Science and Technology Resource Allocation, Spatial Association, and Regional Innovation
Round 1
Reviewer 1 Report
The Author(s) have conducted a sound background research and investigated the relevant literature (especially about China). The idea of regressing innovative output against a set of (more or less) policy-controlled variables is appealing.
My main concerns are related to the research design:
1) The Author(s) mention that the two main models in the practice of spatial econometric analysis are: SLM and SEM. There is a fundamental interpretational difference between them. If one concludes that SLM reflects the true data generating process, one can speak of spatial interactions within the dependent variable. Conversely, if SEM is the one, it's not about spatial interactions, but most likely a missing, spatially autocorrelated variable. While it's hard in practice to distinguish between the two, there are some tools to do that: LM test, AIC comparison, inspection of spatial autocorrelation of residuals, etc. The Author(s) should provide evidence that their data indeed speaks for SLM specification (as reported) and against SEM (unreported), since the conclusions that are drawn largely hinge upon identifying SLM as a true model.
2) The model is static. I don't think it's very likely that any policy effort towards innovation brings the result on impact. Lags in explanatory variables should be considered.
3) Table 2 reports "OLS results". Not sure what is meant here: a "pooled" panel regression (without any individual effects) or the LSDV/FE regression (in fact estimated with OLS). If the former is the case, that is not a good reference point for future FE/RE spatial models. In other words, I can't agree with the statement in line 405 that before running SLM, one needs to decide whether FE or RE; in fact, this should be done earlier, even before the initial non-spatial model. Otherwise the two dimensions get mixed up in the comparison.
4) "Local spatial correlation analysis" (line 366) is not a good header because, in the language of spatial econometrics, it invokes the notion of Anselin's (1995) LISAs - Local Indicators of Spatial Association. What is investigated here is the Moran's plot. I don't mean here that this investigation is a bad thing - in fact, it's useful - nor that LISA should be run. I just mean that this part of analysis should be re-labelled.
Some other comments:
5) Line 252: are innovation output levels of provinces really measured by ArcGIS?! There's something wrong with this statement - either grammatically, or logically. Please reconsider.
6) Equation (4) comes without any introduction.
7) Part of the text between equations (1) and (3) appears in red.
8) There's a double dot in line 61.
Author Response
First of all, thank you for your valuable comments on this manuscript. We have carefully revised it based on your comments. We have revised them one by one based on your comments and marked them with a yellow background in the manuscript.
Point 1: The Author(s) mention that the two main models in the practice of spatial econometric analysis are: SLM and SEM. There is a fundamental interpretational difference between them. If one concludes that SLM reflects the true data generating process, one can speak of spatial interactions within the dependent variable. Conversely, if SEM is the one, it's not about spatial interactions, but most likely a missing, spatially autocorrelated variable. While it's hard in practice to distinguish between the two, there are some tools to do that: LM test, AIC comparison, inspection of spatial autocorrelation of residuals, etc. The Author(s) should provide evidence that their data indeed speaks for SLM specification (as reported) and against SEM (unreported), since the conclusions that are drawn largely hinge upon identifying SLM as a true model.
Response 1: I'm sorry, it may not be clear enough in the manuscript. In fact, in Table 2 (Table 3 now), I have reported that the SLM model was selected based on the LM test results. Comparing the Lagrange multiplier in the Table, it can be seen that the R-LM (lag) level of SLM model is significantly higher than the R-LM (error) of SEM model in the impact of technological capital investment on regional innovation output. Select the more significant SLM model for further analysis.
Point 2: The model is static. I don't think it's very likely that any policy effort towards innovation brings the result on impact. Lags in explanatory variables should be considered.
Response 2: First of all, I agree with you. In fact, during the calculation of the model in this manuscript, I have done a lag phase treatment in explanatory variables, but did not explain this in the article. In order to clarify the data source of each variable, we have made some adjustments and added a table to explain (Table 1, in line 335).
Point 3: Table 2 reports "OLS results". Not sure what is meant here: a "pooled" panel regression (without any individual effects) or the LSDV/FE regression (in fact estimated with OLS). If the former is the case, that is not a good reference point for future FE/RE spatial models. In other words, I can't agree with the statement in line 405 that before running SLM, one needs to decide whether FE or RE; in fact, this should be done earlier, even before the initial non-spatial model. Otherwise the two dimensions get mixed up in the comparison.
Response 3: In this manuscript, we, along the lines of Xue Q. G. (2014), analyze the impact of the allocation of scientific and technological resources on regional innovation output through OLS without considering the space factor. Then, based on the LM test, a spatial econometric model is selected in consideration of spatial correlation. Finally, the Hausman test is used to determine the fixed effect or random effect to determine the final model.
Point 4: "Local spatial correlation analysis" (line 366) is not a good header because, in the language of spatial econometrics, it invokes the notion of Anselin's (1995) LISAs - Local Indicators of Spatial Association. What is investigated here is the Moran's plot. I don't mean here that this investigation is a bad thing - in fact, it's useful - nor that LISA should be run. I just mean that this part of analysis should be re-labelled.
Response 4: Thank you for your suggestion on the header. After discussion, we found that there is indeed a problem with this and it is not a good header. Therefore, we think that changing the header to Local Moran ’s I Statistics may be a better choice. And, to correspond, we also adjusted the title of line 337 to Global Moran ’s I Statistics.
Some other comments:
Point 5: Line 252: are innovation output levels of provinces really measured by ArcGIS?! There's something wrong with this statement - either grammatically, or logically. Please reconsider.
Response 5: Thank you for pointing out the problem in line 252(now in line 262). My expression is wrong here. ArcGIS measures the Euclidean distance between two regions, not the innovations previously expressed.
Point 6: Equation (4) comes without any introduction.
Response 6: Thank you for pointing out the problem. In the process of writing the manuscript, we have explained the formula (4), but in the process of finishing, we may have missed this part. Now, the adjustments have been made according to your suggestions, from line 190 to 201.
Point 7: Part of the text between equations (1) and (3) appears in red.
Response 7: Thank you for your careful review. This is my fault. In the process of adjusting the article, the text was modified. Now this part of the text has been properly displayed in black.
Point 8: There's a double dot in line 61.
Response 8: Thank you for your careful review. This is my fault. Now we have deleted the extra dot.
Author Response File: 
Author Response.pdf
Reviewer 2 Report
See the attached pdf.
Comments for author File: Comments.pdf
Author Response
First of all, thank you for your valuable comments on this manuscript. We have carefully revised it based on your comments. We have revised them one by one based on your comments and marked them with a yellow background in the manuscript.
Point 1: Reading through the introduction, it is not clear that what exactly the contribution of the current study is. There is a lot of information on the allocation problem the authors think matters, but exactly what do they contribute? Indeed, the claimed contribution of the paper comes in the last paragraph of the literature review.
Response 1: At first, thank you for your advice. In fact, it is indeed not clear that what exactly the contribution of the previous manuscript is. In previous manuscript, we focused more on the research background in the foreword and ignored the research content and research contributions. We have now supplemented the introduction accordingly, from lines 61 to 74. If you have any question about this manuscript, please don’t hesitate to contact us.
Point 2: In equation (1), the subscripts i,t are missing for D . There is no Beta 3 in equation (2), but the authors mention Beta 3 as the coefficient of FDIit in equation (2). How does equation (4) follow from equation (3)?
Response 2:
(1) Thank you for your careful review. This is my fault. Now we have adjusted the equation (1) according to your suggestions.
(2) In fact, corresponding to formula (2), the output elasticity coefficients of science and technology capital investment, science and technology personnel investment, and foreign direct investment should be Beta 0, Beta 1 and Beta 2, instead of Beta 1, Beta 2 and Beta 3 as previously shown in the draft. Then, correspondingly, the output elasticity coefficient of FDIit should be Beta 2. The text is modified as follows.
(3) Thank you for pointing out the problem. In the process of writing the manuscript, we have explained the formula (4), but in the process of finishing, we may have missed this part. Now, the adjustments have been made according to your suggestions.
The specific amendments are shown in lines 190 to 201 of the manuscript.
Point 3: Since there is no formal derivation of the estimation equation (equation (5)) from a structural model, I think the authors should only state equation (5).
Response 3: Although the estimation equation (equation (5)) is not formally derived from the structural model, equation (5) is indeed based on the previous formula. And, in the later empirical research part, before the estimation of the spatial econometric model, OLS was done first, and the effect of the explanatory variables on the innovation output was initially considered.
Point 4: After equation (6), the authors mention “wij is the order weight matrix describing the spatial relationship of the n×n regions.” There are a couple of problems with this statement. First, there are only n regions. Second, if wij is indeed n×n, how does the algebra work when the terms involving wij (again n×n matrix) are added to the scalars in equations (5) and (6). Do the authors mean wij is an element of the n×n weights matrix?
Response 4: Maybe something is wrong with my statement. In this manuscript, wij is an element of the n×n weights matrix. First, there indeed are only regions, but measured the relationship of region i and region j (i=1,2,…,n; j=1,2,…,n). The specific setting method of wij is explained later(from line 237 to 279). In addition, when the terms involving wij (again n×n matrix) are added to the scalars in equation (5), variable ∑wijlnINNOjt is the spatial lag in the dependent variable, which represents the spatially weighted average value of innovation output from region i’s neighbouring area at time t. In fact, lnINNOit and ∑wijlnINNOjt are matrix forms of i×t. Equation 6 and equation 5 are similar. In order not to cause ambiguity, we have made some adjustments to the content of the spatial weight matrix.
The specific amendments are shown in lines 236 to 239 of the manuscript.
Point 5: After equation (6), in the definitions of lnWRDEit and lnWRDPit , for i≠j , the j index in the summation cannot run from 1 to 30. They can correct this by mentioning that for i=j ,wij=0; or place i≠j in the subscript of the summation along with j=1.
Response 5: Thank you very much for your comments, and we very much agree with you. Now we have adjusted the model.
The specific amendments are shown in line 233 of the manuscript.
Point 6: Equation (10) seems to be missing some parentheses.
Response 6: Thank you for your comments, but we may have different ideas. We think that equation (10) does not miss parentheses. This manuscript draws on Yu Yongze et al. (2015) estimation method of R&D capital stock to obtain the R&D capital stock of 30 provinces in China from 1998 to 2017. In equation (10), we assume that only half of the technological capital investment in that year formed the capital stock, and the other half was depreciated.
The specific amendments are shown in lines 304 to 308 of the manuscript.
Point 7: The explanatory variables RDE, RDP, the flow variables in equations (11) and (12), and the FDI are all potentially endogenous. All these factors self select them into regions, and it is not difficult to find unobserved time varying region characteristics (that affect innovation) correlated with these explanatory variables. I don’t see anything mentioned on this problem by the authors, and there is no robustness check towards this problem in the manuscript.
Response 7: First of all, I agree with your point of view. The explanatory variables RDE, RDP, the flow variables in equations (11) and (12), and the FDI are all potentially endogenous. However, during the model building process, we added a spatial weight matrix. In this case, each explanatory variable and the explained variable are not separate, and the correlation between the variables is considered.
Point 8: The wijs defined based on equation (9) are likely to be endogenous. Dealing with endogenous weights in the estimation requires analysis along the lines of Qu and fei Lee (2015).
Response 8: This manuscript draws on Lim (2003) to analyze the spatial weight matrix established by analyzing the spatial correlation of regional innovation in the United States, that is, the innovation interaction between provinces i and j is considered to be related to the total innovation output and proximity effect between the two provinces. At the same time, we do not deny expert opinions, but we still hold our original views. Ma, Deng and Zhang (2018) also uses this spatial weight matrix that takes into account innovative interactions between regions.
The specific amendments are shown in lines 274 to 282 of the manuscript.
Lim, U. (2003). The Spatial Distribution of Innovative Activity in U.S. Metropolitan Areas: Evidence from Patent Data. Journal of Regional Analysis and Policy, 33(2), 97-126.
Ma J., Deng H-B, and Zhang H. (2018). Spatial Patterns of Innovation Output of Cities in China Based on Spatial Knowledge Spillovers. Economic Geography, 38(09),96-104.
Point 9: After Table 1, the authors claim all values are statistically significant at the 1% level.
There are indeed many values with ∗ and ∗∗, table notes indicate that they correspond to levels of 10% and 5%, respectively.
Response 9: Thank you for your careful review. This is my fault. Actually, *, **, *** indicate that they passed the significance test at the levels of 10%, 5%, and 1%. From Table 1, we find the Moran ’s I values of regional innovation output from 1998 to 2017 were all greater than 0, and all passed the test at a significance level of 10%, even most of them passed the test at a significance level of 5%.
The specific amendments are shown in lines 360 to 362 of the manuscript.
Point 10: In Tables 2, 3 and 4, why is the analysis carried out separately for RDE and RDP? Equation (5) (the main specification of the paper in the methodology section) puts them together. Also, if there is a breakdown of these variables by enterprises, universities and research institutions, why don’t the authors include them together and drop the aggregated ones? In other words, have CRDE, XRDE and YRDE (along with their spatial lags) and drop RDE (and WRDE), and the same for RDP.
Response 10: In Tables 2, 3 and 4, the analysis carried out separately for RDE and RDP, which is to judge the impact of technological capital investment and scientific and technological personnel investment on innovation output respectively.
Although there is a breakdown of these variables by enterprises, universities and research institutions, we don’t include them together and drop the aggregated ones. The main reason is that the CRDE, XRDE, and YRDE are relative value, and RDE is absolute value. Reserved summary variables is to investigate the effect of RDE on innovation output as a whole, and the same for RDP.
Point 11: The interpretation of the coefficient after Table 3 is not correct. Note that the reduced form of the spatial model implies that the marginal effect of variable changes over i’s and j's. The authors can compute the so called direct, indirect, and total effects suggested by LeSage and Pace (2009).
Response 11: In Table 3, we report the specific impact of technological capital investment and scientific and technological personnel investment on innovation output of enterprises, universities and research institutions. The model this manuscript used is SLM simplified by SDM. This model only considers the spatial correlation of the dependent variables. As for the direct effects, indirect effects, and total effects you mentioned, we think it should be a partial differentiation of the spatial Dubin model.
Point 12: The authors mention that they choose SLM over SEM because R-LM test results is higher for the SLM. This is not a valid approach for model selection in comparing SLM with SEM, because these models are not nested (Fei and Lee, 2013).
Response 12: In the model selection process, we determined the model according to the Lagrange multiplier test method. Finally, because the LM test results of the SLM model were more significant than the SEM test results, we chose SLM. This method is also used in model selection in many articles (Jiao C. H.，Chen Y. F., 2018). Therefore, we consider this method feasible and continue to use it.
Jiao C. H.，Chen Y. F. (2018). R＆D resource allocation, spatial correlation and regional TFP growth. Studies in Science of Science, 36(01):81-92.
Point 13: The authors mention that they have estimated their main specification using the weights definitions in equations (8) and (9). Where are these results presented?
Response 13: Thank you for pointing out the problem. In the previous manuscript, the calculation results according to Equations 8 and 9 are not listed, but a simple explanation is given. Based on your comments, this section has now been supplemented.
The specific amendments are shown in lines 516 to 525 of the manuscript.
Point 14: A minor suggestion to the authors is that they should change the bibliography style. Bibliography should follow an alphabetical order. Also, citations in the body, should not differ between noun citations and citations in parentheses.
Response 14: Thanks for your advices, the references have been adjusted according to your advices. Citations in the body are the same between noun citations and citations in parentheses. Also, bibliography follow an alphabetical order now.
The specific amendments are shown in lines 645 to 723 of the manuscript.
Author Response File: Author Response.pdf
Round 2
Reviewer 1 Report
The improvement, and accompanying comments, are now satisfactory to me.
Author Response
Thank you very much for your recognition of the last modified version. Since there are still some minor language issues, we have now adjusted the language of the manuscript accordingly.
Author Response File: 
Author Response.docx
Reviewer 2 Report
Looking at equations (5) and (6), the terms involving RDE and RDP on the right hand side are now lagged for one time period. This was not the case in the previous version of the manuscript. Yet, looking at the results in Tables 3, 4 and 7, I observe no change. They are the same as Tables 2, 3 and 4 in the previous manuscript. Do the authors use lagged values of the terms involving RDE and RDP in the estimation?
By definition the elements of the weights matrix in equation (9) are endogenous, and the estimation of SLM and SEM models with endogenous weights require a more sophisticated approach. See Qu, X. and fei Lee, L. (2015). Estimating a spatial autoregressive model with an endogenous spatial weight matrix, Journal of Econometrics 184(2): 209 - 232.
In line 520, I think the authors meant tow write the SEM model is set as:
Author Response
First of all, thank you for your valuable comments on this manuscript. We have carefully revised it based on your comments. We have revised them one by one based on your comments and marked them with a yellow background in the manuscript.
Point 1: Looking at equations (5) and (6), the terms involving RDE and RDP on the right hand side are now lagged for one time period. This was not the case in the previous version of the manuscript. Yet, looking at the results in Tables 3, 4 and 7, I observe no change. They are the same as Tables 2, 3 and 4 in the previous manuscript. Do the authors use lagged values of the terms involving RDE and RDP in the estimation?
Response 1:
Sorry, maybe there is something wrong with my statement. In previous manuscripts, RDE and RDP actually used data lagging by one year, but did not specify. In the last modified version, this part of the increase is described. Actually, we use lagged values of the terms involving RDE and RDP in the estimation
Point 2: By definition the elements of the weights matrix in equation (9) are endogenous, and the estimation of SLM and SEM models with endogenous weights require a more sophisticated approach. See Qu, X. and fei Lee, L. (2015). Estimating a spatial autoregressive model with an endogenous spatial weight matrix, Journal of Econometrics 184(2): 209 - 232.
Response 2:
Thank you for pointing out the problem. There are indeed some problems in setting up the spatial weight matrix. The spatial weight matrix has now been adjusted. In order to avoid recurrence of endogenous problems, the spatial weight matrix we are using now uses only geographic distances, without considering innovation output. However, in the manuscript, we cite your recommended article as the basis for not using the technical distance spatial weight matrix.
For more information, please see lines 239-272.
Point 3: In line 520, I think the authors meant tow write the SEM model is set as:
Response 3:
I am sorry, it’s my mistake. And now, I have changed the expression as you suggest in line 230.
Author Response File: Author Response.docx
Round 3
Reviewer 2 Report
My comments have been addressed.
