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Paper summary
The authors studied long-only, fully invested portfolio optimization under the assumption that there is no short selling or borrowing. In their study they identified two key shortcomings of the DF-STPO model; first, the DF-STPO model is trained using dense soft portfolios; second, the DF-STPO model operates in the Cholesky-transformed coordinate space rather than the asset space. The authors developed an alternative approach called RA-STPO. RA-STPO learns to apply bounds to each asset-specific correction around a fixed prediction-based anchor. During the training phase, RA-STPO generates random samples of sparse asset subsets. For each generated sample, RA-STPO solves a non-negative quadratic allocation problem.
Finally, RA-STPO optimizes a loss function based upon the Sharpe Ratio. At test time, RA-STPO calibrates and ensembles the corrected signals, accounts for uncertainty, and applies a causally-updated performance weighting factor to combine the corrected portfolio with the original anchor portfolio. The authors provided guarantees regarding approximation, scale-invariance, differentiability, and robustness. The authors evaluated RA-STPO against four other portfolio optimization techniques by applying them to data from five different equity markets. Their results indicated that RA-STPO had the highest average Sharpe Ratio and terminal wealth among all the techniques tested. The authors performed additional analyses including ablation studies and sensitivity analysis; however, their evaluation used the current index constituents and did not account for transaction costs.
Critical strengths
The RA-STPO model has the ability to evaluate real-time (and) true sparse, long-only, unit-budget allocations during training using a different method than simply doing a dense relaxation and then making a "hard" choice in what we will call evaluation. One important thing to note is that the sampled asset sets are dependent on the anchor being fixed and not dependent on the correction parameters. As such, the lack of a selection-gradient term can be seen as justified for the specified objective and not as an unrecognized approximation to a selection rule that depends on parameters.
Critical weaknesses
Appendix D.3 has indicated that PFL and DF-STPO checkpoints were chosen based on the average validation rank information coefficient, whereas the RA-STPO correction checkpoints were selected based on the average validation Sharpe ratio. These selections have a significant impact on how you compare results. If your main evaluation metric is the Sharpe ratio, then this selection process will affect both how you choose models and which learning approach you use.
In addition, Appendix D.5 has fixed DF-STPO's loss mixture and soft-selection sharpness at and , without evaluating how they respond to validation. Even if we match the number of networks used in each case, these differences remain.
Although the no-correction ablation study is useful, it does not demonstrate that the bounded correction and resampled sparse-path objective performs better than a less complicated anchor-based decision-focused fine-tuning control, given that all three share the same allocator, loss, and checkpoint criteria. Similarly, the sensitivity study continues to randomly draw a new face for each epoch; therefore, it does not allow us to determine the benefits of resampling as opposed to a deterministic anchor-face control. Both of these points are important because the primary contribution of this work lies in developing this specific learning construction, rather than simply demonstrating that using decision-focused training can enhance a prediction-focused model.
Questions for authors
I'm interested in why you've selected DF-STPO using validation rank information coefficient instead of using validation sharpe ratio. Additionally, I'd like to know if your results from the primary comparison would be different if your checkpoints were chosen in a similar fashion to how you've selected the checkpoints of RA-STPO based on portfolio-level validation. Lastly, can you explain to me how you decided to select and and if there was a validation search involved? Your answer will greatly assist me in interpreting the improvements that your method has shown compared to the most similar decision-focused baseline.
3 comments
Response to Reviewer Geha (2/2)
W3, W4 (simpler anchor-based control; deterministic anchor-face control). Thank you for these two suggestions; they turned out to be the most informative experiments for us. All controls share the frozen anchors, the sparse allocator, the batch-SR loss, the checkpoint rule, and the deployment, and each uses 16 seeds. With all switches at their defaults, the control code reproduces the paper's RA-STPO members exactly.
| Control | Correction | Training faces | Complete | Corrected only |
|---|---|---|---|---|
| RA-STPO (paper) | bounded, m + σ⊙tanh(g) | resampled around the anchor, J = 8 | 2.357 | 2.260 |
| Deterministic anchor face | bounded | fixed anchor face (J = 1, no perturbation) | 2.350 | 2.269 |
| Current face | bounded | face of the current corrected signal | 2.287 | 2.202 |
| Unbounded correction | linear, m + σ⊙g | resampled, J = 8 | 2.212 | 2.118 |
| Decision-focused fine-tuning of the PFL network | network itself | current face | 2.084 | 1.939 |
| Same, with resampled faces | network itself | resampled, J = 8 | 2.117 | 2.047 |
| No correction (anchor only) | – | – | 2.046 | – |
Most of the gain comes from parametrizing the update as a bounded correction around a frozen anchor. This adds 0.24–0.27 over decision-focused fine-tuning of the predictor itself, and about 0.15 of it comes from the bound itself (bounded vs. unbounded correction). Resampled sparse paths add essentially nothing over the deterministic anchor-face control (+0.01). No market shows a significant difference (HAC p-values: ESTX 0.89, FTSE 0.29, KOSPI 0.82, NIKKEI 0.88, S&P 0.63). The reviewer's concern was therefore well founded: the paper's attribution of the gain to resampling is not supported by these controls.
Survivorship and transaction costs (noted in the summary). Thank you for noting both issues. Restricting the S&P 500 panel to the constituents at the start of the test period removes 27 later entrants (e.g., SMCI, KKR, APO). This lowers every method's SR (no retraining).
| Method | Current constituents (465) | Point-in-time constituents (438) | Change |
|---|---|---|---|
| Historical / OSCAR | 2.444 | 2.088 | −0.36 |
| Historical / mSSRM-PGA | 1.442 | 0.781 | −0.66 |
| PFL / OSCAR | 1.807 | 1.694 | −0.11 |
| DF-STPO | 1.628 | 1.532 | −0.10 |
| RA-STPO | 2.392 | 2.109 | −0.28 |
RA-STPO remains the highest, but only 0.02 above Historical/OSCAR. Stocks delisted during the test period are still missing from our data, so this removes the bias only partially. With proportional costs, the advantage of daily rebalancing disappears at 10 bps (RA-STPO 0.76 vs. 1/N 1.36; daily one-way turnover 65%). We acknowledge both as fundamental limitations of our evaluation.
Thank you again for the thoughtful review. Your questions on controls and selection criteria changed how we attribute our own results.
Thank you for the additional experiments. I have decided to maintain my original score.
Response to Reviewer Geha (1/2)
We thank the reviewer for the careful and detailed reading, and especially for recognizing that the parameter-independent proposal law justifies omitting the selection-gradient term. The questions about fair comparison were exactly the right ones, and we ran every requested control. Entries are five-market mean annualized Sharpe ratios (SR). All additional models were trained with the paper's code and configuration.
W1, Q1 (asymmetric checkpoint criteria). Thank you for identifying this asymmetry. In the paper, the forecasting baselines (PFL and DF-STPO) were selected by validation rank IC, a criterion that does not depend on the allocator. The correction was selected by the validation SR of its allocated portfolio. We agree that this makes the comparison harder to interpret, so we crossed the criteria in both directions.
Selected by rank IC, RA-STPO stays above every baseline (2.35). Selecting the baselines by validation SR lowers their test SR rather than raising it. The main comparison is therefore not driven by the asymmetric criteria. These results also show that one year of validation SR is a noisy selection criterion, which we discuss under Q2.
W2, Q2 (DF-STPO's α and β). Thank you for this question. In the paper, α = 0.5 followed the fixed default of the DF-STPO authors, and β = 10 was set without a validation search. The DF-STPO authors state in their public discussion that they used β = 5 in all of their experiments, so we searched α ∈ {0.1, 0.5, 0.9, 1.0} × β ∈ {5, 10, 20}. Each configuration was trained with four seeds, and each member was checkpointed by validation SR. Configurations were then ranked by mean validation SR over the five markets. Test SR is shown for every configuration.
Retrained with 32 members, the selected configuration (α = 1.0, β = 20) reaches a test SR of 1.857, or 1.870 when the same forecasts are allocated by greedy. Both are close to the default configuration (1.83) and well below RA-STPO (2.36), so tuning does not change the comparison. The best test value in the grid (1.92, with four members) could not have been identified from validation.
More importantly, the rank correlation between validation and test SR across these 13 configurations is −0.03 (p = 0.92). With a one-year validation window, hyperparameter and checkpoint selection is close to random. This applies equally to our own checkpoint selection, and we regard it as a genuine weakness of our evaluation protocol.