Significance Comment

The antioxidant examined in the paper has a significant industrial role and so there seems to be little reason to contest the significance of the problem itself, as optimizing its production appears to be a worthy task.

The significance of the study is less clear, since, as mentioned above, it is not obvious how the optimization procedure carried out here would be any different from those already carried out for other chemical compounds. Could one not take another paper for Compound A, replace A with “ascorbyl palmitate”, and carry out the reported procedure to obtain similar results? This is an important question that the authors do not really address. In their defense, they do cite a number of relevant studies in the results section, but it is not very clear (at least, to me) how these studies combine with the present study to advance our mutual knowledge of optimal ascorbyl palmitate synthesis. It is also not entirely clear how the results of the other studies are compatible with the results of the study here, if they are at all, and if it would not be better to include the references in the paper’s introduction as part of the literature review instead.

Quality Comment

The paper essentially considers finding the optimal experimental conditions for the production of ascorbyl palmitate, an antioxidant food additive, by varying the ascorbic-to-palmitic-acid mole ratio, the temperature, the enzyme concentration, and the solvent volume (a total of four factors) so as to maximize the conversion of the product. I will mostly restrict my comments to the portions of the paper that deal with optimization, leaving the chemical and experimental set-up considerations to other reviewers.

On the whole, I find that the paper suffers from a lack of rigor, with the statistical analysis performed largely unconvincing and a number of conclusions premature. I will list below the points that I took issue with:

• The authors carry out a fairly limited central composite design for a problem with 4 factors, testing only 9 unique points, and based on only this data conclude that temperature and mole ratio are the key factors. There does not appear to be a proper analysis of whether or not the response surface relating the optimization variables to the product conversion may have curvature. If the authors are supposing that there is no curvature and that a linear response surface is sufficient, they should state that they are making this assumption and why they are making it.

• Supposing that enzyme concentration and solvent volume make relatively small contributions to production, the authors then carry out a full 2^2 experimental design to optimize over these two factors. They decide to keep the interaction term between the two factors in the response surface (though they do not justify why), and fit a 4-degree-of-freedom model to 5 unique points. Based on this model regressing the data well, they conclude that the fit is statistically valid and describes the true response surface well. Personally, I am not convinced by the validity of a 4-degree-of-freedom model fit to only 5 points, especially in the presence of experimental noise/error, which is clearly present. The corresponding linear system is only borderline overdetermined.

• The authors do not mention if the experiments that are carried out are costly or not. If not, then it is not clear why more elegant designs that would take into account all of the different interactions between optimization variables and the different curvature effects were not carried out (e.g., the 4^3 full factorial or Box-Behnken design for all four factors). It is also not clear what motivates the sequential experimental design as the technique of choice in the first place.

• The authors put a lot of effort into examining the individual effects of the different factors on the conversion. However, such studies must be justified by a “separability assumption” – i.e., the effect of a factor should be similar regardless of what the values of the other factors are. If, for example, temperature changes have a large effect when the solvent volume is low but a negligible effect when the volume is high, then one cannot make general conclusions about the effect of temperature on production. Such an assumption must be stated and justified, however.

• It is not clear how the authors chose their design space (the lower and upper limits on the optimization variable values). This could be justified in more detail.

• The metric – maximizing the conversion – should be challenged, as the different factors themselves (e.g., using more or less solvent) should inevitably contribute to the cost of the overall production process. It is the cost of the overall process that should ideally be minimized, which is a metric that should simultaneously account for the conversion and the economical cost of obtaining that conversion (the amount of acid/solvent used, the heat energy spent, etc.)

On a different note, I did not understand what role the identification of the reaction rate v (presented in Eq. 1) played in the paper, as the authors do not appear to come back to it in the results section.

Finally, I feel like the paper could have benefited from a more detailed literature review. Regardless of whether or not the optimization of ascorbyl palmitate production has been considered in the literature, using experimental designs to optimize the production of some chemical compound is very well-trodden ground, bolstered by an enormous collection of papers. While there is nothing wrong with publishing a paper on ascorbyl palmitate in particular, it does not appear that the optimization here should be in any major way different from similar studies for other chemical compounds. From this, one has the question: is the optimization approach pursued here similar to that of similar studies for other compounds and, if not, what motivates the differences? Unfortunately, the authors do not address this, and appear to stake the originality of the paper on the identity of the chemical compound and not on the method.

Summary

Some miscellaneous comments in addition to the above:

• What justifies not using the stirring speed and reaction time as optimization variables? Is there reason to believe that their effects on the conversion would be small when compared to the others?

• From Eq. 1 and Eq. 2, it would appear that Eq. 2 is just an unconstrained, convex least-squares problem. In this case, one should be able to easily find its minimum by differentiating the objective and setting the derivative to 0. What motivates using Nelder-Mead or simulated annealing?

• If longer reaction times led to greater conversion, then why was 17h chosen instead of 30h?

• I am not sure what the authors mean by a 2^(4-1) design. Doing the math, this would just be the 2^3 design, but that is not what the design in Table 1 is.

• The authors need to explain what they mean when they say that the data was “statistically treated” and what p < 0.05 means in this context.

• I find the label “predicted conversion” in Table 2 to be misleading, as “predicted” makes me think that there is already a model prior to experimental investigations that predicts the results. What this is, in fact, is simply the value of the regressed model fit to the experimental data. It smoothes the data a posteriori rather than predicts it. As mentioned before, low “prediction errors” here are not very convincing, however, since this is not a very difficult feat when describing 5 unique points by a 4-degree-of-freedom model.