Summary: This paper documents the tuning of relaxation parameters for an ocean DA based on EnKF and IAU. The methods used in this study are well established in other DA practice. Since ocean DA faces the challenge from dynamical imbalance with shorter cycling periods, the use of relaxation with IAU is a good approach and tuning results are meaningful for the ocean prediction community. I've found several issues in experimental design and result presentation, which I believe the authors should be able to address before the paper can be accepted.

Major Issues:

1. Are cases with alpha<0.9 tested for RTPP/RTPS without IAU? As RTPP+IAU approaches NO INFL+IAU results in both balance and accuracy, I guess the RTPP cases will also approach NO INFL as alpha decrease. If you have tested several points (maybe RTPP05 and RTPP07) it would be interesting to add them in the plots. For example, could there be an alpha value for RTPP that beats RTPP09+IAU?

2. The choice of inflation factor in MULTI is more problematic. Since the multiplicative inflation is applied throughout the domain, it is more sensitive the the rho value. The relaxation methods have build-in spatial variations in inflation so I think it is not a fair comparison between MULTI and RTPP/RTPS methods. In regions where analysis increments are smaller (fewer observations) the inflation of spread can accumulate over time exponentially. Ideally using a spatial varying inflation (such as in adaptive MULTI algorithms) can help. So, if you choose to show MULTI results here the exact value of rho is very important. Could you estimate an equivalent rho from the best RTPP/RTPS cases? You can averaged the (1-alpha) + alpha*prior_spread/posterior_spread over the domain and time (for RTPP) to estimate the equivalent rho, is it near 1.05 or much smaller?

3. Tuning of relaxation can also be case-dependent, you also need to consider the density of observations and localization radius. In the method description maybe you should state more clearly how you tuned localization with this observing network (can you also show a map of observation density for reference?), and the results from tuning alpha in relaxation would likely change if one use another set of observations with different density and localization radius. A discussion in the conclusion would be nice.

4. I found time evolution of imbalance and errors to be important in this particular case. Since you used fixed values in inflation schemes, it is not guaranteed that the performance will be steady in time. Does the imbalance gradually increase or decrease over time for a chosen alpha value? A time series of spatially averaged delta NBE could be more convincing that the performance is steady. I would be also curious about how long the initial spin up period is for DA solutions to become steady.

Minor Issues:

Line 153: abs denotes taking the absolute value, please use standard notation |x|.

Line 160: the same term IR is used for both RMSE and NBE?, maybe add a suffix to distinguish.

Line 220, Table 3: gross error check not "growth error check"?

Line 237: SSS nudging: could you provide more details of this approach, maybe a reference or technical report?

Line 246: is every experiment tested against NO INFL for significance of improvement/degradation? If so, you should state this more clearly.

Line 264: this imbalance is substantially improved => reduced.

Line 276: I guess the RTPP09 and RTPS09 cases are also tested against NO INFL for significance?

Figures 1, 3, 4, 7 and 8: you used hollow/solid circles to denote significant/non-significant improvements, but for degradation you used "x" which cannot show hollow/solid differences, maybe use another symobal (triangle?) so you can be consistent.

Line 551: confidence limit: do you mean confidence level (p value < 0.01)? and no significant difference has p>0.01?, if you used t-test just state the p value threshold to be clear.

The manuscript discusses a setup of an ocean circulation model (the Stony Brook Parallel Ocean Model, sbPOM) for the north-western Pacific region combined with an LETKF data assimilation step. Daily assimilation of satellite and in situ observations is applied and sensitivity experiments are performed with and without incremental analysis updates (IAU) in which the parameters of different covariance inflation methods (in particular RTPP and RTPS) are varied. In addition, a multiplicative inflation is tested with a single fixed inflation value. The study finds that IAU improves the balance of the model increments while the inflation schemes disturb the balance. In contrast IAU leads to higher estimation errors and less ensemble spread than the inflation methods. The multiplicative inflation is found to be failing by not reducing error enough. Parameter ranges are described in which the different methods yield the best assimilation results (low imbalance combined with low estimation errors) and the overall conclusion if that IAU in combination with RTPP with a parameter value of 0.8-0.9 provides the best configuration.

Overall, I have large problems to find what is actually new in this study and what are relevant research results. Actually, while the authors write 'This study develops an ... (EnKF)-based regional ocean data assimilation system' (Abstract line 12), this system is certainly not new. Actually, Miyazawa et al. (2012) already described an LETKF in combination with the sbPOM model. This earlier publication did not use the same model configuration, but this implies that an actual LEKTF-sbPOM DA system already exists for 10 years and this leaves the impression that in the manuscript the authors (Y. Miyazawa is one of the co-authors) merely present some new model configuration. Even more, the applied methods IAU, RTPS and RTPP are established standard methods for ensemble data assimilation. Thus, it is unclear what new insight the experiments described in the manuscript actually provide. The given numbers like 'RTPP with the parameter of 0.8-0.9' (Abstract line 26) are not at all generalizable to other model configurations or other models. Further, the authors do not show any attempt to actually find explanations for their findings. As such it remains that they describe the behavior of a single data assimilation application when parameters of established standard methods are varied. For me, this is insufficient for a scientific publication. To this end, I can only recommend to reject the manuscript. Perhaps, the authors can then find a proper scientific question to assess with this ocean DA system and submit a new study that provides general insights.

Apart from the aspect of novelty and relevance, I have a few major comments:

1. The manuscript is submitted as a 'development and technical paper' and its title suggests that it might document particularities of the EnKF-sbPOM model system. However, the manuscript is missing detailed descriptions of the actual system. 

2. The authors list EnKF-based ocean data assimilation systems in Table 1. Unfortunately, this list is very incomplete. E.g. there are EnKF/based system run operationally by the Copernicus Marine Service (CMEMS) for the global ocean and for the Baltic Sea (It is easy to find these systems via the CMEMS website marine.copernicus.eu). From the operational CMEMS systems, Table 1 only lists the TOPAZ4 system. There is also an operational EnKF-based system in Germany (the latest article about it is Bruening et al, 2021, but there are several publications about earlier versions dating back to the year 2012. This system uses 12-hourly analysis, thus even shorter than what is pointed out in the manuscript). Also there is an EnKF-based coupled system which focuses on the ocean (e.g. Tang et al. 2020). Overall the authors should perform a much more careful research on current systems. Publications dating back to 2011 or 2012 do most likely not describe the current status.

3. The authors express that their data assimilation setup is particular because of daily assimilation. However, when one has a sufficiently complete overview one sees that short assimilation cycles like daily are not that special. On the other hand there are good reasons for longer cycles. One particular reason is the repeat cycle of the altimetry satellite data. Further, while applying e.g. weekly analyses steps, systems like TOPAZ4 use asynchronous filtering, e.g. for SST. Thus, the system is able to also take some of the faster variability into account. The authors should take such characteristics of the DA systems into account to provide a sound overview of EnKF-based ocean DA systems. 

4. As mentioned above, IAU, RTPP and RTPS are standard methods in DA already for quite some years. As such it is surprising to still see a manuscript submission about these schemes. Unfortunately, the authors also miss to take into account the study by Yan et al. (2014), which discusses IAU in ocean data assimilation. However, also the CMEMS system for the global ocean uses IAU. Given that these methods are well established and well studied, I am quite skeptical that it is possible to find new general insights by just using standard methods and varying their parameters. 

5. The authors use a model spin-up of 4.5 years from an ocean in rest. This spin-up period looks far to short for properly spinning up the ocean unless one only looks at the upper layers.

6. The observation errors of 1.5degC for satellite SST and in situ temperature and of 0.2m for SSH are very large compared to what is commonly used today.

7. In lines 220-221 it is described that the localization settings are chosen following the studies by Miyazawa et al. (2021) and Penny et al., (2013). However, in these studies other model configurations with different resolutions are used and both use different localization radii. It is known that localization settings depend also on the model configuration. To this end, just selecting some settings from model configurations at other resolutions is not a reasonable approach. One can use values from other studies as a starting point for ones own tuning, but this tuning will be required as otherwise, there is a high risk that the DA system is suboptimal. Thus sub-optimality then also influences other DA parameters like those for the inflation.

8. In line 60 the authors describe the TOPAZ4 system with 'but with inflation of observation errors'. I'm unsure what the authors intend to express by 'but'. However, when the authors look carefully, the 'moderation of observation errors' used in TOPAZ4 is in fact a careful inflation that should have similar effect as a carefully tuning multiplicative inflation scheme.

9. The multiplicative inflation schemes is described as 'not demonstrate sufficient skill'. This description is actually misleading and invalid. The authors only run a single experiment with a fixed inflation of 5%. Thus, any sensitivity assessment is missing. Actually, the data assimilation process in the system of the manuscript runs already stable with successful assimilation even without inflation as the figures show. This is a clear indication that 5% multiplicative inflation is too large.

10. The residual of the nonlinear balance equation {\Delta}NBE (Eq. 8) is not normalized. As such it is unclear whether any of values shown in Fig. 1 and described in the text (like 2.11x10^{-10} for MULT+IAU in line 249) is actually significant. 

References:

Bruening, T., Li, X, Schwichtenberg, F., Lorkowski, I. (2021) An operational, assimilative model system for hydrodynamic and biogeochemical applicatios for German coastal waters. Hydrographische Nachrichten, 118, 6-15, doi:10.23784/HN118-01

Tang, Q., Mu, L., Sidorenko, D., Goessling, H., Semmler, T., Nerger, L. (2020) Improving the ocean and atmosphere in a coupled ocean‐atmosphere model by assimilating satellite sea surface temperature and subsurface profile data. Q. J. Royal Metorol. Soc., 146, 4014-4029 doi:10.1002/qj.3885

Yan, Y., Barth, A., Beckers, JM. (2014) Comparison of different assimilation schemes in a sequential Kalman filter assimilation system, Oce. Mod. 73, 123-137, doi:10.1016/j.ocemod.2013.11.002

Title: An ensemble Kalman filter system with the Stony Brook Parallel Ocean Model v1.0

Authors: Ohishi et al.

Recommendation: Major revision

Summary

This manuscript describes the local ensemble transform Kalman filter (LETKF) implemented in the Stony Brook Parallel Ocean Model (sbPOM), with daily assimilation of satellite and in-situ observations. Sensitivity experiments with IAU and various multiplicative inflation methods are performed. Results show that the application of IAU improves the analysis balance, but degrades the analysis accuracy and also reduces ensemble spread. The constant multiplicative inflation with or without IAU had much larger imbalances and errors than the other configurations. RTPP and RTPS with IAU had improved balances and smaller errors when the inflation parameter is tuned. The presentation of the manuscript is fine, and the lessons of inflation and IAU with influences on imbalance and accuracy are useful for the ocean DA community. But the results need further clarifications and explanations. Please see my comments below.

1. It is confusing about the impact of IAU on the assimilation results. Compared to NOINFL, IAU in NOINFL+IAU degrades the accuracy. Why IAU degrade the accuracy for ocean assimilation that has longer time scale than atmosphere?
2. The authors state that IAU reduces the spread and accuracy of DA. But MULT, RTPP and RTPS have totally different impacts on the spread and accuracy when IAU is applied. Why MULT that also inflate the ensemble spread has the opposite impacts on spread and accuracy than RTPP and RTPS? Since the results with different inflation methods are inconsistent, it would be helpful to understand the roles of different inflation methods, especially the interactions with IAU.
3. Previous studies of IAU (e.g., Lei and Whitaker 2016, He et al. 2020) showed that IAU has more advantages for variables that are more influenced by imbalances that variables that are less influenced by imbalances. However, results here are inconsistent with the previous findings. IAU improves the accuracy of wind field more than the accuracy of height field (Figures 3 and 4). Please provide explanations or insights for these counter-intuitive results.
4. Details of how the verification are done are needed. Which time is the imbalance deltaNBE computed at? Is it the prior or posterior at middle of DA window? The RMSD is computed for the prior or posterior? How the RMSD is computed for experiments with IAU?
5. Since assimilation is conducted at a daily frequency, both the daily prior and free forecast at longer forecast lead times worth to check.

Minor comments:

1. L90, for the IAU configuration here, is the analysis computed at the middle of an DA window or not? The 1.5 times computational cost is compared to the standard method with or without IAU? It is not clear why analysis is performed at the beginning of an DA window.

References

He, L. Lei, J. S. Whitaker, and Z.-M. Tan, 2020: Impacts of Assimilation Frequency on Ensemble Kalman Filter Data Assimilation and Imbalances. J. Adv. Model. Earth Syst., 12, e2020MS002187.

Lei, L., and J. S. Whitaker, 2016: A four-dimensional incremental analysis update for the ensemble Kalman filter. Mon. Wea. Rev., 144, 2605-2621. doi: http://dx.doi.org/10.1175/MWR-D-15-0246.1.