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Under review as a conference paper at ICLR 2027

Same Error, Different Function: The Optimizer as an Implicit Prior in Financial Time Series

Abstract

Neural networks applied to financial time series operate in a regime of underspecification, where predictors achieve comparable out-of-sample error. Using large-scale volatility forecasting for S&P 500 stocks—twelve architecture–optimizer configurations, thirteen seeds each, evaluated on 564,795 held-out observations—we show that comparable test loss conceals measurably different predictors. In eleven of twelve comparisons, models trained from identical initialization and identical data order diverge to times further than repeated runs of either optimizer alone, ruling out initialization noise as the explanation. On a common scale, predictions differ by 5–17% of the typical forecast error while the models' error magnitudes differ by less than 0.7% of it. The divergence reshapes non-linear response profiles, temporal dependence, and ultimately decisions: volatility-ranked portfolios trace a Sharpe–turnover frontier with up to 58% turnover dispersion at comparable gross Sharpe ratios. In underspecified settings, optimization is a consequential source of inductive bias, and model evaluation must extend beyond scalar loss to functional and decision-level behavior.

Primary area:
learning on time series and dynamical systems
Keywords:
implicit bias, optimization, financial time series, volatility forecasting, underspecification, predictive multiplicity, functional divergence, model interpretability, edge of stability

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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3(+1)
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2
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Paper summary

This study examines whether two models that produce similar forecasts for the same variable (in this case, one-step ahead equity volatility) can be considered functionally and behaviorally identical. In order to assess this question, the researchers used a historical S&P 500 panel provided by CRSP to develop a model that predicts Garman-Klass log-variance based upon 100 previous data points. They tested three different types of neural networks (SGD, Adam, Muon) and compared them to a linear baseline. Each neural net type was fitted 13 times and evaluated using 564,795 out-of-sample observations.

While many of the configurations produced very similar test NMSE values, the determination of statistical equivalence depends on the chosen tolerance level. A major finding of this study is that there are significant differences between these models even though they have similar forecasting errors. The authors measured the distance in the prediction-space of each model with respect to its within-configuration variability. They also conducted additional trials using matched initialization and data order.

Additionally, they investigated the impact of model architecture on impulse response and SHAP lag-attribution. The authors explored how learning rate and batch size affect curvature dynamics as a potential explanation for why these models behave differently.

Lastly, they demonstrated how the models vary in terms of target-allocation turnover when constructing volatility-sorted portfolios. The authors argue that training configurations should be assessed based on their functional and downstream behavior rather than simply on their scalar forecasting loss.

Critical strengths

This work’s main advantage is that it will never draw conclusions about functional differences based solely upon visual distinctions in the generated response surfaces. Instead, this paper assesses the degree to which there are disagreements among various optimizations when run on the same set of held-out data; then, it compares those disagreements to the variation that occurs when multiple optimizations of the same model are performed. The use of the "stronger" normalization (i.e., using the larger within-optimizer distance) is particularly beneficial. As an illustration of this, the MLP Adam-Muon comparison results in a cross-optimizer distance of 0.0539 compared to within-optimizer distances of 0.0400 and 0.0119, with a pointwise interval for the "stronger" ratio excluding unity.

In addition, the seed-level jackknife accounts for the dependencies created due to distances being shared among different optimizations. By combining the seed-level jackknife with the differentiation between non-rejection and tolerance-based equivalence, this work provides a great deal more descriptive evidence than a traditional optimizer-leaderboard study would.

Critical weaknesses

The comparative analysis of optimizer performance has the potential to influence the overall optimization update rule more than the individual optimization update rule itself. In Table 4, the weight-decay values are varied among the different optimizers. Appendix E.2 clearly indicates that the paired experiments control for initialization and the order of the data; however, they do not control for regularization or computation time.

While the CNN-SGD optimizer is trained for seven epochs, all other CNN optimizers are trained for 50 epochs. Similarly, the paired LSTM-SGD experiment has a different configuration than the main 13-run cohort.

Although matching initialization and batches is helpful, this approach does not provide the means to distinguish implicit optimization biases from explicit regularization and finite-training effects.

Thus, the evidence demonstrates how differences exist between entire training configurations rather than providing additional support for the optimizer-specific interpretations that are presented in the title and conclusions. A controlled comparison of optimizers without explicit decay, or with an explicitly regularized and comparably sized training budget would substantially improve the interpretation of these findings. Curvature-based interventions do not address this gap in identifying causality. Appendix F provides useful information regarding how interventions affect both predictions and curvature.

However, altering learning rate does not isolate curvature as the causal factor behind functional movement.

Moreover, Appendix F.1 acknowledges that contractions occurring within a non-quadratic region could also result in changes to curvature. Such acknowledgment directly contradicts the more definitive claims made in Sections 4.4 and 6 concerning the fitted solution being a minimum. The interventions provide support for a possible dynamic explanation of the observed phenomena, but do not provide support for excluding alternative explanations.

Questions for authors

Will the main differences in function space continue to exist if we control for explicit regularization (i.e., disable weight decay) and have the same amount of time to train in each architecture, and use appropriate learning rates for each optimizer? A single, well-defined example will allow us to determine if an optimizer-specific implicit bias is present as opposed to the overall effects of a properly tuned training setup. Is it possible to limit your conclusions to only those cases where the entire training setup has been optimized?

Can Table 12 be expanded to include the distribution of held out turnover (turnover in the testing set) and the forecast error for each of the retained repeated-fit checkpoints? The main issue with expanding Table 12 is whether the difference between configuration allocations continue to be significantly greater than the difference that results from running the same configuration again. It would also be helpful to compare HAR to other methods in this downstream comparison because HAR produced the lowest NMSE in Table 1 and is a good example of why neural predictors should be retained even though they do not improve forecasting error.

3 comments

Thank you for recognizing the value of our paper. We have completed the zero-decay, matched-budget experiment and repeated-fit downstream analysis you requested. Supporting pictures.

Critical Weaknesses and Question 1: regularization and training budget.

Thank you for suggesting this control. We are sorry the role of the validation-selected settings was not clearer. Below we explain the choices and the additional experiment.

  • Original hyperparameters. Learning rate and native weight decay were selected for each optimizer by validation loss. Table 4 therefore reports validation-selected decay values. We tested whether separation persists without decay and with equal duration.

  • Additional control disabling weight decay. Transformer–SGD and Adam use the same architecture, final-fit data (train+validation), preprocessing and batch size, with zero decay in every parameter group. Both train for exactly 50 epochs without early stopping, over 13 paired initializations. Starting weights, minibatch order and stochastic-layer seeds are paired. Learning rates remain optimizer-specific and previously validation-selected. We compare epoch-50 checkpoints.

  • Results. Mean test NMSE is 0.57445 ± 0.00139 (SGD) and 0.57613 ± 0.00139 (Adam), mean ± seed SD. Group mean errors are equivalent within the existing exploratory tolerance 0.005 NMSE (paired TOST, p=0.0000136). Paired prediction distance is 0.06309, versus 0.03974 within SGD and 0.05100 within Adam: 1.24 times the larger within baseline, with exploratory pointwise 95% interval [1.08, 1.41]. Thus separation persists with equivalent group errors under the controls you requested. We will include all seed results in the revision.

  • CNN duration and paired LSTM configuration. Thank you for identifying these issues. CNN–SGD retained its selected seven-epoch recipe for compute budget but we can repeat it at matched horizons in the final version. We corrected the three paired LSTM–SGD fits using the selected configuration and saved starts/data order. Test NMSE is 0.57662 ± 0.00016 (SGD), 0.57541 ± 0.00056 (Adam), 0.58189 ± 0.00050 (Muon). Ratios to the larger within baseline, with paired distances in parentheses, are SGD–Adam: 2.87 (0.04683); SGD–Muon: 1.40 (0.08726); Adam–Muon: 1.31 (0.08188). All three exceed both within baselines. We will update Appendix E.2.

Curvature interventions: interpretation and scope.

Thank you for highlighting where the interpretation needs clarification.

  • What the intervention tests. A curvature change alone would not establish constrained dynamics; we appreciate the opportunity to clarify this. Appendix F.1 asks a more specific question. At a fixed quadratic minimum, LR/10 reduces fluctuations without changing the Hessian. In Appendix F.3, for instance MLP–SGD instead shows sustained sharpening and further loss reduction relative to a stable control. This sustained contrast supports a learning-rate-dependent curvature constraint.

  • Causal interpretation. You are right that LR/10 does not uniquely identify curvature as the mediator of functional movement. Appendix F.1 explicitly discusses the nonquadratic alternative. We will make this scope equally clear in Sections 4.4 and 6: the interventions support constrained dynamics without excluding every alternative explanation.

Question 2: held-out turnover across repeated fits and HAR.

Thank you for suggesting this check across initializations, the results further strengthen our previous conclusion.

  • Expanded Table 12. We evaluated all 13 retained fits of each of the 12 paper configurations, reporting held-out turnover and gross Sharpe as mean ± seed SD. Companion tables give every checkpoint and its forecast error. All methods use the same test dates, assets and portfolio rule.

  • Results across initializations. Across-optimizer allocation distance exceeds both within baselines in all 24 architecture/pair/quintile comparisons for Q1/Q5, with exploratory pointwise 95% ratio intervals above one. For MLP Adam–Muon Q5, turnover is 14.97 ± 0.25% versus 11.31 ± 0.14%, with gross Sharpe 0.841 ± 0.007 versus 0.845 ± 0.005. Allocation distance is 1.99 [1.90, 2.08] times the larger baseline. This directly addresses your question: allocation differences exceed rerun variability, with substantially different turnover at very similar gross Sharpe. We also added HAR on the same panel: Q1/Q5 turnover is 26.00%/18.78%, with gross Sharpe 1.176/0.833. As set forth in the introduction of the paper and Question 1, our contribution concerns optimizer-dependent functions and decisions, rather than forecasting superiority over established methods.

Please let us know what doubts remain. We are happy to provide clarification or targeted experiments and hope this evidence gives you grounds to reconsider your assessment and score.

Thank you for the detailed rebuttal and clarifications. The responses have adequately addressed my main concerns and improved my assessment of the paper. I have raised my score.

Thanks a lot!

Good luck with your papers!

Best,

The authors

Reviewer_qkJ5OpenReview ↗
Rating
3(+2)
Confidence
3
Informativeness
2(+1)
Presentation
3
Soundness
3(+2)
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Paper summary

The paper’s work is motivated by the following observation. Many financial forecasting models have comparable out-of-sample (oos) prediction error or loss. The question is whether such comparable metrics mean similar fitted functions. The paper’s first claim is that these models, i.e., the fitted functions, are different from each other, although they share similar oos loss. The second claim is that what causes such differences in the functional forms is the optimizer.

To support the claims of the paper, the volatility forecasting task is studied. The work trains models with different architectures (MLP, CNN, LSTM, Transformer) paired with different optimizers (Adam, SGD, Muon). The inputs of the learning task are the past volatilities, and the target is the forward volatility. Then, the authors measure the differences between the fitted models by computing the distances between the predictions outputed from these models. The authors also show the fitted functions by plotting the model’s response surface. The response surface is defined as follows. For an input index (e.g., the k-th input feature), we fix the other inputs but vary the values of the one input to plot the responses of the model. The work is done on the real-world dataset of S&P 500 constituents on daily data. The paper concluded that the aforementioned claims are real via the experiments.

Critical strengths

The work targets an interesting aspect in financial forecasting, i.e., evaluating the models using a single metric can lose information, especially when the values of the metric are close. The paper aims to reveal this by showing that the same error could mean very different functions and, in this case, the optimizer is acting as an implicit prior for the functional forms. These claims are, if shown to hold true, significantly insightful. When I first read the claims, I felt excited. Therefore, I would say that the problem chosen by the authors and the kind of contributions they are aiming at are well-aligned with ICLR.

Critical weaknesses

Unfortunately, it turns out that the paper fails to convince me that the claims are true. It certainly did not show that they are false. My assessment is that it simply did not give sufficient evidence to support the claims. I elaborate my assessment in the following two aspects.

  1. The paper did not show that the fitted functions are actually different from each other when they share similar errors. The key figure I am referring to is Figure 2(b). The plot did not show that the fitted functions are different. In this figure, the scale of the axis is in the log-variance units. Reporting an RMS prediction distance of 0.10, for example, does not give a sense of difference, as it is not a normalized value. The typical values of the predictions should be reported along with the typical measurement error, such as the average difference between the predictions if we fix an architecture and optimizer, but with changing initialization. Therefore, my first critique is that the figure did not show that the functions are different.

  2. The plots of the response surface (Figure 1 or Figure 13) give little information about the structure of the fitted functions, especially when the inputs are highly correlated. This also brings another key weakness, which I will discuss soon. The response plot is fixing the other input index but changing one. It is fine when the inputs are independent to each other. It is not fine when the inputs are correlated with each other. Consider the following toy example.

I have two time series xx and yy, which can be viewed as random variables with a standard deviation 1.0, so σx=σy=1\sigma_x = \sigma_y = 1. They are highly correlated as corr(x,y)=0.99corr(x, y) = 0.99 (imagine they are the same variables). Then, we use these variables to forecast another time-series random variable zz with z=ax+byz = ax + by. Suppose that the ground true model is z=0.018x+0.002y+0.98ez = 0.018x + 0.002y + 0.98e, where ee is a standard normal variable with standard deviation 1.0. In this case, we fit a model on the historical data for the model z=ax+byz = ax + by. If you use SGD, you get, for example, z1=−0.0509x+0.0607yz_1 = -0.0509x + 0.0607y. If you use Adam, you get z2=−0.1068x+0.1167yz_2 = -0.1068x + 0.1167y. I am making up these numbers for discussion. If you look at the functional form, they are certainly different because one has coefficients -0.0509, 0.0607, and the other has -0.1068 and 0.1167, which means, if you plot the response surface, they look different. However, they are very close to each other, given corr(x,y)=0.99corr(x, y) = 0.99. If you input x=0.3,y=0.3x = 0.3, y = 0.3, z1z_1 outputs 0.00294 and z2z_2 outputs 0.00297, which, to me, are close to each other.

This example shows that the difference between the exact functional forms might be due to the correlation between the features. They (z1z_1 and z2z_2) should be regarded as similar not different with each other, and the response curve will misleadingly show that they are different. In the case of volatility forecasting, inputs are highly correlated as the past volatilities have overlapping lookback windows and the volatility process is autocorrelated.

The key takeaways from this discussion include 1) the work did not show that the fitted functions are different from each other by looking at the response surfaces, and 2) the paper does not separate, for the difference in the fitted functions, the effects due to the correlation between the features and the optimizers.

In conclusion, the paper fails to convince me that the claims are real. They might be real, but sufficient evidence is required.

Questions for authors

Consider the toy example I mentioned in the critical weakness. Can you illustrate, with a small sample data, how different optimizers, not initialization/regularization/early stop, create different fitted functions with similar loss?

If you find any flaw in my arguments in the critical weaknesses where I might go completely wrong? I am happy to reverse my assessment if a strong argument shows that I misunderstood anything.

5 comments

Thank you for recognizing the interest of the question and explaining what would change your assessment. We appreciate the opportunity to clarify the evidence. Supporting pictures.

Critical Weakness 1: evidence and calibration of functional differences.

We are sorry we did not make the extensive evidence in Appendices C–E clear enough. In retrospect, we should have brought it forward more effectively in the main body. Thank you very much for flagging this. Below we explain where to find the evidence and what we added. Please let us know how we could further improve the clarity; we are working on it.

  • Errors versus distances. Section 3.1/Table 1 and Appendix D compare forecasting errors against outcomes. Sections 4.1–4.2 and Appendix E compare predictions with one another on the same test inputs. Figure 2(b) alone does not make the calibration clear enough; Appendix E supplies the repeated-initialization comparisons.
  • Output scale. Appendix C standardizes inputs and targets to mean zero and variance one on the final-fit data. A distance of 0.10 means one tenth of the target SD. MLP–Adam/Muon forecasts have SDs of 0.553/0.539 across test observations, distinct from initialization variability.
  • The initialization baseline you request. Each configuration is trained 13 times with different initial weights and minibatch orders. Appendix E.1 averages RMS prediction differences within each configuration and compares them with distances across configurations, all on identical test histories. We compare fits, not ensembles.
  • Quantifying the requested comparison. Section 4.1, Eq. (4), defines prediction distance. Section 4.2, Eqs. (5)–(6), defines the within- and across-configuration averages and their ratio. Appendix E.1 reports their values and seed-level uncertainty, comparing disagreement across optimizers with disagreement from changing initialization.
  • Which lags matter to the forecasts. Section 4.3 and Appendix E.3 use SHAP to assess each input lag’s contribution to the forecast. We summarize lag importance across 13 fits using medians and interquartile ranges. This further helps describe how the fitted functions differ.

We will bring these comparisons forward, clarify the ratios and baselines, and explain that distances establish disagreement while response surfaces provide graphical intuition.

Critical Weakness 2 and Question 2: correlated inputs and the toy example.

Thank you for making this concern concrete. Your example illustrates why different-looking coordinate slices need not imply different predictions on correlated data. This is precisely why we included distances on real test inputs.

  • Feature correlations remain intact in the distance calculation. Both models receive the same complete histories from the test set. We do not change individual lags or break their correlations. If two different formulas produce nearly identical forecasts on these histories, our distance records that agreement. It compares the outputs, not the coefficients or responses to artificial inputs.
  • Improved visualizations. Representing a function with 100 inputs is difficult. We added PC1–PC2 optimizer-difference views along a PCA plane through a real history and averages over actual test histories grouped by PC scores. The first uses synthetic probes; the second uses unchanged inputs. Differences remain visible. We offer these and actual stock forecasts as clearer illustrations, alongside the full-input distances.

Question 1: a controlled optimizer experiment.

Thank you for suggesting this additional experiment.

  • New experiment. We trained Transformer–SGD and Adam with zero weight decay in every parameter group, exactly 50 epochs and no early stopping, using 13 paired initializations. Architecture, final-fit data (train+validation), preprocessing and batch size are identical. Starting weights, minibatch order and stochastic-layer seeds are paired. Learning rates remain optimizer-specific and previously validation-selected. We compare epoch-50 checkpoints.
  • Results. Mean test NMSE is 0.57445 ± 0.00139 (SGD) and 0.57613 ± 0.00139 (Adam), mean ± seed SD. Group mean errors are equivalent within the existing exploratory tolerance 0.005 NMSE (paired TOST, p=0.0000136). Yet paired prediction distance is 0.06309, versus 0.03974 within SGD and 0.05100 within Adam: 1.24 times the larger baseline, with exploratory pointwise 95% interval [1.08, 1.41]. Thus separation persists with equivalent group errors under the controls you requested.

Please let us know whether this addresses your concerns, or what doubts remain. We would be happy to provide further clarification or focused experiments to strengthen the manuscript. We hope this evidence gives you grounds to revise your assessment and score upward.

I appreciate the authors' response. The response has not addressed my key question, but I’d like to take this chance to clarify it.

Can you show that, on a synthetic 1-dimensional data (one input and one output) and 2-dimensional data (two inputs and one output), with no more than 20 data points, how two different optimizers that optimize the same objective function end up with different fitted functions. You should specify the data generation process and list all data points. You should pick two optimizers. Then, this should show clearly how different optimizers end up with different functions despite having the same objective function. For the 2-dimensional case, please make the inputs correlated.

Thanks a lot for the second chance and being active unlike most reviewers :)

This was already shown in a few places in the literature, so it's not difficult to replicate! Please note that the effects of optimizers and different hyperparameters on the solutions are studied by a large community under the keyword of implicit regularization and edge of stability and there is really a world down there. However, in vision, most of these lead to different test errors (as we said in the paper). In finance, they lead to similar test errors which is surprising.

Before linking plots and code snippets I would like to understand from the AC whether this is possible at ICLR27, please AC let us know.

Let us anyways describe what tiny experiments are so that they can be replicated by codex/claude code independently: Imagine input and output dimensions are 1, take 5 data points that lie on a W, e.g., {(-2,1), (-1, -1), (0, 1), (1,-1), (2, 1)}. Train a ReLU network with 20 hidden units and MSE. Here, GD converges to local minima which do not represent the W, SGD even starting from those local minima converges to the W, Adam converges much faster than SGD to another model which still fits the W. In fact, I use this example in the course I teach. We can not show code snippets or pictures here. But from standard initialization GD converges often to horizontal lines passing by 0, SGD and Adam at different speed go to weirder functions which fit the W. Note that this setting is similar to next day prediction in terms of losses, data representations, models.

Now this setting can be replicated in 2 dimensions by putting 2 orthogonal Ws. Also, by choosing one hyperplane and the generating process which only generates inputs from that hyperplane (so correlation 1) and putting a W on the ys as above. You will see that different optimizers converge to different 2d-to2d functions consistently.

Now, when you get to more difficult data distribution, you can for instance show that the batch size biases the way the model "looks" at data. See, e.g., here found through chatGPT https://arxiv.org/pdf/2406.11110, whose first author has a few more papers on the effects of optimizers as effect of initialization (Neurips26, https://arxiv.org/pdf/2605.29152), picture 1 in the first page. As you get to data distributions with more leeway the effect of the optimizer is stronger and stronger.

I also remember seeing some literature about linear regions. You can think of a ReLU network as a piecewise linear function, if you count the number of linear regions, you will see that it changes a lot with the optimizer. Moreover, some literature under the keyword of "backward error analysis/implicit regularization" characterizes mathematically the drifts in weight spaces between optimizers.

We remain at your disposal for any further question! We hope that this shows that we know what we are doing :) in fact we are biased but we think this paper is great as, to our knowledge, the finance community was not aware:

  • of this effect in vision at all.
  • that this effect shapes also the models in financial applications.
  • we are raising that happens in a much more subtle way and explaining how.
  • this implies that the practitioners should actually try to train many models and plot them instead of choosing GARCH.

Again, thanks for being open to discussion and let us know if there is any further question we can address!

Best, The authors

Reviewer_unhXOpenReview ↗
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1
Confidence
4
Informativeness
1
Presentation
1
Soundness
3
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Paper summary

This paper studies a problem in volatility forecasting of the stock market: when multiple neural models reaches same forecasting error, can they replace each other and the whether the choice of optimizer only affect the training effeciency or the way model predict. The authors conducted experiments on S&P500 data from 2000-2024 by forecasting next day's fluctuation rate. By comparing 4 neural network structure trained with 3 optimizers, they display very close forecasting error and they are all worse than a linear model. However, they display very different forecasting behavior given same data. When model initialization and order of training data were fixed, difference introduced by swapping optimizer is 1.3~7.8 times larger than retraining by same optimizer, which means the difference is mainly introduced by the choice of optimizer rather than randomness. Volatility-ranked portfolios trace a Sharpe–turnover frontier with up to 58% turnover dispersion at comparable gross Sharpe ratios. Based on that, the authors suggest that we should also consider forecast behavior of models rather than only considering the return rate forecasting accuracy.

Critical strengths
  • The overall validation of the proposed idea is sound. In this paper, the authors proposed that under the circumstance that multiple models reach the same accuracy of volatility prediction, the optimizer decides which model we eventually arrive at. To validate idea, the authors conducted large scale experiments covering datas from CRSP datasets and run each model with 13 random seeds.
Critical weaknesses
  • This paper cites appendix content very frequently in the main article, which is hard for human readers to follow.
  • The paper uses many 'innovative' terms such as predictive equivalence, leaderboard tie, matched-loss region, Rashomon regime and underspecification to denote similar error and uses terminologies such as functional divergence, functional separation, functional disagreement, prediction disagreement, behavioral divergence, decision multiplicity and economic divergence to denote functional difference. These terminologies make the article extremely hard to follow. And as a reviewer in the field of financial time series, it still takes me to read the abstract multiple times to grasp the meaning of the article.
  • In the field of volatility prediction, it is common knowledge that many deep model can't defeat HAR/GARCH. Despite this article displayed from the view point of optimizer that different optimizer lead to different model, but have the authors tried on return rate forecasting? Also, constructing porfolio by volatility is weird. So I think the novelty of this article is very limited
Questions for authors
  • The paper could benefit by fixing problems addressed in critical weakness.
2 comments

First of all, thanks so much for recognizing the soundness of the empirical validation. Please let us know whether the concerns are resolved :) If not, please let us know the specific claim, missing comparison or uncertainty that remains, we are really keen to addressing then directly and quickly!

Presentation: We are keen to make the paper’s question and contribution clearer, thanks for pointing this out! In particular:

  • We believe we cited the Appendix often in accordance with common standards for short ML papers which require further extensive empirical evidence for every claim. We'd like to defend this as, in our opinion, signals the solidity (by you recognized) of the empirical validation. We are aware that in finance venues this is not practice. We are happy to change this as per your suggestion.
  • Regarding the "innovative terms": we are sorry you did not find our paper clear, we will clearly define many of them. We did our best to report where the terms have been firt introduced (see, e.g., line 151-152) or equation 3. We will put a strong effort towards making this clearer and we will add a table in appendix A with terms and their definition.

Contribution and HAR/GARCH. We are aware of this common knowledge in industry, in fact this is exactly how we open the introduction (see line 29). Let us, however, point out that this is not what we are establishing, in fact, this common knowledge is exactly the motivation behind this paper: we are asking whether its grounding is compelling (see Question 1 in line 37 which is exactly about this). We show that surprisingly the answer is no! Our contribution is that models (we also include HAR/GARCH as a reference) with comparable forecasting errors are not necessarily interchangeable, and optimizer choice can select between them. We further show what knobs make their predictions differ: the training procedure.

Return forecasting. We explored extensively daily-return prediction in preliminary experiments. However, in our commonly available SP500 data (as common knowledge) you can not obtain useful out-of-sample signal with the setup examined (efficient market hypothesis empirically applies at the daily level). We focused on volatility because its predictive structure allows us to study function selection among models that learn the task. We will clarify this scope.

Volatility-based portfolios. Volatility-based allocation is established in the literature: cross-sectional volatility sorts in Ang et al. (2006), and volatility-managed strategies in Moreira and Muir (2017). Our purpose is a controlled comparison of the decisions induced by volatility forecasts. Every predictor feeds the same equal-weight quintile rule, so differences in holdings and turnover can be traced to its forecasts. Mean–variance allocation (Markowitz, 1952) would additionally require expected-return and cross-asset covariance estimates, which our models do not produce; minimum-variance allocation would still require covariances. Introducing these additional models would broaden the study into a different allocation problem. Keeping the decision rule fixed lets us examine the consequences of optimizer-dependent forecasts directly.

Concluding We hope these clarifications address your concerns about the contribution and fix your critical weaknesses. We are happy to clarify further points and hope you will reconsider your assessment and score in light of our discussion. Thank you again for helping us strengthen the manuscript :) and good luck with your own submissions!

AuthorsOpenReview ↗

Just a follow up

Hello! As the deadline is approaching, we'd be greatful if you could find the time to comment on this :) We genuinely believe that we could convince you, gives us a change to convince you the worth of our paper :)

Good luck with your own submissions,

Best,

The authors

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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