Formal Preliminaries

3.1 The visuomotor imitation problem

Let the robot's state be $s_t$, its observation $o_t = (I_t, x_t)$ where $I_t$ is one or more camera images and $x_t$ is proprioception, and its action $a_t \in \mathcal{A}$. A demonstration dataset is

$\mathcal{D} = \{ \tau^{(i)} \}_{i=1}^N, \qquad \tau^{(i)} = (o_0, a_0, o_1, a_1, \ldots, o_{T_i}, a_{T_i}).$

Behaviour cloning fits $\pi_\theta(a \mid o)$ by maximum likelihood. The classical result is that the compounding-error penalty of BC is quadratic in horizon: if the learned policy has per-step error $\epsilon$ under the expert's state distribution, its expected cost can degrade as $O(\epsilon T^2)$ relative to the expert, because errors move the policy off the training distribution.

Two architectural families dominate current practice and both address this by predicting sequences rather than steps.

Action chunking (ACT). Zhao, Kumar, Levine & Finn (RSS 2023) [arXiv:2304.13705] predict $a_{t:t+k}$ jointly, reducing the effective horizon by a factor $k$. Their ablation is striking: success rises from 1% at $k=1$ to 44% at $k=100$ on a simulated human-demonstration task. Temporal ensembling averages overlapping chunk predictions with exponential weights $w_i = \exp(-m \cdot i)$, adding a further ~3.3%. Crucially, removing the CVAE latent — the component that absorbs demonstrator stochasticity — costs 33.3% on human data and approximately nothing on scripted data. This is the cleanest isolation in the literature of the specific damage done by human demonstration noise.

Diffusion policy. Chi, Feng, Du, Xu, Cousineau, Burchfiel & Song (RSS 2023) [arXiv:2303.04137] model $p(a_{t:t+T_p} \mid o)$ as a conditional denoising process, reporting +46.9% average improvement across 12 tasks and 4 benchmarks. Their stated motivation for sequence prediction is directly relevant here: it prevents "jittery actions that alternate between the two valid trajectories" when a demonstrator solves a task multiple ways.

Both families converge on the same fix from opposite modelling philosophies. That convergence tells us something about the failure mode they are both patching: single-step regression is brittle precisely when the demonstrator's action is not a deterministic function of the observed state. Hold that thought; §4.8 argues that EMG teleoperation manufactures exactly that condition.

3.2 Demonstration quality, formally

Belkhale, Cui & Sadigh, Data Quality in Imitation Learning (NeurIPS 2023) [arXiv:2306.02437] provide the framework this review uses throughout. They identify two axes:

• Action divergence — $D_f(\pi_A(\cdot \mid s), \pi_E(\cdot \mid s))$, the divergence between learner and expert action distributions at a state, driven in practice by the entropy of the expert's own actions at similar states.
• Transition diversity — the spread of successor states, $\rho(s' \mid s,a) = \mathcal{N}(\mu(s,a), \sigma^2 I)$.

Their Theorem 4.1 bounds the distribution shift:

$D_{\mathrm{KL}}(\rho_{\pi_A}, \rho_{\pi_E}) \;\le\; \frac{1}{H}\sum_t (H-t)\, \mathbb{E}_{s \sim \rho^t_{\pi_A}}\big[ D_{\mathrm{KL}}(\pi_A(\cdot|s), \pi_E(\cdot|s)) \big].$

Two consequences matter for us. The $(H-t)$ weighting means early-episode errors are penalised far more than late ones. And $H$ appears explicitly, so slow, hesitant demonstrations are penalised twice — once through longer horizons and once through whatever inconsistency produced the hesitation.

Their empirical practice is decisive. Diversity arising from system noise (environment stochasticity) helps, because it teaches recovery; diversity arising from policy noise (an inconsistent operator) hurts. In their controlled injection study on the Square task, at 1,000 episodes the gap is modest (82.0% system noise vs 80.7% policy noise), but at 50 episodes it widens to 69.7% vs 48.3%. Operator inconsistency is most corrosive exactly in the low-data regime any EMG study will occupy.

A caution the authors themselves raise: their metrics are incomplete and not monotone. On robomimic Square, the MH-Worse subset has the lowest action variance (0.061) and the worst success (2%), with the residual attributed to horizon length.

3.3 The empirical anchor: robomimic

Mandlekar et al. (CoRL 2021) [arXiv:2108.03298] constructed proficient-human (PH: 1 operator, 200 trajectories) and multi-human (MH: 6 operators, 50 each = 300 trajectories, binned "worse"/"okay"/"better") datasets per task. MH has 50% more data than PH and performs substantially worse — BC-RNN on Transport drops from 72% (PH) to 42% (MH). Offline RL collapses specifically on mixed human data: on Can (MH), BC-RNN reaches 100% while BCQ manages 62.7% and CQL 22.0%, despite both performing acceptably on machine-generated data.

The MH-specific architectural finding is equally important: history-dependent models (BC-RNN, HBC) gain ~25% on Square (MH) versus only ~5% on Square (PH). Architecture partially substitutes for data quality, and the value of the substitution scales with how bad the data is.

We found no paper contradicting the PH > MH ordering. Belkhale et al. independently reproduce it on the same subsets (Square: PH 58%, Better 36%, Okay 12%, Worse 2%).

3.4 Smoothness metrics

Because §4 argues that EMG artifacts manifest as non-smoothness, we need the metrics. Balasubramanian, Melendez-Calderon, Roby-Brami & Burdet (2015), J. NeuroEngineering and Rehabilitation 12:112 [DOI] is the definitive comparative treatment.

Spectral Arc Length (SPARC):

$\mathrm{SAL} \triangleq -\int_0^{\omega_c} \left[ \left(\tfrac{1}{\omega_c}\right)^2 + \left(\tfrac{d\hat V(\omega)}{d\omega}\right)^2 \right]^{1/2} d\omega, \qquad \hat V(\omega) = \frac{V(\omega)}{V(0)}$

where $V(\omega)$ is the Fourier magnitude spectrum of the speed profile. Normalising by $V(0)$ makes it amplitude-invariant; the modified SPARC uses an adaptive cutoff $\omega_c \triangleq \min\{\omega_c^{\max}, \min\{\omega \mid \hat V(r) < \bar V \; \forall r > \omega\}\}$ to make it duration-invariant too.

Log dimensionless jerk (LDLJ):

$\mathrm{DLJ} \triangleq -\frac{(t_2-t_1)^5}{v_{\text{peak}}^2}\int_{t_1}^{t_2}\left|\frac{d^2 v(t)}{dt^2}\right|^2 dt, \qquad \mathrm{LDLJ} \triangleq -\ln|\mathrm{DLJ}|.$

The 2015 paper is explicit that DLJ "lacks sensitivity in the physiological range" and that LDLJ has "poor reliability" under measurement noise — a serious caveat for teleoperation data, where jerk requires double-differentiating noisy pose estimates. The practical ranking is SPARC > LDLJ > number-of-peaks.

These are not idle formalisms. Kulkarni, Dhar & Cui (2026), RINSE [arXiv:2604.23000] [C] use spectral arc length directly as a demonstration-filtering criterion, reporting +16% success on RoboMimic Transport using one-sixth of the data and +20% on a real push-block task using half the data. Critically for this review, both of their metrics rank kinesthetic teaching above teleoperation, matching downstream policy performance. Smoothness is not merely correlated with quality; it is usable as a filter.

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