Expression and significance of MiR-126 and VEGF in proliferative diabetic retinopathy
Authors: L Zhou
X-D Wei
R Liu
L-L Cui
N Li
C-M Liu
Journal: European review for medical and pharmacological sciences (2019)
Discipline: PHARMACOLOGY & TOXICOLOGY
Keywords: miR-126; VEGF; proliferative diabetic retinopathy; vitreous body; plasma
Affiliations: Department of Ophthalmology, Tangshan Worker' Hospital, Tangshan, China. .

Abstract:  Objective: To study the expression and significance of micro ribonucleic acid (miR)-126 and vascular endothelial growth factor (VEGF) in the vitreous body and proliferative membrane tissues of affected eyes and plasma in proliferative diabetic retinopathy (PDR). Patients and methods: A total of 50 PDR patients admitted to our hospital from January 2017 to January 2018 were collected, including 17 cases in stage IV, 20 cases in stage V, and 13 cases in stage VI according to the DR staging criteria. Another 30 patients with an idiopathic macular hole were selected as control group. After admission, the examinations were performed, venous blood was drawn, and vitrectomy was performed, during which the vitreous body and proliferative membrane tissues were taken. The plasma VEGF content was detected via enzyme-linked immunosorbent assay (ELISA). The VEGF protein expression level was detected via Western blotting in vitreous body and proliferative membrane tissues. Moreover, the miR-126 expression was detected via quantitative polymerase chain reaction (qPCR). Results: In the vitreous body tissues, proliferative membrane tissues and plasma, the expression level of miR-126 was significantly lower in control group than that in stage IV, V, and VI groups (p&lt;0.05). The miR-126 expression was significantly lower in stage IV group than that in stage V and VI groups (p&lt;0.05), meanwhile, miR-126 expression was significantly lower in stage V group than that in stage VI group (p&lt;0.05). In the vitreous body tissues, proliferative membrane tissues and plasma, the VEGF mRNA and protein expression levels were significantly higher in control group than those in stage IV, V, and VI groups (p&lt;0.05). The VEGF expressions were significantly higher in stage IV group than those in stage V and VI groups (p&lt;0.05). In addition, VEGF expressions were significantly higher in stage V group than those in stage VI group (p&lt;0.05). Furthermore, the VEGF expression level was negatively correlated with the miR-126 expression level. Conclusions: We found that the abnormally high expression of miR-126 negatively regulates VEGF, which may be one of the important mechanisms of occurrence of PDR. The miR-126 and VEGF content can serve as important predictors for the condition of PDR. 

Retracted: No

PubPeer comments:
 The authors argue that there is an association between the local SARS-CoV-2 daily test positivity rate and the daily PM2.1 measure of air quality, during a series of wildfire events between 15 May and 20 October, 2021, in the Reno-Sparks, Nevada, metropolitan area. Their reasoning includes a case for the scientific plausibility of a causal relationship, but the main argument is based on a time-series analysis ot the data, which successfully shows that the data is consistent with their hypothesis. The authors conclude that their findings  should help shape regional policies that seek to manage the combined threats of wildfires and the pandemic. I argue that this last claim has not yet been justified, as three key methodological weaknesses of their study remain unaddressed. *Data limitations*. The authors use test positive counts, and totals of tests administered, from Renown Health s testing laboratories, which they concede are responsible for just 25% of the confirmed positive cases in Washoe County. Their PM2.5 air quality data are calculated based on a weighted average of data from four monitoring stations,  with the weights proportional to the count of Renown patients living within five kilometers of each monitor. These data do not by any means constitute a random sample of the population in the Reno-Sparks area; rather they are a highly systematic sample (complete data from a single testing organization) whose ability to represent the full population is potentially biased. This potential bias affects not only the response variable, but (through the weighted average described) the principal covariate of interest. *Estimating excess cases*. The authors empirical analysis rests on their ability to estimate a counterfactual - what would the PM2.5 data have been if there had not been wildfire events during a subset of their time period of interest, 16 August to 10 October, 2021? They assume, perhaps reasonably, that  the 7-day average of PM2.5 would have remained at the average level of the same period in 2019, when no major wildfire smoke events occurred. Their subsequent analysis leans heavily on this unverified, and unverfiable assumption. To the authors credit, they dislose many of their choices in both managing the data and model design, and they even subjected some (though not all) of their assumptions to sensitivity analyses, by fitting models that varied those assumptions. However, the pivotal assumption about the counterfactual was *not* subject to a sensitivity analysis, and it was carried over to all the candidate models they fitted. The authors did not even report a comparison of the PM2.5 data between 2019 and 2020 during the non-wildfire months. The authorsu2019 entire empirical argument depends on the leap of faith required by their assumption about the counterfactual. *Model validation*. As good statistical modelers, the authors were careful to use residual analysis to assess the quality of model fits. They fit many models to the same data set, retaining only those with reasonable residual characteristics. This is sound statistical practice for exploratory research, but their resulting statistical inferences (model parameter estimates with confidence intervals) have no validity, due to the well known issue of model selection bias (eg, Freedman, 1983; Hjorth, 1989; Chatfield, 1995; Simmons, et al. 2011). Simply put, the heavy reuse of the u201ctraining data allows the analyst to improve model fit, but with little protection from, nor ability to assess, overfitting and lack of generalizability. Moreover, the flexibility in the choice of models entertained, even if other conceivable models were not considered, creates a  garden of forking paths that undermines the validity of the resulting statistical inferences (Gelman Loken, 2014). Fortunately, the first problem I described suggests a solution to this last one. Best practices in reproducible research require *model validation* using data not seen by the analyst during the model building model criticism model selection process. This principle is widely used in the machine learning community (eg, Webb, 2002), the Genome Wide Association Studies community (eg, Lin, 2020), and the regulated human clinical trials arena (ICH E8, 1997), where the distinction between exploratory and confirmatory phases has a legacy of nearly 60 years. As Freedman (1991) observed, u201cGenerally, replication and prediction of new results provide a harsher and more useful validating regime than statistical testing of many models on one data set. Fewer assumptions are needed, there is less chance of artifact, more kinds of variation can be explored, and alternative explanations can be ruled out.u201d In this case, the model(s) trained on the Renown data could be evaluated on test positivity data from the other Washoe County testing laboratories. (County-wide data are publicly available, and could be adjusted by subtracting the Renown data.) The evaluation should have two components: (1) does the (now) pre-specified model developed from the Renown data provide similar goodness-of-fit properties on the non-Renown data, when fit to it, and (2) if so, are the resulting model parameter estimates (and their confidence intervals) consistent with the authorsu2019 current findings? This simple step of model validation would have made the authors arguments more compelling if it had been done. *References* Chatfield C. Model uncertainty, data mining and statistical inference. *Journal of the Royal Statistical Society*, series A. 1995; 158:419-466. Freedman D. A note on screening regression equations. *The American Statistician*. 1983; 37:152-155. Freedman D. Statistical models and shoe leather. *Sociological Methodology*. 1991; 21: 291-313. Gelman A, Loken E. The statistical crisis in science. *American Scientist*. 2014; 102:460-465. Hjorth U. On model selection in the computer age. *Journal of Statistical Planning and Inference*. 1989; 23:101-115. International Conference on Harmonisation of Technical Requirements for Registration of Pharmaceuticals for Human Use. *ICH Harmonised Tripartite Guidelines: General Considerations for Clinical Trials*, E8. 1997. Lin X. Learning lessons on reproducibility and replicability in large scale genome-wide association studies. *Harvard Data Science Review*. 2020; 2.4. Simmons JP, Nelson LD, Simonsohn U. False-positive psychology: undisclosed flexibility in data collection and analysis allows presenting anything as significant. *Psychological Science*. 2011; 22:1359-1366. Webb A. *Statistical Pattern Recognition*. 2nd ed. John Wiley Sons, Hoboken, NJ, 2002. Disclaimer: I write solely in my personal capacity. The views expressed do not necessarily represent the policies, views, or opinions of any institution with which I am affiliated. , 
 Christopher, Thank you for your insightful and valuable comments. We very much appreciate your constructive criticism, and what follows is our best attempt to respond to each of your points. *Data limitations* Your first point regarding the limitations of our data is well placed. We examined a patient population, and not the whole population of Reno-Sparks. While Renown Health serves a large proportion of the Reno-Sparks population, we would expect there to be some differences between their patient population and the population at large. For example, it is possible that the prevalence of conditions that may make people more sensitive to wildfire smoke would be higher among Renown patients than people who are not Renown patients. How this might influence the association between PM2.5 and the rate of positive COVID-19 cases is unknown, which is exactly your point. This is not a limitation that our group would have been able to overcome using publicly available county data, for reasons that we will address in regards to your third point. But you are certainly correct that we would have done well to address this limitation more directly in our discussion and to emphasize its effect on the interpretation of our results. Our results are best framed as: u201cfor an important **subset** of the population in Washoe County, NV, we observed an association between the COVID-19 positivity rate and PM2.5.u201d Thank you for emphasizing this, and we will in turn be careful to emphasize this in our conversations with scientific and non-scientific audiences. While in no way reducing the importance of your point, we would like to make a few counterpoints that we feel are also important: (1) The observation of a 17.7% increase in cases among a patient population would be no less alarming if this result ultimately failed to generalize to the broader population who were not patients. There would still be an urgent need for taking precautions during wildfire smoke events. Thus, we argue that our claim that our results u201cshould help shape regional policiesu201d is still very much justified, even if those policies might ultimately be modified as more information about susceptible populations becomes available. (2) Our sample population does represent a very large segment of the Reno-Sparks population: nearly 36,000 patients were tested for COVID-19 during our study period. This number is equivalent to 7.5% of the Washoe County population, where Reno-Sparks is located. While the size of the sample does nothing to correct for potential biases, it does serve to emphasize the breadth of Renown Health s service in the community. Furthermore, this population was diverse (in terms of age and gender, though perhaps not so much in terms of race). So despite any biases that may have been introduced by limiting ourselves to COVID-19 testing at Renown, our results would still be directly applicable to a broad swathe of the population. (3) There is good reason to think that our finding of an association between PM2.5 and COVID-19 cases does generalize to the broader population, based on associations found between air pollution and COVID-19 cases in other studies which looked at other populations. Thus, we argue that the primary question has to do with whether the magnitude of the association we found is generalizable, not whether an association itself is generalizable. While the magnitude of an association obviously has important implications, we believe that this is an important distinction to mention. (4) At some level, the limitation you are describing is inherent to any observational study. The Reno-Sparks population is itself a non-random sample of humanity, with cultural and demographic differences that set it apart from any other metropolitan area, and with a wildfire smoke exposure that was uniquely severe and prolonged. While we could have better emphasized that our focus was on a patient population, with its unique qualities, we have already emphasized the need for caution in generalizing our results to other populations across the world. As always in public health, our study should be considered to be one piece of evidence among a greater body of work. *Estimating excess cases* As we understand your second point, you are concerned about the dependence of our results regarding excess cases on our use of PM2.5 levels from 2019 as a counterfactual scenario, which you describe as an u201cunverifiable assumption.u201d It is true that our key result, a 17.7% increase in cases, is highly dependent on our choice of a counterfactual scenario. However, we believe that it is a mischaracterization to describe our choice of a counterfactual scenario as a u201cleap of faith.u201d The intention was not to compare actual COVID-19 cases with cases during a hypothetically less severe 2020 wildfire smoke season, but to report the difference in cases predicted by our model if we removed the wildfire smoke events from the data. This is not as straightforward as it may seem, because not all PM2.5 in Reno-Sparks comes from wildfires. Some PM2.5 comes from vehicle traffic and industry. Thus, there was a need to establish a reasonable baseline of u201cbackgroundu201d PM2.5. Since the Reno-Sparks metropolitan area is frequently subjected to wildfire smoke during the Aug-Oct time period we were examining, we concluded that determining the baseline using all recent years of PM2.5 data would yield an inflated baseline that would result in an underestimation of excess cases attributable to wildfire smoke. For instance, we observed concentrations of PM2.5 in excess of 50 ug m3 in July 2018, when there was another major wildfire smoke event. In contrast, levels of PM2.5 (aggregated between all monitors) between 16 Aug and 10 Oct 2019 never exceeded 9 ug m3, with an average concentration of 4.5 ug m3. Since levels of PM2.5 generated by vehicle traffic or industry in Reno-Sparks were not expected to meaningfully vary from year to year, PM2.5 data from 2019 seemed to be the most reasonable data from which to construct a baseline. It is possible that even in 2019 there was some PM2.5 from wildfire smoke in the air, which would make our baseline a little too high and thus cause us to slightly underestimate the size of the effect we observed in 2020. Thus, while debate is possible regarding how to estimate a reasonable baseline for PM2.5, our method was hardly a u201cleap of faith.u201d With regards to conducting sensitivity analyses using different PM2.5 baselines, those sensitivity analyses would not be particularly valuable if we thought that other possible PM2.5 baselines were unreasonable (which we did). We admit that we are not sure why a comparison of PM2.5 levels during the non-wildfire months of 2019 and 2020 would be beneficial, and so we would certainly welcome further clarification on that point. *Model validation* With regards to your third point, we very much appreciate the concerns you raise about the dangers of using a plurality of models, and how that can lead to overfitting. This was why we made a distinction between our initial six models investigating the association between PM2.5 and COVID-19 cases and subsequent models that were intended to better elucidate the nature of the lag effects, which could correctly be labeled u201cexploratoryu201d models. This was described in the 7th paragraph of our methods. It was also why we used the 7-day average PM2.5 model to calculate excess cases, which u201cwas chosen because the lags were selected a priori and it was more parsimonious than the distributed lag modelsu201d (9th paragraph of methods). This was not a model that we endlessly tweaked, but rather one of the original models that we had used to test for an association. Thus, we tried very hard to avoid the u201cgarden of forking pathsu201d you described. Regarding another element of your third point, about validating models on a data set that is separate from our training data set, we risk getting a little out of our depth in our response. However, there are a few counterpoints that we would like to make: (1) The first counterpoint (which I believe you recognized) is that we could not feasibly divide the data from the hospital into test and training data sets, since both the surges of PM2.5 and test positivity were of limited duration. (2) The second counterpoint has to do with your suggestion that publicly available data from Washoe County could have been used as a test data set. In the initial stages of our analysis, we did examine data from Washoe County. However, we determined that it was not the best data for our purposes, because of uncertainty about when SARS-CoV-2 tests were collected. Not only might there be delays of a few days in returning the results, but there might also be delays in reporting the results to the county. Given the importance of finding the correct lag specification, we had greater confidence in the data we received directly from the hospital, which included sample collection dates. In short, the data we received from the hospital and the publicly available data from the county are not as similar as they superficially appear. However, your overall point about the importance of model validation on new data is indisputable, and we certainly agree that it would make our findings more compelling. While we may have lacked the ability to test our models on new data, we hope that other researchers will find it worthwhile to seek to replicate our results and those of other authors who have found similar associations. And it may be that if the 2021 wildfire season is as bad as the 2020 wildfire season, we will have the (unfortunate) opportunity to test the validity of our models this fall. Even so, it may not be ideal circumstances for testing model validity, as there are major reasons to think that this season might look different from last season: a large proportion of the population is now vaccinated, and there are new COVID-19 variants that are much more infectious. Such are the pitfalls of observational science in general. *A few other points* We are big believers in checking model diagnostics and in following best practices to avoid overfitting the data. These steps are absolutely necessary if the results of any study are to be trusted. However, we also find it valuable to take a step back and visualize the raw data, to ensure that relatively complex modeling techniques are not manufacturing a signal where none exists. This is not always possible, but in our case we are fortunate because time-series data is easy to visualize. In Figure 2 of our paper, we plot the seven-day average of PM2.5 against the seven-day average of the SARS-CoV-2 test positivity rate, and surges in the test positivity rate appear to follow surges in the PM2.5. This observation is clearly subjective and does not substitute for rigorous modeling practices, but it is one factor that gives us increased confidence in the effect sizes reported by our models. We would also argue that another strength of our study is that we did not begin by hunting for random associations. Clearly, if enough associations are tested between enough variables, a small fraction of them will be statistically significant just by chance. Instead, our study was motivated by an editorial published by Sarah Henderson in the American Journal of Public Health arguing that a moderate wildfire smoke event could increase the severity of the COVID-19 pandemic in the affected area by approximately 10% [1]. A prediction was made, and we in turn attempted to test that prediction. Thus we limited the possibility that the association we observed was due to random chance. We are well aware that neither our study nor our response to your comments have been perfect or represents the last word, and we hope for further research and dialogue about this pressing issue. We apologize if we have misunderstood or failed to address any of your concerns. Thank you for your thoughtful consideration and healthy criticism of our work, and for taking the time to make this dialogue possible. 1. Henderson SB. The COVID-19 pandemic and wildfire smoke: potentially concomitant disasters. Am J Public Health. 2020;110:1140u20132.u00a0https: doi.org 10.2105 AJPH.2020.305744. , 
 I am very grateful that the authors have promptly entertained u201cpost-publication peer reviewu201d of their work in this open forum, and have provided helpful clarifications here. Equally valuable is their choice to make their original paper open access, without which this level of scrutiny would be impossible. In the spirit of constructive dialog, I offer the following response. *Data limitations*. The authors now provide their rationale for not using the publicly available county-level data. Essentially, the county-level data collection was never intended to support fine-detailed time series analysis, and individual case-reporting delays were undocumented. I agree that this issue effectively rules out my suggestion for using such data for the authorsu2019 model validation. One minor suggestion could still be considered: the same subjective graphical comparison they describe (u201cA few other pointsu201d, first paragraph) between test positivity data and PM2.5 could also be offered for the county-level data, as a crude check for consistency between the two data sets, with the stated caveat. With regard to the authorsu2019 counterpoint (3) under Data Limitations, I do not currently have access to the Copat et al. (2020) systematic review cited in their paper, but its abstract states that u201cthe cases included in the reviewed studies cannot be considered conclusiveu201d and that u201cmore studies are needed to strengthen scientific evidences and support firm conclusionsu201d. The authorsu2019 work is a valuable incremental addition to the further studies called for by Copat et al. (2020). Comparison with other studies, as well as testing the Henderson (2020) prediction, are in the proper spirit of the iterative learning cycle of science (Ehrenberg Bound, 1993; Box, 2001). Beware though that mutually reinforcing consistency could sometimes be the result of self-fulfilling group-think (u201cconfirmation biasu201d) committed by sincere investigators acting in good faith. A case study of the latter, involving the far more rigorous arena of designed experiments, is discussed by Cartlidge (2021). Open dialogue with members of the wider scholarly community, such as that facilitated by PubPeer, may help to mitigate such effects. Again, the authorsu2019 willingness to engage with non-experts here is praiseworthy. *Estimating excess cases*. The authors now provide their rationale for choosing a counterfactual u201cbaselineu201d for PM2.5 data. I originally used the term u201cleap of faithu201d because in the original paper their reasoning was very opaque; with the clarification presented here, I stand corrected. With regard to comparing PM2.5 during the non-wildfire months of 2019 and 2020, I made this suggestion in anticipation of the authorsu2019 remark here that u201clevels of PM2.5 generated by vehicle traffic or industry in Reno-Sparks were not expected to vary from year to yearu201d. Data from non-wildfire months could be compared to crudely verify this expectation. The assumed counterfactual plays a pivotal role in the authorsu2019 modeling, but they dismiss sensitivity analyses for it because the competing baselines they considered u201cwere unreasonableu201d. I will propose some naive possibilities that vary from those discarded by the authors. The counterfactual used by the authors appears to be a constant value, call it *C*, equal to u201cthe average level of the same period in 2019, when no major wildfire smoke events occurredu201d. Suppose that during that period, the 2019 PM2.5 also varied around this average by (say) + - 5%. As sensitivity analyses, the authors could adjust the assumed *C* upward and downward by 5% to bracket u201cbestu201d and u201cworstu201d case scenarios, or more realistically, they could augment *C* with quasirandom noise mimicking the PM2.5u2019s variance and autocorrelation properties from 2019 and other comparable years. Alternatively, other values of *C* could be estimated from other recent years with minimal wildfire events during the period of interest (excluding, e.g., the July 2018 smoke event). I would be interested in learning of the flaws in my suggestions. *Model validation*. I agree that it was clear from the original paper that the authors voluntarily refrained from certain aspects of model design flexibility, and were testing a pre-specified prediction rather than conducting a search for u201canything significantu201d. By doing so, the authors exhibited good habits that are not always followed in the literature. Nonetheless, a point made by Gelman Loken (2014) that goes well beyond the other references I cited above, is that u201cit is possible to have multiple potential comparisons (that is, a data analysis whose details are highly contingent on data, invalidating published *p*-values) without the researcher performing any conscious procedure of fishing through the data or explicitly examining multiple comparisons.u201d The fact that scientifically plausible routes exist in the garden of forking paths, even if they are never actually taken, creates u201cinvisible multiplicityu201d with regard to the reported statistical inferences. This is an incredibly subtle point that readers should best evaluate from Gelman Lokenu2019s paper (see also Gunter Tong, 2017). Gelman Loken and Gunter Tong acknowledge that for unique, non-replicable situations, like the 2020 Reno wildfire season, this limitation is difficult to surmount. Policy-makers will simply need to consider the inherent, irreducible, and not fully quantifiable uncertainty that attends conclusions derived from modeling such data. *Additional References* Box G. Statistics for discovery. *Journal of Applied Statistics*. 2001; 28:285-299. Cartlidge, E. Solving the proton puzzle. *Physics World*. 2021; [Solving the proton puzzle.] Copat C, Cristaldi A, Fiore M, Grasso A, Zuccarello P, Signorelli SS, et al. The role of air pollution (PM and NO2) in COVID-19 spread and lethality: a systematic review. *Environ Res.* 2020;191:110129 Gunter B, Tong C. What are the odds!? The u2018airport fallacyu2019 and statistical inference. *Signficance*. 2017; 14(4): 38-41. [DOI] Ehrenberg ASC, Bound JA. Predictability and prediction. *Journal of the Royal Statistical Society*, series A. 1993; 156:167-206. Disclaimer: I write solely in my personal capacity. The views expressed do not necessarily represent the policies, views, or opinions of any institution with which I am affiliated. , 
 Christopher, Thanks again for taking the time to dialogue about this. It is gratifying to have our work treated seriously by thoughtful peers. Here are some additional responses to your most recent comments: *Data limitations* It has been awhile since we conducted the analysis, but we did make the visual comparisons you suggested using the county data. When we did so, an association could perhaps be imagined between PM2.5 and cases across the county, but it was not as clear as it was in the data for the hospital. Perhaps this could be taken as evidence that our results don t generalize, but because of the reasons mentioned previously (concerns about the delay between sample collection and reporting to the county) we decided that we trusted the hospital data more. With regards to your second comment under Data limitations, u201cself-fulfilling group-thinku201d is truly a scary thing to consider. Certainly we are aware of the phenomenon where studies that report statistically significant results are more likely to be published than studies that report null results, which could perhaps contribute to the confirmation bias you mention. We have no way of knowing how many other research groups might have looked for an association between PM2.5 and COVID-19 but decided not to publish because they didn t find anything. If this is happening frequently with regards to this research question, that would clearly be cause for concern about the generalizability of our results. *Estimating excess cases* It was unfair of us to imply that no other reasonable PM2.5 baselines existed, as your examples certainly prove the contrary. Given how important the determination of the baseline was to our final result, it would have been wise for us to have experimented with alternative methods, if only to see how much difference the alternative baselines made to our results (i.e., perform sensitivity analyses, per your original argument). If you had been one of our reviewers, we would have happily done so. Alas, it was not something we considered. However, we would make two points in response: (1) We have a strong suspicion that alternative methods of determining the baseline PM2.5 would not meaningfully change the results, because of the huge difference between concentrations of PM2.5 during wildfire smoke events and any reasonable baseline. For example, changing the baseline from 4.5 ug m3 to 7.5 ug m3 on a day when PM2.5 is 50 ug m3 would change our estimate of the wildfire PM2.5 concentration from 45.5 to 42.5 ug m3. This is a change of only 6.6% in our estimate of the wildfire PM2.5 concentration after changing our baseline PM2.5 by 66.7%. Thus, it seems like our baseline would have to be way off before we would expect our conclusions to be meaningfully different. This in no way negates your suggestion, though, and it would have been an easy thing to check. (2) One advantage of our method in comparison with the methods you suggested is that it is simple. While simplicity does not guarantee accuracy, it does seem like a worthwhile default option until its accuracy is called into serious doubt. **Update: **Upon writing the above, I realized that it would indeed be so easy for me to check the influence of our selected baseline that it would be almost dishonest for me not to. Hence, I recalculated what our estimates of excess cases would have been if we had changed our baseline by + - 3 ug m3, which would represent a substantial percent change (66.7%). Here is a summary of all of the results: (1) Original baseline of 4.5 ug m3: 17.7% (95% CI: 14.4-20.1%) increase in cases (2) Lower baseline of 1.5 ug m3: 19.9% (95% CI: 16.5-22.4%) increase in cases (3) Higher baseline of 7.5 ug m3: 15.6% (95% CI: 12.5-17.9%) increase in cases While there are clearly differences in the numbers (roughly an absolute difference of 2%), the differences don t seem particularly concerning to me, as they would not meaningfully alter our conclusions. While I did not make an effort to implement your more complex suggestions (sorry), this little exercise gives me additional confidence that our conclusions are robust to the chosen baseline. *Model validation* With regards to your comments here, I have now read Gunter Tong, 2017 and Gelman Loken, 2014 and found both articles to be illuminating. The overall takeaway seems to be that researchers in fields such as our own, where new data is difficult to come by, need to be especially cautious and humble in how they present their conclusions. We certainly will make a greater effort to consider any ways we can make our modeling choices less dependent on the data and to look for opportunities to replicate our results on new data. It appears that the 2021 wildfire season may provide such data, though the opportunity may be limited due to the caveats mentioned earlier about the presence of the vaccine and new COVID-19 variants. Thank you again for taking the time to discuss our work. Your insight and ideas have been much appreciated. , 
 The authors have now provided a set of sensitivity analyses of their counterfactual assumption, varying the assumed PM2.5 by + - 3 ug m^3. Though we are not told whether this is reflective of actual variation in the 2019 PM2.5 data, it provides much insight into the insensitivity of the model findings to a substantial change in the assumed counterfactual. I am grateful for their continued efforts to clarify their research. In the remainder of this note, I will return to an argument the authors made in their first reply: u201cThere is good reason to think that our finding of an association between PM2.5 and COVID-19 cases does generalize to the broader population, based on associations found between air pollution and COVID-19 cases in other studies which looked at other populations.u201d Thus, to what extent do the authorsu2019 findings corroborate others in the literature? I have now been able to access the Copat et al. (2020) systematic review paper that they cited. Unfortunately the findings, represented in Table 1 of that paper, are seemingly inconsistent in both methodology and results. Many of the analyses reported there are surprisingly simplistic, estimating either simple correlation coefficients between number of cases and PM2.5, or performing crude regression modeling that, as far as I can tell, treats daily data as if independent, with no regard to the dependent, time series structure of the data. The resulting estimated correlations, coefficients of variation, or relative risks are often surprisingly low; and in some cases the correlation