This paper was the first to summarize effects of elevated atmospheric CO₂ concentration on plant respiration (respiration being activities of glycolysis, the oxidative pentose phosphate pathway, the TCA cycle, oxidative phosphorylation, and closely related reactions) and to outline why a change in CO₂ concentration might affect respiration rate. That is probably the reason it was cited as often as it was. Only a few data on the subject were available when the paper was written, however, so I included the disclaimer "Due to a lack of critical experiments and theory, some of what follows is speculative, with the intent of stimulating new thought on the topic" in the paper’s introduction. Moreover, I later changed my mind—and so have others—about a key assertion of the paper, i.e., that CO₂ directly affects plant respiration.

My first notable exposure to the topic of effects of elevated CO₂ on plant respiration occurred in early 1985 when I was a Ph.D. student at Yale University. Plant, Cell and Environment asked me to review a manuscript by Jossef Reuveni and Joe Gale. The key point of their paper, published later that year [1], was that alfalfa nighttime respiration was slowed when nighttime CO₂ level was increased, presumably as a direct response to CO₂ concentration in the dark. But why should CO₂ directly affect respiration? After all, CO₂ is a respiratory by-product, so respiration increases CO₂ levels in respiring cells. If CO₂ inhibits respiration, then respiration would in effect be inhibiting itself, and that inhibition would be strongest when respiration was most needed and therefore most rapid. What would be the adaptive or evolutionary benefit of such an effect? Certainly not to regulate respiration rate since other elegant respiratory control mechanisms tied to demand for the products of respiration (those products being ATP, NAD[P]H, and carbon skeleton intermediates) are well known [e.g., 2]. But there it was—experimental data showing that small increases in CO₂ (a few hundred ppm) slowed respiration. And other papers reported the same effect. The most important question raised by such results was, Is some fraction of respiration unnecessary for plant health and growth? While I realized that experimental artifacts could result in an apparent (i.e., fictitious) inhibition of respiration by elevated CO₂ (e.g., Hole [3] had shown that the inhibition of respiration by CO₂ reported by Harvey et al. [4] was due to an instrument error rather than a change in actual respiration rate), I accepted the idea that an increase in CO₂ "may directly suppress respiration rate" [5].

I did not devote much additional thought to plant respiratory responses to elevated CO₂ until I attended a workshop on elevated-CO₂ research at San Diego State University in May 1989 (research on effects of rising atmospheric CO₂ on plants and ecosystems was ‘taking off’ in the late 1980s). Several effects of growing plants in elevated CO₂ on plant respiration were mentioned at the workshop, but no explanations for those effects were articulated. I thought I saw relationships in the data being discussed, and asked for a few minutes of speaking time to present them. The workshop participants were obliging, and I outlined my main idea that two types of respiratory responses to elevated CO₂ were apparent. The first was a "direct effect" of CO₂ on respiration, which I first learned about reading the Reuveni and Gale paper in 1985. There was no biochemical or physiological explanation available for a direct effect. The second, separate effect was a normal response of respiration to other changes in plants brought about by growth in elevated CO₂. For example, elevated CO₂ increases photosynthesis, translocation, and growth in C3 plants (the largest and most studied group of terrestrial plants), and this should be accompanied by increased respiration to supply ATP, NAD[P]H, and carbon skeletons used in growth, transport, and maintenance activities. At the same time, elevated CO₂ often results in a lower tissue protein (or nitrogen) concentration, and a lower protein concentration might lead to slower respiration per unit dry mass because of smaller growth and maintenance requirements per unit biomass [5,6]. I called these "indirect effects" of CO₂ on respiration. An important distinction was that direct effects resulted from instantaneous CO₂ levels (i.e., CO₂ level during a respiration measurement) whereas indirect effects resulted from longer-term CO₂ levels (e.g., the CO₂ level a plant had been growing in for hours, days, weeks, months, or years). On my way home from the workshop, I decided to write an article (the subject of this essay), before someone else did, reviewing direct and indirect effects of elevated CO₂ on respiration. I thought the topic had room to grow, and I wanted to be part of that growth. I also decided to conduct research on the direct effect of CO₂ on respiration.

I worked on a manuscript in my spare time during the months following the San Diego workshop, but there was little to go on; the literature was sparse and I had no data of my own. Nonetheless, I produced a paper that expanded on my ideas developed at the workshop that I thought was worth publishing. I submitted it to Plant, Cell and Environment in late 1989, choosing that journal for three reasons: (1) it was publishing many of the better papers about plant responses to elevated CO₂, (2) it had a good readership, and (3) I published a paper on maintenance respiration in it in 1984 [7] and had had good experiences during the review and publication processes. In hindsight, the manuscript was simplistic. One of the reviews was no more than lukewarm (rightly) and the journal recommended that I revise the manuscript and resubmit it. I took the reviews to heart and began a significant rewrite. During this period I also decided to get going on experimental studies of the direct effect of CO₂ on respiration.

One thing was clear to me about the direct effect of CO₂ on respiration seen in experiments. If it was not due to gas exchange measurement errors (and most people reporting a direct effect knew their way around plant physiological gas exchange measurement systems), the next obvious thing to eliminate as a possible artifact causing the response was accelerated dark fixation of CO₂ (catalyzed by phosphoenolpyruvate carboxylase) caused by experimentally raising nighttime CO₂ levels. That is, because most measurements of respiration were based on CO₂ efflux, stimulated dark CO₂ fixation (occurring simultaneously with respiratory CO₂ release) would be interpreted as a slowing of respiration (i.e., net CO₂ efflux would decline). The simplest way in principal to distinguish changes in respiration from changes in dark CO₂ fixation would be to simultaneously measure CO₂ efflux and O₂ uptake because O₂ uptake is not immediately affected by dark CO₂ fixation. In practice, such measurements are difficult. I did not have appropriate instrumentation, but I learned that Arnold Bloom at the University of California, Davis, had developed a laboratory system to measure both gas fluxes [8] and I contacted him about doing some experiments with his system. He agreed, and on January 22, 1990, George Koch (who was a postdoc in Arnold’s lab at the time) and I began measuring the direct effect of short-term changes in CO₂ level in the dark on Rumex crispus (the ubiquitous weed curly dock) leaf respiration. Unfortunately, we experienced technical difficulties with the O₂ measuring part of the system, and were unable to address our objective. On the CO₂ side of things, though, we observed consistent, dramatic effects of instantaneous CO₂ level in the dark (in the range 50–950 ppm) on CO₂ efflux from leaves. Arnold’s system was built and operated to avoid CO₂ flux measurement errors, so we were confident that background CO₂ level was affecting CO₂ efflux from the leaves. One of the best aspects of my delving into this fresh area of research was meeting new people. Before this, I didn’t know Arnold or George, and 12 years later we are still good friends.

While we were conducting our experiments at Davis, and I was rewriting the Plant, Cell and Environment paper, Jim Bunce published [9] what I thought was the most comprehensive study of effects of elevated CO₂ on respiration conducted to that time. His experiments quantified both short-term (direct) and long-term (indirect) effects of elevated CO₂ on respiration in three species. In most cases, respiration was slowed by growth for several weeks in elevated CO₂. It was also slowed by short-term increases in CO₂ during measurements. I incorporated Bunce’s results and our Rumex experiments in the rewrite, and submitted the revised paper in March 1990. The main themes of the paper were that indirect effects should be distinguished from a direct effect of CO₂ on respiration. Indirect effects could (perhaps) be explained by basic knowledge of nonrespiratory plant responses to CO₂ and the links between respiration and those other responses. On the other hand, a direct effect could not be explained with available data; the effect was only an empirical observation. I proposed some biochemical mechanisms for a direct effect, but there was little to link them to experimental results. Following one more round of revisions, the paper was published (in January 1991). I think it provided a good mix of data, theory, and speculation for the immature subspecialty of effects of CO₂ concentration on plant respiration.

A few months after the 1991 paper was published, I attended a CO₂-effects workshop at the Smithsonian Environmental Research Center near Edgewater, Maryland, and reported on our 1990 experiments with Rumex crispus and a few key points from the 1991 paper. Based on our Rumex crispus experiments, available literature, and conversations with others making respiration measurements, I stated publicly at the workshop that elevated CO₂ "always, always, always" inhibits respiration in the short term. There is no written record of that statement, which is fortunate because published results I uncovered after the workshop, other results published shortly after the workshop, and our own soon-to-be-conducted experiments, revealed that respiration was often independent of short-term changes in CO₂ concentration. Nonetheless, we submitted our Rumex crispus results for publication later in 1991. They were published in 1992 [10] and impacted, we think, later research, though not necessarily for the better since we now know they were in error.

In February 1993, George and I measured O₂ exchange by Rumex crispus leaves while changing CO₂ level in the dark with equipment in Olle Björkman’s lab at the Carnegie Institution of Washington, in Stanford, California. We determined two things during those experiments. Oxygen uptake was not slowed by elevated CO₂ in the dark, and leaks in gas exchange measurement systems mimicked a direct effect of CO₂ on respiration measured as CO₂ efflux. Later that year, Reuveni et al. published a report [11] stating that CO₂ did inhibit O₂ uptake in the dark (their measurement system was similar to what we had used). Still, we trusted our results.

As a result of my 1991 and 1992 papers—and our related research—I was invited to give a presentation on respiration in the elevated-CO₂ symposium at the November 1993 American Society of Agronomy annual meeting in Cincinnati, Ohio. The presentation allowed me to consider the papers published since I wrote the 1991 paper (e.g., the papers of Ryle et al. [12,13] indicating the absence of a direct effect of CO₂ on respiration). The issue of the direct effect was becoming cloudy in my mind, and I placed some emphasis in the presentation on measurement errors. On the other hand, the slowly developing literature about indirect effects of CO₂ on respiration [e.g., 14] tended to support, at least in part, ideas expressed in the 1991 paper.

Following the 1993 symposium, I took advantage of the fact that the papers presented there were not published until 1997 (my manuscript was not one of those delaying publication) to update the presentation. Thus, my published paper resulting from the symposium [15] was current through 1995. With respect to the direct effect, George and I had conducted other CO₂ and O₂ exchange measurement experiments, and in all cases found respiration to be independent of CO₂ level in the dark. I mentioned this in the paper, and also noted other recent cases of a lack of a direct effect of CO₂ on respiration [e.g., 16]. Because I thought the direct effect might be artifactual, but also that CO₂ exchange measurements were generally being made correctly, I devoted considerable space in the 1997 paper to dark CO₂ fixations. With respect to indirect effects, the symposium paper was largely an expansion of my 1991 paper, and for the first time I carefully spelled out that indirect effects of CO₂ on respiration should be called "indirect effects of CO₂ on respiration because any environmental change that altered photosynthesis, growth, or plant composition in the same way as an increase in [CO₂ concentration] might affect respiration in the same way as does CO₂ enrichment." It was my view then (and remains so now) that much of the experimental literature on the subject could be properly interpreted in terms of the indirect effect approach/philosophy outlined in my 1991 and 1997 reviews. As an example, I showed by calculation [15] that the report of Thomas et al. [17] that daytime elevated CO₂ increased leaf respiration could be explained in terms of an indirect effect on the metabolic cost of translocation of sugars out of leaves. In the end, to the extent that rising daytime CO₂ increases plant growth, whole-plant respiration will increase about proportionally. Thus, rising atmospheric CO₂ will probably bring with it rising plant respiration.

Later, while making the "elevated-CO₂ workshop" rounds during the middle 1990s, George and I (together and independently) made a case for a lack of a direct effect of CO₂ on respiration. We presented several methodological problems that can result in apparent changes in respiration when no changes actually occur. As far as we could tell, our arguments were often dismissed by a significant fraction of the audience. I think that dismissal arose because it can be difficult to admit that measurement errors are the basis of published results (we freely admitted that our 1992 paper was probably in error), and many people working in this area were convinced that their methods were sound. On the other hand, several papers published during the middle 1990s indicated that the direct effect was small or did not exist.

Where do things stand now with respect to a direct effect of CO₂ on respiration? Several measurements of O₂ exchange and studies assessing potential artifacts of CO₂ exchange measurements indicate that respiration rate is independent of short-term changes in CO₂ level in the dark. Because all causes of CO₂ exchange measurement errors (e.g., gas analyzer sensitivity to background CO₂ level, leaks in gas handling systems, lateral transfer of gases through leaves partially enclosed in cuvettes, dilution of CO₂ caused by transpiration, adsorption/desorption of CO₂ on surfaces in a gas exchange measurement system, uptake and release of CO₂ by liquid "traps" used to control dew point in gas exchange systems) mimic a direct inhibition of respiration by an increase in CO₂, the onus is on the investigator to show that all artifacts are eliminated before concluding that a direct inhibition of respiration by CO₂ is being observed. Although reports of a direct effect of CO₂ on respiration continue to appear [e.g., 18], the weight of recent evidence [e.g., 19–27] indicates to me that respiration is not directly affected by CO₂ in the concentration range of 0 to at least 1,000 ppm. This means that a negative feedback on rising atmospheric CO₂ level from a direct inhibition of plant respiration by CO₂ is unlikely. In defense of those making plant respiration measurements, such measurements are technically difficult (usually much more difficult than standard measurements of leaf photosynthesis even though similar, or identical, equipment is used). Respiratory CO₂ fluxes are often small compared to typical high-light photosynthesis rates, so small errors that can be tolerated with photosynthesis measurements may have dire consequences for the accuracy of respiration measurements. An under-appreciation of the difficulties of respiration measurements when background CO₂ level was changed during an experiment probably resulted in some of the reports of a direct inhibition of respiration by elevated CO₂ (whereas an actual inhibition of respiration may not have existed). This was true of our 1992 paper [10].

In summary, our own work since 1990 (much of it supported by the U.S. Department of Energy’s Office of Biological and Environmental Research [BER]) has gone full circle, from indicating a strong and consistent direct effect of CO₂ on respiration to indicating a complete independence of respiration from short-term changes in CO₂. Other literature, though not all of it, indicates a similar shift in thinking within a larger community of scientists. My regret with respect to the considerable attention paid to a presumably artifactual direct effect of CO₂ on plant respiration is that the effort expended to characterize that nonexistent phenomenon could have been directed at more important topics, such as quantifying and explaining indirect effects of CO₂ on respiration. Thus, in part because of a distraction caused by several early reports of direct effects of CO₂ on respiration, work on indirect effects of rising CO₂ on respiration was slow. With the rapidly mounting evidence that direct effects are measurement artifacts, I hope that more work will be directed at other aspects of CO₂-respiration interactions. In particular, more research on whole-plant (not just individual leaf) respiration in response to long-term elevated CO₂ is needed. But if future research is to answer important questions about CO₂-respiration interactions, it will be "essential that measurements of respiratory fluxes [of CO₂ and/or O₂] are accompanied by measurements of other processes [that use the metabolic products of respiration], and of the status of the tissue being investigated (e.g. nutrient status, sugar concentration, N content and categories)" [28]. Only when respiration is placed in the context of overall metabolism will respiratory responses to environmental changes be amenable to explanation [29].

In closing, although I am now a government bureaucrat, I remain first and foremost a plant physiologist (my present position is temporary and I plan to return to research in a year). While fate did not dictate my chosen field (as far as I know), I discovered an interesting coincidence around the time I first read the Reuveni and Gale manuscript in 1985. I came across a 1957 paper by Herb Bormann in Plant Physiology [30]. It was published in the January issue. I was born in January 1957. And Herb was my dissertation advisor. So my eventual advisor (and good friend) had published a paper the month I was born in the journal bearing the name of my vocation. What is more, the article immediately before Herb’s in that issue (both articles shared page 48) was about plant respiration. Although these coincidences probably have no mystical significance, I find them intriguing.