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Compared head-to-head across ten satellite-imagery tasks, two geospatial foundation models differ less in which model you pick than in how you deploy it: token size and decoder choice together explain more performance variance than model id

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2026-08-01 15:11 UTC pith:I6FRL3AK

load-bearing objection A transparent, useful GFM comparison whose qualitative findings are solid, but the headline variance-decomposition claim is not statistically supported because the ANOVA design is non-orthogonal. the 4 major comments →

arxiv 2607.18504 v2 pith:I6FRL3AK submitted 2026-07-20 cs.LG cs.AIcs.CV

Now We Know? A Systematic Comparison of TerraMind and THOR

Frederick Schindlegger , Kenzo Bounegta , Eva Gmelich Meijling , Johannes Jakubik , Arnt-B{\o}rre Salberg , Theodor Forgaard , Nicolas Longepe , Valerio Marsocci This is my paper
classification cs.LG cs.AIcs.CV
keywords geospatial foundation modelsEarth observationpatch size ablationvariance decompositiondecoder complexitySAR-optical fusionbenchmark attributionViT fine-tuning
verification ladder T0 review T1 audit T2 compute T3 formal T4 reserved

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

This paper tries to establish why geospatial foundation models differ, rather than which one wins. Using two models built under a shared programme with opposite design philosophies — one that invests heavily in pretraining at a fixed resolution, one that can change its token resolution at inference time — the authors ran more than 800 controlled configurations across ten satellite-imagery use cases. Their central finding: within the configurations they explored, patch size and decoder choice jointly explain more of the observed performance differences than the identity of the model itself. They also find the two models embody complementary investment strategies, that simple sensor fusion fails to beat optical-only input in the full-data regime, and that interpreting results requires dataset-level characterisation. The practical upshot is that fixing compute budget and decoder configuration matters as much as choosing the model.

Core claim

The paper claims that the 'which model is better' question is the wrong question. Through a controlled ablation of two geospatial foundation models, it finds that architectural deployment choices — the spatial token grid (patch size) and the decoder head — jointly account for more of the variance in downstream performance than which foundation model is used, across the swept datasets and under the shared training recipe. It further shows the two models represent two viable investment strategies: TerraMind's heavy multimodal pretraining buys strong features at a fixed patch size, while THOR's variable patch size buys accuracy through denser tokenisation at inference time, closing the gap only

What carries the argument

The load-bearing device is a controlled ablation grid run under a single shared evaluation framework: ten Earth-observation use cases, with each model varied along patch size (THOR alone, over four levels), decoder type (a minimal linear head vs. a multi-scale pyramid decoder), backbone freeze state, input modality, and model scale — more than 800 runs. Performance differences are then decomposed with a one-way ANOVA, reporting eta-squared, the fraction of variance in the task metric attributable to each design factor. Patch size is the side length, in pixels, of each image patch a Vision Transformer tokenises; halving it quadruples the token count and roughly quadruples compute. This decomp

Load-bearing premise

The headline variance ranking (Section 6.9) treats every configuration as an independent, fairly sampled observation, but all full-data runs share a single seed (Section 5.1), only THOR gets a four-level patch-size sweep, and headline numbers pick each model's best configuration — if that grid asymmetry is doing the work, the ranking is a property of the experiment design, not of the models.

What would settle it

Recompute the variance decomposition on a symmetric grid: give TerraMind a properly re-pretrained patch-size sweep (ps4/8/32) and run every configuration with at least five seeds. If model identity then explains as much variance as patch size — or if the patch-size effect drops below the decoder effect — the paper's central claim is an artefact of its asymmetric single-seed grid.

Watch this falsifier — get emailed when new claim-graph text bears on it.

If this is right

  • Fix the compute budget and decoder before choosing between models: on the tested tasks, those choices move performance more than the foundation model itself.
  • For tasks with small or rare targets — floods, icebergs, artisanal mines — fine tokenisation (small patch size) is the strongest available lever, and coarse fixed tokenisation can collapse performance outright.
  • At matched compute, a pretraining-heavy model is the better buy on optical tasks; an inference-adaptive model is the better buy where spatial detail or SAR signal dominates, at several times the compute.
  • Shallow channel-concatenation or mean-pooling sensor fusion does not reliably beat optical-only input when labels are plentiful; expressive cross-attention fusion is the indicated direction.
  • Benchmarks should report attribution-style decompositions and dataset characterisation as first-class evaluation output, and headline comparisons of variable-resolution models should control for the tokenisation axis.

Where Pith is reading between the lines

These are editorial extensions of the paper, not claims the author makes directly.

  • If the variance ranking generalises beyond this pair, it predicts that re-evaluating any two ViT-based geospatial models under swapped decoders and token grids can reverse their perceived ranking — a testable prediction for future GFM comparisons.
  • Because each model tends to lead on tasks contributed by its own consortium, the decisive attribution experiment is to run both models on a task suite curated by a third party; the authors leave this open.
  • The authors' partially re-patched TerraMind — tiny-scale, only 48 epochs of embedding retraining — matching full-size rivals on three tasks hints that patch size and pretraining quality are separable axes; a full re-pretraining of TerraMind at multiple patch sizes is the natural next test.
  • A multi-seed re-run of the headline variance analysis would reveal how much of the patch-size dominance is stable signal rather than single-seed luck; the authors flag that gaps under about one percentage point may not reproduce.

Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, simulated authors' rebuttal, and a circularity audit.

Referee Report

4 major / 6 minor

Summary. The paper presents a systematic, ablation-driven comparison of two ESA Φ-lab geospatial foundation models, THOR and TerraMind, across ten EO use cases. It varies patch size, decoder type, backbone freeze regime, input modality, and model scale, and reports compute-accuracy trade-offs, low-data behaviour, cross-sensor transfer, and dataset-specific anomalies. The central claim is that, within the explored configuration space, design choices—especially patch size and decoder type—explain more downstream performance variance than the choice of foundation model itself, and that the two models embody complementary investment strategies (pretraining-time scale for TerraMind vs. inference-time tokenisation for THOR). The paper also argues that dataset-level characterisation is a necessary component of GFM benchmarking. The empirical material is extensive and transparently reported, with code availability, compute profiling, and several explicitly acknowledged limitations.

Significance. If the central attribution claim were statistically supported, this would be a valuable contribution to GFM benchmarking: it would redirect attention from leaderboard ranking to design axes, and it provides a reusable diagnostic template. The paper's strengths include the breadth of the ablation (10 datasets, >800 runs), the careful compute accounting (Table 3, Figures 1 and 3), the low-data regime analysis with multiple seeds (Section 6.8, Tables 6–7), the explicit discussion of dataset-specific anomalies (Appendix J.2), and the honest acknowledgement of confounds such as asymmetric search space, single-seed full-data runs, and consortium-of-origin provenance. However, the headline variance-decomposition claim rests on a statistically non-identifiable ANOVA design, so the main quantitative conclusion is not currently supported.

major comments (4)
  1. [§6.9, Figure 9] The central claim that 'patch size and decoder type jointly explain more performance variance than model identity' is not identifiable from the reported one-way ANOVA. The design is non-orthogonal: patch size is varied only for THOR (ps∈{4,8,16,32}), while TerraMind appears only at ps16. Consequently, the factor 'patch size' is partially confounded with model identity—the ps16 level contains both THOR and TerraMind observations, while other levels contain only THOR—and the factor 'model' is confounded with within-model patch-size variation (THOR's ps4/8/32 pulling its mean away from ps16). The sums of squares overlap; separate one-way η² values cannot be interpreted as unique variance contributions. Section 4.1 acknowledges the asymmetric search space, but Figure 9 and the text in §6.12 and §7 still treat the factors as independent. This requires either an orthogonal or properly modelled
  2. [§5.1, §6.9] All full-data runs use a single seed (seed=0), so there is no replication-based estimate of run-to-run variability. The one-way ANOVA in §6.9 treats each (model, patch size, decoder, freeze-state, modality) configuration as an independent observation; with no error variance, the analysis cannot distinguish design effects from seed noise. The paper itself cautions that gaps below ~1 pp may not be reproducible across seeds, but this caveat is not carried into the variance decomposition, where even small, non-replicated differences are converted into η² fractions. At minimum, the variance decomposition should be accompanied by a noise model or by multi-seed replication of a representative subset of configurations.
  3. [§6.11, Tables 9–10] The partially re-pretrained TerraMind-ps4 experiment is used to conclude that 'patch size and pretraining regime are, to some extent, separable design axes.' This is a load-bearing interpretive step for the patch-size attribution, but the comparison involves several uncontrolled confounds: the retrofit is Tiny-scale while the reference points are Base-scale, only the patch embedding was retrained (48 epochs, no validation split), and the tokenizer and full pretraining recipe were not used. The text acknowledges these caveats, but the conclusion is still stated more strongly than the evidence allows. The result should be presented only as a preliminary probe, with the separability claim explicitly deferred to a controlled re-pretraining study.
  4. [§6.12, §7 and Appendix J.1] The 'complementary investment strategies' narrative is partly confounded by consortium-of-origin: THOR tends to lead on FM4CS-contributed use cases and TerraMind on FAST-EO-contributed use cases, and the paper itself notes in J.1 that dataset selection, annotation protocols, and preprocessing may be more aligned with the originating consortium. This confound is acknowledged in the appendix but not reflected in the main-text synthesis, where the pattern is presented as evidence of pretraining-domain emphasis. The main text should carry the same caution, or the claim should be explicitly limited to 'consistent with, but not proof of, targeted pretraining emphasis.'
minor comments (6)
  1. [§4.2] Typo: 'Tables 4 summarises' should be 'Table 4 summarises'.
  2. [§6.9] Formatting: 'one way ANOV A' should be 'one-way ANOVA'.
  3. [Figure 5] The legend lists 'TerraMind Base+TiM' but the main text does not describe how TiM is applied in this figure; clarify or remove.
  4. [Figure 19] The caption and axis labels contain the artifact 'U/glyph1197et' (likely 'UNet'), which should be fixed.
  5. [Table 3] The table shows TerraMind at ps16 with 324 tokens, but §4.3 states 288×288 crops for large images; confirm that this is the tiled-inference token count and clarify why it differs from the 196 tokens of the native 224×224 pretraining size.
  6. [§6.2] The text says 'matched compute (ps16)' but Table 3 shows THOR ps16 at 62 GMACs vs. TerraMind ps16 at 56 GMACs; use 'near-matched' or report compute explicitly.

Circularity Check

0 steps flagged

No circularity found: the comparisons are empirical and self-citations are descriptive; the ANOVA confound is a validity limitation, not a derivation from inputs.

full rationale

The paper's central claims are based on recorded finetuning results across a shared TerraTorch protocol, not on fitting a target value and re-reporting it as a prediction. The variance decomposition in Section 6.9 uses eta^2 = SS_between / SS_total over observed mIoU values; the result is a summary of the runs, not an equation identity. The asymmetric grid (patch size varied only for THOR) and single seed are genuine statistical limitations, explicitly acknowledged in Section 4.1 ('The search space is also inherently asymmetric: THOR's variable patch size introduces four additional configurations per experiment cell...') and Section 5.1 ('All experiments use seed=0' / 'single-seed results should be interpreted with caution'). These affect the causal attribution of the headline 'patch size/decoder > model identity' claim, but they do not make the claim equivalent to its inputs by construction: the eta^2 ranking could have differed if model-identity effects were large. Self-citations to THOR [5], TerraMind [6], and PANGAEA [30] describe the models and protocol; the one borrowed qualitative finding (Section 6.3, decoder-gap 'already observed by Forgaard et al. [5]') is independently re-tested in this paper's runs. Appendix J.1 even flags a consortium confound 'by construction,' showing the authors are not hiding the limitation. No circular step meets the quotation/reduction bar.

Axiom & Free-Parameter Ledger

6 free parameters · 6 axioms · 0 invented entities

The central claim is an empirical attribution statement, so the ledger consists mainly of evaluation-validity assumptions rather than fitted physical parameters. The most load-bearing entries are the single-seed design, the asymmetric search space, and the consortium-of-origin comparability assumption; together they determine whether the variance decomposition is a fair test of 'patch size/decoder vs model identity'.

free parameters (6)
  • Random seed for full-data experiments = 0
    All full-data runs use seed=0 (Section 5.1); the headline numbers and ANOVA effect sizes in Figures 1-9 are built from single-seed runs, so any sub-1pp gap or variance share could shift with another seed.
  • Low-data split seeds = 0, 1, 2
    Low-data fractions are averaged over 3 seeds (Appendix B.3); these support the data-efficiency claims and the THOR ps4 low-data advantage.
  • Per-dataset best-configuration selection = best decoder/patch/freeze per model and dataset
    Headline results in Table 5 and Figures 1-2 select the best configuration per model and dataset. This maximizes each model's score but inflates apparent gaps and makes the variance decomposition sensitive to how many configurations were tried.
  • Loss function per task = Dice, CE, MAE, Dice+CE depending on dataset
    Loss functions are hand-selected per task (Section B.1); e.g., cross-entropy is used on CocoaMining because it 'yielded the best empirical results', a choice that can favor one model on a given dataset.
  • ground_covers for THOR = 1,280-8,640 m depending on dataset
    THOR's GSD-aware positional encoding is set with a dataset-specific ground_covers parameter matching each crop's physical extent (Section 4.3). These are operational inputs rather than fitted constants, but they are choices that affect THOR's behavior.
  • Physical batch size / gradient accumulation at THOR ps4 = physical batch 2 with 4 accumulation steps
    At ps4 on Sen1Floods11 and HLS Burn Scars, THOR uses a reduced physical batch with gradient accumulation (Section B.2). The authors check one anomaly is not a batch-size artefact, but this remains a configuration choice in the grid.
axioms (6)
  • domain assumption TerraTorch provides a neutral, shared evaluation framework for both models
    All experiments run inside TerraTorch [9] (Section 4.1); if the framework introduces model-specific protocol biases, the comparison inherits them.
  • domain assumption The two models can be treated as a controlled natural experiment despite different pretraining data, objectives, and consortium provenance
    Section 4.1 and Section J.1 acknowledge that pretraining data volume, modality coverage, and optimisation recipe differ, so any comparison reflects the full pipeline, not just the backbone. The central attribution claim depends on this comparability assumption.
  • domain assumption ANOVA on configurations is a valid decomposition of performance variance
    Section 6.9 uses one-way ANOVA treating configurations as independent observations; configurations share seeds and the patch-size factor is only defined for THOR, so independence and balance are approximate.
  • domain assumption Single-seed full-data results are representative enough for the reported effect sizes
    Section 5.1 and 6.9 warn that gaps below ~1pp may not be reproducible, yet the variance decomposition and many headline comparisons rely on single-seed runs.
  • domain assumption Dataset splits and preprocessing are valid for both models
    The paper flags split instability in Sea Ice and Flood Zone (Appendix J.2), and these datasets are excluded from the variance decomposition; other datasets are assumed to have stable splits and correct preprocessing.
  • domain assumption THOR and TerraMind pretrained weights match the descriptions in the cited prior papers [5, 6]
    The study does not retrain either model from scratch; it trusts the pretraining recipes and released weights described in the THOR and TerraMind papers authored in part by the same teams.

pith-pipeline@v1.3.0-alltime-deepseek · 38320 in / 10984 out tokens · 127077 ms · 2026-08-01T15:11:17.826276+00:00 · methodology

0 comments
read the original abstract

Benchmarks for Geospatial Foundation Models (GFMs) increasingly rank models by aggregate score, but such rankings obscure why models differ: how much of the gap is architecture, how much is decoder capacity, and how much is a use-case-specific artefact? This study addresses that gap through a controlled comparison of two GFMs developed under European Space Agency's $\Phi$-lab with contrasting design philosophies: THOR, which introduces a compute-adaptive architecture supporting variable patch sizes and unifies Sentinel-1, -2, and -3 data at their native resolutions; and TerraMind, a multimodal generative GFM pretrained with a dual-scale token/pixel objective that enables any-to-any cross-modal generation (Thinking-in-Modalities) to infer missing sensors at inference time. Rather than reporting a single leaderboard, we investigate the axes along which the two architectures actually differ - patch size, decoder complexity, finetuning regime, input modality, and model scale - across ten use cases spanning segmentation and regression in diverse domains, including climate disaster response, methane leak detection, snow monitoring, or sea ice mapping. We find that architectural design choices - patch size and decoder type in particular - explain more performance variance than model identity itself, that the two models embody complementary investment strategies (pretraining-time scale for TerraMind versus inference-time tokenisation for THOR), and that correctly interpreting results requires dataset-level characterisation. The resulting picture is not a single winner but a set of hypotheses and a diagnostic ablation methodology that we expect to generalise to future GFMs beyond THOR and TerraMind.

Figures

Figures reproduced from arXiv: 2607.18504 by Arnt-B{\o}rre Salberg, Eva Gmelich Meijling, Frederick Schindlegger, Johannes Jakubik, Kenzo Bounegta, Nicolas Longepe, Theodor Forgaard, Valerio Marsocci.

Figure 1
Figure 1. Figure 1: Performance versus computational cost across benchmark datasets. [PITH_FULL_IMAGE:figures/full_fig_p007_1.png] view at source ↗
Figure 2
Figure 2. Figure 2: Radar profile of THOR and TerraMind performance [PITH_FULL_IMAGE:figures/full_fig_p008_2.png] view at source ↗
Figure 3
Figure 3. Figure 3: Encoder and decoder compute cost by model, patch size, and decoder type on Sen1Floods11. [PITH_FULL_IMAGE:figures/full_fig_p009_3.png] view at source ↗
Figure 4
Figure 4. Figure 4: Decoder and freeze-state interaction on downstream performance, by model and dataset. [PITH_FULL_IMAGE:figures/full_fig_p010_4.png] view at source ↗
Figure 5
Figure 5. Figure 5: Frozen versus fine-tuned backbone performance across datasets, decoders, and patch sizes. [PITH_FULL_IMAGE:figures/full_fig_p011_5.png] view at source ↗
Figure 6
Figure 6. Figure 6: Modality ablation on Sen1Floods11 and CocoaMining. [PITH_FULL_IMAGE:figures/full_fig_p013_6.png] view at source ↗
Figure 7
Figure 7. Figure 7: Base versus Tiny backbone scaling across datasets, decoders, and patch sizes. [PITH_FULL_IMAGE:figures/full_fig_p013_7.png] view at source ↗
Figure 8
Figure 8. Figure 8: Data-efficiency curves on Sen1Floods11 (left) and HLS Burn Scars (right). [PITH_FULL_IMAGE:figures/full_fig_p014_8.png] view at source ↗
Figure 9
Figure 9. Figure 9: Variance decomposition of downstream performance by design factor, across four datasets. [PITH_FULL_IMAGE:figures/full_fig_p015_9.png] view at source ↗
Figure 10
Figure 10. Figure 10: Effect of Thinking-in-Modalities (TiM) on TerraMind Base performance, Sen1Floods11. a, [PITH_FULL_IMAGE:figures/full_fig_p023_10.png] view at source ↗
Figure 11
Figure 11. Figure 11: Cross-dataset rank consistency of configuration performance. [PITH_FULL_IMAGE:figures/full_fig_p024_11.png] view at source ↗
Figure 12
Figure 12. Figure 12: Compute-normalized efficiency across configurations, by dataset. [PITH_FULL_IMAGE:figures/full_fig_p025_12.png] view at source ↗
Figure 13
Figure 13. Figure 13: Marginal value of design upgrades on downstream performance, by model and dataset. [PITH_FULL_IMAGE:figures/full_fig_p026_13.png] view at source ↗
Figure 14
Figure 14. Figure 14: Computational scaling laws: performance versus total compute, by model and dataset. [PITH_FULL_IMAGE:figures/full_fig_p027_14.png] view at source ↗
Figure 15
Figure 15. Figure 15: Performance by configuration, ordered by encoder compute, across five datasets. [PITH_FULL_IMAGE:figures/full_fig_p028_15.png] view at source ↗
Figure 16
Figure 16. Figure 16: THOR performance versus patch size, across datasets, with TerraMind reference levels. [PITH_FULL_IMAGE:figures/full_fig_p029_16.png] view at source ↗
Figure 17
Figure 17. Figure 17: Performance versus token count, by dataset. [PITH_FULL_IMAGE:figures/full_fig_p030_17.png] view at source ↗
Figure 18
Figure 18. Figure 18: Performance versus total compute (GMACs), including a UNet baseline, across three datasets. [PITH_FULL_IMAGE:figures/full_fig_p031_18.png] view at source ↗
Figure 19
Figure 19. Figure 19: Performance gap between foundation models and a UNet baseline across training data fractions, for Sen1Floods11 (left) and [PITH_FULL_IMAGE:figures/full_fig_p031_19.png] view at source ↗
Figure 20
Figure 20. Figure 20: Target-class (mining) performance relative to macro mIoU on CocoaMining. a, [PITH_FULL_IMAGE:figures/full_fig_p034_20.png] view at source ↗

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