We thank Reviewer 1 for a detailed and helpful review. Please, see below our response and proposed changes to specific review comments (italic).

Introduction could be better written. After reading the introduction part a few times, I still feel the goal of the study is not clearly stated,  although everything is there already. I had a mixed feeling that the manuscript is dealing with diffusion of 3He in pyroxene and plagioclase in general but it also seems that the authors are focusing on a more specific goal of how pre-experiment conditions impact acquisition of the kinetics.

The main goal of the manuscript is to determine the diffusion kinetics of 3He in plagioclase and pyroxene. However, the forward MDD model does not explain the experimental diffusion results well, indicating that initial gas loss has occurred. Previous work has ignored this initial loss. Therefore, to obtain accurate diffusion kinetics, we need to identify and account for this loss in the forward MDD model. We agree that the specific goal of the research and structure of the paper could be better described and we will make this more clear in the introduction.

It might be just me, but the misfit determination (in section 2.3.2) does not include a weight term. My concern is the impact from heating steps that involve very small fractional loss of gas (later in the manuscript, authors mentioned this in section 4.1). Can authors include such weight term? Would that change the model fitting?

In general, the choice of a weighting term in fitting models to step-degassing experiments turns out to be important and somewhat complicated. In particular, because it is rarely possible to develop a heating schedule in advance of the experiment that releases the same amount of gas in each step, the released gas amounts and therefore the measurement uncertainties are commonly widely variable among heating steps, and most of the gas is often released in a few steps. Thus, any weighting term based on the measurement uncertainty has a tendency to emphasize the fit to a small minority of the data that have unrepresentatively small uncertainties. A few large, precisely measured heating steps also tend to span a small temperature range, so biasing fitting toward these steps tends to ignore data at other temperatures, which of course makes it difficult to fit the correct activation energy. This is especially a problem as the overall goal is usually to extrapolate the inferred activation energy outside the range of experimental temperatures. Thus, error-weighting is generally not used in this and related applications (see, for example, Schildgen et al., 2010).

For this paper in particular, as we state in section 4.1, the modeled diffusivity does not align well with the observed data from the high-temperature heating steps. These steps include the greatest uncertainty in the data set and account for the least amount of gas. However, as we show in Fig. 8, when we include a weighted misfit statistic such as the χ2, this makes the parameter fitting less constrained as less weight is applied to those high-temperature heating steps where important information is stored. Of course, this is mostly important for diffusion experiments where significant initial gas loss has occurred. As we show in Fig. 8, whether or not we apply a weighted term in the misfit statistics does not significantly impact the modeled parameters for samples where limited initial gas loss has occurred (ROB-plag). We will include a statement in section 2.3.2 referring to this.

It would be beneficial to have a justification of the use of 2-10 domains. Of course a large number of domains improve fitting. I would like to see a brief discussion of its implications and/or plausibility in the context of the studied minerals.

The lower limit is determined by the fact that all the diffusion experiments display non-linearity and a single domain cannot explain the data set, hence, >1 domain is needed. The upper limit in the optimization model is determined from the fact that when applying a reduced misfit statistics, none of the diffusion kinetics (except ROB-PX-Da) requires > 9 domains to fit the observed data. Therefore, for computational efficiency, the upper  limit is set to 10. As the reviewer points out, adding more domains does improve the fitting, however the reduced misfit applied provides a constraint on the optimal number of domains. In the text we will include a short justification of the range in MDD domains used for the optimization.

For each sample category, the authors describe the observation and did modeling for one sample aliquot. Some justification is needed why a particular sample aliquot is selected. Is the observation and insights from the unique sample applicable to other analyzed samples?

It is  true that the premise of the study is that diffusion kinetics for different samples of the same mineral with the same composition in the same lithology with the same thermal history should be the same. Given this, a single diffusion experiment should be sufficient to determine the kinetics. In reality, this is probably true in a general sense, but there is some evidence that for paleothermometry applications where small differences in diffusion kinetics inferred from an experiment lead to large differences when extrapolated to surface temperatures, sample-specific characterization is necessary (Tremblay et at al., 2014). For this study, the aim was to generally characterize helium diffusion in plagioclase, not to make paleotemperature estimates for specific samples, and we chose the number of samples accordingly. In addition, an important conclusion of the paper is that we think that differences in apparent diffusion kinetics between the LABCO and ROB samples, which are from the same lithology, are mainly due to room-temperature storage and not to differences in the true values. In other words, we can’t disprove the hypothesis that the diffusion kinetics in all Ferrar plagioclase are fairly similar.

The author propagated uncertainties for observed ln(D/a2). I am curious if the diffusion parameters from MDD models can be determined with uncertainties. Is it mathematically feasible and/or practically useful.

In general, standard error propagation by linearization and adding in quadrature is feasible (and described in the Ginster and Reiners, 2018), as the reviewer says, for the apparent value of ln(D/a2) for each heating step. Of course, this completely disregards structural uncertainty derived from the fact that the assumption that the initial distribution in the grain was homogeneous fails for the plagioclase experiments, which has a large effect on apparent ln(D/a2) at small release fractions. Regardless, because of the nonlinear nature of the Arrhenius plot, linear error propagation fails once you start trying to fit an activation energy to the apparent diffusivities in each step. 

It would be mathematically feasible to compute an uncertainty in the fitted diffusion kinetic parameters by wrapping the entire optimization calculation in a Monte Carlo simulation in which a set of release fractions was drawn from the measurement error distributions in each iteration. However, this would be computationally very time-consuming (the optimization calculations are already fairly slow on a desktop PC), and, because we are arguing that much of the variation in apparent diffusion parameters is due to model inadequacy (specifically, nonuniqueness of solutions in the presence of storage loss) and not measurement error, it is not clear that fully propagating an uncertainty based on experimental measurement errors would be useful or helpful.

Title. Maybe “implication” would be a better word choice than “applications”?

‘...implications for…’ and ‘...applications to…’ would have similar meaning. We decided that ‘applications to’ was more clear.

Line 200. Should you state here if either one of the production of 3He or loss of 3He during the irradiation more significant? Later you did have statements like “in such a case, any storage (e.g., 1 month) of the sample at room temperature prior to step heating analysis would suppress any measurable signal.” and “for a diffusive mineral, simultaneous production and gas loss (loss via just irradiation or combined irradiation and storage? Please specify) do result in a measurable amount of 3He”. I found a little hard to follow.

Line 203. Shouldn’t the end-members be (1) no diffusion loss (storage) + include irradiation production vs. (2) diffusion loss (storage) included + no irradiation?

We are not sure if the reviewer is referring to irradiation production or irradiation loss in (2) “+ no irradiation”. However, if you account for any production (gain in 3He atoms) while also accounting for diffusion (loss of 3He atoms), then the amount of 3He modeled falls somewhere between the two end-members:

1. Only accounting for gas loss (irradiation and storage loss) and not including any production, will result in the maximum gas loss since any production during irradiation will add 3He atoms.
2. Not including any loss at all, takes into account that all the gas that was produced during irradiation is still present at the start of the experimental analysis.

We acknowledge that this part of section 2.3.1 appears confusing and we will make this more clear in the text.

Line 220. Is there any strategy involved with selecting this particular “arbitrary” three-domain model? Any tests for how sensitive the result is to different MDDs?

No, the prescribed diffusion kinetics were simply chosen from the fact that they provide apparent diffusivities where both irradiation and storage loss can clearly be observed in the Arrhenius plot. That is, it is the minimally complex kinetics needed to make the point visually clear.

Line 266. Maybe justify the 20-time repetition of optimization. Why not 10 or >20?

Previous studies (Gorin et al., 2024) repeated the forward MDD optimization model 10 times, which is enough to obtain a best fit value. Since our forward MDD optimization involves fitting to <2 % of the produced gas, making the diffusion kinetics less constrained for plagioclase grains experiencing storage loss, we decided to extend the optimization repetition to 20, but no further as this is computationally time consuming. We will address this in the revised manuscript.

Figure 2. I recommend to plot the data in grey point in a supplement figure for each aliquot analyzed; same advice for some of the following figures. Otherwise, it’s hard for readers to see Arrhenius data arrays for individual analyses.

It appears the caption was not clear enough here. In fact, each individual experiment is plotted in color in one of the panels in Figure 2 – every one of the gray dots that appear in all panels is plotted as a colored dot in one of the panels. Furthermore, each experiment is shown separately in Figs. 3-4.  We will make this more clear in the caption.

Very minor point, but I wish the authors add a replicated horizontal axis (inverse temperature) for the top to subplot as this should help readability.

We did include this in most Arrhenius plots, but we omitted some of them in Figs. 2 and 5 for clarity.

Table 2. Giving sample radii in microns should be more common given the overall small size and the readership of this article. Probably too many significant digits for column Storage loss (could make the style consistent between Table 2 and Table 3)

This is true, but the counter-argument is that diffusivity D is conventionally taken to have units of cm2/s, so listing the radii in cm makes it simpler to convert apparent D/a2 to standard units for D. Thus, we used cm.

As regards to the significant figures in the loss columns, four digits are necessary so that a fractional loss of 0.9999 is not misleadingly stated as 1, which obviously would not make any sense. We could have solved this by tabulating retention instead of loss and using exponential notation, but this seemed excessively complicated.

Line 326. Figure 6 is not described or discussed in the manuscript.

We refer to Figure 6 in line 324.

Line 404-407. Instead of arbitrary assignment, would it be possible to have better estimations based on some end-member considerations?

This section is fairly complicated and we will try to clarify it in a revised manuscript. Basically, what we are trying to do is to put together a forward model that takes into account what we do know about the irradiation and storage conditions, without overly complicating things. In this section we try to discuss the range in total initial gas loss based on various initial gas loss scenarios, which acts as end-members. Hence, we find the initial gas loss to be between 20-39% based on model inclusions ranging from simple and complex storage conditions, for minerals where 3He is poorly retained at room temperature. However, remember the goal is not actually to estimate the storage loss, but to account for the fact that loss has occurred, such that we can get accurate estimations of the diffusion kinetic parameters. In any case, we will clarify this.

This review includes a number of technical corrections and stylistic suggestions, which are grouped below. Some of these are a matter of journal style which should be addressed during copy-editing; we will correct or clarify all the others in the revised text.

Fig. 2 I recommend to add subplot identifiers A, B, C, … for each plots and refer to specific subplots in the manuscript.

The usage of “diffusive mineral” throughout the manuscript. The “diffusive mineral” should be defined upfront quantitatively since many chronometers are diffusive at certain level.

Line 27. “Surface temperature thermochronology”.. redundant word?

Line 43-45. “In other words, … temperature”. I feel this sentence is redundant, as this is mentioned earlier.

Line 47-48. “In a review, Baxter … noble gases”. This statement seems odd here by itself. It should be more specified if the authors brought up this reference.

Line 50. Can you provide some sort of quantitative description of “generally retentive at low temperatures”?

Line 53-55. Since the authors brought up activation energy here, the authors might want to introduce both pre-exponential factor together with Ea?

Line 70, I feel the authors should not only cite Gribenski et al., 2022 but should also mention the study more explicitly —  study of cosmogenic 3He diffusion in quartz.

Line 100-109. This paragraph might better be placed under section 2.1?

Line 111-112 and line 129. Writing here is a bit hard to follow. I was not able to tell there is indeed a second group of sample until reading the line 129. Maybe introduce the two group at the beginning or be more strategic in paragraphing?

Line 143. If the criteria include similar dimension (since you mentioned grain size in line 142), add that as well.

Line 196-198. Perhaps it’s just me, but I wasn’t able to understand why the “gas loss during irradiation is more complex”. Is it similarly also dependent on diffusivity, time duration, and temperature? Is it just that the temperature is not well known? Nevertheless, unless for other reasons, I woundn’t use “more complex” as it seems to imply some other mechanism involved with irradiation beyond thermally-activated diffusion.

Line 382-385. simultaneous production and diffusive loss? Regardless, I feel the statement of “this is likely overestimate” should be made after the author report the net gain/loss of 3He due to irradiation (using the kinetics from this work).

Line 410. Missing punctuation mark.

We thank Florian Hofmann for the review and interesting and thoughtful comment on the potential effect of ³H. We will make the specific corrections in the revised text where appropriate, or provide a response to the comment (italic) below.

I am wondering if there is any significant production of ³H during neutron or proton irradiation compared to ³He. Any ³H extracted as gas would not be resolved from ³He and measured on mass 3 (or would be part of clumped isotopes if not disintegrated during ionization). The presence of ³H could cause issues if it is lost by diffusion faster or slower than ³He or reacts to form compounds that would not be extracted by heating the samples. This is probably not an issue for samples analyzed within a year or so of the irradiation. However, at long storage times, a significant amount of ³He could be produced from the decay of ³H (half-life = ~12 a), which would increase the 3He concentrations relative to those at the end of irradiation if ³H is still present. Do you have any constraints on the amount of ³H produced during neutron and proton irradiation (³H/³H production ratio) and the diffusion of ³H in the materials discussed here? Would this have any significant effect on your data interpretation?

This is a good question and there has been some discussion of it since the initial use of proton irradiation to produce synthetic ³He in mineral grains. Cross-section estimates mostly from the meteoritics literature indicate that similar amounts of ³H and ³He should be produced in a proton irradiation, but generally the ³He contribution from ³H decay has been ignored because the idea is that the analysis of the irradiated grain should be taking place fairly soon after the irradiation. Obviously, this is not the case if we wait one half-life before analysis – theoretically then about ⅓ of the initial ³He should be the result of tritium decay. Note that this is also true for naturally cosmic-ray irradiated samples – about half the ³He present will be the result of ³H decay, so by waiting 12 years after proton irradiation, we might have inadvertently created a better analogue for the natural system.  Regardless, if we assume (see below) that ³H is not spuriously detected as ³He, and we also assume that ³H produced in either irradiation is not immediately lost from the sample, then the main effect in this paper is just that it would make it more complex to estimate ³He loss during storage – instead of only loss by diffusion we would have simultaneous production and diffusion, possibly coupled with different diffusion kinetics for the parent and daughter. This is basically just an extension of the approximation we already made in estimating loss during irradiation as only diffusive loss, and not simultaneous production and diffusion. Seen from the overall perspective of the paper, however, we already come to the conclusion that diffusion kinetics inferred from plagioclase samples that have been stored at room temperature for a long time after irradiation are not reliable. Adding some extra uncertainty about the fate of ³H-derived ³He would tend to reinforce this conclusion. 

As regards whether ³H could be spuriously detected as ³He on mass 3, we think this is very unlikely. During these measurements the mass spectrometer was operated with a SAES GP50 getter attached to the source and heated to 300° C. Thus, the H inventory in the mass spec comprises whatever exists as a gas in the vacuum envelope as well as a much larger amount dissolved in the getter material, and these are in a dynamic equilibrium in which the partitioning depends on the getter temperature. The purpose of using a hot getter is to rapidly stabilize the H pressure in the mass spec after sample inlet, so getter-vacuum exchange of H is quite rapid. Thus, any ³H that survives sample processing (which also involves exposure to getters) and enters the mass spectrometer will be rapidly diluted by an overall H inventory that is many orders of magnitude larger and mostly dissolved in the getter material. Furthermore, the ratio of H⁺ to H₂⁺ is expected to be fairly small – we haven’t actually tried to measure this on the MAP-II during typical operating conditions, but based on some observations on other mass specs we expect it to be of order 0.1. Overall, therefore, we conclude that the chances of observing any ³H⁺ ions derived from the sample are very low. Finally, if this were significant, because of the exchange between gettered and ungettered H, we’d expect ³H to gradually build up in the getter and lead to an increasing mass 3 background over time. We don’t see this. 

Lines 45-50: You mention the diffusion of He in general. Do you expect to see a difference in diffusion between 3He and 4He? There has been some debate about this, which should be mentioned here.

Because of the mass difference, we expect that the difference in diffusion kinetics of ³He and ⁴He should be nonzero. Measurements of this difference are highly variable among materials – the difference is very large in some glasses (Trull and Kurz, 1999) and almost negligible in many minerals. However, the purpose of this paper is to focus on ³He, mainly because there is not any obvious geological application for ⁴He diffusion in poorly retentive minerals. There’s recently been a lot of attention to ³He paleothermometry in minerals for which Earth surface temperatures are in the partial retention zone, and that is the main potential application of this study. However, by definition, if the partial retention zone overlaps with Earth surface temperatures, then you can’t really use that mineral/nuclide system for any kind of subsurface thermochronometry based on ⁴He from U/Th decay, because the subsurface is always too hot. 

Line 266: Why 20 times? Do the values converge after that number of repetitions? Does this change from analysis to analysis? There should be some justification for that particular number.

Previous studies (Gorin et al., 2024) repeat the forward MDD optimization model 10 times and is enough to obtain a best fit value. Since our forward MDD optimization involves fitting to <2 % of the produced gas and making the diffusion kinetics less constrained for plagioclase grains experiencing storage loss, we decided to extend the optimization repetition to 20, but no further as this is computationally time consuming. We will address this in the revised manuscript.

This review includes a number of technical corrections and stylistic suggestions, which are grouped below. We will correct or clarify all of these in the revised text.

Line 101: What is a “diffusive mineral”? In the conclusions, you mention “<70 kJ mol-1”. If that is your definition, this should be defined with the first use.

Line 259: The term “lnD0/a2” is ambiguous. I assume the natural log applies to the whole term, but this could also mean that it only applies to D0. Use brackets to make it clear which terms the natural log is applied to, e.g., “ln(D0/a2)”.

Line 288: Exponents on “mol” should be superscript.

Figure 3: Toolbar(?) is visible in subfigure b).

Table 2: Make “0” in “D0” subscript. The unit of Ea should be “kJ mol-1”, not “KJ mol-1”.

Table 3: Same changes as for Table 2.

Line 589: The unit of Ea should be “kJ mol-1”, not “KJ mol-1”