A continuous glucose monitor (CGM) is a small enzyme-coated electrode under the skin that turns interstitial glucose into an electrical current every few minutes. Software then forecasts where glucose is heading and warns the wearer before a dangerous low. Forecasting models are judged by average error on public datasets. The people in those datasets are not the people who most need the warnings. Spanish-preferring patients in safety-net clinics adopt CGMs far less often than English-preferring patients, even after adjusting for insurance and socioeconomic status (Walker et al.). Language barriers therefore shape who ends up in CGM training data, much as European overrepresentation shapes genetic association studies. When the warning does fire, it still has to reach the patient in words they can act on.
This proposal treats a CGM alert as a single chain with three links. The electrode reports a signal that may be corrupted by drift or fouling. A forecaster turns that signal into an alarm decision whose reliability may differ by population. A message carries the decision to the patient in their language. The proposal makes two contributions. The first is to evaluate and calibrate the alarm decision separately for each population, on the event that matters (an upcoming low), rather than on pooled average error. The second is to restrict the alarm's outputs to a small fixed set of messages that humans can translate once and verify. That set is chosen so that no machine translation or speech synthesis sits on the safety-critical path.
Core Claim
Pooled forecasting accuracy hides population-specific alarm failures. A precedent comes from genetic diagnosis of diabetes: a single screening rule calibrated on White patients delayed monogenic diabetes diagnosis by about ten years in non-White patients. Group-specific thresholds doubled detection, from 8.8% to 16% (Jones et al.). We claim CGM hypoglycemia alarms behave the same way.
Two components should close most of this gap at a known, small data cost. The first is group-conditional calibration, meaning a separately set alarm threshold per population with a finite-sample coverage guarantee. The second is a representation trained to separate population-invariant glucose dynamics from population- and device-specific nuisance, such as sensor drift. Once the alarm's output space is a closed set of actionable messages, the language link can be made nearly lossless by human translation. Machine translation is then confined to non-urgent explanatory text, where its errors are survivable.
What is new is not any single component. It is the claim that alarm reliability must be certified per population and per language at the level of the event. It is also the measurement of how many patients from a new population are needed to certify it.
Research Program
The forecasting core. This builds on GlucoBench, which curates five public CGM datasets (Broll, Colas, Dubosson, Hall, Weinstock). They span Type 1 diabetes, Type 2 diabetes and healthy subjects. GlucoBench scores one-hour-ahead forecasts by RMSE, MAE, likelihood and calibration error. It found that simple models win on small cohorts and that a Transformer generalizes best to unseen Weinstock patients.
We keep its preprocessing and models but change the unit of evaluation. We convert every forecast into a binary alarm: "glucose predicted below 70 mg/dL within 30 minutes." We then score sensitivity at a fixed false-alarm rate, separately for each cohort.
The datasets carry no ancestry or language labels, so in the first phase the five cohorts serve as stand-in populations. They really do differ in disease type, sensor hardware and recruitment. This is a proxy, and the ancestry claim proper is tested later.
The representation, borrowed from Mendelian randomization. Mendelian randomization is a method that uses genetic variants as natural experiments to estimate causal effects. Recent work in that field trains an autoencoder whose code splits into an ancestry-invariant part and an ancestry-specific part (Addressing Instrument-Outcome Confounding in Mendelian Randomization through Representation Learning). On the All of Us biobank, that split cut bias from up to 0.3 to near zero, where standard estimators failed. We reuse the same two penalties on CGM windows:
$$\mathcal{L} = \mathcal{L}_{\text{forecast}} + \lambda_1 \sum_{g \neq g'} \mathrm{MMD}\big(h_W^{(g)}, h_W^{(g')}\big) + \lambda_2\, \mathrm{HSIC}\big(h_W, h_V\big).$$
Here $h_W$ is the invariant part of the encoding and $h_V$ the population-specific part. MMD measures how different the distributions of $h_W$ are across groups $g, g'$. HSIC measures statistical dependence between $h_W$ and $h_V$. The $\lambda$ terms weight the two penalties.
The forecast head reads both parts. The motivation is that $h_V$ should absorb what does not transfer. The same paper also constrains us: the split is only identifiable when environments differ in their nuisance. Our cohorts differ in sensor generation and population, so the condition is plausible. We test it directly rather than assume it.
Where electrochemistry enters. Electrochemistry supplies the nuisance model. CGM error is not only physiological. The enzyme layer loses sensitivity, the electrode fouls, and readings drift after insertion. Sensor studies routinely note that real biological matrices degrade signals that look clean in buffer (FeMn@C sensor).
We inject controlled, physically shaped artifacts into held-out traces. These are first-order sensitivity decay, baseline offset drift, and transient compression lows, at cohort-specific rates. They give a ground-truth test of whether $h_V$ captures sensor corruption and whether the alarm survives it.
We deliberately do not try to recover circuit-level electrode parameters from scalar CGM readings. Even with full impedance spectra, classifying equivalent-circuit topology reaches only a weighted F1 of 0.50 (ML Benchmarks for ECM Classification). That is a negative result ruling out a physically detailed inverse model here.
Group-conditional calibration. For each population $g$, we set the alarm threshold $q_g$ as the $\lceil (1-\alpha)(n_g+1)\rceil / n_g$ empirical quantile of a nonconformity score on $n_g$ calibration windows from that group. Split conformal prediction then guarantees
$$\Pr\big(\text{true event is flagged} \mid \text{group } g\big) \ge 1-\alpha,$$
as long as windows within the group are exchangeable. The bound comes from standard split-conformal rank arguments.
The guarantee says nothing about a population with no calibration data. That is exactly the ancestry problem, and it turns it into a measurable quantity: how many patients from a new population we need before its guarantee holds at a usable false-alarm rate.
Making the language link translatable by design. The alarm emits one of roughly a dozen fixed messages, each pairing a direction, a time horizon, an urgency level and an action (for example, "glucose likely low within 30 minutes; take 15 g of fast sugar now"). Each message is translated by bilingual clinicians into Spanish, the language in Walker et al.'s gap, and into Yoruba, the low-resource case with existing medical translation evidence. Translations are verified by independent back-translation.
For audio, we use human recordings, because synthesized Yoruba speech scored only 40% accuracy in a pharmacist-rated drug-information system (RAG Meets Local Languages). For low-literacy users, we render each message as a pictograph sequence through a concept-level intermediate representation, following PictoDr. That work warns that abstract notions like risk lack good icons. We therefore test whether a categorical urgency level survives pictographic rendering when a numeric probability does not.
Machine translation is used only for free-text follow-up explanations. Its error rate is measured and reported, not hidden.
Baselines
The naive reference point is what many devices do: alarm when the current reading falls below a fixed threshold, with no forecast. Every method must beat its event sensitivity at matched false-alarm rate in every cohort. Otherwise forecasting adds nothing for that population.
The strongest simple competitor is per-cohort linear regression or ARIMA, the classical time-series model. GlucoBench found these beat deep models on small cohorts. They are run with GlucoBench's splits and given the same hyperparameter search budget as our model.
The strongest deep competitor is the GlucoBench Transformer. It generalized best to unseen patients, with a reported RMSE of 13.22 on Weinstock (GlucoBench). We first reproduce that number under GlucoBench's protocol before any comparison. Gluformer and Latent ODE are also included, the latter because GlucoBench reports it as best on mixed populations.
No reported result on Lacuna was found for event-level hypoglycemia sensitivity per cohort on GlucoBench. Our reproduction of these baselines therefore defines the comparison point. Beating them means one of two things. Either worst-cohort alarm sensitivity at a fixed false-alarm rate rises by a margin larger than the bootstrap confidence interval over patients, or the per-group coverage guarantee is met in every cohort where the baseline misses it. Both must hold without pooled RMSE worsening beyond its own confidence interval.
Two ablations isolate the key ingredients. The first applies group-conditional calibration to the reproduced Transformer with no invariance penalties. If this alone matches the full method, the representation is unnecessary and we will say so. The second keeps the invariance penalties but uses one pooled threshold, which isolates the value of calibration.
On the language side, the baselines are zero-shot NLLB and NLLB fine-tuned on the available Yoruba medical corpus. In the veterinary domain, zero-shot NLLB 3.3B scored BLEU 2.9 and fine-tuned scored 45.89 (VetYorùbá). Both are compared against human-translated templates. We use clinician-rated actionability, not BLEU, because a fluent but wrong dosing instruction is the failure that matters.
Why not just…?
Why not just pool all data and train the best Transformer? GlucoBench shows the Transformer generalizes well to unseen patients on average. Average error is exactly the quantity that hid a decade of misdiagnosis in Jones et al. Pooled training optimizes the majority cohort. Our first experiment reports per-cohort alarm sensitivity for the pooled Transformer. If its worst-cohort sensitivity is within noise of the best-cohort sensitivity, the population problem is absent in these data. The proposal would then shrink to the calibration and language components.
Why not just tune an alarm threshold separately for each group? That is essentially what group-conditional conformal calibration does. We regard it as the main threat to the representation-learning component, not as a weak alternative. Conformal calibration adds a finite-sample guarantee and a clean answer to how much data a new group needs. The first ablation decides whether the invariant representation earns its place: it should matter mainly under injected sensor drift, where a threshold alone cannot separate electrode decay from physiology. If it does not help there, we drop it.
Why not just fit a model to each patient as data arrive? Per-patient ARIMA sidesteps population bias once enough personal data exist, and GlucoBench's small-data results make this a real competitor. It cannot help in the first days after insertion. That is also when electrochemical warm-up drift is worst and when new users decide whether to keep the device. We measure the number of days per-patient adaptation needs to match the calibrated population model. If the answer is one or two days, the population-level contribution matters only for onboarding, and we will frame it that way.
Why not just send alerts through a good machine translator? Domain-specific medical text breaks zero-shot translation: BLEU 2.9 for NLLB in the Yoruba veterinary setting. Yoruba speech synthesis was rated 40% accurate. Literal translation of chatbot interfaces also failed to keep non-primary-language users engaged (Chugh et al.). A closed message set makes human translation cheap and verifiable, so machine translation is unnecessary for urgent alerts. The design concedes the skeptic's real point, that templates are simpler, and builds the model's output space around it.
Proposed Experiments
Experiment 1: does the problem exist? We reproduce GlucoBench's Transformer, Gluformer, Latent ODE and linear baselines, confirm the reported Weinstock RMSE of 13.22, and add event-level alarm metrics per cohort. We use leave-one-cohort-out training, so each cohort is in turn an unseen population. The decisive check is whether the gap between best- and worst-cohort hypoglycemia sensitivity at a 10% false-alarm rate exceeds the bootstrap interval. If it does not, the population-calibration component is unmotivated on these data.
Experiment 2: how much data does a new population need? In each held-out cohort, we vary the number of calibration patients from one upward. We record the smallest number at which group-conditional calibration meets the coverage target with an acceptable false-alarm rate. This calibration-patients curve is the transferable deliverable: it tells a clinic how many local patients to enroll before trusting the alarm for its population.
Experiment 3: does the representation separate sensor error from physiology? We inject drift, sensitivity decay and compression artifacts at cohort-specific rates. We test whether the population-specific part of the encoding predicts the injected artifact parameters while the invariant part does not. We then test whether alarm sensitivity under artifacts degrades less than for the calibration-only ablation. We repeat this with artifacts made identical across cohorts. The Mendelian randomization work predicts the separation should then fail, a falsification check on whether the mechanism is what we think.
Experiment 4: does the message survive language and literacy? Bilingual clinicians rate each of the roughly twelve alert messages for correct, actionable meaning in Spanish and Yoruba, in text, audio and pictograph form. Human templates are compared with zero-shot and fine-tuned NLLB, and human audio with synthesized speech. End-to-end reliability is reported as alarm sensitivity times the rated probability that the message is understood correctly. That makes visible whether the weakest link is the electrode, the model or the words.
What would require new data. The genuine ancestry and language-preference test needs a CGM cohort labeled by ancestry and language. The research file contains none. This is the step we would pursue with a safety-net clinic network like the one Walker et al. studied. The proxy results above determine whether that collection is worth its cost, and the calibration-patients curve from Experiment 2 sets its minimum size.
References
- Not all healthcare inequities in diabetes are equal: a comparison of two medically underserved cohorts
- Precision diagnosis for monogenic diabetes requires ethnicity specific criteria for genetic testing
- GlucoBench: Curated List of Continuous Glucose Monitoring Datasets with Prediction Benchmarks
- Addressing Instrument-Outcome Confounding in Mendelian Randomization through Representation Learning
- A Carbon Nanofiber Electrochemical Sensor Made of FeMn@C for the Rapid Detection of Tert-Butyl Hydroquinone in Edible Oil
- Machine Learning Benchmarks for the Classification of Equivalent Circuit Models from Electrochemical Impedance Spectra
- Retrieval-Augmented Generation Meets Local Languages for Improved Drug Information Access and Comprehension.
- A Concept Based Approach for Translation of Medical Dialogues into Pictographs
- Beyond Generalization :Evaluating Multilingual LLMs for Yorùbá Animal Health Translation
- A Digital Health Intervention to Improve the Clinical Care of Inflammatory Bowel Disease Patients