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Ether cleavage and chemical removal of SU-8

by José M. Ripalda, Raquel Álvaro, and María Luisa Dotor

Submission summary

As Contributors: José M. Ripalda
Preprint link: scipost_202203_00018v1
Data repository: https://zenodo.org/record/6351619
Date submitted: 2022-03-14 15:25
Submitted by: Ripalda, José M.
Submitted to: SciPost Chemistry
Academic field: Chemistry
Specialties:
  • Organic Chemistry
  • Physical Chemistry
  • Materials Chemistry
  • Theoretical and Computational Chemistry
  • Nanoscience
Approaches: Experimental, Computational

Abstract

The high chemical stability of SU-8 makes it irreplaceable for a wide range of applications, most notably as a lithography photoresist for micro and nanotechnology. This advantage becomes a problem when there is a need to remove SU-8 from the fabricated devices. Researchers have been struggling for two decades with this problem, and although a number of partial solutions have been found, this difficulty has limited the applications of SU-8. Here we demonstrate a fast, reproducible, and comparatively gentle method to chemically remove SU-8 photoresist. An ether cleavage mechanism for the observed reaction is proposed, and the hypothesis is tested with ab initio quantum chemical calculations. Also described are a polymer-metal adhesion treatment, and a complementary removal method, based on atomic hydrogen inductively coupled plasma.

Current status:
Editor-in-charge assigned


Submission & Refereeing History


Reports on this Submission

Anonymous Report 1 on 2022-6-5 (Contributed Report)

Strengths

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.

Weaknesses

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.

Report

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.

Requested changes

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.

  • validity: low
  • significance: low
  • originality: ok
  • clarity: good
  • formatting: excellent
  • grammar: excellent

Author:  José M. Ripalda  on 2022-06-09  [id 2571]

(in reply to Report 1 on 2022-06-05)

We agree with all the comments and assessments made by the reviewer. Changes to the manuscript will be done when given the opportunity by the editors.

In the following we provide answers to each of the questions and suggestions raised by the reviewer.

  • "Three current technological issues with SU-8 have been addressed in this work" seems a very big claim compared to the results available.

Agreed. We will withdraw this statement.

  • 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. 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.

We compare two pathways, with and without dimethylamine. We are mostly experimentalists. Our capabilities for DFT are limited, thus it would be imprudent for us to pursue a study beyond a very routine level of theory. Nevertheless we felt that the possible mechanism of the reaction required at least some discussion and thus we have included our modest DFT effort to support such discussion.

The mechanistic study is admittedly incomplete, but nevertheless we think it would be beneficial to the community to have these results published even if the mechanism of the discovered reaction has not been completely elucidated.

We have experimentally found that dimethylamine exposure induces a change in SU8 that makes it soluble in sulfuric acid, but definite proof of what is the mechanism of action is a matter for future research.

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.

We agree with the referee that our claims in regard to this aspect of our work would require more quantitative data, and thus we will withdraw most of our statements in regards to this aspect of our work. The adhesion improvement manifested itself by fewer delamination events at the SU8 / Pt interface. Before using the described process based on mercaptohexadecanoic acid self assembled monolayers we were using a process based on a commercial solution (Jentner Oxiprotect) that in some cases led to a complete lack of wetting during spin coating, particularly when attempting to coat with Brewer-Science bottom antireflective coating ARC I-con.

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.

We will include a discussion of the interdependence of the various experimental factors. The parameter window for high quality lithography is quite narrow and the combination of optimal parameters needs to be determined on a case by case basis. A large number of experiments were done to determine this combination of parameters for each photoresist thickness. A complete description of all experiments would only add confusion to our manuscript as many of those experiments correspond to suboptimal photoresist exposure conditions in a trial and error effort. We have chosen to report instead the experiments resulting in high quality photolithography and subsequent photoresist removal. In case of overexposure the time for removal greatly increases, and conversely in case of subexposed photoresist the removal time is not representative of the optimal process. If the experimental parameters are independently scanned, then in most cases the results obtained correspond to sub-optimal process conditions that are not of interest. As observed by the reviewer, this merits a more detailed discussion in the manuscript.

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.

Samples were examined after removal by optical microscopy, electrical contact resistance and in some cases with scanning electron microscopy and energy dispersive x-ray emission spectroscopy. A very thin residual layer (50 nm) cannot be ruled out as it can be easily pierced by the electrical contact probes, but a photoresist layer of more than 50 nm is easily detected as it changes the reflectivity of the underlying metal due to interference. So we will modify the manuscript to reflect that we experimentally verified in that in all cases a residue of no more than 2.5% of the initial thickness remains on the surface. The phrase "complete removal" will be withdrawn.

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

A scale bar will be included.

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 reaction of dimethylamine with epoxide functional groups has repeatedly been verified in the literature. We will include sufficient references to support this claim. E.g.:

Epoxide Reactions, Thomas Bertolini, Journal of Chemical Education • Vol. 79 No. 7 July 2002

Highly Chemoselective Addition of Amines to Epoxides in Water Najmodin Azizi and Mohammad R. Saidi Org. Lett. 2005, 7, 17, 3649–3651 https://doi.org/10.1021/ol051220q

Assessing the Potential for the Reactions of Epoxides with Amines on Secondary Organic Aerosol Particles Santino J. Stropoli and Matthew J. Elrod, J. Phys. Chem. A 2015, 119, 40, 10181–10189 https://doi.org/10.1021/acs.jpca.5b07852

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 also merits further discussion in the manuscript with appropriate references to the literature. The carbocation results from the protonation of the epoxide functional group, this is a well known reaction of epoxide groups. It has also been widely reported that this carbocation subsequently reacts with other epoxide functional groups producing further polymerization, and it is the reason for SU8 being, by design, a chemically amplified photoresist, as a single photon results in the generation of a carbocation by the Triarylsulfonium/hexafluoroantimonate photoacid, and this single carbocation can lead to several polymerization events as it persists after polymerization. The anion associated to the carbocation is the SbF6- anion from the photoacid in the SU8 formulation. Appropriate references describing the role of carbocations in SU8 polymerization will be included.

Triarylsulfonium hexafluorophosphate salts as photoactivated acidic catalysts for ring-opening polymerisation January 2013Chemical Communications 49(12) DOI:10.1039/c2cc38114a

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.

We base our work on the previous computational mechanistic investigation of Sturgeon et al (ref. 16) in a similar case of acid catalyzed cleavage of ether links. Sturgeon first performed a Monte Carlo Multiple minimum (MCMM) conformational search optimizing structures with the semi-empirical PM6 Hamiltonian. All low lying conformers within 15 kcal/mol of the global energy minimum were selected for DFT calculations. We take advantage of this previous effort to directly explore the most promising reaction pathways. But even in the case of the extensive exploration by Sturgeon et al., only stable configurations were studied as semiempirical methods are required (for cost reasons) for such an extensive exploration, and these are not adequate for transition states. The study of possible transition states is indeed possible and often done, but unless it can be shown that all possible transition states have been systematically studied, the effort is not justified. In practice this usually done in particularly simple cases. In complex cases such as the present one, an exhaustive search of all possible transition states is well beyond our capabilities. The presented DFT calculations do however show that the proposed pathways are energetically feasible.

We are grateful for the effort made by the reviewer and the useful feedback.

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