In their Correspondence, Charlotte Peterson's group suggests that methodological weaknesses of our paper (Egner et al., 2016) preclude the interpretation that satellite cells (SCs) are obligatory for hypertrophy after mechanical overload (OL), a finding conflicting with their own study concluding that SC depletion does not affect overload hypertrophy (McCarthy et al., 2011).

Most papers are subject to methodological strengths and weaknesses. In our paper (Egner et al., 2016), we highlight some limitations of the McCarthy study (McCarthy et al., 2011), specifically: their reliance on muscle weights as a proxy for fiber hypertrophy rather than using direct cell size measurements; the inclusion in their histological analysis of a high number of fibers with central nuclei or embryonic myosin (eMyHC); and the fact that their paper is based on an unusually small increase in fiber size (≈10%) compared with the 25-60% increase in the existing literature on the 2-week plantaris synergist ablation model (Dearth et al., 2013; Egner et al., 2016; Huey et al., 2016; Perez-Schindler et al., 2013; Zempo et al., 2016). It is this ≈10% hypertrophy in control muscles that they subsequently fail to blunt by SC depletion.

These limitations of the McCarthy paper (McCarthy et al., 2011) can, in our opinion, explain the discrepancies between the two papers. As we understand it, these limitations are uncontested in their Correspondence.

Another important difference between our work and that of McCarthy et al. is that we studied both the plantaris and the extensor digitorum longus (EDL) muscles. We regret that the Peterson group does not regard the EDL as a relevant overload model for hypertrophy, particularly since it has frequently been used as such for at least 40 years by various laboratories (Deveci and Egginton, 2002; Dick and Vrbová, 1993; Egginton et al., 1998; Fortes et al., 2015; Freeman and Luff, 1982; Frischknecht and Vrbová, 1991; Goldspink, 1981; Hamilton et al., 2010; Johnson and Klueber, 1991; Rosenblatt and Parry, 1993; Schiaffino et al., 1972; Young et al., 1992). It seems implausible that the load on the EDL should not be increased by ablating its synergist; the question is how much. We do not think that the electromyography data from stereotype walking experiments in cats cited by the Peterson group (Carlson-Kuhta et al., 1998) provides full justice to the varied movement patterns of free mice in cages (climbing, standing, jumping, etc.), and regardless of this, the EDL clearly undergoes hypertrophy after overload and therefore offers an independent muscle in which to evaluate the necessity of satellite cells.

It is interesting that the Peterson group now suggests that the low degree of hypertrophy in their overloaded plantaris could be due to fiber splitting. A very small increase or even reduction in cross-sectional area (CSA) accompanied by an increase in the number of fibers has previously been reported in a few studies (Ferry et al., 2014; Joanne et al., 2012; Parsons et al., 2004), but to our knowledge not for observation periods as short as 2 weeks, and even most long-term studies report a robust hypertrophy (Ballak et al., 2016, 2015; Dunn et al., 1999, 2000; Guerci et al., 2012; Ito et al., 2013; Johnson and Klueber, 1991; White et al., 2009). Although fiber splitting was not studied in either of the two papers, and is not a well-understood phenomenon, we agree that it is a reasonable speculation about the causes of the poor hypertrophy observed in the SC+OL+ muscles by McCarthy et al. (2011) (since we observed more robust hypertrophy, we think it less likely to be a significant issue in our own work). Although it is possible that an initial hypertrophy was masked by subsequent fiber splitting, we would argue that this makes the material poorly suited to unravel the importance of SCs for hypertrophy defined as a size increase of pre-existing cells.

We are pleased that the Peterson group agrees that both papers demonstrate that the SC depletion was sufficient to abolish myonuclear accretion. The number of myonuclei is the crucial parameter because it is the myonuclei and not the SCs that are involved in the protein synthesis during hypertrophy. We therefore do not understand why a discussion about possible moderate differences in the degree of SC depletion is relevant. It also seems illogical to us that an alleged higher residual SC population in our study should lead to less hypertrophy.

We also disagree that McCarthy has demonstrated a more efficient SC ablation, and are unable to follow the authors when they state in the Correspondence that ‘We do not include tamoxifen-treated mice that are less than 90% depleted in our analyses’ as in their paper they report a range of 84 to 98% (fig. 1B legend in McCarthy et al., 2011). Moreover, whereas we report data from the plantaris, where the degree of depletion ranged from 66 to 84%, they reported data from the gastrocnemius. This is unfortunate as observations from the gastrocnemius are not directly relevant for studies on the plantaris. The numbers are not comparable because both the absolute number of SCs and their ability to proliferate varies between muscles (Gibson and Schultz, 1983; Lagord et al., 1998; Ono et al., 2010).

The Peterson group moves on to state ‘That SCs are not effectively depleted is most clearly demonstrated by the observation that markers of muscle regeneration [embryonic myosin heavy chain (eMyHC)-positive and centrally nucleated fibers] are significantly higher in SC− compared with SC+ plantaris with overload (figure 2B-D in Egner et al., 2016)’. This description of the data is formally correct, but highly misleading. Thus, the difference between the two papers is that McCarthy et al. reported a >15× higher frequency of fibers with such markers in their OL+SC+ group compared with our data (comparing figure 3C,D in McCarthy et al., 2011 and figure 2B,C in Egner et al., 2016). We attribute this to more overload- or surgery-induced damage observed in their muscles. Both groups reported, however, the same frequency of fibers with such markers in the OL+SC− muscles. If the frequency of fibers with central nuclei or eMyHC is related to the number of SCs, this would indicate that the number of residual SCs is similar in the two studies.

In any case, the reduction in a prominent damage and repair process by SC depletion reported in the McCarthy paper has little bearing on our paper as, contrary to what is argued in the Correspondence, we observed much less damage. Thus, in the material analyzed in McCarthy et al., they reported that 30% of the fibers in the OL+SC+ population displayed central nuclei/eMyHC, whereas we report 4% and none of our experimental groups was above 13%. We also would point out that whereas McCarthy included their significant population of fibers with such markers, we excluded the relatively few we had from further analysis. Our reasoning was that hypertrophy is defined as a size increase in pre-existing cells, and that damage or repair are confounding factors in the study of this phenomenon. Although it seems likely that such markers are related to damage and repair, at this stage we do not know if they appear in pre-existing fibers, regenerating fibers, new fibers or split fibers. In any case, a high incidence of fibers with such markers is a confounding factor.

Importantly, the appearance of central nuclei/eMyHC is less of a problem in the EDL. The fraction of fibers with such markers was 1.3% or lower in all the experimental groups. The EDL model has the advantage that the overload is probably gentler than for the plantaris because the size ratio between the ablated and remaining synergist is smaller, and perhaps because the muscles on the ventral side are less loadbearing, as discussed by the Peterson group. Thus, the EDL model might be less supraphysiological than the plantaris model.

Regarding the age difference in mice used between the two studies (McCarthy et al. report using 4 month-old and we 3-4 month-old mice), although we cannot exclude that there is a critical period for SC dependence between 3 and 4 months, we are not aware of any evidence for such a notion. C57BL/6J mice are considered mature adults when they are 3-6 months old (Flurkey et al., 2007), and we do not understand why referring to rapid bone growth of mice age <3 months (Ferguson et al., 2003) is relevant to our study.

The Peterson group raises valid concerns about the effect of tamoxifen on body weight. Both groups, however, used the same dosage and our animals appeared healthy. As far as we can tell, neither the McCarthy paper (McCarthy et al., 2011), nor the other papers from the Peterson group quoted in this context in their Correspondence (Fry et al., 2014, 2015; Jackson et al., 2015, 2012), reported numbers for body weights, but by comparing muscle weights corrected and non-corrected for body weight we calculate a difference of 9% for the non-running group in Jackson et al. (2015) compared with our 13%. In their Correspondence, the Peterson group also provides hereto unpublished data on body weight for the McCarthy material, and report that the tamoxifen effect was smaller (4%).

Lower body weights are commonly observed in animals given the estrogen antagonist tamoxifen compared with controls. This seems to be due to reduced accumulation of body fat (Lampert et al., 2013; Liu et al., 2015), whereas protein is not significantly affected (Wade and Heller, 1993). We agree that controls with tamoxifen treatment of the parental Pax7-CreER strain would have been desirable, but these were not used in either of the two studies (Egner et al., 2016; McCarthy et al., 2011). Although we cannot exclude the possibility that the lower weights might have had some influence on the hypertrophic response in our case, we observed no atrophy in OL− muscles that were given tamoxifen; the fibers were similarly large with and without tamoxifen. Moreover, tamoxifen did not blunt hypertrophy after 8 weeks synergist ablation in the parental Pax7-CreER mouse strain (Fry et al., 2014).

Although randomized sampling of fibers on sections is a common method in the literature and provides good estimates of the average values for the whole population, we agree with the Peterson group that measuring all relevant fibers (but we suggest excluding damaged/regenerating fibers) rather than a randomized sample would have been an optimal strategy. It is correct that using standard grid sampling, as we did, would tend to oversample large fibers, but automatic CSA measurements (as used by McCarthy et al.) might also introduce systematic differences. Although such factors might influence absolute values, there would be a similar bias for controls and experimental groups, so we do not think these methodological differences could explain the completely different outcomes of the two studies.

We are more inclined to attribute the different outcome to the appearance and inclusion of a significant population of damaged fibers by McCarthy et al. Their cell size analysis might also be statistically underpowered because there was such a low degree of hypertrophy in the control muscles with intact SCs (Fig. S2E). A potential blunting of a ≈10% hypertrophy by SC depletion might be hard to detect. The re-analysis published in their Correspondence seems to have increased the variance, further aggravating this problem.

Thus, based on our interpretation of the current literature, including the two papers debated here (Egner et al., 2016; McCarthy et al., 2011), we maintain our conclusion that satellite cells seems to be obligatory for a robust de novo hypertrophy.

While we were finalizing this Correspondence Response, this conclusion was supported by new data from a completely different genetic model, but subjected to the same overload experiment. In this study, when satellite cells were prevented from fusing to muscle fibers during overload, hypertrophy was prevented (Goh and Millay, 2017).