(1) The method has relatively limited innovation, as its core technical design is built upon existing approaches.
This is my main concern regarding the paper. The core design of AutoPrune primarily includes loss-based sample selection, random pruning, inverse probability weighting, and learning rate scheduling adjustments. Among these, using loss to measure sample value, dynamically updating sample selection, and applying inverse probability weighting are all relatively common techniques in existing research. The gradient preservation strategy proposed in the paper essentially relies on inverse probability weighting to ensure that the weighted gradients of randomly retained samples match, in expectation, the full-data gradient. While this design is reasonable, the underlying derivation mainly stems from standard unbiased estimation principles and does not represent a significant theoretical breakthrough. Similarly, the training dynamic adaptation component primarily uses loss quantiles to determine the sample retention range and adjusts the learning rate based on the ratio between actual and original iteration numbers. These designs are rather straightforward and largely constitute combinations and engineering adaptations of existing techniques. Therefore, I believe the paper needs to further clarify what substantive new mechanisms AutoPrune introduces compared to existing dynamic data pruning and importance sampling methods, rather than merely integrating multiple established strategies into an end-to-end autonomous driving training framework.
(2) The theoretical analysis of gradient preservation is limited and insufficient to fully explain the observed training performance.
Section 3.2 proves, via inverse probability weighting, that the pruned weighted aggregated gradient is consistent with the full-data gradient in expectation under fixed model parameters and sample partitioning. However, during actual training, model parameters are continuously updated and gradients are correlated. Particularly under mini-batch stochastic optimization and adaptive optimizers, expected consistency of a single aggregated gradient does not imply alignment in model update direction or final optimization trajectory. Moreover, Figure 2(b) primarily validates the gradient compensation effect by comparing the sum of gradient norms across different training methods. Yet, similar gradient norms do not necessarily indicate similar gradient directions, nor do they sufficiently demonstrate that gradient compensation restores the optimization behavior of full-data training. Although the authors mention this limitation in the appendix, given that Gradient-Preserving is one of the core contributions of this paper, I believe the current theoretical analysis and experimental evidence remain insufficient. Further investigation into the similarity of gradient directions before and after compensation, estimated variance, and their impact on optimization stability is recommended.
(3) The training acceleration benefits lack sufficient validation regarding actual computational costs.
The paper presents training acceleration as one of its main contributions, reporting speedup ratios of 1.22x, 1.56x, and 2.17x in Table 1. Notably, these values exactly match the theoretical reduction in number of iterations calculated based on the proportion of reduced training data. For instance, if training consists of ten rounds—using full data in the first round and pruning 20%, 40%, and 60% respectively in the subsequent nine rounds—the theoretical speedups would precisely be approximately 1.22x, 1.56x, and 2.17x. Therefore, it remains unclear whether these speedup figures are derived from actual end-to-end training time measurements or merely computed based on reduced iteration counts. In practice, dynamic sample selection, loss tracking maintenance, data reorganization, and other operations may introduce additional overhead. The paper fails to adequately present real training time comparisons that include these costs, and lacks analysis on training duration and GPU resource consumption across different models. Furthermore, the primary acceleration experiments only involve the second stage of SparseDrive's training, rather than the complete two-stage process. Consequently, I believe the current experimental setup is insufficient to fully support the paper’s overall conclusion regarding end-to-end training acceleration.
(4) Experimental validation remains incomplete, and the fairness of comparison methods and reliability of results require further strengthening.
Although the paper evaluates multiple end-to-end autonomous driving models, all experiments are based on the nuScenes dataset, and cross-architecture experiments use a randomly sampled 50% subset of the original training set. This somewhat limits the persuasiveness of the conclusions when generalizing to full-scale training and other data distributions. Furthermore, the paper primarily relies on open-loop planning metrics for evaluation, including trajectory L2 error and collision rate. For autonomous driving tasks, these metrics alone are insufficient to fully reflect a model's actual planning capability in complex interactive scenarios. On the other hand, Appendix C shows that some compared methods have undergone substantial reconfiguration. For example, RHO-Loss uses historical minimum sample loss instead of the reducible holdout loss calculated by an independent reference model as originally proposed. Such modifications may alter the original method's sample selection behavior, meaning the current comparisons might not adequately represent the performance of these methods under reasonable configurations. Finally, the paper does not explicitly report means, standard deviations, or confidence intervals from multiple independent training runs. Some performance differences are small, particularly in collision rate, so further replication experiments are needed to validate the stability of these improvements.