The paper describes the mechanisms that drive variability in fog and low cloud cover at two locations in the Namib Desert by using a cloud controlling factor framework and by testing statistical relationships between different indices and a historical reconstruction of FLC. I find the results interesting, though I feel the paper could make its statistical methods more robust, which may strengthen some of the results. I recommend major revisions, which primarily focus on handling the high dimensionality of the cloud controlling factor framework. Please see below my specific comments:

Major Comments:

1. The CCF input features seem to be an order of magnitude greater than the number of monthly observations for the timeseries (thousands of features versus hundreds of observations). The tuning of the lambda was done to maximize out of sample performance, and therefore reduce overfitting. While that can provide an acceptable model for the historical reconstruction analysis in 3.2, it can still lead to many spurious coefficients when working with such a high dimensional problem. Perhaps using a harsher penalty for the sensitivity analysis in 3.1, could yield a more reasonable number of important input features. Alternatively, the authors could also use a dimensionality reduction technique like PCA (i.e. apply PCA to an n x n matrix of spatial points to reduce the total number of input features while conserving spatial variance information). Another option could be to remove the input fields over land for RH at 700 hPa and U10 and V10. This could additionally reduce noise in ridge coefficients because the authors mention that the wind fields are not as reliable over the land as over the ocean. I don’t feel super strongly about which approach is used, but I do think the CCF analysis would benefit from some dimensionality reduction or a harsher penalty to clarify which spatial fields and variables control FLC variability. 

Minor Comments:

1. It is unclear what the spatial range of AN and CN are, the paper shows the central point, but I didn’t see any description of the specific area of focus. I recommend indicating the spatial averaging box for FLC in Figure 1. Also, I recommend using an open circle to show the centers, so that the value for that grid cell is visible and that the color of the circle is not the same as the shades used in the color bar. 
2. Ln 129-130: After removing trend and monthly seasonality, is there still autocorrelation in the residuals?
3. What is the standard deviation in out of sample performance across the cross validation?
4. Ln 164: Why only show CN-ERA5? It could be worth discussing one of the AN results as well because some of the findings differ.
5. Ln 190: The negative sensitivity may also be due to the LUCI located to the south of CN. 
6. Ln 220: How much is the skill improved by averaging annually post-prediction?
7. Ln 237: What statistical methods are being used to determine the trend? Have the authors considered non-linear trends?
8. Ln 273: This does make me question why the wind components are in the reconstruction model, maybe justify why it is still important to include them.
9. Ln 280-281: Another reason the trends are unreliable could be due to the lack of statistical significance as opposed to reanalysis differences.
10. It's a little hard to differentiate the purple and blue on figures 6 and 7, perhaps make the anomalies green as was done in the appendix. 
11. Ln 326:328 I wonder how robust the finding of the correlation between the LUCI/BNI is with the respective AN/CN locations, due to SST anomalies being used to reconstruct the timeseries. I would be curious to see the correlation between any same-sized patch of SST anomalies with the AN/CN anomalies. If the correlation for the LUCI/BNI is significantly higher than any random SST anomaly patch, this could strengthen the findings. Also, it would be helpful to mention the periodicity of LUCI/BNI. Does it vary on short or long timescales?
12. Appendix Figure B2
1. Clouds are most frequent September to March (ln 29), some of these months are missing from the analysis, any reason?
2. Does this analysis just compare the closest grid cell to the Marble Koppie station?
3. Why show the wind direction and not directly the u10 and v10 components? 

General Comments:

The manuscript details drivers of interannual variability in coastal fog in two regions within the Namib dessert utilizing a cloud controlling factor methodology. The manuscript is well written and scientifically rigorous, but I believe a few sections could be refined to maximize its impact and readability. I recommend minor revisions to emphasize sections with notably novel results (comparison of reanalyses and links to Benguela Niño events).

Specific Comments:

Methods –The differences between the winds is an interesting result! Figure B2 highlights the lack of the diurnal cycle tracking for DJF, but it seems that previous papers indicate log-fog season in April-June and high-fog season September-November? Any reason the cycle isn't grouped by fog-season?

From Figure 4, also related to the winds– Since the bars are the contribution from each component, and SST data is the same, is the MERRA2 AN linear model therefore more sensitive to SST than its ERA5 counterpart? Could this mean that when constructing historical interannual variability, that ERA5 is more sensitive to low-level winds, and therefore has a higher correlation to El Niño if the primary mechanism is indeed strengthened northwesterly winds (sort of apparent in higher r values in line 289). Would it be possible to make the weight of the SST sensitivity the same between ERA5 and MERRA2, and might that indicate which reanalysis wind is more sensitive to the significant land warming (https://wires.onlinelibrary.wiley.com/doi/full/10.1002/wcc.70025), or would that excessively disrupt the construction of the model? Are there any previous cases from higher-temporal scales (diurnal, synoptic) that point to more fidelity in a particular reanalysis?

Section 3.2, line 220 – Any further information on the annual FLC anomalies would be a great addition for the reader. Such as, do annual anomalies follow the seasonal cycle for the AN, so a positive anomaly means more fog in the peak season, or a slightly longer season (to the extent it’s tractable in monthly data)? Similarly for the CN, do any months consistently appear from the historical reconstruction in years with strong reductions?

Section 3.3 – As a suggestion, I would restructure section 3.3 to lead with the BNI influence (lines 303-335) and Figure 7, as it ties into the regional climate more directly than ENSO (and reflects the title of the manuscript).

Technical Comments:

Abstract, Line 12: I would start the conclusions of the interannual variability section with the last conclusion, “..half of the variability in Angolan Namib comes from Benguela Niño events..”. I would also include the % increase/reduction in FLC occurrence during El Niño years for reader context.

Introduction, Line 50: It seems the Li (2025) reference sets up your study analyzing spatial drivers of interannual variability as a next step nicely (decrease in fog water since 1996, some discrepancies in El Nino periods before and after this period with in-situ observations, although only in one location). If desired, one could add another sentence here to supply some of those motivations to the reader? Or maybe just the mechanism they supply that increases fog occurrence, and potential limitations? Some results later in this work reference the Li paper, so a bit more context would strengthen the impact of this study’s results.

2.2, Line 102: Long term warming trend removed from BNI? Maybe mention the value in the case the reader is curious?

3.1, Figure 2, Line 192: Add titles to subplots, even if small text, just makes looking at them together easier.

3., Line 194: Add parentheses in Table 1 after SST (NOAA OI) so reader can’t mistake reanalysis SST being used.

Figure 3 – Is there a time series of predicted vs observed FLC occurrence for 2003-2020 using the network? Maybe add in dots to both panels to show spread in observed fog anomalies. It would be nice to see observations next to what the network predicts. Any additional context to the 1996 divide posited by Li et al (2025) that you can add would be great, since the CN region includes Gobabeb research station, correct?

I think this is decent manuscript and it looks promising, but it is impossible to recommend it for publication if the authors don’t release their code upfront. I couldn’t readily verify the claims, and as such, I recommend rejecting this manuscript. If the authors release their code as part of the submission, I am happy to take another look.

Below I list a few comments that could be helpful in a revision, if pursued.

General

• The manuscript would benefit greatly from more discussion at the end — more contextualization, more outlook, and the like. In the other words, what's the point in all of this and how does this manuscript help the field?
• Is it necessary to test the stationarity assumption around line 159?
• Can you comment on the co-variability (or absence thereof) between EIS and SST around line 275?
• This is in a special issue on ‘aerosol, fog, climate, and biogeochemistry in southern Africa’ and yet this manuscript has nothing to do with aerosol as a CCF… is that common? Or are aerosols not important around this area?
• Can you better situate this manuscript against/along the findings of Li et al 2025?

Specific

• L 70: seems a bit defensive and giving up prematurely? More details?
• Fig 1: help the reader understand the fig with two color bars?
• L 83: convection? Typo?
• L 87: quantify skill improvement/degradation and how you judged it?
• Fig 2: maybe put the variable names on the fig itself?
• L 373: It's rather difficult to verify the claims without taking a quick look at the code, so to me, it feels like I wasted my time reviewing this manuscript. Without code, anyone can make up all sorts of claims, etc. — I recommend a rejection here because it is impossible to support the claims made by the authors without at least a cursory look at the code.

This study describes the mechanisms that drive interannual variability of fog and low clouds in two fog host spots: the Angolan and Central Namibs. A statistical model was built using a cloud-controlling framework based on observations from 2004 to 2019 to reconstruct the interannual variability of fog and low cloud cover  anomalies from 1982 – 2019 using ERA5 and MERRA-2 datasets. The results explores the causes of interannual variability of FLC highlighting the strong modulation of local SST dynamics rather than global SST anomalies (ENSO). The paper is well written-and well-structured, although some physical explanatios are lacking related to important physical processes in marine stratocumulus formation that are missing. Below general and specific comments are made to improve the paper clarity.

General Comments:

Ln25-28: This paragraph uses several terms that seem to describe similar phenomena (e.g., “advection fog”, and “advected marine stratus clouds”). Clarifying the distinctions between these terms, if any, and using consistent terminology would improve readability.

Ln65-67: Validation against surface observations is reported to demonstrate good performance of the FLC detection algorithm; however, the specific surface observation datasets used are not specified. Please clarify which observations were used.

Ln75-77: It is unclear what is meant by “spatially and temporally averaged” FLC cover. Please clarify whether this corresponds to a domain-averaged time series and specify the spatial domain used for each zone.

Section 2.2 Cloud controlling factors

Ln82-89: The section introduces five controlling factors supported by literature, but these are also referred to as predictor variables (e.g. EIS, relative humidity at 700 hPa). It would be helpful clarify the physical processes represented by each variable and their relationship to FLC variability, rather than only listing them as predictors. In particular, linking these variables to processes such as cloud-top radiative cooling and entrainment, and how these processes may influence EIS, would improve the physical interpretation.

Ln86-87: Subsidence is excluded from the final set of predictors because it does not improve model skill. However, this factor has been used in previous studies cited in the manuscript (e.g., Klein et al., 2018; Scott et al, 2020; Ceppi&Nowack,2021; Andersen et al., 2022). It is very important to provide an explanation for its exclusion beyond the model skill since subsidence is one of the main physical processes controlling marine low stratus formation in tropical oceans.

Ln101: The use of the 1991-2020 period as the reference climatology for SST anomalies is not fully justified. Could you clarify whether this choice affects the results and why it was preferred over the 1982-2019 period?

Ln149: In relation to the comment on Ln101, why is the 2004-2019 period used as the reference for calculating the anomalies? It would be preferable to use a consistent reference period throughout the analysis to ensure comparability.

Ln232-233: Li et al. (2025) is cited multiple times. Could the authors clarify the reason for the difference in the reported decline in fog amount after 1996? In particular, is this related to differences between low clouds and fog, or could it be attributed to methodological choices or other factors?

Ln236 - Fig 4.: I would question whether Fig. 4 is needed, as it is only mentioned twice in the text. If retained, it should be used more effectively to summarize the contribution of each cloud-controlling factor and their general behavior.

Fig.6c. Ln.287. Please provide a clearer description of how the Pearson correlation coefficients are calculated as a function of monthly time lag, including how the lag is applied. If it is necessary, this information should be included in the Methods section.

Fig 6 and 7. The correlation between FCL and ONI es low and scattered and the correlation between FLC and BNI is stronger. Even though anomalies time series are a nice way to represent these findings, adding a inset or small scatter plot between those variables highlighting cool and warm phases might improve the visualization.

Ln12, 49-50,  292-294 and 295-296: Please clarify which ENSO phase is associated with the enhancement of FLC. ENSO is typically characterized by warm (El Nino) and cold (La Nina) phases, and it would be helpful to specify the phase-dependent behavior in this context.

Specific comments:

Ln12-14: The statement on interannual FLC variability would benefit from clarification of whether the SST-FLC relationship, i.e., whether SST anomalies are positively or negatively associated with FLC occurrence.

Ln18: The word “harsh” may be perceived as subjective. A more specific or objective term would improve clarity.

Ln29: The term “these clouds” is ambiguous. Please clarify whether it refers to advection fog, advected marine stratus clouds, fog, or high fog.

Ln38-48: The paragraph initially introduces the fog hotspots, but the description subsequently shifts to upwelling and the intrusion of warm tropical waters. Explaining the relationship between these processes and fog occurrence would improve the coherence of the paragraph.

Ln53: The term “non-local effects” is somewhat vague. Please clarify which processes are included under this definition and provide representative examples.

Ln56: This further highlights the need for consistent terminology as mentioned in the comment on Ln38-48. Please ensure that “marine low clouds” is either clearly defined or aligned with the previously used terminology, and adjust accordingly throughout the manuscript.

Ln69-71: The reference to Malik et al. (2026) appears somewhat out of context in this paragraph. It introduces an alternative approach for estimating cloud base height, but this method is not used in the present study and is immediately followed by its exclusion. Clarifying the purpose of this citation or better integrating it into the argument would improve the flow of the paragraph.

Fig 1. In relation to the general comment on Ln75-77, please add boxes indicating the spatial domains used for the domain-averaged calculations.

Ln189-191: The reference to a weakened South Atlantic High is not fully supported by the analyses presented, as pressure systems and subsidence are not explicitly examined. If this interpretation is based on previous literature, please include relevant references to support this statement.

Ln197: Please clarify which features are referred to as “the features discussed above”, as this is not clearly specified.

Fig. 3. It would be useful to include observed fog occurrence anomalies in order to better evaluate which configuration performs best.

Line 256-257: Please clarify the sign of the U10 and V10 trend contributions (i.e., which is positive and which is negative), as this is currently not specified despite stating that they compensate each other.

Ln323-325: This final statement reads more like a conclusion than a discussion point. Please consider moving it to the Conclusions section or remove/rephrase it.