Presenilins: a novel link between intracellular calcium signaling and lysosomal function?.
J Cell Biol. 2012 Jul 9;198(1):7-10.
Please login to recommend the paper.
To make a comment you must login or register.
When Lee et al. published their study in 2010, it made a big impact in the field because it described a novel role for PS1 in lysosomal acidification and—even more importantly—suggested that mutations in PS1 attributed to familial AD (FAD) can cause similar defects in patients' fibroblasts. This finding would have nicely tied together PS mutations in FAD, Aβ formation, and pathologically observed lysosomal and autophagosomal deficits (Pickford et al., 2008; Nixon et al., 2005; Boland et al., 2008).
In 2011, Neely et al. published a study that explored the role of PS on autophagosomal-lysosomal degradation. It found that PS1 and PS2 are "important for overall degradation through autophagy in multiple cell types and indicate that presenilins are key regulators of autophagolysosome formation or lysosome function." However, the authors did not find signs of altered lysosomal acidification and conclude "presenilins might function at the lysosome in another manner besides lysosome acidification." Given the high-profile nature of the study by Lee et al. and the potential implications for the treatment of FAD patients, many independent groups have tried to repeat and expand on the Lee findings.
Now, two new studies (Zhang et al., 2012; Coen et al., 2012) support the findings of Neely et al. in that a lysosomal acidification defect is absent and thus appears not to be the primary cause of PS1/2-mediated autophagosomal-lysosomal deficits. The Zhang study systematically reexamines the findings from the Lee paper, and the authors cannot reproduce many of the acidification-related findings, both in vitro and in vivo. While they discuss the possibility that some clonal drift might have occurred in the cells studied by Lee et al., causing the differences in results between the two studies, the Coen paper uses many of the same cell lines as the Lee study and also fails to observe acidification deficits. Currently available data suggest that acidification defects are unlikely to be involved in PS-mediated autophagosomal-lysosomal deficits.
Nevertheless, all these studies collectively strongly support an important role for PS1/2 in maintaining proper flux and degradation capacity in the autophagosomal-lysosomal system. Further studies will be needed to elucidate this crucial cellular degradation pathway and its role in AD/FAD—whether PS acts by "selective impairment of autolysosome acidiﬁcation and cathepsin activation" (Lee), by "mediating autophagosome-lysosome interaction or lysosome function" (Neely), by "calcium storage/release" (Coen), or by "regulating lysosomal biogenesis" (Zhang). This latest rush of partially contradictory findings will undoubtedly stimulate more exciting research, and future studies will show if PS contributes to some or all of the proposed functions.
Controversy makes for better news than consensus but we need to keep in mind that there is considerable agreement about the links between PS1 and autophagy defects in AD. Four different lab groups agree that autophagy is disrupted by PS-deletion and/or PS1FAD mutations (1-4). Each of these groups also implicates defects in lysosomal function directly or indirectly as a basis for autophagy dysfunction. The one exception is the report from a fifth group led by Sam Sisodia, which concluded that PS has no role in autophagy at all (5). A careful look at that report will show that no direct assessment of autophagic protein turnover was actually made in the Zhang et al. study. The points of agreement among the four different labs are of paramount importance for AD pathogenesis and therapy since autophagy, particularly the proteolytic clearance steps, are clearly disrupted in all forms of AD and AD models (6-8). Selectively enhancing lysosomal function in AD mouse models by any of several mechanisms has been shown to have marked therapeutic effects on amyloid and lysosome pathology, synaptic function, and behavior (9-12). Conversely, AD-related pathologies can be produced experimentally by inducing selective lysosomal proteolytic dysfunction (8,13). Autophagy impairment provides a basis for the amplified amyloid and lysosomal system neuropathology and the earlier clinical onset seen in PS-FAD versus sporadic AD (14,15).
Divergence arises in views on the mechanism(s) underlying PS-related lysosomal dysfunction. Coen et al., in one of the two studies that addresses mechanism (1,4), challenge the mechanism we reported, which is based on impaired lysosomal acidification due to PS1-dependent vATPase hypofunction. Instead they show abnormal calcium release from lysosomes, although they do not explain the mechanism of this defect or how the defect is mechanistically linked to PS or PS loss. In extensive ongoing studies, we observe the same calcium abnormality but we can show that the effect is secondary to impaired lysosomal acidification and can be corrected by normalizing lysosomal pH. This is not surprising given the very close relationship already known to exist between pH and calcium regulation in lysosomes (16,17). What is more surprising to us, based on the literature, is why Coen et al. did not see a lysosomal pH alteration in the face of such significant lysosomal calcium release.
Why, then, is it that we can consistently measure abnormal pH elevation in lysosomes of PS1-deficient blastocysts, PS1-FAD fibroblasts, PS-deficient neurons, and, in our newer analyses, in all of the cell lines reported in the recent studies, while three groups claim to see no differences in lysosomal pH values? A closer look at the data in two of the papers (3,5), reveals that these groups did not actually measure lysosomal pH.
The Zhang, Sisodia et al. study used an unconjugated dye that enters all vesicular compartments of the cell, not lysosomes specifically. The value for “vesicular pH” of 6.6, which is the basis for the claim in the report’s title that lysosome acidification in PS models is normal, has no relevance to the pH of lysosomes, which is well established to be below 5.0. Of significant concern is that the majority of the pH values measured in the wild-type cells were above pH 7.0 and even above the range of the standard curve. Inexplicably, these values were excluded from the calculation of “vesicular pH,” which is astonishingly high even without including these arbitrarily omitted values. Clearly, this analysis bears little relationship to pH of even the acidic vacuolar system of the cell, much less the lysosome itself.
In the earlier Neely et al. report (3), pH was only assessed indirectly by LysoTracker intensity. Although LysoTracker is a pH-sensitive dye, it is mainly an organelle marker and not a substitute for dyes designed to measure pH rigorously. LysoTracker signal intensity does not consistently reflect acidity of lysosomes (18,19). Importantly, unless LysoTracker signal is calculated per lysosome, rather than per cell as in this report, the size and/or number of lysosomes confound the signal intensity as a readout of acidity.
Coen et al. used several methods to assess pH, including LysoTracker—at 250 times the manufacturer’s recommended concentration. They also used dextran-conjugated fluorescein, which exhibits pH dependent changes in fluorescence intensity within the pH range of 5-9 and is most appropriately used to assay pH values closer to neutrality due to its extremely low sensitivity at acidic pH, according to the manufacturer’s technical bulletins. This group also used LysoSensor Yellow/Blue DND-160, which was not targeted specifically to lysosomes, and obtained ratiometric values but did not calculate pH values, thus limiting any evaluation of whether relevant lysosomal pH values were obtainable with this method.
In contrast to these approaches, we measured lysosomal pH with a dextran-conjugated ratiometric dye specifically targeted to lysosomes and optimally sensitive to the pH range of lysosomes (1). The elevation of pH in PS1 models was supported by demonstrating predicted changes in a broad range of lysosomal pH-dependent phenomena, including but not limited to (1) decreased in situ activity of cathepsin D and of cathepsin B in lysosomes of living cells (2) decreased activity and specific activity of cathepsins D, B, and L measured in vitro (3) impaired maturation of cathepsin D (4) failed dissociation of MP6R from cathepsins (5) accumulation of autophagy substrates in autolysosomes and pathological accumulation of autolysosomes confirmed by double immunofluorescence labeling and EM (6) delayed clearance of autophagy substrates from autolysosomes after induction of autophagy and (7) recapitulation of the above phenotypic features by bafilomycin 1 treatment (1).
These findings are consistent with the loss of lysosomal vATPase we reported. Our new soon to be submitted work will provide, in our opinion, compelling further evidence implicating vATPase hypofunction in PS cell models and AD mouse models. A similar mechanism has now been shown to explain autophagy dysfunction in Parkinson’s Disease due to mutations of another lysosomal proton pump, ATPase13a (20). Space limits do not permit a detailed discussion of concerns about the vATPase data in the new reports but the exclusive use of vATPase over-expression in the Zhang et al. study is not expected to yield definitive insight into the behavior of the protein at endogenous levels and, in the Coen et al. report, the atypical molecular weight of the vATPase band monitored, >20 kD lower than the molecular weight reported by all other labs, is quite puzzling (21, 22). Moreover, Coen et al. report that vATPase V0a1 and V0a2 knock down in PC12 cells had no effect on lysosome acidification, citing the work of Saw et al. (23) as support. In fact, this finding actually directly conflicts with Saw et al., who reported lysosomal acidification defects induced by V0a1 or V0a1/V0a2 knockdown using the identical knockdown construct and PC12 cells (23).
In 2010. Lee et al. (Lee et al., 2010) reported that, as a consequence of presenilin deficiency, lysosomes fail to acidify. In their view, presenilin 1 is required for proper glycosylation of the Voa1 subunit of the vATPase, and improper glycosylation in presenilin-deficient cells precludes delivery of the vATPase to lysosomes. This is an attractive model, but the notion that single cells, let alone multicellular organisms (like people), can exist without functional lysosomes needs to be examined very carefully. Indeed, a number of groups—including our own—tested the model, but failed to replicate the findings of Nixon’s group (Coen et al., 2012; Zhang et al., 2012; Neely et al., 2011).
In a recent submission to Alzforum, Nixon and colleagues summarily dismiss these more recent findings, stating that “these groups did not actually measure lysosomal pH.” This statement is inaccurate and ill informed. In addressing our work, Nixon et al. state that we not only used the wrong concentrations of pH-sensitive probes, but even the wrong probes! This conclusion is seemingly based on the manufacturer's technical bulletins. Nixon and colleagues would have reached a different conclusion had they instead read the original scientific literature in some detail (including our paper). Firstly, their claim that we used LysoTracker at 250 times "the manufacturer's recommended concentration" is simply untrue. As explicitly stated in our paper (Coen et al., 2012), we used 250 nM LysoTracker Red, about three times the concentration recommended by Invitrogen and 2.5 times the concentration used by Lee et al. themselves (Lee et al., 2010). Considering the buffering capacity of lysosomes (upwards of 30 mM/pH), there is no reason to expect nanomolar concentrations of LysoTracker to affect the measured pH. Indeed, we could readily document differences between untreated lysosomes and lysosomes treated with vATPase inhibitors or weak bases, yet never saw a difference between wild-type and presenilin-deficient cells.
Nixon et al. also criticized our use of fluorescein-conjugated dextran to measure lysosomal pH, again based on a manufacturer’s technical bulletin. Since the pioneering work of Ohkuma and Poole (Ohkuma and Poole, 1978), fluorescein-conjugated dextran has been the method of choice to measure lysosomal pH, as attested by dozens of publications from multiple laboratories (e.g., Barriere et al., 2007; Trombetta, 2003; Ohkuma and Poole, 1978; Yoshimori et al., 1991; Carraro-Lacroix et al., 2011). The pKa and dynamic range of this probe make differentiation between acidic and neutral lysosomes trivial (the 485 nm/440 nm fluorescence ratio changes by >fivefold). Accordingly, we could easily distinguish untreated lysosomes from those exposed to ammonium (which is not a vATPase inhibitor, but a membrane-permeant weak base) or concanamycin (a bona fide vATPase inhibitor). Still, we did not detect differences between wild-type and presenilin-deficient cells.
In another attempt to dismiss our findings, Lee et al. suggest that we inappropriately cited a coauthor’s manuscript and presented data that are in direct conflict with his previously published work (Saw et al., 2011). The record needs to be set straight on this account as well. We indeed utilized PC12 cells with stably knocked-down expression of the Voa1 and Voa2 subunits of the vATPase, and failed to detect any lysosomal acidification defects (in direct contradiction with the model of Lee et al.). This is by no means in conflict with the findings of Saw et al. (Saw et al., 2011), who described altered acidification of dense core vesicles, which Lee et al. would surely agree are secretory organelles, distinct from lysosomes.
In summary, none of the claims made by Lee et al. on Alzforum regarding our pH determinations are correct. Careful reading of the original scientific literature would have avoided such misstatements. We are confident in our data, which are consistent with those of others and do not support the claims made by Nixon’s group.
We would like to continue this collegial, public discussion of why our respective studies are at odds. We believe such discussion is important as numerous labs independently attempt to replicate and build on published work, so that the field as a whole develops robust advances. We agree with Nixon and coworkers that "controversy makes for better news than consensus." On the other hand, some controversy is truly needed to prevent dogma. After all, the first level where consensus can be reached is the scientific data, not necessarily the interpretation of those data. Collectively, we should be able to agree at least on the scientific data at hand.
We point out here that in their comment on the three independent studies that failed to reproduce their original data (Lee et al., 2010), Nixon and coworkers make errors both in interpreting consensus and in their critique of the science.
We and others have shown that PSEN1 regulates (in a γ-secretase-independent way) organelle and protein turnover (1,2), but stating that this function is linked to autophagy defects in AD is premature. Autophagy is a trendy topic, not least in neurodegenerative diseases, including AD. However, just because autophagic vacuoles accumulate in AD does not mean that one can claim autophagy defects in the disease. To our knowledge, autophagosomes may accumulate in people with AD, but the fact that they do form indicates that there is no defect whatsoever with respect to the molecular mechanism of autophagosome formation. Furthermore, the profiling data of Zhang et al. (3) and ours (unpublished), as well as the study by Neely et al. (5), confirm that in PS-deficient cells the formation of autophagosomes is not corrupted.
Autophagy is, in the first place, a "rescue pathway" for the cell to dispose of aberrant or accumulating organelles. As such, autophagy in PS-deficient cells and AD should, in our opinion, not be regarded as the cause but the consequence of transport dysregulation elsewhere in the cell/neuron. Both our group and Kim Green/Frank LaFerla come to exactly the same conclusion—that the defect is located at the level of lysosomal fusion efficiency, not in the autophagy limb of degradation (4,5). We prefer to focus in our future work on unraveling the causes, not being distracted by the consequences.
With respect to Nixon and colleagues’ list of what they consider technical flaws in our data, these "flaws" do not reflect a profound knowledge of the literature or are simply erroneous. Therefore, they contribute to the controversy about the original paper by Lee et al.
Many of the reports discussed here (4-6) highlighted our previous findings that PSEN1 has a role in the degradative machinery of the cell, whether it be in neurons or any other cell type used so far (1,2). The novelty of our report lies in uncovering the underlying mechanism, namely defective storage and release of lysosomal calcium (4), leading to the accumulation of autophagic vacuoles that are unable to be cleared from the cells (1). We therefore provide a mechanism that likely explains the observed endolysosomal defects and impaired lysosomal fusion capacity in PSEN-deficient cells and neurons. How lysosomal calcium is distorted is the next question, and we are currently addressing that. We are pleased to notice that two independent laboratories confirmed this lysosomal calcium deficit (Nixon's and Green's labs; see Kim Green’s comment). This consensus makes us confident of the quality of our experimental approaches.
Nixon and coworkers express surprise that the pH is not altered in the face of observed lysosomal calcium deficit. It is correct that pH and calcium in lysosomes are close partners, but either one can be independently affected. This was demonstrated in the case of Niemann-Pick disease type C patient fibroblasts. There, the late endosomal/lysosomal dysfunction originates from sphingosine accumulations, thereby compromising lysosomal calcium storage and release, and, hence, lysosomal fusion without concomitant lysosomal acidification defects (7).
Nixon and coworkers argue that the failure to demonstrate pH defects is based on the lack of quantitative measurements or technical flaws. This is a surprising statement, given that the original work by Lee et al. (2010) predominantly used the qualitative LysoTracker probe as a readout for acidification defects. In only one single case (Panel I, Figure 3) did they use LysoSensor, and then only to compare wild-type (WT) with PS1 knockout blastocysts (without including any rescue cell lines). The most surprising aspect of their original methodology is that they did not use LysoSensor to quantify pH in individual lysosomes (as it should be done), but, on the contrary, in trypsinized cells, measured total fluorescence of cell suspensions using fluorometry. Molecular Probes, the maker of these reporters, recommends that LysoSensor and LysoTracker should not be used to measure pH by flow cytometry or fluorometry.
The approach by Lee et al. strongly contrasts with ours. We utilized strategies generated independently by two different labs (ours and the Grinstein lab). Besides basic LysoTracker experiments, we used LysoSensor to evaluate pH at the organellar level. Secondly, we included a robust, well-established, live-imaging approach that uses pH-sensitive fluorescein derivatives. Our ability to monitor pH continuously also enabled us to study "online" the effects of reversible alkalinizing drugs or proton pump blockers. This allowed us to extract exact values for different parameters related to proton pump function in addition to the basal pH, including buffering power and rates of H+-leakage from lysosomes. None of these quantitative parameters revealed differences between wild-type and PSEN-deficient mouse embryonic fibroblasts and embryonic stem cells, or fibroblasts from familial AD patients. In an additional approach, we used DQ-BSA, a probe of acid proteases, to assess the activity of enzymes that function optimally in media of low pH. These experiments failed to show any indication of differential pH between the wild-type and mutant/PS knockout cells. Finally, the comment that we exceed LysoTracker concentrations 250 times above the manufacturer’s recommendation is false. We used 200 nM for 30 minutes, as opposed to Lee et al., who used 100 nM for one hour. For live imaging, our collaborators (Grinstein lab) used 250 nM for eight minutes. All experiments were therefore done well within the range used in the literature.
We would also like to comment on the criticisms regarding V0a1 trafficking. Using three independent approaches, we demonstrate that endogenous V0a1 exits the endoplasmic reticulum (ER budding assay), traffics to the cell surface (surface biotinylation), and localizes to endosomal/lysosomal compartments (cell fractionation) in both WT and PSEN-deficient cells, neurons, or blastocysts (the latter unpublished). In other cases, we used stable viral transduction of V0a1 to minimize overexpression artifacts—here, also, V0a1 localized normally to LAMP1-positive organelles.
We used exogenous expression to demonstrate that there is only one N-glycosylation site on V0a1. These experiments, as well as the in-vivo experiments in Drosophila, demonstrate that glycosylation of V0a1 is not important for its trafficking or function in post-Golgi compartments. This is an important finding, as it directly challenges the hypothesis put forth by Lee et al. According to them, PSEN1 chaperones the glycosylation of V0a1 during its translocation in the rough ER. In PSEN-deficient cells, V0a1 fails to become glycosylated, impeding its traffic to lysosomes and consequently affecting proton pump function and lysosomal acidification.
The fact that there is only one glycosylation site—as Nixon and coworkers did not comment on this crucial finding, we assume they agree—has important consequences for the interpretation of the Western blot data. One N-glycan chain maximally gives a mobility shift of 1.5 kDa. We were unable to clearly resolve such a subtle mobility shift in the size range of the protein (100-120 kDa) using the low-resolving 4 to 20 percent precast gels used by Lee et al. Secondly, the primary antibodies Lee et al. used to detect endogenous V0a1 give additional background bands that migrate in the same range as V0a1, complicating further any interpretation of glycosylation differences. We noticed this after selectively downregulating V0a1 with high efficiency—a simple control for antibody specificity that seems absent in the original Cell paper of Lee et al. We invested quite some time to optimize both the gel type and running buffer conditions in order to increase resolution required to properly and indisputably evaluate the glycosylation status of V0a1 in the multiple cell lines used in our study. This allowed us to detect a mobility shift of the endogenous V0a1 and show that these immunoreactive bands indeed represented the endogenous V0a1, and again we controlled by both overexpression and siRNA-mediated knockdown of V0a1. We found that PS knockout had no effect on V0a1 glycosylation.
Secondly, we think most biochemists might agree that the electrophoretic mobility of a protein is a relative measure based on the mobility of commercial reference marker proteins. (The original "p116" name of V0a1 is simply derived from the fact that it runs like the 116 kDa marker). We made an effort to compare six different commercial reference markers in the two electrophoresis conditions (NuPAGE 4-12 percent Tris-Bis gel system using a MOPS-SDS running buffer and Novex 4-20 percent Tris-Glycine gel system using a Tris-Glycine-SDS running buffer, as in Lee et al.). The same sized pre-stained markers not only run at different heights within one gel system (thus different between different companies), but the same set of markers (of one given company) behaves quite differently between the two gel systems. Thus, changing gel systems and running buffers not only alters the electrophoretic mobility of V0a1, but also that of reference markers. This indicates that protocol-based mobility shifts are not a unique feature of V0a1, but are more general than assumed. Again, in these cases, both overexpression and siRNA KD controls rule out any confusion (and such controls are lacking in the work by Lee et al.). Lastly, that proteins behave differently in different gel/running buffer conditions shouldn’t be surprising, particularly for AD researchers. Most in the field agree, for example, that amyloid peptides run in a reverse mobility when analyzed on urea gels.
With respect to the note that we wrongly cited the work of Saw et al., again we have to correct this. The paper by Saw et al. (8) was not about lysosomal acidification induced by V0a1/V0a2 knockdown. Saw and coworkers used an NPY-epHluorin probe for quantification of acidification, but NPY is a neuropeptide and thus marks secretory vesicles in PC12 cells, not lysosomes. This is similar to NPY-EmGFP, which showed strong colocalization with secretogranin II, a secretory granule marker. Secretory granules belong to the biosynthetic-secretory route, while lysosomes are the endstage of endosomal/degradative routes.
As a final note, our paper was submitted to Cell as a Matters Arising paper more than a year ago: According to Cell’s policy, Nixon and colleagues have had our full dataset (including the lysosomal calcium defect) for over a year. In this period they confirmed our original findings on lysosomal calcium. With respect to pH measurements, they focus only on sparse technical details as the basis for a critique that appears to be erroneous. On the other hand, we see no criticisms on our work demonstrating that glycosylation is not required for V0a1 function in vitro and in vivo, or that V0a1 is normally trafficked and located where it should be. Thus, the relevance of the key element in their hypothesis, namely that PSEN1 chaperones the N-glycan transfer in the rough ER, is brought into question. Why would nature bestow such a fundamental role to PSEN1 when V0a1 doesn’t even require it to function?
We appreciate the responses of Annaert and colleagues. We believe disagreement centers on the definition of autophagy. We would respectfully submit that Annaert and Coen misunderstand fundamental concepts of autophagy and the essential role of successful lysosomal proteolysis in this process. This leads them (and Zhang et al. ) to believe that autophagy is completed upon formation of the autophagosome (AP) rather than after autophagosomes and their contents are digested in autolysosomes and the lysosomes are reformed (4,5). Their view of autophagy is at odds with the consensus view of the autophagy community reflected in guidelines on autophagy coauthored by 1,270 investigators in the field (6). When correctly defined as being a much broader, lysosomal degradative process, there is considerable consensus among labs that initial steps in autophagy such as autophagosome formation are normal in PS1 deficiency, but that autophagolysosome clearance by lysosomes is compromised. We reported this (1), and Neeley et al. (2) confirmed.
The main unresolved issue concerns defective lysosomal acidification mechanisms as the main basis for these autophagy defects in PS deficiency. While we were not persuaded by the detailed technical discussion of methods Annaert et al. used to challenge the pH mechanism, this issue will likely resolve itself with forthcoming data. To correct an assertion in Grinstein and Flannagan’s comment, lysosomal function is not completely blocked in PS-deficient cells. If true, this would indeed be incompatible with maintaining cell life: Lysosomes have mechanisms for partial acidification that do not depend on vATPase activity.
The lysosome is, in fact, the only organelle common to all forms of autophagy. New evidence even points to additional critical roles of lysosomal proteolysis in regulating upstream events in autophagy. For example, the mTOR complex controlling autophagy induction is located on lysosomes (7) and is regulated by amino acids released during lysosomal digestion of autophagic substrates (8). Moreover, many of the genes regulating autophagy induction and autophagosome formation are transcriptionally controlled by the TFEB-activated CLEAR network of genes that regulates lysosomal biogenesis (9).
The basic misunderstanding of autophagy reflected in the Annaert commentary explains subsequent unsupportable statements that autophagy impairment is not established in Alzheimer’s disease and AD models. Work in our and others' labs unequivocally documents autophagy-related pathology in AD and AD mouse models (10-16), and links it to AD-related mechanisms that drive lysosome dysfunction (1,10-14,16-26). The additional finding that PS1 hypofunction selectively disrupts lysosomal proteolysis required for autophagy and for recycling of unneeded endocytosed proteins (1) is just one more facet of a rapidly expanding literature underscoring the pathogenic importance of lysosomal proteolytic failure in AD, PD, and some other neurodegenerative disorders (27,28). As also discussed below, scant evidence has been presented by the Annaert group or others for any alternative mechanism that could explain the autophagy phenomenon or specifically the lysosomal calcium defect they describe. We look forward to new, evidence-based ideas on this important area of AD research.
Annaert and Coen challenge the evidence for autophagy defects in AD and PS-deficient models, mainly by citing a consensus finding from reports by Neely et al. (2), Wilson et al. (28), and Zhang et al. (3) that autophagosome formation is normal in PS-deficient cells. We also reported that autophagosome formation is normal in PS-deficient cells (1). Therefore, we all agree on this point. But it is the second part of the autophagy process that is defective in PS-deficient cells. Here again, there seems to be little disagreement among most labs (1,2,28-30) that some aspect of the lysosomal clearance of autophagosomes is impaired by PS deficiency. It is worth reiterating that our studies of PS deficiency revealed diverse evidence of lysosomal proteolytic dysfunction in addition to acidification deficits and vATPase instability.
While the calcium data reported in Coen et al. clearly imply altered lysosome function (30), Annaert dismisses this, and autophagy deficits in general, as consequences of a hypothetical defect in AP-lysosome fusion. Alteration of AP-lysosome fusion is a reasonable idea, and not be mutually exclusive of pathogenic lysosomal deficits, but where are the data to back up the hypothesis? Coen et al. provide no evidence in their paper to demonstrate such a defect, or to clarify a possible mechanism, or to show how this hypothetical defect is mechanistically linked to either calcium dysregulation or to presenilin. In a previous paper, the Annaert group suggested that AP-lysosome fusion was impaired based on one preliminary finding in PS-deficient cells (29), but fusion impairment was not confirmed by either Wilson et al. (28) or Lee et al. (1). Zhang et al. (3) and Neely et al. (2) didn’t investigate AP-lysosome fusion. Specifically, Neely et al. concluded that “our results do indicate that presenilin loss leads to dysfunction at the lysosome.” Moreover, neither of Annaert’s reports provides evidence linking lysosomal calcium release to this putative defect in AP-lysosome fusion.
It may ultimately turn out that AP-lysosome fusion is not normal, particularly when lysosome pH is altered. However, even if solid evidence for a fusion deficit existed, why would one assume that it is primary rather than secondary to lysosomal defects, which they and we have demonstrated? How does this proposed abnormality in fusion come about? In this regard, we have evidence that calcium defects in PS-deficient cells are secondary to lysosome pH elevation, which is a well known basis for altering lysosomal calcium. If there are alternative molecular mechanisms and supporting evidence, we look forward to learning what they are and integrating them into our current thinking.
We have already pointed out some possible reasons why pH measurements by Zhang et al. and Coen et al. yielded different results from ours. Despite the detailed discussion of their procedures, we remain puzzled why Coen et al. presented LysoSensor data as ratios and not pH values, especially given that a similar procedure used by Zhang et al. yielded pH values that were frequently well above 7.0 when they interpolated pH values from LysoSensor ratios using their standard curve. Also, we have previously expressed our concerns about the vATPase data in Zhang et al. and Coen et al. Our published data are fully supported by our latest findings that will be forthcoming. The diminished V01a levels in PS1-deficient cells are consistent with PS1 holoprotein having chaperone function, which is not necessarily restricted to effects on this vATPase subunit. Consistent with such a function, misfolding/degradation of unchaperoned the V01a subunit is critical for its failure to reach lysosomes.
Finally, we hope Annaert and Coen’s last statement in their comment was not meant to imply that our own observations on lysosomal calcium dysregulation were made after reading a limited treatment of their calcium finding in an earlier version of their manuscript submitted to Cell. Given our three decades of work on lysosomes, our longstanding awareness of lysosomal acidification deficits in PS-deficient cells, and the well-known connection between pH and calcium regulatory mechanisms in lysosomes, the logic of investigating lysosomal calcium regulation has occurred to us more than once, certainly dating back more than a year.