On 2014 Aug 04, Paul Brookes commented:

This paper addresses a very important point... namely, one of the proposed mechanisms by which ischemic preconditioning (IPC) is thought to bring about cardioprotection. It has been hypothesized that increased leakiness of the mitochondrial membrane to protons may lead to a lowering of ROS generation. We provided some evidence to support increased H+ leak in IPC in 2006 Nadtochiy SM, 2006. Unfortunately, it's not immediately clear to me exactly how the authors measured H+ leak in this study, and also whether their ROS measurements were performed correctly.

First proton leak: The normal way this is determined is to make simultaneous measurements of membrane potential and respiration in a single chamber equipped with an oxygen electrode and another electrode sensitive to a lipophilic cation such as TPP+. The authors are to be commended on their choice to use a TPP+ electrode, which instantly makes this paper more quantitative than others using qualitative fluorescent probes such as TMRE. They measured membrane potential (as reported in Figure 3) using succinate as a substrate for complex II, with rotenone to inhibit complex I. All good so far. However, normally oligomycin is added to inhibit the ATP synthase as a potential source of leak. In addition nigericin is added to equilibrate K+/H+ and thus ensure the potential is a measure of protonmotive force. As such, the potential measured here was not in a true state 4 condition which is typically required for quantitation of proton leak.

After describing membrane potential measurements, the methods section describes respiration and H+ leak methodology. It appears oligomycin was added this time (good!), but then something very odd happens... it is stated that "H+ leak was measured as the state 2 respiration rate required to maintain membrane potential at -150mV". Nowhere is it stated how that value of 150mV was arrived at. Normally, when doing these measurements, you set the mitochondria in state 4 (succinate, rotenone, oligomycin, nigericin), and then titrate the activity of the respiratory chain with an inhibitor such as malonate. Step-wise titration then gives you a series of membrane potential and respiration traces, a curve, from which the leak rate at any given potential can be read off. The question is, if such curves were made, how were they made (no mention of malonate anywhere), and why aren't they shown in the paper? The scary alternative explanation may be that they "measured" leak by imposing the 150mV membrane potential by titrating in uncoupler. This is incorrect - you can't add something that changes the leak as a way of measuring the leak. The other odd thing is that the average baseline membrane potential in the IR group barely above 150mV, so some replicates in that group must have had a potential value below 150mV to begin with. How did they authors get those mito's UP to 150mV for the leak measurement? Overall, it would be a whole lot better if they just showed the full leak curves.

What about ROS? The problems here are two-fold. First it appears that SOD was not added to the incubations to scavenge any stray superoxide and turn it into H2O2 for the assay to pick up. Second, the calibration of the assay was performed incorrectly. It is stated in the methods that the signal was calibrated by "adding known concentrations of H2O2 to buffer solution containing horseradish peroxidase and Amplex-Red" The problem is, it is necessary to calibrate in the presence of mitochondria, so the signal you measure with the calibrating H2O2 is under the same condition as the measurement itself. The way this is commonly done is to just add a bolus of H2O2 at the end of each run. This has the advantage of making every run internally calibrated, which cuts down on noise (this is a very noisy assay). The outcome here is a bit odd... the values of H2O2 generation are in the range of 10-40 nM/min/mg protein. Ignoring the odd units (rates of things should be expressed in moles not Molar), let's assume they meant to write nmols/min/mg - that would put their rates about 1500-fold greater than typical for these conditions (e.g.Chen Q, 2003).

So, TL/DR - good ideas, but more info' is needed on the proton leak method, and the ROS numbers are just wild. Also, lest anyone think I'm attacking this work because I happen to be one of the people who originally proposed proton leak --> lower ROS --> protection in IR injury, that's not the case. In-fact, my lab' is now pursuing a completely different downstream signaling mechanism, as a mediator of the protective effects of mitochondrial uncoupling, so if the results of this paper are true, my life just got a whole lot easier! I just want to be sure before I start citing it.

On 2014 Aug 04, Paul Brookes commented:

This paper addresses a very important point... namely, one of the proposed mechanisms by which ischemic preconditioning (IPC) is thought to bring about cardioprotection. It has been hypothesized that increased leakiness of the mitochondrial membrane to protons may lead to a lowering of ROS generation. We provided some evidence to support increased H+ leak in IPC in 2006 Nadtochiy SM, 2006. Unfortunately, it's not immediately clear to me exactly how the authors measured H+ leak in this study, and also whether their ROS measurements were performed correctly.

First proton leak: The normal way this is determined is to make simultaneous measurements of membrane potential and respiration in a single chamber equipped with an oxygen electrode and another electrode sensitive to a lipophilic cation such as TPP+. The authors are to be commended on their choice to use a TPP+ electrode, which instantly makes this paper more quantitative than others using qualitative fluorescent probes such as TMRE. They measured membrane potential (as reported in Figure 3) using succinate as a substrate for complex II, with rotenone to inhibit complex I. All good so far. However, normally oligomycin is added to inhibit the ATP synthase as a potential source of leak. In addition nigericin is added to equilibrate K+/H+ and thus ensure the potential is a measure of protonmotive force. As such, the potential measured here was not in a true state 4 condition which is typically required for quantitation of proton leak.

After describing membrane potential measurements, the methods section describes respiration and H+ leak methodology. It appears oligomycin was added this time (good!), but then something very odd happens... it is stated that "H+ leak was measured as the state 2 respiration rate required to maintain membrane potential at -150mV". Nowhere is it stated how that value of 150mV was arrived at. Normally, when doing these measurements, you set the mitochondria in state 4 (succinate, rotenone, oligomycin, nigericin), and then titrate the activity of the respiratory chain with an inhibitor such as malonate. Step-wise titration then gives you a series of membrane potential and respiration traces, a curve, from which the leak rate at any given potential can be read off. The question is, if such curves were made, how were they made (no mention of malonate anywhere), and why aren't they shown in the paper? The scary alternative explanation may be that they "measured" leak by imposing the 150mV membrane potential by titrating in uncoupler. This is incorrect - you can't add something that changes the leak as a way of measuring the leak. The other odd thing is that the average baseline membrane potential in the IR group barely above 150mV, so some replicates in that group must have had a potential value below 150mV to begin with. How did they authors get those mito's UP to 150mV for the leak measurement? Overall, it would be a whole lot better if they just showed the full leak curves.

What about ROS? The problems here are two-fold. First it appears that SOD was not added to the incubations to scavenge any stray superoxide and turn it into H2O2 for the assay to pick up. Second, the calibration of the assay was performed incorrectly. It is stated in the methods that the signal was calibrated by "adding known concentrations of H2O2 to buffer solution containing horseradish peroxidase and Amplex-Red" The problem is, it is necessary to calibrate in the presence of mitochondria, so the signal you measure with the calibrating H2O2 is under the same condition as the measurement itself. The way this is commonly done is to just add a bolus of H2O2 at the end of each run. This has the advantage of making every run internally calibrated, which cuts down on noise (this is a very noisy assay). The outcome here is a bit odd... the values of H2O2 generation are in the range of 10-40 nM/min/mg protein. Ignoring the odd units (rates of things should be expressed in moles not Molar), let's assume they meant to write nmols/min/mg - that would put their rates about 1500-fold greater than typical for these conditions (e.g.Chen Q, 2003).

So, TL/DR - good ideas, but more info' is needed on the proton leak method, and the ROS numbers are just wild. Also, lest anyone think I'm attacking this work because I happen to be one of the people who originally proposed proton leak --> lower ROS --> protection in IR injury, that's not the case. In-fact, my lab' is now pursuing a completely different downstream signaling mechanism, as a mediator of the protective effects of mitochondrial uncoupling, so if the results of this paper are true, my life just got a whole lot easier! I just want to be sure before I start citing it.