Review Reports - Study on the Gamma-Ray Radiation Properties of High-Redshift Blazars at <i>z</i> > 2.5

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript presents interesting results regarding the physical properties of high-redshift blazars. However, many details of data reduction and modeling are missing. Detailed comments are listed below.

Section 2

Table 1

According to my understanding, the authors compiled the SEDs of 38 sources and performed fitting procedures, which should allow for the determination of the corresponding peak frequencies and peak fluxes. Therefore, I am unclear as to why Table 1 presents the peak frequencies and fluxes of the synchrotron and IC components as provided by the references. I would appreciate a clear explanation regarding this point.
Similarly, why did the authors not calculate the accretion disk luminosity themselves? The historical data they compiled should already include thermal emission from the accretion disk, and the authors also applied a disk model in their fitting process. Is there a significant discrepancy between the authors' fitting results and those reported in the references?
The authors could briefly clarify the method by which the black hole masses reported in the references were derived—were they obtained through observation or theoretical modeling?

Section 3

line 130-132

This sentence appears to lack strong logical coherence. If there is no X-ray data available, it implies that no X-ray emission was detected, regardless of its origin.

line 139

Did the authors adopt an anisotropic magnetic field in their study for real?

line 140

From the units of N_pk listed in Table 3, I infer that N_e represents a steady-state EED. However, the description in this sentence appears to suggest it is an injection EED.

line 145

The authors stated their intention to maintain charge neutrality; however, why is the ratio of cold protons to electrons set to 0.1 rather than 1?

line 179-182

Did the authors derive the model parameters based on the peak frequencies and peak fluxes of the low-energy and high-energy components reported in the references? Was an analytical estimation method employed? If so, why do the authors also state that the parameters were obtained using emcee?
Moreover, if the model parameters are entirely free, degeneracies among them would likely prevent emcee from converging. The inclusion of historical data encompassing multiple states would further exacerbate this issue.

line 184-190

The fitting of the low-energy peak in the right panel of Figure 1 is not acceptable. Despite the abundance of historical data points, the authors have disregarded infrared data that are clearly unaffected by self-absorption. In fact, the infrared fitting in the left panel is also barely satisfactory. I suggest presenting all SED fitting figures in a machine-readable format or as an appendix, to allow proper evaluation of the fitting quality.
From Figure 1, it can be seen that the fitting performance of the BLR case and MT case for the Fermi data differs significantly. In particular, for the BLR case, should this interpretation be considered untenable?
The explanation in line 186 is incorrect. The energy density of the external photon field can only change the height (normalization) of EC peak. As noted above, the differing X-ray origins arise from adopting electron spectra of different breadths (i.e., broader vs. narrower), rather than from the photon field energy density.
Line 190: Is the statement regarding the equal contribution of MT and BLR applicable to all sources? This seems questionable, as Figure 1 (left panel) clearly indicates that MT dominates. In fact, there is not even a visible green dashed line representing BLR.

line 191-193

Since the uncertainties of the model parameters have been obtained via emcee, the reported values of all powers should include corresponding uncertainty ranges (e.g., credible intervals propagated from the posterior).

line 196

‘it is challenging to distinguish between particle-dominated or Poynting-dominated…’

There is reason to suspect that this arises from the authors’ assumption that the proton-to-electron number density ratio is only 0.1.

line 201-206

It is difficult to understand how such a small chi-square could be obtained given the abundance of historical data with small error bars—or even without reported uncertainties. I consider this implausible. I strongly request that the authors explicitly detail the chi-square calculation procedure and carefully check for errors (e.g., weighting scheme, treatment of points without errors or with upper limits, degrees of freedom, and whether a reduced chi-square is being reported).

line 219

I cannot understand why the electron-to-proton number density ratio (n_e/n_p) was set to 10 previously, yet here it is taken as 1.

line 219-220

Please clearly specify the reasons why the remaining eight sources are considered unreliable.

Figure 3

The conclusions related to Figure 3 are entirely absent from this section and are instead discussed in detail in Section 4.2. I recommend merging the two parts to improve readability.

Section 4

line 241-243

The electron spectral index predicted by shock acceleration is 2, not 3. Moreover, Table 3 shows that the spectral indices span a very wide range. I therefore urge the authors to carefully reconsider whether the conclusion presented here is appropriate.

line 244-250

As stated by the authors below Table 1, both R_BLR and R_MT are proportional to (L_disk)^0.5. Therefore, assuming the dissipation region is located near the BLR or MT, the corresponding energy density U_BLR/MT ~ L_disk/(R²_BLR/MT)becomes a constant value, independent of redshift.

line 255-260

Comparing the derived jet powers from SED fittings based on simultaneous data would be highly beneficial. I encourage the authors to conduct a comprehensive review of the relevant literature. While I will refrain from listing references, one closely related work—ApJS, 2020, 248, 27—should naturally be cited and discussed in the manuscript.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

I reviewed the paper with great enthusiasm since it discusses a relevant topic and it is written well. However I need to suggest major revision due to the following three reasons:

In my opinion applying only one EBL model is not sufficient for high redshift (z > 2.5), since gamma-gamma absorption on the EBL strongly changes the observed spectrum. Kindly consider applying modern EBL models, eg. Domínguez 2011 or Franceschini 2017. If the effect of this is estimated and found negligible by the writers add a paragraph with the estimation please.

PKS 1830-211 is strongly lensed as far as I know. Were jet powers and luminosities de-lensed? If not, they need to be.

It is not stated whether χ² values are divided by degrees of freedom. If so, kindly add them. If not recalculate the values.

Other minor comments, suggestions:

I would propose adding a recent relevant paper into the introduction, Sahakyan (2024, MNRAS). It is on the study of γ-ray blazars at z = 2.0 - 2.5. Roughly 80 sources and reaches the same broad conclusions about extreme luminosities and jet powers at high redshift.

Some of the fitted Doppler factors (> 50) are extreme. Kindly consider double checking against other ways of estimation, eg. radio brightness-temperature estimates.

Figure 1: below 10^11 Hz the model does not fit radio, right? Therefore I would suggest adding “radio emission from extended regions is excluded from the fit” so it is clear to the reader.

Typos:

Table 2 title: “Reasults” -> “Results”

Line 204 “commonly assumption” -> “common assumption”

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

This paper performs an interesting analysis of the time-averaged SEDs of a modest number (38) of high-z blazers that are adequately detected (TS > 25) with Fermi-LAT. The authors collect a good amount of data in other bands and use the usual one-zone models to fit the SEDs. This work is an updating and expansion of the work of Sahakyan et al. (2015) which also modeled high-z blazar SEDs.

The sample selection is sensible and the way in which the Fermi data were reduced is explained clearly. The approach used to perform the SED fits to the data is standard and described well. The tables are thorough and well presented, and the figures are clear and informative. In general, the discussion and conclusions are sensible; however, there are
a few weaknesses noted below that should be addressed before acceptance of the paper can be recommended. The writing is clear, smooth and grammatical.

One unavoidable weakness is that the authors had to use average SEDs and combine those of their entire sample to mitigate the problems that come with low deleted fluxes and the relatively large errors on them. This is adequately justified however.

The following points should be addressed in a revised version.

1)The authors make a good case that the leptonic models they employ provide good fits to the overall SEDs; however, it is quite surprising that they do not mention hadronic models at all. This is particularly so since there are many blazers for which the hadronic models have been shown to provide better fits to quasi-simultaneous SEDs than leptonic ones. Some reason for ignoring hadronic models for the gamma-ray emission should be given.

2) The authors use an efficiency of 0.3, corresponding to a rapidly spinning SMBH on line 149 (and reiterate this on line 217 and elsewhere). However, on line 151 they use a Shakura-Sunyaev disk model with the inner radius at 3R_S. But of course that model is for a non-rotating, Schwarzschild, BH. Either they should use the ~0.057 efficiency for a Schwarszchild BH or use relativistic accretion disk models including the effects of maximally spinning Kerr BHs.

3) How sensitive are the results to the assumption that the density of cold protons is 0.1 that of the radiating electrons? A discussion of how things change if that ratio increases to 1 would be worthwhile.

4) The authors compare their high-z sample, which is strongly dominated by FSRQs, with the more inclusive sample of Ghisellini et al, dominated by sources with <2.5. They should state the number of sources in the latter sample; they only mention that 10 of them have z>2.5. But they also must say what fraction of the Ghisellini et al sample are FSRQs and what fraction are BLLs. If the fractions are not similar to those in their high-z sample, then the claimed differences may well be due to the difference between FSRQs and BLLs and not to redshift. Hence, these comparisons would be better made only between sources in both samples that are classified as FSRQs. Fig. 3 should have another panel where only FSRQs for both low and high-z samples are compared.

5a) In the text (lines 227-229 and 253-254) the authors do note that many of the nominal differences between the low and high z samples could arise from an obvious selection effect: only the most luminous sources will have sufficient detectable fluxes if they are at high-z. This reviewer strongly suspects that this selection effect is very important. The authors should attempt to estimate the strength of this effect on their conclusions by restricting the low-z sample to sources with luminosities in the same range as the the high-z sample and thus dropping the weaker closer sources.

5b) Unless the authors can show that the selection effects are unimportant, they should be acknowledged in the abstract, following the sentence that ends on line 12. They should also be mentioned in the discussion following the paragraph ending on line 299.

6) A more minor point: some of the values in the tables are quoted to unrealistically high numbers (5 or 6) of significant figures (e.g. in column 7 in Table 2 and in columns 6 and 14 in Tables 3 and 4).

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

Thanks for replying to my previous comments. However, I find that several key issues I raised have not been adequately addressed. I would appreciate more thorough and well-justified explanations and revisions.

1.The authors argues that SSDC SED data are insufficient to constrain the SED, motivating the use of literature peak frequency and peak flux as fixed inputs. This is unconvincing. Even your Figure 1 contains rich multi-band coverage that already constrains the SED shape to first order, and Refs. 42 and 43 also derive SEDs from SSDC. Please reconcile these statements and justify, with evidence, why SSDC is inadequate here while acceptable in those works and why Refs. 42 and 43 with SSDC SED data can provide reliable peak frequency and peak flux.

Conceptually, the synchrotron peak frequency and peak flux are model outputs, not inputs. Treating them as fixed reduces physical transparency and risks circular inference. If you insist on fixing them, you must: (i) explain how they are determined independent of your model; (ii) quantify the induced bias; and (iii) propagate their uncertainties to all downstream quantities.

There is a specific inconsistency: for 4FGL J1345.5+4453, the peak frequency in Table 1 is visibly incompatible with the SED in Figure 1. Please explain the discrepancy, correct whichever element is in error, and clarify the exact role Table 1 peak values play in the modeling (inputs, priors, or merely descriptive). If they serve as priors, report their uncertainties and prior shapes explicitly; if they are outputs, they must not be fixed.

2. Thanks for the private clarification of the black hole mass estimation. However, I believe such explanations should be included in the main text to ensure readers can fully understand and evaluate the information.

3. My previous concern about the potential impact of parameter degeneracy and the treatment of multi-state SEDs on the MCMC results has not been directly addressed. I request a more explicit discussion of these issues.

4. While I appreciate the authors’ effort in providing an online summary of the SEDs, my earlier concern regarding the omission of infrared data remains unanswered. In addition, many of the SED fits appear unacceptable. For instance: in your online materials: in 2.pdf and 6.pdf the synchrotron peak is evidently shifted to the right relative to data; in 5.pdf (right panel) the synchrotron component is even absent. I strongly urge the authors to carefully review and improve the SED fits to ensure reliable and meaningful results.

5. Thank you for the detailed explanation regarding the χ² calculation. However, I believe this information must be included in the manuscript to help readers understand why Table 3 and Table 4 report only the gamma-ray χ² values instead of the full multi-wavelength χ².

6. I understand that the calculation of various powers was not included into the MCMC procedure. Nevertheless, it should be possible to estimate their uncertainties standard methods such as: Linear or logarithmic error propagation from the posterior of primary parameters; draw parameter sets from the fitted posteriors and compute derived powers to obtain credible intervals.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

Thank you for the detailed and on point review. In the current form I do recommend the paper for publication.

Author Response

Thank you for the positive assessment and recommendation.

Reviewer 3 Report

Comments and Suggestions for Authors

The authors have appropriately addressed all of the issues raised in my initial report. Hence, I am pleased to recommend publication of the revised manuscript in the current form.