Moving a TyG Risk Cutoff to a New Hospital Without Its Outcomes

The triglyceride-glucose (TyG) index is a cheap blood-test score for insulin resistance, the condition in which the body stops responding properly to insulin. It is computed from two routine fasting lab values, triglycerides and glucose. It predicts heart attacks, strokes and death across many cohorts. Yet the "high-risk" cutoff moves from study to study: 8.43 in young hypertensive adults in Beijing, 8.95 to 9.0 for mortality in US diabetics, and about 9.0 after coronary stenting. Some of that spread is real biology and differences in which patients each hospital sees. Some may be measurement: how each lab calibrates its machines, reagent lots, and whether patients really fasted. Pooling and transfer methods built to remove such site-specific measurement artifacts (called batch effects) exist, but they were built for brain scans and gene panels with hundreds of features. Nobody has asked what they do to a two-ingredient clinical score.

Here is the idea in two sentences. TyG is the logarithm of a product, so any multiplicative calibration bias at a site in either lab test becomes a single constant shift of that site's TyG values. The practical problem is therefore not "harmonize a feature table" but "estimate one number per hospital, and decide how much of it is lab artifact versus true difference in patients." That number can be estimated before any outcomes are collected. We propose such an estimator, together with an honest sensitivity analysis. We test whether it makes a TyG cutoff or risk model transfer to a new site better than the simple alternatives do.

Core Claim

Write the observed index at site $s$ for patient $j$ as

$$\widetilde{\text{TyG}}_{sj} = \text{TyG}_{sj} + \underbrace{\ln a_s + \ln b_s}_{\theta_s} + \eta_{sj},$$

where $a_s$ and $b_s$ are the site's multiplicative calibration factors for triglycerides and glucose, $\theta_s$ is the resulting additive site offset, and $\eta_{sj}$ is within-site measurement noise. This follows directly from the definition $\text{TyG}=\ln(\text{TG}\times\text{FBG}/2)$.

Two consequences follow. First, a cutoff estimated at one site is really a cutoff on $\text{TyG}+\theta_s$. A U-shaped mortality curve like the one in Zhao et al. is shifted horizontally, not reshaped, by assay bias. Second, $\theta_s$ cannot be separated from a true shift in the site's patient population using observational data alone. Some assumption must break the tie.

Our claim is that a covariate-conditional anchor assumption beats both doing nothing and the high-dimensional harmonizers for transporting TyG cutoffs and risk models to unseen sites. The assumption says that among people with similar age, sex, body size and diabetes status, the true TyG distribution does not depend on site. We also claim that the gain, and its limits, can be measured precisely.

Research Program

The estimator borrows its structure from DeepResBat, which first predicts biological effects from covariates, then harmonizes only the leftover residuals, and finally adds the biology back. That design kept false discoveries at the nominal 5% under covariate permutation when site and covariates were correlated. We keep the residual logic but drop the neural network. With one effective feature there is nothing for a conditional autoencoder to learn.

The procedure has three steps. We fit a pooled model of log triglycerides and log glucose on clinical covariates (age, sex, BMI, waist, diabetes and lipid-lowering treatment, and fasting duration where recorded). Each site's offset $\theta_s$ is then the robust mean residual in an anchor subgroup: people with no diagnosed diabetes and no lipid medication, where we expect less disease-driven heterogeneity. We subtract $\theta_s$ to obtain corrected TyG values.

We report $\theta_s$ with a bootstrap interval. We also report a sensitivity bound: how large an unmeasured true population difference in the anchor group would have to be to explain the estimated offset. Separately estimating $\ln a_s$ and $\ln b_s$ is optional. It matters for indices like the atherogenic index of plasma (log of triglycerides over HDL cholesterol), studied alongside TyG in Shi et al., where the biases enter with different signs.

Why not plain ComBat, the empirical Bayes method that shrinks per-feature site corrections toward a shared prior? It needs many features to pool across, and the TyG panel has two. It is also known to be fragile in exactly the conditions clinical sites present. Kim et al. found ComBat unstable below roughly 162 to 308 subjects and badly degraded once mean age differed by more than 2 to 4 years between sites. A post-PCI hospital and a population survey differ by far more than that. ComBat-MLE shows a closed-form version that works well on phantoms, where biology is fixed by construction. Clinical sites are the opposite case.

We also take a caution from Ye Tao et al.. In their deliberately confounded test, a model trained with all cases at one site and all controls at another reached 100% accuracy purely from scanner differences. Post-hoc ComBat reduced site predictability without restoring biology. Our setting is much simpler, but the same trap applies: any method that removes site differences can also remove real case-mix differences.

Baselines

The naive reference point is uncorrected transfer. We fit the TyG cutoff or Cox model at the source site and apply it unchanged at the target. The published single-site numbers set the scale of what transfer must preserve. Tao et al. report an AUC of 0.810 for their one-year MACE model after stenting. Chen et al. report that adding TyG to recalibrated SCORE2 raised AUC from 0.698 to 0.736. That 0.038 gain is the quantity that can quietly vanish under miscalibration across sites. No reported result was found on Lacuna for cross-site transfer of any TyG model, harmonized or not.

The first statistical competitor is within-site standardization: convert TyG to site-specific percentiles or z-scores and transfer cutoffs in those units. It needs no outcomes, so it is the most direct rival to our method.

The strongest existing harmonizers are ComBat with covariates applied jointly to log triglycerides and log glucose, and Cluster ComBat. Cluster ComBat assigns a new site to an existing cluster of site parameters without refitting. It reported lower downstream error on unseen sites in neuroimaging and targets exactly our unseen-hospital setting. We include Fed-ComBat, which replaces the linear covariate model with a neural network and matched centralized ComBat-GAM on 13,479 brain scans. Its reported 35% RMSE gain over d-ComBat is on synthetic data, not on clinical chemistry. We also include DeepResBat as published.

The oracle upper bound is local recalibration. Here the target site's intercept and slope are refit on its own outcomes.

All methods see the same source and target data and the same covariates. The fitted target risk model is identical across methods; only the TyG input differs. Each method's tuning parameters (for example, how many clusters Cluster ComBat uses, or how wide the network is) are chosen on held-out source data with an equal budget. Two ablations isolate our key ingredients: the offset estimated from the whole target population instead of the anchor subgroup, and the offset estimated without the covariate model.

Beating the baselines means two things at once. On semi-synthetic data, our method must recover the injected offsets better than every outcome-free baseline while not removing real case-mix shifts. On real transfers, it must close a clear fraction of the calibration gap between uncorrected transfer and local recalibration. Discrimination should not suffer.

Why not just…?

Why not just use site-specific percentiles? Percentiles erase every difference between sites, including real ones. A stenting hospital where 40% of patients have an event within a year (Tao et al.) should not have its top tertile treated like the top tertile of a population survey. This is a real threat when sites draw similar patients, because then percentiles are nearly unbiased and simpler than our method. The semi-synthetic design settles it by varying case-mix difference and assay bias independently. We expect percentiles to win only when case-mix difference is near zero, and we will report it if they win more broadly.

Why not just run ComBat or Cluster ComBat on the two lab values? With two features, the empirical Bayes prior has almost nothing to pool across. Kim et al.'s age-imbalance results predict that ComBat will mix site and biology when populations differ. Cluster ComBat's assignment of new sites has never been checked on tabular clinical chemistry. These are empirical claims about our setting, not settled facts, so we run both as full baselines. The UK Biobank negative control described below directly measures how much biology each method wrongly removes.

Why not just recalibrate locally on outcomes? When outcomes are available, local recalibration is the right answer, and we treat it as the ceiling. The case for our method is the common situation where a hospital wants to use a published cutoff before it has years of follow-up. We will also report how many local events recalibration needs before it overtakes the outcome-free correction. If that number is small, our method's practical value shrinks, and we will say so.

Why not just standardize the assays? Lab standardization removes calibration bias at its source. It does not touch fasting noncompliance or historical data already collected. Our semi-synthetic sweep reports the offset size below which correction is irrelevant, which tells labs when the issue matters at all.

Proposed Experiments

Semi-synthetic test. We use NHANES with fasting labs, linked to death records as in Zhao et al.. We split it into pseudo-sites with deliberately different age, BMI and diabetes mixes. We then multiply each pseudo-site's triglycerides and glucose by known factors, which gives a known ground-truth offset $\theta_s$. Every method is scored on four things: error in recovering $\theta_s$; wrongly removing the induced case-mix shift; mortality-curve nadir location; and calibration of a Cox model at held-out pseudo-sites.

Real-data negative control. UK Biobank analyzes its biochemistry on a single central platform, so true assay offsets between its assessment centers should be near zero. Any method that reports large center offsets there is removing biology. Because UK Biobank samples are often non-fasting, fasting time enters as a covariate. Fasting-restricted subsets are analyzed separately. This also tests whether fasting state behaves like a correctable offset; we suspect it does not, since it shifts triglycerides far more than glucose and not by a constant factor.

Decisive real-data check. We transfer a TyG-plus-clinical-covariates model for cardiovascular death between NHANES and UK Biobank in both directions. The metrics are calibration intercept and slope, C-index, and net benefit from decision curve analysis at the published cutoffs. A second check asks whether the spline-estimated risk inflection points converge after correction; they should converge if the 8.43 versus 9.0 disagreement is partly measurement. If the corrected inflection points stay as far apart as the raw ones, the field's cutoff disagreement is biological, and published cutoffs should be reported as population-specific rather than harmonized. That would be a useful negative result.