does not change the verdict: the paired difference over the 46 flood maps is −0.0012, 95% CI [−0.008, +0.006], with the student ahead on 20 of 46 and p = 0.46, so the two are not separated at this unit of replication. Per event (29 groups) it is +0.0007, p = 0.78. This holds on one benchmark only. On WorldFloods the student remains below the teacher, by 0.007 mIoU pooled and 0.023 per scene (ahead on 2 of 18 scenes, pholm = 0.002),

TABLE II: Deployment operating results. Pool-cap removed: N = 2,500 FPS-selected (curated dataset) tiles. The Sen1Floods11 column of Table I has no counterpart here because Sen1Floods11 has no further images to add. Micro mIoU; subscripts are the seed standard deviation over 4 seeds. EfficientViT-B0 is 0.7 M parameters, UNet-ResNet50 32.5 M; † = higher-capacity model not tested for deployment. Bold marks the best model & distillation per column. Model (N = 2,500 teacher-supervised) Prithvi-EO-2.0, teacher EfficientViT-B0, CE EfficientViT-B0, Logit-KD EfficientViT-B0, OFA (ours) UNet-ResNet50, CE† UNet-ResNet50, Logit-KD†

S11

STURM

WF-fo

0.897

0.755

0.771

0.873±.002 0.875±.003 0.877±.003 0.881±.013 0.889±.006

0.754±.003 0.758±.003 0.756±.005 0.730±.016 0.747±.005

0.754±.008 0.767±.009 0.764±.002 0.755±.018 0.762±.003

and on the in-distribution S11 split the 300 M model is still ahead by 0.020 mIoU. The claim is therefore specific: on STURM-Flood, the more shifted out-of-distribution set under our protocol, a paired per-flood-map test does not separate the 0.7 M student from the foundation model it was distilled from, and the confidence interval bounds any remaining difference at well under 0.01 mIoU. This comparison has three qualifications. It does not hold on WorldFloods. STURM’s processing-level shift (Appendix A) may contribute to the reduced teacher lead. The comparison also depends on the evaluation tensor: re-scoring the same weights at STURM-Flood’s native 128×128 grid moves the paired difference to −0.028 water IoU per flood map; the teacher is ahead, but the paired test narrowly misses the 0.05 threshold (student ahead on 16 of 46, p = 0.054). Because STURM’s ground extent is fixed, this control changes effective sampling and network feature-map size jointly and cannot separate them (Supplementary Section S3). Objective differences at the deployment budget: The gap that the objective opens below 252 scenes has closed by 2,500:

clean mIoU (micro)

STURM-Flood (OOD)

WorldFloods-v2 (OOD, flood-only)

0.8

0.7

0.6

0.5

0.4

CE Logit-KD OFA

0.4 20

100

251

1000

pseudo-label pool size N

2500

Sen1Floods11 test (in-distribution)

0.9

0.7 0.6

100

251

1000

pseudo-label pool size N

2500

0.3

100

251

1000

pseudo-label pool size N

2500

Fig. 2: Effect of pool size and distillation objective. Clean micro mIoU against pseudo-label pool size for the three objectives, on all three benchmarks. EfficientViT-B0, one recipe, one pool, four seeds (±1 sd). The shaded band marks 50 ≤ N ≤ 251, the range in which OFA’s seed mean is ahead of Logit-KD on all three benchmarks; outside it the sign is not consistent. Per-seed win rates and the per-N spans are in the released CSV.

the three EfficientViT rows of Table II span 0.004 mIoU on STURM and their ordering is no longer monotone, with Logit-KD and OFA separated by less than either one’s seed spread. OFA stays above CE on every benchmark at both budgets, but the strict CE < Logit-KD < OFA ordering does not hold throughout. Read together with Table I, where the same objective comparison spans 0.018, this suggests that the choice of distillation objective matters most when training data are limited, while its effect becomes smaller at the larger deployment budget (§V). At N = 2,500, the choice among the three objectives has little effect on clean accuracy. We deploy the OFA configuration because it is the strongest one in the scarce regime a new collection starts in, and because it is the one we carried through quantization-aware training, not because it is measurably better here. The 32.5 M UNet is the more accurate model in distribution, with the best S11 score in both tables, and the less accurate one on STURM. This is consistent with the higher-capacity model fitting the teacher’s output distribution more closely at this pool size and transferring less well; the disagreement audit of Supplementary Section S8 points the same way. We do not claim the compact student is universally superior: on WorldFloods under pixel pooling at a matched budget, the Sen1Floods11 UNet-Logit-KD configuration is the strongest model in this paper (Table I). D. External Benchmark Interpretation STURM-Flood and WorldFloods-v2 are used as external evaluation sets, not as independent proof of a general robustness mechanism. They differ in scene composition, aggregation sensitivity, product preprocessing and label conventions, and they partially overlap in Copernicus Emergency Management Service activations. We therefore report both pixelpooled and per-scene summaries where appropriate and keep benchmark-specific conclusions separate. A fixed, parameter-free baseline provides a reference for interpreting external benchmark performance. We evaluate MNDWI [31], MNDWI = (B3 − B11)/(B3 + B11), thresholded at zero, through the same dataloaders, resizing, class mapping, and ignore masks as the learned models. Under pixel pooling it reaches 0.747 mIoU on STURM-Flood and 0.763

on WorldFloods-v2, against 0.755 and 0.771 for the teacher and 0.756 and 0.764 for the N=2,500 student. Paired grouplevel tests do not resolve either learned model from the rule on either clean external benchmark. This does not establish equivalence, and pooled mIoU is only one aggregation. The index is substantially weaker in distribution (0.789 mIoU and 0.650 water IoU on the Sen1Floods11 test split, against 0.877 and 0.787 for the N=2,500 student and 0.897 and 0.822 for the teacher). Its perscene WorldFloods water IoU is 0.418 against the teacher’s 0.504, while on STURM under per-scene averaging it is ahead of both models. It is exactly invariant to a scenewide multiplicative gain because it is a normalized difference, and it loses 44–66% of its mIoU under the additive haze envelope of §IV-F, where the teacher loses 4–5%. Neither the choice of index nor the threshold transfers across datasets: the normalized difference water index (NDWI) is the stronger rule in distribution and collapses on WorldFloods, and the optimum threshold differs between the benchmarks (Supplementary Section S4). Strong test-time performance of MNDWI does not make the foundation model redundant as a supervision source. In the teacher-free hard-label control, replacing teacher-generated masks with MNDWI masks reduces mIoU by approximately 0.038 on both Sen1Floods11 and STURM-Flood, although WorldFloods-v2 does not show the same ordering (Supplementary Section S4). Taken together, these results limit the interpretation of clean external accuracy. Under our group-level tests, neither learned model is statistically distinguished from the fixed MNDWI baseline on the two clean external datasets. We therefore use STURM-Flood and WorldFloods-v2 to assess external generalization of the compact model, while treating synthetic perturbation and spectral-index analyses as diagnostics. E. Label Efficiency and Scaling The matched-budget experiment is intentionally conservative because both arms are capped at 252 training scenes. The practical advantage of teacher supervision is that the cap can be removed: once the task teacher has been trained, additional Sentinel-2 scenes can be labeled automatically and

Fig. 3: Four qualitative scenes at two training budgets. Rows are the four evaluation sources (Sen1Floods11, STURM-Flood, WorldFloods-v2, and a held-out GDACS tile whose “ground truth” is the teacher’s pseudo-label); RGB, reference and teacher are budget-independent and shown once. The four model columns repeat at N = 50 and N = 2,500, with per-panel water IoU; the Sen1Floods11 column caps at the split size, so its right-hand entry is the 251-image ladder point. At N = 50 the failures differ by configuration; at the operating point all four converge onto the teacher’s answer. Display scenes were selected for low cloud cover.

F. Acquisition-Shift Diagnostics Synthetic perturbations are used here to diagnose model sensitivity, not to support a general robustness claim. Three axes are applied in reflectance space before the frozen normalization: a scene-wide multiplicative gain g ∈ [0.8, 1.3]; an additive, wavelength-dependent haze offset of strength h ∈ [0, 0.20] [23]; and a per-band gain that perturbs the visible and near-/short-wave-infrared groups differentially. Sensitivity is summarized as the worst-case mIoU drop over an axis,

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added without acquiring new manual annotations. Figure 4 and Fig. 5 show this scaling behavior under a fixed student architecture and training recipe. On STURM-Flood, teacher-supervised training is ahead of the direct Sen1Floods11 arm at the matched budgets and continues improving after the manually labeled split is exhausted. At N = 2,500 the EfficientViT-B0 OFA student reaches 0.756 mIoU against the teacher’s 0.755. The same operating point remains below the teacher on WorldFloods-v2, so scaling reduces but does not eliminate the teacher–student gap across domains. In distribution, water IoU rises from 0.743 at the matched budget to 0.787 at N = 2,500, against 0.822 for the teacher. We therefore describe scaling as narrowing the gap rather than closing it. Figure 3 illustrates the same scaling effect qualitatively at N = 50 and N = 2,500. The choice of subset selector is secondary to this result. The pre-filter prevents pathological selections, whereas differences among reasonable ranking rules are small at the deployment budget and benchmark-dependent below it. The selector comparison is reported in Supplementary Section S2.

0.5

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Fig. 4: Matched-budget and scaling comparison on STURM-Flood. EfficientViT-B0 with OFA, 4 seeds, ±1 sd. Both curves distill from the same frozen teacher and differ only in the training scenes and in the source of the hard target: N Sen1Floods11 images with the human masks, or N GDACS tiles with the teacher’s (§III-C). That teacher was fine-tuned on the same split and no GDACS imagery, so both rest on the same annotation budget; the x-axis is training-set size, not annotation cost. The pseudo-label configuration is ahead at every matched N under both aggregation rules and continues into the shaded region, where the Sen1Floods11 configuration cannot go because there are no more labeled images. The N = 4,000 run is included only as a scaling diagnostic and shows saturation beyond the N = 2,500 deployment operating point.

computed per seed and then averaged. Definitions and full results are in Supplementary Section S3. Under the scalar-gain axis the teacher-supervised student is

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Fig. 5: Matched-budget and scaling comparison as in Fig. 4 on WorldFloods-v2. The shape replicates with one visible exception: the pseudo-label configuration leads at every matched N under per-scene averaging, while under pixel pooling the Sen1Floods11 arm is 0.010 ahead at N = 200 and 252 (§IV-D). The architecture control is Supplementary Fig. S4. The N = 4,000 run is included only as a scaling diagnostic and shows saturation beyond the N = 2,500 deployment operating point.

the flatter of the two arms, and this survives the geometrymatched control (all three objective pairs, p ≤ 2.5 × 10−8 per flood map). The robustness test is a weak one, because the normalized-difference index cancels a scene-wide scalar. Therefore its worst-case drop on this axis is exactly zero, with no parameters, and the tested range overlaps the perchannel jitter both arms train on. The supported statement is brightness invariance under this diagnostic, not general radiometric robustness. The ordering does not carry over to the other two axes. Under per-band gain, with the visible and infrared groups perturbed differentially at magnitudes spanning documented Sentinel-2 Level-2A uncertainty ranges [32], the advantage disappears or reverses across objectives and benchmarks. Under haze the matched-budget advantage does not survive the geometry-matched control for any of the three objectives. Within the teacher-supervised arm, the worst-case STURMFlood haze drop decreases from 0.081 at N = 252 to 0.028 at N = 2,500; because both budgets use the same training source, this comparison is not exposed to the geometry confound above. Training-pool diversity is not isolated from other differences between the datasets, including label source, imagery, geography, and acquisition geometry. We therefore do not attribute the observed effects causally to diversity. G. Teacher Annotation Semantics The student is trained from teacher supervision and therefore is not an independent observer of the teacher’s systematic label errors. Sen1Floods11 defines surface water, and the finetuned teacher carries that convention into the pseudo-labeled pool. A pre-event audit shows that many tiles labelled as water by the teacher contain permanent or seasonal water rather than flooding from the target event. The student largely reproduces this behaviour: across four seeds, it agrees with the teacher on 96.1 ± 1.0% of these flagged baselines. At the same time,

it predicts water on only 1.9 ± 0.8% of the baselines that the teacher left empty. This agreement is not explained by overlap with the training set. Of the 2,942 flagged baselines, 961 are part of the training subset and 1,981 are held out. Agreement is almost identical for both groups: 96.0±0.6% for training tiles and 96.2±1.2% for held-out tiles. The result shows that the student also learns the teacher’s definition of water. For an operational flood-increment product, permanent or seasonal water must therefore be removed using an additional reference-water or change-detection step. We report this audit mainly as a limitation and reproducibility check rather than as a separate contribution. Increasing the amount of teacher-generated supervision also increases the amount of the teacher’s annotation semantics transferred to the student. The full audit is in Supplementary Section S5. V. E FFECT OF T RAINING -S ET S IZE AND D ISTILLATION O BJECTIVE The experiments separate two effects. At small trainingset sizes, access to soft teacher targets and the OFA auxiliary heads can improve sample efficiency. As the teachersupervised pool grows, however, objective differences shrink while all objectives benefit from additional scene coverage. At the N = 2,500 operating point, OFA and Logit-KD are not reliably separated on STURM-Flood, so we do not present OFA as the source of the final OOD performance. This is consistent with the role of the teacher in our pipeline: the student approximates the same teacher output over an increasingly broad set of inputs. At larger trainingset sizes, adding supervised scenes has a larger observed effect than changing among the evaluated output-space objectives. Supplementary diagnostics retain the gradient-path, representation-alignment, and auxiliary-supervision analyses that support this interpretation, but they are not required for the central claim. VI. D EPLOYMENT A. INT8 Deployment Accuracy Table III follows the deployment chain at N = 2,500. EfficientViT-B0 is retrained with ReLU6 for TensorRT compatibility, then quantization-aware trained, exported and compiled. Every row is the mean over the same four training seeds. The first three rows use the workstation evaluator and the last two use the on-device inference path. The higher WorldFloodsv2 mIoU after QAT is consistent with a regularization effect from quantization-aware fine-tuning and is not used as a primary accuracy claim. The like-for-like quantization comparison is device float versus device INT8. Clean accuracy is the deployment criterion; efficiency is reported separately in Table IV. Activation calibration and checkpoint selection use the Sen1Floods11 validation split. Thus the pipeline requires no new manual annotation, but existing ground-truth validation data still enters model selection and calibration. No groundtruth label contributes a training gradient to the pseudo-labeled student.

TABLE III: Accuracy through the deployment chain. EfficientViT-B0 with OFA at the N = 2,500 operating point; mean ± std over the four training seeds (42, 64, 91, 107). Micro mIoU. The first three rows are scored with the workstation evaluator, the last two through the on-device inference path. The like-for-like quantization cost is device float → device INT8. Stage

Labels

EfficientViT-B0, OFA EfficientViT-B0, OFA + ReLU6

Sen1Floods11, 252 0.7357 ± .0063 0.7701 ± .0077 pseudo, 2,500 0.7561 ± .0046 0.7639 ± .0018 pseudo, 2,500 0.7481 ± .0055 0.7714 ± .0119

+ QAT, float export (device) pseudo, 2,500 + QAT, INT8 engine (deployed) pseudo, 2,500

STURM-Flood

WorldFloods-v2

0.7557 ± .0062 0.7861 ± .0105 0.7448 ± .0236 0.7702 ± .0214

Quantization cost (device float → INT8)

−0.0110

−0.0158

B. On-Device Benchmark (Jetson Xavier NX) We use the NVIDIA Jetson Xavier NX (JetPack 5.0, TensorRT 8.4) as an accessible embedded GPU testbed. Table IV reports timing, engine size and power for the OFA, ReLU6from-scratch, 2,500-scene QAT model. These are properties of one compiled engine rather than of the trained weights, so they are hardware-build measurements and not four-seed training statistics; accuracy over the four training seeds is in Table III. Latency is measured with trtexec on one representative compiled engine per precision: 200 engine executions with 20 warm-up iterations at 512×512, batch size 1, timing GPU kernel time only (no Python, host↔device transfers, or I/O). Accuracy and export validation: Each compiled engine is checked against its corresponding float export before deployment. Evaluated through the same on-device inference path, the INT8 engine costs 0.011 mIoU on STURM-Flood and 0.016 on WorldFloods-v2 relative to the float export, over the four training seeds (Table III). TensorRT build settings, calibration choices and the export checks are in Supplementary Section S7. Deployment characteristics: FP16 is the fastest precision on this platform at 5.20 ms and 214.6 FPS; the deployed INT8 engine reaches 5.57 ms and 179.2 FPS. INT8’s advantage is footprint and peak power: a 1.5 MB engine against 2.4 MB for FP16 and 3.4 MB for FP32, and 5.83 W peak GPU power against 7.26 and 7.67 W. The profiled INT8 engines use 13.9–14.2 MB of runtime device memory (1.8 MB persistent weights, 4.0 MB scratch, 8.1–8.4 MB activations at 1×6×512×512). Host-to-device and device-to-host transfers add 0.36–0.39 ms on top of the kernel time. We did not benchmark the 300 M teacher on the Xavier NX, so the premise that it does not fit an embedded budget is argued from parameter count rather than measured here. UNet-ResNet50 would also run on this device. The compact student’s advantage on this platform is therefore engine size, latency and power characteristics rather than basic execution feasibility, and the stronger memory argument concerns tighter on-board and NPU/FPGA targets that we did not evaluate (§VII). VII. L IMITATIONS Scope of teacher, task and hardware. The study uses one geospatial foundation-model teacher, one primary compact

student, binary Sentinel-2 segmentation and one embedded deployment platform. The 300 M teacher was not benchmarked on the Xavier NX, and UNet-ResNet50 would also execute on that device. The deployment result therefore establishes a small measured engine footprint, latency and power profile, not universal infeasibility of larger models. Teacher agreement is not independent validation. The student is trained from the teacher’s output and reproduces its systematic annotation conventions (§IV-G), so agreement between them cannot be used as evidence that either is correct. All accuracy claims here rest on held-out ground truth, and the teacher-independent checks we do report are spectral proxies rather than annotations. Teacher semantics and dry-scene operation. Sen1Floods11 targets surface water, and the student largely reproduces this convention. An operational flood-increment product therefore needs a reference-water or temporal change component. The pseudo-label pre-filter also removes fully dry scenes, while both external benchmarks are centered on flood extents; false alarms on ordinary dry imagery are consequently not characterized well enough for unattended event detection. Benchmark-guided development. Method choices were refined using the same public benchmarks reported in the paper. Four training seeds, event-level tests, contamination auditing and multiplicity correction reduce but do not eliminate this risk. A future evaluation should reserve a genuinely untouched event set. VIII. C ONCLUSION We presented a foundation-model-to-edge distillation pipeline for Sentinel-2 flood segmentation. A 300 M-parameter Prithvi-EO-2.0 teacher, adapted from 252 manually labeled Sen1Floods11 training scenes, supervises additional unlabeled flood-event imagery and trains a 0.7 M-parameter EfficientViTB0 student. At the same 252-scene budget, teacher-supervised training is competitive with direct use of the human-labeled split and raises STURM-Flood performance in all tested configurations, although a geometry-matched control shows that the difference cannot be attributed to label source alone. The main benefit of the teacher route is therefore scale. Once the task teacher exists, the student training set can grow beyond the fixed manual annotation set without acquiring new manual labels. At 2,500 teacher-supervised scenes the student narrows the in-distribution water-IoU gap to the teacher (0.787 against 0.822) and matches its STURM-Flood mIoU under our evaluation protocol, while still trailing it on WorldFloods-v2. A competitive fixed-threshold MNDWI baseline bounds the interpretation of clean external accuracy: these benchmarks support external generalization of the compact model, not a general claim that learned models dominate spectral indices. After ReLU6 retraining and quantization-aware training, the student compiles to a 1.5 MB INT8 TensorRT engine and runs on a Jetson Xavier NX at 5.57 ms of GPU compute per 512 × 512 image, with approximately 14 MB of runtime device memory. These measurements demonstrate a route from a large geospatial foundation model to a compact embedded

TABLE IV: On-device efficiency on Jetson Xavier NX: GPU kernel time (trtexec, 200 iterations, 20 warm-up; no I/O overhead), for one representative compiled engine per precision. EfficientViT-B0 OFA, ReLU6+QAT. Engine size = compiled TensorRT binary on disk. Power = GPU mean/max over the run. FPS is the throughput reported by trtexec over total wall time; because successive inferences can overlap, it need not equal 1000/mean GPU latency. Italics mark the deployed configuration; bold marks the best value in each column. FP16 is the fastest precision here, INT8 the smallest. These are hardware-build measurements, not training-seed statistics; the accuracy of the chain over the four training seeds is Table III. Precision

Latency mean Latency p99 (ms ↓) (ms ↓)

FPS Engine GPU power Speedup (↑) (MB ↓) (W mean/max) vs FP32

Teacher (300 M) — not benchmarked on device FP32 FP16 INT8 (QAT, deployed)

7.91 5.20 5.57

segmenter: a fixed manual annotation budget is extended through teacher supervision to a larger training set, while most of the teacher’s task performance is retained in a model roughly 430× smaller by parameter count.

DATA , C ODE , AND E THICS S TATEMENT All satellite imagery used in this work is Copernicus Sentinel-2 data, freely available under the Copernicus open data license. The GDACS event catalog is publicly accessible, and imagery was retrieved via Google Earth Engine in accordance with its terms of service. Sen1Floods11, STURMFlood, and WorldFloods-v2 are published open datasets and were used under their respective licenses. Code for dataset construction and curation, training, evaluation, robustness experiments, and deployment is available in the repository at https://github.com/sycz00/FloodDistill. The repository also provides the curated pseudo-label pool identifiers and curation index, experiment configurations, exported ONNX models, and TensorRT engine-build configuration required to reproduce the reported pipeline. The teacher is the unmodified public Prithvi-EO-2.0-300M-TL Sen1Floods11 checkpoint. The teacher-semantics audit in Section IV-G and Supplementary Section S5 documents which systematic annotation conventions are retained by the distilled student.

ACKNOWLEDGMENT Generative AI tools were used for language editing and grammatical refinement. Anthropic Claude was also used to assist with code review and minor modifications to the plotting and experimental result-collection code. All modifications and experimental results were manually reviewed and verified by the authors.

A PPENDIX A I MPLEMENTATION D ETAILS This appendix gives the preprocessing and normalization pipeline that maps every dataset into a common reference space, and the training hyperparameters.

8.05 134.1 5.28 214.6 5.60 179.2

3.4 2.4 1.5

3.95 / 7.67 4.21 / 7.26 3.42 / 5.83

1.00× 1.52× 1.42×

Data Preprocessing and Cross-Dataset Normalization All training data (Sen1Floods11 and the GDACS pseudolabel pool) and all evaluation data are Sentinel-2, but they do not arrive in a common numerical range, and the single most important preprocessing principle in this work is that the normalization applied at evaluation time must reproduce the normalization seen during training. A model trained on Sen1Floods11 learns decision boundaries at specific positions in a normalized feature space; if an OOD dataset is mapped into a different space, those boundaries no longer apply and the apparent “domain gap” is partly an artifact of mismatched scaling. Anchor: Sen1Floods11 (S11): Sen1Floods11 is Level-1C (top-of-atmosphere reflectance). We use six bands (B2, B3, B4, B8A, B11, B12); note B8A (narrow NIR, 865 nm), not B8. Raw digital numbers (DNs) are converted to reflectance via r = DN×10−4 and then channel-standardized, r̂ = (r−µ)/σ, with per-band µ, σ computed on the S11 training split: µ = [0.1413, 0.1380, 0.1235, 0.3090, 0.2045, 0.1191], σ = [0.0741, 0.0737, 0.0869, 0.1180, 0.0977, 0.0766]. These constants define the reference space; every other dataset is mapped into it. Input resolution: The native chip sizes differ across datasets (S11 512×512, GDACS 264×264, STURM 128×128, WorldFloods 512 × 512), so we standardise on two working sizes. Training resizes every chip to 224 × 224 (bilinear for images, nearest-neighbor for masks; a resize, not a random crop). Unless otherwise stated, the main experiments use the same augmentation: dihedral flips and rotations plus multiplicative jitter in [0.80, 1.20], applied consistently to the images. For Logit-KD and OFA, the frozen teacher is evaluated on the transformed 224×224 image during training to produce the corresponding soft target (§IV-B). All students are optimized at this size. Benchmark evaluation is performed at 512 × 512 unless otherwise stated: S11 is used at its native 512, WorldFloods at its native 512, and STURM’s native 128×128 chips are upsampled to 512 (images bilinearly, label masks with nearest-neighbor interpolation) so every model sees a consistent evaluation resolution (both EfficientViT-B0 and UNet require the side length to be a multiple of their patch/stride, which 512 satisfies).

Effect of the input size: Training tensors are resized to 224×224. Because the native chip extents differ across datasets, this implies dataset-dependent effective spatial sampling and extent: a Sen1Floods11 chip covers 4.63×5.12 km and reaches ≈23 m effective sampling, whereas a GDACS tile covers ≈2.60 km and reaches ≈11.7 m. At evaluation, 512 is native sampling for Sen1Floods11 and WorldFloods-v2 (10.0 m) but a 4× upsample for STURM, whose 1282 chips cover 1.28 km and therefore reach 2.50 m effective sampling. The two OOD benchmarks are consequently not scored at a common physical scale, and no result that pools them should be read as one; §IV-C reports the STURM evaluation-scale control. The two training arms of Table I likewise differ in geometry as well as in label source; §IV-C reports the geometry-matched control. Because the students are fully convolutional [33] and EfficientViT’s linear attention is likewise resolution-agnostic, inference is not restricted to the 224 × 224 training resolution, and the models produce dense predictions for 512×512 inputs without architectural modification; evaluation uses frozen BN statistics, and the receptive fields cover both scales. We nevertheless treat the change in spatial dimensions as a potential distribution shift rather than assuming exact resolution invariance. Training at 224 keeps the ∼80-configuration ablation program computationally tractable. We fix evaluation at 512×512 as a common study protocol and did not sweep the evaluation size systematically. RGB visualization: All qualitative figures show the truecolor composite B4/B3/B2 (red/green/blue) of the six-band input. Because the tensors are channel-standardized, each displayed image is rescaled with a per-image min–max stretch to [0, 1]; this stretch is for display only and plays no role in training or evaluation. On-device evaluation: The evaluation on Jetson reuses these loaders, normalization constants, and benchmark masks at 5122 , so the TRT engines see the same preprocessing as the workstation evaluation. Differences between the pre-QAT workstation rows and the QAT device rows can therefore reflect the QAT stage and export precision rather than a preprocessing change. The higher WorldFloods-v2 mIoU of the QAT float export is consistent with a regularization effect from QAT and is not interpreted as a general accuracy gain. The device-float-to-INT8 comparison in Table III isolates quantization within the on-device path. GDACS pseudo-label pool and WorldFloods-v2: Both are Level-1C and fall naturally into the S11 space, so the S11 µ, σ are applied directly after the ×10−4 scaling, with no datasetspecific adjustment. For GDACS this also means the S11-finetuned teacher is applied in the same spectral regime it was fine-tuned in, so no dataset-specific rescaling is required. The pool carries no ground truth, so label accuracy on it is not directly measurable; §IV-G reports what the paired pre-event acquisitions establish. Training-pool composition: A side effect of the prefilter of §III-B is that every training tile contains at least 5% predicted flood, so the student never sees a fully dry scene during distillation. False-positive behavior on entirely waterfree landscapes is therefore not exercised by the training data, and neither OOD benchmark can score it because both are

cut from delineated flood extents. The pre-event baselines of §IV-G are the closest measurement we have: the student raises a false alarm on 1.9 ± 0.8% of the 8,883 baselines the teacher left empty, over four seeds. STURM normalization: STURM needs one extra step, because its chips are not distributed in reflectance units. The dataset paper documents the forward transform used to produce them: a min–max scaling with a fixed digital-number range of 400–1600 applied identically to every Sentinel-2 channel. We invert it exactly. Writing v for the stored pixel value, DN = 400 + 1200 v and reflectance = DN × 10−4 = 0.04 + 0.12 v. We apply this inverse without clipping; stored STURM values can fall below the nominal [0, 1] interval, so recovered reflectance can fall below 0.04. The six S11matching bands are then selected from STURM’s nine (indices [0, 1, 2, 6, 7, 8] of B2, B3, B4, B5, B6, B7, B8, B11, B12) and the S11 µ, σ applied unchanged. Note that STURM’s near-infrared band is B8, not the narrower B8A the other datasets supply: its authors state that they excluded B8a. We feed B8 into the model’s B8A slot, a 32 nm center-wavelength mismatch that we did not correct. A guard removes the ≈0.6% of chips containing NaN pixels. The transform is dataset-wide and image-independent, so nothing about the test set enters the normalization: no test-time adaptation and no per-image statistics. It also follows the same rule as every other dataset here, namely recover reflectance and then apply the training-split statistics. We prefer a documented inverse to an empirical rescaling of the evaluation set, since the latter fits the evaluation data to the model, and model rankings on this benchmark are sensitive to that choice. STURM’s label legend has five water classes: non-flood (0), flooded (1), river-related features (2), open water (3), reservoirs (4) and lakes (5), plus a no-data class. We score {1, 2} as flood, set {3, 4, 5} to ignore, and treat cloud and no-data as ignore (§IV-A). Relevance to the OOD claim: Applying the same fixed normalization removes simple scale differences, but STURM retains a processing-level shift and a B8/B8A band mismatch, so its domain gap mixes geographic generalization with product-level shift. The blue band provides a diagnostic for the processing-level difference. Sen1Floods11, the GDACS pool and WorldFloods-v2 are Level-1C top-of-atmosphere; the STURM chips appear not to follow the same distribution. At top-of-atmosphere the air itself scatters light into the sensor, most strongly at short wavelengths, so the blue band has a floor below which no surface can take it. Pooled over the valid pixels of 200 Sen1Floods11 tiles the 1st percentile of B2 is 0.081, and the percentiles run blue 0.081 > green 0.069 > red 0.039, which is the Rayleigh ordering. WorldFloods gives 0.080. STURM, pooled over 600 tiles, gives 0.013, with blue below green. These statistics are inconsistent with the Level1C distributions observed in Sen1Floods11 and WorldFloodsv2 and indicate that an atmospheric or radiometric correction was applied. The dataset paper does not state a processing level, so this is an inference from the data and it identifies only that a correction was applied, not which one. We do not correct for it, since atmospherically correcting the training data would change the space every model in this

paper was fitted in. Two consequences follow: part of the STURM domain gap is a processing-level gap rather than a purely geographic one, and on STURM the haze axis of §IV-F adds an atmosphere back onto a corrected image rather than deepening one that is already present. Hyperparameters Table V summarizes the training hyperparameters used across all experiments. All pseudo-label experiments use the FPS-selected pool unless the selector is named. The QAT phase uses the ReLU6-from-scratch checkpoint as starting point. TABLE V: Default training hyperparameters for the main comparisons; deviations are stated in the relevant table captions and sections. Hyperparameter

EfficientViT-B0 (all objectives)

UNet-ResNet50

Optimizer Learning rate Weight decay Learning-rate schedule Batch size Epochs Training input (resize) Evaluation resolution Input bands Data augmentation Head mixture α (focal/KD) OFA branch weight αOFA OFA modulation γ KD temperature Pseudo-label pool Seeds (reported)

AdamW 5e-5 0.05 Cosine 16 50 224×224 512×512 B2, B3, B4, B8A, B11, B12 dihedral + jitter 0.5 0.3 1.2 4.0 23,720 → 5,987 → 2,500 4

AdamW 5e-5 0.05 Cosine 16 50 224×224 512×512 B2, B3, B4, B8A, B11, B12 dihedral + jitter 0.5 N/A N/A 4.0 idem 4

QAT fine-tuning (ReLU6 model only) QAT optimizer QAT learning rate QAT epochs Quantization bits BatchNorm γ/β MatMul precision

AdamW 1e-5 10 W8A8 frozen FP16 (LiteMLA)

N/A N/A N/A N/A N/A N/A

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[33] J. Long, E. Shelhamer, and T. Darrell, “Fully convolutional networks for semantic segmentation,” in Proceedings of the IEEE Conference on Computer Vision and Pattern Recognition (CVPR), 2015, pp. 3431– 3440. [34] K. Killamsetty, D. Sivasubramanian, G. Ramakrishnan, and R. Iyer, “GLISTER: Generalization based data subset selection for efficient and robust learning,” in Proceedings of the AAAI Conference on Artificial Intelligence, vol. 35, no. 9, 2021, pp. 8110–8118. [35] T. Yu, S. Kumar, A. Gupta, S. Levine, K. Hausman, and C. Finn, “Gradient surgery for multi-task learning,” Advances in neural information processing systems, vol. 33, pp. 5824–5836, 2020. [36] S. Kornblith, M. Norouzi, H. Lee, and G. Hinton, “Similarity of neural network representations revisited,” in International conference on machine learning. PMLR, 2019, pp. 3519–3529. [37] S. I. Mirzadeh, M. Farajtabar, A. Li, N. Levine, A. Matsukawa, and H. Ghasemzadeh, “Improved knowledge distillation via teacher assistant,” in Proceedings of the AAAI conference on artificial intelligence, vol. 34, no. 04, 2020, pp. 5191–5198. Fabian Schmalstieg received the M.S. degree in computer science from the University of Freiburg, Freiburg, Germany, in 2023. Since 2024, he has been with the Fraunhofer Institute for Telecommunications, Heinrich-Hertz-Institut, Berlin, where he works as a research scientist in the Efficient Deep Learning Group. His research interests include climate-focused AI and making geospatial foundation models deployable on resource-constrained hardware. He has contributed to international standardization activities within the ISO/IEC Moving Picture Experts Group. Karsten Müller (Senior Member, IEEE) received the Dr. Ing. degree in electrical engineering and the Dipl. Ing. degree from the Technical University of Berlin, Berlin, Germany, in 2006 and 1997, respectively. Since 1997, he has been with the Fraunhofer Institute for Telecommunications, Heinrich-HertzInstitut, Berlin, where he is currently the Head of the Efficient Deep Learning Group. His research interests include multi-dimensional video coding, efficient federated learning, and compression of neural networks. He has been involved in international standardization activities, successfully contributing to the ISO/IEC Moving Picture Experts Group for work items on visual media content description, multiview, multi-texture, 3D video coding, and neural network representation. He co-chaired an adHoc Group on 3D Video Coding from 2003 to 2012. He was the Chair and Editor of IEEE conferences and the Senior Area Editor of IEEE Transactions on Image Processing.

Wojciech Samek (Member, IEEE) received the Dr. rer. nat. degree with distinction (summa cum laude) from the Technical University of Berlin, Berlin, Germany, in 2014. He is currently a Professor with the Department of Electrical Engineering and Computer Science, Technical University of Berlin, Berlin, Germany, and is jointly heading the Department of Artificial Intelligence and the Explainable AI Group, Fraunhofer Heinrich Hertz Institute (HHI), Berlin, Germany. He studied computer science with the Humboldt University of Berlin, Berlin, Germany, Heriot-Watt University, Edinburgh, U.K., and The University of Edinburgh, Edinburgh, U.K. He has coauthored more than 150 peer-reviewed journal and conference papers, some of them listed by Thomson Reuters as “Highly Cited Papers” (i.e., top 1%) in the field of Engineering. During his studies, he was awarded scholarships from the German Academic Scholarship Foundation and the DFG Research Training Group GRK 1589/1, and was a visiting Researcher with NASA Ames Research Center, Mountain View, USA. Dr. Samek is associated faculty, BIFOLD – Berlin Institute for the Foundation of Learning and Data, ELLIS Unit Berlin and DFG Graduate School BIOQIC, and a Member of the scientific advisory board of IDEAS NCBR. Furthermore, he is the Senior Editor of IEEE Transactions on Neural Networks and Learning Systems, an Editorial Board Member of PLoS ONE and Pattern Recognition, and an elected Member of the IEEE MLSP Technical Committee. He was the recipient of multiple best paper awards, including the 2020 Pattern Recognition Best Paper Award, and part of the expert group developing the ISO/IEC MPEG-17 NNC standard. He is the leading Editor of the Springer book “Explainable AI: Interpreting, Explaining and Visualizing Deep Learning” in 2019, the Co-Editor of the open access Springer book “xxAI – Beyond Explainable AI” in 2022, and organizer of various special sessions, workshops and tutorials on topics such as explainable AI, neural network compression, and federated learning.

Supplementary Material for “Cross-Architecture Foundation-Model Distillation for Edge Flood Segmentation” Fabian Schmalstieg, Karsten Müller, and Wojciech Samek The main article contains the minimum evidence needed for the central argument: the matched-budget comparison, scaling beyond the manual annotation set, external clean evaluation, and measured edge deployment. This supplement retains the longer audit trails, curation ablations, acquisition-shift diagnostics, teacher-semantics checks, optimization analyses and deployment implementation details needed for reproducibility. Robustness experiments are presented here as diagnostics rather than as a headline claim. Table, figure, section and equation numbers written without an S prefix refer to the main article; numbers carrying an S prefix are in this supplement. The abbreviations cross-entropy (CE), knowledge distillation (KD), and One-for-All (OFA) are used as in the main article. S1 DATA -OVERLAP AND C ONTAMINATION AUDIT The main article reports overlap thresholds and the sensitivity of the label-source result to removing nearby inputs. The full audit is retained here. The pseudo-pool is assembled from a global event catalog, while both out-of-distribution (OOD) datasets draw on Copernicus Emergency Management Service (EMS) flood events. The question is whether any OOD benchmark scene is effectively also a training scene. Every pool tile has a geolocation and an acquisition date, while every STURM chip and WorldFloods area of interest (AOI) has corresponding location metadata, so we answer it by comparing coordinates and dates rather than by asserting that two catalogs must be disjoint. At the matched budget no STURM chip and no WorldFloods test AOI lies within 25 km of any of the 252 training tiles the audit was run against, at any date. At the deployment budget of 2,500 tiles, 54 of the 2,675 STURM chips (2.0%, three of the 29 activations) lie within 25 km and 30 days of a training tile; no WorldFloods AOI does, and tightening the test to 5 km and two days, the scale at which two acquisitions could share ground, leaves nothing on either benchmark. Dropping those three activations raises STURM mean intersection over union (mIoU) by 0.003–0.007 for every model in the study, including the teacher, which never saw the pool, and the Sen1Floods11 configurations, which never saw GDACS: it is a difficulty property of those maps rather than an advantage that training created. Those three activations account for 4 of the 46 flood maps, and the quantity the main article reports is unmoved by dropping them: at the matched budget the pseudo-minus-Sen1Floods11 gap for our student is +0.0193 mIoU per flood map over all 46 and +0.0189 over the remaining 42. Distances are computed between chip and AOI centroids rather than footprint geometry; for WorldFloods, whose AOIs are full scenes, this is the looser of the two tests.

Separately, STURM and WorldFloods themselves share three EMS activations, amounting to coincident ground at two of the eighteen WorldFloods AOIs, so we call the two benchmarks complementary rather than independent throughout; excluding those AOIs moves every WorldFloods number by less than 0.001 mIoU. The audit is one script over the pool manifest and the two benchmark metadata tables, released with the code. Secondary statistics for the matched-budget block: The main paper reports the paired Wilcoxon test, with Holm correction across the five model comparisons. As a more conservative check, we also apply the exact sign test. After the same correction, two of the five comparisons remain significant: EfficientViT-CE (p = 4.5×10−2 ) and UNet-LogitKD (p = 7.8 × 10−4 ). Across the 46 flood maps, the pseudo-label model performs better on 32, 30, 30, 27, and 36 maps for EfficientViTCE, EfficientViT-Logit-KD, EfficientViT-OFA, UNet-CE, and UNet-Logit-KD, respectively. When the paired Wilcoxon analysis is repeated at the event level using 29 flood events, three of the five comparisons remain significant after Holm correction. S2 S UBSET S ELECTION The main article deploys farthest-point sampling (FPS) over the 15-dimensional descriptor of Eq. (2) and states that the prefilter, not the ranking rule, is the component whose effect is measurable at the deployment budget. This section records the comparison behind that statement. Selectors compared: All selectors draw N tiles from the same 5,987-tile filtered candidate pool and are followed by the identical training recipe. FPS is the greedy k-center rule of Eq. (3). Confidence ranking takes the N tiles with the highest mean teacher confidence µT . GLISTER [34] selects a subset by greedy maximization of a validation-set log-likelihood surrogate, evaluated here on the Sen1Floods11 validation split. R2Core (Reliability × Robustness Core-set) uses a lazily greedy weighted facility-location objective over the pool embedding, with tile weights combining reliability, informativeness, and measured cloud probability. Uniform filtered draws N tiles at random from the filtered pool, and uniform unfiltered draws them at random from the full 23,720-tile pool, which isolates the contribution of the pre-filter itself. Result: At N = 2,500 the clean STURM-Flood spread across all selectors is 0.012 mIoU, of the order of the seed spread, so the ranking rule is not resolved at the deployment budget. The pre-filter is: removing it costs up to 0.048 mIoU clean, and confidence ranking without the pre-filter degrades in the manner the active-learning literature predicts, because it concentrates the selection in the region of high µT and low σT .

sensor ±5% ±10% (90% px) ±20% tail

0.76 STURM mIoU (micro)

0.75 0.74 0.73

OFA, Sen1Floods11 random (no filter, 23,720) uniform (filtered, 5,987) FPS diversity (filtered, 5,987) confidence (filtered, 5,987) GLISTER (filtered, 5,987) R2-Core (filtered, 5,987)

0.72 0.71 0.70 0.69

0.7

(b)

deviation from nominal reflectance (%) 30 20 10 0 10 20

0.8 0.9 1.0 1.1 1.2 1.3 radiometric gain g (reflectance ×g)

worst-case drop in mIoU f(g = 1.0, h = 0) minf over the envelope

(a)

0.25

solid = gain · hatched = haze

0.20 0.15

OFA, Sen1Floods11 · haze

0.10 0.05

OFA, Sen1Floods11 · gain

0.00 R m m ty re ce rando unFifPoSr diverscionfiden GLISTE R2-Co

Fig. S1: Subset-selection robustness at N = 2,500 (four seeds, micro mIoU). (a) Clean accuracy across the scene-wide gain envelope, with the documented Sentinel-2 uncertainty bands shaded. (b) Worst-case mIoU drop under gain and haze, with the Sen1Floods11 reference at its N = 252 cap shown as dashed lines. R2-Core is included as an additional selector for context; no conclusion depends on this individual variant. All selector runs use the unaugmented N=2,500 curation recipe and are not comparable with Table II or §IV-F; While Sen1Floods11 OFA model at N=252 matches the augmented recipe.

FPS is retained as the deployed selector on that basis rather than on a measured advantage over the alternatives. Perturbation behavior: On the scalar-gain axis the curated configurations are uniformly flat, losing 0.003–0.010 worst-case mIoU at N = 2,500 and 0.004–0.011 in a recipematched replication at N = 252, against 0.037 for the Sen1Floods11 reference at the same budget. Because the N = 2,500 curation runs use no augmentation while the Sen1Floods11 reference trains with exactly the per-channel jitter that the gain axis tests, we repeated the comparison with the recipe matched; the difference is not an artifact of the augmentation. On the haze axis the selectors do spread, but the ordering does not survive a change of pool size, so we report no selector-level haze result. Worst-case drop is also not scale-free, and a configuration with lower clean accuracy has less to lose. These controls associate the scalar-gain difference with the training source under the tested recipes; they do not isolate scene diversity as a causal variable, and we make no diversity-causality claim. Figure S1 shows the same selector family on the two perturbation axes. The filtered selectors remain closely grouped under global gain, whereas their haze sensitivity is more dispersed. Because the haze ordering changes in the recipematched smaller-budget replication, we treat that spread descriptively rather than as a stable selector ranking. S3 S PATIAL H ARMONIZATION , E VALUATION S CALE , AND R ADIOMETRIC D IAGNOSTICS The two training sources differ in physical geometry before the common 224×224 student-training resize. Sen1Floods11 chips are approximately 4.63 × 5.12 km, whereas the downloaded GDACS tiles are approximately 2.60 × 2.62 km. A deterministic center crop of Sen1Floods11 to 264 native pixels was therefore used as a geometry-matched control. The crop is not a perfect isolation of geometry because it also removes

flood content: more than half of the positive area is lost in many chips and some become fully dry. Nevertheless, it was done for asking whether the original training-field-of-view difference can explain the matched-budget result. For the primary EfficientViT One-for-All (OFA) comparison on STURM-Flood, the clean pseudo-minus-croppedSen1Floods11 difference is about +0.006 mIoU per flood map and is not resolved at p < 0.05. Cross-entropy similarly loses a clear separation, while Logit-KD retains a stronger positive margin. This does not mean that teacher supervision has no effect, but that the original matched-budget results (pseudo labels ahead) cannot be accounted as exclusive label-source effect. Evaluation-scale control: STURM-Flood chips are distributed at 128×128 over a fixed 1.28 km extent, so the 512 evaluation tensor used throughout is a 4× upsample to 2.50 m effective sampling, against WorldFloods-v2’s native 10.0 m. We re-scored the same weights at 128, 224 and 512 while holding the ground extent fixed. Because the extent is fixed, this changes effective sampling and the network’s deepest feature-map size together and the two cannot be separated on this benchmark; 128 and 512 are exact integer resamplings of the native grid, whereas 224 is not, so the 128-versus-512 comparison is the clean one. The modified normalized difference water index (MNDWI) reference uses the same evaluation resampling as the learned models. The MNDWI index is nearly scale-invariant, moving by ≤ 0.003 across 128 − 512. The data driven models move by 0.010–0.014 and the teacher by +0.007 in the opposite direction. And the paired student–teacher comparison of the main article is not scale-invariant: at native 128 px the deployed model’s paired difference is −0.028 water IoU per flood map; the teacher is ahead, but the paired test narrowly misses the 0.05 threshold (student ahead on 16 of 46, p = 0.054). The

TABLE S1: STURM-Flood clean micro mIoU for identical weights at three evaluation tensors (fixed 1.28 km ground extent). Four training seeds where seeds exist; the teacher and the index are single deterministic models. Model

128 px 224 px 512 px (10.0 m) (5.71 m) (2.50 m)

MNDWI > 0 Teacher, Prithvi-EO-2.0 EfficientViT-B0 OFA, N = 2,500 EfficientViT-B0 Logit-KD, N = 2,500 EfficientViT-B0 CE, N = 2,500

0.7443 0.7619 0.7464 0.7436 0.7422

0.7449 0.7569 0.7590 0.7596 0.7558

0.7467 0.7550 0.7561 0.7578 0.7537

main article reports the 512 protocol throughout and discloses this sensitivity rather than claiming sampling invariance. Perturbation models: All three axes are applied in reflectance space, before the Sen1Floods11 normalization statistics are applied. Writing rb for the reflectance of band b: the scalar gain axis maps rb 7→ g rb for a single factor g ∈ {0.80, 0.90, 1.00, 1.10, 1.20, 1.30} applied to all six bands; The haze perturbation adds a wavelength-dependent offset to each band, rb′ = rb + h wb , where wb decreases from blue to short-wave infrared [23] and h ∈ {0, 0.05, 0.10, 0.20} controls the perturbation strength. For the per-band gain perturbation, we use two variants. In the first, only the visible bands (B2, B3, B4) are increased or decreased by a factor of 1 + d or 1 − d, while the near- and short-wave-infrared bands (B8A, B11, B12) remain unchanged. In the second, the two spectral groups are changed in opposite directions: when the visible bands are multiplied by 1+d, the near- and short-wave-infrared bands are multiplied by 1 − d, and vice versa. We use d ∈ {0.05, 0.10, 0.20, 0.30}. The first three severities span the order of band-dependent uncertainties reported for Sentinel-2 Level-2A products, while d = 0.30 is included as an explicit stress level [32]. Sensitivity is summarized as the worst-case drop: clean mIoU minus the lowest mIoU over the axis, computed per seed and then averaged over seeds. Figure S2 provides a qualitative illustration of the additive haze perturbation used in this diagnostic. The scalargain perturbation is visually simpler: it multiplies all six reflectances by the same factor and therefore changes the overall scene brightness without changing band ratios. We include the example only to make the synthetic perturbations concrete; the qualitative panel is not used as evidence for the robustness comparisons. Two properties of these axes matter for interpretation. A scalar gain changes neither within-band contrast nor band ratios, so a normalized-difference index (MNDWI) is exactly invariant to it, so its worst-case drop on that axis is exactly zero with no parameters; the range g ∈ [0.8, 1.2] also lies inside the per-channel jitter both training arms use for augmentation, so only g = 1.3 is an extrapolation. Per-band gain preserves within-band contrast and moves band ratios, and haze does

both. Under the per-band axis the teacher-supervised advantage does not persist and reverses on WorldFloods-v2 across objectives and severity tiers. We therefore interpret the scalargain result as brightness invariance, not as evidence of general radiometric robustness. The haze axis is additive and wavelength-dependent. Its matched-budget advantage is removed by the geometrymatched control, so it cannot be attributed to the label source. Within the teacher-supervised arm, the worst-case STURMFlood haze drop decreases from 0.081 at N = 252 to 0.028 at N = 2,500; because both budgets use the same training source, this comparison is not exposed to the geometry confound above. Paired group-level results: Under the uncropped matched-budget comparison, all six tests (three configurations × two axes) remain significant after Holm correction; the weakest is EfficientViT-CE under haze at p = 1.2 × 10−2 . Under the geometry-matched control, only the scalar-gain result survives: all three objective pairs separate per flood map at p ≤ 2.5 × 10−8 under both the Wilcoxon signed-rank and the exact sign test. Under the haze axis the matched-budget difference does not survive the geometry-matched control: against the cropped Sen1Floods11 experiment none of the three objective pairs reaches p < 0.05 (cross-entropy −0.0112, 17 of 46; Logit-KD +0.0025, 24 of 46; OFA +0.0170, 27 of 46). Part of the haze contrast is therefore attributable to acquisition geometry rather than to the label source. We consequently make no general robustness claim to the pseudo-labelled pool being more robust due to sample diversity. S4 S PECTRAL -I NDEX R EFERENCE BASELINE A fixed MNDWI threshold is evaluated through the same dataloaders, resizing, class mapping and ignore masks as the learned models. The rule is B3 − B11 , ŷ = 1[MNDWI > 0]. MNDWI = B3 + B11 It has no learned parameters and loads no checkpoint. Under the main clean protocol it reaches 0.747 mIoU on STURMFlood and 0.763 on WorldFloods-v2, and paired group-level tests separate neither the 300 M teacher nor the deployed student from it on either benchmark. Comparison Across Datasets and Aggregations: The result depends on how performance is averaged. On WorldFloods-v2, the learned models are clearly better when each scene is weighted equally: the MNDWI rule reaches only 0.418 macro water IoU, compared with 0.504 for the teacher. This shows that MNDWI performs poorly on several individual scenes, even though its pooled score remains competitive. On STURM-Flood, the opposite is true. When performance is averaged over individual scenes, MNDWI slightly outperforms both learned models. It reaches 0.5945 mIoU and 0.3891 water IoU, compared with 0.5921/0.3723 for the teacher and 0.5909/0.3664 for the N=2,500 student. We therefore report these per-scene results rather than only the pooled scores.

Fig. S2: Qualitative illustration of the haze perturbation for input, GT, teacher, UNet-Logit KD, EViT-S11, EViT-OFA pseudo, EViT-OFA INT8 with corresponding flood/water IoU. One STURM-Flood scene (rows 1–2) and one WorldFloods-v2 scene (rows 3–4) are shown clean and with additive haze at h = 0.10. The true-color composite uses a fixed zero-referenced stretch so that the applied perturbation remains visually comparable between rows. The panel is included to illustrate the appearance of the synthetic perturbation rather than to support the quantitative robustness results.

On the in-distribution Sen1Floods11 test set, however, the learned models are clearly better. MNDWI reaches 0.789 mIoU and 0.650 water IoU, compared with 0.877/0.787 for the N=2,500 student and 0.897/0.822 for the teacher. Here, the teacher performs best, followed by the N=2,500 student, with MNDWI clearly behind both. Three further properties separate the rule from the learned models. It is exactly invariant to a scene-wide multiplicative gain, so its worst-case drop on that diagnostic axis is exactly zero with no parameters. It is far more sensitive to additive haze, losing 44% of its STURM mIoU and 66% of its WorldFloods mIoU at the strongest tested level against 4–5% for the teacher, and the teacher separates from it per flood map at every tested severity. And neither the choice of index nor the threshold transfers: NDWI is the stronger rule in distribution (0.721 against 0.650 water IoU) and collapses to 0.249 on WorldFloods-v2, while the optimal threshold sits at +0.05 on STURM-Flood and +0.15 on the other two sets, so tuning it on the in-distribution split yields 0.7379 on STURM, below the untuned zero rule. Setting a threshold per domain requires labels from that domain, which is what the pipeline exists to avoid. Hard-labeler control: Replacing the teacher’s stored hard masks by MNDWI > 0 masks on the same 2,500 tiles, with everything else held fixed, separates two roles. As a labeler the foundation model is not replaceable: under plain

cross-entropy, which involves no teacher forward pass, the index-labeled student loses 0.038 mIoU in distribution and on STURM-Flood (7 of 46 flood maps, p = 1.8 × 10−6 ) and is markedly more seed-variable. As a source of hard targets it is: under OFA, where the live frozen teacher still supplies the soft targets, the two label sources are indistinguishable in distribution and on STURM-Flood, and the index-labeled arm is ahead on WorldFloods-v2 (16 of 18 scenes, p = 1.3×10−3 ). The component the pipeline depends on is therefore teacher supervision as a whole rather than the stored hard mask specifically. S5 T EACHER S EMANTICS AND F OLLOW-U P T ESTS The main article states that the student reproduces the teacher’s surface-water convention, so target-event flood products still require a reference-water step. This section gives the proxy construction, tile-level measurements, and followup self-training and teacher-assistant tests. Training on a model’s output raises a question that accuracy tables cannot answer: when the student and the teacher agree, is that because the student learned the task or because it learned the teacher? The pre-event half of the GDACS pool (Section IV-A) lets us ask it without any annotation: nothing a model marks on the 11,825 pre-event baselines (Section IVA) can be inundation caused by the target GDACS event. The teacher marks water on 2,942 of them (24.9%).

Spectral corroboration of the flagged baselines: The teacher was fine-tuned on Sen1Floods11’s surface-water annotations (Section IV-A), and a permanent river is surface water in January as much as in July. So before calling any of these predictions an invention we ask a question the teacher cannot influence: is there water there at all? We use MNDWI as an independent check of what the teacher detects on the pre-event baselines. We denote by ρwater the IoU between a model’s predicted water mask and the corresponding binary MNDWI > 0 water mask. Because these images were acquired before the target flood event, water detected in them cannot represent inundation caused by that event. MNDWI confirms that most flagged baselines do contain substantial surface water: in 77.3% of the 2,942 tiles, at least 10% of the image is classified as water, while only 9.3% contain almost no MNDWI water (water fraction below 0.02). The teacher predictions also largely coincide with these spectrally identified water areas. The median ρwater is 0.65 on flagged baselines, compared with only 0.14 on baselines where the teacher predicts no water. This suggests that the teacher is mostly detecting real surface-water features rather than producing arbitrary false positives. The problem is therefore mainly one of annotation semantics: permanent or seasonal water is a valid target for surface-water segmentation, but it should not be interpreted as new inundation caused by the target flood event. Student–teacher agreement against teacher-independent references: The two teacher-independent checks give complementary results. Across the full pool, the student’s masks agree with the teacher’s at IoU 0.624 ± 0.024 over four seeds, corresponding to disagreement over approximately 38% of the mask area. Scoring both models against two teacher-independent references shows where that difference helps from where it hurts. The first reference is ρwater , defined above. The second, ρnew , targets the flood increment. From the same MNDWI > 0 masks computed at the two dates, we take the water present at the event date and absent in the pre-event acquisition of the same location, and score a model’s mask against exactly that difference. No annotation is involved, and the pre-event acquisition acts as the reference-water layer. Two confounds limit how far this proxy can be pushed and are the reason we use it only for a directional reading. Baselines were retrieved under a stricter 20% cloud gate than event-window tiles (50%, falling back to 80%) and no cloud masking is applied at any stage, so unmasked cloud and cloud shadow enter the difference asymmetrically. The paired acquisitions are 25–502 days apart (the baseline search window is 30–395 days before the event start), so seasonal water change enters it as well. Both push in the direction of over-counting “new” water, and neither affects ρwater , which is measured on a single date. Relative to the teacher, the student moves toward both references on the 11,895 flood-date tiles (+0.013 and +0.019) and away from both on the 11,825 baselines (−0.011, −0.012). On the 2,942 baselines (teacher predicts flood) specifically it agrees with the teacher’s call on 96.1 ± 1.0% over the four training seeds, at mask IoU 0.833 ± 0.009, while raising a false alarm on only 1.9 ± 0.8% of the 8,883 baselines the teacher left empty, so this is a targeted reproduction of one specific failure rather

than a generally water-prone model. The agreement is not explained by overlap with the training set. Of the 2,942 pre-event baselines on which the teacher predicts water, about one third are part of the N = 2,500 training subset and the remaining two thirds are held out. The student’s agreement with the teacher is almost identical in both groups: 96.0 ± 0.6% on training tiles and 96.2 ± 1.2% on held-out tiles. The student therefore reproduces the teacher’s surface-water convention just as strongly on images it never saw during training. The false-alarm analysis is even more clearly held out. None of the 8,883 baselines that the teacher leaves empty can enter the training subset, because the pre-filter requires a predicted flood fraction above 0.05. The reported false-alarm rate is therefore measured entirely on unseen tiles. A compact student need not reproduce every teacher error exactly: architecture, regularization, and averaging across many scenes can make some deviations helpful on an independent reference. The flood-date proxy comparison is consistent with that possibility, but it does not establish a general zeromean-noise theorem. The baseline result shows the opposite case clearly: when the teacher’s error is tied to a systematic annotation convention, the student retains it almost intact. Consequences: The audit rules out two simple fixes in this experiment. Relabelling the pool with the student would reproduce some 96% of the flagged baseline labels, so iterative self-training does not address this semantic failure mode. A teacher-assistant experiment using a four-seed UNet-ResNet50 Logit-KD ensemble to relabel the same pool was also null across the sweep; Section S8 shows that the foundation model is the more accurate of the two on the pixels where the labelers disagree. A direct way to address the semantic mismatch is instead to use information that is independent of the teacher’s current-event mask. The paired pre-event acquisition provides exactly that reference, and the same construction that defines ρnew could be used as a reference-water veto at inference. We did not test that, so it is a suggestion rather than a result. The dominant systematic error a distilled flood segmenter carries over here is therefore not imagined water but the annotation semantics of the dataset the teacher was fine-tuned on. This is a semantic mismatch rather than an arbitrary false-positive mechanism. It can be addressed at the labeling stage or with a reference-water layer at inference, rather than by changing the distillation objective. None of our current benchmarks directly scores this failure mode (Section VII). Any pipeline that distills a surface-water foundation model into a flood product carries it, whether or not it measures it. S6 OFA G RADIENT-PATH A NALYSIS The main article retains the empirical OFA window and the interpretation that its auxiliary heads alter the optimization path without adding an independent label source. The branchlevel analysis is kept here. OFA Gradient-Path Diagnostic: OFA adds branch losses at each encoder stage i: X LOFA = LKD + αOFA Ex ℓbr (bi (x), pT (x)). i

Every branch is derived from the same frozen teacher output. The branches can therefore change how gradients reach intermediate student stages, but they do not add an independent annotation source. We do not assume that OFA and Logit-KD have identical parameter-space minima; the claim tested here is narrower: OFA’s advantage should appear as an optimization effect whose size depends on the training regime. The additional gradient paths are ⊤ L X ∂Fiθ ∇θ LOFA = ∇θ LKD + αOFA gi , (S1) ∂θ i=1 where gi = ∂ℓbr (bi , pT )/∂Fiθ . These terms provide shorter supervision paths to intermediate stages instead of routing every update through the full encoder and main head. This is the mechanism we examine below; the measurements, not an assumption of a shared optimum, are the evidence for the interpretation. Location of the OFA Difference: The gradientconditioning argument makes one clean prediction: deep supervision can only help once the branch targets themselves are stable. With too few scenes, each branch fits its own unstable local flood signal and the shared backbone receives contradictory updates, so in this regime OFA should bring no advantage. Figure 2 (main paper) is consistent with this, and it locates the effect more precisely than “scarce data” does. At N = 20 the three objectives are tied on STURM within a span of 0.008 mIoU (CE 0.401, Logit-KD 0.401, OFA 0.409); at N = 40 OFA is behind Logit-KD, by 0.008 on STURM and 0.016 on WorldFloods, on three of four seeds in both cases. OFA’s advantage exists in a window rather than at the scarce end in general: from N = 50 to N = 251 its seed mean is ahead on all three benchmarks, widest at N = 50, and by N = 2,500 the three-objective spread has narrowed to 0.004. The per-branch diagnostic (Fig. S5, Section S8) shows the branch gradients in active conflict below that window. If the observed differences mainly reflect finite-sample optimization, they should shrink as coverage grows. The data show that: the three-objective comparison spans 0.018 mIoU on STURM at 252 scenes and 0.004 at 2,500 (Tables I and II), with the ordering no longer resolvable at the larger pool. This pattern is consistent with a finite-sample optimization effect rather than a persistent advantage of the final supervisory target. Gradient surgery (PCGrad [35]) applied to the conflicting branches does not help, which is consistent with the problem being broader than removable directional conflict alone. As the exact cosine magnitudes are sensitive to the averaging window, we report the full diagnostic in Section S8. In summary, the CE-to-OFA endpoint gap at the matched budget is driven mainly by the CE-to-Logit-KD step; OFA’s distinct advantage appears over the intermediate data window and is gone at 2,500 scenes. The branch diagnostics are consistent with an optimization effect rather than with access to a new supervision source. The practical ways to improve beyond this regime are therefore different from simply adding more teacher-derived loss terms: expand scene coverage, improve the labeler, or change the student’s capacity or inductive bias. A stronger labeler only helps if its advantage is expressed on

the transfer pool itself; Section S5 and Section S8 examine that distinction. S7 D EPLOYMENT I MPLEMENTATION AND E XPORT VALIDATION Quantization and export details The main article states the 8-bit weights-and-activations (W8A8) quantization-aware training (QAT) recipe, the quantize–dequantize (QDQ) placement, the frozen batchnormalization (BN) parameters, the static export shape, and the mixed 8-bit integer (INT8)/16-bit floating-point (FP16) engine. The details below record the graph mechanics and numerical failure modes. Quantization-aware training: We apply QAT on the pseudo-label dataset using W8A8 quantization. During QAT, fake-quantize nodes are inserted at the input of each quantizable operation: a QuantizeLinear/DequantizeLinear (QDQ) pair simulates the quantization error during the forward pass using the formula x̂ = clamp(round(x/s), −128, 127) × s, where s is the per-tensor calibration scale. The backward pass computes gradients through the straight-through estimator; the model learns to minimise both segmentation loss and the representation error introduced by the fixed-scale quantization. Two non-obvious decisions had to be made to make this work without accuracy collapse: (1) QDQ only on convolution inputs and weights, never on outputs. On an intermediate layer a second quantization of the same tensor is redundant, while on the output head it is actively harmful, because there the int32 accumulator really is rescaled into int8 with a background class-dominated scale. By omitting output QDQ we leave the final logits in float (the int32 accumulator is dequantized via the input×weight scales), so the flood range survives; on intermediate layers it simply avoids a redundant node. (2) Frozen BatchNorm affine parameters during QAT. TensorRT folds each BatchNorm into its preceding√convo′ 2 lution, producing an effective weight √ w = w γ/ σ + ϵ ′ 2 and a folded bias b = β − µ γ/ σ + ϵ. The per-tensor activation scale of that fused Conv is set by the largestmagnitude channel of its output. If the BN affine parameters γ, β keep training during QAT, a few channels’ folded bias b′ can drift to large negative values, inflating the layer’s amax and hence its INT8 scale by up to 9×; every other channel in that tensor is then quantized against an over-large scale, reducing the effective resolution of the remaining channels. Freezing γ and β and the BatchNorm (BN) running statistics during quantization-aware training (QAT) keeps the folded bias stable, so only the INT8 scales adapt. Export and compilation: Export follows the standard PyTorch route: torch.onnx.export on the QAT model, followed by onnx-simplifier for constant folding. This is the common practice for QDQ deployment to TensorRT (NVIDIA’s pytorch-quantization toolkit and the TensorRT developer guide follow the same pattern). We emit three Open Neural Network Exchange (ONNX) files: a BNfolded float baseline, a simplified static-shape graph for 32bit floating-point (FP32)/FP16 compilation, and the QDQ

graph for INT8. One non-standard step is needed. When torch.onnx.export is run with dynamic batch/spatial axes, the graph carries the input shape symbolically through Shape→Gather→Concat→Reshape subgraphs operating on INT64 shape tensors (“INT64 shape chains”). TensorRT 8.4 either rejects these or builds an unnecessary dynamicshape engine. Our shape-fixing pass pins the input to a static 1×6×512×512 and constant-folds those INT64 subgraphs into fixed dimensions, leaving a clean static graph for the builder. The LiteMLA attention MatMul layers in EfficientViT remain in FP16 throughout the INT8 engine. These layers compute a linear-attention accumulator whose dynamic range is 200–400, far too large for INT8 at per-tensor granularity: at that range each INT8 bin spans ≈2.4, leaving only 1–5 distinct values for the attention normalizer channel and degrading the attention computation. INT16×INT16→INT32 accumulation would comfortably hold that range, but it is not available: TensorRT 8.4 exposes only FP32, FP16 and INT8 as builder precisions and has no INT16 GEMM tensor type, so there is no INT16 kernel for the builder to select on this hardware. INT8 being numerically unsafe and INT16 unavailable, FP16 is the only viable precision for these eight MatMuls; the resulting engine is a mixed INT8/FP16 graph. Engine compilation must be performed on the target device itself: using TRT 8.4 on the Jetson Xavier NX (JetPack 5.0) cannot transfer its engine to a different architecture target. The compiled engine is not transferable between device types. Deployment accuracy and calibration All float and quantized accuracy values use the same four training seeds (42, 64, 91, 107) and the same teachersupervised pool. ReLU6 retraining is the architecture change required for the TensorRT path; quantization-aware training is then applied to that model. Activation calibration and checkpoint selection use the existing Sen1Floods11 validation split, so no additional manual annotation is acquired and no ground-truth label contributes a training gradient to the student. Table III reports the deployment stages scored with the workstation evaluator and the two exported models scored through the on-device inference pipeline. Both paths use the same benchmark definitions and ignore masks. The higher WorldFloods-v2 mIoU of the QAT float export is consistent with a regularization effect from QAT and is not used as a primary accuracy claim. The quantization effect is evaluated within the device pipeline itself. INT8 changes mIoU from 0.7557 ± 0.0062 to 0.7448 ± 0.0236 on STURM-Flood and from 0.7861 ± 0.0105 to 0.7702±0.0214 on WorldFloods-v2, corresponding to drops of 0.0110 and 0.0158 mIoU, respectively. The larger seed spread of the INT8 engines is reported as measured. The deployment claim is restricted to clean accuracy plus measured engine characteristics. No corruption-robustness recovery is attributed to quantization. Export validation and profiling Each TensorRT export is validated against its corresponding float model before device reporting. The profiling protocol

uses batch size one with input 1 × 6 × 512 × 512, 20 warm-up iterations and 200 timed iterations. Latency, engine size and power are properties of a compiled engine rather than of the trained weights, so they are hardware-build measurements and must not be read as training-seed statistics: the main article reports one representative compiled engine per precision. For the deployed INT8 engine these are a 1.5 MB engine, 5.57 ms of graphics processing unit (GPU) compute, and 13.9–14.2 MB of device memory (1.8 MB persistent, 4.0 MB scratch, 8.1– 8.4 MB activations); host-to-device and device-to-host transfers add a further 0.36–0.39 ms. FP16 is the faster precision on this Xavier NX configuration, while INT8 gives the smallest engine and the lowest peak GPU power. S8 A DDITIONAL D IAGNOSTICS AND A BLATIONS This section collects the analyses that support design choices and secondary claims in the main article: the student– teacher representation alignment that motivates the absence of a feature-matching loss, the pixel-level imitation diagnostics, the per-branch gradient measurement behind the optimization reading of OFA, the spectral-proxy experiment, and the architecture ablation behind the choice of student. Representation Alignment via Centered Kernel Alignment This analysis asks whether the compact convolutional neural network (CNN) develops internal features similar to those of the foundation model despite the Vision Transformer (ViT)-toCNN architecture gap. Centered Kernel Alignment (CKA) [36] scores the similarity of two feature sets extracted from the same inputs, returning 1 when they agree up to an orthogonal rotation and a rescaling and near 0 when they are unrelated; that invariance is what lets it compare tensors of different channel count and resolution. We use the linear estimator and spatial CKA, with features compared on an 8×8 grid and each location treated as a sample. This is both the right question for a dense-prediction model and far more stable than pooling each image to one vector. We compute a 4×4 matrix per training condition between the four encoder stages of EfficientViT-B0 and the matched neck levels of Prithvi-EO-2.0, over 100 fixed Sen1Floods11 probe batches, and report the mean of its diagonal.1 Each condition is measured at all four training seeds. Within a seed all ten conditions share one probe loader, one probe ordering and one teacher checkpoint; across seeds the probe seed is held fixed and only the student checkpoint changes, so the model is the random variable and the instrument is not. The untrained baseline is identical to four decimal places in all four runs (0.1866), which is the check that this holds. Absolute CKA values are probe-dependent and should not be compared across papers. Figure S3 supports three observations. Alignment increases with the objective for both label sources. Mean diagonal CKA rises with the objective in every case: 0.445 → 0.474 → 0.518 on Sen1Floods11 labels, 1 Ten conditions: the ImageNet-initialized backbone without task training, and the three objectives on Sen1Floods11 labels at N = 252 and on pseudolabels at N = 252 and N = 2,500.

0.8 0.7 0.6 0.5 0.4 0.3 0.2 0.1 0.0

(a) alignment to the teacher Sen1Floods11 pseudo-labels

0.66 0.56

0.52 0.47

0.44

0.52

spatial CKA

mean diagonal spatial CKA

ImageNet-init, untrained (0.19)

Logit-KD training objective

OFA

0.8 0.7 0.6 0.5 0.4 0.3 0.2 0.1

(b) resolved by depth

Sen1Floods11 pseudo-labels untrained

S0 ×T0

S1 ×T1

S2 ×T2

S3 ×T3

student stage × matched teacher neck level

Hue = objective (CE / Logit-KD / OFA). Mean ± s.d. over 4 training seeds; 100 probe batches, identical teacher and loader for every bar and line.

Fig. S3: Representation alignment by objective and label source. (a) Mean diagonal spatial CKA between EfficientViTB0 and Prithvi-EO-2.0; the CE → Logit-KD → OFA ordering is monotone in the seed mean for both label sources. The Sen1Floods11 bars use N = 252 and the plotted pseudo-label bars use N = 2,500; the matched-budget pseudo-label values are reported in the text. (b) The same quantity resolved by depth, which is where the two label sources part company. Mean ± s.d. over four training seeds, identical teacher and probe for every bar. 0.390 → 0.435 → 0.490 on pseudo-labels at the matched budget and 0.517 → 0.563 → 0.663 at N = 2,500, against 0.187 untrained. The endpoints are the reliable part: OFA exceeds CE in 4/4 seeds in all three objective comparisons, while the individual objective steps are not all resolved at n = 4, so we claim the ordering of the endpoints and not a gap at each step. The label-source ordering in alignment reverses once the budget is released. At the matched budget the pseudo configuration is behind Sen1Floods11 labels at all three objectives (−0.055, −0.039, −0.029); released to the full pool it is ahead at every objective and in every seed (+0.072, +0.089, +0.144). So a teacher-generated label is not intrinsically better-aligned than a human one at equal count. At equal count it is measurably worse, as expected for a noisier label, but it can be produced in quantities a human label cannot, and alignment keeps buying with quantity where the accuracy curve of Section IV-E has already flattened. The matchedbudget deficit also shrinks monotonically as the objective strengthens, so distillation recovers part of what the label noise costs in representation space. The difference is concentrated in the deep stages. Panel (b) is the more informative view and the most robust result here. Hand-label training aligns the shallow and middle stages and then decreases at the deepest stage. The OFA configuration reaches 0.675 at stage 1 and falls to 0.304 at stage 3, and both other Sen1Floods11 configurations show the same pattern, while pseudo-label training at N = 2,500 holds 0.63–0.72 across all four stages. The stage-3 gap of 0.32 is present in every seed. The largest label-source difference therefore occurs at the deepest measured stage, which is consistent with limited late-stage alignment under the smaller training distribution. CKA is a representation-similarity diagnostic, so we treat this as supporting evidence rather than a causal explanation of the OOD gap. Two conclusions follow. First, the alignment ordering tracks

the accuracy ordering of Table I at the level of the endpoints, and both flatten at the deployment budget; we do not push the correspondence to the individual objective steps, since the alignment steps and the accuracy steps do not rank the two objective steps the same way. Second, and this is why we do not use feature distillation: the student already reaches high deep-stage alignment through logit-level supervision alone, so an explicit feature-matching loss has little alignment left to add. MSE matching between intermediate student and teacher features did not improve results in our experiments. Because that loss is teacher-derived, the proposition of Section S9 says only that it adds no independent label source; it does not predict the null result. The per-term gradient-cosine logs also show no consistent conflict between feature and task losses (cosines are near zero and roughly balanced in sign), so the simplest empirical reading is that the added feature objective was redundant in this setup. Two properties of the full matrices behind these diagonal means are worth recording. The objective ordering appears across the full matrix rather than on the diagonal alone: all sixteen teacher-neck × student-stage cells rise from CE to OFA, and in every trained condition on both pools the strongest single entry is off-diagonal, at teacher T0 × student S2 (0.784 for CE, 0.794 for Logit-KD and 0.810 for OFA). The student’s third stage is the layer that best reproduces the teacher’s first neck level, and the alignment stays high without peaking again deeper. This depth compression is consistent with the mismatch in capacity between a four-stage 0.7 M encoder and a 300 M ViT neck. One structural limit belongs here rather than being left to be noticed: CKA as we compute it needs discrete backbone stages to pair with the teacher’s neck levels, so the UNet-ResNet50 capacity reference cannot be measured this way at all and is absent from this analysis; nothing in this subsection should be read as a statement about it.

Student

student right

EfficientViT-B0, OFA (0.7 M) 53.8 ± 3.5% EfficientViT-B0, Logit-KD (0.7 M) 52.6 ± 0.8% UNet-ResNet50, Logit-KD (32.5 M) 44.1 ± 3.7%

pixel acc (teacher: 0.892) 0.895 0.894 0.889

0.8

(a) micro

pixel-pooled

(b) macro

Teacher (Prithvi 300M)

0.6 0.5

0.4

0.3

0.3 0.2

0.2 20

50 100

252

1000

dataset size N (scenes)

4000

beyond the Sen1Floods11 ceiling

UNet-LKD (Sen1Floods11 labels)

Imitation Diagnostics This part collects the two pixel-level diagnostics referenced in Section V and Section VII. Both are evaluated on STURMS2 at the paper’s OOD protocol (5122 , BN eval mode, identical adapter input for all models). Disagreement audit: Restrict to the valid pixels where a student and the Prithvi teacher predict different classes (2.5– 2.9% of pixels); the task is binary, so one of the two matches the ground truth. A student that corrects the teacher wins more than half of these pixels; a student whose deviations are its own imitation errors loses them. Both compact students are correct slightly more often than the teacher on pixels where they disagree: OFA on 53.8% of these pixels and Logit-KD on 52.6%. OFA also has the highest overall pixel accuracy of the three models in this audit. The 32.5 M UNet is correct on only 44.1% of its disagreement pixels. This is consistent with its lower STURM score in Table II and suggests that, at this pool size, it follows the teacher more closely rather than improving on the task itself. The advantage of the compact students is small, so we use this audit only to indicate the direction of the effect. It suggests that OFA and Logit-KD can sometimes correct teacher errors, but it does not provide a precise estimate of how large that advantage is. The audit is therefore only an indirect check and cannot replace STURM ground truth on the disagreement pixels. Section IV-G examines the same question using teacher-independent reference signals. Two-labeler audit: This audit evaluates the UNetResNet50 ensemble used in the teacher-assistant experiment (Section S5). EfficientViT-B0 is the final student architecture in this study rather than a separate intermediate-capacity assistant, so the UNet ensemble provides the distinct assistant model in this test. We examine the 4.2% of STURM pixels where the Prithvi teacher and the UNet-ensemble relabeler disagree, because only those pixels distinguish the two labeling sources. On that slice the foundation model is the more accurate of the two: it matches ground truth 60.9% of the time against the ensemble’s 39.1%. The premise of the teacherassistant chain [37], in which the intermediate model should provide the better teacher, therefore does not hold in this setting, consistent with the null relabeling result. The students behave consistently with this. At the full pool they side with the UNet ensemble on only 39.5 ± 6.8% and 40.4 ± 4.8% of those pixels across the two configurations tested: the directly distilled student, trained on pool labels generated by the Prithvi teacher, and the teacher-assistant stu-

per-scene, unweighted

Teacher (Prithvi 300M)

0.7

STURM-Flood mIoU

TABLE S2: Disagreement audit on STURM-S2 against the Prithvi teacher; students are the N = 2,500 pseudo-label configurations of Table II, 4 seeds each. Student-right = share of disagreement pixels where the student, not the teacher, matches ground truth (mean ± std over seeds); above 50% means the student corrects its teacher more often than not.

50 100

252

1000

dataset size N (scenes)

4000

UNet-LKD (Pseudo labels)

Fig. S4: Architecture control for Fig. 4: the same comparison with a 32.5 M UNet-ResNet50 under logit distillation instead of a 0.7 M EfficientViT-B0 under OFA. The gap is present throughout and is much wider at small N , where the Sen1Floods11 configuration’s seed spread is large. Routing the label budget is therefore not a property of our student. The N = 4,000 run is included only as a scaling diagnostic; the UNet curve declines beyond N=252, consistent with §IVC.

dent, the same architecture and objective trained on pool labels written by the four-seed UNet-ResNet50 Logit-KD ensemble. Swapping the labeler moves this rate by 0.9 percentage points, within the seed spread. In the scarce regime (N = 150), both configurations are close to chance level (53.2 ± 6.7% and 52.2 ± 5.9%). In neither regime does the assistant’s output displace the foundation model as the effective supervisor. OFA Inter-Branch Gradient Conflict This analysis supports the optimization interpretation of OFA with a per-branch gradient diagnostic. The OFA step is not statistically resolved at the matched budget under either label source (Section IV-C), while objective differences are also small at the deployment budget. The diagnostic therefore does not establish that OFA always helps; it shows that the deep-supervision gradients are more internally conflicting when the training set is small and become more consistent as it grows. We decomposed the OFA gradient into per-term components {gmain , gofa,i }3i=0 , where gmain is the gradient of the main head’s hard-label (focal) term and gofa,i are the four branch losses, and recorded pairwise cosine similarities during training at N ∈ {100, 300, 500} (2 seeds each; Figure S5). The direction of the effect is clear and reproducible, though the exact cosine magnitudes depend on the averaging window and should be read qualitatively. At N = 100 the branch gradients are in conflict: early-stage branches (receptive field 19–43 px) have negative cosine both with the late branches (RF 251–667 px) and, more strongly, with each other. With only 100 scenes, the branch targets are less stable and the shared backbone receives more conflicting updates. By N = 300, all inter-branch cosines are positive, and they increase further by N = 500. We describe this simply as a change in gradient consistency. The transition in the gradients (N between 100 and 300) and the threshold read off accuracy (Fig. 2: OFA is behind Logit-KD

at N = 40 and ahead from N = 50) are not the same number. At N = 100 the branches measurably conflict and OFA is nonetheless +0.010 mIoU ahead of Logit-KD on STURM, on three of four seeds. So branch conflict does not abolish the deep-supervision benefit wherever it is present; what the diagnostic establishes is the weaker claim that the conflict is real, that it resolves with N , and that it is largest exactly where OFA stops being the better objective. We do not claim it is the sole cause of that reversal. Where conflict is present, the two main-head terms remain positively aligned and continue to drive learning. The logs therefore establish the presence and disappearance of branch conflict with N , but not a unique causal role for that conflict in the accuracy curve.

Fig. S5: Inter-branch gradient conflict in OFA versus pseudolabel pool size (N ∈ {100, 300, 500}, 2 seeds; shaded bands = seed range). Negative cosine = conflicting gradient directions in the shared backbone. At N = 100 the early branches conflict with the late branches (−0.07) and, most strongly, with each other (−0.21); by N = 300 every pair has flipped positive, and cooperation strengthens further by N = 500. Exact magnitudes are averaging-window dependent; the sign change is the robust finding. Gradient surgery (PCGrad [35]) applied to the OFA branch set produced no measurable improvement. In this experiment, resolving gradient direction conflicts was therefore not sufficient to improve the small-N result. Read together with Section IV-C, this bounds the objective effect on both sides: at smaller N , branch conflict can attenuate the benefit of deep supervision; it does not eliminate it, because OFA is already ahead of Logit-KD at N = 100. At larger N , the objective differences shrink to the point that they are no longer resolved. The window in between is where the objective differences in Table I occur. Architecture Ablation To check that EfficientViT-B0 is a reasonable architecture choice (not merely the one we tuned most), we trained two additional compact CNN students on the same curated pool. To keep the comparison fair, we evaluate every architecture under the two objectives they all support (plain CE and logit-KD) and report OFA only for our own EfficientViT-B0 student, since OFA is the method we propose rather than a general baseline. We flag the missing OFA variants as a scoping decision, not a result: we cannot claim OFA would fail to help the other two, only that we did not test it.

TABLE S3: Architecture ablation at a full curated pool, 4 seeds (mean ± std). Small CNN is a 1.64 M convolutional segmentation baseline of our own, trained from scratch. ⋆ = no ImageNet pretraining. Italics mark our model; bold marks the best value. All rows share one recipe, so comparisons between rows are valid, but the absolute values are not comparable with Tables I and II. Architecture

Params Pretrain

Loss

S11 mIoU

ImageNet CE ImageNet Logit-KD None⋆ CE None⋆ Logit-KD

EfficientViT-B0 EfficientViT-B0 EfficientViT-B0

ImageNet CE 0.861 ± 0.008 ImageNet Logit-KD 0.869 ± 0.006 ImageNet OFA (ours) 0.870 ± 0.003

0.7 M 0.7 M 0.7 M

STURM mIoU

0.868 ± 0.013 0.734 ± 0.020 0.872 ± 0.002 0.746 ± 0.008 0.887 ± 0.004 0.737 ± 0.037 0.882 ± 0.002 0.739 ± 0.033

MobileNetV3-Small 3.55 M MobileNetV3-Small 3.55 M Small CNN 1.64 M Small CNN 1.64 M

0.737 ± 0.032 0.754 ± 0.023 0.760 ± 0.014

We read Table S3 conservatively. Under the objectives that all backbones support the three architectures are within 0.015 mIoU of each other under each shared objective on STURM, of the order of their seed spreads, so no architecture dominates on a like-for-like objective. EfficientViT-B0 with OFA is the best row by +0.014 over the strongest alternative configuration (MobileNetV3-Small with Logit-KD) at 5× fewer parameters. The only backbone without ImageNet pretraining is also the most seed-unstable (±0.037), consistent with the initialization mattering more than the architecture at this scale. The claim we make from this table is narrow: EfficientViT-B0 with OFA is the strongest deployable compact configuration we found, and the smallest. S9 S CALING B EYOND A F IXED M ANUAL A NNOTATION S ET This section formalizes the narrow information statement used in Section V of the main article. Let D = {(xi , T (xi ))}M i=1 be the pseudo-label dataset, where T (x) = pT (x) denotes the frozen teacher output. Proposition 1 (No independent label information). Fix the teacher T (including its parameters) and the input set {xi }. Any auxiliary training signal computed deterministically from the teacher and these inputs (for example, soft outputs, inputsensitivity maps, output variance, saliency masks, or intermediate teacher features) is a function of (T, {xi }). Conditional on (T, {xi }), it therefore contains no additional information about the unknown ground-truth labels. Such signals can change optimization, regularization, or inductive bias, but they do not introduce an independent annotation source. Let A = f (T, X) denote any deterministic auxiliary signal derived from the frozen teacher and inputs. Then H(A | T, X) = 0,

(S2)

and therefore I(Y ; A | T, X) = H(A | T, X) − H(A | Y, T, X) = 0. (S3) Thus A may alter the optimization path or inductive bias, but conditional on the teacher and inputs it cannot introduce an independent source of ground-truth label information.

The proposition is an information statement, not a bound on benchmark accuracy and not a claim that all teacher-derived objectives have the same neural-network minimiser. A useful reference is the best KL imitator available to the student class H, ∗ SKD = arg min Ex KL(pT (x) ∥ S(x)) , (S4) S∈H

but a mixed or auxiliary objective can select a different function through finite-sample optimization or regularization. That different function may score above or below the teacher on a particular ground-truth benchmark. Proposition 1 only says that such a gain is not caused by a new, independent label signal. This distinction is consistent with the disagreement audit of Section S8: some deviations from the teacher help, while systematic annotation semantics are largely retained. The KD+CE target: For a fixed temperature, Gibbs’ inequality gives the unrestricted minimizer of the KD term at q = pT . Adding a hard teacher-argmax cross-entropy term with weight 1 − α gives, per pixel, q ∗ (x) = α pT (x) + (1 − α) δŷT (x) ,

(S5)

where δŷT is one-hot at the teacher argmax. Thus α changes the mixture between two teacher-derived targets. Changing the temperature changes the soft teacher distribution pT itself; neither operation introduces labels independent of the teacher. Equation S5 is a per-pixel result for this specific KD+CE mixture and should not be read as a statement that OFA or other auxiliary objectives share its parameter-space optimum. The main experiments use focal modulation for the hardtarget term, so their exact optimum need not equal the convex mixture in Eq. S5; this does not affect Proposition 1, because both targets remain deterministic functions of the same frozen teacher. Binary soft targets: For binary segmentation (C = 2), a normalized class distribution has one independent probability degree of freedom per pixel. The teacher’s soft value can retain confidence information that its argmax removes, but its numerical precision should not be confused with an additional source of ground-truth supervision. Without assumptions about teacher calibration, pT alone does not provide a quantitative bound on how much class information the soft target adds over the argmax. We therefore interpret the measured CE-toLogit-KD differences in Tables I and II of the main article as empirical sample-efficiency effects, not estimates of an information bound. Multi-class tasks may behave differently and are outside the scope of this study.

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