Diamonds are expensive: lessons learned about applying synthetic biology for 1000+ year carbon dioxide removal  

December 4, 2023

Using biotechnology for long-term durable (1000+ years) carbon removal has been of interest for several years, although this field is still in its early stages. Proposed ideas have included the production of highly decay-resistant molecules (such as suberin, enhanced lignin, and sporopollenin), increased root biomass, bio-enhanced rock weathering and carbon mineralization, and hybrid approaches that use biology to enhance direct air capture (DAC).  

At Living Carbon, we had experience engineering trees for enhanced photosynthesis and fungal decay resistance, but wanted to add a long-term durable carbon dioxide removal (CDR) approach to our portfolio. We applied to Stripe’s Spring 2022 carbon removal purchase cycle with an idea that we had been considering for a while: engineering increased production of sporopollenin. Otherwise known as the “diamond of the plant world,” sporopollenin is the main component of exine, the outer coating of most pollen grains and spores. It is the toughest biopolymer nature has ever produced and has been found in rocks over 500 million years old.

The sporopollenin polymer. [Source: MIT News]

Our approach to choosing and developing the sporopollenin project

Our investigation of biological, durable CDR began by taking an inventory of the most recalcitrant forms of carbon storage existing in nature. We then focused on sporopollenin because of its high durability. We wanted to leverage the ability of biological systems to grow autotrophically, covering the “capture” part of carbon removal with a fast growth rate. Then, we would synthetically add the “storage” component to enable durable CDR at a theorized low cost. We assumed that by adding long-term storage to a rapid-growth organism, we could deliver 1000+ years of storage at less than $100/ton.

In retrospect, we believe this was not the correct starting point. Rather than starting with a list of potential solutions (in this case, durable substances that could be produced biologically), going forward, we would start by surveying the largest-scale and/or most efficient existing forms of CO₂  sequestration and questioning whether these processes could be biologically enhanced. 

A floating hexagon bioreactor: one of the ideas Living Carbon considered for algae production of sporopollenin.

A year later, our science team had made impressive progress, but we concluded it would be near-impossible to produce sporopollenin at <$100/ton. We learned a lot about what it means to use synthetic biology for high-quality, low-cost carbon removal, and wanted to share these learnings with the broader community. There are certain commercial pitfalls that may be applicable to other proposed synbio-for-CDR solutions and are worth considering early in their evaluation. We believe solutions that clearly articulate a strategy to avoid these pitfalls are much more likely to succeed and to move the emerging field of synthetic biology for climate toward research that has the best chance of scaling. 

Our initial hypothesis: successful applications of synbio to CDR would involve the rapid accumulation of durable substances with limited arable land.

During our initial evaluation of durable CDR ideas, we evaluated ideas based on these criteria: (i) a path to scale at <$100/ton, (ii) limited competition for arable land, and (iii) a reasonably clear path to quantifying MRV and storage uncertainty. 

In any organism, production of sporopollenin (or another highly decay-resistant substance) would likely be limited to a relatively small percentage of overall biomass.In our decomposition resistant trees, decay-resistant lignin comprises a much higher percentage of biomass, but it’s unlikely that decomposition will be prevented for over 1000 years. For this reason, we expected arable land to be a challenge from the outset. Producing sporopollenin in 1-20% of the stems or roots of grasses or other small plants would have required millions of acres of land to remove carbon at megaton-scale.Living Carbon’s mission includes the development of forest carbon projects on millions of acres of degraded land, but these are intended to be restored forests that establish biodiverse ecosystems. We ruled out the planting of millions of acres of switchgrass monoculture. Early calculations for switchgrass, hemp, and other species pushed us in the direction of thinking about microalgae, which grows extremely rapidly and is often cultivated in desert ponds.

We developed a preliminary concept for sporopollenin production using microalgae in desert-based raceway ponds. Several microalgae species naturally produce sporopollenin in their cell walls, including auxenochlorella protothecoides, haematococcus pluvialis, and dunaliella salina (in its cyst stage). Our goals were to maximize the growth rate of the algae, and the percentage of sporopollenin in the cell wall, and also to decrease the costs of the production system as much as possible by 2040. 

Example of how sporopollenin could be grown at scale.

Our progress and findings

Over the next year, our R&D team made rapid progress against our scientific milestones in terms of strain selection and enzyme engineering while we investigated species + deployment scenarios that would get us closer to the <$100/ton target. We evaluated various types and combinations of production systems - raceway ponds, algae biorefineries (producing multiple products from one feedstock), and hybrid approaches involving semi-permeable open-water bioreactors. We were only planning to sell the sporopollenin as permanent carbon (rather than burying the entire algal biomass, which would be possible without synthetic biology).We did consider briefly whether a high-sporopollenin cell wall might result in durable storage of the entire cell contents. After going down a rabbit hole reading about pollen and bee poop, we concluded that sporopollenin-based shells can likely be infiltrated without being broken down, and we tabled this idea.

After conducting more detailed techno-economic analyses of these systems, we found that one of the following would have to be true if sporopollenin comprised a maximum of 20% dry biomass: 

  • We could produce biomass so cheaply that sporopollenin could be sold for <$100/ton, implying the production of algae biomass at <$20/ton. Even in the cheapest, most productive scenario we could imagine, it does not seem possible to achieve this in a controlled environment. Biomass can likely only be grown that cheaply in an open, self-regulating environment, where ambient conditions are adequate to sustain growth (but culture contamination and competition are a constant risk). Engineered microbes in an open system would also face regulatory and MRV challenges.
  • We could offset the production costs with a high-value co-product. The biggest issue here was the need for an established co-market with millions of tons of demand. Bio-fuels, bio-plastics, and the idea of massive algae food protein markets were too early and uncertain, while high-value products like astaxanthin and other algae-based supplements currently have markets of <100 tons/year.

We assumed there would be biological limitations on producing more than 20% sporopollenin in a cell. If sporopollenin was our only product, this meant we would always be stuck producing at least 80% more biomass than we intended to sell as CDR. Meanwhile, if we wanted to separate and sell the rest of the biomass, we would incur much higher separation and processing costs without a lucrative secondary market for millions of tons of algae biomass. Reflecting on this project led us to refine our understanding of the criteria that determine whether a synbio solution is likely to scale CDR at a low cost.  

Sporopollenin isolation from Algae in Living Carbon’s lab.

Based on our work in trees, we assumed that there would be economies of scale involved in growing megatons of biomass because live organisms are self-replicating. When we plant a forestry project, there are high up-front costs for site prep and planting, but also exponential biomass accumulation during most of the project lifetime. The algae projects we considered were different in key ways that illustrated how biological solutions are not always cheaper and more scalable. Biological solutions are most effective when they have a strong multiplier effect in terms of value created. In this case, even though the algal biomass would have grown rapidly, this did not translate to equivalent growth in sufficiently valuable output.

The conversion efficiency of systems should be evaluated carefully, whether they are engineered or biological.

When we started modeling sporopollenin systems, we focused on “diffuse” sporopollenin production comprising a small percentage of each plant over a large area. This would have had the cost benefits of one-time planting and no harvest requirement, as long as the rest of the plant could decay - leaving the sporopollenin to self-scatter.This may have been an MRV hurdle but we think not an insurmountable one, given the overall promise of open-system CDR. The tradeoff here would be the amount of required arable land. The per-acre yield of permanent carbon credits would have been diluted by a huge supply of either fast-decomposing biomass (for example, in grass) or medium-term carbon credits (in trees).

As a result, we developed production concepts that were so different from nature-based solutions that they resembled what we traditionally understand as “engineered solutions.” The resulting high capex and opex would have required the same conversion efficiency as any other engineered solution in order to be profitable. In the absence of a strong use case for the remaining 80% of biomass, we were left with a fundamentally low conversion efficiency that could not be overcome by other forms of cost reduction.

Improving the efficiency of a system is an appropriate target for synthetic biology by increasing either the organism’s overall growth rate, resilience to unfavorable conditions, or the yield of the target substance. However, especially when trying to engineer the production of a recalcitrant substance, there may be limitations set by the organism’s other metabolic requirements that likely make certain engineering targets unrealistic.We considered an example involving a “mold bioreactor,” since sporopollenin is the main outer component of spores. We were unable to model a realistic but favorable ratio of mycelium to spore production in a highly engineered, expensive bioreactor environment. The idea of a massive tank full of spores was also pretty gross.

We developed the following graph that shows the “spectrum” of potential applications of synbio to climate grouped by input cost vs. yield:

Four examples are provided to illustrate solutions along the spectrum, although these are far from the only possibilities. 

We think the two general solution categories highlighted in green have the most promise but would evaluate solutions critically to make sure they don’t fall into the other two categories.

“Set it and forget it” nature-based solutions can improve or restore land with low input costs over time. These are self-regulating systems that may have higher land use requirements, but the land change is positive and involves co-benefits such as biodiversity restoration. The “downside” is that prioritizing biodiversity means limiting the concentration of the target species, which can cap the reasonable per-acre yield of durable carbon storage. 

Trees accumulate so much biomass overall that planting photosynthesis-enhanced trees alongside diverse other species is projected to have a large impact on additionality. However, when it comes to small plants and/or creating a substance that is only a small percentage of the plant, the risk here is creating low-cost, low-yield projects. The pitfall we recommend avoiding is trying to get around this by growing as much of the synbio species as possible per acre. At best, such a solution might require intensive maintenance. At worst, the species might become ecologically disruptive. 

Living Carbon’s trees growing on an abandoned mineland in Pennsylvania.

Meanwhile, certain types of engineered solutions that involve a biological component might still incur the high capital and operating costs of any other engineered solution. If high costs are incurred to maintain a controlled environment such as a bioreactor, the biological component should be held to the same output standards as a material or chemical solution. This seems straightforward, but there are situations where a high growth rate does not equal a high yield of 1000+ years of CO₂  storage. If there is a favorable ratio of primary production to CO₂  storage, we regard this as a sign that high input costs may be justified. The pitfall we recommend avoiding is relying too heavily on cost reductions in closing the cost gap, without high confidence that the synbio species is going to act as a force multiplier in terms of the CDR yield. Our observation has also been that for more complex systems, higher capital costs are also correlated with high emissions due to processing. This makes it even more important that a force multiplier relationship is introduced by the synbio trait - more linear improvements can easily be offset by added emissions associated with handling and processing the biomass. 

Our takeaway: the most powerful solutions may involve significant uncertainty, but they should also have straightforward calculations showing that biology is a force multiplier in terms of CDR output.

The path forward: How can we achieve durable synbio carbon dioxide removal?

We know that nature-based solutions can scale quickly and cheaply, but only when they involve genuine restoration of self-sustaining ecosystems. If low input costs are the goal, we would start with an inventory of the most powerful carbon sinks in nature, and ask which biological interventions can increase their overall rate of carbon drawdown or slow their decomposition over time. Under this framework, we would prioritize meaningful improvements in the health and performance of forests, grasslands, peatlands, and other large-scale carbon sinks, even if there are open questions regarding the durability of these solutions. They can still act as a powerful net carbon sink as they scale to millions of acres, not to mention the ecosystem co-benefits. 

For biological engineered systems, we have learned that conversion efficiency is paramount. Biology tends to not favor the concentrated production of metabolically taxing, highly inert substances, which is guiding us in the direction of investigating other reactions and methods aside from CO₂ permanently stored in plant matter.Biomass burial seems to be the clearest path to a near-100% conversion efficiency of grown to stored biomass. Decay-resistant biopolymers may still be a valid path, but we think there will continue to be complex questions around the fate of the remaining biomass.

We believe the challenge will be to identify opportunities where synbio can rapidly achieve permanent storage while overcoming similar versions of the same issues:

  • Excess production of unrelated biomass 
  • Requiring a monoculture to achieve sufficient scale 
  • Needing highly controlled, expensive growth environments to perform adequately 
  • Slow and/or diffuse yield of CDR, resulting in negligible carbon yield per acre and low project returns 

As we look at other applications of synbio for CDR (bio-enhanced weathering reactions, bio-enhanced ocean alkalinity enhancement, and bio-enhanced DAC), we can see potential parallel challenges. What species will be used? Will the new species singlehandedly accelerate CO₂  sequestration and storage enough to be worth it? What conditions will be employed to grow and maintain adequate population levels of the target species? Are these conditions too expensive and sensitive to justify the cost? 

An example of cover cropping, a form of regenerative agriculture. Cover cropping is referring to growing crops specifically to improve and protect soil health between periods of regular crop production. A synthetic biology approach that enhanced other practices such as regenerative agriculture may be more likely to succeed than a plant cultivated without clear co-benefits.

The level of excitement we see in the CDR community around synbio is motivating, and we learned through this project that there is a lot of industry demand for synbio traits to improve various processes. Because this area is still in its early stages, we invite open discussion and objective evaluation of these challenges to guide the field toward the ideas that are most likely to scale. While we’re sorry for now to say goodbye to the diamond of the plant world, our takeaway is not to become discouraged - it’s to refine our understanding of the true opportunities and limitations of biological solutions and evolve in this direction.

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