Training Channel Predictors on CSI Logs That Drop the Deep Fades

Base stations with many antennas aim their signals using channel state information (CSI), the measured description of how the radio channel between antenna and user currently looks. When users move fast, that description is stale by the time it is used. The usual fix is to learn a predictor that extrapolates the channel forward in time, trained on archives of past CSI reports. Those archives are not a random sample of channel conditions. A report is lost or never scheduled exactly when the channel is bad: the user's feedback fails to decode, link adaptation stops triggering reports, or a handover cuts the trace. A predictor trained on such a log sees a world where deep fades are rarer and shorter than they really are. It is then deployed in the conditions it rarely saw, which are the conditions where accurate prediction matters most.

Clinical epidemiology has a name for this problem. It is selection bias in retrospective data, and in particular data that are missing not at random (MNAR): whether a value is recorded depends on the unrecorded value itself. Epidemiology also has a hard lesson about it. Matching and imputation cannot repair MNAR data when the recording mechanism is unknown. Wireless has one advantage that medicine lacks: the recording mechanism is an engineered protocol, so it is largely known and partly logged. This note proposes to exploit that fact. We would quantify how much opportunistic CSI logging biases learned channel predictors, and correct the bias with a likelihood that models the dropped reports explicitly. A selection-aware procedure would also choose which past observations the predictor uses as inputs.

Core Claim

Channel predictors trained on CSI archives with channel-dependent report loss will underestimate fade depth and duration. Their errors will be concentrated in the low-gain tail, and the problem should be worst in non-line-of-sight segments. Because the loss rule (an SNR threshold, a decoding-failure curve, an event trigger) is specified by the protocol, the dropped reports can enter training as censored observations: we do not know their value, but we know it lay in the region that causes a drop. This turns an unrecoverable MNAR problem into a tractable one. A second claim concerns input selection. Stepwise selection of history lags and delay taps, run on a biased log, picks inputs that are informative mainly in good-channel conditions. Scoring candidate inputs with a selection-corrected criterion should give smaller and more stable input sets that hold up in fades.

Relation to Prior Work

Several papers motivate the gap. Riepe et al. showed in a two-center surgical registry that uncomplicated patients systematically skip follow-up, so outcome data drop out non-randomly and distort the curves learned from them (90-day mortality prediction in elective visceral surgery). Meng et al. showed that diagnostic tests are ordered preferentially for sicker patients, which links record completeness to outcome (Risk factors for steroid-refractory ICI colitis). Our setting has the same structure with the sign of the bias reversed: the bad cases are the ones that vanish.

Other papers constrain the design. Zhou et al. note that propensity score matching balances only observed covariates (Laparoscopic versus open pancreaticoduodenectomy). Zhao et al. note that imputation cannot overcome structurally biased recording (Risk factors and nomogram for gastric cancer). Together these rule out a generic "impute then train" design. Any correction must use knowledge of the drop mechanism, which is what we propose.

Three papers supply the predictors we would correct. Turan et al. fit an offline Gaussian mixture over channel trajectories with Toeplitz-structured covariances. At run time they combine the component-wise linear predictors according to how well each component explains the noisy observations (Wireless Channel Prediction via Gaussian Mixture Models). Its expectation-maximization fitting is the natural place to add censored observations, and that model is our primary testbed. KPIN replaces the Kalman gain with a learned recurrent weighting and trains without labels through a likelihood loss (Hybrid Data-Driven SSM for mmWave Channel Prediction). Its likelihood can likewise take a censoring term. CSI-4CAST predicts in the delay domain and stress-tests models with burst and packet-drop noise across 3,060 scenarios (CSI-4CAST).

CSI-4CAST is the closest existing work, and the difference is precise. It injects drops into test inputs independently of channel quality. We study drops in the training archive that depend on channel quality. Its finding that packet-drop noise is among the most damaging perturbations motivates us, but it does not ask what a predictor learns from a log shaped by those drops.

For input selection, the neck-pain benchmark compared eight selection algorithms on a 3,001-patient cohort (Automatic Variable Selection Algorithms in Prognostic Factor Research in Neck Pain). It found that adjusted-p-value stepwise selection over-pruned, with disability sensitivity dropping by 0.23, that LASSO kept up to 28 predictors, and that the algorithms disagreed widely on which variables mattered. We borrow its evaluation stance, which is to report sparsity, stability under resampling, and stratified performance rather than average fit alone.

The retrospective interference-alignment line of work (Completely Stale Transmitter CSI is Still Very Useful) uses "retrospective" in a different sense: it transmits using knowledge of past channels. It assumes lossless delayed feedback and is outside our scope. Our results would, however, bear on whether its feedback assumption is realistic.

Research Program

The first component is a bias audit. We generate complete channel trajectories with QuaDRiGa under 3GPP Urban Macrocell, Urban Microcell and Highway settings, as used by KPIN and by Li et al. (CSI-ALM). We also use the measured industrial-hall trajectories from the Gaussian mixture paper, which include line-of-sight to non-line-of-sight transitions. We then pass each trajectory through three logging mechanisms that mimic real protocols. The first is a hard threshold, in which a report is kept only if estimated SNR exceeds $\tau$. The second is a soft decoding-failure curve, in which the keep probability is logistic in SNR. The third is event-triggered reporting, which logs more densely when the channel changes. As controls, we also apply a random drop at a matched rate (MCAR, missing completely at random) and keep the full log. Every predictor is trained on each log and evaluated on the complete trajectories, so the bias is directly measurable.

The second component is censored training. Let $y_t$ be the logged observation at time $t$, $r_t \in \{0,1\}$ the indicator that it was logged, and $\pi(h_t) = P(r_t = 1 \mid h_t)$ the protocol-defined keep probability given the true channel $h_t$. The corrected objective for model parameters $\theta$ is the full-data likelihood

$$ \log L(\theta) = \sum_{t: r_t=1} \log \big[ p_\theta(y_t \mid y_{<t}) \, \pi(y_t) \big] + \sum_{t: r_t=0} \log \int p_\theta(h \mid y_{<t}) \,\big(1-\pi(h)\big)\, dh . $$

Here $p_\theta$ is the predictor's conditional density of the next channel given the logged past $y_{<t}$. The second sum states that a missing report carries information: the channel probably sat in the drop region. For the Gaussian mixture we implement this with stochastic EM. Dropped segments are imputed by sampling from each component's conditional Gaussian restricted to the drop region, using rejection or importance sampling on the channel-gain constraint. The covariance M-step keeps its Toeplitz structure. For KPIN the second term is estimated by Monte Carlo inside the existing unsupervised loss. When $\pi$ is soft, inverse-probability weighting of logged samples (clipped weights) serves as a cheaper variant. Under a hard threshold weighting is undefined, so only the censored form applies.

The third component is selection-aware input selection. The candidate inputs are history lags crossed with delay-domain taps. We run bidirectional stepwise selection, in which each step may add one candidate and drop any previously kept one. Group moves add or remove a whole tap across lags, which addresses the collinearity concern raised for neighbouring taps. Each candidate set is scored by a censoring-corrected held-out log-likelihood with a BIC-style penalty, rather than by fit on the logged samples alone. We measure stability by how often each input is selected across bootstrap resamples of the training trajectories.

Baselines

The naive reference point is the same predictor trained on the biased log with dropped reports simply absent from training windows, which is current practice. Two further references bracket the problem. An oracle trains on complete trajectories, which bounds what any correction can recover. An MCAR-augmented model trains on the biased log plus random-drop augmentation in the style of CSI-4CAST's robustness tests, the most obvious practical fix. All variants share the same trajectories, architecture, hyperparameter search budget (the same number of configurations, selected on a censoring-corrected validation set), and training compute. We report the extra cost of sampling in the E-step separately.

The strongest existing predictor on measured data is the Gaussian mixture predictor of Turan et al. It beat LMMSE Jakes and neural baselines on the industrial-hall measurements, but no reported raw MSE value was found on Lacuna for it. We therefore re-run it ourselves. KPIN is the strongest on QuaDRiGa mmWave data, with a reported 2 dB NMSE improvement over the autoregressive Kalman filter and 5–7 dB over pure GRUs and Transformers (KPIN). That number concerns clean training data. Our comparison is KPIN trained on biased logs, with and without the censoring term.

Beating a baseline means recovering at least half of the gap between the naive model and the oracle in NMSE on the lowest channel-gain decile, without losing more than 0.2 dB on the median decile. It must also increase zero-forcing sum rate computed with predicted channels.

For input selection, the baselines are the full input set, LASSO and group LASSO, uncorrected stepwise selection with BIC, and multivariate adaptive regression splines. The splines were the best-balanced method in the neck-pain benchmark. The key ablation pairs selection-corrected scoring with an uncorrected predictor, and the reverse, to show which ingredient drives each gain.

Why not just…?

Why not just train on simulated data, where nothing is missing? For QuaDRiGa scenarios this works, and the oracle row reports exactly what it buys. The reason to learn from operational logs is that simulators break in real geometries. The industrial-hall measurements are where LMMSE Jakes failed because its scattering model did not hold (GMM predictor). Any site-specific predictor must therefore learn from logs. We test this directly with a sim-to-measured transfer row: a model trained on simulated data and evaluated on the hall data. If it matches the censored, log-trained model, the correction has little practical value and we will say so.

Why not just add random packet-drop augmentation? This is the most serious threat. Random augmentation teaches the model to tolerate gaps, but it does not restore the missing fade statistics, because the logged values still under-sample low gain. The experiment that settles it is the MCAR-augmented baseline on the lowest-gain decile. If augmentation closes most of the gap there, the paper's main claim fails.

Why not just use a Kalman-style predictor that skips updates during drops? Skipping updates handles missing inputs at run time, but the model parameters were still fit to a biased archive. KPIN with dropped steps skipped is exactly our uncorrected KPIN baseline, so the comparison isolates the training-time bias.

Why not just select inputs with LASSO? In the neck-pain benchmark LASSO produced the densest models. Among correlated neighbouring taps it tends to keep one arbitrarily. More fundamentally, any selection criterion computed on the biased log inherits the bias. The bootstrap stability results and the corrected-versus-uncorrected scoring ablation show whether correction, not the search method, is what matters.

Proposed Experiments

The decisive first check is whether the bias exists at a size worth correcting. We will plot NMSE against channel-gain decile for naive models trained under each logging mechanism, compared with MCAR drops at a matched rate. If channel-dependent and random drops give the same tail error, the project stops there with a useful negative result. We expect the gap to grow with drop threshold $\tau$ and user speed, and to be largest in non-line-of-sight segments, where CSI-4CAST already reports the hardest prediction.

The second check measures how much of the naive-to-oracle gap the censored likelihood recovers for the Gaussian mixture predictor and KPIN, across QuaDRiGa settings at 3–100 km/h and on the industrial-hall data. Results are stratified by line-of-sight state and include downstream sum rate.

The third check covers mechanism misspecification: we train with an assumed threshold $\tau$ that is wrong by ±3 dB, because real deployments will not know the drop curve exactly.

The fourth check compares input-set size, bootstrap selection frequency and tail NMSE across the selection methods.

A final robustness pass evaluates on the CSI-RRG benchmark's out-of-distribution velocity scenarios (up to 45 m/s) to see whether correction transfers under distribution shift, where CSI-4CAST reports top performance in 88.9% of TDD and 43.8% of FDD scenarios.