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Under review as a conference paper at ICLR 2027

PhysCrop-Risk: Progress-Aligned Sequential Risk Control for Early Crop Monitoring

Abstract

Early crop monitoring requires repeated decisions from irregular observations before harvest. Two challenges arise: calendar time poorly reflects crop development, and repeated decisions accumulate false alarms even when each is calibrated separately. We present PhysCrop-Risk, a progress aligned framework that uses growing degree days (GDD) to define causal observation boundaries and decision checkpoints, aligns Sentinel-2 and weather observations on a common thermal scale, and calibrates low yield evidence over the full season. At three crop specific checkpoints, risk scores are converted into empirical one sided -values against held out normal yield fields, and a shared significance budget controls the probability of at least one false watch. Two consecutive crossings define a more conservative action tier. On 2,171 fields spanning four countries, four crops, and nine seasons, the final checkpoint on a 322 field audit reaches an AUROC of and an AUPRC of at a median lead time of days before harvest. Under the frozen protocol, watch and persistent-action tiers achieve field season false positive rates of and , with the watch confidence interval covering the budget. An exploratory post hoc calibration analysis yields and but does not inherit the finite sample guarantee. These results show that progress aware alignment and sequence level calibration can turn partial season observations into reliable early crop risk decisions.

Primary area:
learning on time series and dynamical systems
Keywords:
sequential risk control, progress-aligned learning, partial-observation learning, multimodal time series, phenology-aware learning, remote sensing

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_wLYmOpenReview ↗
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Paper summary

The paper presents an approach to predict from multimodal data, including low resolution satellite data (Sentinel-2), weather and static geospatial variables the yield of crops. This is definitely a topic worth exploring and the ideas presented seem well motivated and sound. The presentation of the proposed approach is a bit difficult to follow, especially the notation and operationalisation of the problem could be improved with respect to clarity.

Critical strengths

Interesting, timely and relevant topic

Dedicated preprocessing pipeline with substantial domain expertise.

Well embedded in scientific literature

Critical weaknesses

The main problem when reading the modelling approach is that many of the variables are not easy to understand. It is not clear what „process“, "causal observation boundaries“, „frozen protocol“ or „persistent-action tiers“ refer to.

Additionally some of the notation could be clarified a bit better. For instance, whether variables are scalars, vectors or matrices, which dimensionality they have, what indices refer to etc. in line 141 for instance it’s not clear was X_i and the context u_i is. Are modalities indexed? Or are they assumed to be represented via the multivariate nature of the variables X_i? Examples could be helpful to illustrate this.

Many decisions of the modelling are not easy to follow - if it’s standard in the application scenario, it would be good to mention references or additional motivation, why three checkpoints are needed for instance. Also, why the process coordinate has to be monotonous (and what the process refers to).

For the empirical results it would be good to have error bars (ideally quantiles) to assess the differences between methods. The comparisons Table 1 could be explained a bit better in terms of the exact experimental settings. An important question is for instance, whether all preprocessing parameters and procedures were the same and only the ML model was changed? It seems that the advantages of the proposed model could be due to the preprocessing hyperparameters, and in that case it’s a bit misleading to present the proposed methods as the winner, it’s just a tree based model, right?

Questions for authors

Does the approach present a new model or is the contribution the preprocessing pipeline?

Were all hyperparameters of the preprocessing pipeline optimised with some standard HPO procedures (grid search, random search, bayesian global optimization,...)?

4 comments
AuthorsOpenReview ↗

R1. Meaning of the terms and notation (W1, W2)

Thank you for flagging the unclear notation. Here, process means crop development indexed by cumulative thermal time; causal observation boundary is the crop-specific GDD cutoff for a decision; frozen protocol means the preprocessing, prediction, calibration, and alert settings fixed for the original audit; and Persistent Action is an alert after two consecutive Watch crossings.

The progress coordinate is

gi(t)=∑u≤tclip(Ti,umean−5,0,25)g_i(t) = \sum_{u \le t} \mathrm{clip}(T^{\mathrm{mean}}_{i,u}-5,0,25)

a non-decreasing scalar. At look kk, crop cic_i has a scalar threshold Lci,kL_{c_i,k}. The causal prefix is defined as Xi(k)=(xi,t)gi(t)≤Lci,k\mathcal{X}_i^{(k)} = (x_{i,t})_{g_i(t) \le L_{c_i,k}} , containing only observations available up to this cutoff in their original temporal order. These prefixes are nested across successive checkpoints.

Table R1a. Main symbols and dimensions.

SymbolDimension / typeMeaning
Xi\mathcal{X}_iTi×18T_i \times 18 sequenceIrregular dynamic observations
xi,tx_{i,t}R18\mathbb{R}^{18}Satellite, spectral-index, validity, precipitation channels
uiu_iR23\mathbb{R}^{23}Static soil, terrain, geometry and domain context
Xi(k)\mathcal{X}_i^{(k)}Sequence prefixObservations available up to the crop-specific GDD cutoff
hi,kh_{i,k}R131\mathbb{R}^{131}Constructed model input
gi(t),Lc,kg_i(t), L_{c,k}ScalarsProgress and checkpoint thresholds

Modalities are identified by channel position, rather than a separate modality index. The 18 dynamic channels are sampled at six positions (108 values), then concatenated with 23 static features; see HZZH R5.

The alert rules are

\qquad A_{i,k}=W_{i,k-1}W_{i,k}.$$ We will add these definitions and a step-by-step input schematic to the methods section.
AuthorsOpenReview ↗

R2. Why GDD, why three looks, and how settings were chosen (W3, Q2)

GDD increments are nonnegative, so later checkpoints include earlier observation histories. It also aligns fields by accumulated heat, which is closer to crop development than calendar time. In the controlled comparison, GDD gives RMSE 1.0361 versus 1.0961 with calendar-day alignment (paired 95% CI for the difference [−0.1328,−0.0001][-0.1328, -0.0001]; HZZH R4, Table R4a).

The three look thresholds at 35/50/65% of crop-specific median seasonal GDD provide an early reading, an update, and a later decision. The 278-field development sensitivity experiment shows Action FPR/recall of 0.43%/13.33% for the original schedule, versus 3.00%/24.44% for four looks and 3.86%/28.89% when three looks shift later (HZZH R4, Table R4b). These results demonstrate the trade-off; the original schedule was not selected to maximize recall.

Preprocessing involved three categories of design choices: fixed agronomic/data definitions (SCL classes 4/5, four indices, GDD base 5°C and cap 25, six sampling positions); training-fold estimates (crop-specific GDD cutoffs, imputation, country–crop target normalization and q20 thresholds); and development selection (11-point mixture grid on 154 farm-disjoint early-stop fields, giving λ=(0,0,0.1)\lambda=(0,0,0.1), plus the original alpha spending and persistence rule). We did not perform an exhaustive grid, random, or Bayesian search across all preprocessing and model configurations. Normal-field scores from early-stop were reused in the original pooled null, with the formal consequence explained in PrXb R1.

AuthorsOpenReview ↗

R3. What is new, and what is being compared? (W4, Q1)

The main contribution is a progress-aligned multimodal representation and an integrated monitoring framework, rather than a new regression architecture. GDD defines both observation boundaries and a common temporal coordinate; a constructed 131-dimensional vector enters ExtraTrees/HGB; risk scores support screening and optional, conservative escalation. The mean-preserving spatial branch adds 10 m within-field evidence without changing the field prediction (original paper, Fig. 4: median localization AUROC 0.7316).

The full baseline comparison in HZZH R1, Table R1a evaluates complete pipelines, not the same preprocessing with only the predictor swapped. Architecture-specific inputs differ: aligned tabular features for trees, sequences for temporal models, frozen image features for AgriFM, and adapted modality fusion for MMGF. We therefore use separate controlled ablations for the representation: the same predictor and causal prefix under calendar vs GDD alignment (HZZH R4, Table R4a) and modality removal on the development challenge (full 1.0361, without weather 1.0936, without static context 1.0496, without indices 1.0521, Sentinel-2 only 1.1419 RMSE).

Model settings were fixed or selected by model-specific development early stopping; no common exhaustive HPO was used. The MLP's 15% internal validation was not farm-grouped and belongs only to the fixed-split comparison. The ExtraTrees/HGB mixture gives a small fixed-split benefit over aligned ExtraTrees (1.0361 vs 1.0459), but five-fold farm-disjoint OOF RMSE is essentially tied (1.2224 vs 1.2212, paired 95% CI [−0.0087, 0.0130]; HZZH R2, Table R2a). Our evidence therefore points primarily to the representation and integrated monitoring use case. The incremental advantage of the mixture itself is limited. A direct same-calibration policy comparison (PrXb R3) finds that Persistence reduces false alerts but also substantially reduces recall; its value depends on the costs of false alerts and missed fields.

Thank you very much again for your thoughtful review and for taking the time to consider our detailed response.

We sincerely hope that our clarifications have helped address your concerns. We would be very grateful if you could let us know whether there is anything else we might clarify or improve. We would be more than happy to provide any additional explanations or evidence that could be helpful for your assessment.

We truly appreciate your time and patience, especially during this busy reviewing period. Thank you again for your consideration!

Reviewer_PrXbOpenReview ↗
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Paper summary

PhysCrop-Risk addresses early crop monitoring as a sequential decision problem, aiming to identify low-yield fields while controlling the probability of any false alert over a growing season. It uses growing degree days to define three observation checkpoints and align partial Sentinel-2 and weather histories, combined with static environmental information. Tree-based regressors predict final yield, and domain-normalized risk scores are converted into empirical p-values with a shared significance budget. A single threshold crossing triggers a watch, while consecutive crossings trigger an action. A spatial residual model additionally produces 10 m yield maps while preserving field-level predictions.

Validation uses 2,171 fields spanning four countries, four crops, and nine seasons, including alignment and modality ablations, season-held-out and farm-disjoint evaluations, and spatial comparisons. On a 322-field audit, the final checkpoint achieves AUROC 0.8331 and AUPRC 0.6245. The frozen protocol reports season-level false-positive rates of 5.24% for watches and 2.02% for persistent actions.

Critical strengths

1.Controlled evidence for progress-aligned multimodal prediction.

Table 2 compares temporal coordinates while holding the causal observation prefix, feature dimension, and predictor family fixed. GDD alignment improves RMSE over calendar alignment, with a paired confidence interval excluding zero; the modality ablations also show complementary contributions from weather and domain context. This is consequential because it provides evidence that the proposed representation choices contribute useful predictive information, rather than attributing improvements solely to a different model or access to later observations.

2.Quantitatively validated spatial refinement that preserves the field-level decision.

Equations (13)–(14) ensure that the spatial residual branch preserves the field-level prediction exactly. Section 5.5 and Figure 4 show lower spatial RMSE than both uniform field predictions and an NDVI residual baseline, alongside a median within-field low-yield localization AUROC of 0.7316. This strengthens the empirical contribution by connecting field-level risk estimates to spatially localized evidence for scouting, while ensuring that refinement does not alter the prediction underlying the alert.

Critical weaknesses

1.The finite-sample guarantee is not established for the implemented calibration protocol.

Proposition 1 follows if the reference and evaluation scores are exchangeable. However, the early-stop partition is used to select mixture weights and is then incorporated into the null calibration library (Sections 4.1–4.2; Appendices A–C). Freezing this procedure before accessing audit outcomes does not itself establish the required exchangeability, and the proof does not account for this data reuse. This is consequential because season-level risk control is a central contribution: the conditional theorem alone does not substantiate the guarantee claimed for the deployed protocol.

2.The evaluation does not sufficiently establish the benefit of sequential early-warning decisions.

The reported 62.5-day lead time measures the interval from the latest satellite acquisition to harvest, rather than the actual checkpoint or alert time (Section 5.3). Moreover, the watch/action comparisons change both false-positive rate and sensitivity, without isolating persistence against a stricter single-crossing rule or a final-checkpoint-only rule under a matched season-level false-positive constraint (Table 3; Figure 3(d); Table 9). Conservative sensitivity can be appropriate, but these omissions leave unclear whether repeated monitoring delivers earlier or more effective warnings than simpler alternatives. This limits support for the paper’s decision-level contribution beyond yield prediction.

Questions for authors

1.Clarification of calibration validity.

Sections 4.1–4.2 and Appendices A–C indicate that early-stop labels are used both to select mixture weights and to construct the frozen null library. What establishes the score exchangeability required by Proposition 1 under this reuse? Was there an independent calibration step not described in the manuscript, or an argument accounting for model selection? The answer would determine whether the finite-sample guarantee applies to the evaluated protocol.

2.Clarification of actual warning time.

Section 5.3 defines the reported lead time using the latest satellite acquisition. What are the lead times measured from the actual checkpoint decisions and first watch/action events, and were all required inputs available at those times? This would determine whether the reported early-prediction performance translates into comparably early operational warnings.

3.Evidence supporting the current sequential-decision claim.

Do the existing experiments compare persistence with a stricter single-crossing rule and a final-checkpoint-only rule under the same season-level false-positive constraint, using development-only threshold selection? If so, please identify the results and report sensitivity and first-alert timing on the same evaluation cohort. This is a request to substantiate the claimed benefit of the current method, rather than a suggestion for an additional application or future research direction.

4 comments
AuthorsOpenReview ↗

R1. Calibration reuse and the validity claim (W1, Q1)

Thank you for identifying the data-reuse problem. The finite-sample guarantee is not established for the original pooled-null implementation. The 154 early-stop development fields were used to select mixture weights, and normal-yield scores from that role were subsequently reused in the pooled null reference library. Freezing the procedure before audit does not resolve that dependence. We will correct the calibration description and qualify the guarantee throughout the abstract, method, proposition/proof discussion, limitations, and conclusion.

A separate conformal-only analysis uses the designated 125-field calibration role, excluded from predictor fitting and mixture selection. It supplies 96/97/97 non-low-yield reference scores at Looks 1–3. Under the original allocation (0.010, 0.015, 0.025), Look 1 cannot fire because the minimum p-value is 1/97=0.01031>0.0101/97 = 0.01031 > 0.010. We therefore evaluated equal Bonferroni allocation, αk=0.05/3≈0.01667\alpha_k=0.05/3\approx0.01667, retrospectively on the existing 322-field audit.

Table R1a. Separate retrospective conformal-only/equal-Bonferroni analysis; full 322-field audit (74 low-yield, 248 normal-yield).

TierTP/FPFNRecallFPRPrecision
Watch25/134933.78%5.24%65.79%
Persistent Action9/56512.16%2.02%64.29%

The original frozen pooled-null audit instead has Action 8/5 (HZZH R3, Table R3a). The manuscript also reports an earlier conformal-only analysis under the original alpha allocation (Watch 23/12, Action 8/4). The equal-Bonferroni results above are a third, distinct retrospective analysis; these three sets of counts should not be merged. PrXb R3 applies the revised equal-Bonferroni scheme to the 299-field common policy cohort, where Persistence yields 6 TP/4 FP. For a prospectively fixed conformal-only scheme, if reference and future normal-field scores are exchangeable at each look conditional on the fitted predictor and mixture weights, the +1 empirical p-values are super-uniform; the union bound gives Pr⁡(∃k:Wi,k=1∣zi=0)≤∑kαk=0.05\Pr(\exists k:W_{i,k}=1\mid z_i=0)\le\sum_k\alpha_k=0.05. This does not require independent looks, and Action is a subset of Watch. Exchangeability remains an assumption, including across heterogeneous country/crop domains; this retrospective audit does not verify it. The resulting proposed protocol is a correction to be evaluated prospectively, not proof that the original frozen procedure was valid.

AuthorsOpenReview ↗

R2. Actual checkpoint and first-alert times (W2, Q2)

The Look-3 checkpoint decision occurs a median 56 days before harvest (IQR 41–72), rather than 62.5 days. The latter measures the time from the latest satellite acquisition, not the decision. The corresponding decision-to-harvest medians are 102 days at Look 1 and 78 days at Look 2.

Table R2a. Reconstructed decision times; medians in days before harvest.

LookLatest image to harvestDecision to harvest, median [IQR]
1107102 [88, 122]
28678 [62, 94]
362.556 [41, 72]

The first true-positive alert is a different quantity. In the separate retrospective conformal-only/equal-Bonferroni analysis of all 322 fields, median first-TP lead time is 62 days for Watch (farm-bootstrap 95% CI [53, 113]) and 49 days for Action ([41, 112]). First true-positive Actions occur at Look 2 for 5 fields and Look 3 for 4 fields. PrXb R3 gives the direct, same-calibration comparison against simpler policies on the 299-field three-look-eligible subset.

We reconstructed Look-3 decision dates for 321 of 322 cached records; the remaining field did not reach the GDD threshold before harvest and is also excluded from the 299-field three-look comparison (PrXb R3). Across 931 valid field-look observations, none used an image acquired after the reconstructed decision date. The available archives lack complete product-release and delivery timestamps, so this verifies image-acquisition timing, not real-time availability of every operational input. We will correct the lead-time claim accordingly.

AuthorsOpenReview ↗

R3. Sequential persistence versus simpler decisions (W2, Q3)

We now compare the revised conformal-only/equal-Bonferroni Persistence rule directly with single-crossing and final-only decisions. All three use the same conformal-only reference library, 291 development fields (50 low-yield, 241 normal-yield), and 299 eligible audit fields (67 low-yield, 232 normal-yield). Comparator thresholds were chosen on development data to maximize true positives subject to season-level FPR ≤5%; each policy's nominal alert budget is at most 0.05. Persistence uses the fixed 0.05/3 per-look allocation, which allows a Look-1 Watch and hence a Look-2 Action; the original-alpha conformal-only version could not trigger at Look 1. Tuning Persistence under the same development criterion produced identical alerts.

Table R3a. Same-calibration, same-cohort comparison. Development FPR uses 241 normal fields; audit Recall uses 67 low-yield and audit FPR uses 232 normal fields. TP lead is the median first true-positive alert-to-harvest interval, not a paired timing difference.

PolicyDev TP/FPDev FPRAudit TP/FPRecallPrecisionAudit FPRTP lead
Persistence (equal Bonferroni)7/31.24%6/48.96%60.00%1.72%89 d
Single-crossing19/124.98%18/1026.87%64.29%4.31%84.5 d
Final-only17/93.73%16/923.88%64.00%3.88%65 d

Persistence produces fewer false alerts but misses more low-yield fields. With 10,000 paired farm-cluster bootstrap resamples, single-crossing minus Persistence increases recall by 17.91 percentage points (95% CI [8.33, 28.99]) and FPR by 2.59 points ([0.86, 4.82]). Final-only minus Persistence increases recall by 14.93 points ([4.08, 27.03]) and FPR by 2.16 points ([0.00, 4.39]). Single-crossing minus final-only gives recall +2.99 points ([−2.70, 9.09]) and FPR +0.43 points ([−1.61, 3.05]). All three paired precision-difference intervals include zero; the data do not establish a precision advantage for Persistence.

For a paired timing comparison, we restrict attention to fields detected by both policies. Single-crossing alerts a median 20.5 days earlier than Persistence among six shared true positives. Persistence alerts a median 19 days earlier than final-only among five shared true positives, while single-crossing alerts a median 24 days earlier than final-only among 15 shared true positives. These within-field comparisons should not be confused with the separate policy-level lead-time medians in Table R3a. They show a timing benefit for Persistence relative to final-only on shared detections, but no general early-warning advantage over single-crossing.

The common cohort requires, at all three looks, at least three usable images by the decision date, a GDD-threshold crossing before harvest, no future-dated imagery, and complete daily valid temperatures through the checkpoint. From the full 322-field audit, 22 fields (all in Brazil) lacked three usable images at Look 1 (10 at Look 1 only; 12 at Looks 1–2), and one Argentine field did not reach Look 3's GDD threshold. This leaves 299 fields (67 low-yield, 232 normal-yield), excluding 7 low-yield and 16 normal-yield fields. No field was excluded for future imagery or incomplete temperatures after a reached threshold.

The 5% cap is shared on development data, not matched realized audit FPR. These post-audit comparisons reuse an existing audit cohort; their intervals are conditional on the fitted model, calibration library, and chosen thresholds, and do not provide independent validation or establish calibration exchangeability (PrXb R1). The results support Persistence as a more conservative escalation option, with substantially lower recall; they do not support its overall superiority to simpler rules. The separate 322-field equal-Bonferroni audit outcomes and first-action times are reported in PrXb R1–R2, not substituted for this 299-field comparison.

Thank you again for your time and for considering our response.

We just wanted to kindly follow up to ask whether our clarifications have addressed your main concerns. If there are any remaining questions or aspects that would benefit from further explanation, we would be more than happy to elaborate or provide additional evidence.

We fully understand this is a busy reviewing period and sincerely appreciate your time and consideration.

Reviewer_HZZHOpenReview ↗
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Paper summary

The authors have tackled the important problem of early crop monitoring, based on irregular time series observations. They have developed a framework based on growing degree days and weather observations to create a watch/action signal. Their contributions include a sequence based risk recognition framework which is evaluated on the existing YieldSAT dataset. SOTA comparisons include an agriFM model, Random Forest and ExtraTrees.

Critical strengths
  1. The problem tackled is relevant and challenging, given the nature of data available.

  2. The evaluation is done against an existing dataset with code made available.

  3. Insights like those highlighted in Figure 3 are useful and substantiated with experiments.

Critical weaknesses

There are several design choices that need further elaboration (please refer to the section on Questions for details). The key weakness is the evaluation against SOTA approaches (Table 1). The chosen baselines appear to focus on more classical techniques. The only exception is the AgriFM encoder + context approach, but details on the training and architecture used for this setting are missing.

In addition, the size of the dataset is quite small (approximately 2000 fields). Given this small number, no significance values, standard deviation or confidence intervals are reported. This is extremely crucial to gauge the performance of the proposed approach, given the relatively smaller delta seen in Table 1.

Questions for authors
  1. In Section 3, the authors talk about ensuring that false positives are avoided (eq. 3). Why is a false negative not an important concern? Would it not be more important to avoid the scenario when a field with lower yield is not flagged at the right time?

  2. Is GDD a recognized measure? Please provide the intuition behind eq. (4)

  3. Were any sensitivity tests run in the choice of 3 checkpoints?

  4. Description for learning h_{i, k} is unclear, especially the part on “combines aligned Sentinel-2 and weather history with soil, terrain, field, crop and country context”

  5. Why are baselines like MMGated Fusion[1] not included? If not possible, please provide details.

  6. In table 1, please provide details of the AgriFM used.

  7. Have you checked if the model overfits, given the small size of the data. Please report cross validation scores and confidence intervals to showcase the improvements achieved.

  8. From table 2b, it appears as if the country and crop context is the most important factor. Can this model generalize well in this case?

[1] Francisco Mena, Deepak Pathak, Hiba Najjar, Cristhian Sanchez, Patrick Helber, Benjamin Bischke, Peter Habelitz, Miro Miranda, Jayanth Siddamsetty, Marlon Nuske, Marcela Charfuelan, Diego Arenas, Michaela Vollmer, and Andreas Dengel. Adaptive fusion of multi-modal remote sensing data for optimal sub-field crop yield prediction. Remote Sensing of Environment, 318:114547, 2025. doi: 10.1016/j.rse.2024.114547.

8 comments
AuthorsOpenReview ↗

R1. Multimodal baselines and AgriFM (W1, Q5, Q6)

Thank you for pointing out the need for a stronger multimodal comparison. We added an MMGF-style field adaptation of Mena et al. (2025). On the same 316-field development challenge, its RMSE is 1.1507, compared with 1.0361 for PhysCrop-Risk (paired difference −0.1146 t ha⁻¹, farm-cluster 95% CI [−0.1942, −0.0451]). The adaptation uses four modality encoders, sample-adaptive fusion, six GDD-aligned positions, a precipitation stream, and shared field context.

For AgriFM, we use a frozen 3D Video Swin encoder with six 10-band 32×32 frames. Its embedding is reduced to 64 PCA components, combined with 35 context features, and passed to a Ridge head. This is frozen-feature evaluation, not end-to-end fine-tuning.

Table R1a. Final-look comparisons on the 316-field development challenge. The CI is for PhysCrop-Risk minus the comparator's RMSE; a negative interval excludes zero in favour of PhysCrop-Risk. All RMSE values are in t ha⁻¹.

MethodRMSE ↓R² ↑AUROC ↑AUPRC ↑Farm-cluster ΔRMSE 95% CI
Random Forest1.07020.85400.79500.5718[−0.0685, 0.0002]
ExtraTrees1.04590.86060.81100.5717[−0.0219, −0.0003]
Temporal Transformer1.14930.83170.78410.4906[−0.2019, −0.0319]
ConvLSTM + context1.14430.83320.76880.4998[−0.1607, −0.0646]
AgriFM frozen + context1.32680.77570.66220.2913[−0.4359, −0.1480]
MMGF-style field adaptation1.15070.83130.78240.4328[−0.1942, −0.0451]
PhysCrop-Risk1.03610.86320.81120.5735—

The added MMGF-style baseline has higher RMSE and lower AUROC and AUPRC than PhysCrop-Risk on this development split (Table R1a). Its paired farm-cluster RMSE interval excludes zero, as do those for ExtraTrees, Temporal Transformer, ConvLSTM, and AgriFM. The Random Forest interval [−0.0685, 0.0002] includes zero, leaving that comparison inconclusive at the farm-cluster level. Farm-disjoint results are reported separately in HZZH R2 (Tables R2a).

AuthorsOpenReview ↗

R2. Statistical uncertainty and cross-farm evaluation (W2, Q7)

We ran five-fold farm-disjoint cross-validation covering 1,848 out-of-fold predictions from 81 farms. PhysCrop-Risk has OOF RMSE 1.2224, versus 1.2212 for ExtraTrees (paired difference +0.0012, farm-cluster 95% CI [−0.0087, 0.0130]). Thus the small fixed-split RMSE gain over ExtraTrees does not persist in this cross-farm test.

Table R2a. Farm-disjoint CV. Fold RMSE is mean ± SD; CIs compare PhysCrop-Risk against each baseline using paired farm-cluster resampling.

MethodFold RMSE mean ± SD ↓OOF RMSE ↓OOF AUROC ↑OOF AUPRC ↑ΔRMSE 95% CI
Random Forest1.2280 ± 0.26991.25170.80220.5415[−0.0516, −0.0119]
HGB1.2701 ± 0.30801.29990.78310.4777[−0.1326, −0.0265]
ExtraTrees1.2027 ± 0.23631.22120.80750.5383[−0.0087, 0.0130]
Temporal Transformer1.2782 ± 0.23711.29580.77470.4609[−0.1199, −0.0319]
MMGF-style field adaptation1.2653 ± 0.25061.28520.76510.4365[−0.1110, −0.0161]
PhysCrop-Risk1.2026 ± 0.24421.22240.81160.5435—

No farm appears in more than one outer fold. Each fold recomputes GDD thresholds, q20 cutoffs, imputation, and target-normalization statistics using its training partition; inner selection is farm-disjoint. PhysCrop-Risk's mean inner-selection RMSE is 1.1341 versus 1.2026 on outer test folds (gap 0.0685), close to ExtraTrees' gap of 0.0666. Against Random Forest, HGB, Transformer, and MMGF-style adaptation, the paired OOF intervals exclude zero; against ExtraTrees they do not. AgriFM and ConvLSTM were assessed on the fixed split only. The comparative evidence is strongest for the progress-aligned representation and monitoring setup, rather than an advantage from the tree-model mixture itself.

AuthorsOpenReview ↗

R3. False negatives and the two alert tiers (Q1)

False negatives are a major cost of our conservative escalation rule. On the original 322-field frozen audit (74 low-yield; 248 normal-yield), Watch detects 25/74 low-yield fields and produces 13 false alerts. Requiring two consecutive crossings reduces false alerts to 5, but detects only 8/74 low-yield fields—17 more misses than Watch.

Table R3a. Original frozen pooled-null audit; alpha spending (0.010, 0.015, 0.025).

TierTPFPFNRecallFPRPrecision
Watch25134933.78%5.24%65.79%
Persistent Action856610.81%2.02%61.54%

Watch provides a screening signal; Action is a more selective option when unnecessary field visits are costly. The lower FPR comes at substantial loss of recall and does not improve precision here. The original calibration's formal limitation and the separate retrospective conformal-only results (Action 9/5, not 8/5) are explained in PrXb R1. PrXb R3 now compares the revised rule with single-crossing and final-only on the same eligible fields. We will report missed detections alongside false alerts rather than presenting persistence as an unconditional gain.

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

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