The paper „Wind tunnel investigations of an individual pitch control strategy for wind farm power optimization“ investigates the impact of the Helix approach for wake control on the total power output of two turbines in tandem configuration as well as the effect of the Helix control on the wake development. The paper is well written and the analysis presented gives good insight in what is happening in the manipulated wake. The procedure of the Helix control and the contribution of the respective Nevertheless, there are a few points the authors should address and clarify, respectively.  

Specific comments

1. The authors mention, that the blockage in this experiment is rather high and present a correction for the inflow velocity. Since that correction is needed, can the authors also say anything about the possible impact of the blockage on the results of the measured wake? It would be helpful to get a feeling if these results are representative for the Helix control or if it might be an artefact. Are there aspects from other investigations with lower blockage that are comparable?

2. The authors mention that they expect an impact of higher turbulence intensity on the results with which I totally agree. What about different wind velocities? I assume that this control is applied in the partial load region. Do the authors expect comparable results for the complete wind velocity range in the partial load region?

3. When looking at the total power of the two turbines the second turbine is also running at a constant rotational velocity. The second turbine clearly sees different and non-uniform and temporally changing inflow condition to which an activated turbine control would react to. Did the authors try to activate the „normal“ control of their turbine? What effect did that have on the total power? Why did they decide to run the second turbine also at a constant rotational frequency?

4. The traversing system and the support of the five hole probe looks pretty massive in figure 2 and can affect the measurements. Can the authors give more details about the distance of the sensing head to the support? Are they sure that the measurements are not influenced by the traverse?

5. Section 3.4 gives many details on the five hole probe and the calibration. Since these details can be found in other also mentioned publications, I recommend to leave that section out of the paper since it is not contributing to the overall story.

6. In figure 8, the authors observe a ditch in the thrust coefficient for St_add = 0. Do they have any idea where this is coming from? 

7. In figure 9 the authors leave out the results for St_add = 0. They mention, that it more or less matched the results from another investigation but without load feedback. I don’t understand why this one point right in the middle of the curve should be left out. I would highly recommend to add that point also to provide the complete picture.

8. The presented DELs show a clear increase especially for the first turbine. Unfortunately I have not knowledge or feeling what that would mean e.g. for a real turbine. Even though the authors state in the end, that the results can not directly be applied to real turbines they should at least discuss what an increase of the DELs would have for consequences for real turbines. Would that be a total show stopper for already existing machines or would that addition be within a range that is accounted for in the current design process?

9. In the text (page 17, lower part) the authors mention four points P1 to P4 for which the spectra are presented in figure 12. Figure 12 only shows 2 points closer to the turbine x = 0.5D and not x = 2D.

10. Shifting the spectra in figure 12 vertically could help to better show the peaks for the different conditions. 

11. Line 465 second sentence: Why does the measured data solely consist of the azimuthal and the blade 1 pitch position? Why blade 1? Even though the data is phase-locked analysed, the resulting wake is a results of the complete rotor. Am I wrong?

12. In section 4.2.3 the authors explain how they got the data for the phase-locked data with the additional frequency. I think it could help to show graphically how they get the beat frequency and how they apply this to the five hole data.

13. For this analysis, how did you make sure that the pitching starts at the same position of the blades?

14. Is there any reason, why the authors do not perform the same analysis with the fluctuations for the phase-locked with additional frequency?

15. The authors state that the meandering of the tip vortices in the blade tip region is the main driver for the increase wake mixing. Following their analysis, I can only conclude that there is a meandering of the blade tip vortices. By performing the same analysis for other St_add, for wich the total power is not or just slightly increased, should provide clear evidence that this meandering is either not there or decreased. The authors should add such an analysis.

Technical comments

- The authors mix the value for the Strouhal number St_add — that value is sometimes 0.45 and sometimes 0.47. According to the definition it should be 0.47 all the time unless I missed something.

- Line 308: as seen in figure 8

- Line 368: what does the index „1“ stand for in the definition of P1 = (x/D, y/D)_1 ??

- Line 411, last sentence should be x=5D for the complete merge of the tip vortices. 

- Line 439: the youtube link is not finalised. 

- Line 443:  Isn’t the „“additional rotational frequency f_(r,a) identical to the additional excitation frequency f_e ?

- Line 474: Youtube link is not finalised. 

- Line 493: in which an x-y plane

This article presents a wind tunnel study of a wake control strategy named ‘Helix’. The article is of relevance to wind energy community and fits within the scope of the journal. The study is performed systematically and data quality is good. There are, however, some concerns regarding the work which need to be addressed properly. These are listed below:

1. My main concern is regarding the blockage effect in the experiments. As authors indicate, the blockage is about 20%, which is considerably high. To tackle this, they propose a ‘blockage-corrected free-stream velocity’. Does correcting the free-stream velocity resolve completely the effect of blockage? In principle, your turbine is placed in a confined channel, where the flow acceleration can affect the turbine power output and also affect the development of the wake due to an effective favorable pressure gradient in the flow. How is this addressed in the work? At least, the authors should mention the limitations introduced in the work due to the blockage effect to properly guide the reader.
2. The experiments are performed in an almost laminar uniform flow (Tu<0.5%). I understand that the authors intend to isolate the effect of control strategy. However, the relevancy of the control approach to field conditions with turbulence intensity greater than 5% and boundary layer shear must be discussed. In other words, does the control strategy remain effective at high turbulence intensities and in the presence of flow shear?
3. The authors indicate that the turbine rotation is fixed at an optimum value. How is this optimum value obtained and does it remain the same for the uncontrolled and controlled turbine configurations?
4. The pressure probe measurements are performed for 40 seconds. Is that time interval sufficient to give converged flow statistics?
5. The baseline plots in figure 7 are very hard to distinguish from the background of the plot. Consider improving the figure.
6. The authors compare the trend in the thrust coefficient with that in the available power, and identify some differences. Is that a fair comparison? If so, what is the possible explanation for the difference? Wouldn’t it be more appropriate to compare thrust coefficient with power coefficient?
7. Is the blade pitch synchronized with the rotor rotation for all the cases?
8. For phase-locked measurements, how is it ensured that during a certain azimuthal phase the pitching phase is also the same for all the cases?
9. There are several minor grammatical mistakes throughout the article, which need to be addressed: e.g., line 31 (‘turbine excitation “triggers” wake meandering’); line 101 (‘dynamic variation’); line 293 (‘does not apply to’); line 308 (‘as seen in’); line 396 (is ‘data basis’ a correct word?); line 411 (sounds a bit repetitive); line 439 (the link is missing).

The authors present an experimental study in a wind tunnel for a control strategy for wind turbines. The control system, named Helix, increases the rotational component of the wake by pitch control for sinusoidally varying yaw and tilt moments. Experiments are performed under low turbulence conditions using a single or two scaled turbines, studying in different steps, the wake averaged statistics and phase-locking techniques. Also, several sensors provide turbine level observations. The authors then discuss and quantify wake recovery and vortex meandering. It is found that operating the scaled turbine with the Helix control results in faster wake recovery when compared with the baseline cases.

The manuscript is well written and the experiments and results of interest for the wind energy community. Nevertheless, before recommending publications I ask the authors to address the following comments and remarks:

- The study concerns low turbulence conditions only. Nevertheless, background turbulence significantly affects the development of the wake and the structures within it. This therefore raises the question, discussed by the authors in the introduction, about the relevance of present results in realistic conditions. While the present study presents a fundamental interest, I consider that the authors should discuss in better detail, using the several works available in the literature, how their results will be modified when background turbulence is present.

- Also, the setup presents a large blockage. This is also briefly discussed by the authors, and they use a very simple model to cater for this issue. Nevertheless, blockage not only affects the hub velocity but it also severely modifies the wake development, the air it entrains and the evolution of structures. Several works discuss the relevance of blockage and propose different corrections (see for instance Saghi et al 2016, Steiros et al 2022, among several others). Blockage is one of the main limitations of the experimental setup and should be addressed carefully.

- The time-resolved five-hole probe has a large head surface (around 8 squared millimeters) and therefore, for a turbulent wake in a wind tunnel, lies within the inertial range of turbulence. It is then important to check the effective temporal resolution, taking into account both background noise in the wind tunnel and spatial filtering effects. I therefore suggest that the authors show some typical spectra obtained with the probe. Also, the description of the calibration process is quite long, has it been performed by the authors or by the manufacturer? If it is the latter case, I suggest that the discussion is taken out of the manuscript.

- Figure 10 suggests, despite the presence of an adjustable ceiling, a significant pressure gradient in the tunnel. Is that the case or an effect of the y-axis limit?

- In its current form, the manuscript is very long and, given the large number of results presented, some sections are hard to follow. The authors should consider putting some results and discussions in an appendix.

- The manuscript is overall very well written, but it still presents several typos.