X-ray Fluorescence Analysis of Feldspars and Silicate Glass: Effects of Melting Time on Fused Bead Consistency and Volatilisation

Round 1

Reviewer 1 Report

Making fused beads for XRF analysis requires the use of melting times sufficiently long to obtain a good homogeneity and at the same time sufficiently short to minimize losses due to volatilization.

In this framework, this paper report on the influence of this melting time on the volatilization processes. Using LiB4O7 as fusion flux and a melting temperature of 1065°C, they derived 3 mains conclusions which reflect the presented results: (i) The ideal melting time is found to be between 25 and 60 minutes, (ii) As expected, the evaporation of SO3 is well described by a simple diffusion-based model, (ii) The latter is associated to additional mechanisms regarding the evaporation of Iodine.

This paper is well organized and reads very well. In particular, the introduction is well documented, the experimental section gives all necessary information and finally, the results are well discussed with a review of all possible errors that could influence the interpretation.

I recommend the publication of the paper in Minerals as is.

Author Response

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Author Response File: Author Response.docx

Reviewer 2 Report

Dear authors, this is a painstaking piece of work. You produced a large amount of analytical data, and I trust these data are accurate. However, the conclusions derived from these data are vage. The recommendation given in the CONCLUSION applies to users of the same type of equipment only. Thus, the relevance of your recommendation is quite limited.

Comments for author File: Comments.pdf

Author Response

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Author Response File: Author Response.pdf

Reviewer 3 Report

I like the attempt to quantify basic method choices, but I am not convinced by the arguments and data presented that this paper represents a significant advance in understanding some of the difficulties in preparation of fused glass. With some additional effort I think this could be a publishable work. My primary concern is there is no mention in the paper of the possible effect of grain size, the only variables are thought to be fusion time and temperature. Some CRMs are very poorly ground, and at least one of the CRMs used in this study (BCS375) contains many silt sized particles (and is very difficult to make a pressed pellet with for that reason), and thus is a problem both to sub-sample properly when weighing as well as requiring more fusion time to dissolve. The grain size variable needs to be tackled before one can isolate the effect of fusion time. At a minimum I would like to see a grain size distribution for the CRMs used, and some discussion of whether or not grain size is a significant variable to consider.

The other bothersome issue is the very poor accuracy in the data presented (e.g., in the case of BCS375 Al2O3 is ~10% off from the CRM value). The authors use the method promoted by Giles et al, but the Giles et al paper shows excellent validation data, with the only problems found at low Na2O concentrations. The wide disparities shown don't help convince this reader that the variations found with fusion time aren't due to other issues such as matrix correction or concentration based spectral interference correction. Notably, some CRMs (e.g. 532 for Al, Si, and 525 for Na, Si) tested are more accurate with the shortest fusion time, whilst others are more accurate, but still very inaccurate, at the longer fusion times (e.g., 375). No explanation is offered for these conflicting results other than that the WOXI routine is not so hot (sorry). There is mention of the spectral overlap of I on Ti and it's evidence in the data, one wonders why the interference was not corrected in the intensity terms prior to the concentration calculation, where it would be highly effective, rather than relying solely on Giles et al's concentration corrected spectral interference when the concentration of I is not determined. How could anyone ever trust the Ti determined with this method? Giles et al do not mention use of a releasing agent in their paper.

Also bothersome is the use of the counting error for the 525 CRM to express the measurement error of the analytes versus fusion time. The counting error of any single pellet should always be very small. That is not the error representative of the fusion time, however, that error can only be assessed by duplicate (or quadruplicate etc., more is better) preparation of pellets with the same fusion times. If CRMs are too expensive for this test, any in-house finely ground sample would do, especially because accuracy is less important than precision in this case. (And I agree the accuracy is not the critical factor here).

Some local comments:

lines 42-99: a shorter version of these lines, emphasizing the main points about diffusion models etc, with fewer references, would be easier to read and set the paper up better in my view. It's nice the things that are here, but they aren't all necessary.

lines 52-55: awkward sentence, do you mean to say on line 54 that the relationship between mass loss and reciprocal temperature is log-linear?

lines 67-69: uses semi-colons where commas would be more correct.

lines 120-122: F may behave very differently during fusion than the other halides, especially Cl, due to its affinity for melt rather than vapor. F is markedly less volatile during fusion at 1000 C in LiT than either Cl or Br in my experience.

line 131: a minor quibble, but there is no "pouring" involved when using static graphite crucibles.

lines 144-146: are repeated almost verbatim in lines 167-170.

lines 171-172: the use of the word "approximately" with regards to weighing confuses me. All weighing is "approximate" but what needs expressing here is how precise was the weighing and how precise was the maintenance of the 10:1 flux:CRM ratio. What precision target was set, to 0.1 mg or 1 mg or what? 

lines 466 and 491 contain spelling errors.

Author Response

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Author Response File: Author Response.pdf

Round 2

Reviewer 2 Report

Thank you for the careful revision.

Reviewer 3 Report

I thank the authors for responding positively to all of the first review comments. The revised MS does include responses to all of the issues raised. However, after further examination of their results I still remain unconvinced that fusion time is the most important variable accounting for their data. Firstly, I note that the three feldspars and one glass sample do not all show improvements in accuracy with fusion time, that is a telling fact in my view. Secondly, the absolute differences in concentration that are shown to support their case amount to ~0.2 wt%. Considering that they include TiO2 in their normalization, which declines by ~0.1 wt% absolute with increasing fusion time, the overall variations they are arguing from are very small. Without a more thorough demonstration of the precision of their method I cannot accept their conclusion that fusion time is the most critical variable. I suggested in the first review that they do multiple experiments at each fusion time, that work would serve to satisfy the question of whether or no such small variations are indeed significant. I suggest they also do a validation study of their method because the CaO and K2O data they show for these 4 RMs are all biased the same direction, if the bias is systematic it should be easy to correct. The authors do not seem to have understood my suggestion that they correct the I overlap influence on Ti in intensity terms, because they answer that such a correction is not possible without determining I concentrations. The efficacy of doing spectral overlap corrections in intensity, rather than concentration, terms is that one doesn't need to know the concentrations, only the ratio of the intensity measured on the overlapping element (or its proxy) to the intensity of the overlapped line.