Also, the benefit of the research for the subjects of research has not been mentioned either directly or indirectly. It is very important that the research should aim at comforting the subjects so that they cooperate happily in the research process. Here, 1/3 of the OAT therapy patients declined to cooperate fully in the research. "Trauma and PTSD data were collected in 2/3 of the patients screened for Depression and Anxiety, and the other 1/3 refused to fill in the LEC-5 and PCL-5 screeners. Therefore, it is impossible to make reliable conclusions on PTSD prevalence." Counselling, other psychosocial supports such as breathing exercises, etc., could have persuaded the 1/3  subjects to fill in the screeners. Nothing has been mentioned to the effect that efforts were made to persuade the 1/3 of the patients. Of course, the patients' cooperation had to be voluntary, but little counselling could have made them understand that the screener survey was for their benefit, as it would decide the medicines and terminir dosage for these 1/3 patients.

In the revised manuscript, we have added a clarification that all participants were informed of the study’s purpose, including its potential to inform service improvements and individualised care. All participants could receive on-site psychological support after the data collection.

However, due to the limited resources at the time of data collection, structured counselling or relaxation techniques were not feasible prior to screener administration.

Also, there are no specific recommendations made in the paper. The conclusion is very general. Specific recommendations are lacking.

We appreciate the reviewer’s observation and agree that actionable recommendations are essential to enhance the utility of our findings. In response, we have revised the conclusion section to include specific, context-sensitive recommendations for both clinical practice and policy development.

These include:

Integrating routine mental health screening (e.g., PHQ-4, LEC-5, PCL-5) into OAT programmes, especially during periods of heightened stress such as armed conflict.

Training OAT staff in trauma-informed care, including brief psychosocial interventions to improve patient engagement and reduce screener refusal rates.

Establishing referral pathways for patients with elevated symptoms of depression, anxiety, or PTSD to receive timely psychological support.

Advocating for policy-level support to ensure mental health resources are embedded within addiction treatment services, particularly in conflict-affected regions.

These recommendations are now reflected in the revised conclusion, and we hope they will support both immediate service improvements and longer-term system strengthening.

Dosage variation due to heightened stress of war is not recommended when it is categorically mentioned that "A significant deterioration in the mental health of OAT patients in Ukraine during the second year of the full-scale Russian invasion" was found.

We thank the reviewer for raising this important concern. We agree that dosage adjustments in opioid agonist treatment (OAT) must be approached with caution, particularly in contexts of psychological distress and systemic instability.

In our manuscript, we do not advocate for dosage variation as a direct response to mental health deterioration. Rather, we analys the data on the correclation between the dosage satisfaction and psychological wellbeing of the patients.  

The absence of any change in suicidal ideation is interesting. Some additional authorities could be added to explain that generally, suicide ideation does not increase during wartime, rather it increases in the post-war phases.

We thank the reviewer for this thoughtful observation. We agree that the stability in suicidal ideation rates, despite elevated symptoms of depression and anxiety, is noteworthy and merits further contextualization.

In response, we have expanded the discussion section to include references to literature suggesting that suicidal ideation may not peak during active conflict.

There is a discrepancy in the reported gender distribution. The body of the article states: “Among study participants (95 males and 889 females),” while Tables 1–3 show the opposite: 95 females and 889 males. This inconsistency should be corrected to ensure clarity and accuracy.

We thank the reviewer for this observation, it is corrected now: 95 females and 889 males.

While the study is robust, it would benefit from the inclusion of additional demographic and clinical characteristics commonly reported in similar research. For example, age, marital status, employment status, duration in treatment, mean percentage of opioid-positive drug screens, total number of opioid screens prior to and during study enrollment.

These variables are routinely included in comparable studies, such as:

Rosic et al. (2025), PLOS ONE, https://doi.org/10.1371/journal.pone.0314296

Yang et al. (2025), Pain Medicine, https://doi.org/10.1093/pm/pnaf011

Including these would enhance the study’s comparability and depth.

The inclusion of additional demographic and clinical characteristics would definitely benefit the study; however, the article presented all characteristics that were collected during the second study. During the first study, the set of collected characteristics was even lower due to certain organisational limitations in the study process.

The central inference hinges on comparing two independent clinic cohorts. Comparability of the two cohorts is currently under-reported and needs to be shown. Because the pre-war sample (Kyiv/Lviv/Sumy) differs in composition from the wartime sample (Vinnytsia/Lviv/Sumy), readers need to see whether cross-cohort differences reflect true changes or simply different case-mix. The article would benefit from adding two concise descriptive tables, one for each cohort, reporting, at a minimum, gender, age, city, and OAT medication (methadone/buprenorphine/buvidal), with n/N shown for each stratum. Alongside those tables, acknowledge explicitly that Kyiv was replaced by Vinnytsia in the wartime wave. If possible, include a brief sensitivity check restricting pre/post comparisons to the overlapping sites (Lviv and Sumy); if re-analysis is not feasible, a clear caveat in Results and Limitations about the site swap and possible influence of confounders that was not tested is sufficient.

We thank the reviewer for this important methodological observation. We agree that the comparability of the pre-war and wartime cohorts is essential to interpreting observed differences in mental health outcomes.

We have also explicitly acknowledged that Kyiv was replaced by Vinnytsia in the wartime wave due to logistical constraints. While a full sensitivity re-analysis restricted to Lviv and Sumy was not feasible given the original data structure, we have added a clear caveat in the Limitations sections noting that site composition may have influenced observed differences.

The pre/post analyses themselves are currently unadjusted (Mann–Whitney U for severity; χ² for prevalence), and therefore they compare the two time periods without controlling for things that also differed between periods (site mix: Kyiv vs Vinnytsia; season/month of data collection (pre-war (Oct–Jan) vs war-year-2 (Apr–Oct)) invites seasonal effects on mood/anxiety; gender proportions; medication mix). If those factors relate to the outcomes, they can confound the pre-/post-contrast. Reasonable confounders should be mentioned in the Discussion and the Limitations sections. Reporting effect sizes with 95% CIs throughout the article and interpreting the results as associations rather than causal effects is necessary. If the authors can add one lightweight robustness model (e.g., a site-adjusted logistic regression for the primary prevalence outcomes (pre vs during + site as a covariate), that would further strengthen confidence without expanding the paper.

We thank the reviewer for this rigorous and constructive feedback. We agree that unadjusted comparisons may be influenced by contextual and demographic differences between the pre-war and wartime cohorts. In response, we now explicitly discuss key potential confounders, including site composition (Kyiv vs Vinnytsia), season/month of data collection (Oct–Jan vs Apr–Oct), gender proportions, and medication mix, in Limitations sections. We have revised the language throughout the manuscript to interpret findings as associations rather than causal effects, in line with the observational design.

In the Participants section (in the Methods section, not the Results), reporting sample sizes for each cohort and providing a brief description of each sample (sites, gender distribution, age, and OAT medication mix) is highly desirable.

The inclusion of additional demographic and clinical characteristics would definitely benefit the study; however, the article presented all characteristics that were collected during the second study. During the first study, the set of collected characteristics was even lower due to certain organisational limitations in the study process.

The manuscript should also explicitly state that informed consent was obtained.

The “Informed consent was obtained from all participants.” was added to the to the “Pariticipants” section.

Moreover, because screening was interviewer-administered by clinic staff, noting in the Limitations the risks of social desirability and interviewer bias, especially potential underreporting of suicidal ideation, and briefly describing privacy safeguards (private setting, standardized script, and whether a self-administration option was offered) is highly recommended.

Thank you for this notion, the relevant part was added to the Limitation section.

Finally, nonresponse on trauma/PTSD is substantial and likely informative (376 refused LEC-5; only 608 completed LEC-5, and 549 trauma-exposed completed PCL-5), so PTSD prevalence is plausibly underestimated (people with the highest trauma may refuse).

Thank you for this notion, the relevant part was added to the Limitation section.

Furthermore, the manuscript would benefit from a brief Methods subsection describing each measurement scale (PHQ-9, GAD-7, PCL-5 with LEC-5 anchoring, and PHQ-9 item 9 for suicidal ideation; number of items used in the current study) and reporting summary statistics for each cohort; as well as a succinct Data Analytics section explaining the rationale for each analysis choice.

We thank the reviewer for this thoughtful recommendation. While we agree that detailed descriptions of instruments and analytic rationale can enhance transparency, we respectfully believe that the current manuscript structure sufficiently addresses these elements within the constraints of journal length and scope.

Specifically, each instrument is referenced with its full name and citation, and the number of items used is standard across validated formats. Summary statistics for each cohort are already reported in the Results section and accompanying tables. Additionally, the rationale for analytic choices (e.g., Mann–Whitney U for non-parametric severity comparisons, χ² for prevalence contrasts) is briefly noted in the Methods and further contextualized in the Discussion and Limitations sections.

To maintain clarity and conciseness, we have opted not to expand these sections further. However, we have reviewed the manuscript to ensure that all analytic decisions and measurement tools are clearly described and appropriately cited.

Medication group contrasts (higher suicidal ideation/PTSD among buprenorphine vs methadone recipients) are valuable but potentially influenced by confounders. Framing these as exploratory and presenting minimal adjusted comparisons (medication + age + gender + site) with adjusted odds ratios and CIs, ideally in a compact supplement, would temper inference.

We thank the reviewer for highlighting the potential influence of confounders in medication group contrasts. We agree that these findings should be interpreted with caution and have now explicitly framed them as exploratory in the revised manuscript.

While we recognize the value of adjusted comparisons, we respectfully note that the sample size and data structure do not support robust multivariable modeling without risking overfitting or unstable estimates. Given the observational design and limited statistical power for subgroup analysis, we have opted not to include adjusted odds ratios or a supplemental model at this stage.

Clinical relevance warrants explicit comment where statistically significant differences are small. For example, the PHQ-9 mean increase from 7.42 to 7.90 is modest; reporting the standardized mean difference and noting that the absolute change appears below typical minimal clinically important difference thresholds would help avoid over-interpretation of p-values.

Thank you for this notion, the relevant notion was added to the Results section.

Several small inconsistencies are present, which I believe are typos, but should be fixed. Sex counts are reversed in text (it says “95 males, 889 females”; tables indicate 95 females, 889 males) and the methadone totals (764 in tables vs 746 elsewhere).

Thank you, corrected 