Independent theta phase coding accounts for CA1 population sequences and enables flexible remapping
Peer review process
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Decision letter
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Frances K SkinnerReviewing Editor; University Health Network, and University of Toronto, Canada
eLife posts the editorial decision letter and author response on a selection of the published articles (subject to the approval of the authors). An edited version of the letter sent to the authors after peer review is shown, indicating the substantive concerns or comments; minor concerns are not usually shown. Reviewers have the opportunity to discuss the decision before the letter is sent (see review process). Similarly, the author response typically shows only responses to the major concerns raised by the reviewers.
[Editors’ note: this article was originally rejected after discussions between the reviewers, but the authors were invited to resubmit after an appeal against the decision.]
Thank you for choosing to send your work entitled “Independent Theta Phase Coding Accounts for CA1 Population Sequences and Enables Flexible Remapping” for consideration at eLife. Your full submission has been evaluated by Eve Marder (Senior editor) and three peer reviewers, one of whom is a member of our Board of Reviewing Editors, and the decision was reached after long discussions between the reviewers. We regret to inform you that your work will not be considered further for publication.
In summary, although there was some enthusiasm among the reviewers for the work, this was tempered by concerns regarding insufficient support provided for the strong claims being made. Specifically, it was felt that this work does not represent a significant advance in the field without a more substantial analysis to support the authors’ claim that the experimental evidence is consistent with independent generation. Details of major substantive concerns raised by the reviewers are provided below for your consideration.
Reviewer #1:
The authors propose an independent coding hypothesis (as compared to a coordinated assembly hypothesis), in which an essential difference lies in currently active assemblies not determining future ones in the independent hypothesis case. An addition to existing phenomenological models (Geisler et al.) is the addition of spike generation (via an inhomogeneous Poisson process).
1) Given that a 'pacemaker' theta rhythm is included, it does not seem quite appropriate to talk about the generation of an emergent population theta rhythm. And, how should this be interpreted in light of the mentioned alternative of “populations… generate their own theta frequency…”, as stated in the seventh paragraph of the subsection “Independent coding accounts for phase sequences”, in the Results section?
2) It is not clear to me what the new and experimentally testable predictions are? Given that this is mentioned in the Introduction and Discussion, it should be clearly delineated. When it appears in the Discussion, subsequent sentences are more about the differences between the different hypotheses and its consequences, and how the independent hypothesis is better etc., but not what is 'experimentally testable' (and feasible?). In earlier parts of the manuscript, there is mention of optimal peer prediction timescale depending on phase locking, running speed dependencies etc.
So, what sorts of (feasible) experimental tests are being suggested? And what explicit predictions (differences from other hypotheses, coordinated assembly) should one look for? It would help the reader if this was more clearly set down, rather than the statement of “Important future tests of the independent coding…”, in the fourth paragraph of the Discussion section.
Since several experimental studies exist, the work as presented does not make it clear what 'new' experiments need to be done to support and distinguish this proposed independent hypothesis.
Reviewer #2:
This modeling study explores the population-level implications of the assumption that CA1 cells phase precess independently.
The main claim that the model “is sufficient to explain the organization of CA1 population activity during theta states” is a bold one, because several experimental studies argue strongly against independence. The authors re-examine some of these findings, providing useful new insights in the process. However, I do not think this main claim is adequately supported. In particular:
1) Some key pieces of evidence against independence are not considered: a) Dragoi and Buzsaki (2006) show that cells with correlated firing rates across laps have more reliable phase lags within theta cycles. If the authors model correlated firing rates using the Nspikes parameter, it is not obvious that an increased sequence compression index would result.
b) Schmidt et al. (J Neurosci, 2009) found that on a single pass through a place field, CA1 cells tend to precess through only about 180 degrees, and that the full 360-degree range is only obtained after averaging across passes. Thus, a single theta sequence does not randomly sample the 360 degree range as I believe would be the prediction from the authors' model. In addition, single trial sequences drawn from the average place-phase fields were a poor match to the observed sequences, a direct and strong test of independence.
c) Gupta et al. (2012) show that forward and backward sequence length are anticorrelated; this is not the distribution that would result from the authors' model. In addition, the relationship between velocity and sequence length reported here in Figure 6B is the opposite relationship from that shown in the Gupta paper (their Figure 1c).
2) The authors argue that some pertinent pieces of evidence, although originally advanced as evidence against independence, are in fact consistent with results from their model. However, in both cases (Harris et al., 2003; Foster and Wilson, 2007) the authors' argument hinges on a technical point in the original reports. It thus remains an open, empirical issue whether or not in those papers the main result would hold if the analyses were performed following the revised method the authors suggest.
To expand: in the case of Harris et al. it is shown that including more accurate (direction-dependent) phase fields into the analysis of data generated by the model improves peer prediction. However, this leaves open the empirical issue of when tested on actual data, adding peers would further improve the prediction. In the case of Foster and Wilson, the authors find that shuffling their model data as reported in that paper reduces correlations indicative of theta sequences, demonstrating that this result can in fact be obtained from independent neurons. Interestingly, the authors note that the method reported in the original paper may be modified to be a stronger test of non-independence. As reported it remains to be seen whether if, with this modified shuffling procedure, correlations would be reduced.
Given the above issues, I think the authors should align their interpretation with what they have shown (and not shown!). Overall I am enthusiastic about several aspects of the work: the model is compact and intuitive, providing not only satisfying insight, but also novel applications to experimental data sets with arbitrary speed profiles. It is thus a useful tool that sharpens the interpretation of such data sets, and suggests new analyses and experiments moving forward. The exploration of the relationship between theta sequences and remapping is thoughtful and generates useful testable predictions.
Reviewer #3:
This manuscript describes a model of hippocampal cell activity in which phase precession arises due to “traveling waves” within CA1. The authors first define their model, and then demonstrate that this model matches a number of data sets from experiments examining phase precession.
I think this model is clearly described and easy to understand. It should be easily generalized to other areas that demonstrate phase precession (for example CA3). However, the model is mainly descriptive, meaning it describes and characterizes the phenomenon of phase precession, but does not provide any new insights into the underlying mechanisms of phase precession, nor any new insights into how information is encoded in the hippocampus. The equations used to predict the firing rates of CA1 cells are very similar to equations used in previous studies of phase precession (the authors even cite some of these references). While I do think that having a clear description of phase precession and the implications that the existence of this phenomenon has on activity patterns within CA1 would be useful to the field, such a discussion is almost more appropriate for a review paper rather than a research article. Also, the manuscript is rather dense with concepts that are specific to temporal coding in the hippocampus. I am not sure how understandable this paper would be to those outside of this field.
Major comments:
1) Through their comparisons of the model with experimental data, the authors have provided an excellent review of the literature concerning hippocampal phase precession. I suspect, however, that sections of this paper may be incomprehensible to those not specifically working on phase precession. For example, I would have rather seen a more in-depth review of peer-predictions and its implications, rather than what felt like a cursory explanation and a citation of the Harris paper.
2) There is not much discussion of previous models of phase precession, although many of the experimental results used by the authors to support their model is predicted/explained by other models as well. For example, Geisler et al (2010) already demonstrated that the LFP theta rhythm can from a population of neurons oscillating faster than the theta-frequency. Although this paper is cited, I feel more attention should be paid to the analytical results of that paper rather than just focusing on the experimental data.
3) Along the same lines, it would have been nice to see at least some discussion of previous models of phase precession. While an exhaustive comparison is perhaps beyond the scope of this manuscript, O'Keefe's dual oscillator model is a classic and should at least be discussed.
https://doi.org/10.7554/eLife.03542.023Author response
[Editors’ note: this article was originally rejected after discussions between the reviewers, but the authors were invited to resubmit after an appeal against the decision.]
In summary, although there was some enthusiasm among the reviewers for the work, this was tempered by concerns regarding insufficient support provided for the strong claims being made. Specifically, it was felt that this work does not represent a significant advance in the field without a more substantial analysis to support the authors’ claim that the experimental evidence is consistent with independent generation. Details of major substantive concerns raised by the reviewers are provided below for your consideration.
We thank the reviewers and editor for their helpful comments. In recognizing the initial concerns identified by the reviewers we have carried out substantial additional analyses: a) we now compare predictions from independent coding with a coordinated coding model, and b) we now compare analysis of experimental data with model predictions. Our new analysis provides further support to our initial conclusions. We outline these and further changes in the response below.
Reviewer #1:
The authors propose an independent coding hypothesis (as compared to a coordinated assembly hypothesis), in which an essential difference lies in currently active assemblies not determining future ones in the independent hypothesis case. An addition to existing phenomenological models (Geisler et al.) is the addition of spike generation (via an inhomogeneous Poisson process).
We note that while our model, like that of Geisler et al., addresses phase precessing assemblies at a phenomenological level, it differs conceptually in a number of important ways. First, our model allows an analysis of the spatiotemporal patterns of population activity, whereas Geisler et al. only investigated the temporal dynamics of single unit and population average activity. This is important because it allows analysis of theta sequences at the population level, which is central to the new advances made by our study. Second, our model generates realistic activity at arbitrary running speeds, while the fixed phase lags assumed by Geisler et al. are inconsistent with experimental data if running speeds are allowed to vary. Third, our model allows systematic variation of the phase locking of cells against the theta rhythm, leading to novel predictions for sequence properties, including a dependence of the decoded sequence path length and propagation speed on phase locking (Figures 5 and Figure 5–figure supplement 1 in our original and revised manuscripts). We appreciate we may not have made these important conceptual differences clear in our initial manuscript and have addressed this in the revised submission (across the subsection headed “Independent phase coding generates traveling waves”, in the Results section).
1) Given that a 'pacemaker' theta rhythm is included, it does not seem quite appropriate to talk about the generation of an emergent population theta rhythm. And, how should this be interpreted in light of the mentioned alternative of “populations… generate their own theta frequency…”, as stated in the seventh paragraph of the subsection “Independent coding accounts for phase sequences”, in the Results section?
We appreciate the reviewer's point and believe it perhaps reflects a lack of clarity on our part in the original manuscript. Thus, while the origin of the theta frequency oscillation is not central to our main conclusions, the reviewer identifies an element of our model that, because it is conceptually similar to that of Geisler et al., we perhaps did not explain sufficiently clearly. In our single cell model, we define neurons to precess in phase against a reference theta rhythm. As a result, each neuron oscillates at a velocity-dependent frequency which is always higher than that of the reference theta. Regardless of velocity, however, we find that the global population activity oscillates at the same frequency as the reference theta, i.e. at a lower frequency than each individual cell. Our use of the word “generate” is restricted to this scenario, where the network theta is “generated” from the sum of the higher frequency oscillations in each neuron. In the revised manuscript we have clarified this point (second paragraph of the subsection “Independent phase coding generates traveling waves”, in the Results).
2) It is not clear to me what the new and experimentally testable predictions are? Given that this is mentioned in the Introduction and Discussion, it should be clearly delineated. When it appears in the Discussion, subsequent sentences are more about the differences between the different hypotheses and its consequences, and how the independent hypothesis is better etc., but not what is 'experimentally testable' (and feasible?). In earlier parts of the manuscript, there is mention of optimal peer prediction timescale depending on phase locking, running speed dependencies etc.
So, what sorts of (feasible) experimental tests are being suggested? And what explicit predictions (differences from other hypotheses, coordinated assembly) should one look for? It would help the reader if this was more clearly set down, rather than the statement of “Important future tests of the independent coding… ”, in the fourth paragraph of the Discussion section.
Since several experimental studies exist, the work as presented does not make it clear what 'new' experiments need to be done to support and distinguish this proposed independent hypothesis.
We appreciate this was a major weakness of the previous manuscript and have carried out substantial new simulations and analysis of experimental data to address the point at length. We previously identified predictions that distinguish different scenarios for independent coding, but we did not make explicit predictions for analyses that would distinguish independent from coordinated coding. We also did not compare predictions from independent and coordinated coding models directly with experimental data and, as the reviewer notes, we did not distinguish predictions that require new experiments. We have addressed these issues as follows:
a) To address the question of how the independent coding hypothesis might be empirically distinguished from the coordinated coding hypothesis, we have developed an additional model and performed extensive additional simulations and analyses. The additional model includes interactions between cells within the population in order to simulate data under the coordinated assembly hypothesis (Figure 3–figure supplement 1 in the revised manuscript), while the additional simulations compare the behavior of the independent coding and coordinated assembly models when subjected to statistical tests of independence. In particular, we compared the performance of a shuffling analysis (adapted from Foster and Wilson, 2007; see Figure 5–figure supplement 2E, F in the revised manuscript) and a prediction analysis (adapted from Harris et al. 2003; please see Table 1 and Figure 4–figure supplement 1 and 2 in the revised manuscript). We find in both cases that spike patterns generated by independent coding and coordinated assembly models can be distinguished by the shuffling analysis and by the prediction analysis. We are able to estimate the statistical power of each analysis method given assumptions about the effect size and the number of recorded neurons.
We include these new results in the Results section of the revised manuscript (please see the subsections: “Assembly coordination stabilizes sequential activation patterns”, “Independent coding accounts for apparent peer-dependence of CA1 activity”, and “Independent coding accounts for phase sequences”).
We also clarify novel predictions requiring new data, including predictions involving membrane potential oscillations and place field remapping (subsection “Linear phase coding constrains global remapping” in the Results and paragraph three in the Discussion). We note here that, in addition to our previous predictions, our new coordinated assembly model has allowed the additional prediction that phase precession would be severely disrupted following remapping if CA1 assemblies were generated by coordinated coding (Figure 7–figure supplement 1 and subsection “Linear phase coding constrains global remapping”, in the Results of the revised manuscript).
b) Having demonstrated that these new analyses have the statistical power to distinguish independent from coordinated data, we applied these analyses to experimental data (for details of these data, see Mizuseki et al., 2014). For both tests, the experimental data favor the independent coding hypothesis (please see the subsections “Independent coding accounts for apparent peer-dependence of CA1 activity” and “Independent coding accounts for phase sequences” of the Results, Table 1, Figure 4–figure supplement 1, 2 and Figure 5–figure supplement 2E, F in the revised manuscript). We believe this new analysis provides very substantial new evidence which supports our original conclusions.
Reviewer #2:
This modeling study explores the population-level implications of the assumption that CA1 cells phase precess independently.
The main claim that the model “is sufficient to explain the organization of CA1 population activity during theta states” is a bold one, because several experimental studies argue strongly against independence. The authors re-examine some of these findings, providing useful new insights in the process. However, I do not think this main claim is adequately supported. In particular:
1) Some key pieces of evidence against independence are not considered: a) Dragoi and Buzsaki (2006) show that cells with correlated firing rates across laps have more reliable phase lags within theta cycles. If the authors model correlated firing rates using the Nspikes parameter, it is not obvious that an increased sequence compression index would result.
We appreciate the suggestion, but unfortunately we find that certain steps of the analysis reported by Dragoi et al. were not exactly reproducible due to a lack of information in their study. For example, the method for isolating the central cloud (their Figure 2B) from the overall CCG plot (their Figure 2A) was not disclosed. Nevertheless, in attempting to reproduce their methods as closely as possible, we found that their key results could be accounted for by independent coding. First, when analyzing the correlations in lap by lap firingrates using the methods of Dragoi et al., we found a similar number of apparently dependent cell pairs as the original study, despite the absence of true firingrate correlations within the simulated data. Hence, the analysis used by Dragoi et al. artificially separates homogeneous populations of place cells into apparently dependent and independent cell pairs. Second, these dependent and independent cell groups displayed different spatial distributions of firing rate fields. This suggests that the effects reported by Dragoi et al. might result from a sampling bias introduced by the separation of a homogeneous population of cells into dependent and independent groups. Thus, as far as we can tell, the results reported by Dragoi et al. are consistent with the independent coding hypothesis. We report these new analyses in the revised manuscript (paragraph seven of subsection “Independent coding accounts for phase sequences”, in the Results). We hope the reviewers and editors will also recognize the difficulty in making comparisons to previous work where that work has not been documented to a level where it can be reproduced.
b) Schmidt et al. (J Neurosci, 2009) found that on a single pass through a place field, CA1 cells tend to precess through only about 180 degrees, and that the full 360-degree range is only obtained after averaging across passes. Thus, a single theta sequence does not randomly sample the 360 degree range as I believe would be the prediction from the authors' model. In addition, single trial sequences drawn from the average place-phase fields were a poor match to the observed sequences, a direct and strong test of independence.
We note that the data of Schmidt et al. do not provide evidence for or against independent coding. This is because Schmidt et al. did not analyze sequences, but only single unit phase precession. Hence, while their results suggest a more complex single cell phase code than that included in our model, they cannot reveal coordination between cells as this would require an analysis of ensemble activity. Our single cell model can be readily extended to incorporate more complex single cell phase codes while maintaining independence between cells in the population. We now discuss this issue in the manuscript and include an additional appendix detailing a model which includes trial-by-trial single cell coding properties resembling those described by Schmidt et al. while maintaining independence between cells (final paragraph of subsection headed “Single Cell Coding Model”, in the Results section, and Appendix: A2).
c) Gupta et al. (2012) show that forward and backward sequence length are anticorrelated; this is not the distribution that would result from the authors' model. In addition, the relationship between velocity and sequence length reported here in Figure 6B is the opposite relationship from that shown in the Gupta paper (their Figure 1c).
While we agree with the reviewer that our previous presentation of the independent coding model did suggest a difference to the observations in Gupta et al., it does not follow that the Gupta et al data are inconsistent with independent coding. We have performed additional simulations using the Gupta protocol which show that, if the number of cells simulated is sufficiently small as to match the number of cells per theta cycle reported by Gupta et al., the anticorrelation between ahead and behind length arises naturally due to the sequence selection criteria. Importantly, these results are fully reproducible for realistic values of phase locking and also for zero phase locking, where no theta sequences exist in the data (revised manuscript Figure 6C, D). We further note that the relationship between velocity and sequence path length that we presented in our original manuscript was a consequence of our assumed change in firingrate as a function of running speed. Further simulations in which the number of spikes per theta cycle does not vary with running speed produce a relationship similar to that reported by Gupta et al. (revised manuscript Figure 6B). Thus, the Gupta et al. data are fully consistent with the independent coding model. We make these issues clear in the revised manuscript (paragraph eight of the subsection “Independent coding accounts for phase sequences”, in the Results section).
2) The authors argue that some pertinent pieces of evidence, although originally advanced as evidence against independence, are in fact consistent with results from their model. However, in both cases (Harris et al., 2003; Foster and Wilson, 2007) the authors' argument hinges on a technical point in the original reports. It thus remains an open, empirical issue whether or not in those papers the main result would hold if the analyses were performed following the revised method the authors suggest.
To expand: in the case of Harris et al. it is shown that including more accurate (direction-dependent) phase fields into the analysis of data generated by the model improves peer prediction. However, this leaves open the empirical issue of when tested on actual data, adding peers would further improve the prediction. In the case of Foster and Wilson, the authors find that shuffling their model data as reported in that paper reduces correlations indicative of theta sequences, demonstrating that this result can in fact be obtained from independent neurons. Interestingly, the authors note that the method reported in the original paper may be modified to be a stronger test of non-independence. As reported it remains to be seen whether if, with this modified shuffling procedure, correlations would be reduced.
Given the above issues, I think the authors should align their interpretation with what they have shown (and not shown!). Overall I am enthusiastic about several aspects of the work: the model is compact and intuitive, providing not only satisfying insight, but also novel applications to experimental data sets with arbitrary speed profiles. It is thus a useful tool that sharpens the interpretation of such data sets, and suggests new analyses and experiments moving forward. The exploration of the relationship between theta sequences and remapping is thoughtful and generates useful testable predictions.
We appreciate these points reflected substantial weaknesses in the previous manuscript. As detailed in our response to Reviewer 1, we have now performed extensive additional simulations and analyses which address these issues directly and in full. In particular, we show through simulations that our improved tests can successfully distinguish between coordinated and independent coding (please see the subsections “Independent coding accounts for apparent peer-dependence of CA1 activity” and “Independent coding accounts for phase sequences”, in the Results section of the revised manuscript), and we show that the results of these tests when applied to experimental data suggest independent coding rather than coordinated assemblies (see revised manuscript Table 1, Figure 4–figure supplement 1, 2 and Figure 5–figure supplement 2E, F). Our new simulations and analysis therefore provide further and we believe very substantial support to the independent coding hypothesis.
Reviewer #3:
This manuscript describes a model of hippocampal cell activity in which phase precession arises due to “traveling waves” within CA1. The authors first define their model, and then demonstrate that this model matches a number of data sets from experiments examining phase precession.
I think this model is clearly described and easy to understand. It should be easily generalized to other areas that demonstrate phase precession (for example CA3). However, the model is mainly descriptive, meaning it describes and characterizes the phenomenon of phase precession, but does not provide any new insights into the underlying mechanisms of phase precession, nor any new insights into how information is encoded in the hippocampus. The equations used to predict the firing rates of CA1 cells are very similar to equations used in previous studies of phase precession (the authors even cite some of these references). While I do think that having a clear description of phase precession and the implications that the existence of this phenomenon has on activity patterns within CA1 would be useful to the field, such a discussion is almost more appropriate for a review paper rather than a research article. Also, the manuscript is rather dense with concepts that are specific to temporal coding in the hippocampus. I am not sure how understandable this paper would be to those outside of this field.
We disagree with the Reviewer 3's suggestion that the model is descriptive and does not provide new insights. The reviewer's comments focus on our phenomenological model of phase precession in single cells. While this is in fact novel, as we make clear in our response to Reviewer 1 above, the conceptual importance of our work comes from our investigation of the population level activity predicted by this model. In this respect, it is only necessary that our model provides a good account of phase precession in single cells. We do not make any claims about mechanisms of phase precession. Given this misconception, we highlight again the key conceptual advances made by our study.
While considerable previous work has argued that population activity in CA1 during theta states involves coordinated coding, our model demonstrates that experimental evidence to support this conclusion can be fully accounted for by independent coding. We then use the model to develop novel insights into the implications of independent coding for place cell remapping. Thus, our manuscript provides a fundamentally different conception of population activity in CA1 to previous studies. Because theta activity in CA1 is coordinated with other circuits including prefrontal cortex and entorhinal cortex, our results have wide reaching implications for neural coding in general.
Our new simulations identify experimentally testable predictions that distinguish population activity under coordinated and independent coding scenarios. By comparison of these predictions to experimental data we now provide strong evidence in support of independent coding. We provide novel predictions for the consequences of different independent coding models for remapping of place representations. We have now extended this analysis to show that coordinated and independent coding fundamentally differ in their capabilities and limitations. Independent coding offers a massively increased ability to encode multiple environments, while coordinated coding provides a mechanism by which robust sequential activity can be generated despite the noisy intrinsic properties of individual place cells.
Thus, the models and analysis introduced by our study offer fundamental insights into both information processing and coordination of spike timing in hippocampal populations. In our revised manuscript we take care to make these novel insights much clearer to the reader.
Major comments:
1) Through their comparisons of the model with experimental data, the authors have provided an excellent review of the literature concerning hippocampal phase precession. I suspect, however, that sections of this paper may be incomprehensible to those not specifically working on phase precession. For example, I would have rather seen a more in-depth review of peer-predictions and its implications, rather than what felt like a cursory explanation and a citation of the Harris paper.
We have performed extensive additional peer prediction simulations on both simulated and experimental data (see comments above). Accordingly, this section of the manuscript has been expanded and a more in-depth explanation is included (subsection “Independent coding accounts for apparent peer-dependence of CA1 activity”, in the Results section).
2) There is not much discussion of previous models of phase precession, although many of the experimental results used by the authors to support their model is predicted/explained by other models as well. For example, Geisler et al. (2010) already demonstrated that the LFP theta rhythm can from a population of neurons oscillating faster than the theta-frequency. Although this paper is cited, I feel more attention should be paid to the analytical results of that paper rather than just focusing on the experimental data.
While we agree that several previous models of phase precession can account for the same phenomenological results as our model at the single-cell level, the purpose of our study is not to explain the mechanisms of single-cell phase precession but rather to understand the emergence of population activity. We now carefully explain the similarities and differences from the Geisler model, which we detailed above in our response to Reviewer 1.
3) Along the same lines, it would have been nice to see at least some discussion of previous models of phase precession. While an exhaustive comparison is perhaps beyond the scope of this manuscript, O'Keefe's dual oscillator model is a classic and should at least be discussed.
In the Discussion we outline which previous models of phase precession could provide a mechanistic basis for our single cell coding model and which models would instead imply coordinated assemblies. We now pay specifically mention the dual oscillator and other models in the Discussion section of the updated manuscript. Since the cellular mechanisms of phase precession are not a focus of our study we do not discuss these at length.
https://doi.org/10.7554/eLife.03542.024