How Much of the Movable-Antenna Gain Is the Study Design? A Harmonized Re-analysis

Movable antennas are radio antennas that a small motor or fluid channel can slide a few centimeters within a fixed region. The published gains are large. One study reports a 63% higher worst-user rate than a conventional static array, and another reports that four movable antennas match twenty fixed ones. Yet almost every paper in this area builds its own simulator. Each chooses its own number of propagation paths, its own model of how much the base station knows about the channel, its own region size, and above all its own fixed-antenna reference to beat. Microbiome research went through the same problem. Independent studies of one disease disagreed, and the disagreement turned out to come mostly from lab and pipeline choices rather than biology. That field partly recovered comparability by re-processing many cohorts through one shared pipeline and reporting results over many repeated splits.

We propose to apply that remedy to movable antennas. We will build one shared simulator in which every design choice is an explicit, recorded setting. Inside it we will re-run the representative published algorithms and then vary the settings in a full factorial grid, so that the spread in "movable-over-fixed gain" can be split into what comes from the algorithm and what comes from the study setup. The claim is falsifiable. We expect that most of the variation in reported gains is explained by three setup choices: the fixed reference, the richness of the scattering, and whether channel knowledge is perfect or estimated. We also expect a large share of the headline gain to disappear against a fair fixed reference, meaning a denser static grid with the same number of radio chains and antenna selection. If the gains survive these controls, the field gains a defensible number. If they do not, it learns where movable antennas actually help.

Where the idea comes from and what is new

The metagenomics literature supplies the method. It does not supply data. Avalos et al. showed that the sampling protocol alone, sputum versus bronchial wash, shifts a headline diversity metric independently of patient state. We take from this the idea that the measurement choice can manufacture the effect. Li et al. re-processed five disease cohorts through a single pipeline and recovered consistent viral–bacterial networks that study-specific pipelines had hidden. We copy that design, uniform re-processing of heterogeneous studies. A Framework for Effective Application of Machine Learning to Microbiome-Based Classification Problems reported model performance as distributions over 100 repeated splits and found that simple logistic regression came within 0.015 AUROC of Random Forest. We adopt both lessons: report distributions over random draws rather than single averages, and give simple baselines a serious chance. LLMs Can Learn the Language of the Microbiome found that a pretrained model beats Random Forest only beyond roughly 10,000 labeled samples. That gives us a useful framing: a method's advantage is best reported as a regime boundary, not as a single number.

On the wireless side, CeBed is the closest existing work. It is an open benchmark for learned channel estimation, and it found that in-distribution rankings reverse out of distribution, with transformer estimators falling below plain least squares at unseen high signal-to-noise ratios. CeBed covers only fixed arrays on standard grids and does not address antenna position at all. The movable-antenna papers we re-analyze each contribute an algorithm and a reported gain under their own setup. Pi et al. use particle-swarm search over positions, with an inner loop that alternates beamformer updates, on 16 antennas in a 3λ×3λ region serving 12 users. Zheng et al. use diffusion-based position planning and count antenna equivalences. A Tutorial on Movable Antennas for Wireless Networks describes the field-response channel model and reports up to 40 dB power variation and more than 10 dB gain over a randomly placed static antenna. Ye et al. place antennas using slowly varying channel statistics.

We do not propose a new positioning algorithm, and we do not propose a CeBed clone. What is new is the explicit accounting of study-design choices as experimental factors, together with a fairness protocol for the fixed reference. The Tutorial's "random fixed antenna" reference already shows why this matters: the gain is measured against a deliberately unfavorable static placement.

Core claim and the quantity we measure

For a study configuration $s$ (paths, angular spread, channel-knowledge model, region size, user count, fixed reference, metric) and an algorithm $a$, define the reported gain

$$G(a,s) = \frac{R_{\text{movable}}(a,s)}{R_{\text{fixed}}(s)},$$

where $R$ is the chosen rate metric averaged over channel draws. We fit a factorial decomposition of $\log G$ over all settings and algorithms. We then attribute its variance to each factor and each pairwise interaction using Shapley-style shares, which divide explained variance fairly among correlated factors. The central hypothesis is that the algorithm's share is small compared with the combined share of the fixed reference, the scattering richness, and the channel-knowledge model. A second hypothesis is that $G$ drops toward 1 once two things hold at the same time: channel knowledge is estimated from a realistic pilot budget, and the fixed reference may select its active elements from a dense static grid.

Research Program

We will write one open simulator for the field-response channel described in the Tutorial. It will be built on NVIDIA Sionna so that it shares tooling with existing work such as PyJama. Every paper-specific choice becomes a named configuration field. The first milestone is reproduction. We encode the published configurations of Pi et al. and Zheng et al. and require the simulator to recover their headline numbers within Monte-Carlo error before any other experiment runs. This mirrors checking that a re-processing pipeline reproduces a cohort's original result before pooling it.

The second step is the factorial study. It crosses the following settings: path count (sparse versus rich scattering) and angular spread; region size from 1λ to 5λ; users and antennas on the Pi et al. scale and on smaller scales; channel knowledge (perfect, estimated from a fixed pilot budget, and statistical only as in Ye et al.); and the fixed reference. The fixed reference takes four forms: a half-wavelength array, random static positions, the best static arrangement chosen once for the site's channel statistics, and selection of M active elements from a dense static grid covering the same aperture. Algorithms include particle-swarm search with alternating beamformer updates, statistical-knowledge placement, a reimplemented diffusion planner, and a random-position movable control.

The third step is cross-study transfer, the analog of training on one cohort and testing on another. Positions and planners are tuned under one paper's assumptions and evaluated under another's. This measures how much of an optimized placement's value is tied to the study that produced it. Each result is reported as a distribution over at least 100 independent channel-and-user draws, following the repeated-split practice above. For energy we include the "flexible-position power" model from Zheng et al. and report the repositioning rate at which energy efficiency breaks even, in the same spirit as the Waypoint break-even sample size.

Baselines

The do-nothing reference is a conventional fixed half-wavelength array with the same number of antennas and radio chains, the same MMSE receiver, and the same users and channel draws. Every gain is reported against it first so that it can be compared with the literature.

The strongest simple competitor is dense-grid antenna selection. The static array has more elements than radio chains over the same 3λ×3λ aperture, and the M best elements are switched in per channel. This is the "switching" category that Zheng et al. list among flexible-position designs. It is the fairest static reference because it can exploit the same spatial variation without moving parts. It runs on identical channel knowledge, and its selection search gets the same number of rate evaluations as the particle-swarm budget. We also include a static placement optimized once for the channel statistics. That reference answers whether continuous motion is needed at all, as opposed to good one-time placement.

The strongest existing movable method is the Pi et al. two-loop optimizer. They report a max-min user rate of 2.36 bps/Hz against 1.44 bps/Hz for fixed arrays, a 63% improvement, with M=16, K=12, a 3λ×3λ region, and λ=0.1 m. For the diffusion planner of Zheng et al., the file gives no rate figure to match, only antenna-count equivalences and a qualitative win over reinforcement learning. Our reimplementation is therefore checked against the "4 antennas, 30 positions ≈ 20 fixed" equivalence.

A random-position movable array isolates how much of the gain comes from optimizing positions rather than from the larger aperture. Swapping perfect for estimated channel knowledge in every method isolates the contribution of the perfect-knowledge assumption.

A movable method "beats" the fair static reference if its median max-min rate exceeds dense-grid selection, and the 95% interval of the per-draw difference excludes zero, under estimated channel knowledge. Beating the half-wavelength array alone does not count.

Why not just…?

Why not just trust each paper's own sensitivity sweeps? Most papers vary one parameter at a time around their own default. That approach cannot reveal interactions, such as a gain that exists only with perfect channel knowledge and sparse paths together. It also cannot compare studies whose defaults differ. The factorial decomposition exists to measure exactly those interactions. If interactions turn out negligible, the one-at-a-time sweeps were adequate, and we will say so.

Why not just extend CeBed? CeBed standardizes channel estimation for fixed grids. It shows that rankings flip under distribution shift, which motivates us, but it has no notion of antenna position, a region, or a fixed reference. Adding those is most of the work proposed here, and the novel contribution is the variance attribution rather than a leaderboard.

Why not just use a larger fixed array or antenna selection instead of moving parts? This is the real threat, and we treat it as a hypothesis rather than a strawman. Zheng et al. argue that extra fixed elements cost radio chains, power, and coupling, and the Tutorial argues that a coarse static lattice misses peaks that exist only at sub-lattice spacing. Those arguments only matter if the peaks survive estimation error. Our selection baseline has fixed radio chains and grid spacing that we sweep. If selection at λ/4 spacing recovers most of the movable gain under estimated channel knowledge, the honest conclusion is that switching suffices in that regime, and we will report the boundary.

Why not just standardize on one scenario, as with factory-locked protocols? A single canonical setup produces comparable numbers that may describe no deployment. The metagenomics experience recorded in the file is that post-hoc re-processing across varied cohorts scaled better than mandating one protocol. We keep the variety and make it explicit.

Decisive checks

The study passes its first gate if the simulator reproduces 2.36 versus 1.44 bps/Hz for the Pi et al. configuration and the four-to-twenty equivalence of Zheng et al. within Monte-Carlo error. If it cannot, the discrepancy is itself a comparability finding and we document which unreported choice explains it. The main claim is confirmed if the algorithm factor explains less variance in $\log G$ than the fixed-reference and channel-knowledge factors combined. It is refuted if the ranking of algorithms and the size of the gain stay stable across configurations.

The practical output is a map of where the movable-array gain over dense-grid selection is significantly positive under estimated channel knowledge, drawn over path count, region size, and repositioning rate. The map is paired with the energy break-even rate. Cross-study transfer is decisive for the placement question: if positions optimized under one paper's assumptions lose most of their value under another's, then published placements are study-specific. In that case future papers should report gains under the shared protocol.