Letter to the editor on the article “Alteration of redox status by commonly used antimalarial drugs in the north-western region of Nigeria” by Muhammad A et al.

Abstract

Malaria belongs to the most dangerous infectious diseases globally. Every effort to understand the mechanisms involved in Plasmodium spp. malaria infection and the antimalarial action cannot be overestimated. We have read with great interest the recently published article by Muhammad et al. entitled “Alteration of redox status by commonly used antimalarial drugs in the north-western region of Nigeria.” Several questions have arisen about the conducted study that we would like to comment on.

Despite the remarkable progress, malaria belongs to the most dangerous infectious diseases globally. According to the World Health Organization data, ¹ 212 million new cases and 429,000 deaths were reported in 2015 worldwide. Every effort to understand the mechanisms involved in Plasmodium spp. malaria infection and the antimalarial action cannot be overestimated. Therefore, we have read with great interest the recently published article by Muhammad et al. entitled “Alteration of redox status by commonly used antimalarial drugs in the north-western region of Nigeria.” ² We have hoped that this research would add to the discussion of the role of oxidative stress in these processes. However, several questions have arisen about the conducted study that we would like to comment on.

1. We assume that the authors planned an in vitro study to examine the effect of antimalarials on the oxidative stress in the whole blood of healthy people and Plasmodium falciparum-affected patients. However, the equal volumes of whole blood, pH 7.4 phosphate buffer, and drug solution were mixed (“100 µL of the blood sample was diluted with 100 µL of the phosphate buffer (pH 7.4) followed by the addition of 100 µL of each drug…”), undoubtedly leading to the hemolysis of the erythrocytes. Any information in the Materials and Methods section does not point that the authors used the iso-osmotic solution, for example, phosphate buffered saline. In the hypo-osmotic environment, erythrocyte cell membranes rupture easily, releasing hemoglobin and flooding the sample with potassium and other internal components. In the case of Plasmodium-infected erythrocytes, parasitic vacuoles are also supposed to be released in these conditions. Thus, numerous artefacts could interfere with the effect of drug action described in the article. By the way, the final drug concentrations were reduced three-fold from the initial stock solution in the experiment, not by half, as the authors claimed.

2. It should be also explained why the authors incubated the blood samples at room temperature, which did not reflect the in vivo parasite environment. In the methods of P. falciparum culture, temperature of 38°C is used. ³ At this temperature, the metabolism rate of both erythrocytes and parasites is most effective. Moreover, it has been proven that room temperature significantly activates platelets. ⁴ At 20°C, platelets exhibit significant changes in morphology, ultrastructure, membrane protein expression, and serotonin content, which may be associated with hemostatic effects. These changes might also affect the results of the study. It is worth to add that temperature of 37°C is commonly used in in vitro experiments studying the effects of drugs on the whole blood metabolism. ⁵

3. The next question concerns the level of parasitemia in the blood samples examined in the study. It has been shown that patients infected with different malaria parasite density differ in many hematological parameters, including leukocyte count, platelet count, and hemoglobin concentration. ⁶ Hence, the percentage of parasite-infected erythrocytes in the whole blood samples might have an important impact on the results of the experiment, and the specimens should be standardized. The possibility of bacterial contamination also should be taken under consideration. The authors did not provide any details about the clinical and biochemical characteristics of P. falciparum-infected patients. It should be also noted that the number of patients and healthy human subjects participating in the study was also omitted in the article.

4. We have many doubts about the biochemical methods carried out in the experiment. Firstly, the use of biuret method to determinate total protein content in the whole blood samples seems inappropriate. According to the authors, “biuret method was adopted in the determination of the total protein level of blood”, but the procedure for this adaptation was not described. It is particularly interesting what type of protein standard solution was used. If the protein concentration is measured in blood plasma or serum, a standard solution of bovine serum albumin is used in the calibration, but the high hemoglobin (Hb) content causes a positive interference without the proper blank correction. ⁷ At a high Hb concentration in blood serum samples, corrective measurements should be conducted using a solution containing no copper(II) sulfate instead of a biuret reagent solution. ⁸ The total protein concentration in whole blood can be correctly calculated as the sum of plasma protein concentration, weighted by hematocrit, and of Hb concentration. ⁹ It should be also taken into account that the drugs used in the experiment might interfere with biuret reagent. We are also interested why the total protein levels were measured, because there is no explanation provided in the Introduction or Discussion sections. In our opinion, the protein changes observed during the experiment could be influenced by numerous factors independent of the parasite or drug action.

Secondly, it was not determined what isoenzymes of superoxide dismutase (SOD) were measured in the study. This could be intracellular SOD-1 released from the erythrocytes during hemolysis, extracellular SOD-3 present in the plasma, or the parasite isoform of SOD. This information is crucial to discuss the changes in enzyme activity after incubating a blood sample with a drug solution. The same problem applies to the differences in catalase (CAT) activities observed during experiment.

Thirdly, the determination of CAT activity is really surprising. The authors claimed that they used the method of Brannan et al. ¹⁰ In fact, the method described for the first time by Sinha ¹¹ with the aid of a dichromatic/acetic acid solution instead of a reagent containing peroxidase and a chromogen was used. In addition, as described in the article, the dichromate/acetic acid solution was added to the reaction mixture at the beginning of the procedure and incubation was carried out at 80°C. Thus, the CAT was inhibited before any enzymatic reaction could take place.

5. Finally, last but not least important problem is the incomprehensible inconsistency between the Results, the Figures, and the Discussion sections. The Results are consistent with the Figures, indicating lower SOD and CAT activities, as well as higher glutathione levels in the infected samples. But in the Discussion, you can read that:

the activity of SOD was low in normal blood samples and high in the infected samples (…) the activity of catalase was reduced in healthy subjects and elevated in the malarial infected, whereas reduced glutathione level was elevated in healthy subjects and depleted in the infected patients.

The same problem concerns the description of malonyldialdehyde (MDA) changes in healthy and infected samples. It is not possible for the reader to determine which information is correct. This makes the publication completely incomprehensible and requires a thorough explanation.

Summing up, we expect a thorough revision of the study presented. We believe that it is important to investigate the effect of antimalarials on the oxidative stress in the blood of healthy and malaria-infected subjects. However, experiments should be accurately planned and performed to obtain reliable results.