Altered γ-secretase activity in mild cognitive impairment and Alzheimer's disease

We investigated why the cerebrospinal fluid (CSF) concentrations of Aβ42 are lower in mild cognitive impairment (MCI) and Alzheimer's disease (AD) patients. Because Aβ38/42 and Aβ40/43 are distinct product/precursor pairs, these four species in the CSF together should faithfully reflect the status of brain γ-secretase activity, and were quantified by specific enzyme-linked immunosorbent assays in the CSF from controls and MCI/AD patients. Decreases in the levels of the precursors, Aβ42 and 43, in MCI/AD CSF tended to accompany increases in the levels of the products, Aβ38 and 40, respectively. The ratios Aβ40/43 versus Aβ38/42 in CSF (each representing cleavage efficiency of Aβ43 or Aβ42) were largely proportional to each other but generally higher in MCI/AD patients compared to control subjects. These data suggest that γ-secretase activity in MCI/AD patients is enhanced at the conversion of Aβ43 and 42 to Aβ40 and 38, respectively. Consequently, we measured the in vitro activity of raft-associated γ-secretase isolated from control as well as MCI/AD brains and found the same, significant alterations in the γ-secretase activity in MCI/AD brains.


Transaction Report:
(Note: With the exception of the correction of typographical or spelling errors that could be a source of ambiguity, letters and reports are not edited. The original formatting of letters and referee reports may not be reflected in this compilation.) 1st Editorial Decision 10 February 2011 Thank you for the submission of your manuscript "γ-Secretase activity may be altered in the brain affected by mild cognitive impairment and Alzheimer's disease" to EMBO Molecular Medicine. We have now heard back from the three referees whom we asked to evaluate your manuscript. You will see that they find the topic of your manuscript potentially interesting. However, they also raise significant concerns on the study, which should be convincingly addressed in a major revision of the manuscript.
You will see that Reviewer #1 is rather supportive, while Reviewers #2 and #3 are much more reserved. The major concerns raised by these reviewers refer to the following issues: -Your main hypothesis of a shift of gamma-secretase activity towards Abeta40/Abeta38 production appears to be at odds with previous studies and it remains unclear that alternative explanations (eg Abeta42 deposition) can be rejected based on the data provided.
-The main conclusions of your study are currently based on the interpretation of a single line of evidence (ELISAs) and therefore remain rather preliminary.
In view of these key issues, the reviewers provide several suggestions for additional analyses that may strengthen the conclusions you wish to draw. While we realize that not all of these suggestions can be fully addressed in a revision, we feel that some complementary evidence is required to improve the impact and conclusiveness of this study. The suggestion provided by reviewer #3 to investigate gamma-secretase activity in an AD mouse model appears as a particularly constructive one in this regard.
Importantly, reviewers #2 and #3 also highlight that a more rigorous statistical analysis has to be included.
Given the balance of these evaluations, we feel that we can consider a revision of your manuscript if you can convincingly address the issues that have been raised within the space and time constraints outlined below.
Revised manuscripts should be submitted within three months of a request for revision. They will otherwise be treated as new submissions, unless arranged differently with the editor.
I look forward to seeing a revised form of your manuscript as soon as possible.
Yours sincerely, Editor EMBO Molecular Medicine ***** Reviewer's comments ***** Referee #1: This is an interesting, exciting, and potentially important paper. Ihara and colleagues have provided the first consideration of potentially important A species such as A 43. They also provide convincing evidence that 42 is cleaved to 38 while A 43 is cleaved to A 40, and that various peptide levels and quotients of levels can be used to distinguish control, MCI, and AD CSF. The model that they present is that the levels of each peptide are determined as a quotient of g-secretase action / exopeptidase action. While it would be nice to have peptidase assays and to know which exopeptidase(s) is/are involved, the data are so compelling that I would not delay this publication until those data were in hand. The A 42/ A 38 story is especially satisfying because it goes a long way in explaining the effect of NSAIDs, and this explanation fits existing published data very well.
I would like to see how the authors envision dovetailing their model based on disease-dependent generation of A peptide variants with the Bateman model for differential clearance. Aggregation could be an important confound; i.e., excess long A s could aggregate and be cleared more slowly, giving the appearance of a clearance defect to what is really a generation abnormality.
The future directions vis-a-vis serial studies of individuals will be very important in clarifying the natural history of A metabolism defects, especially re proving whether the A metabolism defects are basically traits that may be present long before clinical symptoms.
Referee #2 (Novelty/Model system Comments): The whole study is based on only one approach and one set of data that are maximally explored by statistics and simulations. No complementary data using other experiments or strategies are included, though the authors suggest that this is possible. Because of this, I believe it is at the stage not yet suitable for publication in this journal.
identified in their previous work. To achieve this they set up an ELISA's for each species allowing to calculate ratio's of the different (pairs of) species resulting from both -secretase cleavages in both pipelines., and as a key achievement they were able to detect the low levels of A 43. Kakuda et al found that, in AD and MCI patients, the levels of A 42 and -43 were decreased and linked to an increase of their respective cleavage products, A 38 and -40. Their overall conclusion is that -secretase activity is altered in MCI/AD and AD thereby providing an explanation for the fact that A 42 levels are decreased in the CSF of AD patients. Secondly, this work provides an in vivo validation for previous in vitro data from Takami et al 2009 (where they put forward the dual pipeline -secretase model and analyzed the tri-and tetrapeptides resulting from the cleavage of different A species in a CHAPSO-reconstituted -secretase system).
Although Kakuda et al give us a more in depth analysis of decreased A 42 levels which was previously observed in AD and MCI patients CSF, and can fairly fit their data in the sequentialsecretase cleavage model, the final outcome is that they have to remain cautious about the cause as stated already in the title '....may be altered...'. It doesn't elucidate much more about how this differential cleavage might occur, and as such remains very descriptive. The whole study is at the end based on only one set of ELISA data without exploring alternative and complementary approaches.The timing of the Ab formation during disease development on the other hand is a very important question, that hopefully can be answered in the near future. Although the authors provide an explanation for the earlier observation of decreased A 42 in CSF, this aspect is of direct interest to only the AD field and likely not appealing to a broader audience of molecular medicine. I would recommend a more specialized journal.
Selected remarks: The data fits the cleavage events A 43 to -40 and A 42 to -38 and the increase of the latter is nicely mirrored by a decrease in the former, the plots shown clearly show that both pipelines are somehow linked, and in AD/MCI Fig 5 shows the stated increase in A 38 and 40. Although the errors on some data points are quite high, this is a common problem working with patient material, and the authors rigorous statistical analysis supports what they claim. But from here the rest is speculation. The plots could become more clear if the different correlation coefficients and regression lines for the separate data groups were displayed, instead of just the control, especially when this is argued about in the text.
The observation that more 40 results in less 43, and the same for 42 to 38, their immediate precursors is a good internal control, why state "points to the possibility that more 42 and 43 are converted to 38 and 40 ... in AD and MCI"? To me this is exactly what you hope to expect if the hypothesis is correct. But it also underscores that the authors cannot rule out other explanations as well.
Throughout the text the authors regularly mention the tri-and tetrapeptides, but actually never measured them. They have shown in their previous paper that this is possible and the question is worth asking whether these peptides can be measured in the CSF as well: if so, this would strengthen their model on APP processing. Also,neither here nor in the Takami paper the so-called NSAID-effect is tested. The authors suggest that MCI patients have already a NSAID-like effect, but can this be experimentally tested?
The stepwise processing kinetics fit the data and the authors claim that this supports alteredsecretase in the brain, rather than preferential deposition of longer A forms in senile plaques. This again remains a speculation and no simulation for the deposition kinetics is supplied. Further speculation is found in the attempt to explain the lowering of A 42 and 43 which "seems to be planned to prevent further accumulation of Ab42 and 43".
As it stands, the data are explained and models are simulated starting from the assumption that A levels are in steady state in CSF. There is here no experimental proof for that, however the authors suggest that this is possible by performing a longitudinal study. Given the importance of this study in validating in vivo the presence of distinct processing pipelines, I think that at this level (and for this journal) such a study should be included.
The Discussion section is as long as the Results and remains superficial. This is not surprising as the whole paper is built on only one set of data, namely the ELISA measurements of different A species and subsequent statistical analysis and simulations. The authors try to explain (or rather speculate) by their data observations made in other studies such as the PS1 R-mutation or the difference between iNPH and MCI/AD. They make relevant comments on what future directions should be taken, but some of these suggestions seem to be technically feasible that I wonder why not more effort is done in making a more complete study. For instance, also their comment that the alteredsecretase activity could be due to alterations in the activities of the different -secretase activities in the brain could be at least addressed experimentally. In summary, the discussion is therefore not easy to follow, and touches very different topics not always directly related to the presented data (PS1 mutation and unclear link to product line 1, different effects in iNPH due to dilution effects, hypothetical shifts in the plots during lifetime, subtle differences in -secretase composition, novelsecretase inhibitors possibly blocking the A bulk flow and NSAID-like effect in the brain of AD/MCI patients) Referee #3: In this study, Kakuda et al. have investigated the levels of four Abeta (43/42/40/38) species in CSF samples of individuals with AD or MCI and healthy controls using specific ELISA assays. The authors have previously proposed a sequential cleavage model of gamma-secretase processing, which claims that Abeta peptides are generated in two product lines, and that Abeta43/Abeta40 and Abeta42/Abeta38 behave as precursor/product in these product lines. They now report significant reductions in Abeta43/Abeta42 levels and significant increases in Abeta40/Abeta38 levels in AD/MCI versus controls. Based on the sequential cleavage model they propose that this Abeta signature indicates that gamma-secretase activity is enhanced in AD/MCI towards the generation of Abeta40/Abeta38. They speculate that this change in gamma-secretase activity could be induced by amyloid formation in the brain and might be a compensatory mechanism to avoid further Abeta deposition or oligomer formation. Furthermore, they put forward the provocative hypothesis that this is the underlying mechanism for the drop in CSF Abeta42 levels in AD/MCI, which has been observed in numerous previous studies. The manuscript is clearly written but ignores some important earlier studies that reported on CSF Abeta levels in AD, MCI and FAD individuals.
Specific criticisms: 1. Overall, the study seems rather descriptive at this point. Based solely on their Abeta measurements in CSF and on their persuasive but not yet universally accepted sequential cleavage model, the authors make far-reaching claims with potential therapeutic implications. No supporting data from experimental models is provided. At the same time, they challenge the prevailing hypothesis that reductions in Abeta42 CSF levels in AD/MCI are caused by preferential deposition of Abeta42 in brain parenchyma or by formation of Abeta42 oligomers, which might escape detection by conventional ELISA assays. However, this hypothesis, while not proven in humans, does have substantial support from both genetic studies and experimental models. For example, APP and presenilin mutations associated with familial AD clearly enhance production of Abeta42. While some of these mutations may impair overall gamma-secretase activity, even the sequential cleavage model concludes that this would result in increased absolute levels of Abeta42, which has been proven by Abeta42 plasma measurements in FAD patients (Scheuner 1996, Nat Med 2:864-9). Nevertheless, the exact same phenomenon of reduced Abeta42 levels and a reduced Abeta42/Abeta40 ratio is observed in CSF samples of FAD patients (Ringman 2008, Neurology 71:85-92). This is clearly at odds with the proposition of the authors that the drop in Abeta42 CSF levels is caused by a shift in gamma-secretase activity towards Abeta40/Abeta38 production. The "deposition" hypothesis has further substantial experimental support from transgenic mouse models of AD, in which plaque deposition and a rise in brain Abeta levels is tightly correlated with Abeta42 reductions in CSF and plasma (e.g., see Kawarabayashi 2001, J Neuroci 21:372-81). Consequently, the authors would greatly strengthen their case if they could demonstrate changes in gammasecretase activity in AD mouse models before and after the development of amyloid pathology. In the absence of such experimental data, the interpretation of the CSF Abeta measurements by the authors is too speculative, particularly given that contradictory findings have been published previously (see below). 2. Previous studies have not measured Abeta43 levels in CSF, and little information is available for Abeta38. However, much larger, longitudinal studies have not found changes in Abeta40 levels in MCI versus control (e.g., see Hansson 2007, Dement Geriatr Cogn Disord 23:316-20). This needs to be mentioned, discussed and studies should be cited. 3. The authors refer to a previous study and claim that a gamma-secretase modulator not only decreased Abeta42 and increased Abeta38 but also had significant effects on Abeta43 (decrease) and Abeta40 (increase) levels. However, the effect on Abeta40 levels was not significant in this study, only a trend was observed (Takami 2009, J Neurosci 29:13042-52). This should be corrected. 4. Statistics are key in this study. However, the description of statistical methods is rather opaque in the method section and the figure legends. In Table 1, it is unclear whether and how Bonferroni correction was applied for the multiple comparisons. In Figure 2, Spearman correlation is used, which assumes non-Gaussian distribution in the data set. In Figure 3, the same data set is analyzed by analysis of covariance, which assumes Gaussian distribution. This is obviously contradictory. While it is possible to perform a non-parametric analysis of covariance, it is unclear whether this was done here. In Figure 3, it is also unclear why analysis of covariance was used to analyze the data set, and why Abeta40 and Abeta38 were chosen as covariates. Furthermore, analysis of covariance is only permitted if a linear correlation is observed between the variables. However, significant correlation was only found for the control individuals in Figure 3. In Figure 5, it is not disclosed which test was used to calculate P values.
1st Revision -Authors' Response 03 June 2011 Dear Dr. Funk: Thank you for your kindness to move back the deadline one month. We have finally finished the experiments and now send the revised manuscript. The revised one, I believe, address the major issues-more rigorous statistical analysis and AD model mice analysis-raised by the reviewers.
Replies to the two reviewers are on the separate sheets. The most important and new observations described in the revised manuscript is that g-secretase in aged Tg2576 mouse brains appears to behave as we anticipated, though not absolutely statistically significant (the number of mice are n=3 for each group: It was extremely difficult to obtain aged Tg2576 mice and littermates). This supports our hypothesis that lower Ab42 and 43 in CSF is the consequence of altered g-secretase activity rather than preferential deposition of Ab42/43. I do hope that the revised one is now suitable for the publication in EMBO Molecular Medicine. I am looking forward to hearing from you.
Reply to Reviewer 2 Thank you for your suggestion. As you pointed out, we estimated the correlation coefficients and regression lines for the separate data groups. The results are shown in the following The results could give us some interested findings, for example, correlation coefficients of separated data groups tend to increase, comparing with that of the pooled data group. However, we are able to describe all of what we want to claim in the revised manuscript without the above table. Accordingly, we do not add this table to our manuscript.

Reply to reviewer 3
We added the detailed description of statistical methods in the method section.
In We think the ANOCOVA can be applied to the logarithmic-transformed data in Figure 3, because all correlation coefficients have statistical significance.
In Figure 5, we used ANOVA, Dunnett's t-test and Bonferroni's t-test to compare the means of ln(Ab40/43) and ln(Ab38/42) among three groups. We described the statistical methods in the method section.
As the reviewer suggested, we measured g-secretase activities in the brains of aged Tg2576, young Tg2576, aged littermates, and aged littermates. I hope the reviewer can understand it is extremely hard to obtain a large number of aged Tg2576 and aged littermates enough for accurate statistical analysis. Our experiments were done with 3 mice for each group. We focused on raft-associated gsecretase rather than detergent-soluble g-secretase, because the previous data suggest that gsecretase is concentrated in rafts (Wada et al, Biochemistry 47:13977-13986, 2003). As the method of measuring the raft g-secretase activity was not established, we first determined the assay conditions. The incubation of raft fraction with bCTF generated exactly the same peptides we previously found in the detergent-soluble g-secretase assay system. Preexisting bCTF bound in rafts generated only negligible levels of Abs, and their generation was found to be dependent exclusively on exogenously added bCTF. Thus we concluded that addition of bCTF to raft fraction make possible to measure the raft-associated g-secretase activity, although we do not know how the exogenously added bCTF is integrated into raft, get access to and is degraded, by g-secretase embedded in raft. To assess the g-secretase activity in each brain, produced Abs, Ab43, 42, 40, 38 were quantified by Western blotting, and the product ratios Ab40/43 and Ab38/42 were calculated. As you can see in Fig S4, the ratio Ab38/42 for aged Tg2576 tended to be higher than those for other mice, and the ratio Ab40/43 for aged Tg2576 was significantly higher than those for other mice except young littermates. These observations are consistent with our assumption that gsecretase activity in MCI/AD brain has higher ratios of Ab40/43 and Ab38/42. This highly suggests that lower Ab42/43 in CSF reflects altered g-secretase activity rather than preferential deposition of Ab42/43 to senile plaques.
2nd Editorial Decision 21 July 2011 Thank you for the submission of your revised manuscript "γ-Secretase activity may be altered in the brain affected by mild cognitive impairment and Alzheimer's disease" to EMBO Molecular Medicine and please accept my sincere apologies for the delayed reply. We have now received the enclosed report from the referee whom we asked to re-assess it and received external advice on the manuscript.
As you will see, the Reviewer still raises significant concerns about the conclusiveness of the results. However, since we do acknowledge the potential interest of your findings, we would be willing to consider a revised manuscript with the understanding that the referee concerns must be convincingly and conclusively addressed.
Specifically, the Reviewer is not convinced that the newly added animal data support the conclusions since they do not reach statistical significance and the numbers used were very low. It will thus be crucial to extend these studies. Importantly, the Reviewer also points out that discussion of previously published data on the production of Abeta42 and 40 in AD should be included.
Regarding the statistical analysis of the data, we consulted with a statistics expert and he/she indicated that the analyses are justified and sufficient.
We realize that the addition of more in vivo data will be time-consuming and are thus able to extend the standard review time.
I look forward to reading a new revised version of your manuscript as soon as possible.
Should you find that the requested revisions are not feasible within the constraints outlined here and choose, therefore, to submit your paper elsewhere, we would welcome a message to this effect.

Yours sincerely,
Editor EMBO Molecular Medicine ***** Reviewer's comments ***** Referee #3 (Comments on Novelty/Model System): In my view, this revision does not adequately address the weak points of the initial submission. Both reviewer 2 and myself have criticized the lack of supporting evidence from an experimental model. The quality of the animal data provided in the revised manuscript is low and mostly shows nonsignificant trends. The authors have further made changes to the statistical analysis, which has weakened some of the conclusions (e.g., the Abeta38 levels in AD are not significantly different from controls anymore). I continue to be skeptical about some of the statistics, e.g., I am not sure whether the data transformations in the revised manuscript are permitted and whether regression analysis is at all appropriate to analyze correlation between two independent variables. However, I have to admit that my statistical expertise is too limited to fully assess these details. If the journal continues to be interested in this study, I would advise two things: 1. Give the authors enough time to perform a conclusive animal study with a sufficient number of animals (> 6-9 months). 2. I would have a statistician review the next revision as the statistics are key in this study.

Referee #3 (Other Remarks):
This is the revised version of a manuscript by Kakuda et al. The authors have investigated the levels of four Abeta (43/42/40/38) species in CSF samples of individuals with AD or MCI and healthy controls. Based on the sequential cleavage model of gamma-secretase processing, the authors propose that the observed Abeta signature indicates that gamma-secretase activity is enhanced in AD/MCI towards the generation of Abeta40/Abeta38, and that this is the underlying mechanism for the drop in CSF Abeta42 levels in AD/MCI reported in numerous previous studies. The initial submission was based solely on data from the CSF measurements. The authors have now added animal data to the supplementary material, which they claim provides support for their hypothesis. They have further made some changes to the statistical analysis.
Specific criticisms: 1. Unfortunately, the authors continue to ignore previous studies that do not support their own data (see my previous comments 1 and 2), particularly the fact that familial AD is associated with both enhanced production of Abeta42 and a drop in CSF Abeta42, and previous CSF measurements of Abeta40 levels that did not find changes in MCI/AD. While these studies do not discredit the results of the authors, it is critical that the authors discuss their own findings in the context of the existing literature and cite these studies appropriately.
2. The authors have now included data showing that raft preparations from young and old Tg2576 mice and littermate controls can (de novo) generate Abeta peptides in the presence of APP-C100 substrate. They show that the Abeta38/Abeta42 ratio tends to be higher in old Tg2576 mice compared to the control groups. In addition, they report a significant difference in the Abeta40/Abeta43 ratio of old Tg2576 as compared to two control groups, but not the third one (young littermates). They claim that this data is highly supportive of their hypothesis that gammasecretase activity is altered in the AD brain, and that this phenomenon is responsible for reductions in CSF Abeta42 levels in AD. It is acknowledged that it is difficult to perform conclusive animal studies in the short period of time provided for the revision of a manuscript. However, I disagree that the quality of the presented animal data is sufficient to strengthen the claims of the authors. The trends shown for the Abeta38/Abeta42 ratio are meaningless given the small number of animals included in the study. Furthermore, the lack of a significant difference in the Abeta40/Abeta43 between old Tg2576 and young littermates also suggests that the distribution of the data could be entirely due to chance at this point. Both reviewer 2 and myself have criticized that the hypothesis of the initial submission was based solely on the presented CSF measurements. These measurements were in part contradictory to previous studies. No supporting data from experimental models was provided, and this has not fundamentally changed with this revision.
2nd Revision -Authors' Response 03 November 2011 Reply to reviewer 3 Thank you for your kind advice and critical comments on our work. We would give our thoughts on three points. 1) Higher Ab40 measures in MCI/AD; 2) Difference between S(sporadic)AD and FAD in the plot; and 3) Direct quantification of human brain raft-associated g-secretase activity.
1) The reviewer points out that higher Ab40 of CSF is not previously reported in MCI/AD, but our data indicate that they are clearly higher than controls. We do not know the exact reason, but one reason would be that the specificities and combination of used antibodies. 82E1, anti-Ab N-terminal specific antibody, recognized only 1-X Abs but not amino-terminally truncated Abs and aminoterminally extended Abs (Qi-Takahara et al. J Neurosci. 25:436-445, 2005). Thus, we measured only Asp-starting Abs, but it is possible that other groups would have measured amino-terminally truncated Abs in addition to 1-X. In this regard, we would like to add that the ratio Ab40/43 rather than the absolute level of Ab40 alone appears to have much more power to discriminate between MCI/AD and control. Part of this is included in page 11, line 20 to page 12, line 7. 2) We measured the ratio Ab40/43 and Ab38/42 in CSF from 5 (symptomatic) FAD patients carrying mutant PS1s, T116N, L173F, G209R, L286V and L381V. These plots are grouped into three types. Two are distant from the origin like sporadic AD cases and one is closer than controls to the origin. Remaining three are extremely displaced from the regression line. Thus, the CSF alternations by PS1 mutation is not the same in found in sporadic AD cases. Currently we do not have appropriate interpretation to this observation: Probably a larger number of mutant PS1 cases would be needed for reasonable speculation. A part of the above is included in page 8, line 23 to page 9, line 7.
3) The reviewer suggested that a larger number of mice have to be examined because of great individual variability observed in this kind of model mice. However, it is extremely hard for us to obtain a large number of aged Tg2576 and aged littermates sufficient for accurate statistical analysis. Thus, we used human brain specimens (PMI<12h) to measure brain g-secretase activity. We focused on raft-associated g-secretase rather than detergent-soluble g-secretase, because the previous data suggest that g-secretase is concentrated in rafts (Wada et al, Biochemistry 47:13977-13986, 2003; see "Quantification of human brain raft-associated g-secretase activity " in the materials and methods in the revised manuscript).
To assess the raft g-secretase activity in each brain, produced Abs, Ab43, 42, 40, 38 were quantified by Western blotting, and the product ratios Ab40/43 and Ab38/42 were calculated. As you can see in Fig 5 (new figure), the ratios Ab38/42 and Ab40/43 for MCI/AD were found significantly higher than controls. These observations are consistent with our speculation based on CSF data suggesting that g-secretase activity in MCI/AD brain has higher ratios of Ab40/43 and Ab38/42. Thus, lower Ab42/43 in MCI/AD CSF reflects altered g-secretase activity rather than preferential deposition of Ab42/43 to senile plaques.
3rd Editorial Decision 25 November 2011 Thank you for the submission of your revised manuscript to EMBO Molecular Medicine. We have now received the enclosed report from the reviewer that were asked to re-assess it. As you will see the reviewer is now supportive and I am pleased to inform you that we will be able to officially accept your manuscript pending the following final amendments: Importantly, the reviewer highlights that existing literature should be discussed adequately.
On a more editorial note, please see below for information regarding EMBO Molecular Medicine guidelines for statistical analysis of data and accordingly please mention the actual p value in each case. Please also include a Table of Contents as the first page of the Supplementary Information. Importantly, please note whether informed consent has been obtained from the patients in the respective part of the Material and Methods section.
Please submit your revised manuscript within two weeks. I look forward to seeing a revised form of your manuscript as soon as possible.

Statistical analysis
The description of all reported data that includes statistical testing must state the name of the statistical test used to generate error bars and P values, the number (n) of independent experiments underlying each data point (not replicate measures of one sample), and the actual P value for each test (not merely 'significant' or 'P < 0.05'). Descriptive statistics should include a clearly labelled measure of centre (such as the mean or the median), and a clearly labelled measure of variability (such as standard deviation or range). Ranges are more appropriate than standard deviations or standard errors for small data sets. Standard error or confidence interval is appropriate to compare data to a control. Graphs must include clearly labelled error bars for cases where more than two independent experiments have been performed (error bars for replicate samples are less useful). Authors must state whether a number that follows the {plus minus} sign is a standard error (s.e.m.) or a standard deviation (s.d.) Figure legends should contain a basic description of n, P and the test applied, and the Methods should contain further discussion of statistical methodology. Since for complex biological experiments the number of independent repeats of a measurement often has to be limited for practical reasons, statistical measures with a very small n are commonplace. However, statistical measures applied to too small a sample size are not significant and they can suggest a false level of significance. We recommend that the actual individual data from each experiment should be plotted if n < 5, alongside an error bar. In cases where n is small, a justification for the use of the statistical test employed has to be provided. Presenting a single 'typical result' of n experiments is sometimes unavoidable, but should be accompanied by an indication of the variability of data between independent experiments. If n is not based on independent experiments (that is, n merely represents replicates of a measurement), statistics may still be useful, but a detailed description of the repeated measurement is required.
Authors must justify the use of a particular test and explain whether their data conform to the assumptions of the tests. Editor EMBO Molecular Medicine ***** Reviewer's comments ***** Referee #3: This is the second revision of a manuscript by Kakuda et al. The authors have investigated the levels of four Abeta species in CSF samples of individuals with AD/MCI and healthy controls, and propose that the observed Abeta signature indicates that gamma-secretase activity is enhanced in AD/MCI towards the generation of Abeta40/Abeta38, and that this is the underlying mechanism for the drop in CSF Abeta42 levels in AD/MCI. In the first revision, the authors had added experimental animal data to support their hypothesis, showing that Abeta generation from raft preparations of old APP-transgenic also tended toward enhanced generation of Abeta40/Abeta38. However, the results from these studies were only partially significant and the experiments were abandoned for this second revision. Instead, the authors have now performed similar experiments with raft preparations from human brain tissue. These experiments again demonstrated that the cleavage efficiency from Abeta42 to Abeta38 and Abeta43 to Abeta40 is significantly enhanced in AD/MCI versus control. While, in my opinion, these data do not reach the same level of proof as verification in an experimental animal model, I believe that the manuscript now contains enough interesting information to justify publication and to invite rapid replication by other groups. What continues to be an issue is that the authors do not sufficiently acknowledge the existing literature and alternative points of view. A recent study by Dennis Selkoe's group has provided direct experimental evidence in APP-transgenic mice that soluble Abeta42 is increasingly sequestered into insoluble parenchymal Abeta deposits (Hong et al. 2011 J Neurosci 31:15861-9). This study needs to be cited and adequately discussed. We finally submit the revised manuscript entitled "Altered g-secretase activity in mild cognitive impairment and Alzheimer's disease". Corrected parts or additions follow.
2 Regarding every autopsy material used for the additional experiments from Brain Bank at Tokyo Metropolitan Institute of Gerontology, there was a written informed consent from patient or his/her family. This statement was added in page 17, lines 24 -page 18, lines 2).
3 We have just received exact P-values from our statistician, which replaced previous expressions throughout the manuscript except two parts, Dunnett's t-test for multiple comparisons in the Table and P-values in Figure 3. In the latter case his software does not give exact numbers, if the values are <0.001.
We do hope that revised one is now suitable for the publication in EMBO Molecular Medicine.

Editorial Correspondence 05 January 2012
Thank you again for the resubmission of your article and please accept my apologies for the delayed reply.
I now had the chance to read and edit the article. Since I changed some sentences with the aim to make them clearer, please find the edited version of the article attached for your approval/comment. Please go carefully through the abstract and article to ensure that I didn't inadvertently change meaning.
In addition, I would encourage you to add regression lines to the graphs in Fig 3 since