Ether cleavage and chemical removal of SU-8

1. The work is interesting and undoubtedly relevant for various communities working on nanotechnology, photovoltaics, electronics, etc…
2. The need for the present work is justified in the introduction based on the well-presented state of the art.
3. Different challenges of the optical lithography using SU-8 are targeted. The reported process is simple, based on widely available and unexpensive chemicals and is compatible with a wide range of materials, making it technologically relevant.

1. Some claims in the text have little or no proof based on the reported results. Many statements need to be supported by references, experimental proof or simulations. More characterization would be desirable.
2. The scope of the paper is too wide to go deep into the details.

The content of the paper is interesting and the results presented by the authors have a high technological relevance. The work meets the general acceptance criteria and presents a breakthrough on a previously-identified and long-standing research stumbling block. Therefore, I recomend it for publication in Scipost Chemistry provided that the questions below are clarified and/or corrected in the manuscript.

1. The main focus of the paper is the effectiveness of the chemical etching procedure discovered by the authors to remove SU-8 residues after lithography processes. The authors claim that their method is effective with the great advantage of being gentler for a wide range of materials and devices than previously reported procedures. However, no evidentiary result is provided in the manuscript to support this claim at all, apart from figure 3, which gives very little information. Characterization of the sample after processing should be therefore provided. At the very least, an SEM image after SU-8 dissolution should be given for comparison with figure 2. A good way to present it could be to move figure 2 to the results section and group it with the SEM picture of the final result. This is especially relevant for photovoltaic devices as the cells need to be further processed after finger deposition to add antireflection coatings and cleanness is crucial to achieve the desired optical properties.
2. The statements in section 1.3 (SU-8 chemistry and figure 1), which set the framework for the DFT investigation in section 3.2, are not obvious to me and should be supported by references.
3. A minor issue is that the sample preparation procedure in section 2.1 is not clear enough in my view. Are the samples metallized with Ti/Pt before the SU-8 deposition? Why? I would expect metallization to proceed after the deposition and development of the resist. Is that to test metal-polymer adhesion treatments? Is the top surface of the solar cells also metallized before photolithography? I encourage the authors to clarify these questions.
4. Section 2.2 (Polymer-metal adhesion treatment) looks a bit speculative. The authors should provide evidence of the formation of the self-assembled monolayer or support this assumption with references. Molecular self-assembly of alkyl thiols on metal surfaces is a widely studied matter so this minor issue should be easy to solve. More important is to clarify if there is evidence of the improvement of polymer-metal adhesion. Does the polymer delaminate during the baking in the absence of the self-assembled monolayer? Is the adhesion tested somehow or just proven by delamination (or not) during further processing? This part is interesting; however, it needs to be reformulated if the authors want to fit it properly in the scope of the present paper. Alternatively, as it is not the main issue addressed in the paper and not even discussed in the result section, the authors could further investigate and develop this part and leave it for another publication without detracting too much from the relevance of this paper.
5. As the authors explain in section 3.2, thermodynamical data from their DFT calculations does not proof that the proposed mechanism is the actual mechanism behind the observed results as transition states may play an important role and favor other reaction pathways. To my view and because of the technological relevance of the developed process, it is enough for the present work to prove that this is a feasible and likely mechanism with the performed calculations. However, the quality and significance of this work would be greatly enhanced if the authors provide further evidence supporting their hypothesis, either by more sophisticated simulations or by characterization of the dissolution with analytical chemistry methods.

1- The topic is of clear interest and relevance to applications.

2- The introduction provides a clear and concise presentation of the knowledge of the field.

1- The actual results presented are relatively scarce, and do not go in depth into any of the areas studied.

2- The claims made are overall too general and overreaching compared to the data obtained. For example, in the conclusion: "Three current technological issues with SU-8 have been addressed in this work" seems a very big claim compared to the results available.

3- The authors present a lot of hypotheses and suppositions, and often lack actual data to confirm or infirm them. As such, the manuscript is mostly speculative/argumentative, rather than scientific findings.

4- The DFT section, done at a reasonable but very routine level of theory, presents only one possible pathway. It does not compare pathways, or explain some of the choices in the pathway studied.

The content of the paper is overall interesting, but it feels a bit like a mixed pot of very different results (surface preparation, UV exposure, removal, computational results), where none of the areas involved have really been pursued in depth: it does not mean that the findings have no merit, but it raises more questions than it answers.

1- The authors present, in the "Polymer-metal adhesion treatment" section, a "an in house developed procedure to chemically modify the metal surface […] described for the first time". However, this procedure is not explicitly compared to the other state-of-the-art methods (in the Methods section), and its impact on the sample obtained is not presented in the manuscript. Is the adhesion obtained better? (one supposes so) If so, how was this improvement characterized, what quantitative and qualitative factors were compared? Etc.

2- In the section about chemical removal, only three experimental conclusions are investigated and reported. It is not entirely clear to me why these three were chosen, and why the different factors were not investigated separately. It seems to be difficult to reach conclusions, as the authors do, on the basis of only these three experiments.

3- In that same section, how is "complete removal" characterized? Is it visual inspection, or are tests actually performed to quantify the removal? Figure 3 is not very useful in this regard, as a very macroscopic view of dissolution, with no real information provided.

4- Figure 4 needs a scale bar, the diameter of the field of vision is not sufficient for accurate measurements.

5- Section 3.2 and Figure 5: the authors present this reaction in the text as "a hypothesis", but the Figure is less clear and presents it as a fact. The author should perform analysis to confirm whether the tertiary amine is indeed observed after treatment with dimethylamine, which would either confirm the presence of this species (and validate the findings), or invalidate the hypothesis. More than half a page is spent presenting this hypothesis, so it would need to be checked experimentally.

6- This is a major point, which I do not understand: the mechanism proposed and studied by DFT implies the pre-existence of a stable carbocation, that exists as a stable species? The authors state in the caption of Figure 1 "The carbocation persists after polymerization", but that seems surprising to me, so it needs to be argue: how has it been observed and confirmed? what is the anion associated? This is a very unexpected hypothesis, so it needs a strong confirmation in my view.

7- In the discussion of the DFT section, the authors discuss a lowering of the "energy barrier", but transition states have not been characterized or discussed at all. The transitions states need to be determined, and the alternative pathways characterized as well, for comparison and confirmation that the chosen mechanism is representative. The current presentation is way too speculative.

7bis- The authors acknowledge so, saying: "the results are consistent with the proposed hypothesis, but this does not confirm the hypothesis as valid, it merely serves to gain confidence in its validity" and "only a few of all the possible reaction pathways can be explored, and only thermodynamic results on stability are easily achievable, results on reaction kinetics being much more challenging to obtain". But this is not true, there are a lot of DFT studies of chemical reactivity and mechanisms that study both intermediates and transitions states, and compare different mechanisms to conclude: this is, in fact, what DFT studies are routinely used for, in order to reach conclusions about reactivity. Just confirming one set of relative stabilities seems well under the typically bar for mechanistic studies, in this respect.