Registered report: Senescence surveillance of pre-malignant hepatocytes limits liver cancer development

Thank you for sending your work entitled “Registered report: Senescence surveillance of pre-malignant hepatocytes limits liver cancer development” for consideration at eLife. Your article has been favorably evaluated by Sean Morrison (Senior editor), a Reviewing editor, and 4 reviewers, one of whom is a statistician.

The Reviewing editor and the reviewers discussed their comments before we reached this decision, and the Reviewing editor has assembled the following comments to help you prepare a revised submission. All believe this is a generally very well-conceived plan for replication, but also raised some specific issues that need to be addressed before a protocol is finalized, and the registered report accepted for publication in eLife.

Major issues to be addressed in a revised submission:

Technical points:

1) As the proposed reproduction experiments involve hydrodynamic tail vein injection, it is crucial that these experiments are conducted in a laboratory with high experience with these technique. It is important to note that the efficiency of DNA uptake is influenced by blood pressure and heart rate. Preferably, the technique is conducted without anesthesia, as in this way there will be no drop in blood pressure, and the cardiovascular system of the mouse can fully adapt to the volume challenge by hydrodynamic tail vein injection. In any case, two studies can only be compared if the same anesthesia is used. The anesthesia proposed for the reproduction experiment involves, in addition to ketamine, acepromazine. As acepromazine is known to induce vasodilation and decreases blood pressure, it cannot be ruled out that acepromazine impacts the efficiency of hydrodynamic DNA delivery. This is important to keep in mind, as in the original paper by Kang et al. I could not find information that acepromazine was used.

2) To ensure comparability of two studies it is furthermore important that mice of the same age and weight are subjected to hydrodynamic delivery. Kang et al. describe that mice 4–6 weeks of age were used for hydrodynamic delivery while in the outline of the reproducibility project it is stated that mice 4–6 weeks or 6–8 weeks of age are ordered and used after one week of adjustment time. It should be ensured that mice are injected at the same age as described by Kang et al. Likewise, the hydrodynamic injections are a critical step in this experiment. The researcher who conducts these injections should learn this method in a laboratory in which this protocol is well-established, if possible the Zender lab itself.

3) Even though the mice are being caged under SPF conditions, there is no evidence that the research team will test for the presence of viruses that are largely confined to mice with highly significant immunodeficiencies. These can often have significant effects on the anti-tumor activity of innate immunity. At a minimum that the investigators should test for the presence of Norovirus in their SCID/Beige mice as a marker for such infections, especially since Norovirus is found in many SPF colonies across the country. The experimental groups should also be co-caged to control, at least partially, for strain specific microbiota that can also have profound influences on natural anti-tumor activity.

4) With respect to Protocol 2, Kang et al. went to extreme lengths to carefully look at the role of class II restricted CD4 T cells, including using CD4^−/− mice, Class II^–/– mice, and wt mice depleted of CD4⁺ cells using CD4 specific mAb. All of their results agree that CD4⁺ T cells are playing a major role in surveillance. However, in the proposed study, the research team only proposes to use CD4^−/− mice. There may be effectors or Tregs that emerge from these mice that can still influence the response, and at least one more of the previously employed models of mice lacking CD4 T cells should also be used to substantiate the effects that may or may not be seen with CD4^−/− mice.

Statistical issues:

1) The authors state that: “The original authors of the study performed this [statistical] analysis, and we are therefore including it in the replication analysis plan. We are also including the more statistically appropriate tests detailed below”. The used wording implies that the authors of the replication study regard the statistical analyses by Kang et al. as not adequate. More detailed information should be provided as to why the authors think the analyses by Kang et al. are not adequate.

2) Each protocol has statistics mentioned in the confirmatory analysis plan and the power calculation sections. In protocol 1 the analyses will be two-way ANOVA applied to three datasets. In each ANOVA are the effects treatment and time? The summary data from the original report suggests this. Means and SD are reported for each of the four groups within each experiment but the factor specific effects are not reported. A two-way ANOVA can consist of up to three tests, the treatment, the time, and the treatment–time interaction. The power calculations use a single effect size, which we do not understand. As the experiment is trying to replicate an already detected effect, then each such effect can be clearly stated. The power calculation is reported for one degree of freedom suggesting only one of these terms (treatment?) is expected to be significant though time clearly seems to have a strong effect in one group.

3) The plans for protocol 2 are easier to understand in that simple one-way ANOVAs and t-tests are planned, though with just 5 per group this will rely on the very strong assumption of normality. Prior experience involving tumor in vivo studies shows that such experiments have considerable mouse-to-mouse variation. It would be a shame if conclusions are limited by too small sample numbers, and in light of the statistical issue just raised, it seems important to increase the animal numbers per group to n = 10–15 because of the low projecting 81% confidence level at n = 5. Also, the power calculations seem to justify 3 in each sample, yet 5 in each group are planned. The authors need to better explain their power calculations that led them to conclude openly 3 animals per group would be sufficient and why they then choose 5 animals per group. Is this to cover some results lost due to failure? In any case, the power calculations for these comparisons need to state what specific effect sizes will be viewed as a replication of the original study.

4) In a related vein, in a replication study it is important to be clear what specific cut offs will be used to declare a replication or lack of replication. So the explicit effect sizes for each factor and for each of the 6 experiments need to be stated. While it is a good idea to combine the two results (original and replication) in a forest plot, this will give an inflated estimate of any effect sizes due to the publication selection operating on the first article. The decision regarding whether there has been replication should be based on the results of the replication study alone. So it may be that smaller effect sizes than those reported in the original article would still be viewed as strong evidence of the anticipated effect. In such a case, as stated above (point #3), a larger sample size would be justified and should be strongly considered at this stage.

5) Regarding the power calculations, the proposed power calculations use a combination of data reported in the original study and data from an alternative relevant study. This is fine at this stage, however, we suggest the following improvements:

a) Cross-study variation should be taken into account to determine expected power in the proposed study, since loss of power can be expected from the original study. This is hard to estimate, but papers by Giovanni Parmigiani and collaborators at the Dana–Farber provide some estimates about cross-study variation that could be used for this purpose. The authors should budget some additional variability because of cross-study reproducibility, and increase the sample size on-the-fly, as they deem appropriate.

b) The final report on the replicated study should report the actual power of the tests, based on numerical summaries of the data in the replicated study.

[Editors' note: further revisions were requested prior to acceptance, as described below.]

Thank you for resubmitting your article entitled “Registered report: Senescence surveillance of pre-malignant hepatocytes limits liver cancer development” for further consideration at eLife. Your revised Registered report has been favorably evaluated by Sean Morrison (Senior editor), a member of the Board of Reviewing Editors, and by someone with relevant expertise in statistics.

The Registered report is essentially ready for acceptance, but we would ask you to respond to the remaining statistical issues and make additional minor modifications as needed:

1) We do not think it is a good idea to report a combined estimate of any effect size with the original. However displaying results on a forest plot is helpful.

2) With respect to the sample size calculations for the two-way ANOVA, have you used the within group SDs instead of the within group variances in the formulae? If so, this means that you would be over-estimating the power. With 5 in each group the authors should just have 80% power to replicate what was seen in the original study.

1) As the proposed reproduction experiments involve hydrodynamic tail vein injection, it is crucial that these experiments are conducted in a laboratory with high experience with these technique. It is important to note that the efficiency of DNA uptake is influenced by blood pressure and heart rate. Preferably, the technique is conducted without anesthesia, as in this way there will be no drop in blood pressure, and the cardiovascular system of the mouse can fully adapt to the volume challenge by hydrodynamic tail vein injection. In any case, two studies can only be compared if the same anesthesia is used. The anesthesia proposed for the reproduction experiment involves, in addition to ketamine, acepromazine. As acepromazine is known to induce vasodilation and decreases blood pressure, it cannot be ruled out that acepromazine impacts the efficiency of hydrodynamic DNA delivery. This is important to keep in mind, as in the original paper by Kang et al. I could not find information that acepromazine was used.

We thank the reviewers for this suggestion. According to correspondence with the original authors, Kang and colleagues followed the protocol of Bell et al. (2007) in order to perform their hydrodynamic injections. This protocol clearly outlines a drug cocktail of 8 mg ml⁻¹ ketamine HCl, 0.1 mg ml⁻¹ acepromazine maleate and 0.01 mg ml⁻¹ butorphanol tartrate. We agree with the reviewers that deviating from the exact drug cocktail used in the original study may contribute to skewed results; therefore, we will also follow the protocol of Bell, et al., and use the same anesthetics as used in the original study.

We have included a biographical sketch of the scientists directly in charge of performing the hydrodynamic injections. Ms. Lynette Bower has over ten years of experience in laboratory animal procedures, and is certified proficient in performing HPTV injections. She has performed over 50 injections on four separate projects, with a >80% success rate. Ms. Bower will be overseen by Dr. Kristin Evans, who is one of the directors of the Mouse Biology Program at the University of California, Davis.

In order to be overly conservative in our approach, we have increased the sample sizes for each cohort of mice receiving hydrodynamic injections from 5 animals to 7. In this way, we feel confident that we will have enough end-point animals to achieve high statistical power in our analyses.

2) To ensure comparability of two studies it is furthermore important that mice of the same age and weight are subjected to hydrodynamic delivery. Kang et al. describe that mice 4–6 weeks of age were used for hydrodynamic delivery while in the outline of the reproducibility project it is stated that mice 4–6 weeks or 6–8 weeks of age are ordered and used after one week of adjustment time. It should be ensured that mice are injected at the same age as described by Kang et al. Likewise, the hydrodynamic injections are a critical step in this experiment. The researcher who conducts these injections should learn this method in a laboratory in which this protocol is well-established, if possible the Zender lab itself.

We thank the reviewers for calling our attention to this apparent discrepancy. While our initial correspondence with Kang and colleagues implied that two age ranges of mice were used, subsequent communication with Dr. Tae Won Kang has revealed that for the particular experiments outlined in this replication, all mice should be 4–6 weeks of age.

We have clarified the exact ages of mice that will be used for each protocol in the Registered report. For both Protocol 1 and 2, female mice will be ordered at 4 weeks of age, acclimated for 1 week, and injected at 5 weeks of age. The precise ages and weights of mice at the time of injection will be documented.

In regards to performing hydrodynamic injections, we will follow the procedures outlined in Bell et al. (2007), as followed by Kang and colleagues. The replicating scientists are highly experienced in the practice of hydrodynamic injections (please see above response). Additionally, we are increasing the sample sizes for all animals receiving injections, so as to ensure the statistical power of our downstream analyses (see above response).

3) Even though the mice are being caged under SPF conditions, there is no evidence that the research team will test for the presence of viruses that are largely confined to mice with highly significant immunodeficiencies. These can often have significant effects on the anti-tumor activity of innate immunity. At a minimum that the investigators should test for the presence of Norovirus in their SCID/Beige mice as a marker for such infections, especially since Norovirus is found in many SPF colonies across the country. The experimental groups should also be co-caged to control, at least partially, for strain specific microbiota that can also have profound influences on natural anti-tumor activity.

We thank the reviewers for these suggestions. We have attached a sample health report from the University of California–Davis Mouse Biology Program (UCD-MBP) that details the testing parameters in their vivarium. As noted, murine norovirus (MNV) is routinely tested for via serum ELISA. UCD-MBP has not detected any pathogens in their colonies.

We agree with the reviewers’ suggestion to co-cage experimental and control groups of mice within the same strain. Therefore, we have updated the Registered report to indicate that mice of the same strain receiving either Nras^G12V or Nras^G12V/D38A will be co-caged both before and after receiving injections. As far as co-caging mice between strains, we believe this introduces a major procedural difference that did not occur in the original study, as strain mixing may introduce variation in mouse behavior and/or microbiota (as noted by the reviewer). To minimize such differences in our replication, we will continue to house mice strain-specifically.

4) With respect to Protocol 2, Kang et al. went to extreme lengths to carefully look at the role of class II restricted CD4 T cells, including using CD4^−/− mice, Class II^–/– mice, and wt mice depleted of CD4⁺ cells using CD4 specific mAb. All of their results agree that CD4⁺ T cells are playing a major role in surveillance. However, in the proposed study, the research team only proposes to use CD4^−/− mice. There may be effectors or Tregs that emerge from these mice that can still influence the response, and at least one more of the previously employed models of mice lacking CD4 T cells should also be used to substantiate the effects that may or may not be seen with CD4^−/− mice.

We thank the reviewers for this insightful comment, and we agree that this is an important issue to consider during data interpretation. Although we plan to obtain mice from the same vendor as the original authors (Jackson Laboratory), there may be subtle differences that emerge even from seemingly genetically identical animals. The raised concern may be a reason why the experimental effect, or size of the effect, is not replicated and thus will be acknowledged as a potential factor in the Replication Study. Alternatively, the raised concern may result in the same observed effect, but not due to the role of CD4 cells. This too will be acknowledged in the Replication Study.

We recognize that all of the experiments included in the original study are important, and choosing which experiments to replicate has been one of the great challenges of this project. We agree that the exclusion of certain experiments limits the scope of what can be analyzed by the project, but we are attempting to identify a balance of breadth of sampling for general inference with sensible investment of resources on replication projects. The Reproducibility Project: Cancer Biology is aimed to replicate a selection of experiments as faithfully as possible, not necessarily the main conclusions that are drawn from the many experiments in any given paper.

Statistical issues:

1) The authors state that: “The original authors of the study performed this [statistical] analysis, and we are therefore including it in the replication analysis plan. We are also including the more statistically appropriate tests detailed below”. The used wording implies that the authors of the replication study regard the statistical analyses by Kang et al. as not adequate. More detailed information should be provided as to why the authors think the analyses by Kang et al. are not adequate.

We have updated the language in the Registered report to better reflect the strategy for this analysis. As outlined in Nieuwenhuis et al. (Nieuwenhuis et al., 2011), the authors did not report an interaction effect (Nras mutational status–immune defect), which the researchers would have needed to report as significant to support their claim. Thus, we will be performing the two-way ANOVA to determine if the interaction is significant before performing pair-wise comparisons. However, we also plan to perform a t-test outside the framework of an ANOVA similar to the original paper (although performing a planned comparison within the framework of an ANOVA is more powerful than performing a separate t-test if the assumption of ANOVA is valid) to allow for a direct comparison to what was originally reported.

2) Each protocol has statistics mentioned in the confirmatory analysis plan and the power calculation sections. In protocol 1 the analyses will be two-way ANOVA applied to three datasets. In each ANOVA are the effects treatment and time? The summary data from the original report suggests this. Means and SD are reported for each of the four groups within each experiment but the factor specific effects are not reported. A two-way ANOVA can consist of up to three tests, the treatment, the time, and the treatment-time interaction. The power calculations use a single effect size, which we do not understand. As the experiment is trying to replicate an already detected effect, then each such effect can be clearly stated. The power calculation is reported for one degree of freedom suggesting only one of these terms (treatment?) is expected to be significant though time clearly seems to have a strong effect in one group.

We thank the reviewer for these helpful comments. We have revised our confirmatory analysis plan for Protocol 1, as updated in the Registered report. We have also updated the Power Calculations section to better reflect both the analysis we performed on the original data, as well as our future analysis plans. The original data had a significant treatment–time interaction, which we are powered for and that we have more clearly labeled. Thus, the experiment is designed to test the originally observed effect of time differing between the treatments. However, we do see value in adding planned comparisons between the two times for each treatment as this will evaluate the size of the effect in each group. Therefore, we have included such comparisons in the updated version of our confirmatory analysis plan for Protocol 1.

3) The plans for protocol 2 are easier to understand in that simple one-way ANOVAs and t-tests are planned, though with just 5 per group this will rely on the very strong assumption of normality. Prior experience involving tumor in vivo studies shows that such experiments have considerable mouse-to-mouse variation. It would be a shame if conclusions are limited by too small sample numbers, and in light of the statistical issue just raised, it seems important to increase the animal numbers per group to n= 10-15 because of the low projecting 81% confidence level at n = 5. Also, the power calculations seem to justify 3 in each sample, yet 5 in each group are planned. The authors need to better explain their power calculations that led them to conclude openly 3 animals per group would be sufficient and why they then choose 5 animals per group. Is this to cover some results lost due to failure? In any case, the power calculations for these comparisons need to state what specific effect sizes will be viewed as a replication of the original study.

We thank the reviewers for these insightful suggestions. We agree that there is the potential for unanticipated variation in the experimental design that would lead to the exclusion of animals in a given group. Regarding hydrodynamic injections, the original study authors communicated variation in injections that resulted in a ∼20% injection failure rate, leading to exclusion of animals in downstream analyses. To account for variation in injections, we have increased the sample size to seven mice per treatment group for the experiments performed in Protocol 1, as well as the 12-day experimental arm of Protocol 2. We believe this increased sample size will allow us to analyze a minimum of five mice per group in downstream analyses. We have updated the Power Calculations to indicate the statistical power achieved by including five mice per group (89.9–99.9% for Protocol 1; 94.6–99.9% for Protocol 2).

We believe the reviewers have highlighted an important concern regarding the potential for mouse-to-mouse variation in tumor development in the 7-month experimental arm of Protocol 2. Given that we cannot calculate the effect size of the original experimental data in Figure 4B (specifically the CD4^−/− arm), and that we also do not know the variance or the distribution of the data for this arm, it is difficult to properly power this replication with a large enough sample size that also remains within the feasibility of the project. Based on these factors, we have reconsidered the inclusion of the 7-month in vivo tumor formation experiment in this replication study. Given that the original effect size is unknown, we feel that a replication of this experiment would be considered exploratory in nature; thus, we have reallocated our resources toward increasing sample sizes for, and therefore improving, those arms of the study that can be statistically compared to the original data.

4) In a related vein, in a replication study it is important to be clear what specific cut offs will be used to declare a replication or lack of replication. So the explicit effect sizes for each factor and for each of the 6 experiments need to be stated. While it is a good idea to combine the two results (original and replication) in a forest plot, this will give an inflated estimate of any effect sizes due to the publication selection operating on the first article. The decision regarding whether there has been replication should be based on the results of the replication study alone. So it may be that smaller effect sizes than those reported in the original article would still be viewed as strong evidence of the anticipated effect. In such a case, as stated above (point #3), a larger sample size would be justified and should be strongly considered at this stage.

We agree that the replication effect size and the original effect size (with their corresponding 95% confidence intervals) should be compared to each other. Therefore, each confirmatory analysis plan section begins with the phrasing describing the comparison of the two effect sizes and the combination of them. We have slightly modified the text in the Registered report to clarify this plan. We plan to present the effect sizes of each factor for all the experiments this way and to combine each factor (original and replication) using a meta-analytic approach. This will allow direct comparison of the original and replication effect sizes and the combination of the two will give an estimation of the current knowledge for that given effect size. And we agree that the direct comparison will allow for one to determine if the evidence for an anticipated effect is still there, even if the size of that effect, or precision of that effect size estimate is different.

5) Regarding the power calculations, the proposed power calculations use a combination of data reported in the original study and data from an alternative relevant study. This is fine at this stage, however, we suggest the following improvements:

a) Cross-study variation should be taken into account to determine expected power in the proposed study, since loss of power can be expected from the original study. This is hard to estimate, but papers by Giovanni Parmigiani and collaborators at the Dana–Farber provide some estimates about cross-study variation that could be used for this purpose. The authors should budget some additional variability because of cross-study reproducibility, and increase the sample size on-the-fly, as they deem appropriate.

We thank the reviewers for these suggestions. The cross-study variation, such as approaches that utilize the 95% confidence interval of the effect size, can be useful in conducting power calculations when planning adequate sample sizes for detecting the true population effect size, which requires a range of possible observed effect sizes. However, the Reproducibility Project: Cancer Biology is designed to conduct replications that have 80% power to detect the point estimate of the originally reported effect size. While this has the limitation of being underpowered to detect smaller effects than what is originally reported, this standardizes the approach across all studies to be designed to detect the originally reported effect size with at least 80% power. Also, while the minimum power guarantee is beneficial for observing a range of possible effect sizes, the experiments in this replication, and all experiments in the project, are designed to detect the originally reported effect size with a minimum power of 80%. Thus, performing power calculations during or after data collection is not necessary in this replication attempt as all studies included are already designed to meet a minimum power or are identified beforehand as being underpowered and thus are not included in the confirmatory analysis plan. The papers by Giovanni Parmigiani and collaborators highlight the importance of accounting for variability that can occur across different studies, specifically gene expression data. While it is possible for a difference in variance between the originally reported results and the replication data, this will be reflected in the presentation of the data and a possible reason for obtaining a different effect size estimate.

b) The final report on the replicated study should report the actual power of the tests, based on numerical summaries of the data in the replicated study.

As described above, we do not see the value in performing post-hoc power calculations on the obtained data. However, we do agree that reporting the actual power of the tests to detect the originally reported effect size estimate based on the sample size analyzed in the replication study is important and will be reported.

[Editors’ note: further revisions were requested prior to acceptance, as described below.]

1) We do not think it is a good idea to report a combined estimate of any effect size with the original. However displaying results on a forest plot is helpful.

We disagree, and as described in Valentine et al., 2011, and Bumming, 2012, combining multiple studies using a meta-analytic approach is a statistical option that can be employed to describe all of the available evidence about a given effect size. Specifically, we will utilize a random effects meta-analysis because this approach assumes that the effects vary due to known and unknown characteristics of the studies.

2) With respect to the sample size calculations for the two-way ANOVA, have you used the within group SDs instead of the within group variances in the formulae? If so, this means that you would be over-estimating the power. With 5 in each group the authors should just have 80% power to replicate what was seen in the original study.

We used the SD when we calculated the F statistic, which is the input for GraphPad Prism’s software when the original data values are not known. We also obtained the same F values and partial eta squared values when using the R software package ‘rpsychi’ and the function ‘ind.twoway.second’, which conducts a two-way design using published work using the mean, SD, and n (http://cran.r-project.org/package=rpsychi). Please see the “Study 34 2-way ANOVAs.R” file.

References:

Valentine JC, Biglan A, Boruch RF, Castro FG, Collins LM, Flay BR, Kellam S, Moscicki EK, Schinke SP. 2011. Replication in prevention science. Prev Sci. 12(2): 103-17. doi:10.1007/s11121-011-0217-6.

Bumming G. 2012. Understanding The New Statistics: Effect Sizes, Confidence Intervals, and Meta-Analysis. Routledge. ISBN: 978-0-415-87,968-2.