by Pbo, Svante
Another novel aspect of the environment was that my appointment was to the Zoology Institute. I had never studied zoology, or even biology at the university level—just medicine, since in Sweden you can enter medical school directly after high school. This lapse became all too apparent almost as soon as I arrived, when an older professor asked whether I could perhaps teach the course on insect taxonomy in the upcoming semester. I was still jet-lagged, and preoccupied with other concerns, so without much thought I expressed my surprise that a zoology institute would deal with insects, as insects were hardly animals. In my mind, “animals” were things with paws, fur, and preferably floppy ears. The professor stared at me in disbelief and left without a word. I was immediately ashamed of having made such a complete fool of myself in the first week of my new job. But the good news was that no one ever again suggested that I teach any form of taxonomy or entomology at the institute.
As I was settling in, I learned that my predecessor at the institute had died unexpectedly of food poisoning. It was obviously not going to be easy to win the loyalty of all his colleagues, some of whom viewed me as an inexperienced and eccentric foreigner—a usurper of sorts. This was made clear in an unnerving encounter with Hansjochem Autrum, an emeritus professor and my predecessor’s mentor. Professor Autrum had been an influential figure in German zoology; when I arrived in Munich he still edited Naturwissenschaften, a somewhat influential German biology journal, and had an office on the same floor as my lab. During my first days in Munich, when I passed him on the staircase I greeted him cordially, but I got no response. One of my technicians reported that afterward he was heard to loudly complain that many good young German scientists could not find jobs and what did the department do but hire “international trash” (internationaler Schrott). I decided to ignore him from then on. Many years later, after his death, I became a member of a prestigious German order to which he had belonged, and I read his obituary in its proceedings. The author pointed out that before 1945 Professor Autrum had been a member not only of the Nazi Party but also of the Stormtroopers (SA) and had taught National Socialist ideology courses at a university in Berlin. Although I generally have a somewhat exaggerated desire to be liked by everybody, I felt retrospectively justified in having failed to befriend him.
Fortunately, Professor Autrum was an exception at the institute. Equally fortunately, he represented a generation that was on its way out in Germany. Gradually, by being frank about my ignorance not only of taxonomy but of most things zoological and administrative, I succeeded in bringing around even the older technicians in my group, and soon they wanted to help me build something that would be new and exciting. Charlie and Herbert, for their part, were extremely supportive. When the required laboratory renovations became more expensive than expected, the university came up with additional money. Slowly but surely, the equipment I needed was assembled, and all was put in order. Even more important, some students expressed interest in working with me.
Scientifically, I felt we needed to get systematic about establishing reliable procedures for amplifying ancient DNA. In Berkeley, I had begun to realize that contamination of these kinds of experiments with modern DNA was a serious problem, especially when the PCR was used. With the new PCR machines and the heat-resistant DNA polymerase, the process was sensitive enough that under favorable circumstances a handful of DNA molecules, or perhaps even a single molecule, could start the reaction. That sounds wonderful, but could lead to trouble. If, for example, a museum specimen contained no surviving ancient DNA but a few DNA fragments from some museum curator, we could unwittingly wind up studying the curator’s DNA instead of the DNA of an ancient Egyptian priest. Extinct animals, of course, presented much less of an opportunity to mislead ourselves; in fact, it was in the course of doing such work that I first realized the huge potential for contamination, since sometimes when I tried to amplify mtDNA from animal remains, I would get human mtDNA sequences instead. In 1989, shortly before I left Berkeley for Munich, I had published a paper with Allan Wilson and Russell Higuchi, whose quagga work I replicated, in which we introduced what we called criteria of authenticity; these were procedures we thought had to be carried out before a DNA sequence retrieved by the PCR could be confirmed as truly old.{13} We recommended that a “blank extract”—that is, an extract with no ancient tissue but containing all other reagents to be used—be processed in parallel every time extractions from old specimens were performed. This allowed us to detect DNA that might lurk in the reagents themselves, which came to the lab from various suppliers. In addition, extractions and PCRs needed to be repeated several times, to ensure that a DNA sequence could be replicated at least twice. And finally, I had realized that hardly any fragments of ancient DNA were longer than 150 nucleotides. In short, I had concluded that many experiments purporting to have isolated ancient DNA that had been done up to that point, and especially before the PCR became available, were hopelessly naïve.
In hindsight, I now realized that the mummy sequence I had published in 1985 was suspiciously long given that my subsequent work had shown that ancient DNA was almost always degraded to small fragments. One of two factors could explain why the sequence I found, as another group demonstrated, came from a transplantation antigen gene{14} (precisely the type of genes we had studied in our lab back in Uppsala): either because I had identified the sequence with a probe for such genes or because a piece of DNA from the lab had contaminated my experiments. Given the length of the sequence, contamination seemed much more likely. I consoled myself with the thought that this is how science progresses: older experiments are overtaken by new and better ones. And I was happy to be the one to improve on my own work. With time, there also came help from outside the field. In 1993, Tomas Lindahl published a short comment in Nature in which he suggested that criteria much like the ones we championed in 1989{15} were necessary for the ancient DNA field.{16} It was a great help to have a respected scientist from outside the field point this out—especially given my concern that the ancient DNA field tends to attract people without a firm background in molecular biology or biochemistry who, lured by the media attention that accompanies many ancient DNA results, simply apply the PCR to whatever old specimen they happen to be interested in. They practice what we in the lab liked to privately call “molecular biology without a license.”
As I now considered what projects to embark upon in my new lab, I was particularly inclined to study human history by molecular means. It was a fascinating topic but, as generally practiced, riddled with conjecture and biases stemming from preconceived ideas about history. I longed to bring a new rigor to the study of human history by investigating DNA sequence variation in ancient humans. One obvious possibility was to study the Bronze Age humans that were preserved in the peat bogs of Denmark and Northern Germany. But as I read more about them, I realized that these corpses had been preserved because the acid conditions in the bogs had essentially tanned them. Acid conditions lead to nucleotide loss and strand breakage and are therefore extremely bad for DNA preservation. But even worse, the tendency to find human DNA even in animal remains suggested that working with ancient humans could be seriously problematic.
So instead we started to collect samples of extinct animals, such as Siberian mammoths. And we started to do controlled experiments in a systematic way. For example, my first graduate students, Oliva Handt and Matthias Höss, used primers specific for human mtDNA. To my dismay, they found that they could amplify human DNA from almost all our animal samples and generally also from the blank extracts. We made up new reagents from fresh containers that had just been delivered to the lab, but it didn’t help. We did this again and again, trying to be as meticulous as we possibly could, but month after month we continued to find human DNA in almost every experiment. I began to despair. How could we ever trust the data, unless they completely conformed to our expectations, such as finding marsupial-like sequences from a marsupial wolf? And if we could only trust the expected results, that would ma
ke the field of ancient DNA very boring indeed, as we could then never discover the unexpected—which is, of course, the essence of experimental work and the dream of every scientist.
I walked home night after night frustrated and impatient with our failed experiments. But gradually it dawned on me that I was still being naïve about the contamination issue. I had not drawn the logical conclusions from my awareness of the PCR’s extreme sensitivity. At Berkeley, and during the first period in Munich, we would extract DNA from museum specimens on our lab benches—the same benches where we handled large amounts of DNA from humans and other organisms we were interested in. If even a microscopic droplet of a modern DNA solution made it into the ancient DNA extract, the modern DNA would overwhelm the few ancient molecules that might have come from the ancient tissue. This could well happen even if we made no obvious mistakes, such as forgetting to change the plastic tip of a pipette.
Figure 4.1. Oliva and Matthias in the first “clean room” in Munich. Photo: University of Munich.
It became clear to me that what we needed was to achieve complete physical separation of the extraction and handling of DNA from ancient tissues and all other experiments in the lab. In particular, we needed to isolate these experiments from the PCR, where trillions of molecules were produced. We needed a laboratory dedicated solely to ancient DNA extraction and amplification. So we located a small windowless room on our floor, which we emptied out completely and repainted, then spent time thinking about how DNA that might be lurking on the new benches and instruments we bought for this lab could best be destroyed. We came up with some harsh treatments. We cleaned the entire lab with bleach, which oxidizes DNA. We mounted ultraviolet lamps in the ceiling and left them on all night, since UV light wreaks havoc on DNA molecules. And we bought new reagents for our new lab, the first “clean room” in the world devoted to work on ancient DNA (see Figure 4.1). These measures dramatically improved things. Our blank extracts became clean, while, to my delight, some of our samples continued to yield DNA. But gradually, over months, the blanks turned up with DNA again. I was furious. What was going on? We threw out all our reagents and bought new ones.
Things got better again, but only for a while. It was time for paranoia, and the paranoia led not only to my mania for cleanliness in the clean room but to my establishment of several firm rules for how to work in a clean room—rules that to this day remain the standard. First of all, access was limited to the select group who did experiments there—in this case, my first two graduate students, Oliva and Matthias. Before they entered the clean room, they each donned a special lab coat, hairnet, special shoes, gloves, and a face shield. After some additional frustrations with contaminated blank extracts, I decided that they were allowed into the clean room only when they came directly from home in the morning. If they first walked through rooms where PCR products might be present, they were banned from the clean room for the rest of the workday. All chemicals had to be delivered directly to the clean room, and we bought new equipment that also went directly there. Slowly, things got better. Still, all new solutions and chemicals needed to be tested by the PCR for traces of human DNA, and it was not uncommon for a batch to have to be discarded. All of this was taxing work for Oliva and Matthias, who had joined me in hopes of studying ancient humans and extinct animals and found themselves instead vetting chemicals and fretting about contagion.
But the lab’s general mood improved as our efforts began to pay off. As our extracts became clean, we could start working on other methodological issues. So far, all our work had been on soft tissues, such as skin and muscle. But I remembered that one of my DNA-yielding mummy samples in Uppsala had come from cartilage, a tissue not very different from bone. If DNA could be extracted from ancient bones rather than just soft tissues, this would obviously open up great opportunities, as bones are what generally remain from ancient individuals. In 1991, Erika Hagelberg and J. B. Clegg of Oxford University had published a paper describing the extraction of DNA from ancient human and animal bones.{17} So when the contamination issue was under control, Matthias tried many methods for getting DNA out of bones, focusing on animals where the risk of contamination was much smaller (as DNA from most animals was rare in our laboratory). Among them was a protocol described in the literature for DNA extraction from microorganisms. It relied on the fact that DNA binds to silica particles—essentially a very fine glass powder—in solutions that contain high salt concentrations. The silica particles could then be thoroughly washed to get rid of all kinds of unknown components that were in many of the samples and that could interfere with the PCR. Finally, the DNA could be released from the silica particles by lowering the salt concentration. This extraction procedure was an arduous process, but it worked and so represented a major step forward.
Matthias and I published the silica extraction method in 1993; the experiment used Pleistocene horse bones, and the mtDNA sequence they yielded was proof that we could retrieve DNA from bones that were 25,000 years old—the first time that reliable DNA sequences from before the last Ice Age were presented.{18} With small modifications, this is still the extraction protocol used in most ancient DNA extractions today. The many frustrations that preceded this paper were evident from our opening remark that our young field was “marred by problems.” But this was slowly changing. In fact, without realizing it at the time, Matthias and Oliva had laid the foundations for much of what was to come in the next few years. In 1994, Matthias retrieved the first DNA sequences from Siberian mammoths, working with four individuals between 9,700 and more than 50,000 years old. We sent this work to Nature, where it was published together with similar results from Erika Hagelberg, who had isolated DNA from the bones of two mammoths.{19} Although these mtDNA sequences were very short, they hinted at what would be possible if more sequences could be retrieved. We saw, for example, that there were many differences among the DNA sequences from the four mammoths. So we could imagine not only clarifying the relationship of mammoths to the two living members of the same order—the Indian and African elephants—but also tracing the history of mammoths in the Late Pleistocene and on up to their extinction some 4,000 years ago. Things were finally looking brighter for ancient DNA.
This was also a time when our skills in extracting DNA and doing the PCR were applied to other, rather less conventional biological materials. Felix Knauer, a wildlife biologist at the university, showed up one day in my office and asked about the application of our DNA techniques to “conservation genetics,” the field that tries to apply genetics to the question of how best to protect endangered species. Felix had collected feces from the last surviving wild population of Italian bears, who lived on the southern slopes of the Alps. I invited Felix and a few other students to try our silica extraction method and PCR from the bear feces. We showed that we could amplify bear mtDNA from such droppings. Previously, the only way to get DNA from an animal in the wild was either to kill it or to shoot it with a tranquilizing dart and draw blood, a risky (and for the animal obviously very disturbing) procedure. We could now study the genetic relationship of the Italian bears to other European bear populations without bothering the bears at all. We published this work as a small paper in Nature, in which we also showed that we could retrieve DNA from the plants that the bears had eaten and thereby reconstruct aspects of their diet.{20} Extraction of DNA from droppings collected in the wild has since become common practice in wildlife biology and conservation genetics.
As we were painstakingly developing methods to detect and eliminate contamination, we were frustrated by flashy publications in Nature and Science whose authors, on the surface of things, were much more successful than we were and whose accomplishments dwarfed the scant products of our cumbersome efforts to retrieve DNA sequences “only” a few tens of thousands of years old. This trend had begun in 1990, when I was still at Berkeley. Scientists at UC Irvine published a DNA sequence from leaves of Magnolia latahensis that had been found in a Miocene deposit in Clarkia, Idaho, and we
re 17 million years old.{21} This was a breathtaking achievement, seeming to suggest that one could study DNA evolution on a time scale of millions of years, perhaps even going back to the dinosaurs! But I was skeptical. From what I had learned in Tomas Lindahl’s laboratory in 1985, I had concluded that it was possible for DNA fragments to survive for thousands of years, but millions seemed out of the question. Allan Wilson and I did some simple extrapolations, based on Lindahl’s work, in which we determined how long DNA would survive if water were present and conditions were neither too hot nor too cold, neither too acid nor too basic. We concluded that after some tens of thousands of years—and perhaps, under extraordinary circumstances, a few hundreds of thousands of years—the last molecules would be gone. But who knew? Perhaps there was something very special about those fossil beds in Idaho. Before going to Germany, I visited the site. The deposits were formed of dark clay, which was removed by a bulldozer. Upon being pried open, the blocks of clay revealed green magnolia leaves, which rapidly turned black when exposed to air. I collected many of these leaves and brought them with me to Munich. In my new lab, I tried extracting DNA from the leaves and found that they contained many long DNA fragments. But I could amplify no plant DNA by PCR. Suspecting that the long DNA was from bacteria, I tried primers for bacterial DNA instead, and was immediately successful. Obviously, bacteria had been growing in the clay. The only reasonable explanation was that the Irvine group, who worked on plant genes and did not use a separate “clean lab” for their ancient work, had amplified some contaminating DNA and thought it came from the fossil leaves. In 1991, Allan and I published our theoretical calculations in an article about the stability of DNA,{22} and in a second paper we described my failed attempts to get DNA from the plant fossils from Idaho.{23} This was a sad time, since Allan had fallen severely ill with leukemia the year before. Nevertheless, he made substantial contributions to both papers. He died in July of that year at the young age of fifty-six.
