Input-specific gating of NMDA amplification via HCN channels in mouse L2/3 pyramidal neurons

Reviewer #2 (Public review):

Summary:

This paper by Olah et al., uncovers a previously unknown role of HCN channels in shaping synaptic inputs to L2/3 cortical neurons. The authors demonstrate using slice electrophysiology and computational modeling that unlike layer 5 pyramidal neurons, L2/3 neurons have an enrichment of HCN channels in the proximal dendrites. This location provides a locus of neuromodulation for inputs onto the proximal dendrites from L4 without an influence on distal inputs from L1. the authors use pharmacology to demonstrate the effect of HCN channels on NMDA-mediated synaptic inputs from L4. The authors further demonstrate the developmental time course of HCN function in L2/3 pyramidal neurons. Taken together, this a well constructed investigation of HCN channel function and the consequences of these channels on synaptic integration in L2/3 pyramidal neurons.

Strengths:

The authors use careful, well-constrained experiments using multiple pharmacological agents to asses HCN channel contributions to synaptic integrations. The authors also use voltage-clamp to directly measure the current through HCN channels across developmental ages. The authors also provide supplemental data showing that their observation is consistent across multiple areas of the cerebral cortex.

Weaknesses:

The gradient of HCN channel function is based almost exclusively on changes in EPSP width measured at the soma. While providing strong evidence for the presence of HCN current in L2/3 neurons, there are space clamp issues related to the use of somatic whole-cell voltage clamp that should be considered in the discussion. One omission by the authors is related to cell morphology. They make a point of normalizing the current injections to cell capacitance to account for variability in neuronal morphology. It is not clear however, how, if at all, this variability would affect EPSP propagation and modulation by proximal HCN channels. This should at least be discussed. Also, if there is high variability in cell morphology, was this considered in the modeling experiments?

Reviewer #3 (Public review):

Summary:

The authors study the function of HCN channels in L2/3 pyramidal neurons, employing somatic whole-cell recordings in acute slices of visual cortex in adult mice and a bevy of technically challenging techniques. Their primary claim is a non-uniform HCN distribution across the dendritic arbor with greater density closer to the soma (roughly opposite of the gradient found in L5 PT-type neurons). The second major claim is that multiple sources of long-range excitatory input (cortical and thalamic) are differentially affected by the HCN distribution. They further describe an interesting interplay of NMDAR and HCN, serotonergic modulation of HCN, and compare HCN-related properties at 1-, 2- and 6-weeks of age. Several results are accompanied by biophysical simulations.

Strengths:

The authors collected data from both male and female mice, at an age (6-10 weeks) that permits comparison with in vivo studies, in sufficient numbers for each condition, and they collected a good number of data points for almost all figure panels. This is all the more positive, considering the demanding nature of multi-electrode recording configurations and pipette-perfusion. The main strength of the study is the question and focus.

Weaknesses:

Unfortunately, in its present form, the main claims are not adequately supported by the experimental evidence: primarily because the evidence is indirect and circumstantial, but also because multiple unusual experimental choices (along with poor presentation of results) undermine the reader's confidence. Additionally, the authors overstate the novelty of certain results and fail to cite important related publications. Some of these weaknesses can be addressed by improved analysis, statistics, resolving inconsistent data across figures, reorganizing/improving figure panels, more complete methods, improved citations, and proofreading. In particular, given the emphasis on EPSPs, the primary data (example EPSPs, overlaid conditions) should be shown much more.

However on the experimental side, addressing the reviewer's concerns would require a very substantial additional effort: direct measurement of HCN density at different points in the dendritic arbor and soma; the internal solution chosen here (K-gluconate) is reported to inhibit HCN; bath-applied cesium at the concentrations used blocks multiple potassium channels, i.e. is not selective for HCN (the authors have concerns about using the more selective blocker ZD7288, but did use it in a subset of experiments, some of which show quantitatively different results). In response to initial review, the authors performed pathway-specific synaptic stimulation, via optogenetic activation of specific long-range inputs - this approach is valuable and interesting, however the results are presented very minimally and only partially match those obtained by layer-specific electrical stimulation.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

The manuscript by Oleh et al. uses in vitro electrophysiology and compartmental modeling (via NEURON) to investigate the expression and function of HCN channels in mouse L2/3 pyramidal neurons. The authors conclude that L2/3 neurons have developmentally regulated HCN channels, the activation of which can be observed when subjected to large hyperpolarizations. They further conclude via blockade experiments that HCN channels in L2/3 neurons influence cellular excitability and pathway-specific EPSP kinetics, which can be neuromodulated. While the authors perform a wide range of slice physiology experiments, concrete evidence that L2/3 cells express functionally relevant HCN channels is limited. There are serious experimental design caveats and confounds that make drawing strong conclusions from the data difficult. Furthermore, the significance of the findings is generally unclear, given modest effect sizes and a lack of any functional relevance, either directly via in vivo experiments or indirectly via strong HCN-mediated changes in known operations/computations/functions of L2/3 neurons.

Specific points:

(1) The interpretability and impact of this manuscript are limited due to numerous methodological issues in experimental design, data collection, and analysis. The authors have not followed best practices in the field, and as such, much of the data is ambiguous and/or weak and does not support their interpretations (detailed below). Additionally, the authors fail to appropriately explain their rationale for many of their choices, making it difficult to understand why they did what they did. Furthermore, many important references appear to be missing, both in terms of contextualizing the work and in terms of approach/method. For example, the authors do not cite Kalmbach et al 2018, which performed a directly comparable set of experiments on HCN channels in L2/3 neurons of both humans and mice. This is an unacceptable omission. Additionally, the authors fail to cite prior literature regarding the specificity or lack thereof of Cs+ in blocking HCN. In describing a result, the authors state "In line with previous reports, we found that L2/3 PCs exhibited an unremarkable amount of sag at 'typical' current commands" but they then fail to cite the previous reports.

We thank the reviewer for the thorough examination of our manuscript; however, we disagree with many of the raised concerns for several reasons, as detailed here:

To address the lack of certain citations, we would like to emphasize that in the introduction section, we did initially focus on the several decades-long line of investigation into the HCN channel content of layer 2/3 pyramidal cells (L2/3 PCs), where there has undoubtedly been some controversy as to their functional contribution. We did not explicitly cite papers that claimed to find no/little HCN channels/sag- although this would be a significant list of publications from some excellent investigators, as methods used may have differed from ours leading to different interpretations. Simply stated, unless one was explicitly looking for HCN in L2/3 PCs, it might go unobserved. However, we now addressed this more clearly in the revision:

Just to take one example: in the publication mentioned by the reviewer (Kalmbach et al 2018), the investigators did not carry out voltage clamp or dynamic clamp recordings, as we did in our work here. Furthermore, the reported input resistance values in the aforementioned paper were far above other reports in mice (Routh et al. 2022, Brandalise et al 2022, Hedrick et al 2012; which were similar to our findings here), suggesting that recordings in Kalmbach were carried out at membrane potentials where HCN activation may be less available (Routh, Brager and Johnston 2022).

Another reason for some mixed findings in the field is undoubtedly due to the small/nonexistent sag in L2/3 current clamp recordings (in mice). We also observed a very small sag, which can be explained by the following: The ‘sag’ potential is a biphasic voltage response emerging from a relatively fast passive membrane response and a slower Ih activation. In L2/3 PCs, hyperpolarization-activated currents are apparently faster than previously described, and are located proximally (Figure 2 & Figure 5). Therefore, their recruitment in mouse L2/3 PCs is on a similar timescale to the passive membrane response, resulting in a more monophasic response. We now include a more full set of citations in the updated introduction section, to highlight the importance of HCN channels in L2/3 PCs in mice (and other species).

The justification for using cesium (i.e., ‘best practices’) is detailed below.

(2) A critical experimental concern in the manuscript is the reliance on cesium, a nonspecific blocker, to evaluate HCN channel function. Cesium blocks HCN channels but also acts at potassium channels (and possibly other channels as well). The authors do not acknowledge this or attempt to justify their use of Cs+ and do not cite prior work on this subject. They do not show control experiments demonstrating that the application of Cs+ in their preparation only affects Ih. Additionally, the authors write 1 mM cesium in the text but appear to use 2 mM in the figures. In later experiments, the authors switch to ZD7288, a more commonly used and generally accepted more specific blocker of HCN channels. However, they use a very high concentration, which is also known to produce off-target effects (see Chevaleyre and Castillo, 2002). To make robust conclusions, the authors should have used both blockers (at accepted/conservative concentrations) for all (or at least most) experiments. Using one blocker for some experiments and then another for different experiments is fraught with potential confounds.

To address the concerns regarding the usage of cesium to block HCN channels, we would like to state that neither cesium nor ZD-7288 are without off-target effects, however in our case the potential off-target effects of external cesium were deemed less impactful, especially concerning AP firing output experiments. Extracellular cesium has been widely accepted as a blocker of HCN channels (Lau et al. 2010, Wickenden et al. 2009, Rateau and Ropert 2005, Hemond et al. 2009, Yang et al. 2015, Matt et al. 2010). However, it is well known to act on potassium channels as well at higher concentrations, which has been demonstrated with intracellular and extracellular application (Puil et al. 1981, Fleidervish et al. 2008, Williams et al. 1991, 2008).

Although we initially performed ‘internal’ control experiments to ensure the cesium concentration was unlikely to greatly block voltage gated K+ channels during our recordings, we recognize these were not included in the original manuscript. These are detailed as follows: during our recordings cesium had no significant effect on action potential halfwidth, ruling out substantial blocking of potassium channels, nor did it affect any other aspects of suprathreshold activity (now reported in results, page 4 - line 113). Furthermore, we observed similar effects on passive properties (resting membrane potential, input resistance) following ZD-7288 as with cesium, which we now also updated in our figures (Supplementary Figure 1). We did acknowledge that ZD-7288 is a widely accepted blocker of HCN, and for this reason we carried out some of our experiments using this pharmacological agent instead of cesium.

On the other hand, ZD-7288 suffers from its own side effects, such as potential effects on sodium channels (Wu et al. 2012) and calcium channels (Sánchez-Alonso et al. 2008, Felix et al. 2003). As our aim was to provide functional evidence for the importance of HCN channels, we initially deemed these potential effects unacceptable in experiments where AP firing output (e.g., in cell-attached experiments) was measured. Nonetheless, in new experiments now included here, we found the effects of ZD and cesium on AP output were similar as shown in new Supplemental Figure 1.

Many experiments were supported by complementary findings using external cesium and ZD-7288. For example, the effect of ZD-7288 on EPSPs was confirmed by similar synaptic stimulation experiments using cesium. This is important, as synaptic inputs of L2/3 PCs are modulated by both dendritic sodium (Ferrarese et al. 2018) and calcium channels (Landau 2022), therefore the application of ZD-7288 alone may have been difficult to interpret in isolation. We thank the reviewer for bringing up this important point.

(3) A stronger case could be made that HCN is expressed in the somatic compartment of L2/3 cells if the authors had directly measured HCN-isolated currents with outside-out or nucleated patch recording (with appropriate leak subtraction and pharmacology). Whole-cell voltage-clamp in neurons with axons and/or dendrites does not work. It has been shown to produce erroneous results over and over again in the field due to well-known space clamp problems (see Rall, Spruston, Williams, etc.). The authors could have also included negative controls, such as recordings in neurons that do not express HCN or in HCN-knockout animals. Without these experiments, the authors draw a false equivalency between the effects of cesium and HCN channels, when the outcomes they describe could be driven simply by multiple other cesium-sensitive currents. Distortions are common in these preparations when attempting to study channels (see Williams and Womzy, J Neuro, 2011). In Fig 2h, cesium-sensitive currents look too large and fast to be from HCN currents alone given what the authors have shown in their earlier current clamp data. Furthermore, serious errors in leak subtraction appear to be visible in Supplementary Figure 1c. To claim that these conductances are solely from HCN may be misleading.

We disagree with the argument that “Whole-cell voltage-clamp in neurons with axons and/or dendrites does not work”. Although this method is not without its confounds (i.e. space clamp), it is still a useful initial measure as demonstrated countless times in the literature. However, the reviewer is correct that the best approach to establish the somatodendritic distribution of ion channels is by direct somatic and dendritic outside-out patches. Due to the small diameter of L2/3 PC dendrites, these experiments haven’t been carried out yet in the literature for any other ion channel either to our knowledge. Mapping this distribution electrophysiologically may be outside the scope of the current manuscript, but it was hard for us to ignore the sheer size of the Cs⁺ sensitive hyperpolarizing currents in whole cell. Thus, we will opt to report this data.

Also, we should point out that space clamp-related errors manifest in the overestimation of frequency-dependent features, such as activation kinetics, and underestimation of steady-state current amplitudes. The activation time constant of our measured currents are somewhat faster than previously reported; reducing major concerns regarding space clamp errors. Furthermore, we simply do not understand what “too large… to be from HCN currents” means. Our voltage-clamp measured currents are similar to previously reported HCN currents (Meng et al. 2011, Li 2011, Zhao et al. 2019, Yu et al. 2004, Zhang et al. 2008, Spinelli et al. 2018, Craven et al. 2006, Ying et al. 2012, Biel et al. 2009).

Furthermore, we should point out that our measured currents activated at hyperpolarized voltages, had the same voltage dependence as HCN currents, did not show inactivation, influenced both input resistance and resting membrane potential, and are blocked by low concentration extracellular cesium. Each of these features would point to HCN.

(4) The authors present current-clamp traces with some sag, a primary indicator of HCN conductance, in Figure 2. However, they do not show example traces with cesium or ZD7288 blockade. Additionally, the normalization of current injected by cellular capacitance and the lack of reporting of input resistance or estimated cellular size makes it difficult to determine how much current is actually needed to observe the sag, which is important for assessing the functional relevance of these channels. The sag ratio in controls also varies significantly without explanation (Figure 6 vs Figure 7). Could this variability be a result of genetically defined subgroups within L2/3? For example, in humans, HCN expression in L2/3 varies from superficial and deep neurons. The authors do not make an effort to investigate this. Regardless of inconsistencies in either current injection or cell type, the sag ratio appears to be rather modest and similar to what has already been reported previously in other papers.

We thank the reviewer for pointing out that our explanation for the modest sag ratio might have not been sufficient to properly understand why this measurement cannot be applied to layer 2/3 pyramidal cells. Briefly: sag potential emerges from a relatively (compared to I_h) fast passive membrane response and a slower HCN recruitment. The opposing polarity and different timescales of these two mechanisms results in a biphasic response called “sag” potential. However, if the timescale of these two mechanisms is similar, the voltage response is not predicted to be biphasic. We have shown that hyperpolarization activated currents in our preparations are fast and proximal, therefore they are recruited during the passive response (see Figure 2g.). This means that although a substantial amount of HCN currents are activated during hyperpolarization, their activation will not result in substantial sag. Therefore, sag ratio measurement is not necessarily applicable to approximate the HCN content of mouse L2/3 PCs. We would like to emphasize that sag ratio measurements are correct in case of other cell types (i.e. L5 and CA1 PCs_,_ and our aim is not to discredit the method, but rather to show that it cannot be applied similarly in the case of mouse L2/3 PCs.

Our own measurements, similar to others in the literature show that L2/3 PCs exhibit modest sag ratios, however, this does not mean that HCN is not relevant. I_h activation in L2/3 PCs does not manifest in large sag potential but rather in a continuous distortion of steady-state responses (Figure 2b.). The reviewer is correct that L2/3 PCs are non-homogenous, therefore we sampled along the entire L2/3 axis. This yielded some potential variability in our results (i.e., passive properties); yet we did not observe any cells where hyperpolarizing-activated/Cs⁺-sensitive currents could not be resolved. As structural variability of L2/3 cells does result in variability in cellular capacitance, we compensated for this variability by injecting cellular capacitance-normalized currents. Our measured cellular capacitances were in accordance with previously published values, in the range of 50-120 pF. Therefore, the injected currents were not outside frequently used values. Together, we would like to state that whether substantial sag potential is present or not, initial estimates of the HCN content for each L2/3 PC should be treated with caution.

(5) In the later experiments with ZD7288, the authors measured EPSP half-width at greater distances from the soma. However, they use minimal stimulation to evoke EPSPs at increasingly far distances from the soma. Without controlling for amplitude, the authors cannot easily distinguish between attenuation and spread from dendritic filtering and additional activation and spread from HCN blockade. At a minimum, the authors should share the variability of EPSP amplitude versus the change in EPSP half-width and/or stimulation amplitudes by distance. In general, this kind of experiment yields much clearer results if a more precise local activation of synapses is used, such as dendritic current injection, glutamate uncaging, sucrose puff, or glutamate iontophoresis. There are recording quality concerns here as well: the cell pictured in Figure 3a does not have visible dendritic spines, and a substantial amount of membrane is visible in the recording pipette. These concerns also apply to the similar developmental experiment in 6f-h, where EPSP amplitude is not controlled, and therefore, attenuation and spread by distance cannot be effectively measured. The outcome, that L2/3 cells have dendritic properties that violate cable theory, seems implausible and is more likely a result of variable amplitude by proximity.

To resolve this issue, we made a supplementary figure showing elicited amplitudes, which showed no significant distance dependence and minimal variability (new Supplementary Figure 6). We thank the reviewer for suggesting an amplitude-halfwidth comparison control (now included as new Supplementary Figure 6).). To address the issue of the non-visible spines, we would like to note that these images are of lower magnification and power to resolve them. The presence of dendritic spines was confirmed in every recorded pyramidal cell observed using 2P microscopy at higher magnification.

We would like to emphasize that although our recordings “seemingly” violated the cable theory, this is only true if we assume a completely passive condition. As shown in our manuscript, cable theory was not violated, as the presence of NMDA receptor boosting explained the observed ‘non-Rallian’ phenomenon.

(6) Minimal stimulation used for experiments in Figures 3d-i and Figures 4g-h does not resolve the half-width measurement's sensitivity to dendritic filtering, nor does cesium blockade preclude only HCN channel involvement. Example traces should be shown for all conditions in 3h; the example traces shown here do not appear to even be from the same cell. These experiments should be paired (with and without cesium/ZD). The same problem appears in Figure 4, where it is not clear that the authors performed controls and drug conditions on the same cells. 4g also lacks a scale bar, so readers cannot determine how much these measurements are affected by filtering and evoked amplitude variability. Finally, if we are to believe that minimal stimulation is used to evoke responses of single axons with 50% fail rates, NMDA receptor activation should be minimal to begin with. If the authors wish to make this claim, they need to do more precise activation of NMDA-mediated EPSPs and examine the effects of ZD7288 on these responses in the same cell. As the data is presented, it is not possible to draw the conclusion that HCN boosts NMDA-mediated responses in L2/3 neurons.

As stated in the figure legends, the control and drug application traces are from the same cell, both in figure 3 and figure 4, and the scalebar is not included as the amplitudes were normalized for clarity. We have address the effects of dendritic filtering above in answer (5), and cesium blockade above in answer (2). To reiterate, dendritic filtering alone cannot explain our observations, and cesium is often a better choice for blocking HCN channels compared to ZD-7288, which blocks sodium channels as well.

When an excitatory synaptic signal arrives onto a pyramidal cell in typical conditions, neurotransmitter sensitive receptors transmit a synaptic current to the dendritic spine. This dendritic spine is electrically isolated by the high resistance of the spine neck and due to the small membrane surface of the spine, the synaptic current can elicit remarkably large voltage changes. These voltage changes can be large enough to depolarize the spine close to zero millivolts upon even single small inputs (Jayant et al. 2016). Therefore, to state that single inputs arriving to dendritic spines cannot be large enough to recruit NMDA receptor activation is incorrect. This is further exemplified by the substantial literature showing ‘miniature’ NMDA recruitment via stochastic vesicle release alone.

(7) The quality of recordings included in the dataset has concerning variability: for example, resting membrane potentials vary by >15-20 mV and the AP threshold varies by 20 mV in controls. This is indicative of either a very wide range of genetically distinct cell types that the authors are ignoring or the inclusion of cells that are either unhealthy or have bad seals.

Although we are aware of the diversity of L2/3 PCs, resolving further layer depth differences is outside the scope of our current manuscript. However, as shown in Kalmbech et al, resting membrane potential can greatly vary (>15-20 mV) in L2/3 PCs depending on distance from pia. We acknowledge that the variance in AP threshold is large and could be due to genetically distinct cell types.

(8) The authors make no mention of blocking GABAergic signaling, so it must be assumed that it is intact for all experiments. Electrical stimulation can therefore evoke a mixture of excitatory and inhibitory responses, which may well synapse at very different locations, adding to interpretability and variability concerns.

We thank the reviewer for pointing out our lack of detail regarding the GABAergic signaling blocker SR 95531. We did include this drug in our recordings of (50Hz stim.) signal summation, so GABAergic responses did not contaminate our recordings. We now included this information in the results section (page 5) and the methods section (page 15)

(9) The investigation of serotonergic interaction with HCN channels produces modest effect sizes and suffers the same problems as described above.

We do not agree with the reviewer that 50% drop in neuronal AP firing responses (Figure 7b) was a modest effect size. Thus, we opted to keep this data in the manuscript.

(10) The computational modeling is not well described and is not biologically plausible. Persistent and transient K channels are missing. Values for other parameters are not listed. The model does not seem to follow cable theory, which, as described above, is not only implausible but is also not supported by the experimental findings.

The model was downloaded from the Cell Type Database from the Allen Institute, with only minor modifications including the addition of dendritic HCN channels and NDMA receptors- which were varied along a wide parameter space to find a ‘best fit’ to our observations. These additions were necessary to recapitulate our experimental findings. We agree the model likely does not fully recapitulate all aspects of the dendrites, which as we hope to convey in this manuscript, are not fully resolved in mouse L2/3 PCs. This is a previously published neuronal model, and despite its potential shortcomings, is one among a handful of open-source neuronal models of a fully reconstructed L2/3 PC.

Reviewer #2 (Public Review):

Summary:

This paper by Olah et al. uncovers a previously unknown role of HCN channels in shaping synaptic inputs to L2/3 cortical neurons. The authors demonstrate using slice electrophysiology and computational modeling that, unlike layer 5 pyramidal neurons, L2/3 neurons have an enrichment of HCN channels in the proximal dendrites. This location provides a locus of neuromodulation for inputs onto the proximal dendrites from L4 without an influence on distal inputs from L1. The authors use pharmacology to demonstrate the effect of HCN channels on NMDA-mediated synaptic inputs from L4. The authors further demonstrate the developmental time course of HCN function in L2/3 pyramidal neurons. Taken together, this a well-constructed investigation of HCN channel function and the consequences of these channels on synaptic integration in L2/3 pyramidal neurons.

Strengths:

The authors use careful, well-constrained experiments using multiple pharmacological agents to asses HCN channel contributions to synaptic integrations. The authors also use a voltage clamp to directly measure the current through HCN channels across developmental ages. The authors also provide supplemental data showing that their observation is consistent across multiple areas of the cerebral cortex.

Weaknesses:

The gradient of the HCN channel function is based almost exclusively on changes in EPSP width measured at the soma. While providing strong evidence for the presence of HCN current in L2/3 neurons, there are space clamp issues related to the use of somatic whole-cell voltage clamps that should be considered in the discussion.

We thank the reviewer for pointing out our careful and well-constrained experiments and for making suggestions. The potential effects of space clamp errors are detailed in the extended explanations under Reviewer 1, Specific points (3).

Reviewer #3 (Public Review):

Summary:

The authors study the function of HCN channels in L2/3 pyramidal neurons, employing somatic whole-cell recordings in acute slices of visual cortex in adult mice and a bevy of technically challenging techniques. Their primary claim is a non-uniform HCN distribution across the dendritic arbor with a greater density closer to the soma (roughly opposite of the gradient found in L5 PT-type neurons). The second major claim is that multiple sources of long-range excitatory input (cortical and thalamic) are differentially affected by the HCN distribution. They further describe an interesting interplay of NMDAR and HCN, serotonergic modulation of HCN, and compare HCN-related properties at 1, 2 and 6 weeks of age. Several results are supported by biophysical simulations.

Strengths:

The authors collected data from both male and female mice, at an age (6-10 weeks) that permits comparison with in vivo studies, in sufficient numbers for each condition, and they collected a good number of data points for almost all figure panels. This is all the more positive, considering the demanding nature of multi-electrode recording configurations and pipette-perfusion. The main strength of the study is the question and focus.

Weaknesses:

Unfortunately, in its present form, the main claims are not adequately supported by the experimental evidence: primarily because the evidence is indirect and circumstantial, but also because multiple unusual experimental choices (along with poor presentation of results) undermine the reader's confidence. Additionally, the authors overstate the novelty of certain results and fail to cite important related publications. Some of these weaknesses can be addressed by improved analysis and statistics, resolving inconsistent data across figures, reorganizing/improving figure panels, more complete methods, improved citations, and proofreading. In particular, given the emphasis on EPSPs, the primary data (for example EPSPs, overlaid conditions) should be shown much more.

However, on the experimental side, addressing the reviewer's concerns would require a very substantial additional effort: direct measurement of HCN density at different points in the dendritic arbor and soma; the internal solution chosen here (K-gluconate) is reported to inhibit HCN; bath-applied cesium at the concentrations used blocks multiple potassium channels, i.e. is not selective for HCN (the fact that the more selective blocker ZD7288 was used in a subset of experiments makes the choice of Cs+ as the primary blocker all the more curious); pathway-specific synaptic stimulation, for example via optogenetic activation of specific long-range inputs, to complement / support / verify the layer-specific electrical stimulation.

We thank the reviewer for their very careful examination of our manuscript and helpful suggestions. We addressed the concerns raised in the review and presented more raw traces in our figures. Although direct dendritic HCN mapping measurements are outside the scope of the current manuscript due to the morphological constraints presented by L2/3 PCs (which explains why no other full dendritic nonlinearity distribution has been described in L2/3 PCs with this method), we nonetheless supplemented our manuscript with additional suggested experiments as suggested. For example, we included the excellent suggestion of pathway-specific optogenetic stimulation to further validate the disparate effect of HCN channels for distal and proximal inputs. We agree that ZD-7288 is a widely accepted blocker of HCN channels. However, the off-target effects on sodium channels may have significantly confounded our measurements of AP output using extracellular stimulation. Therefore, we chose low concentration cesium as the primary blocker for those experiments, but now validated several other Cs⁺-based results with ZD-7288 as well.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

I have some issues that need clarification or correction.

(1) On page 3, line 90, the authors state "We found that bath application of Cs+ (1mM)..." but the methods and Figure 1 state "2mM Cs+". Please check and correct.

Correct, typo corrected.

(2) Related to Cs+ application, the methods state that "CsMeSO4 (2mM) was bath applied..." Is this correct? CsMeSO4 is typically used intracellularly while CsCl is used extracellularly. If so, please justify. If not, please correct.

It is correct. The justification for not using CsCl selectively extracellularly is that introducing intracellular chloride ions can significantly alter basic biophysical properties, unrelated to the cesium effect. However, no similar distinction has been made for CsMeSO4, which would exclude the use of this drug extracellularly.

(3) The authors normalize the current injections by cell capacitance (pA/pF). Was this done because there is a significant variance in cell morphology? A bit of justification for why the authors chose to normalize the current injection this way would help. If there is significant variation in cell capacitance across cells (or developmental ages), the authors could also include these data.

Indeed, we choose to normalize current injection to cellular capacitance due to the markedly different morphology of deep and superficial L2/3 PCs. Deeper L2/3 PCs have a pronounced apical branch, closely resembling other pyramidal cell types such as L5 PCs, while superficial L2/3 PC lack a thick main apical branch and instead are equipped with multiple, thinner apical dendrites. This morphological variation would yield an inherent bias in several of the reported measurements, therefore we corrected for it by normalizing current injection to cellular capacitance, similar to our previous recent publications (Olah, Goettemoeller et al., 2022, Goettemoeller et al. 2024, Kumar et al. 2024).

(4) On page 15, line 445, the section heading is "PV cell NEURON modeling". Is this a typo? The models are of L2/3 pyramidal neurons, correct?

Correct, typo corrected.

(5) Figures 3F and 3I are plots of the voltage integral for different inputs before and after Cs+. The y-axis label units are "pA*ms". This should be "mV*ms" for a voltage integral.

Correct, typo corrected.

(6) On page 9, line 273, the text reads "Voltage clamp experiments revealed that the rectification of steady-state voltage responses to hyperpolarizing current injection was amplified with 5-CT (Fig. 7c)". Both the text and Figure 7C describe current clamp, not voltage clamp, recordings. Please check and correct.

Correct, typo corrected.

(7) Figure 2i looks to be a normalized conductance vs voltage (i.e. activation) plot. The y-axis shows 0-1 but the units are in nS. Is that a coincidence or an error?

Correct, typo corrected.

Reviewer #3 (Recommendations For The Authors):

This is your paper. My comments are my own opinion, I don't expect you to agree or to respond. But I hope that what I wrote below will help you to understand my perspective.

Please pardon my directness (and sheer volume) in this section - I have a lot of notes/thoughts and hope you may find some of them helpful. My high-level comments are unfortunately rather critical, and in (small) part that is because I encountered too many errors/typos/ambiguities in figures, legend, and text. I expect many would be caught with good proofreading, but uncorrected caused confusion on my part, or an inability to interpret your figures with confidence, given some ambiguity.

The paper reads a bit like patchwork - likely a result of many "helpful" reviewers who came before me. Consider starting with and focusing on the synaptic findings, expanding the number of figures and panels dedicated to that, showing example traces for all conditions, and giving yourself the space to portray these complex experiments and results. While I'm not a fan of a large number of supplemental figures, I feel you could move the "extra" results to the supplementals to improve the focus and get right to the meat of it.

For me, the main concern is that the evidence you present for the non-uniform HCN distribution is rather indirect. Ideally, I'd like to see patch recordings from various dendritic locations (as others have done in rats, at least; I'm not sure if L2/3 mice have had such conductance density measurements made in basal and apical dendrites). Otherwise, perhaps optical mapping, either functional or via staining. I also mention some concerns about the choice of internal and cesium. More generally, I want to see more primary data (traces), in particular for the big synaptic findings (non-uniform, L1-vs-L4 differences, NMDAR).

We thank the reviewer for the helpful suggestions. Indeed, direct patch clamp recording is widely considered to be the best method to identify dendritic ion channel distribution, however, we choose an in silico approach instead, for several reasons. Undoubtedly, one of the main reasons to omit direct dendritic recordings was that due to the uniquely narrow apical dendrites this method is extremely challenging, with no previous examples in the literature where isolated dendritic outside-out patch recordings were achieved from this cell type. However, there are theoretical considerations as well. In primates, it has been demonstrated that HCN1 channels are concentrated on dendritic spines (Datta et al., 2023) therefore direct outside-out recordings are not adequate in these circumstances. In future experiments we could directly target L2/3 PC dendrites for outside out recordings in order to resolve dendritic nonlinearity distribution, although a cell-attached methodology may be better suited due to the HCN biophysical properties being closely regulated by intracellular signaling pathways.

The introduction and Figures 1 and 2 are not so interesting and not entirely accurate: L2/3 do not have "abundant" HCN, nor is there an actual controversy about whether they have HCN. It's been clear (published) for years that they have about the same as all other non-PT neocortical pyramidal neurons (see e.g. Larkum 2007; Sheets 2011). Your own Figure 1A has a logarithmic scale and shows L2/3 as having the lowest expression (?) of all pyramidals and roughly 10x lower than L5 PT, but the text says "comparable", which is misleading.

We thank the reviewer for this comment. Although there are sporadic reports in the literature about the HCN content of L2/3 PCs, most of these publications arrive to the same conclusion from the negligible sag potential (as the mentioned Larkum et al., 2007 publication); namely that L2/3 PCs do not contain significant amount of HCN channels. We have shown with voltage and current clamp recordings that this assumption is false, as sag potential is not a reliable indicator of HCN content in L2/3 PCs. With the term “controversial” we aimed to highlight the different conclusions of functional investigations (e.g. Sheets et al., 2011) and sag potential recordings (e.g. Larkum et al., 2007), regarding the importance of HCN channels in L2/3 PCs.

Non-uniform HCN with distal lower density has already been published for a (rare) pyramidal neuron in CA1 (Bullis 2007), similar to what you found in L2/3, and different from the main CA1 population.

We thank the reviewer for this suggestion. We have now included the mentioned citation in the introduction section (page 3).

Express sag as a ratio or percentage, consistently. Figure out why in Figure 7 the average sag ratio is 0.02 while in Fig. S1 it is 0.07 (for V1) - that is a massive difference.

The calculation of sag ratio is consistent across the manuscript (at -6pA.pF), except for experiments depicted in Fig. 7 where sag ratio was calculated from -2pA/pF steps. Explanation below:

Sag should be measured at a common membrane potential, with each neuron receiving a current pulse appropriate to reach that potential. Your approach of capacitance-based may allow for the same, but it is not clear which responses are used to calculate a single sag value per cell (as in Figure 2d).

Thank you, we now included this info in the methods section. Sag potential was measured at the -6 pA/pF step peak voltage, except for Fig. 7 as noted above. We have now included this discrepancy detail in the methods section (page 14 ). These recordings in Fig. 7 took significantly longer than any other recording in the manuscript, as it took a considerable time to reach steady-state response from 5-CT application. -6pA/pF is a current injection in the range of 400-800 pA, which was proven to be too severe for continued application in cells after more than an hour of recording. Accordingly, we decided to lower the hyperpolarizing current step in these recordings. The absolute value of sag is thus different in Fig. 7, but nonetheless the 5-CT effect was still significant. Notably, we probably wouldn’t have noticed the small sag in L2/3 here (and thus the entire study), save for the fact that we looked at -6pA/pF to begin.

In a paper focused on HCN, I would have liked to see resonance curves in the passive characterization.

We thank the reviewer for the suggestion. Resonance curves can indeed provide useful insights into the impact of HCN on a cell’s physiological behavior, however, these experiments are outside the scope of our current manuscript as without in vivo recordings, resonance curves do not contribute to the manuscript in our opinion.

How did you identify L2/3? Did you target cells in L2 or L3 or in the middle, or did you sample across the full layer width for each condition? A quantitative diagram showing where you patched (soma) and where you stimulated (L1, L4) with actual measurements, would be helpful (supplemental perhaps). You mention in the text that some L2/3 don't have a tuft, suggesting some variability in morphology - some info on this would be useful, i.e. since you did fill at least some of the neurons (eg 3A), how similar/different are the dendritic arbors?

We sampled the entire L2/3 region during our recordings. It has been published that deep and superficial L2/3 PCs are markedly different in their morphology, and a recent publication (Brandelise et al. 2023) has even separated these two subpopulations to broad-tufted and slender tufted pyramidal cells, which receive distinct subcortical inputs. Although this differentiation opens exciting avenues for future research, examining potential layer gradients in our dataset would warrant significantly higher sample numbers and is currently out of the scope of our manuscript.

Distal vs proximal: this could use more clarification, considering how central it is to your results. What about a synapse on a basal dendrite, but 150 or 200 um from the soma, is that considered proximal? Is the distance to the soma you report measured along the 3D dendrite, along the 2D dendrite, as a straight line to the soma, or just relative to some layers or cortical markers? (I apologize if I missed this).

We thank the reviewer for pointing out the missing description in the results section. We have amended this oversight (p15). Furthermore, although deeper L3 PCs have characteristic apical and basal dendritic branches, when recordings were made from more superficial L2 cells, a large portion of their dendrites extended radially, which made their classification ambiguous. Therefore, we did not use “apical” and “basal” terminology in the paper to avoid confusion. Distances were measured along the 3D reconstructed surface of the recovered pyramidal cells. This information is now included in the methods.

Line 445, "PV cell NEURON modeling" ... hmm. Everyone re-uses methods sections to some degree, but this is not confidence-inspiring, and also not from a proofreading perspective.

We have corrected the typo.

It seems that you constructed a new HCN NEURON mechanism when several have been published/reviewed already. Please explain your reasons or at least comment on the differences.

There are slight differences in our model compared to previously published models. Nevertheless, we took a previously published HCN model as a base (Gasparini et al, 2004), and created our own model to fit our whole-cell voltage clamp recordings.

Bath-applied Cs+ can change synaptic transmission (in the hippocampus; Chevaleyre 2002). But also ZD7288 has some such effects. Also, see (Harris 1995) for a Cs+ and ZD7288 comparison. As well as (Harris 1994) for more Cs+ side-effects (it broadens APs, etc). Bath-applied blockers may affect both long-range and local synapses in your recordings, via K-channels or perhaps presynaptic HCN (though I am aware of your Fig. 1e). Since you can do intracellular perfusion, you could apply ZD7288 postsynaptically (Sheets 2011), an elegant solution.

We thank the reviewer for the suggestion. We were aware of the potential presynaptic effects of cesium (i.e., presynaptic Kv or other channel effects) and did measure PPR after cesium application (Fig. 1h), noting no effect. At Cs⁺ concentrations used here, we now also include new data in the results showing no effect on somatically recorded AP waveform (i.e., representative of a Kv channel effect). As stated earlier for reviewer 1, we now performed additional experiments using either cesium or ZD-7288 for comparison (e.g., see updated Fig. 1; Supplementary Figure 1; Fig. 3b-e). Intracellular ZD re-perfusion is an elegant solution which we will absolutely consider in future experiments.

K-Gluconate is reported to inhibit Ih (Velumian 1997), consider at least some control experiments with a different internal for the main synaptic finding - maybe you'll find no big change ...

We thank the reviewer for the suggestion. Although K-Gluconate can inhibit HCN current, the use of this intracellular solution is often used in the literature to measure this current (Huang & Trussel 2014). We have chosen this intracellular solution to improve recording stability.

(Biel 2009) is a very comprehensive HCN review, you may find it useful.

We thank the reviewer for bringing this to our attention, we have now included the citation in the introduction.

"Hidden" in your title seems too much.

We changed the title to more accurately describe our findings and removed ‘hidden’.

While I'm glad you didn't record at room temperature, the choice of 30C seems a bit unfortunate - if you go to the trouble to heat the bath, why not at least 34C, which is reasonably standard as an approximation for physiological temperature?

We thank the reviewer for pointing this out. The choice of 30C was made to approach physiological temperature levels, while preserving the slices for extended amounts of time which is a standard approach. Future experiments in vivo be performed to further understand the naturalistic relevance at ~37C.

Line 506: do you mean "Hz" here? It's not a frequency, is it? I think it's a unitless ratio?

Correct, we have amended the typo.

Line 95: you have not shown that HCN is "essential" for "excess" AP firing.

We have corrected the phrasing, we agree.

Fig. 2b,c: is this data from a single example neuron, maybe the same neuron as in 2a? Or from all recorded neurons pooled?

The data is from several recorded cells pooled.

Fig. 3 (important figure):

Why did you not use a paired test for panels e and f? You have the same number of neurons for each condition and the expectation is that you record each neuron in control and then in cesium condition, which would be a paired comparison. Or did you record only 1 condition per neuron?

This figure presents your main finding (in my opinion). You should show examples of the synaptic responses, i.e. raw traces, for each condition and panel, and overlaid in such a way that the reader can immediately see the relevant comparison - it's worth the space it requires.

We thank the reviewer for the suggestions. Traces are only overlaid in the paper when they come from the same cell. For Fig. 3d-i, EPSPs in every neuron were evoked in 2-3 different locations (i.e., 1-2 ‘L4’ locations for Type-I and Type-II synapses, and one ‘L1’ location in each) with the same stimulation pipette and one pharmacological condition per cell. Therefore two-sample t-test were used since the control and cesium conditions came from separate cells (i.e., separate observations). This was necessary, as we can never assume that the stimulating electrode can return back to the same synapse after moving it. We were not comfortable with showing overlaid traces from different cells, however, we did show representative traces from control and the Cs⁺ conditions in Fig. 3h. Complementary ZD-7288 experiments can be found on panel b and c, where we did perform within-cell pharmacology (and thus used paired t-tests) from one stimulation area/cell. We hope these complementary experiments increase overall confidence as neither pharmacological approach is 100% without off-target effects. We now also included more overlaid traces where appropriate (i.e., Fig. 3b, and in the new Fig. 3k experiments using within-cell pharmacology comparisons). We do realize these complementary approaches could cause confusion to the reader, and have now done our best to make the slightly different approaches in this Figure clearer in the results section.

Consider repeating at least some of these critical experiments with ZD7288 instead of Cs+ (and not K-gluc), or even with ZD7288 pipette perfusion, if it's technically feasible here.

We thank the reviewer for the suggestions. Although many of our recordings using Cs⁺ already had complementary experiments (such as synaptic experiments Figure 3e vs Figure 3b), we recognize the need to extend the manuscript with more ZD-7288 experiments. We have now extended Figure 1 with three panels (Figure 1 c,d,e), which recapitulates a fundamental finding, the change in overall excitability upon HCN channel blockade, using ZD-7288 as well.

Fig. 3a, why show a schematic (and weirdly scaled) stimulating electrode? Don't you have a BF photo showing the actual stimulating electrode, which you could trace to scale or overlay? Could you use this panel to indicate what counts as "distal" and what as "proximal", visually?

The stimulating electrode was unfortunately not filled with florescent materials, therefore it was not captured during the z-stack.

Fig. 3b: is the y-axis labeled correctly? A "100% change" would mean a doubling, but based on the data points here I think y=100% means "no change"?

The scale is labeled correctly, 100% means doubling.

Fig. 3b, c: again, show traces representing distal and proximal, not just one example (without telling us how far it was). And use those traces to illustrate the half-width measurement, which may be non-trivial.

We have extended Figure 3b with an inset showing the effect of ZD-7288 on a proximal stimulating site. The legend now includes additional information indicating stimulating location 28 µm away from the soma in control conditions (black trace) and upon Z-7288 application (green trace).

Line 543, 549: it seems you swapped labels "h" and "i"?

Typo corrected.

Fig. 4b: to me, MK-801 only *partially* blocks amplification, but in the text L198 you write "abolish".

We thank the reviewer for pointing this out. Indeed, there are several other subthreshold mechanisms that are still intact after pipette perfusion, which can cause amplification. We have now clarified this in the text (p7).

Fig. 4e,f: what is the message? Uniform NMDAR? The red asterisk in (e) is at a proximal/distal ratio of roughly 1. I don't understand the meaning of the asterisk (the legend is too basic) and I'm surprised to see a ratio of 1 as the best fit, and also that the red asterisk is at a dendritic distance of 0 um in (f). This could use more explanation (if you feel it's relevant).

We thank the reviewer for pointing this out. We have now included a better explanation in the results and figure legend. We have also updated the figure to make it clearer and added model traces in Fig. 4f, which correspond to example data from slices in Fig. 4g (both green). The graph suggests nonuniform, proximally abundant NMDA distribution. The color coding corresponds to the proximal EPSP halfwidth divided by distal EPSP halfwidth. It is true that the dendritic distance ‘center’ was best-fit very close to the soma, but also note the dispersion (distribution) half-width was >150mm, so there is quite a significant dendritic spread despite the proximal bias prediction. Based on this model there is likely NMDA spread throughout the entire dendrite, but biased proximally. Naturally, future work will need to map this at the spine level so this is currently an oversimplification. Nonetheless, a proximal NMDA bias was necessary to recapitulate findings from Fig. 3, and additional slice recordings in Fig. 4 were consistent with this interpretation.

Fig. 4g: I feel your choice of which traces to overlay is focusing on the wrong question. As the reader, what I want to see here is an overlay of all 4 conditions for one pathway. If this is a sequential recording in a single cell (Cs, Cs+MK801, wash out Cs, MK801), then the overlay would be ideal and need not be scaled. Otherwise, you can scale it. But the L1/L4 comparison does not seem appropriate to me. I find myself trying to imagine what all the dark lines would look like overlaid, and all the light lines overlaid separately. Also, the time axis is missing from this panel. Consider a subtraction of traces (if appropriate).

In these recordings, all EPSPs cells were measured using a stimulating electrode that was moved between L1 and L4 (only once, to keep the exact input consistent) to measure the different inputs in a single neuron. In separate sets of experiments, the same method was used but in the presence of Cs⁺, Cs⁺ + MK-801, or MK-801 alone. This was the most controlled method in our hands for this type of approach, as drug wash outs were either impractical or not possible. Overlaying four traces would have presented a more cluttered image, and were not actually performed experimentally. As our aim was to resolve the proximal-distal halfwidth relationship, therefore we deemed the within-cell L1 vs. L4 comparison appropriate. We have nonetheless added model traces in Fig. 4f, which correspond to example data from slices in Fig. 4g (both green). The bar graphs should serve also serve to illustrate the input-specific relationship- i.e., that the only time the L1 and L4 EPSP relationship was inverted was in the presence of Cs⁺ (green bars) and that this effect was occluded with simultaneous MK-801 in the pipette (red bars).

Line 579: should "hyperpolarized" be depolarized?

Corrected

Fig. 5a: it looks like the HCN density is high in the most basal dendrites (black curve above), then drops towards the soma, then rises again in the apicals (red curve). Is that indeed how the density was modeled? If so, this is completely at odds with the impression I received from reading your text and experimental data - there, "proximal" seems to mean where the L4 axons are, and "distal" seems to mean where the L1 axons are, in other words, high HCN towards the pia and low HCN towards the white matter. But this diagram suggests a biphasic hill-valley-hill distribution of HCN (meaning there is a second "distal" region below the soma). In that case, would the laterally-distant basal dendrites also be considered distal? How does the model implement the distribution - is it 1D, 2D or 3D? As you can probably tell, this figure raised more questions for me and made me wonder why I don't have a better understanding yet of your definitions.

We thank the reviewer for pointing this out. We agree our initial cartoon of the parameter fitting procedure was not accurate and should have just been depicted a single ‘curve’. We have now simplified it to better demonstrate what the model is testing, and also made the terms more consistent and accurate. There is no ‘second’ region in the model. We hope this better illustrates it now. We also edited the legend to be clearer. Because the model description in Fig. 4d suffered from similar shortcomings, we also modified it accordingly as well as the figure legend there.

Fig. 5b: why is the best fit at a proximal/distal ratio of 1, yet sigma is 50 um?

Proximal/distal bias on this figure was fitted to 0.985 (prox/distal ratio) as we modeled control conditions, with intact NDMA and HCN channels, which closely approximated the control recording comparisons.

Fig. 6h, Line 662: "vs CsMeSO4 ... for putative LGN events" The panel shows proximal vs distal, not control vs Cs+. What's going on here?

Typo corrected.

Fig. 7e: the ctrl sag ratio here averages 0.02, while in Fig. S1 the average (for V1 and others) is about 0.07. Please refer to our answer given to the previous question regarding sag ratio measurements. Briefly, recordings made with 5-CT application were made using a less severe, -2 pA/pF current injection to test seg responses. This more modest hyperpolarization activated less HCN channels, therefore the sag ratio is lower compared to previously reported datapoints.

We have included this explanation in the methods section (page 14)

Now hear you are using a paired test for this pharmacology, but you didn't previously (see my earlier comments/questions).

Paired t-test were used for these experiments as these control and test datapoints came from the same cell. Cells were recorded in control conditions, and after drug application.

Line 137: single-axon activation: but cortical axons make multi-synaptic contacts, at least for certain types of pre- and post-synaptic neurons, and (e.g. in L5-L5 pairs) those contacts can be distributed across the entire dendritic arbor. In other words, it's possible that when you stimulate in L1, you activate local axons, and the signal could then propagate to multiple synaptic contact locations, some being distal and some proximal. Maybe you have reasons to believe you're able to avoid this?

We thank the reviewer for this question. Cortical axons often make distributed contacts, however, top-down and bottom-up pathways innervating L2/3 PCs are at least somewhat restricted to L2/3/L4 and L1, respectively (Shen et al. 2022, Sermet et al. 2019). Therefore, due to the lack evidence suggesting a heavily mixed topographical distribution for top-down and bottom-up inputs, we have reason to believe that L1 stimulation will result in mainly distal input recruitment, while L4 stimulation will mainly excite proximal dendritic regions. The resolution of our experiments was also improved by the minimal stimulation and visual guidance (subset of experiments) of the stimulation. Furthermore, new optogenetic experiments stimulating LGN and LM axons, which have been anatomically defined previously as biased to deeper layers and L1, respectively, were now also performed (Fig. 3j-l) with analogous cesium effects as our local electrical stimulation experiments. Future work using varying optogenetic stimulation parameters will expand on this.

L140: "previous reports" ==> citation needed.

We have inserted the citation needed.

L149: "arriving to layer 1"; but I think earlier you noted that some or many L2/3 neurons lack a dendritic tuft; do they all nevertheless have dendrites in L1? Note that cortico-cortical long-range axons still need to pass through all cortical layers on their way up to L1.

We thank the reviewer for the question. Although the more superficial L2/3 PCs lack distinct apical tuft, their dendrites reach the pia similarly to deeper L2/3 PCs. All of our recorded and post-hoc recovered cells had dendrites in L1, except in cases where they were clearly cut during the slicing procedure, which cells were occluded from the study.

When you write "L4 axons" or "L4 inputs", do you specifically mean long-range thalamic axons? Or axons from local L4 neurons? What about axons in L4 that originate from L5 pyramidal neurons?

In case of ‘L4’ axons, we cannot disambiguate these inputs a priori, as they are both part of the bottom-up pathway, and are possibly experimentally indistinguishable. Even with restricted opto LGN stimulation, disynaptic inputs via L4 PCs cannot be completely ruled out under our conditions. On the other hand, the probability of L5 PC axons to terminate on L2/3 PCs is exceedingly low (single reported connection out of 1145 potential connections; Hage et al. 2022). We did find two clearly different synaptic subpopulations (Supp. Fig 3) in L4- which was tempting to classify as one or the other. However we felt there was not enough evidence in the literature as well as our additional optogenetic experiments to make a classification on the source of these different L4 inputs. Thus we deemed them as Type-I or Type-II for now.

Do you inject more holding current to compensate for the resting membrane potential when Cs+ or ZD7288 is in the bath?

We thank the reviewer for the question. We did not inject a compensatory current, as we wanted to investigate the dual, physiologically relevant action of HCN channels (George et al. 2009)

I'd like to see distributions (histograms) of L4 and L1 EPSP amplitudes, under control conditions and ideally also under HCN block.

We have now extended the manuscript with a supplementary figure (Supplementary Figure 6) to show that EPSP peak was not distance dependent in control conditions, and there was no relationship between peak and halfwidth in our dataset.

Line 186, custom pipette perfusion: why not use this for internal ZD7288, to make it cell-specific?

We thank the reviewer for the question, this is a good point. In future work we will consider this when applicable. It is certainly a way to control for bath application confounds in many ways.

L205: "recapitulate our experimental findings" - which findings do you mean? I think a bit of explanation/referencing would help.

Corrected.

Line 210: L4-evoked were narrower than L1-evoked: is this not expected based on filtering?

We thank the reviewer for pointing this out, the word “Intriguingly” has been omitted.

Line 231 and 235: "in L5 PCs" should be restricted to L5 PT-type PCs.

We have corrected this throughout the manuscript.

Neuromodulation, Fig. 7, L263-282: the neuromodulation finding is interesting. However, a bit like the developmental figure, it feels "tacked on" and the transition feels a bit awkward. I think you may want to discuss/cite more of the existing literature on neuromodulatory interactions with HCN (not just L2/3). Most importantly, what I feel is missing is a connection to your main finding, namely L1 and L4 inputs. Does serotonergic neuromodulation put L1 and L4 back on equal footing, or does it exaggerate the differences?

We thank the reviewer for the question. We agree with the reviewer that Figure 7 does not give a complete picture about how the adult brain can capitalize on this channel distribution, as our intention was to show that HCN channels are not a stationary feature of L2/3 PC, but a feature which can be regulated developmentally and even in the adult brain via neuromodulation. In other words, the subthreshold NMDA boosting we observed can be gated by HCN, depending on developmental stage and/or neuromodulatory state of the system. We have now added some brief language to better introduce the transition and its relevance to the current study in the results (p8), and discussed the implications in the discussion section of the original manuscript.

General comment: different types/sources of synapses may have different EPSP kinetics. I feel this is not mentioned/discussed adequately, considering your emphasis on EPSPs/HCN.

See points above on input-specific synaptic diversity.

Line 319/320: enriched distal HCN is found in L5 PT-type, not in all L5 PCs.

Corrected

L320: CA1 reportedly has a subset of pyramidal neurons that have higher proximal HCN than distal (I gave the citation above). In light of that, I think "unprecedented" is an overstatement.

Corrected.

Methods:

L367: What form of anesthesia was used?

Amended.

Which brain areas, and how?

Amended.

Why did you first hold slices at 34C, but during recording hold at 30C?

We held the slices at 34C to accelerate the degradation of superficial damaged parts of the slice, which is in line with currently used acute slice preparation methodologies, regardless of the subsequent recording temperature.

Pipette resistance/tip size?

Amended.

Cell-attached recordings (L385): provide details of recordings. What was the command potential (fixed value, or did you adjust it per neuron by some criteria)?

Amended.

What type of stimulating electrode did you use? If glass, what solution is inside, and what tip size?

We thank the reviewer for pointing these out, the specific points were added to the methods section.

L392/393: you adjusted the holding (bias) current to sit at -80 mV. What were the range and max values of holding current? Was -80 mV the "raw" potential, or did it account for liquid junction? If you did not account for liquid junction potential, then would -80 in your hands effectively be between -95 and -90 mV? That seems unusually hyperpolarized.

All cells were held with bias holding currents between -50 pA and 150 pA. To be clear, as mentioned below, we did not change the bias current after any drug applications. We did not correct for liquid junction potential, and cells were ‘held‘ with bias current at -80 mV as during our recordings, as 1) this value was apparently close to the RMP (i.e. little bias current needed at this voltage on average) (Fig. 2e) and 2) to keep consistent conditions across recordings. The uncorrected -80 mV is in the range of previously reported membrane potential values both in vivo and in vitro (Svoboda et al. 1999, Oswald et al. 2008, Luo et al. 2017), which found the (corrected) RMP to be below -80mV. Naturally this will not reflect every in vivo condition completely and further investigation using naturalistic conditions in the future are warranted.

Did you adjust the bias current during/after pharmacology?

Bias current was not adjusted in order to resolve the effect on resting membrane potential.

L398: sag calculation could use better explanation: how did you combine/analyze multiple steps from a single neuron when calculating sag? Did you choose one level (how) or did you average across step sizes or ...?

Sag ratio was measured at -6 pA/pF current step except for one set of experiments in Fig. 7. Methods section was amended.

L400, 401: 10 uM Alexa-594 or 30 um Alexa-594, which is correct?

10 µM is correct, typo was corrected

L445: "PV cell" seems like a typo?

Typo is corrected.

L450: "altered", please describe the algorithm or manual process.

Alterations were made manually.

L474: NDMA, typo.

Typo is fixed.

L474: "were adjusted", again please describe the process.

Adjustments were made by a grid-search algorithm.

Biel, M., Wahl-Schott, C., Michalakis, S., & Zong, X. (2009). Hyperpolarization-activated cation channels: from genes to function. Physiological reviews, 89(3), 847-885. https://journals.physiology.org/doi/full/10.1152/physrev.00029.2008 - (very comprehensive review of HCN)

Bullis JB, Jones TD, Poolos NP. Reversed somatodendritic I(h) gradient in a class of rat hippocampal neurons with pyramidal morphology. J Physiol. 2007 Mar 1;579(Pt 2):431-43. doi: 10.1113/jphysiol.2006.123836. Epub 2006 Dec 21. PMID: 17185334; PMCID: PMC2075407. https://physoc.onlinelibrary.wiley.com/doi/full/10.1113/jphysiol.2006.123836 - (CA1 subset (PLPs) have a reversed HCN gradient; cell-attached patches, NMDAR)

Velumian AA, Zhang L, Pennefather P, Carlen PL. Reversible inhibition of IK, IAHP, Ih, and ICa currents by internally applied gluconate in rat hippocampal pyramidal neurones. Pflugers Arch. 1997 Jan;433(3):343-50. doi: 10.1007/s004240050286. PMID: 9064651. https://link.springer.com/article/10.1007/s004240050286 - (K-Gluc internal inhibits HCN)

Sheets, P. L., Suter, B. A., Kiritani, T., Chan, C. S., Surmeier, D. J., & Shepherd, G. M. (2011). Corticospinal-specific HCN expression in mouse motor cortex: I h-dependent synaptic integration as a candidate microcircuit mechanism involved in motor control. Journal of neurophysiology, 106(5), 2216-2231. https://journals.physiology.org/doi/full/10.1152/jn.00232.2011 - (L2/3 IT have same sag ratio as all other non-PT pyramidals, roughly 5% (vs 20% PT); intracellular ZD7288 used at 10 or 25 um)

Harris NC, Constanti A. Mechanism of block by ZD 7288 of the hyperpolarization-activated inward rectifying current in guinea pig substantia nigra neurons in vitro. J Neurophysiol. 1995 Dec;74(6):2366-78. doi: 10.1152/jn.1995.74.6.2366. PMID: 8747199. https://journals.physiology.org/doi/abs/10.1152/jn.1995.74.6.2366 - (comparison Cs+ and ZD7288)

Harris, N. C., Libri, V., & Constanti, A. (1994). Selective blockade of the hyperpolarization-activated cationic current (Ih) in guinea pig substantia nigra pars compacta neurones by a novel bradycardic agent, Zeneca ZM 227189. Neuroscience letters, 176(2), 221-225. https://www.sciencedirect.com/science/article/abs/pii/0304394094900876 - (Cs+ is not HCN-selective; it also broadens APs, reduces the AHP)

Chevaleyre, V., & Castillo, P. E. (2002). Assessing the role of Ih channels in synaptic transmission and mossy fiber LTP. Proceedings of the National Academy of Sciences, 99(14), 9538-9543. https://pnas.org/doi/abs/10.1073/pnas.142213199 - (Cs+ blocks K channels, increases transmitter release; but also ZD7288 affects synaptic transmission)

Thank you